% %%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%%% %
%                                                                         %
% Project Gutenberg's A Treatise on Probability, by John Maynard Keynes   %
%                                                                         %
% This eBook is for the use of anyone anywhere at no cost and with        %
% almost no restrictions whatsoever.  You may copy it, give it away or    %
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%                                                                         %
% Title: A Treatise on Probability                                        %
%                                                                         %
% Author: John Maynard Keynes                                             %
%                                                                         %
% Release Date: May 31, 2010 [EBook #32625]                               %
%                                                                         %
% Language: English                                                       %
%                                                                         %
% Character set encoding: ISO-8859-1                                      %
%                                                                         %
% *** START OF THIS PROJECT GUTENBERG EBOOK A TREATISE ON PROBABILITY *** %
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Project Gutenberg's A Treatise on Probability, by John Maynard Keynes

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Title: A Treatise on Probability

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%%%%%%%%%%%%%%%%%%%%%%%%%%% FRONT MATTER %%%%%%%%%%%%%%%%%%%%%%%%%%

\frontmatter

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BY THE SAME AUTHOR
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\begin{center}
\MyHuge\bfseries A TREATISE \\
ON PROBABILITY
\vfill\vfill

\normalfont\footnotesize BY\\[8pt]
\large JOHN\ \ MAYNARD\ \ KEYNES\\[8pt]
\tiny FELLOW OF KING'S COLLEGE, CAMBRIDGE
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\Preface

The subject matter of this book was first broached in the brain
of Leibniz, who, in the dissertation, written in his twenty-third
year, on the mode of electing the kings of Poland, conceived
of Probability as a branch of Logic. A few years before, ``un
problème,'' in the words of Poisson, ``proposé à un austère
janséniste par un homme du monde, a été l'origine du calcul
des probabilitiés.'' In the intervening centuries the algebraical
exercises, in which the Chevalier de la Méré interested Pascal,
have so far predominated in the learned world over the profounder
enquiries of the philosopher into those processes of
human faculty which, by determining reasonable preference,
guide our choice, that Probability is oftener reckoned with Mathematics
than with Logic. There is much here, therefore, which is
novel and, being novel, unsifted, inaccurate, or deficient. I
propound my systematic conception of this subject for criticism
and enlargement at the hand of others, doubtful whether I
myself am likely to get much further, by waiting longer,
with a work, which, beginning as a Fellowship Dissertation,
and interrupted by the war, has already extended over
many years.

It may be perceived that I have been much influenced by
W.~E. Johnson, G.~E. Moore, and Bertrand Russell, that is
to say by Cambridge, which, with great debts to the writers
of Continental Europe, yet continues in direct succession
the English tradition of Locke and Berkeley and Hume, of
Mill and Sidgwick, who, in spite of their divergences of
%% -----File: 005.png---Folio vi-------
doctrine, are united in a preference for what is matter of
fact, and have conceived their subject as a branch rather of
science than of the creative imagination, prose writers, hoping
to be understood.

\hfill J. M. KEYNES.{\qquad}
\bigskip

\footnotesize
\settowidth{\TmpLen}{\textsc{King's College, Cambridge},}%
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\centering
\textsc{King's College, Cambridge},  \\
\textit{May} 1, 1920.
\end{minipage}
\normalsize

%% -----File: 006.png---Folio vii-------

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\fancyhead[CE]{\CtrHeading{A Treatise on Probability}}
\fancyhead[CO]{\CtrHeading{Contents}}
\phantomsection
\pdfbookmark[0]{Contents}{Table of Contents}
\tableofcontents

\iffalse
CONTENTS

PART I
FUNDAMENTAL IDEAS

CHAPTER I                                               PAGE
The Meaning of Probability                                 3

CHAPTER II
Probability in Relation to the Theory of Knowledge        10

CHAPTER III
The Measurement of Probabilities                          20

CHAPTER IV
The Principle of Indifference                             41

CHAPTER V
Other Methods of Determining Probabilities                65

CHAPTER VI
The Weight of Arguments                                   71
%% -----File: 007.png---Folio viii-------

CHAPTER VII
Historical Retrospect 79

CHAPTER VIII
The Frequency Theory of Probability 92

CHAPTER IX
The Constructive Theory of Part I. summarised 111


PART II
FUNDAMENTAL THEOREMS

CHAPTER X
Introductory 115

CHAPTER XI

The Theory of Groups, with special reference to Logical
Consistence, Inference and Logical Priority 123

CHAPTER XII
The Definitions and Axioms of Inference and Probability 133

CHAPTER XIII
The Fundamental Theorems of Necessary Inference 139

CHAPTER XIV
The Fundamental Theorems of Probable Inference 144
%% -----File: 008.png---Folio ix-------

CHAPTER XV                                               PAGE
Numerical Measurement and Approximation of Probabilities  158

CHAPTER XVI
Observations on the Theorems of Chapter XIV., and
their Developments, including Testimony                   164

CHAPTER XVII
Some Problems in Inverse Probability, including Averages  186

PART III
INDUCTION AND ANALOGY

CHAPTER XVIII
Introduction                                              217

CHAPTER XIX
The Nature of Argument by Analogy                         222

CHAPTER XX
The Value of Multiplication of Instances, or Pure Induction 233

CHAPTER XXI
The Nature of Inductive Argument continued                242

CHAPTER XXII
The Justification of these Methods                        251

CHAPTER XXIII
Some Historical Notes on Induction                        265

Notes on Part III                                         274
%% -----File: 009.png---Folio x-------

PART IV
SOME PHILOSOPHICAL APPLICATIONS OF PROBABILITY

CHAPTER XXIV                                             PAGE
The Meanings of Objective Chance, and of Randomness       281

CHAPTER XXV
Some Problems arising out of the Discussion of Chance     293

CHAPTER XXVI
The Application of Probability to Conduct                 307


PART V
THE FOUNDATIONS OF STATISTICAL INFERENCE

CHAPTER XXVII
The Nature of Statistical Inference                       327

CHAPTER XXVIII
The Law of Great Numbers                                  332

CHAPTER XXIX
The Use of à priori Probabilities for the Prediction of
Statistical Frequency---the Theorems of Bernoulli,
Poisson, and Tchebycheff                                  337

CHAPTER XXX
The Mathematical use of Statistical Frequencies for the
Determination of Probability à posteriori--the Methods
of Laplace                                                367
%% -----File: 010.png---Folio xi-------

CHAPTER XXXI                                             PAGE
The Inversion of Bernoulli's Theorem                      384

CHAPTER XXXII
The Inductive Use of Statistical Frequencies for the
Determination of Probability à posteriori--the Methods
of Lexis                                                  391

CHAPTER XXXIII
Outline of a Constructive Theory                          406

BIBLIOGRAPHY                                              429

INDEX                                                     459
\fi
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%[Blank Page]
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\index{Morgan, \textit{vide} De Morgan}%
\index{Succession, Law of!\textit{See} Rule of}%

\mainmatter

\Part{I}{Fundamental Ideas}
%% -----File: 013.png---Folio 2-------
%[Blank Page]
%% -----File: 014.png---Folio 3-------
\index{Logic, academic}%
\index{Proposition, characterisation of}%

\Chapter{I}{The Meaning of Probability}

\begin{Quote}
``J'ai dit plus d'une fois qu'il faudrait une nouvelle espèce de logique, qui
traiteroit des degrés de Probabilité.''---\textsc{Leibniz}.
\end{Quote}

\Paragraph{1.} \First{Part} of our knowledge we obtain direct; and part by
\index{Knowledge!kinds of}%
argument. The Theory of Probability is concerned with that
part which we obtain by argument, and it treats of the different
degrees in which the results so obtained are conclusive or inconclusive.

In most branches of academic logic, such as the theory of the
syllogism or the geometry of ideal space, all the arguments aim
at demonstrative certainty. They claim to be \emph{conclusive}. But
many other arguments are rational and claim some weight without
pretending to be certain. In Metaphysics, in Science, and in
Conduct, most of the arguments, upon which we habitually base
our rational beliefs, are admitted to be inconclusive in a greater
or less degree. Thus for a philosophical treatment of these
branches of knowledge, the study of probability is required.

The course which the history of thought has led Logic to follow
has encouraged the view that doubtful arguments are not within
its scope. But in the actual exercise of reason we do not wait
on certainty, or doom it irrational to depend on a doubtful
argument. If logic investigates the general principles of valid
thought, the study of arguments, to which it is rational to attach
\emph{some} weight, is as much a part of it as the study of those which
are demonstrative.

\Paragraph{2.} The terms \emph{certain} and \emph{probable} describe the various degrees
of rational belief about a proposition which different amounts of
knowledge authorise us to entertain. All propositions are true
or false, but the knowledge we have of them depends on our
circumstances; and while it is often convenient to speak of
%% -----File: 015.png---Folio 4-------
\index{Belief, rational|ifoll}%
\index{Probability, and relevant knowledge}%
\index{Probability relation}%
\index{Proposition, characterisation of}%
propositions as certain or probable, this expresses strictly a
relationship in which they stand to a \textit{corpus} of knowledge, actual or
\index{Knowledge!kinds of}%
hypothetical, and not a characteristic of the propositions in themselves.
A proposition is capable at the same time of varying degrees
of this relationship, depending upon the knowledge to which it is
related, so that it is without significance to call a proposition probable
unless we specify the knowledge to which we are relating it.

To this extent, therefore, probability may be called subjective.
But in the sense important to logic, probability is not
subjective. It is not, that is to say, subject to human caprice.
A proposition is not probable because we think it so. When once
the facts are given which determine our knowledge, what is
probable or improbable in these circumstances has been fixed
objectively, and is independent of our opinion. The Theory of
Probability is logical, therefore, because it is concerned with the
degree of belief which it is \emph{rational} to entertain in given conditions,
and not merely with the actual beliefs of particular individuals,
which may or may not be rational.

Given the body of direct knowledge which constitutes our
ultimate premisses, this theory tells us what further rational
beliefs, certain or probable, can be derived by valid argument
from our direct knowledge. This involves purely logical relations
between the propositions which embody our direct knowledge
and the propositions about which we seek indirect knowledge.
What particular propositions we select as the premisses
of \emph{our} argument naturally depends on subjective factors peculiar
to ourselves; but the relations, in which other propositions stand
to these, and which entitle us to probable beliefs, are objective
and logical.

\Paragraph{3.} Let our premisses consist of any set of propositions~$h$, and
our conclusion consist of any set of propositions~$a$, then, if a
knowledge of~$h$ justifies a rational belief in~$a$ of degree~$\alpha$, we say
that there is a \emph{probability-relation} of degree~$\alpha$ between $a$~and~$h$.\footnote
  {This will be written $a/h = \alpha$.}

In ordinary speech we often describe the \emph{conclusion} as being
doubtful, uncertain, or only probable. But, strictly, these terms
ought to be applied, either to the degree of our \emph{rational belief} in
the conclusion, or to the relation or argument between two sets
of propositions, knowledge of which would afford grounds for a
corresponding degree of rational belief.\footnote
  {See also \Chapref{II}. §\;5.}
%% -----File: 016.png---Folio 5-------
\index{Event, probability of}%
\index{Probability, and relevant knowledge!objective relation of}%

\Paragraph{4.} With the term ``event,'' which has taken hitherto so important
a place in the phraseology of the subject, I shall dispense
altogether.\footnote
  {Except in those chapters (\Chapref[Chap.]{XVII}., for example) where I am dealing
  chiefly with the work of others.}
Writers on Probability have generally dealt
with what they term the ``happening'' of ``events.'' In the
problems which they first studied this did not involve much
departure from common usage. But these expressions are now
used in a way which is vague and ambiguous; and it will be
more than a verbal improvement to discuss the truth and the
probability of \emph{propositions} instead of the occurrence and the
probability of \emph{events}.\footnote
  {The first writer I know of to notice this was Ancillon in \textit{Doutes sur les
\index{Ancillon|inote}%
  bases du calcul des probabilités} (1794): ``Dire qu'un fait passé, présent ou à
  venir est probable, c'est dire qu'une proposition est probable.'' The point was
  emphasised by Boole, \textit{Laws of Thought}, pp.\ 7~and~167. See also Czuber,
  \textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ p.~5, and Stumpf, \textit{Über den Begriff der mathematischen
  Wahrscheinlichkeit}.}

\Paragraph{5.} These general ideas are not likely to provoke much
criticism. In the ordinary course of thought and argument,
we are constantly assuming that knowledge of one statement,
while not \emph{proving} the truth of a second, yields nevertheless
\emph{some ground} for believing it. We assert that we \emph{ought} on the
evidence to prefer such and such a belief. We claim rational
grounds for assertions which are not conclusively demonstrated.
We allow, in fact, that statements may be unproved, without, for
that reason, being unfounded. And it does not seem on reflection
that the information we convey by these expressions is wholly
subjective. When we argue that Darwin gives valid grounds
for our accepting his theory of natural selection, we do not simply
mean that we are psychologically inclined to agree with him;
it is certain that we also intend to convey our belief that
we are acting rationally in regarding his theory as probable.
We believe that there is some real objective relation
between Darwin's evidence and his conclusions, which is independent
of the mere fact of our belief, and which is just as real
and objective, though of a different degree, as that which would
exist if the argument were as demonstrative as a syllogism.
We are claiming, in fact, to cognise correctly a logical connection
between one set of propositions which we call our evidence and
which we suppose ourselves to know, and another set which we
call our conclusions, and to which we attach more or less weight
%% -----File: 017.png---Folio 6-------
\index{Probability, and relevant knowledge!mathematical}%
\index{Relation, of probability}%
according to the grounds supplied by the first. It is this type
of objective relation between sets of propositions---the type
which we claim to be correctly perceiving when we make such
assertions as these---to which the reader's attention must be
directed.

\Paragraph{6.} It is not straining the use of words to speak of this as the
relation of probability. It is true that mathematicians have
employed the term in a narrower sense; for they have often
confined it to the limited class of instances in which the relation
is adapted to an algebraical treatment. But in common usage
the word has never received this limitation.

Students of probability in the sense which is meant by the
authors of typical treatises on \textit{Wahrscheinlichkeitsrechnung} or
\textit{Calcul des probabilités}, will find that I do eventually reach topics
with which they are familiar. But in making a serious attempt
to deal with the fundamental difficulties with which all students
of mathematical probabilities have met and which are notoriously
unsolved, we must begin at the beginning (or almost at the
beginning) and treat our subject widely. As soon as mathematical
probability ceases to be the merest algebra or pretends
to guide our decisions, it immediately meets with problems
against which its own weapons are quite powerless. And even
if we wish later on to use probability in a narrow sense, it will
be well to know first what it means in the widest.

\Paragraph{7.} Between two sets of propositions, therefore, there exists
a relation, in virtue of which, if we know the first, we can attach
to the latter some degree of rational belief. This relation is the
subject-matter of the logic of probability.

A great deal of confusion and error has arisen out of a
failure to take due account of this \emph{relational} aspect of probability.
From the premisses ``$a$~implies~$b$'' and ``$a$~is true,'' we
can conclude something about~$b$---namely that $b$~is true---which
does not involve~$a$. But, if $a$ is so related to~$b$, that a knowledge
of it renders a probable belief in~$b$ rational, we cannot conclude
anything whatever about~$b$ which has not reference to~$a$; and it
is not true that every set of self-consistent premisses which
includes~$a$ has this same relation to~$b$. It is as useless, therefore,
to say ``$b$~is probable'' as it would be to say ``$b$~is equal,''
or ``$b$~is greater than,'' and as unwarranted to conclude that,
because $a$~makes $b$~probable, therefore $a$~and~$c$ together make $b$~probable,
%% -----File: 018.png---Folio 7-------
\index{Evidence, and measurement of Probability}%
\index{Probability, and relevant knowledge!dependent on evidence}%
as to argue that because $a$~is less than~$b$, therefore $a$~and~$c$
together are less than~$b$.

Thus, when in ordinary speech we name some opinion as
probable without further qualification, the phrase is generally
elliptical. We mean that it is probable when certain considerations,
implicitly or explicitly present to our minds at the moment,
are taken into account. We use the word for the sake of shortness,
just as we speak of a place as being three miles distant,
when we mean three miles distant from where we are then situated,
or from some starting-point to which we tacitly refer. No
proposition is in itself either probable or improbable, just as no
place can be intrinsically distant; and the probability of the
same statement varies with the evidence presented, which is,
as it were, its origin of reference. We may fix our attention
on our own knowledge and, treating this as our origin, consider
the probabilities of all other suppositions,---according to the
usual practice which leads to the elliptical form of common
speech; or we may, equally well, fix it on a proposed conclusion
and consider what degree of probability this would derive from
various sets of assumptions, which might constitute the \textit{corpus} of
knowledge of ourselves or others, or which are merely
hypotheses.

Reflection will show that this account harmonises with
familiar experience. There is nothing novel in the supposition
that the probability of a theory turns upon the evidence by which
it is supported; and it is common to assert that an opinion was
probable on the evidence at first to hand, but on further information
was untenable. As our knowledge or our hypothesis changes,
\index{Hypothesis}%
our conclusions have new probabilities, not in themselves, but
relatively to these new premisses. New logical relations have
now become important, namely those between the conclusions
which we are investigating and our new assumptions; but the
old relations between the conclusions and the former assumptions
still exist and are just as real as these new ones. It would be
as absurd to deny that an opinion \emph{was} probable, when at a later
stage certain objections have come to light, as to deny, when
we have reached our destination, that it was ever three miles
distant; and the opinion still \emph{is} probable in relation to the old
hypotheses, just as the destination is still three miles distant
from our starting-point.
%% -----File: 019.png---Folio 8-------
\index{Logic, academic!of probability}%
\index{Probability@{`\textit{Probability}'}}%
\index{Probability, and relevant knowledge!objective relation of}%
\index{Probability, and relevant knowledge!philosophical definition of}%
\index{Probability relation}%

\Paragraph{8.} A \emph{definition} of probability is not possible, unless it contents
us to define degrees of the probability-relation by reference to
degrees of rational belief. We cannot analyse the probability-relation
in terms of simpler ideas. As soon as we have passed
from the logic of implication and the categories of truth and
falsehood to the logic of probability and the categories of knowledge,
ignorance, and rational belief, we are paying attention to
a new logical relation in which, although it is logical, we were
not previously interested, and which cannot be explained or
defined in terms of our previous notions.

This opinion is, from the nature of the case, incapable of positive
proof. The presumption in its favour must arise partly
out of our failure to find a definition, and partly because the
notion presents itself to the mind as something new and independent.
If the statement that an opinion was probable on the
evidence at first to hand, but became untenable on further information,
is not solely concerned with psychological belief, I
do not know how the element of logical doubt is to be defined,
or how its substance is to be stated, in terms of the other
indefinables of formal logic. The attempts at definition, which
have been made hitherto, will be criticised in later chapters.
I do not believe that any of them accurately represent that particular
logical relation which we have in our minds when we
speak of the probability of an argument.

In the great majority of cases the term ``probable'' seems to
be used consistently by different persons to describe the same
concept. Differences of opinion have not been due, I think, to
a radical ambiguity of language. In any case a desire to reduce
the indefinables of logic can easily be carried too far. Even if
a definition is discoverable in the end, there is no harm in postponing
it until our enquiry into the object of definition is far
advanced. In the case of ``probability'' the object before the
mind is so familiar that the danger of misdescribing its qualities
through lack of a definition is less than if it were a highly abstract
entity far removed from the normal channels of thought.

\Paragraph{9.} This chapter has served briefly to indicate, though not
to define, the subject matter of the book. Its object has
been to emphasise the existence of \emph{a logical relation between two
sets of propositions} in cases where it is not possible to argue
demonstratively from one to the other. This is a contention
%% -----File: 020.png---Folio 9-------
of a most fundamental character. It is not entirely novel, but
has seldom received due emphasis, is often overlooked, and
sometimes denied. The view, that probability arises out of
the existence of a specific relation between premiss and conclusion,
depends for its acceptance upon a reflective judgment on the
true character of the concept. It will be our object to discuss,
under the title of Probability, the principal properties of this
relation. First, however, we must digress in order to consider
briefly what we mean by \emph{knowledge}, \emph{rational belief}, and \emph{argument}.
%% -----File: 021.png---Folio 10-------
\index{Belief, rational}%


\Chapter{II}{Probability in Relation to the Theory of Knowledge}
\index{Knowledge}%

\Paragraph{1.} \First{I do} not wish to become involved in questions of epistemology
to which I do not know the answer; and I am anxious to reach
as soon as possible the particular part of philosophy or logic
which is the subject of this book. But some explanation is
necessary if the reader is to be put in a position to understand
the point of view from which the author sets out; I will, therefore,
expand some part of what has been outlined or assumed
in the first chapter.

\Paragraph{2.} There is, first of all, the distinction between that part of
our belief which is rational and that part which is not. If a
man believes something for a reason which is preposterous or
for no reason at all, and what he believes turns out to be true for
some reason not known to him, he cannot be said to believe it
\emph{rationally}, although he believes it and it is in fact true. On the
other hand, a man may rationally believe a proposition to be
\emph{probable}, when it is in fact false. The distinction between
rational belief and mere belief, therefore, is not the same as the
distinction between true beliefs and false beliefs. The highest
degree of rational belief, which is termed \emph{certain} rational belief,
corresponds to \emph{knowledge}. We may be said to know a thing
when we have a certain rational belief in it, and \textit{vice versa}. For
reasons which will appear from our account of probable degrees
of rational belief in the following paragraph, it is preferable to
regard \emph{knowledge} as fundamental and to define \emph{rational belief} by
reference to it.

\Paragraph{3.} We come next to the distinction between that part of our
rational belief which is certain and that part which is only
probable. Belief, whether rational or not, is capable of degree.
The highest degree of rational belief, or rational certainty of
\index{Certainty}%
%% -----File: 022.png---Folio 11-------
\index{Belief, rational!degrees of}%
\index{Johnson, W. E.!propositions@{and propositions}|inote}%
\index{Probability, and relevant knowledge!three senses of}%
\index{Proposition, characterisation of!primary and secondary}%
belief, and its relation to knowledge have been introduced above.
What, however, is the relation to knowledge of \emph{probable} degrees
of rational belief?

The proposition (\emph{say},~$q$) that we \emph{know} in this case is not the
same as the proposition (\emph{say},~$p$) in which we have a probable
degree (\emph{say},~$\DPtypo{a}{\alpha}$) of rational belief. If the evidence upon which
we base our belief is~$h$, then what we \emph{know}, namely~$q$, is that
the proposition~$p$ bears the probability-relation of degree~$\DPtypo{a}{\alpha}$ to
the set of propositions~$h$; and this knowledge of ours justifies
us in a rational belief of degree~$\DPtypo{a}{\alpha}$ in the proposition~$p$. It will
be convenient to call propositions such as~$p$, which do not contain
assertions about probability-relations, ``primary propositions'';
and propositions such as~$q$, which assert the existence of a
probability-relation, ``secondary propositions.''\footnote
  {This classification of ``primary'' and ``secondary'' propositions was
  suggested to me by Mr.~W.~E. Johnson.}

\Paragraph{4.} Thus knowledge of a proposition always corresponds to
certainty of rational belief in it and at the same time to actual
truth in the proposition itself. We cannot know a proposition
unless it is in fact true. A probable degree of rational belief
in a proposition, on the other hand, arises out of knowledge of
some corresponding secondary proposition. A man may rationally
believe a proposition to be probable when it is in fact false,
if the secondary proposition on which he depends is true and
certain; while a man cannot rationally believe a proposition
to be probable even when it is in fact true, if the secondary
proposition on which he depends is not true. Thus rational
belief of whatever degree can only arise out of knowledge,
although the knowledge may be of a proposition secondary, in
the above sense, to the proposition in which the rational degree
of belief is entertained.

\Paragraph{5.} At this point it is desirable to colligate the three senses
in which the term \emph{probability} has been so far employed. In its
most fundamental sense, I think, it refers to the logical relation
between two sets of propositions, which in §\;4~of \Chapref{I}\@. I
have termed the probability-relation. It is with this that I shall
be mainly concerned in the greater part of this Treatise. Derivative
from this sense, we have the sense in which, as above, the
term \emph{probable} is applied to the degrees of rational belief arising
out of knowledge of secondary propositions which assert the
%% -----File: 023.png---Folio 12-------
\index{Acquaintance, direct}%
\index{Proposition, characterisation of!knowledge of}%
existence of probability-relations in the fundamental logical sense.
Further it is often convenient, and not necessarily misleading,
to apply the term \emph{probable} to the proposition which is the object
of the probable degree of rational belief, and which bears the
probability-relation in question to the propositions comprising
the evidence.

\Paragraph{6.} I turn now to the distinction between direct and indirect
knowledge---between that part of our rational belief which we
\index{Knowledge!direct and indirect}%
know directly and that part which we know by argument.

We start from things, of various classes, with which we have,
what I choose to call without reference to other uses of this term,
\emph{direct acquaintance}. Acquaintance with such things does not in
itself constitute knowledge, although knowledge arises out of
acquaintance with them. The most important classes of things
with which we have direct acquaintance are our own sensations,
which we may be said to \emph{experience}, the ideas or meanings, about
which we have thoughts and which we may be said to \emph{understand},
and facts or characteristics or relations of sense-data or meanings,
which we may be said to \emph{perceive};---experience, understanding,
and perception being three forms of direct acquaintance.

The objects of knowledge and belief---as opposed to the
objects of direct acquaintance which I term sensations, meanings,
and perceptions---I shall term \emph{propositions}.

Now our knowledge of propositions seems to be obtained in
two ways: directly, as the result of contemplating the objects
of acquaintance; and indirectly, \emph{by argument}, through perceiving
the probability-relation of the proposition, about which we seek
knowledge, to other propositions. In the second case, at any
rate at first, what we know is not the proposition itself but a
secondary proposition involving it. When we know a secondary
proposition involving the proposition $p$ as subject, we may be
said to have indirect knowledge \emph{about}~$p$.

Indirect knowledge about~$p$ may in suitable conditions lead
to rational belief in~$p$ of an appropriate degree. If this degree
is that of certainty, then we have not merely indirect knowledge
\emph{about}~$p$, but indirect knowledge \emph{of}~$p$.

\Paragraph{7.} Let us take examples of direct knowledge. From acquaintance
with a sensation of yellow I can pass directly to a
knowledge of the proposition ``I have a sensation of yellow.''
From acquaintance with a sensation of yellow and with the
%% -----File: 024.png---Folio 13-------
\index{Probability relation}%
\index{Proposition, characterisation of!primary and secondary}%
meanings of ``yellow,'' ``colour,'' ``existence,'' I may be able
to pass to a direct knowledge of the propositions ``I understand
\index{Knowledge!incomplete and proper}%
the meaning of yellow,'' ``my sensation of yellow exists,'' ``yellow
is a colour.'' Thus, by some mental process of which it is
difficult to give an account, we are able to pass from direct
acquaintance with things to a knowledge of propositions about
the things of which we have sensations or understand the
meaning.

Next, by the contemplation of propositions of which we have
direct knowledge, we are able to pass indirectly to knowledge of or
about other propositions. The mental process by which we pass
from direct knowledge to indirect knowledge is in some cases and
in some degree capable of analysis. We pass from a knowledge
of the proposition~$a$ to a knowledge about the proposition~$b$ by perceiving
a logical relation between them. With this logical relation
we have direct acquaintance. The logic of knowledge is
mainly occupied with a study of the logical relations, direct
acquaintance with which permits direct knowledge of the
secondary proposition asserting the probability-relation, and so
to indirect knowledge about, and in some cases of, the primary
proposition.

It is not always possible, however, to analyse the mental
process in the case of indirect knowledge, or to say by the perception
of \emph{what} logical relation we have passed from the knowledge
of one proposition to knowledge about another. But
although in some cases we \emph{seem} to pass directly from one proposition
to another, I am inclined to believe that in all legitimate
transitions of this kind some logical relation of the proper kind
must exist between the propositions, even when we are not
explicitly aware of it. In any case, whenever we pass to
knowledge about one proposition by the contemplation of it in
relation to another proposition of which we have knowledge---even
when the process is unanalysable---I call it an \emph{argument.}
\index{Argument}%
The knowledge, such as we have in ordinary thought by passing
from one proposition to another without being able to say what
logical relations, if any, we have perceived between them, may
be termed uncompleted knowledge. And knowledge, which
results from a distinct apprehension of the relevant logical
relations, may be termed knowledge proper.

\Paragraph{8.} In this way, therefore, I distinguish between direct and
%% -----File: 025.png---Folio 14-------
indirect knowledge, between that part of our rational belief which
\index{Knowledge!of logical relations}%
is based on direct knowledge and that part which is based on
argument. About what \emph{kinds} of things we are capable of knowing
propositions directly, it is not easy to say. About our
own existence, our own sense-data, some logical ideas, and some
logical relations, it is usually agreed that we have direct knowledge.
Of the law of gravity, of the appearance of the other
side of the moon, of the cure for phthisis, of the contents of
Bradshaw, it is usually agreed that we do \emph{not} have direct knowledge.
But many questions are in doubt. Of \emph{which} logical
ideas and relations we have direct acquaintance, as to whether
we can ever know directly the existence of \emph{other people}, and as
to when we are knowing propositions about sense-data directly
and when we are interpreting them---it is not possible to give
a clear answer. Moreover, there is another and peculiar kind
of derivative knowledge---by memory.
\index{Memory}%

At a given moment there is a great deal of our knowledge
which we know neither directly nor by argument---we remember
it. We may remember it as knowledge, but forget how we originally
knew it. What we once knew and now consciously remember,
can fairly be called knowledge. But it is not easy to
draw the line between conscious memory, unconscious memory
or habit, and pure instinct or irrational associations of ideas
(acquired or inherited)---the last of which cannot fairly be called
knowledge, for unlike the first two it did not even arise (in us at
least) out of knowledge. Especially in such a case as that of
what our eyes tell us, it is difficult to distinguish between the
different ways in which our beliefs have arisen. We cannot
always tell, therefore, what is remembered knowledge and what is
not knowledge at all; and when knowledge is remembered, we
do not always remember at the same time whether, originally, it
was direct or indirect.

Although it is with knowledge by argument that I shall be
mainly concerned in this book there is one kind of direct knowledge,
namely of secondary propositions, with which I cannot
help but be involved. In the case of every argument, it is only
directly that we can know the secondary proposition which makes
the argument itself valid and rational. When we know something
by argument this must be through direct acquaintance
with some logical relation between the conclusion and the premiss.
%% -----File: 026.png---Folio 15-------
\index{Bernoulli, Jac.|inote}%
\index{Fries|inote}%
\index{Laplace|inote}%
In \emph{all} knowledge, therefore, there is some direct element; and
logic can never be made purely mechanical. All it can do is
so to arrange the reasoning that the logical relations, which
have to be perceived directly, are made explicit and are of a
simple kind.

\Paragraph{9.} It must be added that the term \emph{certainty} is sometimes used
\index{Certainty!truth@{and truth}}%
in a merely psychological sense to describe a state of mind
without reference to the logical grounds of the belief. With
this sense I am not concerned. It is also used to describe the
highest degree of rational belief; and this is the sense relevant
to our present purpose. The peculiarity of certainty is that
knowledge of a secondary proposition involving certainty,
together with knowledge of what stands in this secondary
proposition in the position of evidence, leads to \emph{knowledge of},
and not merely \emph{about}, the corresponding primary proposition.
Knowledge, on the other hand, of a secondary proposition involving
a degree of probability lower than certainty, together
with knowledge of the premiss of the secondary proposition,
leads only to a \emph{rational belief of the appropriate degree} in the
primary proposition. The knowledge present in this latter case
I have called knowledge \emph{about} the primary proposition or conclusion
of the argument, as distinct from knowledge \emph{of} it.

Of probability we can say no more than that it is a lower degree
of rational belief than certainty; and we may say, if we like,
that it deals with degrees of certainty.\footnote
  {This view has often been taken, \eg, by Bernoulli and, incidentally, by
  Laplace; also by Fries (see Czuber, \textit{Entwicklung}, p.~12). The view, occasionally
  held, that probability is concerned with degrees of truth, arises out of a
  confusion between certainty and truth. Perhaps the Aristotelian doctrine
  that future events are neither true nor false arose in this way.}
Or we may make
probability the more fundamental of the two and regard certainty
as a special case of probability, as being, in fact, the \emph{maximum
probability}. Speaking somewhat loosely we may say that, if
our premisses make the conclusion certain, then it \emph{follows} from
the premisses; and if they make it very probable, then it very
nearly follows from them.

It is sometimes useful to use the term ``impossibility'' as
\index{Impossibility}%
the negative correlative of ``certainty,'' although the former
sometimes has a different set of associations. If $a$~is certain,
then the contradictory of~$a$ is impossible. If a knowledge of~$a$
makes $b$~certain, then a knowledge of~$a$ makes the contradictory
%% -----File: 027.png---Folio 16-------
\index{Belief, rational}%
\index{Modality and probability|inote}%
of~$b$ impossible. Thus a proposition is impossible with respect
to a given premiss, if it is disproved by the premiss; and the
relation of impossibility is the relation of minimum probability.\footnote
  {Necessity and Impossibility, in the senses in which these terms are used
  in the theory of Modality, seem to correspond to the relations of Certainty and
  Impossibility in the theory of probability, the other modals, which comprise
  the intermediate degrees of possibility, corresponding to the intermediate
  degrees of probability. Almost up to the end of the seventeenth century
  the traditional treatment of modals is, in fact, a primitive attempt to bring
  the relations of probability within the scope of formal logic.}

\Paragraph{10.} We have distinguished between rational belief and irrational
belief and also between rational beliefs which are certain in degree
and those which are only probable. Knowledge has been
distinguished according as it is direct or indirect, according as it
is of primary or secondary propositions, and according as it is
\emph{of} or merely \emph{about} its object.

In order that we may have a rational belief in a proposition~$p$
of the degree of certainty, it is necessary that one of two conditions
should be fulfilled---(i.)~that we know $p$ directly; or (ii.)~that
we know a set of propositions~$h$, and also know some secondary
proposition~$q$ asserting a certainty-relation between $p$~and~$h$.
In the latter case $h$~may include secondary as well as primary
propositions, but it is a necessary condition that all the propositions~$h$
should be \emph{known}. In order that we may have rational
belief in~$p$ of a lower degree of probability than certainty, it is
necessary that we know a set of propositions~$h$, and also know
some secondary proposition~$q$ asserting a probability-relation
between $p$~and~$h$.

In the above account one possibility has been ruled out. It
is assumed that we cannot have a rational belief in~$p$ of a degree
less than certainty except through knowing a secondary proposition
of the prescribed type. Such belief can only arise, that
is to say, by means of the perception of some probability-relation.
To employ a common use of terms (though one inconsistent with
the use adopted above), I have assumed that all direct knowledge
is certain. All knowledge, that is to say, which is obtained in a
manner strictly direct by contemplation of the objects of acquaintance
and without any admixture whatever of argument and the
contemplation of the logical bearing of any other knowledge on
this, corresponds to \emph{certain} rational belief and not to a merely
probable degree of rational belief. It is true that there do \emph{seem}
to be degrees of knowledge and rational belief, when the source of
%% -----File: 028.png---Folio 17-------
\index{Proposition, characterisation of!self-evident}%
\index{Relativity, of knowledge}%
the belief is solely in acquaintance, as there are when its source
is in argument. But I think that this appearance arises partly
out of the difficulty of distinguishing direct from indirect knowledge,
\index{Knowledge!probable and vague}%
\index{Knowledge!relativity of}%
and partly out of a confusion between \emph{probable} knowledge
and \emph{vague} knowledge. I cannot attempt here to analyse
the meaning of vague knowledge. It is certainly not the same
thing as knowledge proper, whether certain or probable, and
it does not seem likely that it is susceptible of strict logical
treatment. At any rate I do not know how to deal with it,
and in spite of its importance I will not complicate a difficult
subject by endeavouring to treat adequately the theory of vague
knowledge.

I assume then that only true propositions can be known,
that the term ``probable knowledge'' ought to be replaced by
the term ``probable degree of rational belief,'' and that a probable
degree of rational belief cannot arise directly but only as the
result of an argument, out of the knowledge, that is to say, of
a secondary proposition asserting some logical probability-relation
in which the object of the belief stands to some known
proposition. With arguments, if they exist, the \emph{ultimate} premisses
of which are known in some other manner than that
described above, such as might be called ``probable knowledge,''
my theory is not adequate to deal without modification.\footnote
  {I do not mean to imply, however, at any rate at present, that the ultimate
  premisses of an argument need always be \emph{primary} propositions.}

For the objects of certain belief which is based on direct
knowledge, as opposed to certain belief arising indirectly, there
is a well-established expression; propositions, in which our
rational belief is both certain and direct, are said to be
\emph{self-evident}.

\Paragraph{11.} In conclusion, the relativity of knowledge to the individual
may be briefly touched on. Some part of knowledge---knowledge
of our own existence or of our own sensations---is clearly relative
to individual experience. We cannot speak of knowledge
absolutely---only of the knowledge of a particular person. Other
parts of knowledge---knowledge of the axioms of logic, for example---may
seem more objective. But we must admit, I think,
that this too is relative to the constitution of the human mind,
and that the constitution of the human mind may vary in some
degree from man to man. What is self-evident to me and what
%% -----File: 029.png---Folio 18-------
I really know, may be only a probable belief to you, or may form
no part of your rational beliefs at all. And this may be true
not only of such things as \emph{my} existence, but of some logical axioms
also. Some men---indeed it is obviously the case---may have a
greater power of logical intuition than others. Further, the
difference between some kinds of propositions over which human
intuition seems to have power, and some over which it has none,
may depend wholly upon the constitution of our minds and
have no significance for a perfectly objective logic. We can no
more assume that all true secondary propositions are or ought
to be universally known than that all true primary propositions
are known. The perceptions of some relations of probability
may be outside the powers of some or all of us.

What we know and what probability we can attribute to our
rational beliefs is, therefore, subjective in the sense of being
relative to the individual. But given the body of premisses which
our subjective powers and circumstances supply to us, and given
the kinds of logical relations, upon which arguments can be based
and which we have the capacity to perceive, the conclusions,
which it is rational for us to draw, stand to these premisses in an
objective and wholly logical relation. Our logic is concerned
with drawing conclusions by a series of steps of certain specified
kinds from a \emph{limited} body of premisses.

With these brief indications as to the relation of Probability,
as I understand it, to the Theory of Knowledge, I pass from
problems of ultimate analysis and definition, which are not the
primary subject matter of this book, to the logical theory and
superstructure, which occupies an intermediate position between
the ultimate problems and the applications of the theory, whether
such applications take a generalised mathematical form or a
concrete and particular one. For this purpose it would only
encumber the exposition, without adding to its clearness or its
accuracy, if I were to employ the perfectly exact terminology
and minute refinements of language, which are necessary for the
avoidance of error in very fundamental enquiries. While taking
pains, therefore, to avoid any divergence between the substance
of this chapter and of those which succeed it, and to employ only
such periphrases as could be translated, \emph{if desired}, into perfectly
exact language, I shall not cut myself off from the convenient,
but looser, expressions, which have been habitually employed
%% -----File: 030.png---Folio 19-------
\index{Moore, G. E.}%
\index{Russell, Bertrand}%
by previous writers and have the advantage of being, in a general
way at least, immediately intelligible to the reader.\footnote
  {This question, which faces all contemporary writers on logical and philosophical
  subjects, is in my opinion much more a question of \emph{style}---and therefore
  to be settled on the same sort of considerations as other such questions---than
  is generally supposed. There are occasions for very exact methods of statement,
  such as are employed in Mr.~Russell's \textit{Principia Mathematica}. But there
  are advantages also in writing the English of Hume. Mr.~Moore has developed
  in \textit{Principia Ethica} an intermediate style which in his hands has force and
  beauty. But those writers, who strain after exaggerated precision without
  going the whole hog with Mr.~Russell, are sometimes merely pedantic. They
  lose the reader's attention, and the repetitious complication of their phrases
  eludes his comprehension, without their really attaining, to compensate,
  a complete precision. Confusion of thought is not always best avoided by
  technical and unaccustomed expressions, to which the mind has no immediate
  reaction of understanding; it is possible, under cover of a careful formalism,
  to make statements, which, if expressed in plain language, the mind would
  immediately repudiate. There is much to be said, therefore, in favour of
  understanding the substance of what you are saying \emph{all the time}, and of never
  reducing the substantives of your argument to the mental status of an $x$~or~$y$.}
%% -----File: 031.png---Folio 20-------
\index{Bentham, measurement of Probability}%
\index{Donkin, W. F.}%
\index{Forbes, J. D.|inote}%
\index{Probability, and relevant knowledge!measurement of|ifoll}%


\Chapter{III}{The Measurement of Probabilities}

\Paragraph{1.} \First{I have} spoken of probability as being concerned with \emph{degrees}
of rational belief. This phrase implies that it is in some sense
quantitative and perhaps capable of measurement. The theory
of probable arguments must be much occupied, therefore, with
\emph{comparisons} of the respective weights which attach to different
arguments. With this question we will now concern ourselves.

It has been assumed hitherto as a matter of course that
probability is, in the full and literal sense of the word, measurable.
I shall have to limit, not extend, the popular doctrine. But,
keeping my own theories in the background for the moment, I
will begin by discussing some existing opinions on the subject.

\Paragraph{2.} It has been sometimes supposed that a numerical comparison
between the degrees of any pair of probabilities is not only conceivable
but is actually within our power. Bentham, for instance,
in his \textit{Rationale of Judicial Evidence},\footnote
  {Book~i.\ chap~vi.\ (referred to by Venn).}
proposed a scale on which
witnesses might mark the degree of their certainty; and others
have suggested seriously a `barometer of probability.'\footnote
  {The reader may be reminded of Gibbon's proposal that:---``A Theological
  Barometer might be formed, of which the Cardinal (Baronius) and our countryman,
  Dr.~Middleton, should constitute the opposite and remote extremities,
  as the former sunk to the lowest degree of credulity, which was compatible with
  learning, and the latter rose to the highest pitch of scepticism, in any wise
  consistent with Religion.''}

That such comparison is \emph{theoretically possible}, whether or not
we are actually competent in every case to make the comparison,
has been the generally accepted opinion. The following quotation\footnote
  {W.~F. Donkin, \textit{Phil.~Mag.}, 1851. He is replying to an article by J.~D.
  Forbes (\textit{Phil.~Mag.}, Aug. 1849) which had cast doubt upon this opinion.}
puts this point of view very well:

``I do not see on what ground it can be doubted that every
%% -----File: 032.png---Folio 21-------
\index{De Morgan}%
\index{Forbes, J. D.}%
definite state of belief concerning a proposed hypothesis is in
itself capable of being represented by a numerical expression,
however difficult or impracticable it may be to ascertain its
actual value. It would be very difficult to estimate in numbers
the \textit{vis viva} of all of the particles of a human body at any instant;
but no one doubts that it is capable of numerical expression. I
mention this because I am not sure that Professor Forbes has
distinguished the difficulty of \emph{ascertaining numbers} in certain
cases from a supposed difficulty of \emph{expression by means of numbers}.
The former difficulty is real, but merely relative to our knowledge
and skill; the latter, if real, would be absolute and inherent in
the subject-matter, which I conceive is not the case.''

De~Morgan held the same opinion on the ground that, wherever
we have differences of degree, numerical comparison \emph{must} be
theoretically possible.\footnote
  {``Whenever the terms greater and less can be applied, there twice, thrice,
  etc., can be conceived, though not perhaps measured by us.''---``Theory of Probabilities,''
  \textit{Encyclopaedia Metropolitana}, p.~395. He is a little more guarded in
  his \textit{Formal Logic}, pp.\ 174,~175; but arrives at the same conclusion so far as
  probability is concerned.}
He assumes, that is to say, that all
probabilities can be placed in an \emph{order} of magnitude, and argues
from this that they must be measurable. Philosophers, however,
who are mathematicians, would no longer agree that, even if the
premiss is sound, the conclusion follows from it. Objects can
be arranged in an order, which we can reasonably call one of
degree or magnitude, without its being possible to conceive a
system of measurement of the differences between the individuals.

This opinion may also have been held by others, if not by
De~Morgan, in part because of the narrow associations which
Probability has had for them. The Calculus of Probability has
received far more attention than its logic, and mathematicians,
under no compulsion to deal with the whole of the subject, have
naturally confined their attention to those special cases, the existence
of which will be demonstrated at a later stage, where
algebraical representation is possible. Probability has become
associated, therefore, in the minds of theorists with those problems
in which we are presented with a number of exclusive and exhaustive
alternatives of equal probability; and the principles, which
are readily applicable in such circumstances, have been supposed,
without much further enquiry, to possess general validity.

\Paragraph{3.} It is also the case that theories of probability have been
%% -----File: 033.png---Folio 22-------
\index{Insurance}%
propounded and widely accepted, according to which its numerical
character is necessarily involved in the definition. It is often
said, for instance, that probability is the ratio of the number of
``favourable cases'' to the total number of ``cases.'' If this
definition is accurate, it follows that every probability can be
properly represented by a number and in fact \emph{is} a number; for
a ratio is not a quantity at all. In the case also of definitions
based upon statistical frequency, there must be by definition a
numerical ratio corresponding to every probability. These
definitions and the theories based on them will be discussed in
\Chapref{VIII}.; they are connected with fundamental differences
of opinion with which it is not necessary to burden the present
argument.

\Paragraph{4.} If we pass from the opinions of theorists to the experience
of practical men, it might perhaps be held that a presumption
in favour of the numerical valuation of all probabilities can be
based on the practice of underwriters and the willingness of
Lloyd's to insure against practically any risk. Underwriters are
actually willing, it might be urged, to name a numerical measure
in every case, and to back their opinion with money. But this
practice shows no more than that many probabilities are greater
or less than some numerical measure, not that they themselves
are numerically definite. It is sufficient for the underwriter if
the premium he names \emph{exceeds} the probable risk. But, apart
from this, I doubt whether in extreme cases the process of thought,
through which he goes before naming a premium, is wholly
rational and determinate; or that two equally intelligent brokers
acting on the same evidence would always arrive at the same
result. In the case, for instance, of insurances effected before
a Budget, the figures quoted must be partly arbitrary. There is
in them an element of caprice, and the broker's state of mind,
when he quotes a figure, is like a bookmaker's when he names
odds. Whilst he may be able to make sure of a profit, on the
principles of the bookmaker, yet the individual figures that make
up the book are, within certain limits, arbitrary. He may be
almost certain, that is to say, that there will not be new taxes on
more than one of the articles tea, sugar, and whisky; there
may be an opinion abroad, reasonable or unreasonable, that the
likelihood is in the order---whisky, tea, sugar; and he may,
therefore be able to effect insurances for equal amounts in each
%% -----File: 034.png---Folio 23-------
at $30$~per cent, $40$~per cent, and $45$~per cent. He has thus made
sure of a profit of $15$~per cent, however absurd and arbitrary his
quotations may be. It is not necessary for the success of underwriting
on these lines that the probabilities of these new taxes
are really measurable by the figures $\frac{3}{10}$,~$\frac{4}{10}$, and~$\frac{45}{100}$; it is sufficient
that there should be merchants willing to insure at these rates.
These merchants, moreover, may be wise to insure even if the
quotations are partly arbitrary; for they may run the risk of insolvency
unless their possible loss is thus limited. That the
transaction is in principle one of bookmaking is shown by the
fact that, if there is a specially large demand for insurance against
one of the possibilities, the rate rises;---the probability has not
changed, but the ``book'' is in danger of being upset. A Presidential
election in the United States supplies a more precise
example. On August~23, 1912, $60$~per cent was quoted at Lloyd's
to pay a total loss should Dr.~Woodrow Wilson be elected, $30$~per
cent should Mr.~Taft be elected, and $20$~per cent should Mr.~Roosevelt
be elected. A broker, who could effect insurances
in equal amounts against the election of each candidate, would be
certain at these rates of a profit of 10 per cent. Subsequent
modifications of these terms would largely depend upon the
number of applicants for each kind of policy. Is it possible to
maintain that these figures in any way represent reasoned
numerical estimates of probability?

In some insurances the arbitrary element seems even greater.
Consider, for instance, the reinsurance rates for the \textit{Waratah},
a vessel which disappeared in South African waters. The
lapse of time made rates rise; the departure of ships in search of
her made them fall; some nameless wreckage is found and they
rise; it is remembered that in similar circumstances thirty
years ago a vessel floated, helpless but not seriously damaged,
for two months, and they fall. Can it be pretended that the
figures which were quoted from day to day---$75$~per cent, $83$~per
cent, $78$~per cent---were rationally determinate, or that the
actual figure was not within wide limits arbitrary and due to
the caprice of individuals? In fact underwriters themselves
distinguish between risks which are properly insurable, either
because their probability can be estimated between comparatively
narrow numerical limits or because it is possible to make a ``book''
which covers all possibilities, and other risks which cannot be
%% -----File: 035.png---Folio 24-------
\index{Leibniz|inote}%
\index{Probability, and relevant knowledge!law@{and law}}%
dealt with in this way and which cannot form the basis of a regular
business of insurance,---although an occasional gamble may be
indulged in. I believe, therefore, that the practice of underwriters
weakens rather than supports the contention that all
probabilities can be measured and estimated numerically.

\Paragraph{5.} Another set of practical men, the lawyers, have been more
subtle in this matter than the philosophers.\footnote
  {Leibniz notes the subtle distinctions made by Jurisconsults between
  degrees of probability; and in the preface to a work, projected but unfinished,
  which was to have been entitled \textit{Ad stateram juris de gradibus probationum et
  probabilitatum} he recommends them as models of logic in contingent questions
  (Couturat, \textit{Logique de~Leibniz}, p.~240).}
A distinction,
interesting for our present purpose, between probabilities, which
can be estimated within somewhat narrow limits, and those which
cannot, has arisen in a series of judicial decisions respecting
damages. The following extract\footnote
  {I have considerably compressed the original report (Sapwell \textit{v.}~Bass).}
from the \textit{Times Law Reports}
seems to me to deal very clearly in a mixture of popular and legal
phraseology, with the logical point at issue:

This was an action brought by a breeder of racehorses to
recover damages for breach of a contract. The contract was
that Cyllene, a racehorse owned by the defendant, should in the
season of the year~1909 serve one of the plaintiff's brood
mares. In the summer of~1908 the defendant, without the consent
of the plaintiff, sold Cyllene for~£30,000 to go to South
America. The plaintiff claimed a sum equal to the average
profit he had made through having a mare served by Cyllene
during the past four years. During those four years he had
had four colts which had sold at~£3300. Upon that basis his
loss came to 700~guineas.

Mr.~Justice Jelf said that he was desirous, if he properly
could, to find some mode of legally making the defendant compensate
the plaintiff; but the question of damages presented
formidable and, to his mind, insuperable difficulties. The
damages, if any, recoverable here must be either the estimated
loss of profit or else nominal damages. The estimate could only
be based on a succession of contingencies. Thus it was assumed
that (\textit{inter alia}) Cyllene would be alive and well at the time of the
intended service; that the mare sent would be well bred and not
barren; that she would not slip her foal; and that the foal would
be born alive and healthy. In a case of this kind he could only
%% -----File: 036.png---Folio 25-------
rely on the weighing of chances; and the law generally regarded
damages which depended on the weighing of chances as too
remote, and therefore irrecoverable. It was drawing the line
between an estimate of damage based on probabilities, as in
``Simpson \textit{v.}\ L.~and~N.W. Railway Co.''\ (1,~Q.B.D.,~274), where
Cockburn,~C.J., said: ``To some extent, no doubt, the damage
must be a matter of speculation, but that is no reason for not
awarding any damages at all,'' and a claim for damages of a
totally problematical character. He (Mr.~Justice Jelf) thought
the present case was well over the line. Having referred to
``Mayne on Damages'' (8th~ed., p.~70), he pointed out that
in ``Watson \textit{v.}\ Ambergah Railway Co.''\ (15,~Jur.,~448) Patteson,~J.,
seemed to think that the chance of a prize might be taken into
account in estimating the damages for breach of a contract to
send a machine for loading barges by railway too late for a show;
but Erle,~J., appeared to think such damage was too remote.
In his Lordship's view the chance of winning a prize was not of
sufficiently ascertainable value at the time the contract was made
to be within the contemplation of the parties. Further, in the
present case, the contingencies were far more numerous and
uncertain. He would enter judgment for the plaintiff for nominal
damages, which were all he was entitled to. They would be
assessed at~1s.

One other similar case may be quoted in further elucidation
of the same point, and because it also illustrates another point---the
importance of making clear the assumptions relative to which
the probability is calculated. This case\footnote
  {Chaplin \textit{v.}\ Hicks (1911).}
arose out of an offer of
a Beauty Prize\footnote
  {The prize was to be a theatrical engagement and, according to the article,
  \DPtypo{he}{the} probability of subsequent marriage into the peerage.}
by the \textit{Daily Express}. Out of $6000$ photographs
submitted, a number were to be selected and published in the
newspaper in the following manner:

The United Kingdom was to be divided into districts and the
photographs of the selected candidates living in each district were
to be submitted to the readers of the paper in the district, who
were to select by their votes those whom they considered the
most beautiful, and a Mr.~Seymour Hicks was then to make an
appointment with the $50$~ladies obtaining the greatest number
of votes and himself select $12$ of them. The plaintiff, who came
%% -----File: 037.png---Folio 26-------
out head of one of the districts, submitted that she had not been
given a reasonable opportunity of keeping an appointment, that
she had thereby lost the value of her chance of one of the $12$~prizes,
and claimed damages accordingly. The jury found that
the defendant had not taken reasonable means to give the
plaintiff an opportunity of presenting herself for selection, and
assessed the damages, provided they were capable of assessment,
at~£100, the question of the possibility of assessment being postponed.
This was argued before Mr.~Justice Pickford, and subsequently
in the Court of Appeal before Lord Justices Vaughan
Williams, Fletcher Moulton, and Harwell. Two questions arose---relative
to what evidence ought the probability to be calculated,
and was it numerically measurable? Counsel for the
defendant contended that, ``if the value of the plaintiff's chance
was to be considered, it must be the value as it stood at the beginning
of the competition, not as it stood after she had been selected
as one of the~$50$. As $6000$ photographs had been sent in, and there
was also the personal taste of the defendant as final arbiter to
be considered, the value of the chance of success was really incalculable.''
The first contention that she ought to be considered
as one of~$6000$ not as one of~$50$ was plainly preposterous and did
not hoodwink the court. But the other point, the personal
taste of the arbiter, presented more difficulty. In estimating
the chance, ought the Court to receive and take account of
evidence respecting the arbiter's preferences in types of beauty?
Mr.~Justice Pickford, without illuminating the question, held that
the damages were capable of estimation. Lord Justice Vaughan
Williams in giving judgment in the Court of Appeal argued as
follows:

As he understood it, there were some $50$~competitors, and
there were $12$~prizes of equal value, so that the average chance
of success was about one in four. It was then said that the
questions which might arise in the minds of the persons who had
to give the decisions were so numerous that it was impossible to
apply the doctrine of averages. He did not agree. Then it
was said that if precision and certainty were impossible in any
case it would be right to describe the damages as unassessable.
He agreed that there might be damages so unassessable that the
doctrine of averages was not possible of application because the
figures necessary to be applied were not forthcoming. Several
%% -----File: 038.png---Folio 27-------
cases were to be found in the reports where it had been so held,
but he denied the proposition that because precision and certainty
had not been arrived at, the jury had no function or duty to
determine the damages\ldots. He (the Lord Justice) denied that
the mere fact that you could not assess with precision and certainty
relieved a wrongdoer from paying damages for his breach of
duty. He would not lay down that in every case it could be left
to the jury to assess the damages; there were cases where the
loss was so dependent on the mere unrestricted volition of another
person that it was impossible to arrive at any assessable loss
from the breach. It was true that there was no market here;
the right to compete was personal and could not be transferred.
He could not admit that a competitor who found herself one of
50 could have gone into the market and sold her right to compete.
At the same time the jury might reasonably have asked themselves
the question whether, if there was a right to compete, it
could have been transferred, and at what price. Under these
circumstances he thought the matter was one for the jury.

The attitude of the Lord Justice is clear. The plaintiff had
evidently suffered damage, and justice required that she should
be compensated. But it was equally evident, that, relative to
the completest information available and account being taken of
the arbiter's personal taste, the probability could be by no means
estimated with numerical precision. Further, it was impossible
to say how much weight ought to be attached to the fact that
the plaintiff had been \emph{head} of her district (there were \emph{fewer} than
$50$~districts); yet it was plain that it made her chance \emph{better} than
the chances of those of the $50$ left in, who were not head of their
districts. Let rough justice be done, therefore. Let the case
be simplified by ignoring some part of the evidence. The
``doctrine of averages'' is then applicable, or, in other words,
the plaintiff's loss may be assessed at twelve-fiftieths of the
value of the prize.\footnote
  {The jury in assessing the damages at~£100, however, cannot have argued
  so subtly as this; for the average value of a prize (I have omitted the details
  bearing on their value) could not have been fairly estimated so high as~£400.}

\Paragraph{6.} How does the matter stand, then? Whether or not such
a thing is theoretically conceivable, no exercise of the practical
judgment is possible, by which a numerical value can actually
be given to the probability of every argument. So far from
%% -----File: 039.png---Folio 28-------
\index{Laplace|inote}%
\index{Probability, and relevant knowledge!similarity@{and similarity}}%
our being able to measure them, it is not even clear that we are
always able to place them in an order of magnitude. Nor has
any theoretical rule for their evaluation ever been suggested.

The doubt, in view of these facts, whether any two probabilities
are in every case even theoretically capable of comparison
in terms of numbers, has not, however, received serious consideration.
There seems to me to be exceedingly strong reasons for
entertaining the doubt. Let us examine a few more instances.

\Paragraph{7.} Consider an induction or a generalisation. It is usually
held that each additional instance increases the generalisation's
probability. A conclusion, which is based on three experiments
in which the unessential conditions are varied, is more trustworthy
than if it were based on two. But what reason or
principle can be adduced for attributing a numerical measure to
the increase?\footnote
  {It is true that Laplace and others (even amongst contemporary writers)
  have believed that the probability of an induction is measurable by means of a
  formula known as the \emph{rule of succession}, according to which the probability of an
  induction based on $n$~instances is~$\dfrac{n+1}{n+2}$. Those who have been convinced by
  the reasoning employed to establish this rule must be asked to postpone judgment
  until it has been examined in \Chapref{XXX}\@. But we may point out here
  the absurdity of supposing that the odds are $2$~to~$1$ in favour of a generalisation
  based on a single instance---a conclusion which this formula would seem to
  justify.}

Or, to take another class of instances, we may sometimes
have some reason for supposing that one object belongs to a
certain category if it has points of similarity to other known
members of the category (\eg\ if we are considering whether
a certain picture should be ascribed to a certain painter), and
the greater the similarity the greater the probability of our
conclusion. But we cannot in these cases \emph{measure} the increase;
we can say that the presence of certain peculiar marks in a
picture increases the probability that the artist of whom those
marks are known to be characteristic painted it, but we cannot
say that the presence of these marks makes it two or three or
any other number of times more probable than it would have
been without them. We can say that one thing is more like a
second object than it is like a third; but there will very seldom be
any meaning in saying that it is twice as like. Probability is, so
far as measurement is concerned, closely analogous to similarity.\footnote
  {There are very few writers on probability who have explicitly admitted
  that probabilities, though in some sense quantitative, may be incapable of
  numerical comparison. Edgeworth, ``Philosophy of Chance'' (\textit{Mind}, 1884, p.~225),
\index{Edgeworth|inote}%
\index{Goldschmidt|inote}%
  admitted that ``there may well be important quantitative, although not
  numerical, estimates'' of probabilities. Goldschmidt (\textit{Wahrscheinlichkeitsrechnung},
  p.~43) may also be cited as holding a somewhat similar opinion. He
  maintains that a lack of comparability in the grounds often stands in the way
  of the measurability of the probable in ordinary usage, and that there are not
  necessarily good reasons for measuring the value of one argument against
  that of another. On the other hand, a numerical statement for the degree of the
  probable, although generally impossible, is not in itself contradictory to the
  notion; and of three statements, relating to the same circumstances, we can
  well say that one is more probable than another, and that one is the most
  probable of the three.}
%% -----File: 040.png---Folio 29-------

Or consider the ordinary circumstances of life. We are out
for a walk---what is the probability that we shall reach home
alive? Has this always a numerical measure? If a thunderstorm
bursts upon us, the probability is less than it was before;
but is it changed by some definite numerical amount? There
might, of course, be data which would make these probabilities
numerically comparable; it might be argued that a knowledge
of the statistics of death by lightning would make such a comparison
possible. But if such information is not included within
the knowledge to which the probability is referred, this fact is
not relevant to the probability actually in question and cannot
affect its value. In some cases, moreover, where general statistics
are available, the numerical probability which might be derived
from them is inapplicable because of the presence of additional
knowledge with regard to the particular case. Gibbon calculated
\index{Gibbon}%
his prospects of life from the volumes of vital statistics
and the calculations of actuaries. But if a doctor had been called
to his assistance the nice precision of these calculations would
have become useless; Gibbon's prospects would have been better
or worse than before, but he would no longer have been able to
calculate to within a day or week the period for which he then
possessed an even chance of survival.

In these instances we can, perhaps, arrange the probabilities
in an order of magnitude and assert that the new datum
strengthens or weakens the argument, although there is no
basis for an estimate \emph{how much} stronger or weaker the new
argument is than the old. But in another class of instances is
it even possible to arrange the probabilities in an \emph{order} of magnitude,
or to say that one is the greater and the other less?

\Paragraph{8.} Consider three sets of experiments, each directed towards
establishing a generalisation. The first set is more numerous;
%% -----File: 041.png---Folio 30-------
in the second set the irrelevant conditions have been more
carefully varied; in the third case the generalisation in view
is wider in scope than in the others. Which of these generalisations
is on such evidence the most probable? There is, surely,
no answer; there is neither equality nor inequality between
them. We cannot always weigh the analogy against the induction,
or the scope of the generalisation against the bulk of the
evidence in support of it. If we have \emph{more} grounds than
before, comparison is possible; but, if the grounds in the two
cases are quite different, even a comparison of more and less,
let alone numerical measurement, may be impossible.

This leads up to a contention, which I have heard supported,
that, although not all measurements and not all comparisons of
probability are within our power, yet we can say in the case of
every argument whether it is \emph{more} or \emph{less} likely than not. Is our
expectation of rain, when we start out for a walk, always \emph{more}
likely than not, or \emph{less} likely than not, or \emph{as} likely as not? I am
prepared to argue that on some occasions \emph{none} of these alternatives
hold, and that it will be an arbitrary matter to decide for or
against the umbrella. If the barometer is high, but the clouds are
black, it is not always rational that one should prevail over the
other in our minds, or even that we should balance them,---though
it will be rational to allow caprice to determine us and
to waste no time on the debate.

\Paragraph{9.} Some cases, therefore, there certainly are in which no
rational basis has been discovered for numerical comparison. It
is not the case here that the method of calculation, prescribed
by theory, is beyond our powers or too laborious for actual
application. \emph{No} method of calculation, however impracticable,
has been suggested. Nor have we any \textit{prima facie} indications of
the existence of a common unit to which the magnitudes of all
probabilities are naturally referrible. A degree of probability
is not composed of some homogeneous material, and is not
apparently divisible into parts of like character with one
another. An assertion, that the magnitude of a given probability
is in a numerical ratio to the magnitude of every
other, seems, therefore, unless it is based on one of the current
\emph{definitions} of probability, with which I shall deal separately
in later chapters, to be altogether devoid of the kind of support,
which can usually be supplied in the case of quantities of which
%% -----File: 042.png---Folio 31-------
the mensurability is not open to denial. It will be worth
while, however, to pursue the argument a little further.

\Paragraph{10.}  There appear to be four alternatives. Either in some
cases there is no probability at all; or probabilities do not all
belong to a single set of magnitudes measurable in terms of a
common unit; or these measures always exist, but in many
cases are, and \emph{must remain}, unknown; or probabilities do
belong to such a set and their measures are \emph{capable} of being
determined by us, although we are not always able so to
determine them in practice.

\Paragraph{11.}  Laplace and his followers excluded the first two alternatives.
\index{Laplace}%
They argued that every conclusion has its place in
the numerical range of probabilities from $0$~to~$1$, \emph{if only we knew
it}, and they developed their theory of \emph{unknown} probabilities.

In dealing with this contention, we must be clear as to what
we mean by saying that a probability is \emph{unknown}. Do we mean
unknown through lack of skill in arguing from given evidence,
or unknown through lack of evidence? The first is alone
admissible, for new evidence would give us a new probability,
not a fuller knowledge of the old one; we have not discovered
the probability of a statement on given evidence, by determining
its probability in relation to quite different evidence. We must
not allow the theory of unknown probabilities to gain plausibility
from the second sense. A relation of probability does not yield
us, as a rule, information of much value, unless it invests the
conclusion with a probability which lies between narrow numerical
limits. In ordinary practice, therefore, we do not always regard
ourselves as \emph{knowing} the probability of a conclusion, unless we
can estimate it numerically. We are apt, that is to say, to
restrict the use of the expression \emph{probable} to these numerical
examples, and to allege in other cases that the probability is
unknown. We might say, for example, that we do not know,
when we go on a railway journey, the probability of death in a
railway accident, unless we are told the statistics of accidents
in former years; or that we do not know our chances in a lottery,
unless we are told the number of the tickets. But it must be
clear upon reflection that if we use the term in this sense,---which
is no doubt a perfectly legitimate sense,---we ought to say that
in the case of some arguments a relation of probability does not
exist, and not that it is unknown. For it is not \emph{this} probability
%% -----File: 043.png---Folio 32-------
that we have discovered, when the accession of new evidence
makes it possible to frame a numerical estimate.

Possibly this theory of unknown probabilities may also gain
strength from our practice of estimating arguments, which, as
I maintain, have \emph{no} numerical value, by reference to those that
have. We frame two ideal arguments, that is to say, in which
the general character of the evidence largely resembles what is
actually within our knowledge, but which is so constituted as
to yield a numerical value, and we judge that the probability of
the actual argument lies between these two. Since our standards,
therefore, are referred to numerical measures in many cases
where actual measurement is impossible, and since the probability
lies \emph{between} two numerical measures, we come to believe that it
must also, if only we knew it, possess such a measure itself.

\Paragraph{12.} To say, then, that a probability is unknown ought to
mean that it is unknown to us through our lack of skill in arguing
from given evidence. The evidence justifies a certain degree of
knowledge, but the weakness of our reasoning power prevents our
knowing what this degree is. At the best, in such cases, we only
know \emph{vaguely} with what degree of probability the premisses invest
the conclusion. That probabilities can be unknown in this sense
or known with less distinctness than the argument justifies,
is clearly the case. We can through stupidity fail to make any
estimate of a probability at all, just as we may through the
same cause estimate a probability wrongly. As soon as we
distinguish between the degree of belief which it is rational to
entertain and the degree of belief actually entertained, we have
in effect admitted that the true probability is \emph{not} known to
everybody.

But this admission must not be allowed to carry us too far.
Probability is, \textit{vide} \Chapref{II}. (§\;12), relative in a sense to the
principles of \emph{human} reason. The degree of probability, which
it is rational for \emph{us} to entertain, does not presume perfect logical
insight, and is relative in part to the secondary propositions
which we in fact know; and it is not dependent upon whether
more perfect logical insight is or is not conceivable. It is the
degree of probability to which those logical processes lead, of
which our minds are capable; or, in the language of \Chapref{II}.,
which those secondary propositions justify, which we in fact know.
If we do not take this view of probability, if we do not limit it
%% -----File: 044.png---Folio 33-------
in this way and make it, to this extent, relative to human
powers, we are altogether adrift in the unknown; for we cannot
ever know what degree of probability would be justified by the
perception of logical relations which we are, and must always be,
incapable of comprehending.

\Paragraph{13.} Those who have maintained that, where we cannot assign
a numerical probability, this is not because there is none, but
simply because we do not know it, have really meant, I feel
sure, that with some addition to our knowledge a numerical
value would be assignable, that is to say that our conclusions
would have a numerical probability relative to \emph{slightly different}
premisses. Unless, therefore, the reader clings to the opinion
that, in every one of the instances I have cited in the earlier
paragraphs of this chapter, it is theoretically possible on \emph{that}
evidence to assign a numerical value to the probability, we are
left with the first two of the alternatives of §\;10, which were
as follows: either in some cases there is no probability at all;
or probabilities do not all belong to a single set of magnitudes
measurable in terms of a common unit. It would be difficult to
maintain that there is \emph{no} logical relation whatever between
our premiss and our conclusion in those cases where we cannot
assign a numerical value to the probability; and if this is so,
it is really a question of whether the logical relation has characteristics,
other than mensurability, of a kind to justify us in
calling it a probability-relation. Which of the two we favour is,
therefore, partly a matter of definition. We might, that is to
say, pick out from probabilities (in the widest sense) a set, if there
is one, all of which are measurable in terms of a common unit,
and call the members of this set, and them only, probabilities (in
the narrow sense). To restrict the term `probability' in this
way would be, I think, very inconvenient. For it is possible,
as I shall show, to find \emph{several} sets, the members of each of
which are measurable in terms of a unit common to all the
members of that set; so that it would be in some degree
arbitrary\footnote
  {Not altogether; for it would be natural to select the set to which the
  relation of certainty belongs.}
which we chose. Further, the distinction between
probabilities, which would be thus measurable and those which
would not, is not fundamental.

At any rate I aim here at dealing with probability in its
%% -----File: 045.png---Folio 34-------
\index{Measurement of Probability}%
\index{Probability, and relevant knowledge!comparison of}%
widest sense, and am averse to confining its scope to a limited
type of argument. If the opinion that not all probabilities can
be measured seems paradoxical, it may be due to this divergence
from a usage which the reader may expect. Common usage,
even if it involves, as a rule, a flavour of numerical measurement,
does not \emph{consistently} exclude those probabilities which are incapable
of it. The confused attempts, which have been made,
to deal with numerically indeterminate probabilities under the
title of unknown probabilities, show how difficult it is to
confine the discussion within the intended limits, if the original
definition is too narrow.

\Paragraph{14.} I maintain, then, in what follows, that there are some pairs
of probabilities between the members of which \emph{no} comparison
of magnitude is possible; that we can say, nevertheless, of some
pairs of relations of probability that the one is greater and the
other less, although it is not possible to measure the difference
between them; and that in a very special type of case, to be
dealt with later, a meaning can be given to a \emph{numerical} comparison
of magnitude. I think that the results of observation, of which
examples have been given earlier in this chapter, are consistent
with this account.

By saying that not all probabilities are measurable, I mean
that it is not possible to say of every pair of conclusions, about
which we have some knowledge, that the degree of our rational
belief in one bears any numerical relation to the degree of our
rational belief in the other; and by saying that not all probabilities
are comparable in respect of more and less, I mean that
it is not always possible to say that the degree of our rational
belief in one conclusion is either equal to, greater than, or less
than the degree of our belief in another.

We must now examine a philosophical theory of the quantitative
properties of probability, which would explain and
justify the conclusions, which reflection discovers, if the preceding
discussion is correct, in the practice of ordinary argument. We
must bear in mind that our theory must apply to all probabilities
and not to a limited class only, and that, as we do not adopt a
definition of probability which presupposes its numerical mensurability,
we cannot directly argue from differences in degree
to a numerical measurement of these differences. The problem
is subtle and difficult, and the following solution is, therefore,
%% -----File: 046.png---Folio 35-------
\index{Evidence, and measurement of Probability}%
\index{Probability, and relevant knowledge!series of}%
\index{Relation, of probability!of `\textit{between}'}%
proposed with hesitation; but I am strongly convinced that
something resembling the conclusion here set forth is true.

\Paragraph{15.} The so-called magnitudes or degrees of knowledge or
probability, in virtue of which one is greater and another less,
really arise out of an \emph{order} in which it is possible to place them.
Certainty, impossibility, and a probability, which has an intermediate
value, for example, constitute an ordered series in which
the probability lies \emph{between} certainty and impossibility. In the
same way there may exist a second probability which lies \emph{between}
certainty and the first probability. When, therefore, we say that
one probability is greater than another, this precisely means that
the degree of our rational belief in the first case lies \emph{between}
certainty and the degree of our rational belief in the second case.

On this theory it is easy to see why comparisons of more
and less are not always possible. They exist between two probabilities,
only when they and certainty all lie on the same ordered
series. But if more than one distinct series of probabilities
\index{Series of probabilities}%
exist, then it is clear that only those, which belong to the \emph{same}
series, can be compared. If the attribute `greater' as applied
to one of two terms arises solely out of the relative order of the
terms in a series, then comparisons of greater and less must
always be possible between terms which are members of the
same series, and can never be possible between two terms which
are not members of the same series. Some probabilities are not
comparable in respect of more and less, because there exists
more than one path, so to speak, between proof and disproof,
between certainty and impossibility; and neither of two probabilities,
which lie on independent paths, bears to the other and
to certainty the relation of `between' which is necessary for
quantitative comparison.

If we are comparing the probabilities of two arguments,
where the conclusion is the same in both and the evidence of
one exceeds the evidence of the other by the inclusion of some
fact which is favourably relevant, in such a case a relation seems
clearly to exist between the two in virtue of which one lies
\emph{nearer} to certainty than the other. Several types of argument
can be instanced in which the existence of such a relation is
equally apparent. But we cannot assume its presence in every
case or in comparing in respect of more and less the probabilities
of every pair of arguments.
%% -----File: 047.png---Folio 36-------
\index{Probability, and relevant knowledge!similarity@{and similarity}}%

\Paragraph{16.} Analogous instances are by no means rare, in which, by a
convenient looseness, the phraseology of quantity is misapplied
in the same manner as in the case of probability. The simplest
example is that of colour. When we describe the colour of
one object as bluer than that of another, or say that it has more
green in it, we do not mean that there are quantities blue and
green of which the object's colour possesses more or less; we
mean that the colour has a certain position in an order of colours
and that it is nearer some standard colour than is the colour
with which we compare it.

Another example is afforded by the cardinal numbers. We
say that the number three is greater than the number two, but
we do not mean that these numbers are quantities one of which
possesses a greater magnitude than the other. The one is
greater than the other by reason of its position in the order of
numbers; it is further distant from the origin zero. One number
is greater than another if the second number lies \emph{between} zero
and the first.

But the closest analogy is that of similarity. When we say
of three objects $A$,~$B$, and~$C$ that $B$~is more like~$A$ than $C$~is, we
mean, not that there is any respect in which $B$~is in itself quantitatively
greater than~$C$, but that, if the three objects are placed
in an order of similarity, $B$~is nearer to~$A$ than $C$~is. There are
also, as in the case of probability, \emph{different} orders of similarity.
For instance, a book bound in blue morocco is more like a book
bound in red morocco than if it were bound in blue calf; and a
book bound in red calf is more like the book in red morocco than
if it were in blue calf. But there may be no comparison between
the degree of similarity which exists between books bound in
red morocco and blue morocco, and that which exists between
books bound in red morocco and red calf. This illustration
deserves special attention, as the analogy between orders of
similarity and probability is so great that its apprehension will
greatly assist that of the ideas I wish to convey. We say
that one argument is more probable than another (\ie\ nearer to
certainty) in the same kind of way as we can describe one object
as more like than another to a standard object of comparison.

\Paragraph{17.} Nothing has been said up to this point which bears on
the question whether probabilities are ever capable of \emph{numerical}
comparison. It is true of some types of ordered series that
%% -----File: 048.png---Folio 37-------
\index{Addition, of probabilities}%
\index{Probability, and relevant knowledge!measurement of}%
there are measurable relations of distance between their members
as well as order, and that the relation of one of its members
to an `origin' can be numerically compared with the relation
of another member to the same origin. But the legitimacy of
such comparisons must be matter for special enquiry in each
case.

It will not be possible to explain in detail how and in what
sense a meaning can sometimes be given to the numerical measurement
of probabilities until \Partref{II}\@. is reached. But this chapter
will be more complete if I indicate briefly the conclusions at
which we shall arrive later. It will be shown that a process
of compounding probabilities can be defined with such properties
that it can be conveniently called a process of \emph{addition}. It will
sometimes be the case, therefore, that we can say that one
probability~$C$ is equal to the \emph{sum} of two other probabilities $A$~and~$B$,
\ie~$C=A+B$. If in such a case $A$~and~$B$ are equal, then
we may write this $C=2A$ and say that $C$~is double~$A$\@. Similarly
if $D=C+A$, we may write $D=3A$, and so on. We can attach a
meaning, therefore, to the equation $P=n· A$, where $P$~and~$A$ are
relations of probability, and $n$~is a number. The relation of
certainty has been commonly taken as the unit of such conventional
measurements. Hence if $P$~represents certainty,
we should say, in ordinary language, that the magnitude of the
probability~$A$ is~$\frac{1}{n}$. It will be shown also that we can define a
process, applicable to probabilities, which has the properties of
arithmetical multiplication. Where numerical measurement is
possible, we can in consequence perform algebraical operations
of considerable complexity. The attention, out of proportion
to their real importance, which has been paid, on account of the
opportunities of mathematical manipulation which they afford,
to the limited class of numerical probabilities, seems to be
a part explanation of the belief, which it is the principal object
of this chapter to prove erroneous, that \emph{all} probabilities must
belong to it.

\Paragraph{18.} We must look, then, at the quantitative characteristics of
probability in the following way. Some sets of probabilities
we can place in an ordered series, in which we can say of any
pair that one is nearer than the other to certainty,---that the
argument in one case is nearer proof than in the other, and that
there is more reason for one conclusion than for the other. But
%% -----File: 049.png---Folio 38-------
we can only build up these ordered series in special cases. If we
are given two distinct arguments, there is no general presumption
that their two probabilities and certainty can be placed
in an order. The burden of establishing the existence of such
an order lies on us in each separate case. An endeavour will
be made later to explain in a systematic way how and in
what circumstances such orders can be established. The
argument for the theory here proposed will then be strengthened.
For the present it has been shown to be agreeable to common
sense to suppose that an order exists in some cases and not in
others.

\Paragraph{19.} Some of the principal properties of ordered series of
probabilities are as follows:
\begin{Subpars}
\item[(i.)] Every probability lies on a path between impossibility
and certainty; it is always true to say of a degree
of probability, which is not identical either with
impossibility or with certainty, that it lies \emph{between}
them. Thus certainty, impossibility and \emph{any} other
degree of probability form an ordered series. This
is the same thing as to say that every argument
amounts to proof, or disproof, or occupies an intermediate
position.

\item[(ii.)] A path or series, composed of degrees of probability,
is not in general compact. It is not necessarily true,
that is to say, that any pair of probabilities in the
same series have a probability between them.

\item[(iii.)] The same degree of probability can lie on more than
one path (\ie~can belong to more than one series).
Hence, if $B$~lies between $A$~and~$C$, and also lies between
$A'$~and~$C'$ it does not follow that of $A$~and~$A'$ either lies
between the other and certainty. The fact, that the
same probability can belong to more than one distinct
series, has its analogy in the case of similarity.

\item[(iv.)] If $ABC$ forms an ordered series, $B$~lying between $A$~and~$C$,
and $BCD$~forms an ordered series, $C$~lying between
$B$~and~$D$, then $ABCD$ forms an ordered series, $B$~lying
between $A$~and~$D$.
\end{Subpars}

\Paragraph{20.} The different series of probabilities and their mutual relations
\index{Probability, and relevant knowledge!series of}%
\index{Series of probabilities}%
can be most easily pictured by means of a diagram. Let us
represent an ordered series by points lying upon a path, all the
%% -----File: 050.png---Folio 39-------
points on a given path belonging to the same series. It follows
from~(i.)\ that the points $O$~and~$I$, representing the relations of
impossibility and certainty, lie on every path, and that all paths
lie wholly between these points. It follows from~(iii.)\ that the
same point can lie on more than one path. It is possible, therefore,
for paths to intersect and cross. It follows from~(iv.)\ that
the probability represented by a given point is greater than that
represented by any other point which can be reached by passing
along a path with a motion constantly towards the point of
impossibility, and less than that represented by any point which
can be reached by moving along a path towards the point of
certainty. As there are independent paths there will be some
pairs of points representing relations of probability such that we
cannot reach one by moving from the other along a path always
in the same direction.

These properties are illustrated in the annexed diagram,
$O$~represents impossibility, $I$~certainty, and $A$~a numerically
measurable probability intermediate
between $O$~and~$I$; $U$,~$V$,~$W$,
$X$,~$Y$,~$Z$ are non-numerical
probabilities, of which, however,
$V$~is less than the numerical
\begin{wrapfigure}{r}{2.5in}%[illustration]
  \includegraphics[width=2.5in]{./images/050.pdf}
\end{wrapfigure}
probability~$A$, and is also less
than $W$,~$X$, and~$Y$\@. $X$~and~$Y$
are both greater than~$W$, and greater than~$V$, but are not
comparable with one another, or with~$A$\@. $V$~and~$Z$ are both
less than $W$,~$X$, and~$Y$, but are not comparable with one
another; $U$~is not quantitatively comparable with any of the
probabilities $V$,~$W$, $X$,~$Y$,~$Z$\@. Probabilities which are numerically
comparable will all belong to one series, and the path of this
series, which we may call the numerical path or strand, will be
represented by~$OAI$.

\Paragraph{21.} The chief results which have been reached so far are
collected together below, and expressed with precision:---
\begin{Subpars}
\item[(i.)] There are amongst degrees of probability or rational
belief various sets, each set composing an ordered
series. These series are ordered by virtue of a relation
of `between.' If $B$~is `between' $A$~and~$C$, $ABC$~form a
series.

\item[(ii.)] There are two degrees of probability $O$ and $I$ \emph{between}
\index{Relation, of probability!of `\textit{between}'}%
%% -----File: 051.png---Folio 40-------
which \emph{all} other probabilities lie. If, that is to say, $A$~is
a probability, $OAI$~form a series. $O$~represents impossibility
and $I$~certainty.

\item[(iii.)] If $A$~lies between $O$~and~$B$, we may write this~$\widehat{AB}$,
so that $\widehat{OA}$~and~$\widehat{AI}$ are true for all probabilities.

\item[(iv.)] If~$\widehat{AB}$, the probability~$B$ is said to be greater than
the probability~$A$, and this can be expressed by~$B>A$.

\item[(v.)] If the conclusion~$a$ bears the relation of probability~$P$
to the premiss~$h$, or if, in other words, the hypothesis~$h$
invests the conclusion~$a$ with probability~$P$, this may
be written~$aPh$. It may also be written~$a/h=P$.
\end{Subpars}

This latter expression, which proves to be the more useful of the
two for most purposes, is of fundamental importance. If $aPh$
and~$a'Ph'$, \ie~if the probability of $a$~relative to~$h$ is the
same as the probability of $a'$~relative to~$h'$, this may be written
$a/h=a'/h'$. The value of the symbol~$a/h$, which represents
what is called by other writers `the probability of~$a$,' lies in
the fact that it contains explicit reference to the \textit{data} to which
the probability relates the conclusion, and avoids the numerous
errors which have arisen out of the omission of this reference.
%% -----File: 052.png---Folio 41-------
\index{Bernoulli, Jac.}%


\Chapter{IV}{The Principle of Indifference}

\begin{Quote}
\textsc{Absolute}. `Sure, Sir, this is not very reasonable, to summon my affection
for a lady I know nothing of.'

\textsc{Sir Anthony}. `I am sure, Sir, 'tis more unreasonable in you to object
to a lady you know nothing of.'\footnote
  {Quoted by Mr.~Bosanquet with reference to the Principle of Non-Sufficient
  Reason.}
\end{Quote}

\Paragraph{1.} \First{In} the last chapter it was assumed that in some cases the
probabilities of two arguments may be \emph{equal}. It was also argued
that there are other cases in which one probability is, in some
sense, greater than another. But so far there has been nothing
to show \emph{how} we are to know when two probabilities are equal or
unequal. The recognition of equality, when it exists, will be
dealt with in this chapter, and the recognition of inequality in
the next. An historical account of the various theories about
this problem, which have been held from time to time, will be
given in \Chapref{VII}.

\Paragraph{2.} The determination of equality between probabilities has
received hitherto much more attention than the determination
of inequality. This has been due to the stress which has been
laid on the mathematical side of the subject. In order that
numerical measurement may be possible, we must be given a
number of \emph{equally} probable alternatives. The discovery of a
rule, by which equiprobability could be established, was, therefore,
\index{Equiprobability}%
essential. A rule, adequate to the purpose, introduced by
James Bernoulli, who was the real founder of mathematical
probability,\footnote
  {See also \Chapref[Chap.]{VII}.}
has been widely adopted, generally under the
title of \emph{The Principle of Non-Sufficient Reason}, down to the
\index{Principle of Non-Sufficient Reason}%
present time. This description is clumsy and unsatisfactory,
and, if it is justifiable to break away from tradition, I prefer to
call it \emph{The Principle of Indifference}.
%% -----File: 053.png---Folio 42-------
\index{Kries, von}%

The Principle of Indifference asserts that if there is no \emph{known}
\index{Principle of Indifference}%
reason for predicating of our subject one rather than another of
several alternatives, then relatively to such knowledge the
assertions of each of these alternatives have an \emph{equal} probability.
Thus \emph{equal} probabilities must be assigned to each of several
arguments, if there is an absence of positive ground for assigning
\emph{unequal} ones.

This rule, as it stands, may lead to paradoxical and even
contradictory conclusions. I propose to criticise it in detail,
and then to consider whether any valid modification of it is
discoverable. For several of the criticisms which follow I am
much indebted to Von Kries's \textit{Die Principien der Wahrscheinlichkeit}.\footnote
  {Published in 1886. A brief account of Von Kries's principal conclusions
  will be given on \Pageref{87}. A useful summary of his book will be found in a review
  by Meinong, published in the \textit{Göttingische gelehrte Anzeigen} for 1890 (pp.~56--75).}

\Paragraph{3.} If every probability was necessarily either greater than,
equal to, or less than any other, the Principle of Indifference
would be plausible. For if the evidence affords no ground for
attributing unequal probabilities to the alternative predications,
it seems to follow that they must be equal. If, on the other hand,
there need be neither equality nor inequality between probabilities,
this method of reasoning fails. Apart, however, from
this objection, which is based on the arguments of \Chapref{III}.,
the plausibility of the principle will be most easily shaken by an
exhibition of the contradictions which it involves. These fall
under three or four distinct heads. In §§\;4--9 my criticism will
be purely destructive, and I shall not attempt in these paragraphs
to indicate my own way out of the difficulties.

\Paragraph{4.} Consider a proposition, about the subject of which we know
only the meaning, and about the truth of which, as applied to
this subject, we possess no external relevant evidence. It has
been held that there are here two exhaustive and exclusive
alternatives---the truth of the proposition and the truth of its
contradictory---while our knowledge of the subject affords no
ground for preferring one to the other. Thus if $a$~and~$\bar a$ are
contradictories, about the subject of which we have no outside
knowledge, it is inferred that the probability of each is~$\frac{1}{2}$.\footnote
  {Cf.\ (\eg)\ the well-known passage in Jevons's \textit{Principles of Science}, vol.~i.\
\index{Jevons!equiprobability@{and equiprobability}|inote}%
  p.~243, in which he assigns the probability~$\frac{1}{2}$ to the proposition ``A Platythliptic
  Coefficient is positive.'' Jevons points out, by way of proof, that no other
  probability could reasonably be given. This, of course, involves the assumption
  that every proposition must have some numerical probability. Such a contention
  was first criticised, so far as I am aware, by Bishop Terrot in the \textit{Edin.\
  Phil.\ Trans.}\ for 1856. It was deliberately rejected by Boole in his last published
  work on probability: ``It is a plain consequence,'' he says (\textit{Edin.\ Phil.\
  Trans.}\ vol.~xxi.\ p.~624), ``of the logical theory of probabilities, that the state
  of expectation which accompanies entire ignorance of an event is properly
  represented, not by the fraction~$\frac{1}{2}$, but by the indefinite form~$\frac{0}{0}$.''  Jevons's
  particular example, however, is also open to the objection that we do not even
  know the \emph{meaning} of the subject of the proposition. Would he maintain that
  there is any sense in saying that for those who know no Arabic the probability
  of every statement expressed in Arabic is even? How far has he been
  influenced in the choice of his example by known characteristics of the predicate
  `positive'? Would he have assigned the probability~$\frac{1}{2}$ to the proposition
  `A Platythliptic Coefficient is a perfect cube'? What about the proposition
  `A Platythliptic Coefficient is allogeneous'?}
In
%% -----File: 054.png---Folio 43-------
\index{Boole|inote}%
\index{Terrot, Bishop|inote}%
the same way the probabilities of two other propositions, $b$~and~$c$,
having the same subject as~$a$, may be each~$\frac{1}{2}$. But without
having any evidence bearing on the subject of these propositions
we may know that the predicates are contraries amongst themselves,
and, therefore, exclusive alternatives---a supposition which
leads by means of the same principle to values inconsistent with
those just obtained. If, for instance, having no evidence relevant
to the colour of this book, we could conclude that $\frac{1}{2}$~is the probability
of `This book is red,' we could conclude equally that the
probability of each of the propositions `This book is black' and
`This book is blue' is also~$\frac{1}{2}$. So that we are faced with the
impossible case of \emph{three} exclusive alternatives all as likely as not.
A defender of the Principle of Indifference might rejoin that we
are assuming knowledge of the proposition: `Two different
colours cannot be predicated of the same subject at the same
time'; and that, if we know this, it constitutes relevant outside
evidence. But such evidence is about the predicate, not
about the subject. Thus the defender of the Principle will be
driven on, either to confine it to cases where we know nothing
about either the subject or the predicate, which would be to
emasculate it for all practical purposes, or else to revise and
amplify it, which is what we propose to do ourselves.

The difficulty cannot be met by saying that we must know
and take account of the \emph{number} of possible contraries. For the
number of contraries to any proposition on any evidence is always
infinite; $\bar ab$~is contrary to~$a$ for all values of~$b$. The same point
can be put in a form which does not involve contraries or
contradictories.  For example, $a/h=\frac{1}{2}$ and $ab/h=\frac{1}{2}$, if $h$~is
%% -----File: 055.png---Folio 44-------
\index{Kries, von|inote}%
\index{Stumpf|inote}%
irrelevant both to~$a$ and to~$b$, in the sense required by the crude
Principle of Indifference.\footnote
  {$a/h$ stands for `the probability of~$a$ on hypothesis~$h$.'}
It follows from this that, if $a$~is true,
$b$~must be true also. If it follows from the absence of positive
\textit{data} that `$A$~is a red book' has a probability of~$\frac{1}{2}$, and that the
probability of `$A$~is red' is also~$\frac{1}{2}$, then we may deduce that, if
$A$~is red, it must certainly be a book.

We may take it, then, that the probability of a proposition,
about the subject of which we have no extraneous evidence, is
\emph{not} necessarily~$\frac{1}{2}$. Whether or not this conclusion discredits the
Principle of Indifference, it is important on its own account, and
will help later on to confute some famous conclusions of Laplace's
\index{Laplace!school of}%
school.

\Paragraph{5.} Objection can now be made in a somewhat different shape.
Let us suppose as before that there is no positive evidence relating
to the subjects of the propositions under examination which
would lead us to discriminate in any way between certain
alternative predicates. If, to take an example, we have no
information whatever as to the area or population of the
countries of the world, a man is as likely to be an inhabitant
of Great Britain as of France, there being no reason to prefer
one alternative to the other.\footnote
  {This example raises a difficulty similar to that raised by Von Kries's
  example of the meteor. Stumpf has propounded an invalid solution of Von
  Kries's difficulty. Against the example proposed here, Stumpf's solution has
  less plausibility than against Von Kries's.}
He is also as likely to be an
inhabitant of Ireland as of France. And on the same principle
he is as likely to be an inhabitant of the British Isles as of
France. And yet these conclusions are plainly inconsistent.
For our first two propositions together yield the conclusion
that he is twice as likely to be an inhabitant of the British
Isles as of France.

Unless we argue, as I do not think we can, that the knowledge
that the British Isles are composed of Great Britain and Ireland
is a ground for supposing that a man is more likely to inhabit
them than France, there is no way out of the contradiction. It
is not plausible to maintain, when we are considering the relative
populations of different areas, that the number of \emph{names} of subdivisions
which are within our knowledge, is, in the absence of
any evidence as to their size, a piece of relevant evidence.

At any rate, many other similar examples could be invented,
%% -----File: 056.png---Folio 45-------
\index{Kries, von|inote}%
\index{Nitsche, A.|inote}%
which would require a special explanation in each case; for the
above is an instance of a perfectly general difficulty. The
possible alternatives may be $a$,~$b$,~$c$, and~$d$, and there may be no
means of discriminating between them; but equally there may
be no means of discriminating between ($a$~or~$b$), $c$, and~$d$.
This difficulty could be made striking in a variety of ways, but
it will be better to criticise the principle further from a somewhat
different side.

\Paragraph{6.} Consider the specific volume of a given substance.\footnote
  {This example is taken from Von Kries, \textit{op.~cit.} p.~24. Von Kries does
  not seem to me to explain correctly how the contradiction arises.}
Let us
suppose that we know the specific volume to lie between $1$~and~$3$,
but that we have no information as to whereabouts in this interval
its exact value is to be found. The Principle of Indifference
would allow us to assume that it is as likely to lie between $1$~and~$2$
as between $2$~and~$3$; for there is no reason for supposing that it
lies in one interval rather than in the other. But now consider
the specific density. The specific density is the reciprocal of
the specific volume, so that if the latter is~$v$ the former is~$\frac{1}{v}$.
Our \textit{data} remaining as before, we know that the specific density
must lie between $1$~and~$\frac{1}{3}$, and, by the same use of the Principle
of Indifference as before, that it is as likely to be between
$1$~and~$\frac{2}{3}$ as between $\frac{2}{3}$~and~$\frac{1}{3}$. But the specific volume being
a determinate function of the specific density, if the latter lies
between $1$~and~$\frac{2}{3}$, the former lies between $1$~and~$1\frac{1}{2}$, and if the
latter lies between $\frac{2}{3}$~and~$\frac{1}{3}$, the former lies between $1\frac{1}{2}$~and~$3$.
It follows, therefore, that the specific volume is as likely to lie
between $1$~and~$1\frac{1}{2}$ as between $1\frac{1}{2}$~and~$3$;
whereas we have already proved, relatively to precisely the same \textit{data}, that it is as likely
to lie between $1$~and~$2$ as between $2$~and~$3$. Moreover, any other
function of the specific volume would have suited our purpose
equally well, and by a suitable choice of this function we might
have proved in a similar manner that any division whatever
of the interval $1$~to~$3$ yields sub-intervals of equal probability.
Specific volume and specific density are simply alternative
methods of measuring the \emph{same} objective quantity; and there
are many methods which might be adopted, each yielding on the
application of the Principle of Indifference a different probability
for a given objective variation in the quantity.\footnote
  {A. Nitsche (``Die Dimensionen der Wahrscheinlichkeit und die Evidenz der
  Ungewissheit,'' \textit{Vierteljahrsschr.\ f.~wissensch. Philos.}\ vol.~xvi.\ p.~29, 1892), in
  criticising Von~Kries, argues that the alternatives to which the principle must
  be applied are the smallest \emph{physically} distinguishable intervals, and that the
  probability of the specific volume's lying within a certain range of values turns
  on the \emph{number} of such distinguishable intervals in the range. This procedure
  might conceivably provide the correct method of computation, but it does not
  therefore restore the credit of the Principle of Indifference. For it is argued,
  not that the results of applying the principle are always wrong, but that it does
  not lead unambiguously to the correct procedure. If we do not know the
  number of distinguishable intervals we have \emph{no} reason for supposing that the
  specific volume lies between $1$~and~$2$ rather than $2$~and~$3$, and the principle can
  therefore be applied as it has been applied above. And even if we do know
  the number and reckon intervals as equal which contain an equal number of
  `physically distinguishable' parts, is it certain that this does not simply
  provide us with a new system of measurement, which has the same conventional
  basis as the methods of specific volume and specific density, and is no
  more the one correct measure than these are?}
%% -----File: 057.png---Folio 46-------
\index{Kries, von|inote}%

The arbitrary nature of particular methods of measurement
of this and of many other physical quantities is easily explained.
The objective quality measured may not, strictly speaking, possess
numerical quantitativeness, although it has the properties necessary
for measurement by means of correlation with numbers.
The values which it can assume may be capable of being
ranged in an order, and it will sometimes happen that the series
which is thus formed is \emph{continuous}, so that a value can always
be found whose order in the series is between any two selected
values; but it does not follow from this that there is any meaning
in the assertion that one value is \emph{twice} another value. The
relations of continuous order can exist between the terms of a
series of values, without the relations of numerical quantitativeness
necessarily existing also, and in such cases we can adopt a
largely arbitrary measure of the successive terms, which yields
results which may be satisfactory for many purposes, those,
for instance, of mathematical physics, though not for those of
probability. This method is to select some other series of
quantities or numbers, each of the terms of which corresponds
in order to one and only one of the terms of the series which
we wish to measure\DPtypo{,}{.} For instance, the series of characteristics,
differing in degree, which are measured by specific
volume, have this relation to the series of numerical ratios
between the volumes of equal masses of the substances, the
specific volumes of which are in question, and of water. They
have it also to the corresponding ratios which give rise to the
measure of specific density. But these only yield conventional
measurements, and the numbers with which we correlate the
%% -----File: 058.png---Folio 47-------
\index{Borel|inote}%
\index{Crofton|inote}%
\index{Czuber|inote}%
\index{Lammel@{Lämmel}|inote}%
\index{Probability, and relevant knowledge!geometrical@{`\textit{geometrical}'}}%
terms which we wish to measure can be selected in a variety of
ways. It follows that equal intervals between the numbers
which represent the ratios do not necessarily correspond to equal
intervals between the qualities under measurement; for these
numerical differences depend upon which convention of measurement
we have selected.

\Paragraph{7.} A somewhat analogous difficulty arises in connection with
the problems of what is known as `geometrical' or `local'
probability.\footnote
  {The best accounts of this subject are to be found in Czuber, \textit{Geometrische
  Wahrscheinlichkeiten und Mittelwerte}; Czuber, \textit{Wahrscheinlichkeitsrechnung},
  vol.~i.\ pp.~75--109; Crofton, \textit{Encycl.\ Brit.}\ (9th~edit.), article `Probability';
  Borel, \textit{Eléments de la théorie des probabilités}, chaps.\ vi.--viii.; a few other
  references are given in the following pages, and a number of discussions of
  individual problems will be found in the mathematical volumes of the
  \textit{Educational Times}. The interest of the subject is primarily mathematical,
  and no discussion of its principal problems will be attempted here.}
In these problems we are concerned with the position
of a point or infinitesimal area or volume within a continuum.\footnote
  {As Czuber points out (\textit{Wahrscheinlichkeiterechnung}, vol.~i.\ p.~84), all
  problems, whether geometrical or arithmetical, which deal with a continuum
  and with non-enumerable aggregates, are commonly discussed under the name of
  `geometrical probability.' See also Lämmel, \textit{Untersuchungen}.}
\index{Geometrical probability}%
The number of cases here is indefinite, but the Principle
of Indifference has been held to justify the supposition that equal
lengths or areas or volumes of the continuum are, in the absence
of discriminating evidence, equally likely to contain the point.
It has long been known that this assumption leads in numerous
cases to contradictory conclusions. If, for instance, two points
$A$~and~$A'$ are taken at random on the surface of a sphere, and we
seek the probability that the lesser of the two arcs of the great
circle~$AA'$ is less than~$a$, we get one result by assuming that the
probability of a point's lying on a given portion of the sphere's
surface is proportional to the area of that portion, and another
result by assuming that, if a point lies on a given great circle, the
probability of its lying on a given arc of that circle is proportional
to the length of the arc, each of these assumptions being equally
justified by the Principle of Indifference.

Or consider the following problem: if a chord in a circle is
drawn at random, what is the probability that it will be less
than the side of the inscribed equilateral triangle. One can
argue:---

\begin{Subpars}
\item[(\textit{a})] It is indifferent at what point one end of the chord lies.
If we suppose this end fixed, the direction is then
%% -----File: 059.png---Folio 48-------
\index{Bertrand|inote}%
\index{Poincaré, Henri}%
\index{Probability, and relevant knowledge!geometrical@{`\textit{geometrical}'}}%
chosen at random. In this case the answer is easily
shown to be~$\frac{2}{3}$.

\item[(\textit{b})] It is indifferent in what direction we suppose the chord
to lie. Beginning with this apparently not less justifiable
assumption, we find that the answer is~$\frac{1}{2}$.

\item[(\textit{c})] To choose a chord at random, one must choose its
middle point at random. If the chord is to be less
than the side of the inscribed equilateral triangle, the
middle point must be at a greater distance from the
centre than half the radius. But the area at a
greater distance than this is $\frac{3}{4}$~of the whole. Hence
our answer is~$\frac{3}{4}$.\footnote
  {Bertrand, \textit{Calcul des probabilités}, p.~5.}
\end{Subpars}

In general, if $x$~and~$f(x)$ are both continuous variables, varying
always in the same or in the opposite sense, and $x$~must lie
between $a$~and~$b$, then the probability that $x$~lies between $c$~and~$d$,
where $a<c<d<b$, seems to be $\dfrac{d-c}{b-a}$, and the probability
that $f(x)$~lies between $f(c)$~and~$f(d)$ to be $\dfrac{f(d)-f(c)}{f(b)-f(a)}$. These
expressions, which represent the probabilities of necessarily
concordant conclusions, are not, as they ought to be, equal.\footnote
  {See (\eg)\ Borel, \textit{Éléments de la théorie des probabilités}, p.~85.}
\index{Borel}%

\Paragraph{8.} More than one attempt has been made to separate the
cases in which the Principle of Indifference can be legitimately
applied to examples of geometrical probability from those in
which it cannot. M.~Borel argues that the mathematician can
\emph{define} the geometrical probability that a point~$M$ lies on a certain
segment~$PQ$ of~$AD$ as proportional to the length of the segment,
but that this definition is \emph{conventional} until its consequences
have been confirmed \textit{à~posteriori} by their conformity with the
results of empirical observation. He points out that in actual
cases there are generally some considerations present which
lead us to prefer one of the possible assumptions to the others.
Whether or not this is so, the proposed procedure amounts to
an abandonment of the Principle of Indifference as a valid
criterion, and leaves our choice undetermined when further
evidence is not forthcoming.

M.~Poincaré, who also held that judgments of equiprobability
in such cases depend upon a `convention,' endeavoured to minimise
%% -----File: 060.png---Folio 49-------
the importance of the arbitrary element by showing that,
under certain conditions, the result is independent of the particular
convention which is chosen. Instead of assuming that the
point is equally likely to lie in every infinitesimal interval~$dx$
we may represent the probability of its lying in this interval by
the function~$\phi(x)\,dx$. M.~Poincaré showed that, in the game of
\textit{rouge et noir}, for instance, where we have a number of compartments
arranged in a circle coloured alternately black and white,
if we can assume that $\phi(x)$~is a regular function, continuous and
with continuous differential coefficients, then, whatever the
particular form of the function, the probability of black is
approximately equal to that of white.\footnote
  {Poincaré, \textit{Calcul des probabilités}, pp.~126 \textit{et seq}.}

Whether or not investigations on these lines prove to have
a practical value, they have not, I think, any theoretical importance.
If, as I maintain, the probability~$\phi(x)$ is not necessarily
numerical, it is not a generally justifiable assumption to
take its continuity for granted. We have, in the particular
example quoted, a number of alternatives, half of which lead to
black and half to white; the assumption of continuity amounts
to the assumption that for every white alternative there is a
black alternative whose probability is very nearly equal to that
of the white. Naturally in such a case we can get an approximately
equal probability for the whites as a whole and for the
blacks as a whole, without assuming equal probability for each
alternative individually. But this fact has no bearing on the
theoretical difficulties which we are discussing.

M.~Bertrand is so much impressed by the contradictions of
\index{Bertrand}%
geometrical probability that he wishes to exclude all examples
in which the number of alternatives is \emph{infinite}.\footnote
  {Bertrand, \textit{Calcul des probabilités}, p.~4: ``L'infini n'est pas un nombre;
  on ne doit pas, sans explication, l'introduire dans les raisonnements. La
  précision illusoire des mots pourrait faire naitre des contradictions. Choisir
  au hasard, entre un nombre infini de cas possibles, n'est pas une indication
  suffisante.''}
It will be argued
in the sequel that something resembling this is true. The discussion
of this question will be resumed in §§\;21--25.

\Paragraph{9.} There is yet another group of cases, distinct in character
from those considered so far, in which the principle does not
seem to provide us with unambiguous guidance. The typical
example is that of an urn containing black and white balls in an
%% -----File: 061.png---Folio 50-------
\index{Boole|inote}%
\index{Kries, von}%
\index{Nitsche, A.|inote}%
\index{Peirce|inote}%
\index{Stumpf|inote}%
unknown proportion.\footnote
  {The difficulty in question was first pointed out by Boole, \textit{Laws of Thought},
  pp.~369--370. After discussing the Law of Succession, Boole proceeds to show
  that ``there are other hypotheses, as strictly involving the principle of the
  `equal distribution of knowledge or ignorance' which would also conduct to
  conflicting results.'' See also Von Kries, \textit{op.\ cit\DPtypo{}{.}}\ pp.~31--34,~59, and Stumpf,
  \textit{Über den Begriff der mathematischen Wahrscheinlichkeit}, Bavarian Academy,
  1892, pp.~64--68.}
The Principle of Indifference can be
claimed to support the most usual hypothesis, namely, that all
possible numerical \emph{ratios} of black and white are equally probable.
But we might equally well assume that all possible \emph{constitutions}\footnote
  {If $A$~and~$B$ are two balls, $A$~white, $B$~black, and $A$~black, $B$~white, are
  different `constitutions.' But if we consider different numerical ratios, these
  two cases are indistinguishable, and count as one only.}
of the system of balls are equally probable, so that each individual
ball is assumed equally likely to be black or white. It would
follow from this that an approximately equal number of black
and white balls is more probable than a large excess of one colour.
On this hypothesis, moreover, the drawing of one ball and the
resulting knowledge of its colour leaves unaltered the probabilities
of the various possible constitutions of the rest of the bag;
whereas on the first hypothesis knowledge of the colour of one
ball, drawn and not replaced, manifestly alters the probability
of the colour of the next ball to be drawn. Either of these hypotheses
seems to satisfy the Principle of Indifference, and a believer
in the absolute validity of the principle will doubtless adopt that
one which enters his mind first.\footnote
  {C.~S.\ Peirce in his \textit{Theory of Probable Inference} (Johns Hopkins \textit{Studies in
  Logic}), pp.~172,~173, argues that the `constitution' hypothesis is alone valid,
  on the ground that, of the two hypotheses, only this one is consistent with itself.
  I agree with his conclusion, and shall give at the close of the chapter the fundamental
  considerations which lead to the rejection of the `ratio' hypothesis.
  Stumpf points out that the probability of drawing a white ball is, in any
  case,~$\frac{1}{2}$. This is true; but the probability of a second white clearly depends
  upon which of the two hypotheses has been preferred. Nitsche (\textit{loc.\ cit.}\ p.~31)
  seems to miss the point of the difficulty in the same way.}

The same point is very clearly illustrated by an example
which I take from Von Kries. Two cards, chosen from different
packs, are placed face downwards on the table; one is taken
up and found to be of a black suit: what is the chance that the
other is black also? One would naturally reply that the
chance is even. But this is based on the supposition, relatively
unpopular with writers on the subject, that every `constitution'
is equally probable, \ie~that each individual card is as likely
to be black as red. If we prefer this assumption, we must relinquish
%% -----File: 062.png---Folio 51-------
\index{Poisson|inote}%
the text-book theory that the drawing of a black ball from
an urn, containing black and white balls in unknown proportions,
affects our knowledge as to the proportion of black and white
amongst the remaining balls.

The alternative---or text-book---theory assumes that there
are three equal possibilities---one of each colour, both black, both
red. If both cards are black, we are twice as likely to turn up
a black card than if only one is black. \emph{After} we have turned up
a black, the probability that the other is black is, therefore, twice
as great as the probability that it is red. The chance of the
second's being black is therefore~$\frac{2}{3}$.\footnote
  {This is Poisson's solution, \textit{Recherches}, p.~96.}
The Principle of Indifference
has nothing to say against either solution. Until some further
criterion has been proposed we seem compelled to agree with
Poincaré that a preference for either hypothesis is wholly arbitrary.

\Paragraph{10.} Such, then, are the kinds of result to which an unguarded
use of the Principle of Indifference may lead us. The difficulties,
to which attention has been drawn, have been noticed before;
but the discredit has not been emphatically thrown on the
original source of error. Yet the principle certainly remains as
a \emph{negative} criterion; two propositions cannot be equally probable,
so long as there \emph{is} any ground for discriminating between them.
The principle is a necessary, but not, as it seems, a sufficient
condition.

The enunciation of some sufficient rule is certainly essential if
we are to make any progress in the subject. But the difficulty
of discovering a correct principle is considerable. This difficulty
is partly responsible, I think, for the doubts which philosophers
and many others have often felt regarding any practical application
of the Calculus. Many candid persons, when confronted
with the results of Probability, feel a strong sense of the uncertainty
of the logical basis upon which it seems to rest. It is
difficult to find an intelligible account of the meaning of `probability,'
or of how we are ever to determine the probability of any
particular proposition; and yet treatises on the subject profess
to arrive at complicated results of the greatest precision and the
most profound practical importance.

The incautious methods and exaggerated claims of the school
of Laplace have undoubtedly contributed towards the existence
\index{Laplace!school of}%
of these sentiments. But the general scepticism, which I believe
%% -----File: 063.png---Folio 52-------
\index{Probability relation!intuition of}%
\index{Psychology and probability}%
to be much more widely spread than the literature of the subject
admits, is more fundamental. In this matter Hume need not
\index{Hume}%
have felt ``affrighted and confounded with that forelorn solitude,
in which I am placed in my philosophy,'' or have fancied himself
``some strange uncouth monster, who not being able to mingle
and unite in society, has been expell'd all human commerce,
and left utterly abandon'd and disconsolate.'' In his views on
probability, he stands for the plain man against the sophisms
and ingenuities of ``metaphysicians, logicians, mathematicians,
and even theologians.''

Yet such scepticism goes too far. The judgments of probability,
upon which we depend for almost all our beliefs in matters
of experience, undoubtedly depend on a strong psychological
propensity in us to consider objects in a particular light. But
this is no ground for supposing that they are nothing more than
``lively imaginations.'' The same is true of the judgments in
virtue of which we assent to other logical arguments; and yet
in such cases we believe that there may be present some element
of objective validity, transcending the psychological impulsion,
with which primarily we are presented. So also in the case of
probability, we may believe that our judgments can penetrate
into the real world, even though their credentials are subjective.

\Paragraph{11.} We must now inquire how far it is possible to rehabilitate
the Principle of Indifference or find a substitute for it. There
are several distinct difficulties which need attention in a discussion
of the problems raised in the preceding paragraphs.
Our first object must be to make the Principle itself more precise
by disclosing how far its application is mechanical and how far
it involves an appeal to logical intuition.

\Paragraph{12.} Without compromising the objective character of relations
of probability, we must nevertheless admit that there is little
likelihood of our discovering a method of recognising particular
probabilities, without any assistance whatever from intuition or
direct judgment. Inasmuch as it is always assumed that we can
sometimes judge directly that a conclusion \emph{follows from} a premiss,
it is no great extension of this assumption to suppose that we
can sometimes recognise that a conclusion \emph{partially follows from},
or stands in a relation of probability to, a premiss. Moreover,
the failure to explain or define `probability' in terms of other
logical notions, creates a presumption that particular relations
%% -----File: 064.png---Folio 53-------
\index{Evidence, and measurement of Probability!relevant and irrelevant}%
\index{Principle of Indifference!analysis of}%
of probability must be, in the first instance, directly recognised
as such, and cannot be evolved by rule out of \textit{data} which themselves
contain no statements of probability.

On the other hand, although we cannot exclude every element
of direct judgment, these judgments may be limited and controlled,
perhaps, by logical rules and principles which possess a
general application. While we may possess a faculty of direct
recognition of many relations of probability, as in the case of
many other logical relations, yet some may be much more
easily recognisable than others. The object of a logical system
of probability is to enable us to know the relations, which
cannot be easily perceived, by means of other relations which
we can recognise more distinctly---to convert, in fact, vague
\index{Knowledge!vague and distinct}%
knowledge into more distinct knowledge.\footnote
  {As it is the aim of trigonometry to determine the position of an object,
  which is in a sense visible, not by a direct observation of it, but by observing
  some other object together with certain relations, so an indirect method of this
  kind is the aim of all logical system. If the truth of \emph{some} propositions, and the
  validity of \emph{some} arguments, could not be recognised directly, we could make no
  progress. We may have, moreover, some power of direct recognition where it
  is not necessary in our logical system that we should make use of it. In these
  cases the method of logical proof increases the certainty of knowledge, which
  we might be able to possess in a more doubtful manner without it. In other
  cases, that, for instance, of a complicated mathematical theorem, it enables
  us to know propositions to be true, which are altogether beyond the reach of
  our direct insight; just as we can often obtain knowledge about the position
  of a partially visible or even invisible object by starting with observations of
  other objects.}

\Paragraph{13.} Let us seek to distinguish between the element of direct
judgment and the element of mechanical rule in the Principle
of Indifference. The enunciation of this principle, as it is
ordinarily expressed, cloaks, but does not avoid, the former
element. It is in part a formula and in part an appeal to direct
inspection; but in addition to the obscurity and ambiguity of
the formula, the appeal to intuition is not as explicit as it should
be. The principle states that `there must be no known
reason for preferring one of a set of alternatives to any other.'
What does this mean? What are `reasons,' and how are
we to know whether they do or do not justify us in preferring
one alternative to another? I do not know any discussion
of Probability in which this question has been so much as
asked. If, for example, we are considering the probability
of drawing a black ball from an urn containing balls which are
%% -----File: 065.png---Folio 54-------
\index{Evidence, and measurement of Probability!relevant and irrelevant}%
\index{Relevance, judgments of}%
black and white, we assume that the difference of \emph{colour} between
the balls is not a reason for preferring either alternative.
But how do we know this, unless by a judgment that, on the
evidence in hand, our knowledge of the colours of the balls is
\emph{irrelevant} to the probability in question? We know of \emph{some}
respects in which the alternatives differ; but we judge that a
knowledge of \emph{these} differences is not relevant. If, on the other
hand, we were taking the balls out of the urn with a magnet,
and knew that the black balls were of iron and the white of tin,
we might regard the fact, that a ball was iron and not tin, as
very important in determining the probability of its being
drawn. Before, then, we can begin to apply the Principle of
Indifference, we must have made a number of direct judgments
\index{Judgments}%
to the effect that the probabilities under consideration are unaffected
by the inclusion in the evidence of certain particular
details. We have no right to say of any known difference
between the two alternatives that it is `no reason' for preferring
one of them, unless we have judged that a knowledge of this
difference is irrelevant to the probability in question.

\Paragraph{14.} A brief digression is now necessary, in order to introduce
some new terms. There are in general two principal types of
probabilities, the magnitudes of which we seek to compare,---those
in which the evidence is the same and the conclusions
different, and those in which the evidence is different but the
conclusion the same. Other types of comparison may be required,
but these two are by far the commonest. In the first
we compare the likelihood of two conclusions on given evidence;
in the second we consider what difference a change of evidence
makes to the likelihood of a given conclusion. In symbolic
language we may wish to compare $x/h$~with~$y/h$, or $x/h$~with~$x/h_1h$.
We may call the first type judgments of \emph{preference}, or,
when there is equality between $x/h$~and~$y/h$, of \emph{indifference}; and
the second type we may call judgments of \emph{relevance}, or, when there
is equality between $x/h$~and~$x/h_1h$, of \emph{irrelevance}. In the first
\index{Irrelevance!judgments of}%
we consider whether or not $x$~is to be preferred to~$y$ on evidence~$h$;
in the second we consider whether the addition of~$h_1$ to evidence~$h$
is relevant to~$x$.

The Principle of Indifference endeavours to formulate a rule
which will justify judgments of \emph{indifference}. But the rule that
there must be no ground for preferring one alternative to another,
%% -----File: 066.png---Folio 55-------
\index{Evidence, and measurement of Probability!independent and complementary}%
\index{Principle of Indifference!modification of}%
involves, if it is to be a guiding rule at all, and not a \textit{petitio
principii}, an appeal to judgments of \emph{irrelevance}.
\index{Irrelevance!definition of}%

The simplest definition of Irrelevance is as follows: $h_1$~is
irrelevant to~$x$ on evidence~$h$, if the probability of~$x$ on evidence~$hh_1$
is the same as its probability on evidence~$h$.\footnote
  {That is to say, $h_1$~is irrelevant to~$x/h$ if $x/h_1h = x/h$.}
But for a reason
which will appear in \Chapref{VI}., a stricter and more complicated
definition, as follows, is theoretically preferable: $h_1$~is irrelevant
to~$x$ on evidence~$h$, if there is no proposition, inferrible from~$h_1h$
but not from~$h$, such that its addition to evidence~$h$ affects the
probability of~$x$.\footnote
  {That is to say, $h_1$~is irrelevant to~$x/h$, if there is no propsition~$h'_1$ such that
  $h'_1/h_1h = 1$, $h'_1/h \neq 1$, and $x/h'_1h \neq x/h$.}
Any proposition which is irrelevant in the
strict sense is, of course, also irrelevant in the simpler sense;
but if we were to adopt the simpler definition, it would sometimes
occur that a part of evidence would be relevant, which taken as
a whole was irrelevant. The more elaborate definition by avoiding
this proves in the sequel more convenient. If the condition
$x/h_1h = x/h$ alone is satisfied, we may say that the evidence~$h_1$
is `irrelevant as a whole.'\footnote
  {Where no misunderstanding can arise, the qualification `as a whole' will
  be sometimes omitted.}

It will be convenient to define also two other phrases. $h_1$~and~$h_2$
are independent and complementary parts of the evidence,
if between them they make up~$h$ and neither can be inferred from
the other. If $x$~is the conclusion, and $h_1$~and~$h_2$ are independent
and complementary parts of the evidence, then $h_1$~is relevant if
the addition of it to~$h_2$ affects the probability of~$x$.\footnote
  {\Ie\ (in symbolism) $h_1$~and~$h_2$ are independent and complementary parts of~$h$
  if $h_1h_2 = h$, $h_1/h_2 \neq 1$, and $h_2/h_1 \neq 1$.  Also $h_1$~is relevant if $x/h \neq x/h_2$.}

Some propositions regarding irrelevance will be proved in
\Partref{II}\@. If $\bar h_1$~is the contradictory of~$h_1$ and $x/h_1h=x/h$, then
$x/\bar h_1h = x/h$. Thus the contradictory of irrelevant evidence is
also irrelevant. Also, if $x/yh = x/h$, it follows that $y/xh = y/h$.
Hence if, on initial evidence~$h$, $y$~is irrelevant to~$x$, then, on the
same initial evidence, $x$~is irrelevant to~$y$, \ie~if in a given state
of knowledge one occurrence has no bearing on another then
equally the second has no bearing on the first.

\Paragraph{15.} This distinction enables us to formulate the Principle \DPtypo{or}{of}
Indifference at any rate more precisely. There must be no
\emph{relevant} evidence relating to one alternative, unless there is
\emph{corresponding} evidence relating to the other; our relevant
%% -----File: 067.png---Folio 56-------
evidence, that is to say, must be symmetrical with regard to the
alternatives, and must be applicable to each in the same manner.
This is the rule at which the Principle of Indifference somewhat
obscurely aims. We must first determine what parts of our
evidence are relevant on the whole by a series of judgments of relevance,
not easily reduced to rule, of the type described above.
If this relevant evidence is \emph{of the same form} for both alternatives,
then the Principle authorises a judgment of indifference.

\Paragraph{16.} This rule can be expressed more precisely in symbolic
\index{Propositional function}%
language. Let us assume, to begin with, that the alternative
conclusions are expressible in the forms $\phi(a)$~and~$\phi(b)$, where
$\phi(x)$~is a propositional function.\footnote
  {If $\phi(a)$, $\phi(b)$, etc., are propositions, and $x$~is a variable, capable of taking
  the values $a$,~$b$, etc, then $\phi(x)$~is a propositional function.}
The difference between them,
that is to say, can be represented in terms of a single variable.

The Principle of Indifference is applicable to the alternatives
$\phi(a)$~and~$\phi(b)$, when the evidence~$h$ is so constituted that, if $f(a)$~is
an independent part of~$h$ (see §\;14) which is relevant to~$\phi(a)$,
and does not contain any independent parts which are irrelevant
to~$\phi(a)$, then $h$~includes~$f(b)$ also.

The rule can be extended by successive steps to cases in
which we have more than one variable. We can, if the necessary
conditions are fulfilled, successively compare the probabilities
of $\phi(a_1a_2)$~and~$\phi(b_1a_2)$, and of $\phi(b_1a_2)$~and~$\phi(b_1b_2)$ and establish
equality between $\phi(a_1a_2)$~and~$\phi(b_1b_2)$.

This elucidation is suited to most of the cases to which the
Principle of Indifference is ordinarily applied. Thus in the
favourite examples in which balls are drawn from urns, we can
infer from our evidence no relevant proposition about white balls,
such that we cannot infer a corresponding proposition about
black balls. Most of the examples, to which the mathematical
theory of chances has been applied, and which depend upon the
Principle of Indifference, can be arranged, I think, in the forms
which the rule requires as formulated above.

\Paragraph{17.} We can now clear up the difficulties which arose over the
group of cases dealt with in §\;9, the typical example of which was
the problem of the urn containing black and white balls in an
unknown proportion. This more precise enunciation of the
Principle enables us to show that of the two solutions the equiprobability
of each `constitution' is alone legitimate, and the
%% -----File: 068.png---Folio 57-------
\index{Evidence, and measurement of Probability!external}%
equiprobability of each numerical ratio erroneous. Let us write
the alternative `The proportion of black balls is~$x$' $\equiv\phi(x)$, and
the datum `There are $n$~balls in the bag, with regard to none
of which it is known whether they are black or white'~$\equiv h$.
On the `ratio' hypothesis it is argued that the Principle of
Indifference justifies the judgment of indifference, $\phi(x)/h=
\phi(y)/h$. In order that this may be valid, it must be possible to
state the relevant evidence in the form $f(x)\,f(y)$. But this is
not the case. If $x=\frac{1}{2}$ and~$y=\frac{1}{4}$, we have relevant knowledge
about the way in which a proportion of black balls of one half
can arise, which is not identical with our knowledge of the way
in which a proportion of one quarter can arise. If there are four
balls, $A$,~$B$, $C$,~$D$, one half are black, if $A$,~$B$ or $A$,~$C$ or $A$,~$D$ or
$B$,~$C$ or $B$,~$D$ or $C$,~$D$ are black; and one quarter are black,
if $A$~or $B$ or $C$ or~$D$ are black. These propositions are not identical
in form, and only by a false judgment of irrelevance can we
ignore them. On the `constitution' hypothesis, however,
where $A$,~$B$ black and $A$,~$C$ black are treated as distinct alternatives,
this want of symmetry in our relevant evidence cannot
arise.

\Paragraph{18.} We can also deal with the point which was illustrated by
the difficulty raised in §\;4. We considered there the probabilities
of~$a$ and its contradictory~$\bar a$ when there is no external evidence
relevant to either. What exactly do we mean by saying that
there is \emph{no} relevant evidence? Is the addition of the word
\emph{external} significant? If $a$~represents a particular proposition,
we must know something about it, namely, its \emph{meaning}. May
not the apprehension of its meaning afford us some relevant
evidence? If so, such evidence must not be excluded. If, then,
we say that there is \emph{no} relevant evidence, we must mean no
evidence beyond what arises from the mere apprehension of the
meaning of the symbol~$a$. If we attach \emph{no} meaning to the
symbol, it is useless to discuss the value of the probability; for
the probability, which belongs to a proposition as an object of
knowledge, not as a form of words, cannot in such a case exist.

What exactly does the symbol~$a$ stand for in the above?
Does it stand for any proposition of which we know no more
than that it is a proposition? Or does it stand for a particular
proposition which we understand but of which we know no more
than is involved in understanding it? In the former case we
%% -----File: 069.png---Folio 58-------
\index{Logic, academic!of implication}%
cannot extend our result to a proposition of which we know even
the meaning; for we should then know \emph{more} than that it is a
proposition; and in the latter case we cannot say what the
probability of~$a$ is as compared with that of its contradictory,
until we know \emph{what particular proposition} it stands for; for, as
we have seen, the proposition itself may supply relevant evidence.

This suggests that a source of much confusion may lie in the\Pagelabel{58}
use of symbols and the notion of variables in probability. In
\index{Variables in Probability}%
the logic of implication, which deals not with probability but
with truth, what is true of a variable must be equally true of all
instances of the variable. In Probability, on the other hand,
we must be on our guard wherever a variable occurs. In Implication
we may conclude that $\psi$~is true of anything of which
$\phi$~is true. In Probability we may conclude no more than that
$\psi$~is probable of anything of which we \emph{only} know that $\phi$~is true of
it. If $x$~stands for anything of which $\phi(x)$~is true, as soon as
we substitute in probability any particular value, whose meaning
we know, for~$x$, the value of the probability may be affected;
for knowledge, which was irrelevant before, may now become
relevant. Take the following example: Does $\phi(a)/\psi(a)=
\phi(b)/\psi(b)$? That is to say, is the probability of $\phi$'s~being true
of~$a$, given only that $\psi$~is true of~$a$, equal to the probability of
$\phi$'s~being true of~$b$, given only that $\psi$~is true of~$b$? If this simply
means that the probability of an object's satisfying~$\phi$ about
which nothing is known except that it satisfies~$\psi$ is equal to
ditto ditto, the equation is an identity. For in this case $\phi(a)/\psi(a)$
\emph{means} the same as~$\phi(b)/\psi(b)$, \ie~we know \emph{nothing} about $x$~and~$y$
except that they satisfy~$\psi$, and there is nothing whatever by
which we can distinguish $a$~from~$b$. But if $a$~and~$b$ represent
specific entities, which we can distinguish, then the equality
does not necessarily hold. If, for instance, $\phi(x)$~stands for `$x$~is
Socrates,' then it is plainly false that $\phi(a)/\psi(a)=\phi(b)/\psi(b)$, where
$a$~stands for Socrates and $b$~does not.

\Paragraph{19.} Bearing this danger in mind, we can now give further
precision to the enunciation of the Principle of Indifference given
\index{Principle of Indifference!modification of}%
in §\;16. Our knowledge of the meaning of $a$ must be taken
account of \emph{so far as it is relevant}; and the Principle is only satisfied
if we have corresponding knowledge about the meaning of~$b$.
Thus $\phi(a)/h=\phi(b)/h$ may be true for one pair of values $a$,~$b$, and
not true for another pair of values $a'$,~$b'$.
%% -----File: 070.png---Folio 59-------

This makes it possible to explain in part the contradiction
discussed in §\;4. Even if it were true that the probability of~$a$ is~$\frac{1}{2}$,
when we know nothing except that $a$~is a proposition, it does
not follow that the probability of `This book is red' is~$\frac{1}{2}$, when
we know the meanings of `book' and `red,' even if we know no
more than this. Knowledge arising directly out of acquaintance
with the meaning of `red' may be sufficient to enable us to infer
that `red' and `not-red' are not satisfactory alternatives to
which to apply the Principle of Indifference. How this may
come about will be discussed in §§\;20,~21.

But the contradictions are not yet really solved; for some
of the difficulties discussed in §\;4 can arise even when we know
no more of $a$ and $b$ than that they are \emph{different} propositions. In
fact, although we have now stated more clearly than before how
the Principle should be enunciated, it is not yet possible to explain
or to avoid all the contradictions to which it led us in §§\;4 to~7.
For this purpose we must proceed to a further qualification.

\Paragraph{20.} The examples, in which the Principle of Indifference
broke down, had a great deal in common. We broke up the
field of possibility, as we may term it, into a number of areas
by a series of disjunctive judgments. But the alternative areas
were not \emph{ultimate}. They were capable of further subdivision
into other areas \emph{similar in kind} to the former. The paradoxes
and contradictions arose, in each case, when the alternatives,
which the Principle of Indifference treated as equivalent, actually
contained or might contain a different or an indefinite number of
more elementary units.

In the type of cases in which the Principle of Indifference
seemed to permit the assertion that, in the absence of relevant
evidence, a proposition is as likely as its contradictory, its contradictory
is not an ultimate and indivisible alternative (in the
sense to be explained in §\;21 below), even if the proposition itself
satisfies this condition. For its contradictory can be disjunctively
resolved into an indefinite number of sets of contraries to
the proposition. It was out of this that our difficulties first arose.
`This book is not red' includes amongst others the alternatives
`This book is black' and `This book is blue.' It is not, therefore,
an ultimate alternative.

In the same way the contradiction of §\;5 arose out of the possibility
of splitting the alternatives `He inhabits the British
%% -----File: 071.png---Folio 60-------
Isles' into the sub-alternatives `He inhabits Ireland or he
inhabits Great Britain.' And in the third type of case, to
which the example of specific volume and density belongs, the
alternative `$v$~lies in the interval $1$~to~$2$' can be broken up into
the sub-alternatives `$v$~lies in the interval $1$~to~$1\frac{1}{2}$ or $1\frac{1}{2}$~to~$2$.'

\Paragraph{21.} This, then, seems to point the way to the qualification of
which we are in search. We must enunciate some formal rule
which will exclude those cases, in which one of the alternatives
involved is itself a disjunction of sub-alternatives \emph{of the same
form}. For this purpose the following condition is proposed.

Let the alternatives, the equiprobability of which we seek to
establish by means of the Principle of Indifference, be $\phi(a_1)$,
$\phi(a_2) \ldots \phi(a_r)$,\footnote
  {The more complicated cases in which the propositional function, of which
  the alternatives are instances, involves more than one variable (see §\;16), can be
  dealt with in a similar manner \textit{mutatis mutandis}.}
and let the evidence be~$h$. Then it is a necessary
condition for the application of the principle, that these
should be, relatively to the evidence, indivisible alternatives of
the form~$\phi(x)$. We may define a divisible alternative in the
following manner:

An alternative $\phi(a_r)$ is \emph{divisible} if
\begin{align*}
\text{(i.)}\quad   & [\phi(a_r)\equiv\phi(a_{r'})+\phi(a_{r''})]/h=1,\\
\text{(ii.)}\quad  & \phi(a_{r'})· \phi(a_{r''})/h=0,\\
\text{(iii.)}\quad & \phi(a_{r'})/h\neq 0 \quad \text{and} \quad \phi(a_{r''})/h \neq 0
\end{align*}

The condition that the sub-alternatives must be \emph{of the same
form} as the original alternatives, \ie\ expressible by means of the
same propositional function~$\phi(x)$, deserves attention. It might
be the case that the original alternatives had nothing substantial
in common; \ie\ $\phi(x)\equiv (x=x)$ is the only propositional function
common to all of them, the alternatives being $a_1$, $a_2,\ldots, a_r$. In
these circumstances the condition in question cannot be satisfied.
For the proposition~$a_r$ can always be resolved into the disjunction
$a_rb+a_r\bar b$, where $b$~is any proposition and $\bar b$~its contradictory. If,
on the other hand, the alternatives which we are comparing can
be expressed in the forms $\phi(a_1)$~and~$\phi(a_2)$, where the function~$\phi(x)$
is distinct from~$x$, it is not necessarily the case that either
of these can be resolved into a disjunctive combination of terms
which can be expressed in their turn in the same form.

Dispensing with symbolism, we can express these conditions
as follows: Our knowledge must not enable us to split up the
%% -----File: 072.png---Folio 61-------
alternative~$\phi(a_r)$ into a disjunction of two sub-alternatives, (i.)~which
are themselves expressible in the same form~$\phi$, (ii.)~which
are mutually exclusive, and (iii.)~which, on the evidence, are
possible.

In short, the Principle of Indifference is not applicable to a
pair of alternatives, if we know that either of them is capable of
being further split up into a pair of possible but incompatible
alternatives of the same form as the original pair.

\Paragraph{22.} This rule commends itself to common sense. If we
know that the two alternatives are compounded of a different
number or of an indefinite number of sub-alternatives which are
in other respects similar, so far as our evidence goes to the
original alternatives, then this is a relevant fact of which we
must take account. And as it affects the two alternatives in
differing and unsymmetrical ways, it breaks down the fundamental
condition for the valid application of the Principle of
Indifference.

Neither this consideration nor that discussed in §§\;18 and~19
substantially modify the Principle of Indifference as enunciated
in §\;16. They have only served to make explicit what was
always implicit in the Principle, by explaining the manner in
which our knowledge of the \emph{form and meaning} of the alternatives
may be a relevant part of the evidence. The apparent contradictions
arose from paying attention to what we may term
the \emph{extraneous} evidence only, to the neglect of such part of the
evidence as bore upon the form and meaning of the alternatives.

\Paragraph{23.} The application of this result to the examples cited in §\;18
is not difficult. It excludes the class of cases in which a proposition
and its contradictory constitute the alternatives. For
if $b$~is the proposition and $\bar b$~its contradictory, we cannot find
a propositional function~$\phi(x)$ which will satisfy the necessary
conditions. It deals also with the type of contradiction which
arose in considering the probability that an individual taken at
random was an inhabitant of a given region. If, on the other
hand, the term `country' is so defined that one country cannot
include two countries, then an individual is, relatively to suitable
hypotheses, as likely to be an inhabitant of one as of another.
For the function~$\phi(x)$, where $\phi(x)\equiv$ `the individual is an inhabitant
of country~$x$,' satisfies the conditions. And it deals
with the example of ranges of specific volume and specific density,
%% -----File: 073.png---Folio 62-------
\index{Probability, and relevant knowledge!geometrical@{`\textit{geometrical}'}}%
because there is no range which does not contain within itself two
similar ranges. As there are in this case no definite units by
which we can define \emph{equal} ranges, the device, which will be referred
to in §\;25 for dealing with geometrical probabilities, is not available.

\Paragraph{24.} It is worth while to add that the qualification of §\;21 is
fatal to the practical utility of the Principle of Indifference in
those cases only in which it is possible to find \emph{no} ultimate alternatives
which satisfy the conditions. For if the original alternatives
each comprise a definite number of indivisible and indifferent
sub-alternatives, we can compute their probabilities. It is often
the case, however, that we cannot by any process of finite subdivision
arrive at indivisible sub-alternatives, or that, if we can,
they are not on the evidence indifferent. In the examples given
above, for instance, where $\phi(x)\equiv x$, or where $x$ is a part of unspecified
magnitude in a continuum, there are \emph{no} indivisible
sub-alternatives. The first type comprises all cases, amongst
others, in which we weigh the probabilities of a proposition and
its contradictory; and the second includes a great number of
cases in which physical or geometrical quantities are involved.

\Paragraph{25.} We can now return to the numerous paradoxes which
arise in the study of geometrical probability (see §§\;7,~8). The
\index{Geometrical probability}%
qualification of §\;21 enables us, I think, to discover the source
of the confusion. Our alternatives in these problems relate to
certain areas or segments or arcs, and however small the elements
are which we adopt as our alternatives, they are made up of yet
smaller elements which would also serve as alternatives. Our
rule, therefore, is not satisfied, and, as long as we enunciate them
in this shape, we cannot employ the Principle of Indifference.
But it is easy in most cases to discover another set of alternatives
which do satisfy the condition, and which will often serve our
purpose equally well. Suppose, for instance, that a point lies
on a line of length~$m.l.$, we may write the alternative `the interval
of length~$l$ on which the point lies is the $x$th~interval of that
length as we move along the line from left to right'~$\equiv\phi(x)$; and
the Principle of Indifference can then be applied safely to the $m$~alternatives
$\phi(1)$, $\phi(2) \ldots \phi(m)$, the number~$m$ increasing as the
length~$l$ of the intervals is diminished. There is no reason why
$l$~should not be of any definite length however small.

If we deal with the problems of geometrical probability in
%% -----File: 074.png---Folio 63-------
this way, we shall avoid the contradictory conclusions, which
arise from confusing together \emph{distinct} elementary areas. In the
problem, for instance, of the chord drawn at random in a circle,
which is discussed in §\;7, the chord is regarded, not as a one-dimensional
line, but as the limit of an area, the shape of which
is different in each of the variant solutions. In the first solution
it is the limit of a triangle, the length of the base of which tends
to zero; in the second solution it is the limit of a quadrilateral,
two of the sides of which are parallel and at a distance apart
which tends to zero; and in the third solution the area is defined
by the limiting position of a central section of undefined shape.
These distinct hypotheses lead inevitably to different results. If
we were dealing with a strictly linear chord, the Principle of
Indifference would yield us no result, as we could not enunciate
the alternatives in the required form; and if the chord is an
elementary area, we must know the shape of the area of which
it is the limit. So long as we are careful to enunciate the alternatives
in a form to which the Principle of Indifference can be
applied unambiguously, we shall be prevented from confusing
together distinct problems, and shall be able to reach conclusions
in geometrical probability which are unambiguously valid.

The substance of this explanation can be put in a slightly
different way by saying that it is not a matter of indifference in
these cases in what manner we proceed to the limit. We must
assign the probabilities \emph{before} proceeding to the limit, which
we can do unambiguously. But if the problem in hand does
not stop at small finite lengths, areas, or volumes, and we
have to proceed to the limit, then the final result depends upon
the shape in which the body approaches the limit. Mathematicians
will recognise an analogy between this case and the determination
of potential at points \emph{within} a conductor. Its value
depends upon the shape of the area which in the limit represents
the point.

\Paragraph{26.} The positive contributions of this chapter to the determination
of valid judgments of equiprobability are two. In the
\index{Equiprobability}%
first place we have stated the Principle of Indifference in a more
accurate form, by displaying its necessary dependence upon
judgments of relevance and so bringing out the hidden element
of direct judgment or intuition, which it has always involved.
It has been shown that the Principle lays down a rule by which
%% -----File: 075.png---Folio 64-------
direct judgments of relevance and irrelevance can lead on to
judgments of preference and indifference. In the second place,
some types of consideration, which are in fact relevant, but which
are in danger of being overlooked, have been brought into prominence.
By this means it has been possible to avoid the various
types of doubtful and contradictory conclusions to which the
Principle seemed to lead, so long as we applied it without due
qualification.
%% -----File: 076.png---Folio 65-------


\Chapter{V}{Other Methods of Determining Probabilities}

\Paragraph{1.} \First{The} recognition of the fact, that not all probabilities are
numerical, limits the scope of the Principle of Indifference. It
has always been agreed that a numerical measure can actually
be obtained in those cases only in which a reduction to a set of
exclusive and exhaustive \emph{equiprobable} alternatives is practicable.
Our previous conclusion that numerical measurement is often
impossible agrees very well, therefore, with the argument of the
preceding chapter that the rules, in virtue of which we can assert
equiprobability, are somewhat limited in their field of application.
\index{Equiprobability}%

But the recognition of this same fact makes it more necessary
to discuss the principles which will justify comparisons of more
and less between probabilities, where numerical measurement is
theoretically, as well as practically, impossible. We must, for
the reasons given in the preceding chapter, rely in the last resort
on direct judgment. The object of the following rules and
principles is to reduce the judgments of preference and relevance,
\index{Judgments!of preference and relevance}%
which we are compelled to make, to a few relatively simple types.\footnote
  {Parts of \Chapref[Chap.]{XV}. are closely connected with the topics of the following
  paragraphs, and the discussion which is commenced here is concluded there.}

\Paragraph{2.} We will enquire first in what circumstances we can expect
a comparison of more and less to be theoretically possible. I
am inclined to think that this is a matter about which, rather
unexpectedly perhaps, we are able to lay down definite rules.
We are able, I think, always to compare a pair of probabilities
which are
\begin{DPalign*}
\text{(i.)}\quad & \text{of the type $ab/h$ and $a/h$}, \\
\lintertext{or}
\text{(ii.)}\quad & \text{of the type $a/hh_1$ and $a/h$},
\end{DPalign*}
provided the additional evidence~$h_1$ contains only one independent
piece of relevant information.
%% -----File: 077.png---Folio 66-------
\index{Evidence, and measurement of Probability!addition of}%
\index{Probability, and relevant knowledge!comparison of}%

(i.) The propositions of \Partref{II}. will enable us to prove that
\[
ab/h < a/h \text{ unless }b/ah = 1;
\]
that is to say, the probability of our conclusion is diminished by
the addition to it of something, which on the hypothesis of our
argument cannot be inferred from it. This proposition will be
self-evident to the reader. The rule, that the probability of two
propositions jointly is, in general, less than that of either of them
separately, includes the rule that the attribution of a more
specialised concept is less probable than the attribution of a less
specialised concept.

(ii.) This condition requires a little more explanation. It
states that the probability~$a/hh_1$ is always greater than, equal to,
or less than the probability~$a/h$, if $h_1$~contains no pair of complementary
and independent parts\footnote
  {See \Chapref[Chap.]{IV}. §\;14 for the meaning of these terms.}
both relevant to~$a/h$. If $h_1$~is
favourable, $a/hh_1 > a/h$. Similarly, if $h_2$~is favourable to~$a/hh_1$,
$a/hh_1h_2 > a/hh_1$. The reverse holds if $h_1$~and~$h_2$ are unfavourable.
Thus we can compare $a/hh'$~and~$a/h$, in every case in which the
relevant independent parts of the additional evidence~$h'$ are
either all favourable, or all unfavourable. In cases in which our
additional evidence is equivocal, part taken by itself being favourable
and part unfavourable, comparison is not necessarily possible.
In ordinary language we may assert that, according to our rule,
the addition to our evidence of a single fact always has a definite
bearing on our conclusion. It either leaves its probability unaffected
and is irrelevant, or it has a definitely favourable or
unfavourable bearing, being favourably or unfavourably relevant.
It cannot affect the conclusion in an indefinite way, which allows
no comparison between the two probabilities. But if the addition
of one fact is favourable, and the addition of a second is unfavourable,
it is not necessarily possible to compare the probability of
our original argument with its probability when it has been
modified by the addition of \emph{both} the new facts.

Other comparisons are possible by a combination of these
two principles with the Principle of Indifference. We may
find, for instance, that $a/hh_1 > a/h$, that $a/h = b/h$, that $b/h > b/hh_2$,
and that, therefore, $a/hh_1 > b/hh_2$. We have thus obtained a
comparison between a pair of probabilities, which are not
of the types discussed above, but without the introduction
%% -----File: 078.png---Folio 67-------
\index{Kries, von|inote}%
of any fresh principle. We may denote comparisons of this
type by~(iii.).

\Paragraph{3.} Whether any comparisons are possible which do not fall
within any of the categories (i.),~(ii.), or~(iii.), I do not feel certain.
We undoubtedly make a number of direct comparisons which
do not seem to be covered by them. We judge it more probable,
for instance, that Caesar invaded Britain than that Romulus
founded Rome. But even in such cases as this, where a reduction
into the regular form is not obvious, it might prove possible if
we could clearly analyse the real grounds of our judgment. We
might argue in this instance that, whereas Romulus's founding of
Rome rests solely on tradition, we have \emph{in addition} evidence of
another kind for Caesar's invasion of Britain, and that, in so
far as our belief in Caesar's invasion rests on tradition, we have
reasons of a precisely similar kind as for our belief in Romulus
\emph{without} the additional doubt involved in the maintenance of a
tradition between the times of Romulus and Caesar. By some
such analysis as this our judgment of comparison might be
brought within the above categories.

The process of reaching a judgment of comparison in this way
\index{Schematisation}%
may be called `schematisation.'\footnote
  {This phrase is used by Von Kries, \textit{op.\ cit.}\ p.~179, in a somewhat similar
  connection.}
We take initially an ideal
scheme which falls within the categories of comparison. Let
us represent `the historical tradition~$x$ has been handed down
from a date many years previous to the time of Caesar' by~$\psi_1(x)$;
`the historical tradition~$x$ has been handed down from
the time of Caesar' by~$\psi_2(x)$; `the historical tradition~$x$ has
extra-traditional support' by~$\psi_3(x)$; and the two traditions,
the Romulus tradition and the Caesar tradition respectively,
by $a$~and~$b$. Then if our relevant evidence~$h$ were of the form
$\psi_1(a)\psi_2(b)\psi_3(b)$, it is easily seen that the comparison $a/h<b/h$
could be justified on the lines laid down above.\footnote
  {For \quad $a/\psi_2(a)=b/\psi_2(b)$;
       \quad $a/\psi_1(a)<a/\psi_2(a)$;
       \quad $b/\psi_2(b)<b/\psi_2(b)\psi_3(b)$;
             $a/\psi_1(a)=a/h$; and $b/\psi_2(b)\psi_3(b)=b/h$.}
A further judgment,
that our actual evidence presented no relevant divergence
from this schematic form, would then establish the practical
conclusion. As I am not aware of any plausible judgment of
comparison which we make in common practice, but which is
clearly incapable of reduction to some schematic form, and as
I see no logical basis for such a comparison, I feel justified in
%% -----File: 079.png---Folio 68-------
\index{Analogy, principle of}%
\index{Evidence, and measurement of Probability!addition of}%
\index{Johnson, W. E.!added evidence@{and added evidence}}%
\index{Middle Term, Fallacy of}%
doubting the \emph{possibility} of comparing the probabilities of arguments
dissimilar in form and incapable of schematic reduction.
But the point must remain very doubtful until this part of the
subject has received a more prolonged consideration.

\Paragraph{4.} Category~(ii.)\ is very wide, and evidently covers a great
variety of cases. If we are to establish general principles of argument
and so avoid excessive dependence on direct individual
judgments of relevance, we must discover some new and more
particular principles included within it. Two of these---those
of Analogy and of Induction---are excessively important, and
\index{Induction!Principle of}%
will be the subject of \Partref{III}. of this book. In addition to these
a few criteria will be examined and established in \Chapref{XIV}.,
§§\;4~and 8~(49.1). We must be content here (pending the
symbolic developments of \Partref{II}.) with the two observations
following:

(1)\Pagelabel{68} The addition of new\footnote
  {$h_1$ is \emph{new} evidence so long as $h_1/h \neq 1$.}
evidence~$h_1$ to a doubtful\footnote
  {The argument is \emph{doubtful} so long as $a/h$~is neither certain nor impossible.}
argument~$a/h$
is \emph{favourably} relevant, if either of the following conditions
is fulfilled:---(\textit{a}) if $a/hh_1=0 $; (\textit{b}) if $a/hh_1=1$. Divested of symbolism,
this merely amounts to a statement that a piece of
evidence is favourable if, in conjunction with the previous
evidence, it is either a necessary or a sufficient condition for the
truth of our conclusion.

(2) It might plausibly be supposed that evidence would be
favourable to our conclusion which is favourable to favourable
evidence---\ie\ that, if $h_1$~is favourable to~$x/h$ and $x$~is favourable to~$a/h$,
$h_1$~is favourable to~$a/h$. Whilst, however, this argument
is frequently employed under conditions, which, if explicitly
stated, would justify it, there are also conditions in which this is
not so, so that it is not necessarily valid. For the very deceptive
fallacy involved in the above supposition, Mr.~Johnson has
suggested to me the name of the \emph{Fallacy of the Middle Term}. The
general question---If $h_1$~is favourable to~$x/h$ and $x$~is favourable to~$a/h$,
in what conditions is $h_1$~favourable to~$a/h$?---will be examined
in \Chapref{XIV}. §§\;4~and 8~(49.1). In the meantime, the intuition
of the reader towards the fallacy may be assisted by the
following observations, which are due to Mr.~Johnson:

Let $x$,~$x'$,~$x''\ldots$ be exclusive and exhaustive alternatives
under datum~$h$. Let $h_1$~and~$a$ be \emph{concordant} in regard to \emph{each} of
%% -----File: 080.png---Folio 69-------
these alternatives: \ie~any hypothesis which is strengthened by~$h_1$
will strengthen~$a$, and any hypothesis which is weakened by~$h_1$
will weaken~$a$. It is obvious that, if $h_1$~strengthens \emph{some} of
the hypotheses $x$,~$x'$,~$x''\ldots$, it will weaken \emph{others}. This fact
helps us to see why we cannot consider the concordance of $h_1$~and~$a$
in regard to one \emph{single} alternative, but must be able to
assert their concordance with regard to \emph{every one} of the exclusive
and exhaustive alternatives, including the particular one taken.
But a further condition is needed, which (as we shall show) is
obviously satisfied in two typical problems at least. This further
condition is that, for \emph{each} hypothesis $x$,~$x'$,~$x''\ldots$, it shall hold
that, were this hypothesis known to be true, the knowledge of~$h_1$
would \emph{not weaken} the probability of~$a$.

These two conditions are \emph{sufficient} to ensure that $h_1$~shall
strengthen~$a$ (independently of knowledge of $x$,~$x'$,~$x''\ldots$);
and, in a sense, they appear to be \emph{necessary}; for, unless they are
satisfied, the dependence of~$h_1$ upon~$a$ would be (so to speak)
\emph{accidental} as regards the `middle terms,' ($x$,~$x'$,~$x''\ldots$).

The necessity for reference to \emph{all} the alternatives $x$,~$x'$,~$x''\ldots$
is analogous to the requirement of distribution of the middle
term in ordinary syllogism. Thus, from premises ``All~$P$ is~$x$,
all~$S$ is~$x$,'' the conclusion that ``$S$'s~are~$P$'' does not formally
follow; but given ``all~$P$ is~$x$ and all~$S$ is~$x'$'' it \emph{does} follow that
``no~$S$ are~$P$'', where $x'$~is any contrary to~$x$. The two conditions
taken together would be analogous to the argument: all~$x$ $S$~is~$P$;
all~$x'$ $S$~is~$P$; all~$x''$ $S$~is~$P$;~\ldots\ therefore all~$S$ is~$P$.

\textit{First Typical Problem.}---An urn contains an unknown proportion
of differently coloured balls. A ball is drawn and replaced.
Then $x$,~$x'$,~$x''\ldots$ stand for the various possible proportions.
Let $h_1$~mean ``a white ball has been drawn''; and let $a$~mean
``a white ball will be again drawn.'' Then any hypothesis which
is strengthened by~$h_1$ will strengthen~$a$; and any hypothesis
which is weakened by~$h_1$ will weaken~$a$. Moreover, were any
one of these hypotheses known to be true, the knowledge of~$h_1$
would not weaken the probability of~$a$. Hence, in the absence
of definite knowledge as regards $x$,~$x'$,~$x''\ldots$, the knowledge
of~$h_1$ would strengthen the probability of~$a$.

\textit{Second Typical Problem.}---Let a certain event have taken
place; which may have been $x$,~$x'$,~$x''$ or~\ldots\DPtypo{}{.} Let $h_1$~mean that
$A$~reports so and so; and let $a$~mean that $B$~reports \emph{similarly} or
%% -----File: 081.png---Folio 70-------
\index{Judgments!direct}%
\index{Port Royal logic}%
identically. The phrase \emph{similarly} merely indicates that any
hypothesis as to the actual fact, which would be strengthened by
$A$'s~report, would be strengthened by $B$'s~report. Of course,
even if the reports were verbally \emph{identical}, $A$'s~evidence would not
necessarily strengthen the hypothesis in an \emph{equal} degree with~$B$'s;
because $A$~and~$B$ may be unequally expert or intelligent.
Now, in such cases, we may further affirm (in general), that, were
the actual nature of the event known, the knowledge of $A$'s~report
on it \emph{would not weaken} (though it also need not strengthen) the
probability that $B$~would give a \emph{similar} report. Hence, in the
absence of such knowledge, the knowledge of~$h_1$ would strengthen
the probability of~$a$.

\Paragraph{5.} Before leaving this part of the argument we must emphasise
the part played by direct judgment in the theory here presented.
The rules for the determination of equality and inequality between
probabilities all depend upon it at some point. This seems to
me quite unavoidable. But I do not feel that we should regard
it as a weakness. For we have seen that most, and perhaps all,
cases can be determined by the application of general principles
to one simple type of direct judgment. No more is asked of the
intuitive power applied to particular cases than to determine
whether a new piece of evidence tells, on the whole, for or against
a given conclusion. The application of the rules involves no
wider assumptions than those of other branches of logic.

While it is important, in establishing a control of direct
judgment by general principles, not to conceal its presence, yet
the fact that we ultimately depend upon an intuition need not
lead us to suppose that our conclusions have, therefore, no basis
in reason, or that they are as subjective in validity as they are
in origin. It is reasonable to maintain with the logicians of the
Port Royal that we may draw a conclusion which is truly probable
by paying attention to all the circumstances which accompany
the case, and we must admit with as little concern as possible
Hume's taunt that ``when we give the preference to one set of
\index{Hume}%
arguments above another, we do nothing but decide from our
feeling concerning the superiority of their influence.''
%% -----File: 082.png---Folio 71-------
\index{Evidence, and measurement of Probability!weight of}%


\Chapter{VI}{The Weight of Arguments}

\Paragraph{1.} \First{The} question to be raised in this chapter is somewhat novel;
after much consideration I remain uncertain as to how much
importance to attach to it. The magnitude of the probability
of an argument, in the sense discussed in \Chapref{III}., depends
upon a balance between what may be termed the favourable and
the unfavourable evidence; a new piece of evidence which leaves
this balance unchanged, also leaves the probability of the argument
unchanged. But it seems that there may be another
respect in which some kind of quantitative comparison between
arguments is possible. This comparison turns upon a balance,
not between the favourable and the unfavourable evidence, but
between the \emph{absolute} amounts of relevant knowledge and of
relevant ignorance respectively.

As the relevant evidence at our disposal increases, the magnitude
of the probability of the argument may either decrease or
increase, according as the new knowledge strengthens the unfavourable
or the favourable evidence; but \emph{something} seems to
have increased in either case,---we have a more substantial basis
upon which to rest our conclusion. I express this by saying that
an accession of new evidence increases the \emph{weight} of an argument.
New evidence will sometimes decrease the probability of
an argument, but it will always increase its `weight.'

\Paragraph{2.} The measurement of evidential weight presents similar
difficulties to those with which we met in the measurement of
probability. Only in a restricted class of cases can we compare
the weights of two arguments in respect of more and less. But
this must always be possible where the conclusion of the two
arguments is the same, and the relevant evidence in the one includes
and exceeds the evidence in the other. If the new evidence
%% -----File: 083.png---Folio 72-------
is `irrelevant,' in the more precise of the two senses defined in §\;14
of \Chapref{IV}., the weight is left unchanged. If any part of the
new evidence is relevant, then the value is increased.

The reason for our stricter definition of `relevance' is now
apparent. If we are to be able to treat `weight' and `relevance'
as correlative terms, we must regard evidence as relevant, part
of which is favourable and part unfavourable, even if, taken as
a whole, it leaves the probability unchanged. With this definition,
to say that a new piece of evidence is `relevant' is the same
thing as to say that it increases the `weight' of the argument.

A proposition cannot be the subject of an argument, unless
we at least attach some \emph{meaning} to it, and this meaning, even if
it only relates to the form of the proposition, may be relevant
in some arguments relating to it. But there may be no other
relevant evidence; and it is sometimes convenient to term the
probability of such an argument an \textit{à~priori} probability. In
this case the weight of the argument is at its lowest. Starting,
therefore, with minimum weight, corresponding to \textit{à~priori}
probability, the evidential weight of an argument rises, though
its probability may either rise or fall, with every accession of
relevant evidence.

\Paragraph{3.} Where the conclusions of two arguments are different, or
where the evidence for the one does not overlap the evidence
for the other, it will often be impossible to compare their weights,
just as it may be impossible to compare their probabilities. Some
rules of comparison, however, exist, and there seems to be a close,
though not a complete, correspondence between the conditions
under which pairs of arguments are comparable in respect of
probability and of weight respectively. We found that there were
three principal types in which comparison of probability was
possible, other comparisons being based on a combination of
these:---

(i.) Those based on the Principle of Indifference, subject
to certain conditions, and of the form ${\phi a}/{\psi a· h_1}={\phi b}/{\psi b· h_2}$,
where $h_1$~and~$h_2$ are irrelevant to the arguments.

(ii.) ${a}/{hh_1}\gtrless {a}/{h}$, where $h_1$~is a single unit of information,
containing no independent parts which are relevant.

(iii.) ${ab}/{h}\leq {a}/{h}$

Let us represent the evidential weight of the argument,
whose probability is~${a}/{h}$, by $V({a}/{h})$. Then, corresponding to
%% -----File: 084.png---Folio 73-------
the above, we find that the following comparisons of weight are
possible:---

(i.) $V(\phi a/\psi a· h_1) = V(\phi b/\psi b· h_2)$, where $h_1$~and~$h_2$ are irrelevant
in the strict sense. Arguments, that is to say, to which the
Principle of Indifference is applicable, have equal evidential
weights.

(ii.) $V(a/hh_1) > V(a/h)$, unless $h_1$~is irrelevant, in which case
$V(a/hh_1) = V(a/h)$. The restriction on the composition of~$h_1$,
which is necessary in the case of comparisons of magnitude, is
not necessary in the case of weight.

There is, however, no rule for comparisons of weight corresponding
to (iii.)~above. It might be thought that $V(ab/h) < V(a/h)$,
on the ground that the more complicated an argument is, relative
to given premisses, the less is its evidential weight. But this
is invalid. The argument~$ab/h$ is further off proof than was the
argument~$a/h$; but it is nearer disproof. For example, if $ab/h=0$
and $a/h>0$, then $V(ab/h)>V(A/h)$. In fact it would seem to
be the case that the weight of the argument $a/h$ is always
equal to that of $\bar{a}/h$, where $\bar{a}$ is the contradictory of~$a$; \ie,
$V(a/h)=V(\bar{a}/h)$. For an argument is always as near proving or
disproving a proposition, as it is to disproving or proving its
contradictory.

\Paragraph{4.} It may be pointed out that if $a/h = b/h$, it does not necessarily
follow that $V(a/h)=V(b/h)$. It has been asserted already
that if the first equality follows \emph{directly} from a single application of
the Principle of Indifference, the second equality also holds. But
the first equality can exist in other cases also. If, for instance,
$a$~and~$b$ are members respectively of \emph{different} sets of three equally
probable exclusive and exhaustive alternatives, then $a/h=b/h$; but
these arguments may have very different weights. If, however,
$a$~and~$b$ can each, relatively to~$h$, be inferred from the other, \ie\ if
$a/bh=1$ and $b/ah=1$, then $V(a/h)= V(b/h)$. For in proving or disproving
one, we are necessarily proving or disproving the other.

Further principles could, no doubt, be arrived at. The above
can be combined to reach results in cases upon which unaided
\DPtypo{common-sense}{common sense} might feel itself unable to pronounce with confidence.
Suppose, for instance, that we have three exclusive
and exhaustive alternatives, $a$,~$b$, and~$c$, and that $a/h = b/h$
in virtue of the Principle of Indifference, then we have
$V(a/h)=V(b/h)$ and $V(a/h)=V(\bar{a}/h)$, so that $V(b/h)=V(\bar{a}/h)$. It is
%% -----File: 085.png---Folio 74-------
\index{De Morgan}%
also true, since $\bar{a}/(b+c)h = 1$ and $(b+c)/\bar{a}h = 1$, that $V(\bar{a}/h) =
V((b+c)/h)$. Hence $V(b/h)=V((b+c)/h)$.

\Paragraph{5.} The preceding paragraphs will have made it clear that the
weighing of the \emph{amount} of evidence is quite a separate process
from the \emph{balancing} of the evidence for and against. In so far,
however, as the question of weight has been discussed at all,
attempts have been made, as a rule, to explain the former in
terms of the latter. If $x/h_1h_2 = \frac{2}{3}$ and $x/h_1 = \frac{3}{4}$, it has sometimes
been supposed that it is \emph{more probable} that $x/h_1h_2$ really is~$\frac{2}{3}$ than
that $x/h_1$~really is~$\frac{3}{4}$. According to this view, an increase in the
amount of evidence strengthens the probability of the probability,
or, as De~Morgan would say, the presumption of the
probability. A little reflection will show that such a theory is
untenable. For the probability of~$x$ \emph{on hypothesis}~$h_1$ is independent
of whether as a matter of fact $x$~is or is not true, and if
we find out subsequently that $x$~is true, this does not make it
false to say that on hypothesis~$h_1$ the probability of~$x$ is~$\frac{3}{4}$. Similarly
the fact that $x/h_1h_2$ is~$\frac{2}{3}$ does not impugn the conclusion that
$x/h_1$ is~$\frac{3}{4}$, and unless we have made a mistake in our judgment or
our calculation on the evidence, the two probabilities are $\frac{2}{3}$~and~$\frac{3}{4}$
respectively.

\Paragraph{6.} A second method, by which it might be thought, perhaps,
that the question of weight has been treated, is the method of
\emph{probable error}. But while probable error is sometimes connected
\index{Probable error}%
with weight, it is primarily concerned with quite a different question.
`Probable error,' it should be explained, is the name
given, rather inconveniently perhaps, to an expression which
arises when we consider the probability that a given quantity is
measured by one of a number of different magnitudes. Our
\textit{data} may tell us that one of these magnitudes is the most probable
measure of the quantity; but in some cases it will also tell
us how probable each of the other possible magnitudes of the
quantity is. In such cases we can determine the probability
that the quantity will have a magnitude which does not differ
from the most probable by more than a specified amount. The
amount, which the difference between the actual value of the
quantity and its most probable value is as likely as not to exceed,
is the `probable error.' In many practical questions the existence
of a small probable error is of the greatest importance,
if our conclusions are to prove valuable. The probability that
%% -----File: 086.png---Folio 75-------
the quantity has any particular magnitude may be very small;
but this may matter very little, if there is a high probability
that it lies within a certain range.

Now it is obvious that the determination of probable error
is intrinsically a different problem from the determination of
weight. The method of probable error is simply a summation of
a number of alternative and exclusive probabilities. If we say
that the most probable magnitude is~$x$ and the probable error~$y$,
this is a way, convenient for many purposes, of summing up a
number of probable conclusions regarding a variety of magnitudes
other than~$x$ which, on the evidence, the quantity may
possess. The connection between probable error and weight, such
as it is, is due to the fact that in scientific problems a large
probable error is not uncommonly due to a great lack of evidence,
and that as the available evidence increases there is a tendency
for the probable error to diminish. In these cases the probable
error may conceivably be a good practical measure of the weight.

It is necessary, however, in a theoretical discussion, to point
out that the connection is casual, and only exists in a limited
class of cases. This is easily shown by an example. We may
have data on which the probability of $x=5$ is~$\frac{1}{3}$, of $x=6$ is~$\frac{1}{4}$,
of $x=7$ is~$\frac{1}{5}$, of $x=8$ is~$\frac{1}{6}$, and of $x=9$ is~$\frac{1}{20}$. Additional evidence
might show that $x$~must either be $5$~or $8$ or~$9$, the probabilities of
each of these conclusions being $\frac{7}{16}$,~$\frac{5}{16}$,~$\frac{4}{16}$.
The evidential weight
of the latter argument is greater than that of the former, but the
probable error, so far from being diminished, has been increased.
There is, in fact, no reason whatever for supposing that the
probable error must necessarily diminish, as the weight of the
argument is increased.

The typical case, in which there may be a \emph{practical} connection
between weight and probable error, may be illustrated by the
two cases following of balls drawn from an urn. In each case we
require the probability of drawing a white ball; in the first case
we know that the urn contains black and white in equal proportions;
in the second case the proportion of each colour is unknown,
and each ball is as likely to be black as white. It is evident that
in either case the probability of drawing a white ball is~$\frac{1}{2}$ but
that the weight of the argument in favour of this conclusion is
greater in the first case. When we consider the most probable
proportion in which balls will be drawn in the long run, if after
%% -----File: 087.png---Folio 76-------
\index{Bernoulli, Jac.}%
each withdrawal they are replaced, the question of probable
error enters in, and we find that the greater evidential weight of
the argument on the first hypothesis is accompanied by the
smaller probable error.

This conventionalised example is typical of many scientific
problems. The more we know about any phenomenon, the less
likely, as a rule, is our opinion to be modified by each additional
item of experience. In such problems, therefore, an argument
of high weight concerning some phenomenon is likely to be accompanied
by a low probable error, when the character of a series
of similar phenomena is under consideration.

\Paragraph{7.} Weight cannot, then, be explained in terms of probability.
An argument of high weight is not `more likely to be right' than
one of low weight; for the probabilities of these arguments only
state relations between premiss and conclusion, and these relations
are stated with equal accuracy in either case. Nor is an
argument of high weight one in which the probable error is small;
for a small probable error only means that magnitudes in the
neighbourhood of the most probable magnitude have a relatively
high probability, and an increase of evidence does not necessarily
involve an increase in these probabilities.

The conclusion, that the `weight' and the `probability' of an
argument are independent properties, may possibly introduce a
difficulty into the discussion of the application of probability
to practice.\footnote
  {See also \Chapref{XXVI}. §\;7.}
For in deciding on a course of action, it seems
plausible to suppose that we ought to take account of the weight
as well as the probability of different expectations. But it is
difficult to think of any clear example of this, and I do not
feel sure that the theory of `evidential weight' has much
practical significance.

Bernoulli's second maxim, that we must take into account all\Pagelabel{76}
the information we have, amounts to an injunction that we should
be guided by the probability of that argument, amongst those of
which we know the premisses, of which the evidential weight is
the greatest. But should not this be re-enforced by a further
maxim, that we ought to make the weight of our arguments as
great as possible by getting all the information we can?\footnote
  {Cf.\ Locke, \textit{Essay concerning Human Understanding}, book~ii.\ chap.~xxi.\ §\;67:
\index{Locke}%
  ``He that judges without informing himself to the utmost that he is capable,
  cannot acquit himself of judging amiss.''}
It is
%% -----File: 088.png---Folio 77-------
\index{Judgments!disjunctive}%
difficult to see, however, to what point the strengthening of an
argument's weight by increasing the evidence ought to be pushed.
We may argue that, when our knowledge is slight but capable of
increase, the course of action, which will, relative to such knowledge,
probably produce the greatest amount of good, will often
consist in the acquisition of more knowledge. But there clearly
comes a point when it is no longer worth while to spend trouble,
before acting, in the acquisition of further information, and there
is no evident principle by which to determine \emph{how far} we ought
to carry our maxim of strengthening the weight of our argument.
A little reflection will probably convince the reader that this is
a very confusing problem.

\Paragraph{8.} The fundamental distinction of this chapter may be briefly
repeated. One argument has more \emph{weight} than another if it is
based upon a greater amount of relevant evidence; but it is not
always, or even generally, possible to say of two sets of propositions
that one set embodies \emph{more} evidence than the other. It has
a greater \emph{probability} than another if the balance in its favour,
of what evidence there is, is greater than the balance in favour
of the argument with which we compare it; but it is not always,
or even generally, possible to say that the balance in the one case
is greater than the balance in the other. The weight, to speak
metaphorically, measures the \emph{sum} of the favourable and unfavourable
evidence, the probability measures the \emph{difference}.

\Paragraph{9.} The phenomenon of `weight' can be described from the
point of view of other theories of probability than that which is
adopted here. If we follow certain German logicians in regarding
probability as being based on the disjunctive judgment, we may
say that the weight is increased when the number of alternatives
is reduced, although the ratio of the number of favourable to
the number of unfavourable alternatives may not have been
disturbed; or, to adopt the phraseology of another German
school, we may say that the weight of the probability is increased,
as the field of possibility is contracted.

The same distinction may be explained in the language of the
frequency theory.\footnote
  {See \Chapref[Chap.]{VIII}.}
We should then say that the weight is increased
if we are able to employ as the class of reference a class
which is contained in the original class of reference.

\Paragraph{10.} The subject of this chapter has not usually been discussed
%% -----File: 089.png---Folio 78-------
\index{Nitsche, A.}%
by writers on probability, and I know of only two by whom the
question has been explicitly raised:\footnote
  {There are also some remarks by Czuber (\textit{Wahrscheinlichkeitsrechnung},
\index{Czuber}%
  vol.~i.\ p.~202) on the \textit{Erkenninisswert} of probabilities obtained by different
  methods, which may have been intended to have some bearing on it.}
Meinong, who threw out a
\index{Meinong}%
suggestion at the conclusion of his review of Von Kries' ``Principien,''
published in the \textit{Göttingische gelehrte Anzeigen} for 1890
(see especially pp.~70--74), and A.~Nitsche, who took up Meinong's
suggestion in an article in the \textit{Vierteljahrsschrift für wissenschaftliche
Philosophie}, 1892, vol.~xvi.\ pp.~20--35, entitled ``Die Dimensionen
der Wahrscheinlichkeit und die Evidenz der Ungewissheit.''

Meinong, who does not develop the point in any detail, distinguishes
probability and weight as `Intensität' and `Qualität,'
and is inclined to regard them as two independent dimensions in
which the judgment is free to move---they are the two dimensions
of the `Urteils-Continuum.' Nitsche regards the weight as being
the measure of the reliability (Sicherheit) of the probability, and
holds that the probability continually approximates to its true
magnitude (reale Geltung) as the weight increases. His treatment
is too brief for it to be possible to understand very clearly what
he means, but his view seems to resemble the theory already
discussed that an argument of high weight is `more likely to be
right' than one of low weight.
%% -----File: 090.png---Folio 79-------
\index{Butler, Bishop}%


\Chapter{VII}{Historical Retrospect}

\Paragraph{1.} The characteristic features of our Philosophy of Probability
must be determined by the solutions which we offer to the
problems attacked in Chapters \Chapref[]{III}~and~\Chapref[]{IV}. Whilst a great part
of the logical calculus, which will be developed in \Partref{II}., would
be applicable with slight modification to several distinct theories
of the subject, the ultimate problems of establishing the premisses
of the calculus bring into the light every fundamental difference
of opinion.

These problems are often, for this reason perhaps, left on one
side by writers whose interest chiefly lies in the more formal parts
of the subject. But Probability is not yet on so sound a basis
that the formal or mathematical side of it can be safely developed
in isolation, and some attempts have naturally been made to
solve the problem which Bishop Butler sets to the logician in the
concluding words of the brief discussion on probability with
which he prefaces the \emph{Analogy}.\footnote
  {``It is not my design to inquire further into the nature, the foundation and
  measure of probability; or whence it proceeds that \emph{likeness} should beget that
  presumption, opinion and full conviction, which the human mind is formed
  to receive from it, and which it does necessarily produce in every one; or to
  guard against the errors to which reasoning from analogy is liable. This
  belongs to the subject of logic, and is a part of that subject which has not yet
  been thoroughly considered.''}

In this chapter, therefore, we will review in their historical
order the answers of Philosophy to the questions, how we know
relations of probability, what ground we have for our judgments,
and by what method we can advance our knowledge.

\Paragraph{2.} The natural man is disposed to the opinion that probability
is essentially connected with the inductions of experience and,
if he is a little more sophisticated, with the Laws of Causation
%% -----File: 091.png---Folio 80-------
\index{Butler, Bishop}%
\index{Port Royal logic}%
and of the Uniformity of Nature. As Aristotle says, ``the
\index{Aristotle}%
probable is that which usually happens.'' Events do not always
occur in accordance with the expectations of experience; but
the laws of experience afford us a good ground for supposing
that they usually will. The occasional disappointment of these
expectations prevents our predictions from being more than
probable; but the ground of their probability must be sought in
this experience, and in this experience only.

This is, in substance, the argument of the authors of the Port
Royal Logic (1662), who were the first to deal with the logic
of probability in the modern manner: ``In order for me to
judge of the truth of an event, and to be determined to believe
it or not believe it, it is not necessary to consider it abstractly,
and in itself, as we should consider a proposition in geometry;
but it is necessary to pay attention to all the circumstances
which accompany it, internal as well as external. I call internal
circumstances those which belong to the fact itself, and external
those which belong to the persons by whose testimony we are led
to believe it. This being done, if all the circumstances are
such that it never or rarely happens that the like circumstances
are the concomitants of falsehood, our mind is led, naturally,
to believe that it is true.''\footnote
  {Eng.\ Trans., p.~353.}
Locke follows the Port Royal
\index{Locke}%
Logicians very closely: ``Probability is likeliness to be true\ldots. The
\emph{grounds of it} are, in short, these two following. \emph{First}, the
conformity of anything with our own knowledge, observation,
and experience. \emph{Secondly}, the testimony of others, vouching
their observation and experience'';\footnote
  {\textit{An Essay concerning Human Understanding}, book~iv. ``Of Knowledge and

  Opinion.''}
and essentially the same
opinion is maintained by Bishop Butler: ``When we determine
a thing to be probably true, suppose that an event has or will
come to pass, it is from the mind's remarking in it a likeness to
some other event, which we have observed has come to pass.
And this observation forms, in numberless instances, a presumption,
opinion, or full conviction that such event has or will
come to pass.''\footnote
  {Introduction to the \textit{Analogy}.}

Against this view of the subject the criticisms of Hume were
\index{Hume}%
directed: ``The idea of cause and effect is derived from \emph{experience},
which informs us, that such particular objects, in all past
%% -----File: 092.png---Folio 81-------
\index{Bernoulli, Jac.}%
instances, have been constantly conjoined with each other\ldots.
According to this account of things~\ldots\ probability is founded
on the presumption of a resemblance betwixt those objects, of
which we have had experience, and those, of which we have had
none; and therefore 'tis impossible this presumption can arise
from probability.''\footnote
  {\textit{Treatise of Human Nature}, p.~391 (Green's edition).}
``When we are accustomed to see two impressions
conjoined together, the appearance or idea of the one immediately
carries us to the idea of the other\ldots. Thus all probable
reasoning is nothing but a species of sensation. 'Tis not
solely in poetry and music, we must follow our taste and sentiment,
but likewise in philosophy. When I am convinced of any
principle, 'tis only an idea, which strikes more strongly upon me.
When I give the preference to one set of arguments above another,
I do nothing but decide from my feeling concerning the superiority
of their influence.''\footnote
  {\textit{Op.\ cit.}\ p.~403.}
Hume, in fact, points out that, while
\index{Hume}%
it is true that past experience gives rise to a psychological anticipation
of some events rather than of others, no ground has been
given for the validity of this superior anticipation.

\Paragraph{3.} But in the meantime the subject had fallen into the hands
of the mathematicians, and an entirely new method of approach
was in course of development. It had become obvious that
many of the judgments of probability which we in fact make
do not depend upon past experience in a way which satisfies the
canons laid down by the Port Royal Logicians or by Locke. In
particular, alternatives are judged equally probable, without
there being necessarily any actual experience of their approximately
equal frequency of occurrence in the past. And, apart
from this, it is evident that judgments based on a somewhat
indefinite experience of the past do not easily lend themselves
to precise numerical appraisement. Accordingly James
Bernoulli,\footnote
  {See especially \textit{Ars Conjectandi}, p.~224. Cf.\ Laplace, \textit{Théorie analytique},
  p.~178.}
the real founder of the classical school of mathematical
probability, while not repudiating the old test of experience, had
based many of his conclusions on a quite different criterion---the
rule which I have named the Principle of Indifference. The
\index{Principle of Indifference}%
traditional method of the mathematical school essentially
depends upon reducing all the possible conclusions to a number
of `\DPchg{equi-probable}{equiprobable} cases.' And, according to the Principle of
%% -----File: 093.png---Folio 82-------
\index{Great Numbers, Law of}%
\index{Locke}%
\index{Succession, Law of}%
Indifference, `cases' are held to be \DPchg{equi-probable}{equiprobable} when there
is no reason for preferring any one to any other, when there is
nothing, as with Buridan's ass, to determine the mind in any one
of the several possible directions. To take Czuber's example
\index{Czuber}%
of dice,\footnote
  {\textit{Wahrscheinlichkeitsrechnung,} p.~9.}
this principle permits us to assume that each face is
equally likely to fall, if there is no reason to suppose any particular
irregularity, and it does not require that we should \emph{know} that the
construction is regular, or that each face has, as a matter of fact,
fallen equally often in the past.

On this Principle, extended by Bernoulli beyond those
problems of gaming in which by its tacit assumption Pascal
\index{Pascal}%
and Huyghens had worked out a few simple exercises, the whole
\index{Huyghens}%
fabric of mathematical probability was soon allowed to rest.
The older criterion of experience, never repudiated, was soon
subsumed under the new doctrine. First, in virtue of Bernoulli's
famous Law of Great Numbers, the fractions representing the
probabilities of events were thought to represent also the actual
proportion of their occurrences, so that experience, if it were
considerable, could be translated into the cyphers of arithmetic.
And next, by the aid of the Principle of Indifference, Laplace
\index{Laplace}%
established his Law of Succession by which the influence of any
experience, \emph{however limited}, could be numerically measured, and
which purported to prove that, if $B$~has been seen to accompany~$A$
twice, it is two to one that~$B$ will again accompany~$A$ on $A$'s~next
appearance. No other formula in the alchemy of logic
has exerted more astonishing powers, For it has established
the existence of God from the premiss of total ignorance; and it
has measured with numerical precision the probability that the
sun will rise to-morrow.

Yet the new principles did not win acceptance without
\index{D'Alembert}%
opposition. D'Alembert,\footnote
  {D'Alembert's scepticism was directed towards the current mathematical
  theory only, and was not, like Hume's, fundamental and far-reaching. His
\index{Hume}%
  opposition to the received opinions was, perhaps, more splendid than discriminating.}
\index{Ancillon}%
Hume, and Ancillon\footnote
  {Ancillon's communication to the Berlin Academy in 1794, entitled \textit{Doutes
  sur les bases du calcul des probabilités}, is not as well known as it deserves to
  be. He writes as a follower of Hume, but adds much that is original and
  interesting. An historian, who also wrote on a variety of philosophical subjects,
  Ancillon was, at one time, the Prussian Minister of Foreign Affairs.}
stand out as
the sceptical critics of probability, against the credulity of
%% -----File: 094.png---Folio 83-------
\index{Bernoulli, Jac.}%
\index{Calculus of Probability|inote}%
\index{Condorcet|inote}%
\index{De Morgan}%
\index{Principle of Indifference|ifoll}%
eighteenth-century philosophers who were ready to swallow
without too many questions the conclusions of a science which
claimed and seemed to bring an entire new field within the
dominion of Reason.\footnote
  {French philosophy of the latter half of the eighteenth century was profoundly
  affected by the supposed conquests of the Calculus of Probability in
  all fields of thought. Nothing seemed beyond its powers of prediction, and
  it almost succeeded in men's minds to the place previously occupied by
  Revelation. It was under these influences that Condorcet evolved his doctrine
  of the perfectibility of the human race. The continuity and oneness of
  modern European thought may be illustrated, if such things amuse the
  reader, by the reflection that Condorcet derived from Bernoulli, that Godwin
  was inspired by Condorcet, that Malthus was stimulated by Godwin's folly
  into stating his famous doctrine, and that from the reading of Malthus
  on \textit{Population} Darwin received his earliest impulse.}

The first effective criticism came from Hume, who was also
\index{Hume}%
the first to distinguish the method of Locke and the philosophers
\index{Locke}%
from the method of Bernoulli and the mathematicians. ``Probability,''
he says, ``or reasoning from conjecture, may be divided
into two kinds, viz.\ that which is founded on \emph{chance} and that which
arises from causes.''\footnote
  {\textit{Treatise of Human Nature}, p.~424 (Green's edition).}
By these two kinds he evidently means the
mathematical method of counting the equal chances based on
Indifference, and the inductive method based on the experience
of uniformity. He argues that `chance' alone can be the
foundation of nothing, and ``that there must always be a mixture
of causes among the chances, in order to be the foundation of
any reasoning.''\footnote
  {\textit{Op.\ cit.}\ p.~425.}
His previous argument against probabilities,
which were based on an assumption of cause, is thus extended
to the mathematical method also.

But the great prestige of Laplace and the `verifications'
\index{Laplace}%
of his principles which his more famous results were supposed
to supply had, by the beginning of the nineteenth century,
established the science on the Principle of Indifference in an
almost unquestioned position. It may be noted, however, that
De~Morgan, the principal student of the subject in England,
seems to have regarded the method of actual experiment and
the method of counting cases, which were equally probable
on grounds of Indifference, as alternative methods of equal
validity.

\Paragraph{4.} The reaction against the traditional teaching during the
past hundred years has not possessed sufficient force to displace
%% -----File: 095.png---Folio 84-------
\index{Ellis, Leslie}%
\index{Kries, von}%
\index{Mathematicians, and probability}%
\index{Pearson, Karl}%
\index{Poincaré, Henri}%
the established doctrine, and the Principle of Indifference is
still very widely accepted in an unqualified form. Criticism
has proceeded along two distinct lines; the one, originated by
Leslie Ellis, and developed by Dr.~Venn, Professor Edgeworth,
\index{Edgeworth}%
\index{Venn}%
and Professor Karl Pearson, has been almost entirely confined
in its influence to England; the other, of which the beginnings
are to be seen in Boole's \textit{Laws of Thought}, has been developed
\index{Boole}%
in Germany, where its ablest exponent has been Von Kries.
France has remained uninfluenced by either, and faithful, on
the whole, to the tradition of Laplace. Even Henri Poincaré,
\index{Laplace}%
who had his doubts, and described the Principle of Indifference
as ``very vague and very elastic,'' regarded it as our only
guide in the choice of that convention, ``which has always
something arbitrary about it,'' but upon which calculation in
probability invariably rests.\footnote
  {Poincaré's opinions on Probability are to be found in his \textit{Calcul des Probabilités}
  and in his \textit{Science et Hypothèse}. Neither of these books appears
  to me to be in all respects a considered work, but his view is sufficiently novel
  to be worth a reference. Briefly, he shows that the current mathematical
  definition is circular, and argues from this that the choice of the particular
  probabilities, which we are to regard as initially equal before the application of
  our mathematics, is entirely a matter of `convention.' Much epigram is,
  therefore, expended in pointing out that the study of probability is no more
  than a polite exercise, and he concludes: ``Le calcul des probabilités offre une
  contradiction dans les termes mêmes qui servent à le désigner, et, si je ne craignais
  de rappeler ici un mot trop souvent répété, je dirais qu'il nous enseigne
  surtout une chose; c'est de savoir que nous ne savons rien.'' On the other
  hand, the greater part of his book is devoted to working out instances of practical
  application, and he speaks of `metaphysics' legitimising particular conventions.
  How this comes about is not explained. He seems to endeavour to
  save his reputation as a philosopher by the surrender of probability as a valid
  conception, without at the same time forfeiting his claim as a mathematician
  to work out probable formulae of practical importance.}

\Paragraph{5.} Before following up in detail these two lines of development,
I will summarise again the earlier doctrine with which the
leaders of the new schools found themselves confronted.

The earlier philosophers had in mind in dealing with probability
the application to the future of the inductions of experience,
to the almost complete exclusion of other problems. For the
\textit{data} of probability, therefore, they looked only to their own
experience and to the recorded experiences of others; their
principal refinement was to distinguish these two grounds, and
they did not attempt to make a numerical estimate of the chances.
The mathematicians, on the other hand, setting out from the
simple problems presented by dice and playing cards, and
%% -----File: 096.png---Folio 85-------
\index{Ellis, Leslie}%
\index{Empirical School}%
requiring for the application of their methods a basis of numerical
measurement, dwelt on the negative rather than the positive
side of their evidence, and found it easier to measure equal
degrees of ignorance than equivalent quantities of experience.
This led to the explicit introduction of the Principle of Indifference,
or, as it was then termed, the Principle of Non-Sufficient Reason.
\index{Principle of Non-Sufficient Reason}%
The great achievement of the eighteenth century was, in the eyes
of the early nineteenth, the reconciliation of the two points of
view and the measurement of probabilities, which were grounded
on experience, by a method whose logical basis was the Principle
of Non-Sufficient Reason. This would indeed have been a very
astonishing discovery, and would, as its authors declared, have
gradually brought almost every phase of human activity within
the power of the most refined mathematical analysis.

But it was not long before more sceptical persons began to
suspect that this theory proved too much. Its calculations, it
is true, were constructed from the \textit{data} of experience, but the
more simple and the less complex the experience the better satisfied
was the theory. What was required was not a wide experience
or detailed information, but a completeness of symmetry in
the little information there might be. It seemed to follow from
the Laplacian doctrine that the primary qualification for one
who would be well informed was an equally balanced ignorance.

\Paragraph{6.} The obvious reaction from a teaching, which seemed to
derive from abstractions results relevant to experience, was into
the arms of empiricism; and in the state of philosophy at that
time England was the natural home of this reaction. The first
protest, of which I am aware, came from Leslie Ellis in~1842.\footnote
  {\textit{On the Foundations of the Theory of Probabilities.}}
At the conclusion of his \textit{Remarks on an alleged proof of the Method
of least squares},\footnote
  {Republished in \textit{Miscellaneous Writings.}}
``Mere ignorance,'' he says, ``is no ground
for any inference whatever. \textit{Ex nihilo nihil}.'' In Venn's
\index{Venn!experience@{and experience}}%
\textit{Logic of Chance} Ellis's suggestions are developed into a complete
theory:\footnote
  {\textit{Logic of Chance}, p.~74.} ``Experience is our sole guide. If we want to discover
what is in reality a series of \emph{things}, not a series of our own conceptions,
we must appeal to the things themselves to obtain it, for
we cannot find much help elsewhere.'' Professor Edgeworth\index{Edgeworth}\footnote
  {\textit{Metretike}, p.~4.}
was an early disciple of the same school: ``The probability,'' he
%% -----File: 097.png---Folio 86-------
\index{Bernoulli, Jac.}%
\index{Intuition \textit{versus} experience}%
\index{Laplace!school of}%
says, ``of head occurring $n$~times if the coin is of the ordinary
make is approximately at least~$(\frac{1}{2})^n$. This value is rigidly deducible
from positive experience, the observations made by gamesters,
the experiments recorded by Jevons and De~Morgan.''

The doctrines of the empirical school will be examined in
\index{Empirical School}%
\Chapref{VIII}., and I postpone my detailed criticism to that
chapter. Venn rejects the applications of Bernoulli's theorem,
\index{Venn!Bernoulli@{and Bernoulli}}%
which he describes as ``one of the last remaining relics of Realism,''
as well as the later Laplacian Law of Succession, thus destroying
the link between the empirical and the \textit{à~priori} methods. But,
apart from this, his view that statements of probability are
simply a particular class of statements about the actual world
of phenomena, would have led him to a closer dependence on
actual experience. He holds that the probability of an event's
having a certain attribute is simply the fraction expressing the
proportion of cases in which, as a matter of actual fact, this
attribute is present. Our knowledge, however, of this proportion
is often reached inductively, and shares the uncertainty to which
all inductions are liable. And, besides, in referring an event to
a series we do not postulate that all the members of the series
should be identical, but only that they should not be \emph{known} to
differ in a relevant manner. Even on this theory, therefore, we
are not solely determined by positive knowledge and the direct
\textit{data} of experience.

\Paragraph{7.} The Empirical School in their reaction against the pretentious
results, which the Laplacian theory affected to develop
out of nothing, have gone too far in the opposite direction. If
our experience and our knowledge were complete, we should
be beyond the need of the Calculus of Probability. And where
our experience is incomplete, we cannot hope to derive from it
judgments of probability without the aid either of intuition or of
some further \textit{à~priori} principle. Experience, as opposed to intuition,
cannot possibly afford us a criterion by which to judge
whether on given evidence the probabilities of two propositions
are or are not equal.

However essential the data of experience may be, they cannot
by themselves, it seems, supply us with what we want. Czuber,\index{Czuber}\footnote
  {\textit{Wahrscheinlichkeitsrechnung}, p.~11.}
who prefers what he calls the Principle of Compelling Reason
\index{Principle of compelling reason}%
(das Prinzip des zwingenden Grundes), and holds that Probability
%% -----File: 098.png---Folio 87-------
\index{Kries, von!equiprobability@{and equiprobability}}%
has an objective and not merely formal interpretation only when
it is grounded on definite knowledge, is rightly compelled to
admit that we cannot get on altogether without the Principle of
Non-Sufficient Reason. On the grounds both of its own intuitive
plausibility and of that of some of the conclusions for which it
is necessary, we are inevitably led towards this principle as a
necessary basis for judgments of probability. In \emph{some} sense,
judgments of probability do seem to be based on equally balanced
degrees of ignorance.

\Paragraph{8.} It is from this starting-point that the German logicians
\index{German logicians}%
have set out. They have perceived that there are few judgments
of probability which are altogether independent of some principle
resembling that of Non-Sufficient Reason. But they also apprehend,
with Boole, that this may be a very arbitrary method of
\index{Boole!German logicians@{and German logicians}}%
procedure.

It was pointed out in §\;18 of \Chapref{IV}. that the cases, in
which the Principle of Indifference (or Non-Sufficient Reason)
\index{Principle of Indifference}%
breaks down, have a great deal in common, and that we break
up the field of possibility into a number of areas, actually unequal,
but indistinguishable on the evidence. Several German logicians,
therefore, have endeavoured to determine some rule by which
it might be possible to postulate actual equality of area for the
fields of the various possibilities.

By far the most complete and closely reasoned solution on
these lines is that of Von Kries.\Pagelabel{87}\footnote
  {\textit{Die Principien der Wahrscheinlichkeitsrechnung. Eine logische Untersuchung.}
Freiburg, 1886.} He is primarily anxious to discover
a proper basis for the numerical measurement of probabilities,
and he is thus led to examine with care the grounds of valid
judgments of equiprobability. His criticisms of the Principle
of Non-Sufficient Reason are searching, and, to meet them, he
elaborates a number of qualifying conditions which are, he
argues, necessary and sufficient. The value of his book, however,
lies, in the opinion of the present writer, in the critical rather
than in the constructive parts. The manner in which his qualifying
conditions are expressed is often, to an English reader at any
rate, somewhat obscure, and he seems sometimes to cover up
difficulties, rather than solve them, by the invention of new
technical terms. These characteristics render it difficult to
expound him adequately in a summary, and the reader must be
%% -----File: 099.png---Folio 88-------
\index{Spielräume, doctrine of}%
referred to the original for a proper exposition of the Doctrine of
\textit{Spielräume}. Briefly, but not very intelligibly perhaps, he may
be said to hold that the hypotheses for the probabilities of which
we wish to obtain a numerical comparison, must refer to `fields'
(\textit{Spielräume}) which are `indifferent,' `comparable' in magnitude,
and `original' (\textit{ursprünglich}). Two fields are `indifferent' if
they are equal before the Principle of Non-Sufficient Reason;
they are `comparable' if it is true that the fields are actually
of equal extent; and they are `original' or ultimate if they are
not derived from some other field. The last condition is exceedingly
obscure, but it seems to mean that the objects with which
we are ultimately dealing must be directly represented by the
`fields' of our hypotheses, and there must not be merely correlation
between these objects and the objects of the fields. The
qualification of comparability is intended to deal with difficulties
such as that connected with the population of different areas of
unknown extent; and the qualification of originality with those
arising from indirect measurement, as in the case of specific
density.

Von~Kries's solution is highly suggestive, but it does not seem,
so far as I understand it, to supply an unambiguous criterion
for all cases. His discussion of the philosophical character of
probability is brief and inadequate, and the fundamental error
in his treatment of the subject is the \emph{physical}, rather than logical,
bias which seems to direct the formulation of his conditions.
The condition of \textit{Ursprünglichkeit}, for instance, seems to depend
upon physical rather than logical criteria, and is, as a result,
much more restricted in its applicability than a condition, which
will really meet the difficulties of the case, ought to be. But,
although I differ from him in his philosophical conception of
probability, the treatment of the Principle of Indifference, which
fills the greater part of his book, is, I think, along fruitful lines,
and I have been deeply indebted to it in formulating my own
conditions in \Chapref{IV}.

Of less closely reasoned and less detailed treatments, which
aim at the same kind of result, those of Sigwart and Lotze are
\index{Sigwart}%
worth noticing. Sigwart's\footnote
  {Sigwart \textit{Logic} (Eng.\ edition), vol.~ii.\ p.~220.}
position is sufficiently explained by
the following extract: ``The possibility of a mathematical treatment
lies primarily in the fact that in the disjunctive judgment
%% -----File: 100.png---Folio 89-------
the number of terms in the disjunction plays a decisive part.
Inasmuch as a limited number of mutually exclusive possibilities
is presented, of which one alone is actual, the element
of number forms an essential part of our knowledge\ldots. Our
knowledge must enable us to assume that the particular terms of
the disjunction are so far equivalent that they express an equal
degree of specialisation of a general concept, or that they cover
equal parts of the whole extension of the concept\ldots. This
equivalence is most intuitable where we are dealing with equal
parts of a spatial area, or equal parts of a period of time\ldots.
But even where this obvious quality is not forthcoming, we may
ground our expectations upon a hypothetical equivalence, where
we see no reason for considering the extent of one possibility to
be greater than that of the others\ldots.''

In the beginning of this passage Sigwart seems to be aware
of the fundamental difficulty, although exception may be taken
to the vagueness of the phrase ``equal degree of specialisation of
a general concept.'' But in the last sentence quoted he surrenders
the advantages he has gained in the earlier part of his explanation,
and, instead of insisting on a knowledge of an equal degree
of specialisation, he is satisfied with an absence of any knowledge
to the contrary. Hence, in spite of his initial qualifications, he
ends unrestrainedly in the arms of Non-Sufficient Reason.\footnote
  {Sigwart's treatment of the subject of probability is curiously inaccurate.
  Of his four fundamental rules of probability, for instance, three are, as he states
  them, certainly false.}

Lotze,\index{Lotze}\footnote
  {Lotze, \textit{Logic} (Eng.\ edition), pp.~364,~365.}
in a brief discussion of the subject, throws out some
remarks well worth quoting: ``We disclaim all knowledge of
the circumstances which condition the real issue, so that when
we talk of equally possible cases we can only mean \emph{coördinated as
equivalent species in the compass of an universal case}; that is to
say, if we enumerate the special forms, which the genus can
assume, we get a disjunctive judgment of the form: if the condition~$B$
is fulfilled, one of the kinds $f_{1}f_{2}f_{3}~\ldots$ of the universal
consequent~$F$ will occur to the exclusion of the rest. Which of
all those different consequents will, in fact, occur, depends in all
cases on the special form $b_{1}b_{2}b_{3}~\ldots$ in which that universal
condition is fulfilled\ldots. A~\emph{coördinated} case is a case which
answers to one and only one of the mutually exclusive values
$b_{1}b_{2}~\ldots$ of the condition~$B$, and these rival values may occur in
%% -----File: 101.png---Folio 90-------
\index{Certainty!Kahle and|inote}%
\index{Kahle and the Probability relation}%
reality; it does not answer to a more general form B, of this
condition, which can never exist in reality, because it embraces
several of the particular values~$b_{1}b_{2}$\ldots.''

This certainly meets some of the difficulties, and its resemblance
to the conditions formulated in \Chapref{IV}. will be evident
to the careful reader. But it is not very precise, and not easily
applicable to all cases, to those, for instance, of the measurement
of continuous quantity. By combining the suggestions of
Von~Kries, Sigwart, and Lotze, we might, perhaps, patch up a
fairly comprehensive rule. We might say, for instance, that if $b_{1}$~and~$b_{2}$
are classes, their members must be finite in number and
enumerable or they must compose stretches; that, if they are
finite in number, they must be equal in number; and that, if
their members compose stretches, the stretches must be equal
stretches; and that if $b_{1}$~and~$b_{2}$ are concepts, they must represent
concepts of an equal degree of specialisation. But qualifications
so worded would raise almost as many difficulties as they solved.
How, for instance, are we to know when concepts are of an equal
degree of specialisation?

\Paragraph{9.} That probability is a \emph{relation} has often received incidental
recognition from logicians, in spite of the general failure to place
proper emphasis on it. The earliest writer, with whom I am
acquainted, explicitly to notice this, is Kahle in his \textit{Elementa
logicae Probabilium methodo mathematica in usum Scientiarum
et Vitae adornata} published at Halle in~1735.\footnote
  {This work, which seems to have soon fallen into complete neglect and is
  now extremely rare, is full of interest and original thought. The following
  quotations will show the fundamental position taken up: ``Est cognitio probabilis,
  si desunt quaedam requisita ad veritatem demonstrativam (p.~15).
  Propositio probabilis esse potest falsa, et improbabilis esse potest vera; ergo
  cognitio hodie possibilis, crastina luce mutari potest improbabilem, si accedunt
  reliqua requisita omnia, in certitudinem (p.~26)\ldots. Certitudo est terminus
  relativus: considerare potest ratione representationum in intellectu nostro\ldots. Incerta nobis dependent a defectu cognitionis (p.~35)\ldots. Actionem
  imprudenter et contra regulas probabilitatis susceptam eventus felix sequi
  potest. Ergo prudentia actionum ex successu solo non est aestimanda (p.~62)\ldots.
  Logica probabilium est scientia dijudicandi gradum certitudinis eorum,
  quibus desunt requisita ad veritatem demonstrativam (p.~94).''}
Amongst more
recent writers casual statements are common to the effect that
the probability of a conclusion is relative to the grounds upon
\index{Boole!relation@{and relation of Probability}}%
which it is based. Take Boole\footnote
  {``On a General Method in the Theory of Probabilities,'' \textit{Phil.\ Mag}., 4th~Series,
  viii., 1854. See also, ``On the Application of the Theory of Probabilities
  to the Question of the Combination of Testimonies or Judgments'' (\textit{Edin.\ Phil.\
  Trans.}\ xxi.\ p.~600): ``Our estimate of the probability of an event varies not
  absolutely with the circumstances which actually affect its occurrence, but with
  our knowledge of those circumstances.''}
for instance: ``It is implied in
the definition that probability is always relative to our actual
%% -----File: 102.png---Folio 91-------
state of information and varies with that state of information.''
\index{Bradley!relativity@{and relativity of Probability}}%
Or Bradley:\footnote
  {\textit{The Principles of Logic}, p.~208.}
``Probability tells us what we ought to believe,
what we ought to believe \emph{on certain data}~\ldots\DPtypo{}{.} Probability is no
more `relative' and `subjective' than is any other act of
logical inference from hypothetical premises. It is relative to
the \textit{data} with which it has to deal, and is not relative in any other
sense.'' Or even Laplace, when he is explaining the diversity
\index{Laplace!relation@{and relation of Probability}}%
of human opinions:
``Dans les choses qui ne sont que vraisemblables,
la différence des données que chaque homme a sur elles,
est une des causes principales de la diversité des opinions que
l'on voit régner sur les mêmes objets~\ldots~c'est ainsi que le
même fait, récité devant une nombreuse assemblée, obtient divers
degrés de croyance, suivant l'étendue des connaissances des
auditeurs.''\footnote
  {\textit{Essai philosophique}, p.~7.}

\Paragraph{10.} Here we may leave this account of the various directions
in which progress has seemed possible, with the hope that it may
assist the reader, who is dissatisfied with the solution proposed in
\Chapref{IV}., to determine the line of argument along which he
is likeliest to discover the solution of a difficult problem.
%% -----File: 103.png---Folio 92-------
\index{Cournot, and frequency theory}%
\index{Ellis, Leslie!frequency@{and frequency theory}}%
\index{Frequency theory|ifoll}%


\Chapter{VIII}{The Frequency Theory of Probability}

\Paragraph{1.} The theory of probability, outlined in the preceding chapters,
has serious difficulties to overcome. There is a theoretical, as
well as a practical, difficulty in measuring or comparing degrees
of probability, and a further difficulty in determining them
\textit{à~priori}. We must now examine an alternative theory which is
much freer from these troubles, and is widely held at the present
time.

\Paragraph{2.} The theory is in its essence a very old one, Aristotle
\index{Aristotle}%
foreshadowed it when he held that ``the probable is that which
for the most part happens'';\footnote
  {\textit{Rhet.}\ i.~2, 1357 a~34.}
and, as we have seen in \Chapref{VII}.,
an opinion not unlike this was entertained by those philosophers
of the seventeenth and eighteenth centuries who approached
the problems of probability uninfluenced by the work of mathematicians.
But the underlying conception of earlier writers
received at the hands of some English logicians during the latter
half of the nineteenth century a new and much more complicated
form.

The theory in question, which I shall call the Frequency
Theory of Probability, first appears\footnote
  {I give Ellis the priority because his paper, published in 1843, was read on
  Feb.~14, 1842. The same conception, however, is to be found in Cournot's
  \textit{Exposition}, also published in 1843: ``La théorie des probabilités a pour objet
  certains rapports numériques qui prendraient des valeurs fixes et complétement
  déterminées, si l'on pouvait répéter à l'infini les épreuves des mêmes hasards,
  et qui, pour un nombre fini d'épreuves, oscillent entre des limites d'autant plus
  resserées, d'autant plus voisines des valeurs \emph{finales}, que le nombre des épreuves
  est plus grand.''}
as the basis of a proposed logical scheme in a brief essay by Leslie Ellis \textit{On the Foundations
of the Theory of Probabilities}, and is somewhat further developed
in his \textit{Remarks on the Fundamental Principles of the Theory of
%% -----File: 104.png---Folio 93-------
\index{Series of probabilities!frequency@{and frequency theory}}%
\index{Statistical frequency, theory of|ifoll}%
Probabilities}.\footnote
  {These essays were published in the \textit{Transactions} of the Camb.\ Phil.\ Soc., the
  first in 1843 (vol.~viii.), and the second in 1854 (vol.~ix.). Both were reprinted
  in \textit{Mathematical and other Writings} (1863), together with three other brief
  papers on Probability and the Method of Least Squares. All five are full of
  spirit and originality, and are not now so well known as they deserve to be.}
``If the probability of a given event be correctly
determined,'' he says, ``the event will on a long run of trials tend
to recur with frequency proportional to their probability. This
is generally proved mathematically. It seems to me to be true
\textit{à~priori}\ldots. I have been unable to sever the judgment that
one event is more likely to happen than another from the belief
that in the long run it will occur more frequently.'' Ellis explicitly
introduces the conception that probability is essentially
concerned with a group or series.

Although the priority of invention must be allowed to Leslie
Ellis, the theory is commonly associated with the name of Venn.
\index{Venn!frequency@{and frequency theory}|ifoll}%
In his \textit{Logic of Chance}\footnote
  {The first edition appeared in 1866. Revised editions were issued in 1876
  and 1888. References are given to the third edition of 1888.}
it first received elaborate and systematic
treatment, and, in spite of his having attracted a number of
followers, there has been no other comprehensive attempt to
meet the theory's special difficulties or the criticisms directed
against it. I shall begin, therefore, by examining it in the form
in which Venn has expounded it. Venn's exposition is much
coloured by an empirical view of logic, which is not perhaps as
necessary to the essential part of his doctrine as he himself
implies, and is not shared by all of those who must be classed as
in general agreement with him about probability. It will be
necessary, therefore, to supplement a criticism of Venn by an
account of a more general frequency theory of probability,
divested of the empiricism with which he has clothed it.

\Paragraph{3.} The following quotations from Venn's \textit{Logic of Chance} will
show the general drift of his argument: The fundamental conception
is that of a series (p.~4). The series is of events which
have a certain number of features or attributes in common (p.~10).
The characteristic distinctive of probability is this,---the occasional
attributes, as distinguished from the permanent, are found
on an examination to tend to exist \emph{in a certain definite proportion
of the whole number of cases} (p.~11). We require that there should
be in nature large classes of objects, throughout all the individual
members of which a general resemblance extends. For this
%% -----File: 105.png---Folio 94-------
\index{Measurement of Probability!frequency@{and frequency theory}}%
purpose the existence of natural kinds or groups is necessary
(p.~55). The distinctive characteristics of probability prevail
principally in the properties of natural kinds, both in the ultimate
and in the derivative or accidental properties (p.~63). The same
peculiarity prevails again in the force and frequency of most
natural agencies (p.~64). There seems reason to believe that it
is in such things only, as distinguished from things artificial, that
the property in question is to be found (p.~65). How, in any
particular case, are we to establish the existence of a probability
series? Experience is our sole guide. If we want to discover
what is in reality a series of \emph{things}, not a series of our own conceptions,
we must appeal to the things themselves to obtain it,
for we cannot find much help elsewhere (p.~174). When probability
is divorced from direct reference to objects, as it substantially
is by not being founded upon experience, it simply resolves
itself into the common algebraical doctrine of Permutations
and Combinations (p.~87). By assigning an expectation in
reference to the individual, we \emph{mean} nothing more than to make
a statement about the average of his class (p.~151). When we say
of a conclusion within the strict province of probability, that it
is not certain, all that we mean is that in some proportion of
cases only will such conclusion be right, in the other cases it will
be wrong (p.~210).

The essence of this theory can be expressed in a few words.
To say, that the probability of an event's having a certain characteristic
is~$\frac{x}{y}$, is to mean that the event is one of a number of events,
a proportion~$\frac{x}{y}$ of which have the characteristic in question; and
the \emph{fact}, that there \emph{is} such a series of events possessing this
frequency in respect of the characteristic, is purely a matter of
experience to be determined in the same manner as any other
question of fact. That such series do exist happens to be a
characteristic of the real world as we know it, and from this
the practical importance of the calculation of probabilities is
derived.

Such a theory possesses manifest advantages. There is no
mystery about it---no new indefinables, no appeals to intuition.
Measurement leads to no difficulties; our probabilities or frequencies
are ordinary numbers, upon which the arithmetical
apparatus can be safely brought to bear. And at the same time it
%% -----File: 106.png---Folio 95-------
\index{Probability@{`\textit{Probability}'}!Venn's use of}%
seems to crystallise in a clear, explicit shape the floating opinion
of common sense that an event is or is not probable in certain
supposed circumstances according as it is or is not usual as a
matter of fact and experience.

The two principal tenets, then, of Venn's system are these,---that
probability is concerned with series or groups of events,
and that all the requisite facts must be determined empirically,
a statement in probability merely summing up in a convenient
way a group of experiences. Aggregate regularity combined
with individual difference happens, he says, to be characteristic
of many events in the real world. It will often be the case,
therefore, that we can make statements regarding the average
of a certain class, or regarding its characteristics in the long run,
which we cannot make about any of its individual members
without great risk of error. As our knowledge regarding the
class as a whole may give us valuable guidance in dealing with an
individual instance, we require a convenient way of saying that
an individual belongs to a class in which certain characteristics
appear on the average with a known frequency; and this the
conventional language of probability gives us. The importance
of probability depends solely upon the actual existence of such
groups or real kinds in the world of experience, and a judgment
of probability must necessarily depend for its validity upon our
empirical knowledge of them.

\Paragraph{4.} It is the obvious, as well as the correct, criticism of such a
theory, that the identification of probability with statistical
frequency is a very grave departure from the established use of
words; for it clearly excludes a great number of judgments
which are generally believed to deal with probability. Venn
himself was well aware of this, and cannot be accused of supposing
that all beliefs, which are commonly called probable, are really
concerned with statistical frequency. But some of his followers,
to judge from their published work, have not always seen, so
clearly as he did, that his theory is \emph{not} concerned with the same
subject as that with which other writers have dealt under the
same title. Venn justifies his procedure by arguing that no other
meaning, of which it is possible to take strict logical cognisance,
can reasonably be given to the term, and that the other meanings,
with which it has been used, have not enough in common to
permit their reduction to a single logical scheme. It is useless,
%% -----File: 107.png---Folio 96-------
\index{Probability@{`\textit{Probability}'}!Edgeworth's use of|inote}%
therefore, for a critic of Venn to point out that many supposed
judgments of probability are \emph{not} concerned with statistical
frequency; for, as I understand the \textit{Logic of Chance}, he admits
it; and the critic must show that the sense different from Venn's
in which the term probability is often employed \emph{has} an important
logical interpretation about which we can generalise. This
position I seek to establish. It is, in my opinion, this other sense
\emph{alone} which has importance; Venn's theory by itself has few
practical applications, and if we allow it to hold the field, we must
admit that probability is \emph{not} the guide of life, and that in following
it we are not acting according to reason.

\Paragraph{5.} Part of the plausibility of Venn's theory is derived, I
think, from a failure to recognise the narrow limits of its applicability,
or to notice his own admissions regarding this. ``In
every case,'' he says (p.~124), ``in which we extend our inferences
by Induction or Analogy, or depend upon the witness of others,
or trust to our own memory of the past, or come to a conclusion
through conflicting arguments, or even make a long and complicated
deduction by mathematics or logic, we have a result of
which we can scarcely feel as certain as of the premisses from
which it was obtained. In all these cases, then, we are conscious
of varying quantities of belief, but are the laws according to which
the belief is produced and varied the same? If they cannot be
reduced to one harmonious scheme, if, in fact, they can at best be
brought to nothing but a number of different schemes, each with
its own body of laws and rules, then it is vain to endeavour to
force them into one science.'' All these cases, therefore, in which
we are `not certain,' Venn explicitly excludes from what he
chooses to call the science of probability, and he pays no further
attention to them. The science of probability is, according to
him, \emph{no more} than a method which enables us to express in a
convenient form statistical statements of frequency. ``The
province of probability,'' he says again on page~160, ``is not so
extensive as that over which variation of belief might be observed.
Probability only considers the case in which this variation is
brought about in a certain definite statistical way.''\footnote
  {Edgeworth uses the term `probability' widely, as I do; but he makes
\index{Edgeworth!use of `\textit{Probability}'|inote}%
  a distinction corresponding to Venn's by limiting the subject-matter of the
  \emph{Calculus} of Probabilities. He writes (`Philosophy of Chance,' \textit{Mind}, 1884,
  p.~223): ``The Calculus of Probabilities is concerned with the estimation of
  degrees of probability; not every species of estimate, but that which is founded
  on a particular standard. That standard is the phenomenon of statistical
  uniformity: the fact that a genus can very frequently be subdivided into species
  such that the number of individuals in each species bears an approximately
  constant ratio to the number of individuals in the genus.'' This use of terms is
  legitimate, though it is not easy to follow it consistently. But, like Venn's,
  it leaves aside the most important questions. The Calculus of Probabilities,
  thus interpreted, is no guide by itself as to which opinion we ought
  to follow, and is not a measure of the weight we should attach to conflicting
  arguments.}
He points
%% -----File: 108.png---Folio 97-------
\index{Probability, and relevant knowledge!rational@{and rational belief}}%
out on p.~194 that for the purposes of probability we must take
the statistical frequency from which we start \emph{ready made} and
ask no questions about the process or completeness of its manufacture:
``It may be obtained by any of the numerous rules
furnished by Induction, or it may be inferred deductively, or
\index{Induction}%
given by our own observation; its value may be diminished by
its depending upon the testimony of witnesses, or its being
recalled by our own memory. Its real value may be influenced
by these causes or any combinations of them; but all these are
preliminary questions with which we have nothing directly to do.
We assume our statistical proposition to be true, neglecting the
diminution of its value by the processes of attainment.''

It must be recognised, therefore, that Venn has deliberately
excluded from his survey almost all the cases in which we regard
our judgments as `only probable'; and, whatever the value or
consistency of his own scheme, he has left untouched a wide
field of study for others.

\Paragraph{6.} The main grounds, which have induced Venn to regard
judgments based on statistical frequency as the only cases of
probability which possess logical importance, seem to be two:
(i.)~that other cases are mainly subjective, and (ii.)~that they
are incapable of accurate measurement.

With regard to the first it must be admitted that there are
many instances in which variation of belief is occasioned by purely
psychological causes, and that his argument is valid against those
who have defined probability as measuring the degree of subjective
belief. But this has not been the usual way of
looking at the subject. Probability is the study of the
grounds which lead us to entertain a \emph{rational} preference for
one belief over another. That there are rational grounds other
than statistical frequency, for such preferences, Venn does
not deny; he admits in the quotation given above that the
`\emph{real value}' of our conclusion is influenced by many other considerations
%% -----File: 109.png---Folio 98-------
\index{Modality and probability!Venn and}%
\index{Probability, and relevant knowledge!statistical@{and statistical frequency}}%
than that of statistical frequency. Venn's theory,
therefore, cannot be fairly propounded by his disciples as \emph{alternative}
to such a theory as is propounded here. For my Treatise is
concerned with the general theory of arguments from premisses
leading to conclusions which are reasonable but not certain;
and this is a subject which Venn has, deliberately, not treated
in the \textit{Logic of Chance}.

\Paragraph{7.} Apart from two circumstances, it would scarcely be necessary
to say anything further; but in the first place some writers
have believed that Venn has propounded a \emph{complete} theory
of probability, failing to realise that he is not at all concerned
with the sense in which we may say that one induction or analogy,
\index{Induction!frequency@{and frequency theory}}%
or testimony, or memory, or train of argument is more probable
than another; and in the second place he himself has not always
kept within the narrow limits, which he has himself laid down
as proper to his theory.

For he has not remained content with defining a probability
as identical with a statistical frequency, but has often spoken
as if his theory told us which alternatives it is \emph{reasonable to prefer.}
When he states, for instance, that modality ought to be banished
from Logic and relegated to Probability (p.~296), he forgets his
own dictum that of premisses, the distinctive characteristic of
which is their lack of certainty, Probability takes account of
\emph{one class only}, Induction concerning itself with another class, and
so forth (p.~321). He forgets also that, when he comes to consider
the practical use of statistical frequencies, he has to admit that
an event may possess more than one frequency, and that we must
decide which of these to prefer on extraneous grounds (p.~213).
The device, he says, must be to a great extent arbitrary, and there
are no logical grounds of decision; but would he deny that it is
often reasonable to found our probability on one statistical
frequency rather than on another? And if our grounds are
reasonable, are they not in an important sense logical?

Even in those cases, therefore, in which we derive our preference
for one alternative over another from a knowledge of statistical
frequencies, a statistical frequency by itself is insufficient
to determine us. We may call a statistical frequency a probability,
if we choose; but the fundamental problem of determining
which of several alternatives is logically preferable still awaits
solution. We cannot be content with the only counsel Venn
%% -----File: 110.png---Folio 99-------
\index{Principle of Indifference!induction@{and induction}}%
can offer, that we should choose a frequency which is derived
from a series neither too large nor too small.

The same difficulty, that a probability in Venn's sense is
insufficient to determine which alternative is logically preferable,
arises in another connection. In most cases the statistical
frequency is not given in experience for certain, but is arrived
at by a process of \emph{induction}, and inductions, he admits, are not
\index{Induction!frequency@{and frequency theory}}%
certain. If, in the past, three infants out of every ten have
died in their first four years, induction may base on this the
doubtful assertion, All infants die in that proportion. But we
cannot assert on this ground, as Venn wishes to do, that the probability
of the death of an infant in its first four years \emph{is}~$\frac{3}{10}$ths.
We can say no more than that it is probable (in my sense) that
there is such a probability (in his sense). For the purpose of
coming to a decision we cannot compare the value of this
conclusion with that of others until we know the probability
(in my sense) that the statistical frequency really is~$\frac{3}{10}$ths.
The cases in which we can determine the logical value of a
conclusion entirely on grounds of statistical frequency would
seem to be extremely few in number.

\Paragraph{8.} The second main reason which led Venn to develop his
theory is to be found in his belief that probabilities which are
based on statistical frequencies are alone capable of accurate
measurement. The term `probabilities,' he argues, is properly
confined to the case of chances which can be calculated, and all
calculable chances can be made to depend upon statistical
frequency. In attempting to establish this latter contention
he is involved in some paradoxical opinions. ``In many cases,''
he admits, ``it is undoubtedly true that we do not resort to direct
experience at all. If I want to know what is my chance of
holding ten trumps in a game of whist, I do not enquire how
often such a thing has occurred before\ldots. In practice, \textit{à~priori}
determination is often easy, whilst \textit{à~posteriori} appeal to experience
would be not merely tedious but utterly impracticable.''
But these cases which are usually based on the Principle of
Indifference can, he maintains, be justified on statistical grounds.
In the case of coin tossing there is a considerable experience of
the equally frequent occurrence of heads and tails; the experience
gained in this simple case is to be extended to the complex
cases by ``Induction and Analogy.'' In one simple case the
%% -----File: 111.png---Folio 100-------
\index{Experience and the Principle of!Indifference}%
\index{Pearson, Karl!frequency@{and frequency theory}}%
result to which the Principle of Indifference would lead is that
which experience recommends. Therefore in complex cases,
where there is no basis of experiment at all, we may assume that
Experience, if experience there was, would speak with the same
voice as Indifference. This is to assert that, because in one case,
where there is no known reason to the contrary, there actually
is none, therefore in other cases incapable of verification the
absence of known reason to the contrary proves that \emph{actually}
there is none.

The attempt to justify the rules of inverse probability on
\index{Inverse Probability!Venn@{and Venn}}%
statistical grounds I have failed to understand; and after a careful
reading, I am unable to produce an intelligible account of
the argument involved in the latter part of chapter~vii.\ of the
\textit{Logic of Chance}.\footnote
  {Let the reader, who is acquainted with this chapter, consider what precise
  assumption Venn's reasoning requires on p.~187 in the example which seeks to
\index{Venn!inverse probability@{and inverse probability}}%
  show the efficacy of Lord Lister's antiseptic treatment \textit{à~posteriori}.
  What is the `inevitable assumption about the bags' when it is translated into the
  language of this example?}
I am doubtful whether Venn should not have
excluded \textit{à~posteriori} arguments in probability from his scheme
as well as inductive arguments. The attempt to include them
may have been induced by a desire to deal with all cases
in which numerical calculation has been commonly thought
possible.

\Paragraph{9.} The argument so far has been solely concerned with the
case for the frequency theory developed in the \textit{Logic of Chance.}
The criticisms which follow will be directed against a more
general form of the same theory which may conceivably have
recommended itself to some readers. It is unfortunate that no
adherent of the doctrine, with the exception of Venn, has attempted
to present the theory of it in detail. Professor Karl
Pearson, for instance, probably agrees with Venn in a general
way only, and it is very likely that many of the foregoing remarks
do not apply to his view of probability; but while I generally
disagree with the fundamental premisses upon which his work
in probability and statistics seems to rest, I am not clearly
aware of the nature of the philosophical theory from which he
thinks that he derives them and which makes them appear to
him to be satisfactory. A careful exposition of his logical presuppositions
would greatly add to the completeness of his work.
In the meantime it is only possible to raise general objections to
%% -----File: 112.png---Folio 101-------
\index{Probability, and relevant knowledge!truth frequency@{and truth frequency}|ifoll}%
\index{Proposition, characterisation of!classes of|ifoll}%
\index{Statistical frequency, theory of!generalisation of}%
\index{Truth frequency}%
any theory of probability which seeks to found itself upon the
conception of statistical frequency.

The generalised frequency theory which I propose to put
forward, as perhaps representative of what adherents of this
doctrine have in mind, differs from Venn's in several important
respects.\footnote
  {In what follows I am much indebted for some suggestions in favour of the
  frequency theory communicated to me by Dr.~Whitehead; but it is not to be
  supposed that the exposition which follows represents his own opinion.}
In the first place, it does not regard probability as
being \emph{identical} with statistical frequency, although it holds that
all probabilities must be based on statements of frequency, and
can be defined in terms of them. It accepts the theory that
propositions rather than events should be taken as the subject-matter
of probability; and it adopts the comprehensive view
of the subject according to which it includes induction and all
other cases in which we believe that there are \emph{logical} grounds for
preferring one alternative out of a set none of which are certain.
Nor does it follow Venn in supposing any special connection to
exist between a frequency theory of probability and logical
empiricism.

\Paragraph{10.} A proposition can be a member of many distinct classes
of propositions, the classes being merely constituted by the
existence of particular resemblances between their members
or in some such way. We may know of a given proposition that
it is one of a particular class of propositions, and we may also
know, precisely or within defined limits, what \emph{proportion} of this
class are true, without our being aware whether or not the given
proposition is true. Let us, therefore, call the actual proportion
of true propositions in a class the truth-frequency\footnote
  {This is Dr.~Whitehead's phrase.}
of the class,
and define the measure of the probability of a proposition relative
to a class, of which it is a member, as being equal to the truth-frequency
of the class.

The fundamental tenet of a frequency theory of probability
is, then, that the probability of a proposition always depends
upon referring it to some class whose truth-frequency is known
within wide or narrow limits.

Such a theory possesses most of the advantages of Venn's,
but escapes his narrowness. There is nothing in it so far which
could not be easily expressed with complete precision in the
terms of ordinary logic. Nor is it necessarily confined to probabilities
%% -----File: 113.png---Folio 102-------
\index{Relativity, of knowledge!of probabilities}%
which are numerical. In some cases we may know the
exact number which expresses the truth-frequency of our class;
but a less precise knowledge is not without value, and we may
say that one probability is greater than another, without knowing
how much greater, and that it is large or small or negligible, if
we have knowledge of corresponding accuracy about the truth-frequencies
of the classes to which the probabilities refer. The
magnitudes of some pairs of probabilities we shall be able to
compare numerically, others in respect of more and less only,
and others not at all. A great deal, therefore, of what has been
said in \Chapref{III}. would apply equally to the present theory,
with this difference that the probabilities would, as a matter of
fact, have numerical values \emph{in all cases}, and the less complete
comparisons would only hold the field in cases where the real
probabilities were partially unknown. On the frequency theory,
therefore, there is an important sense in which probabilities can
be unknown, and the relative vagueness of the probabilities
employed in ordinary reasoning is explained as belonging not
to the probabilities themselves but only to our knowledge of
them. For the probabilities are relative, not to our knowledge,
but to some objective class, possessing a perfectly definite truth-frequency,
to which we have chosen to refer them.

The frequency theory expounded in this manner cannot easily
avoid mention of the relativity of probabilities which is implicit
here, as it is in Venn's. Whether or not the probability of a
proposition is relative to given \textit{data}, it is clearly relative to the
particular class or series to which we choose to refer it. A given
proposition has a great variety of different probabilities corresponding
to each of the various distinct classes of which it is a
member; and before an intelligible meaning can be given to a
statement that the probability of a proposition is so-and-so, the
class must be specified to which the proposition is being referred.
Most adherents of the frequency theory would probably go
further, and agree that the class of reference must be determined
in any particular case by the \textit{data} at our disposal. Here, then,
is another point on which it is not necessary for the frequency
theory to diverge from the theory of this Treatise. It should,
I think, be generally agreed by every school of thought that the
probability of a conclusion is in an important sense \emph{relative to
given premisses}. On this issue and also on the point that our
%% -----File: 114.png---Folio 103-------
\index{Statistical frequency, theory of!criticism of}%
knowledge of many probabilities is not numerically definite,
there might well be for the future an end of disagreement, and
disputation might be reserved for the philosophical interpretation
of these settled facts, which it is unreasonable to deny, however
we may explain them.

\Paragraph{11.} I now proceed to those contentions upon which my
fundamental criticism of the frequency theory is founded. The
first of these relates to the method by which the class of reference
is to be determined. The magnitude of a probability is always
to be measured by the truth-frequency of some class; and this
class, it is allowed, must be determined by reference to the
premisses, on which the probability of the conclusion is to be
determined. But, as a given proposition belongs to innumerable
different classes, how are we to know which class the premisses
indicate as appropriate? What substitute has the frequency
theory to offer for judgments of relevance and indifference?
And without something of this kind, what principle is there for
uniquely determining the class, the truth-frequency of which is
to measure the probability of the argument? Indeed the
difficulties of showing how given premisses determine the class
of reference, by means of rules expressed in terms of previous
ideas, and without the introduction of any notion, which is new
and peculiar to probability, appear to me insurmountable.

Whilst no general criterion of choice seems to exist, where of
two alternative classes neither includes the other, it might be
thought that where one does include the other, the obvious
course would be to take the narrowest and most specialised class.
This procedure was examined and rejected by Venn\DPtypo{:}{;} though the
objection to it is due, not, as he supposed, to the lack of sufficient
statistics in such cases upon which to found a generalisation,
but to the inclusion in the class-concept of marks characteristic
of the proposition in question, but nevertheless \emph{not relevant}
to the matter in hand. If the process of narrowing the class
were to be carried to its furthest point, we should generally be
left with a class whose \emph{only} member is the proposition in question,
for we generally know something about it which is true of no
other proposition. We cannot, therefore, define the class of
reference as being the class of propositions of which everything
is true which is \emph{known} to be true of the proposition whose probability
we seek to determine. And, indeed, in those examples
%% -----File: 115.png---Folio 104-------
\index{Addition, of probabilities!Theorem of}%
\index{Relevance, judgments of!frequency@{and frequency theory}}%
for which the frequency theory possesses the greatest \textit{prima facie}
plausibility, the class of reference is selected by taking account
of \emph{some only} of the known characteristics of the \textit{quaesitum}, those
characteristics, namely, which are \emph{relevant} in the circumstances.
In those cases in which one can admit that the probability can be
measured by reference to a known truth-frequency, the class of
reference is formed of propositions about which our \emph{relevant}
knowledge is the same as about the proposition under consideration.
In these special cases we get the same result from the
frequency theory as from the Principle of Indifference. But
\index{Principle of Indifference}%
this does not serve to rehabilitate the frequency theory as a
\emph{general} explanation of probability, and goes rather to show that
the theory of this Treatise is the generalised theory, comprehending
within it such applications of the idea of statistical truth-frequency
as have validity.

`Relevance' is an important term in probability, of which
the meaning is readily intelligible. I have given my own definition
of it already. But I do not know how it is to be explained
in terms of the frequency theory. Whether supporters of this
theory have fully appreciated the difficulty I much doubt. It is
a fundamental issue involving the essence of the \emph{peculiarity} of
probability, which prevents its being explained away in terms
of statistical frequency or anything else.

\Paragraph{12.} Yet perhaps a modified view of the frequency theory
could be evolved which would avoid this difficulty, and I proceed,
therefore, to some further criticisms. It might be agreed that a
novel element must be admitted at this point, and that relevancy
must be determined in some such manner as has been explained
in earlier chapters. With this admission, it might be argued, the
theory would still stand, divested, it is true, of some of its original
simplicity, but nevertheless a substantial theory differing in
important respects, although not quite so fundamentally as
before, from alternative schemes.

The next important objection, then, is concerned with the
manner in which the principal theorems of probability are to be
established on a theory of frequency. This will involve an
anticipation in some part of later arguments; and the reader
may be well advised to return to the following paragraph after
he has finished Part II.

\Paragraph{13.} Let us begin by a consideration of the `Addition Theorem.'
%% -----File: 116.png---Folio 105-------
If $a/h$~denotes the probability of~$a$ on hypothesis~$h$, this theorem
may be written $(a+b)/h=a/h+b/h-ab/h$, and may be read
`On hypothesis~$h$ the probability of ``$a$~or~$b$'' is equal to the
probability of~$a+{}$ the probability of~$b-{}$ the probability of
``both $a$~and~$b$.''\,' This theorem, interpreted in some way or
other, is universally assumed; and we must, therefore, inquire
what proof of it the frequency theory can afford. A little
symbolism will assist the argument: Let $\DPtypo{a}{\alpha}_f$~represent the truth-frequency
of any class~$\DPtypo{a}{\alpha}$, and let $a_\alpha/h$~stand for `the probability
of~$a$ on hypothesis~$h$, $\DPtypo{a}{\alpha}$~being the class of reference determined
by this hypothesis.'\footnote
  {The question, previously at issue, as to \emph{how} the class of reference is determined
  by the hypothesis, is now ignored.}
We then have~$a_\alpha/h = \DPtypo{a}{\alpha}_f$, and we require to
prove a proposition, for values of $\gamma$~and~$\delta$ not yet determined,
which will be of the form:
\[
(a+b)_\delta/h = a_\alpha/h + b_\beta/h - ab_\gamma/h.
\]
Now if $\delta'$~is the class of propositions $(a+b)$ such that $a$~is an~$\alpha$
and $b$~a~$\beta$, it is easily shown by the ordinary arithmetic of classes
that $\delta'_f = \alpha_f + \beta_f - \alpha\beta_f$ where $\alpha\beta$~is the class of propositions which
are members of both $\alpha$~and~$\beta$. In the case, therefore, where
$\delta=\delta'$ and $\gamma=\alpha\beta$, an addition theorem of the required kind has
been established.

But it does not follow by any reasonable rule that, if $h$~determines
$\alpha$~and~$\beta$ as the appropriate classes of reference for $a$~and~$b$,
$h$~must necessarily determine $\delta'$~and~$\alpha\beta$ as the appropriate classes
of reference for $(a + b)$ and~$ab$; it may, for instance, be the case
that~$h$, while it renders $\alpha$~and~$\beta$ determinate, yields no information
whatever regarding~$\alpha\beta$, and points to some quite different
class~$\mu$ as the suitable class of reference for~$ab$. On the frequency
theory, therefore, we cannot maintain that the addition theorem
is true in general, but only in those special cases where it happens
that $\delta=\delta'$ and $\gamma=\alpha\beta$.

The following is a good example: We are given
that the proportion of black-haired men in the population
is~$\dfrac{p_1}{q}$ and the proportion of colour-blind men~$\dfrac{p_2}{q}$, and there is no
\emph{known} connection between black-hair and colour-blindness:
what is the probability that a man, about whom nothing special
%% -----File: 117.png---Folio 106-------
\index{Probability, and relevant knowledge!Inverse}%
\index{Venn|inote}%
is known, is\footnote
  {In the course of the present discussion the disjunctive $a+b$ is never interpreted
  so as to \emph{exclude} the conjunctive~$ab$.}
\emph{either} black-haired \emph{or} colour-blind? If we represent
the hypotheses by~$h$ and the alternatives by $a$~and~$b$, it would
usually be held that, colour-blindness and black hair being
\emph{independent for knowledge}\footnote
   {For a discussion of this term see \Chapref{XVI}. §\;2.}
relative to the given data,  $ab/h = \dfrac{p_1p_2}{q^2}$,
and that, therefore, by the addition theorem, $(a+b)/h = \dfrac{p_1}{q} +
\dfrac{p_2}{q} - \dfrac{p_1p_2}{q^2}$. But, on the frequency theory, this result might be
invalid; for $\alpha\beta_f = \dfrac{p_1p_2}{q^2}$, \emph{only} if this is the \emph{actual} proportion in fact
of persons who are both colour-blind and black-haired, and that
this is the actual proportion cannot possibly be inferred from
the \emph{independence for knowledge} of the characters in question.\footnote
  {Venn argues (\textit{Logic of Chance}, pp.~173,~174) that there is an inductive
  ground for making this inference. The question of extending the fundamental
  theorems of a frequency theory of probability by means of induction is discussed
  in §\;14~below.}

Precisely the same difficulty arises in connection with the
multiplication theorem $ab/h = a/bh· b/h$.\footnote
  {\textit{Vide} \Chapref{XII}. §\;6, and \Chapref{XIV}. §\;4.}
In the frequency notation,
which is proposed above, the corresponding theorem will
be of the form $ab_\delta/h = a_\gamma/bh· b_\beta/h$. For this equation to be satisfied
it is easily seen that $\delta$~must be the class of propositions~$xy$ such
that $x$~is a member of~$\alpha$ and $y$ of~$\beta$, and $\gamma$~the class of propositions~$xb$
such that $x$~is a member of~$\alpha$; and, as in the case of the addition
theorem, we have no guarantee that these classes $\gamma$~and~$\delta$ will be
those which the hypotheses $bh$~and~$h$ will respectively determine
as the appropriate classes of reference for $a$~and~$ab$.

In the case of the theorem of inverse probability\index{Inverse Probability!frequency@{and frequency theory}}\footnote
  {\textit{Vide} \Chapref{XIV}. §\;5.}
\[
\frac{b/ah}{c/ah} = \frac{a/bh}{a/ch}· \frac{b/h}{c/h}
\]
the same difficulty again arises, with an additional one when
practical applications are considered. For the relative probabilities
of our \textit{à~priori} hypotheses, $b$~and~$c$, will scarcely ever be
capable of determination by means of known frequencies, and in
the most legitimate instances of the inverse principle's operation
%% -----File: 118.png---Folio 107-------
\index{Independence, for knowledge}%
we depend either upon an inductive argument or upon the
Principle of Indifference. It is hard to think of an example in
\index{Principle of Indifference}%
which the frequency conditions are even approximately satisfied.

Thus an important class of case, in which arguments in probability,
generally accepted as satisfactory, do not satisfy the
frequency conditions given above, are those in which the notion
is introduced of two propositions being, on certain \textit{data}, independent
for knowledge. The meaning and definition of this
expression is discussed more fully in \Partref{II}.; but I do not see
what interpretation the frequency theory can put upon it. Yet
if the conception of `independence for knowledge' is discarded,
we shall be brought to a standstill in the vast majority of problems,
which are ordinarily considered to be problems in probability,
simply from the lack of sufficiently detailed data. Thus the
frequency theory is not adequate to explain the processes of
reasoning which it sets out to explain. If the theory restricts its
operation, as would seem necessary, to those cases in which we
\emph{know} precisely how far the true members of $\alpha$~and~$\beta$ overlap,
the vast majority of arguments in which probability has been
employed must be rejected.

\Paragraph{14.} An appeal to some further principle is, therefore, required
before the ordinary apparatus of probable inference can be established
on considerations of statistical frequency; and it may
have occurred to some readers that assistance may be obtained
from the principles of induction. Here also it will be necessary
\index{Induction!frequency@{and frequency theory}}%
to anticipate a subsequent discussion. If the argument of \Partref{III}.
is correct, nothing is more fatal than Induction to the theory
now under criticism. For, so far from Induction's lending
support to the fundamental rules of probability, it is itself
dependent on them. In any case, it is generally agreed that
an inductive conclusion is only probable, and that its probability
increases with the number of instances upon which it is founded.
According to the frequency theory, this belief is only justified if
the majority of inductive conclusions actually are true, and it
will be false, even on our existing data, that \emph{any} of them are even
probable, if the acknowledged possibility that a majority are
false is an actuality. Yet what possible reason can the frequency
theory offer, which does not beg the question, for supposing that
a majority \emph{are true}? And failing this, what ground have we
for believing the inductive process to be reasonable? Yet we
%% -----File: 119.png---Folio 108-------
invariably assume that with our existing knowledge it is logically
reasonable to attach some weight to the inductive method, even
if future experience shows that \emph{not one} of its conclusions is verified
in fact. The frequency theory, therefore, in its present form at
any rate, entirely fails to explain or justify the most important
source of the most usual arguments in the field of probable
inference.

\Paragraph{15.} The failure of the frequency theory to explain or justify
arguments from induction or analogy suggests some remarks of a
more general kind. While it is undoubtedly the case that many
valuable judgments in probability are partly based on a knowledge
of statistical frequencies, and that many more can be held,
with some plausibility, to be indirectly derived from them, there
remains a great mass of probable argument which it would be
paradoxical to justify in the same manner. It is not sufficient,
therefore, even if it is possible, to show that the theory can be
developed in a self-consistent manner; it must also be shown
how the body of probable argument, upon which the greater
part of our generally accepted knowledge seems to rest, can
be explained in terms of it; for it is certain that much of
it does not appear to be derived from premisses of statistical
frequency.

Take, for instance, the intricate network of arguments upon
which the conclusions of \textit{The Origin of Species} are founded:
how impossible it would be to transform them into a shape in
which they would be seen to rest upon statistical frequency!
Many individual arguments, of course, are explicitly founded
upon such considerations; but this only serves to differentiate
them more clearly from those which are not. Darwin's own
\index{Darwin}%
account of the nature of the argument may be quoted: ``The
belief in Natural Selection must at present be grounded entirely
on general considerations: (1)~on its being a \textit{vera causa}, from
the struggle for existence and the certain geological fact that
species do somehow change; (2)~from the analogy of change
under domestication by man's selection; (3)~and chiefly from
this view connecting under an intelligible point of view a host
of facts. When we descend to details~\ldots\ we cannot prove that
a single species has changed; nor can we prove that the supposed
changes are beneficial, which is the groundwork of the theory;
nor can we explain why some species have changed and others
%% -----File: 120.png---Folio 109-------
have not.''\footnote
  {Letter to G.~Bentham, \textit{Life and Letters}, vol.~iii.\ p.~25.}
Not only in the main argument, but in many of the
subsidiary discussions,\footnote
  {\Eg\ in the discussion on the relative effect of disuse and selection in
  reducing unnecessary organs to a rudimentary condition.}
an elaborate combination of induction
and analogy is superimposed upon a narrow and limited knowledge
of statistical frequency. And this is equally the case in
almost all everyday arguments of any degree of complexity.
The class of judgments, which a theory of statistical frequency
can comprehend, is too narrow to justify its claim to present a
complete theory of probability.

\Paragraph{16.} Before concluding this chapter, we should not overlook
the element of truth which the frequency theory embodies and
which provides its plausibility. In the first place, it gives a
true account, so long as it does not argue that probability and
frequency are \emph{identical}, of a large number of the most \emph{precise}
arguments in probability, and of those to which mathematical
treatment is easily applicable. It is this characteristic which
has recommended it to statisticians, and explains the large
measure of its acceptance in England at the present time; for
the popularity in this country of an opinion, which has, so far
as I know, no thorough supporters abroad, may reasonably be
attributed to the chance which has led most of the English
writers, who have paid much attention to probability in recent
years, to approach the subject from the statistical side.

In the second place, the statement that the probability of an
event is measured by its actual frequency of occurrence `in the
long run' has a very close connection with a valid conclusion
which can be derived, \emph{in certain cases}, from Bernoulli's theorem.
\index{Bernoulli's Theorem}%
This theorem and its connection with the theory of frequency will
be the subject of \Chapref{XXIX}.

\Paragraph{17.} The absence of a recent exposition of the logical basis of
the frequency theory by any of its adherents has been a great
disadvantage to me in criticising it. It is possible that some
of the opinions, which I have examined at length, are now held
by no one; nor am I absolutely certain, at the present stage of
the inquiry, that a partial rehabilitation of the theory may not
be possible. But I am sure that the objections which I have
raised cannot be met without a great complication of the theory,
and without robbing it of the simplicity which is its greatest
%% -----File: 121.png---Folio 110-------
preliminary recommendation. Until the theory has been given
new foundations, its logical basis is not so secure as to permit
controversial applications of it in practice. A good deal of
modern statistical work may be based, I think, upon an inconsistent
logical scheme, which, avowedly founded upon a theory
of frequency, introduces principles which this theory has no
power to justify.
%% -----File: 122.png---Folio 111-------


\Chapter{IX}{The Constructive Theory of Part I. Summarized}

\Paragraph{1.} \First{That} part of our knowledge which we obtain directly,
supplies the premisses of that part which we obtain by argument.
From these premisses we seek to justify some degree of rational
belief about all sorts of conclusions. We do this by perceiving
certain logical relations between the premisses and the
conclusions. The kind of rational belief which we \emph{infer} in
this manner is termed \emph{probable} (or in the limit \emph{certain}), and the
logical relations, by the perception of which it is obtained, we
term \emph{relations of probability}.

The probability of a conclusion~$a$ derived from premisses~$h$
we write~$a/h$; and this symbol is of fundamental importance.

\Paragraph{2.} The object of the Theory or Logic of Probability is to
systematise such processes of inference. In particular it aims
at elucidating rules by means of which the probabilities of different
arguments can be compared. It is of great practical importance
to determine which of two conclusions is on the evidence the
more probable.

The most important of these rules is the Principle of
Indifference. According to this Principle we must rely upon
direct judgment for discriminating between the relevant and
the irrelevant parts of the evidence. We can only discard
those parts of the evidence which are irrelevant by \emph{seeing} that
they have no logical bearing on the conclusion. The irrelevant
evidence being thus discarded, the Principle lays it down that
if the evidence for either conclusion is the same (\ie~symmetrical),
then their probabilities also are the same (\ie~equal).

If, on the other hand, there is additional evidence (\ie~in
addition to the symmetrical evidence) for one of the conclusions,
and this evidence is \emph{favourably relevant}, then that conclusion is
%% -----File: 123.png---Folio 112-------
the more probable. Certain rules have been given by which to
judge whether or not evidence is favourably relevant. And by
combinations of these judgments of preference with the judgments
of indifference warranted by the Principle of Indifference
more complicated comparisons are possible.

\Paragraph{3.} There are, however, many cases in which these rules
furnish no means of comparison; and in which it is certain that
it is not actually within our power to make the comparison. It
has been argued that in these cases the probabilities are, in fact,
\emph{not comparable}. As in the example of similarity, where there
are different orders of increasing and diminishing similarity, but
where it is not possible to say of every pair of objects which of
them is on the whole the more like a third object, so there are
different orders of probability, and probabilities, which are not
of the same order, cannot be compared.

\Paragraph{4.} It is sometimes of practical importance, when, for example,
we wish to evaluate a chance or to determine the amount of
our expectation, to say not only that one probability is greater
than another, but by how much it is greater. We wish, that is
to say, to have a numerical measure of degrees of probability.

This is only occasionally possible. A rule can be given for
numerical measurement when the conclusion is one of a number
of equiprobable, exclusive, and exhaustive alternatives, but not
otherwise.

\Paragraph{5.} In \Partref{II}. I proceed to a symbolic treatment of the
subject, and to the greater systematisation, by symbolic methods
on the basis of certain axioms, of the rules of probable argument.

In Parts \Partref[]{III}., \Partref[]{IV}., and~\Partref[]{V}. the nature of certain very important
types of probable argument of a complex kind will be treated
in detail; in \Partref{III}. the methods of Induction and Analogy,
in \Partref{IV}. certain semi-philosophical problems, and in \Partref{V}.
the logical foundations of the methods of inference now commonly
known as \emph{statistical}.
%% -----File: 124.png---Folio 113-------


\Part{II}{Fundamental Theorems}
%% -----File: 125.png---Folio 114-------
%[Blank Page]
%% -----File: 126.png---Folio 115-------
\index{Russell, Bertrand}%


\Chapter{X}{Introductory}

\Paragraph{1.} In \Partref{I}. we have been occupied with the epistemology of our
subject, that is to say, with what we know about the characteristics
and the justification of probable Knowledge. In \Partref{II}. I pass
to its Formal Logic. I am not certain of how much positive value
this Part will prove to the reader. My object in it is to show
that, starting from the philosophical ideas of \Partref{I}., we can
deduce by rigorous methods out of simple and precise definitions
the usually accepted results, such as the theorems of the addition
and multiplication of probabilities and of inverse probability.
The reader will readily perceive that this Part would never have
been written except under the influence of Mr.~Russell's \textit{Principia
Mathematica}. But I am sensible that it may suffer from the
over-elaboration and artificiality of this method without the
justification which its grandeur of scale affords to that great work.
In common, however, with other examples of formal method,
this attempt has had the negative advantage of compelling the
author to make his ideas precise and of discovering fallacies and
mistakes. It is a part of the spade-work which a conscientious
author has to undertake; though the process of doing it may
be of greater value to him than the results can be to the reader,
who is concerned to know, as a safeguard of the reliability of the
rest of the construction, that the thing can be done, rather than
to examine the architectural plans in detail. In the development
of my own thought, the following chapters have been of great
importance. For it was through trying to prove the fundamental
theorems of the subject on the hypothesis that Probability was
a \emph{relation} that I first worked my way into the subject; and the
rest of this Treatise has arisen out of attempts to solve the
successive questions to which the ambition to treat Probability
as a branch of Formal Logic first gave rise.
%% -----File: 127.png---Folio 116-------
\index{Johnson, W. E.}%
\index{Probability, and relevant knowledge!truth@{and truth}}%
\index{Spinoza|inote}%
\index{Truth and probability|inote}%

A further occasion of diffidence and apology in introducing
this Part of my Treatise arises out of the extent of my debt to
Mr.~W.~E. Johnson. I worked out the first scheme in complete
independence of his work and ignorant of the fact that he had
thought, more profoundly than I had, along the same lines; I
have also given the exposition its final shape with my own hands.
But there was an intermediate stage, at which I submitted what
I had done for his criticism, and received the benefit not only of
criticism but of his own constructive exercises. The result is
that in its final form it is difficult to indicate the exact extent of
my indebtedness to him. When the following pages were first
in proof, there seemed little likelihood of the appearance of any
work on Probability from his own pen, and I do not now proceed
to publication with so good a conscience, when he is announcing
the approaching completion of a work on Logic which will include
``Problematic Inference.''

I propose to give here a brief summary of the five chapters
following, without attempting to be rigorous or precise. I shall
then be free to write technically in Chapters \Chapref[]{XI}.--\Chapref[]{XV}., inviting
the reader, who is not specially interested in the details of this
sort of technique, to pass them by.

\Paragraph{2.} Probability is concerned with \emph{arguments}, that is to say,
with the ``bearing'' of one set of propositions upon another set.
If we are to deal formally with a generalised treatment of this
subject, we must be prepared to consider relations of probability
between \emph{any} pair of sets of propositions, and not only between
sets which are actually the subject of knowledge. But we soon
find that some limitation must be put on the character of sets of
propositions which we can consider as the hypothetical subject
of an argument, namely, that they must be \emph{possible} subjects of
knowledge. We cannot, that is to say, conveniently apply our
theorems to premisses which are self-contradictory and formally
inconsistent with themselves.

For the purpose of this limitation we have to make a distinction
between a set of propositions which is merely false in fact
and a set which is formally inconsistent with itself.\footnote
  {Spinoza had in mind, I think, the distinction between Truth and Probability
  in his treatment of Necessity, Contingence, and Possibility. \textit{Res
  enim omnes ex data Dei natura necessario sequutae sunt, et ex necessitate naturae
  Dei determinatae sunt ad certo modo existendum et operandum} (\textit{Ethices} i.~33).
  That is to say, everything is, without qualification, true or false. \textit{At res
  aliqua nulla alia de causa contingens dicitur, nisi respectu defectus nostrae
  cognitionis} (\textit{Ethices} i.~33, scholium). That is to say, Contingence, or, as I
  term it, Probability, solely arises out of the limitations of our knowledge.
  Contingence in this wide sense, which includes every proposition which, in
  relation to our knowledge, is only probable (this term covering all intermediate
  degrees of probability), may be further divided into Contingence in the strict
  sense, which corresponds to an \textit{à~priori} or formal probability exceeding zero,
  and Possibility; that is to say, into formal possibility and empirical possibility.
  \textit{Res singulares voco contingentes, quatenus, dum ad earum solam essentiam
  attendimus, nihil invenimus, quod earum existentiam necessario ponat, vel
  quod ipsam necessario secludat. Easdem res singulares voco possibiles, quatenus
  dum ad causas, ex quibus produci debent, attendimus, nescimus, an ipsae
  determinatae sint ad easdem producendum} (\textit{Ethices} iv.\ Def~3,~4).}
This leads
%% -----File: 128.png---Folio 117-------
\index{Groups, of propositions}%
\index{Proposition, characterisation of!groups of}%
\index{Russell, Bertrand!inference@{and inference}}%
\index{Universe of reference}%
us to the conception of a \emph{group} of propositions, which is defined
as a set of propositions such that---(i.)~if a logical principle
belongs to it, all propositions which are instances of that logical
principle also belong to it; (ii.)~if the proposition~$p$ and the
proposition `not-$p$~or~$q$' both belong to it, then the proposition~$q$
also belongs to it; (iii.)~if any proposition~$p$ belongs to it, then
the contradictory of~$p$ is \emph{excluded} from it. If the group defined
by one part of a set of propositions excludes a proposition which
belongs to a group defined by another part of the set, then the
set taken as a whole is \emph{inconsistent with itself} and is incapable of
forming the premiss of an argument.

The conception of a group leads on to a precise definition of
one proposition \emph{requiring} another (which in the realm of assertion
corresponds to \emph{relevance} in the realm of probability), and of logical
priority as being an order of propositions arising out of their
relation to those special groups, or \emph{real groups}, which are in fact
the subject of knowledge. Logical priority has no absolute
signification, but is relative to a specific body of knowledge, or,
as it has been termed in the traditional logic, to the \emph{Universe of
Reference}.

It also enables us to reach a definition of \emph{inference} distinct from
\emph{implication}, as defined by Mr.~Russell. This is a matter of very
great importance. Readers who are acquainted with the work
of Mr.~Russell and his followers will probably have noticed that
the contrast between his work and that of the traditional logic
is by no means wholly due to the greater precision and more
mathematical character of his technique. There is a difference
also in the design. His object is to discover what assumptions
are required in order that the formal propositions generally
accepted by mathematicians and logicians may be obtainable
%% -----File: 129.png---Folio 118-------
as the result of successive steps or substitutions of a few very
simple types, and to lay bare by this means any inconsistencies
which may exist in received results. But beyond the fact that
the conclusions to which he seeks to lead up are those of common
sense, and that the uniform type of argument, upon the validity
of which each step of his system depends, is of a specially obvious
kind, he is not concerned with analysing the methods of valid
reasoning which we actually employ. He concludes with
familiar results, but he reaches them from premisses, which have
never occurred to us before, and by an argument so elaborate that
our minds have difficulty in following it. As a method of setting
forth the system of formal truth, which shall possess beauty,
\DPchg{inter-dependence}{interdependence}, and completeness, his is vastly superior to
any which has preceded it. But it gives rise to questions about
the relation in which ordinary reasoning stands to this ordered
system, and, in particular, as to the precise connection between
the process of inference, in which the older logicians were principally
interested but which he ignores, and the relation of implication
on which his scheme depends.

`$p$~implies~$q$' is, according to his definition, exactly equivalent
to the disjunction `$q$~is true or $p$~is false.' If $q$~is true, `$p$~implies~$q$'
holds for all values of~$p$; and similarly if $p$~is false, the implication
holds for all values of~$q$. This is not what we mean
when we say that $q$~can be inferred or follows from~$p$. For whatever
the exact meaning of inference may be, it certainly does not
hold between \emph{all} pairs of true propositions, and is not of such a
character that \emph{every} proposition follows from a false one. It is
not true that `A male now rules over England' follows or can be
inferred from `A male now rules over France'; or `A female now
rules over England' from `A female now rules over France';
whereas, on Mr.~Russell's definition, the corresponding implications
hold simply in virtue of the facts that `A male now rules
over England' is true and `A female now rules over France'
is false.

The distinction between the Relatival Logic of Inference and
Probability, and Mr.~Russell's Universal Logic of Implication,
seems to be that the former is concerned with the relations of
propositions in general to a particular limited \emph{group}. Inference
and Probability depend for their importance upon the fact that
in actual reasoning the limitation of our knowledge presents us
%% -----File: 130.png---Folio 119-------
with a particular set of propositions, to which we must relate any
other proposition about which we seek knowledge. The course
of an argument and the results of reasoning depend, not simply
on what is true, but on the particular body of knowledge from
which we have set out. Ultimately, indeed, Mr.~Russell cannot
avoid concerning himself with groups. For his aim is to discover
the smallest set of propositions which specify our formal knowledge,
and then to show that they do in fact specify it. In this
enterprise, being human, he must confine himself to that part of
formal truth which we know, and the question, how far his
axioms comprehend \emph{all} formal truth, must remain insoluble.
But his object, nevertheless, is to establish a train of implications
between formal truths; and the character and the justification of
rational argument as such is not his subject.

\Paragraph{3.} Passing on from these preliminary reflections, our first
task is to establish the axioms and definitions which are to make
operative our symbolical processes. These processes are almost
entirely a development of the idea of representing a probability
by the symbol~$a/h$, where $h$~is the premiss of an argument and $a$~its
conclusion. It might have been a notation more in accordance
with our fundamental ideas, to have employed the symbol~$a/h$
to designate the \emph{argument} from $h$~to~$a$, and to have represented
the probability of the argument, or rather the degree of rational
belief about~$a$ which the argument authorises, by the symbol
$P(a/h)$. This would correspond to the symbol $V(a/h)$ which has
been employed in \Chapref{VI}. for the evidential value of the
argument as distinct from its probability. But in a section
where we are only concerned with probabilities, the use of $P(a/h)$
would have been unnecessarily cumbrous, and it is, therefore,
convenient to drop the prefix~$P$ and to denote the probability
itself by~$a/h$.

The discovery of a convenient symbol, like that of an essential
word, has often proved of more than verbal importance. Clear
thinking on the subject of Probability is not possible without a
symbol which takes an explicit account of the premiss of the
argument as well as of its conclusion; and endless confusion has
arisen through discussions about the probability of a conclusion
without reference to the argument as a whole. I claim, therefore,
the introduction of the symbol~$a/h$ as an essential step towards
any progress in the subject.
%% -----File: 131.png---Folio 120-------
\index{Addition, of probabilities!definition of}%
\index{Equivalence, definition of}%
\index{Groups, of propositions!definition of}%
\index{Inconsistency, definition of}%
\index{Independence, for knowledge!definition of}%

\Paragraph{4.} Inasmuch as relations of Probability cannot be assumed
to possess the properties of numbers, the terms \emph{addition} and
\emph{multiplication} of probabilities have to be given appropriate
\index{Multiplication!definition of}%
meanings by definition. It is convenient to employ these
familiar expressions, rather than to invent new ones, because the
properties which arise out of our definitions of addition and
\index{Definitions!summary of}%
multiplication in Probability are analogous to those of addition
and multiplication in Arithmetic. But the process of establishing
these properties is a little complicated and occupies the greater
part of \Chapref{XII}.

The most important of the definitions of \Chapref{XII}. are the
following (the numbers referring to the numbers of \Chapref{XII}.):

II\@. The Definition of \emph{Certainty}: $a/h=1$.
\index{Certainty!definition of}%

III\@. The Definition of \emph{Impossibility}: $a/h=0$.
\index{Impossibility!definition of}%

VI\@. The Definition of \emph{Inconsistency}: $ah$~is inconsistent if
$a/h=0$.

VII\@. The Definition of a \emph{Group}: the class of propositions~$a$
such that $a/h=1$ is the group~$h$.

VIII\@. The Definition of \emph{Equivalence}: if $b/ah=1$ and $a/bh=1$
$(a\equiv b)/h=1$.

IX\@. The Definition of \emph{Addition}: $ab/h + ab/h\footnotemark = a/h$.
\footnotetext{$\bar{b}$~stands for the contradictory of~$b$.}

X\@. The Definition of \emph{Multiplication}: $ab/h=a/bh· b/h=b/ah· a/h$.
The symbolical development of the subject largely
proceeds out of these definitions of Addition and Multiplication.
It is to be observed that they give a meaning, not to the addition
and multiplication of \emph{any} pairs of probabilities, but only to pairs
which satisfy a certain form. The definition of Multiplication
may be read: `the probability of both $a$~and~$b$ given~$h$ is equal
to the probability of~$a$ given~$bh$, multiplied by the probability of~$b$
given~$h$.'

XI\@. The Definition of \emph{Independence}: if $a_1/a_2h = a_1/h$ and
$a_2/a_1h = a_2/h$, $a_1/h$~and~$a_2/h$ are independent.

XII\@. The Definition of \emph{Irrelevance}: if $a_1/a_2h = a_1/h$, $a_2$ is
\index{Irrelevance!definition of}%
irrelevant to~$a_1/h$.

\Paragraph{5.} In \Chapref{XIII}. these definitions, supplemented by a few
axioms, are employed to demonstrate the fundamental theorems
of \emph{Certain} or \emph{Necessary Inference}. The interest of this chiefly
\index{Inference!necessary}%
lies in the fact that these theorems include those which the
%% -----File: 132.png---Folio 121-------
\index{Addition, of probabilities!Theorem of}%
\index{Independence, for knowledge!Theorem of}%
\index{Johnson, W. E.!cumulative@{and cumulative formula}}%
traditional Logic has termed the \emph{Laws of Thought}, as for example
the Law of Contradiction and the Law of Excluded Middle.
These are here exhibited as a part of the generalised theory
of Inference or Rational Argument, which includes probable
Inference as well as certain Inference. The object of this chapter
is to show that the ordinarily accepted rules of Inference can in
fact be deduced from the definitions and axioms of \Chapref{XII}.

\Paragraph{6.} In \Chapref{XIV}. I proceed to the fundamental Theorems
of Probable Inference, of which the following are the most
interesting:

\textit{Addition Theorem}: $(a + b)/h = a/h + b/h - ab/h$, which reduces
to $(a + b)/h = a/h + b/h$, where $a$~and~$b$ are mutually exclusive;
and, if $p_1p_2 \ldots p_n$ form, relative to $h$ a set of exclusive and
exhaustive alternatives, $a/h = \Sum_1^n p_r a/h$.

\textit{Theorem of Irrelevance}: If $a/h_1h_2 = a/h_1$ then $a/h_1\bar{h}_2 = a/h_1$;
\index{Irrelevance!Theorem of}%
\ie\ if a proposition is irrelevant, its contradictory also is irrelevant.

\textit{Theorem of Independence}: If $a_2/a_1h = a_2/h$, $a_1/a_2h = a_1/h$; \ie\
if $a_1$~is irrelevant to~$a_2/h$, it follows that $a_2$~is irrelevant to~$a_1/h$
and that $a_1/h$~and~$a_2/h$ are independent.

\textit{Multiplication Theorem}: If $a_1/h$ and $a_2/h$ are independent,
\index{Multiplication!theorems of}%
$a_1a_2/h = a_1/h· a_2/h$.

\textit{Theorem of Inverse Probability}: $\dfrac{a_1/bh}{a_2/bh} = \dfrac{b/a_1h}{b/a_2h}· \dfrac{a_1/h}{a_2/h}$. Further,
\index{Inverse Probability!Theorem of}%
if $a_1/h = p_1$, $a_2/h = p_2$, $b/a_1h = q_1$, $b/a_2h = q_2$, and $a_1/bh + a_2/bh = 1$,
then $a_1/bh = \dfrac{p_1q_1}{p_1q_1 + p_2q_2}$; and if $a_1/h = a_2/h$, $a_1/bh = \dfrac{q_1}{q_1 + q_2}$, which
is equivalent to the statement that the probability of~$a_1$ when
we know $b$~is equal to $\dfrac{q_1}{q_1 + q_2}$, where $q_1$~is the probability of~$b$ when
we know~$a_1$ and $q_2$~its probability when we know~$a_2$. This
theorem enunciated with varying degrees of inaccuracy appears
in all Treatises on Probability, but is not generally proved.

\Chapref{XIV}. concludes with some elaborate theorems on the
combination of premisses based on a technical symbolic device,
known as the \emph{Cumulative Formula}, which is the work of Mr.~W.~E.
\index{Cumulative Formula!Johnson and}%
Johnson.

\Paragraph{7.} In \Chapref{XV}. I bring the non-numerical theory of
probability developed in the preceding chapters into connection
with the usual numerical conception of it, and demonstrate how
%% -----File: 133.png---Folio 122-------
and in what class of cases a meaning can be given to a numerical
measure of a relation of probability. This leads on to what
may be termed numerical approximation, that is to say, the
relating of probabilities, which are not themselves numerical,
to probabilities, which are numerical, by means of \emph{greater} and \emph{less},
by which in some cases numerical limits may be ascribed to
probabilities which are not capable of numerical measures.
%% -----File: 134.png---Folio 123-------
\index{Variables in Probability}%


\Chapter{XI}{The Theory of Groups, with special reference to
Logical Consistence, Inference, and Logical Priority}

\Paragraph{1.} The Theory of Probability deals with the relation between
two sets of propositions, such that, if the first set is known to be
true, the second can be known with the appropriate degree of
probability by argument from the first.\footnote
  {Or more strictly, ``perception of which, together with knowledge of the
  first set, justifies an appropriate degree of rational belief about the second.''}
The relation, however,
also exists when the first set is not known to be true and is hypothetical.

In a symbolical treatment of the subject it is important
that we should be free to consider \emph{hypothetical} premisses, and
to take account of relations of probability as existing between
\emph{any} pair of sets of propositions, whether or not the premiss is
actually part of knowledge. But in acting thus we must be
careful to avoid two possible sources of error.

\Paragraph{2.} The first is that which is liable to arise wherever \emph{variables}
are concerned. This was mentioned in passing in §\;18~of \Chapref{IV}\@.
We must remember that whenever we substitute for a
variable some particular value of it, this may so affect the relevant
evidence as to modify the probability. This danger is always
present except where, as in the first half of \Chapref{XIII}., the
conclusions respecting the variable are \emph{certain}.

\Paragraph{3.} The second difficulty is of a different character. Our
premisses may be hypothetical and not actually the subject of
knowledge. But must they not be \emph{possible} subjects of knowledge?
How are we to deal with hypothetical premisses which
are self-contradictory or formally inconsistent with themselves,
and which cannot be the subject of rational belief of any degree?
%% -----File: 135.png---Folio 124-------
\index{Consistence and group theory}%
\index{Groups, of propositions}%
\index{Johnson, W. E.!groups@{and groups}}%
\index{Proposition, characterisation of!groups of}%
\index{Russell, Bertrand|inote}%
\index{Russell, Bertrand!implication@{and implication}}%

Whether or not a relation of probability can be held to exist
between a conclusion and a self-inconsistent premiss, it will be
convenient to exclude such relations from our scheme, so as to
avoid having to provide for anomalies which can have no interest
in an account of the actual processes of valid reasoning. Where
a premiss is inconsistent with itself it cannot be required.

\Paragraph{4.} Let us term the collection of propositions, which are
logically involved in the premisses in the sense that they follow
from them, or, in other words, stand to them in the relation of
certainty,\footnote
  {`$a$~can be inferred from~$b$,' `$a$~follows from~$b$,' `$a$~is certain in relation to~$b$,'
  `$a$~is logically involved in~$b$,' I regard as equivalent expressions, the precise
  meaning of which will be defined in succeeding paragraphs. `$a$~is implied by~$b$,'
  I use in a different sense, namely, in Mr.~Russell's sense, as the equivalent of
  `$b$~or not-$a$.'}
the \emph{group} specified by the premisses. That is to say,
we define a group as \emph{containing} all the propositions logically
involved in any of the premisses or in any conjunction of them;
and as \emph{excluding} all the propositions the contradictories of which
are logically involved in any of the premisses or in any conjunction
of them.\footnote
  {For the conception of a \emph{group}, and for many other notions and definitions
  in the course of this chapter---those, for example, of a real group and of
  logical priority---I am largely indebted to Mr.~W.~E. Johnson. The origination
  of the theory of groups is due to him.}
To say, therefore, that a proposition follows
from a premiss, is the same thing as to say that it belongs to the
group which the premiss specifies.

The idea of a `group' will then enable us to define `logical
consistency.' If any part of the premisses specifies a group
containing a proposition, the contradictory of which is contained
in a group specified by some other part, the premisses are \emph{logically
inconsistent}; otherwise they are logically consistent. In short,
premisses are inconsistent if a proposition `follows from' one
part of them, and its contradictory from another part.

\Paragraph{5.} We have still, however, to make precise what we mean in
this definition by one proposition \emph{following from} or being \emph{logically
involved in} the truth of another. We seem to intend by these
expressions some kind of transition by means of a \emph{logical principle.}
A logical principle cannot be better defined, I think, than in terms
of what in Mr.~Russell's \emph{Logic of Implication} is termed a formal
\index{Implication}%
implication. `$p$~implies~$q$' is a \emph{formal implication} if `not-$p$~or~$q$'
is formally true; and a proposition is formally true, if it is a value
of a propositional function, in which all the constituents other
%% -----File: 136.png---Folio 125-------
\index{Groups, of propositions!definition of}%
than the arguments are logical constants, and of which all the
values are true.

We might define a \emph{group} in such a way that all logical principles
belonged to every group. In this case \emph{all} formally true propositions
would belong to every group. This definition is logically
precise and would lead to a coherent theory. But it possesses
the defect of not closely corresponding to the methods of reasoning
we actually employ, because all logical principles are not in fact
known to us. And even in the case of those which we do know,
there seems to be a logical order (to which on the above definition
we cannot give a sense) amongst propositions, which are about
logical constants and are formally true, just as there is amongst
propositions which are not formally true. Thus, if we were to
assume the premisses in every argument to include all formally
true propositions, the sphere of probable argument would be
limited to what (in contradistinction to formally true propositions)
we may term empirical propositions.

\Paragraph{6.} For this reason, therefore, I prefer a narrower definition---which
shall correspond more exactly to what we seem to mean
when we say that one proposition follows from another. Let us
define a \emph{group} of propositions as a set of propositions such that:

(i.)~if the proposition `$p$~is formally true' belongs to the group,
all propositions which are instances of the same formal propositional
function also belong to it;

(ii.)~if the proposition~$p$ and the proposition `$p$~implies~$q$'
both belong to it, then the proposition~$q$ also belongs to it;

(iii.)~if any proposition~$p$ belongs to it, then the contradictory
of~$p$ is excluded from it.

According to this definition all processes of certain inference
are wholly composed of steps each of which is of one of two simple
types (and if we like we might perhaps regard the first as comprehending
the other). I do not feel certain that these conditions
may not be narrower than what we mean when we say that one
proposition follows from another. But it is not necessary for the
purpose of defining a group, to dogmatise as to whether any other
additional methods of inference are, or are not, open to us. If
we define a group as the propositions logically involved in the
premisses in the above sense, and prescribe that the premisses of
an argument in probability must specify a group not \emph{less} extensive
than this, we are placing the \emph{minimum} amount of restriction upon
%% -----File: 137.png---Folio 126-------
%[** TN: "sub-group" hyphenated in original index; regularized.]
\index{Proposition, characterisation of!subgroups of}%
\index{Russell, Bertrand}%
\index{Subgroups of propositions}%
the form of our premisses. If, sometimes or as a rule, our
premisses in fact include some more powerful principle of argument,
so much the better.

In the formal rules of probability which follow, it will be
postulated that the set of propositions, which form the premiss
of any argument, must not be inconsistent. The premiss must,
that is to say, specify a `group' in the sense that no part of the
premiss must exclude a proposition which follows from another
part. But for this purpose we do not need to dogmatise as to
what the \emph{criterion} is of inference or certainty.

\Paragraph{7.} It will be convenient at this point to define a term which
expresses the relation converse to that which exists between a
set of propositions and the group which they specify. The propositions
$p_1, p_2 \ldots p_n$ are said to be \emph{fundamental} to the group~$h$
if (i.)~they themselves belong to the group (which involves their
being consistent with one another); (ii.)~if between them they
completely specify the group; and (iii.)~if none of them belong
to the group specified by the rest (for if $p_r$~belongs to the group
specified by the rest, this term is redundant).

When the fundamental set is \emph{uniquely} determined, a group~$h'$
is a \DPchg{sub-group}{subgroup} to the group~$h$, if the set fundamental to~$h'$ is
included in the set fundamental to~$h$.

Logically there can be more than one distinct set of propositions
fundamental to a given group; and some extra-logical test
must be applied before the fundamental set is determined uniquely.
On the other hand, a group is completely determined when the
constituent propositions of the fundamental set are given.
Further, any consistent set of propositions evidently specifies
some group, although such a set may contain propositions
\emph{additional} to those which are fundamental to the group it specifies.
It is clear also that only one group can be specified by a given
set of consistent propositions. The members of a group are,
we may say, \emph{rationally bound up} with the set of propositions
fundamental to it.

\Paragraph{8.} If Mr.~Bertrand Russell is right, the whole of pure
mathematics and of formal logic follows, in the sense defined
above, from a small number of primitive propositions. The
group, therefore, which is specified by these primitive propositions,
includes the most remote deductions not only amongst
those known to mathematicians, but amongst those which time
%% -----File: 138.png---Folio 127-------
and skill have not yet served to solve. If we define certainty
\index{Certainty}%
in a logical and not a psychological sense, it seems necessary,
if our premisses include the essential axioms, to regard as
certain all propositions which follow from these, whether or
not they are known to us. Yet it seems as if there must
be some logical sense in which unproved mathematical
theorems---some of those, for instance, which deal with the
theory of numbers---can be likely or unlikely, and in which a
proposition of this kind, which has been suggested to us by
analogy or supported by induction, can possess an intermediate
degree of probability.

There can be no doubt, I think, that the logical relation of
certainty does exist in these cases in which lack of skill or insight
prevents our apprehending it, in spite of the fact that sufficient
premisses, including sufficient logical principles, are known to us.
In these cases we must say, what we are not permitted to say
when the indeterminacy arises from lack of premisses, that the
probability is \emph{unknown}. There is still a sense, however, in which
in such a case the knowledge we actually possess can be, in a
logical sense, only probable. While the relation of certainty
exists between the fundamental axioms and every mathematical
hypothesis (or its contradictory), there are other data in relation
to which these hypotheses possess intermediate degrees of
probability. If we are unable through lack of skill to discover
the relation of probability which an hypothesis does in fact bear
towards one set of data, this set is practically useless, and we must
fix our attention on some other set in relation to which the probability
is not unknown. When Newton held that the binomial
theorem possessed for empirical reasons sufficient probability
to warrant a further investigation of it, it was not in relation to
the axioms of mathematics, whether he knew them or not, that
the probability existed, but in relation to his empirical evidence
combined, perhaps, with \emph{some} of the axioms. There is, in short,
an exception to the rule that we must always consider the probability
of any conclusion in relation to the whole of the data in
our possession. When the relation of the conclusion to the whole
of our evidence cannot be known, then we must be guided by
its relation to some part of the evidence. When, therefore, in
later chapters I speak of a formal proposition as possessing an
intermediate degree of probability, this will always be in relation
%% -----File: 139.png---Folio 128-------
to evidence from which the proposition does not logically follow
in the sense defined in~§\;6.

\Paragraph{9.} It follows from the preceding definitions that a proposition
is \emph{certain} in relation to a given premiss, or, in other words, \emph{follows
from} this premiss if it is included in the group which that premiss
specifies. It is \emph{impossible} if it is excluded from the group---if,
that is to say, its contradictory follows from the premiss. We
often say, somewhat loosely, that two propositions are contradictory
to one another, when they are inconsistent in the sense
that, relative to our evidence, they cannot belong to the same
group. On the other hand, a proposition, which is not itself
included in the group specified by the premiss and whose contradictory
is not included either, has in relation to the premiss an
intermediate degree of probability.

If $a$~follows from~$h$ and is, therefore, included in the group
specified by~$h$, this is denoted by $a/h = 1$. The relation of certainty,
\index{Certainty}%
that is to say, is denoted by the symbol of unity. The reason
why this notation is useful and has been adopted by common
consent will appear when the meaning of the \emph{product} of a pair
of relations of probability has been explained. If we represent
the relation of certainty by~$\gamma$ and any other probability by~$\DPtypo{a}{\alpha}$,
the product $\DPtypo{a}{\alpha}·\gamma = \DPtypo{a}{\alpha}$. Similarly, if $a$~is excluded from the
group specified by~$h$ and is impossible in relation to it, this is
denoted by $a/h = 0$. The use of the symbol zero to denote
impossibility arises out of the fact that, if $\omega$~denotes impossibility
and $\DPtypo{a}{\alpha}$~any other relation of probability, then, in the senses of
multiplication and addition to be defined later, the product
$\DPtypo{a}{\alpha}·\omega = \omega$, and the sum $\DPtypo{a}{\alpha} + \omega = \DPtypo{a}{\alpha}$. Lastly, if $a$~is not included
in the group specified by~$h$, this is written $a/h\neq 1$ or $a/h < 1$;
and if it is not excluded, this is written $a/h\neq 0$ or $a/h > 0$.

\Paragraph{10.} The theory of groups now enables us to give an account,
with the aid of some further conceptions, of logical priority and
of the true nature of inference. The groups, to which we refer
the arguments by which we actually reason, are not arbitrarily
chosen. They are determined by those propositions of which
we have direct knowledge. Our group of reference is specified
by those direct judgments in which we personally \emph{rationally
certify} the truth of some propositions and the falsity of others.
So long as it is undetermined, or not determined uniquely,
which propositions are fundamental, it is not possible to discover
%% -----File: 140.png---Folio 129-------
%[** TN: "sub-group" hyphenated in original index; regularized.]
\index{Groups, of propositions!real and hypothetical}%
\index{Proposition, characterisation of!subgroups of}%
\index{Subgroups of propositions}%
a necessary order amongst propositions or to show in what way
a true proposition `follows from' one true premiss rather than
another. But when we have determined what propositions are
fundamental, by selecting those which we know directly to be true,
or in some other way, then a meaning can be attached to priority
and to the distinction between inference and implication. When
\index{Inference}%
the propositions which we know directly are given, there is a
logical order amongst those other propositions which we know
indirectly and by argument.

\Paragraph{11.} It will be useful to distinguish between those groups which
are hypothetical and those of which the fundamental set is known
to be true. We will term the former \emph{hypothetical groups} and the
latter \emph{real groups}. To the real group, which contains all the
propositions which are known to be true, we may assign the old
logical term \emph{Universe of Reference}. While knowledge is here
\index{Universe of reference}%
taken as the criterion of a real group, what follows will be equally
valid whatever criterion is taken, so long as the fundamental set
is in some manner or other determined uniquely.

If it is impossible for us to know a proposition~$p$ except by
inference from a knowledge of~$q$, so that we cannot know $p$~to be
true unless we already know~$q$, this may be expressed by saying
that `$p$~requires~$q$'. More precisely \emph{requirement} is defined as
\index{Requirement}%
follows:

\textit{$p$~does not require~$q$} if there is some real group to which $p$~belongs
and $q$~does not belong, \ie\ if there is a real group~$h$
such that $p/h = 1$, $q/h \neq 1$; hence

\textit{$p$~requires~$q$} if there is \emph{no} real group to which $p$~belongs
and $q$~does not belong.

\textit{$p$~does not require~$q$ within the group~$h$}, if the group~$h$, to which
$p$~belongs, contains a subgroup\footnotemark~$h'$
\footnotetext{Subgroups have only been defined, it must be noticed (see §\;7 above) when
  the fundamental set of the group has been, in some way, uniquely determined.}
to which $p$~belongs and $q$~does
not belong; \ie\ if there is a group~$h'$ such that $h'/h = 1$, $p/h' = 1$,
$q/h' \neq 1$. This reduces to the proposition next but one above
if $h$~is the Universe of Reference. In §\;13 these definitions
will be generalised to cover intermediate degrees of probability.

\Paragraph{12.} Inference and logical priority can be defined in terms of
\index{Logical priority}%
requirement and real groups. It is convenient to distinguish
two types of inference corresponding to hypothetical and real
%% -----File: 141.png---Folio 130-------
groups---\ie\ to cases where the argument is only hypothetical,
and cases where the conclusion can be asserted:

\textit{Hypothetical Inference.}---`If $p$,~$q$,' which may also be read
\index{Inference!hypothetical and assertoric}%
`$q$~is hypothetically inferrible from~$p$,' means that there is a
real group~$h$ such that $q/ph = 1$, and $q/h \neq 1$. In order that this
may be the case, $ph$~must specify a group; \ie\ $p/h \neq 0$, or in
other words $p$~must not be excluded from~$h$. Hypothetical
inference is also equivalent to: `$p$~implies~$q$' and `$p$~implies~$q$'
does not require~`$q$'. In other words, $q$~is hypothetically
inferrible from~$p$, if we know that $q$~is true or $p$~is false and if
we can know this without first knowing either that $q$~is true or
that $p$~is false.

\textit{Assertoric Inference.}---`$p \therefore q$,' which may be read `$p$~therefore~$q$'
or `$q$~may be asserted by inference from~$p$,' means that `if~$p$,~$q$'
is true, and in addition `$p$'~belongs to a real group; \ie\ there
are proper groups $h$~and~$h'$ such that $p/h = 1$, $q/ph' = 1$, $q/h' \neq 1$,
and $p/h' \neq 0$.

\textit{$p$~is prior to~$q$} when $p$~does not require~$q$, and $q$~requires~$p$,
when, that is to say, we can know~$p$ without knowing~$q$, but
not~$q$ unless we first know~$p$.

\textit{$p$~is prior to~$q$ within the group~$h$} when $p$~does not require~$q$
within the group, and $q$~does require~$p$ within the group.

It follows from this and from the preceding definitions that,
if a proposition is fundamental in the sense that we can only
know it directly, there is no proposition prior to it; and, more
generally, that, if a proposition is fundamental to a given
group, there is no proposition prior to it within the group.

\Paragraph{13.} We can now apply the conception of requirement to
intermediate degrees of probability. The notation adopted is,
it will be remembered, as follows:

$p/h = \alpha$ means that the proposition~$p$ has the probable relation
of degree~$\alpha$ to the proposition~$h$; while it is postulated that $h$~is
self-consistent and therefore specifies a group.

$p/h = 1$ means that $p$~follows from~$h$ and is, therefore, included
in the group specified by~$h$.

$p/h = 0$ means that $p$~is excluded from the group specified by~$h$.

If $h$~specifies the Universe of Reference, \ie\ if its group comprehends
\index{Universe of reference}%
the whole of our knowledge, $p/h$~is called \emph{the absolute
probability of~$p$}, or (for short) \emph{the probability of~$p$}; and if $p/h = 1$
and $h$~specifies any real group, $p$~is said to be \emph{absolutely certain}
%% -----File: 142.png---Folio 131-------
or (for short) \emph{certain}. Thus $p$~is `certain' if it is a member of a
real group, and a `certain' proposition is one which we know
to be true. Similarly if $p/h = 0$ under the same conditions, $p$~is
\emph{absolutely impossible}, or (for short) \emph{impossible}. Thus an `impossible'
proposition is one which we know to be false.

The definition of requirement, when it is generalised so as to
take account of intermediate degrees of probability, becomes, it
will be seen, equivalent to that of relevance:

\emph{The probability of~$p$ does not require~$q$ within the group~$h$}, if
there is a subgroup~$h'$ such that, for every subgroup~$h''$ which
includes~$h'$ and is included in~$h$ (\ie\ $h'/h'' = 1$, $h''/h = 1$), $p/h'' = p/h'$,
and $q/h' \neq q/h$.

When $p$~is included in the group~$h$, this definition reduces to
the definition of requirement given in~§\;11.

\Paragraph{14.} The importance of the theory of groups arises as soon as
we admit that there are \emph{some} propositions which we take for
granted without argument, and that all arguments, whether
demonstrative or probable, consist in the relating of other conclusions
to these as premisses.

The particular propositions, which are in fact fundamental
to the Universe of Reference, vary from time to time and from
person to person. Our theory must also be applicable to hypothetical
Universes. Although a particular Universe of Reference
may be defined by considerations which are partly psychological,
when once the Universe is given, our theory of the relation in
which other propositions stand towards it is entirely logical.

The formal development of the theory of argument from
imposed and limited premisses, which is attempted in the following
chapters, resembles in its general method other parts of formal
logic. We seek to establish implications between our primitive
axioms and the derivative propositions, without specific reference
to what particular propositions are fundamental in our actual
Universe of Reference.

It will be seen more clearly in the following chapters that the
laws of inference are the laws of probability, and that the former
is a particular case of the latter. The relation of a proposition to
a group depends upon the relevance to it of the group, and a
group is relevant in so far as it contains a necessary or sufficient
condition of the proposition, or a necessary or sufficient condition
of a necessary or sufficient condition, and so on; a condition
%% -----File: 143.png---Folio 132-------
being necessary if every hypothetical group, which includes the
proposition together with the Universe of Reference, includes
the condition, and sufficient if every hypothetical group, which
includes the condition together with the Universe of Reference,
includes the proposition.
%% -----File: 144.png---Folio 133-------


\Chapter{XII}{The Definitions and Axioms of Inference and Probability}

\Paragraph{1.} \First{It} is not necessary for the validity of what follows to decide
in what manner the set of propositions is determined, which is
fundamental to our Universe of Reference, or to make definite
assumptions as to what propositions are included in the group
which is specified by the \textit{data}. When we are investigating an
empirical problem, it will be natural to include the whole of
our logical apparatus, the whole body, that is to say, of
formal truths which are known to us, together with that part
of our empirical knowledge which is relevant. But in the
following formal developments, which are designed to display
the logical rules of probability, we need only assume that our data
always include those logical rules, of which the steps of our
proofs are instances, together with the axioms relating to probability
which we shall enunciate.

The object of this and the chapters immediately following is
to show that all the usually assumed conclusions in the fundamental
logic of inference and probability follow rigorously from
a few axioms, in accordance with the fundamental conceptions
expounded in \Partref{I}\@. This body of axioms and theorems
corresponds, I think, to what logicians have termed the \emph{Laws of
Thought}, when they have meant by this something narrower than
the whole system of formal truth. But it goes beyond what has
been usual, in dealing at the same time with the laws of probable,
as well as of necessary, inference.

\Paragraph{2.} This and the following chapters of \Partref{II}. are largely
independent of many of the more controversial issues raised in
the preceding chapters. They do not prejudge the question as
%% -----File: 145.png---Folio 134-------
\index{Definitions|ifoll}%
\index{Equivalence, definition of}%
\index{Probability relation}%
\index{Proposition, characterisation of!disjunction and conjunction of}%
to whether or not all probabilities are theoretically measurable;
and they are not dependent on our theories as to the part played
by direct judgment in establishing relations of probability or
inference between particular propositions. Their premisses are
all \emph{hypothetical}. \emph{Given} the existence of certain relations of
probability, others are inferred. Of the conclusions of \Chapref{III}.,
of the criteria of equiprobability and of inequality discussed
in Chapters \Chapref[]{IV}.~and~\Chapref[]{V}., and of the criteria of inference discussed
in §§\;5,~6 of \Chapref{XI}., they are, I think, wholly independent.
They deal with a different part of the subject, not so closely
connected with epistemology.

\Paragraph{3.} In this chapter I confine myself to Definitions and Axioms.

Propositions will be denoted by small letters, and relations
by capital letters. In accordance with common usage, a disjunctive
combination of propositions is represented by the sign
of addition, and a conjunctive combination by simple juxtaposition
(or, where it is necessary for clearness, by the sign of
multiplication): \eg\ `$a$~or $b$ or~$c$' is written `$a + b + c$,' and `$a$~and
$b$ and~$c$' is written~`$abc$.' `$a + b$'~is not so interpreted as to
exclude `$a$~and~$b$.' The contradictory of~$a$ is written~$\bar{a}$.

\Paragraph{4.} \textit{Preliminary Definitions}:

I\@. If there exists a relation of probability~$P$ between the
proposition~$a$ and the premiss~$h$
\begin{DPgather*}
a/h = P\DPtypo{}{.}
\rintertext{Def.}
\end{DPgather*}

II\@. If $P$~is the relation of certainty\index{Certainty!relation of}\footnote
  {These symbols were first employed by Leibnitz. See p.~155 below.}
\begin{DPgather*}
P = 1\DPtypo{}{.}
\rintertext{Def.}
\end{DPgather*}

III\@. If $P$~is the relation of impossibility\footnotemark[1]
\index{Impossibility!relation of}%
%  {These symbols were first employed by Leibnitz. See p.~155 below.}
\begin{DPgather*}
P = 0\DPtypo{}{.}
\rintertext{Def.}
\end{DPgather*}

IV\@. If $P$~is a relation of probability, but not the relation of
certainty
\begin{DPgather*}
P < 1.
\rintertext{Def.}
\end{DPgather*}

V\@. If $P$~is a relation of probability, but not the relation of
impossibility
\begin{DPgather*}
P > 0.
\rintertext{Def.}
\end{DPgather*}

VI\@. If $a/h = 0$, the conjunction~$ah$ is \emph{inconsistent}. \hfill Def.

VII\@. The class of propositions~$a$ such that $a/h = 1$ \emph{is the
group specified} by~$h$ or (for short) \emph{the group~$h$}. \hfill Def.

VIII\@. If $b/ah = 1$ and $a/bh = 1$, $(a \equiv b)/h = 1$. \hfill Def.

This may be regarded as the definition of \emph{Equivalence}. Thus
we see that equivalence is relative to a premiss~$h$. $a$~is equivalent
to~$b$, given~$h$, if $b$~follows from~$ah$, and $a$~from~$bh$.
%% -----File: 146.png---Folio 135-------
\index{Addition, of probabilities}%
\index{Axioms|ifoll}%
\index{Equivalence, definition of!axiom of}%

\Paragraph{5.} \textit{Preliminary Axioms}:

We shall assume that there is included in every premiss with
which we are concerned the formal implications which allow us
to assert the following axioms:

(i.)\ Provided that $a$~and~$h$ are propositions or conjunctions
of propositions or disjunctions of propositions, and that $h$~is not
an inconsistent conjunction, there exists one and only one relation
of probability~$P$ between $a$~as conclusion and $h$~as premiss.
Thus any conclusion~$a$ bears to any consistent premiss~$h$ one and
only one relation of probability.

(ii.)\ If $(a \equiv b)/h = 1$, and $x$~is a proposition, $x/ah=x/bh$. This
is the Axiom of Equivalence.
\begin{DPalign*}
\lintertext{\indent(iii.)}
(\,\overline{a+b} \equiv \bar{a} \bar{b}\,)/h &= 1 \\
                              (aa \equiv a)/h &= 1 \\
          (\,\overline{\bar{a}} \equiv a\,)/h &= 1 \\
                   (ab + \bar{a}b \equiv b)/h &= 1. \\
                                \text{If }a/h &= 1, ah \equiv h.
\end{DPalign*}
That is to say, %[** TN: Not preserving book's formatting]
if $a$~is included in the group specified by~$h$, $h$~and~$ah$ are
equivalent.

\Paragraph{6.} \textit{Addition and Multiplication}.---If we were to assume that
\index{Multiplication}%
probabilities are numbers or ratios, these operations could be
given their usual arithmetical signification. In adding or
multiplying probabilities we should be simply adding or multiplying
numbers. But in the absence of such an assumption, it
is necessary to give a meaning by definition to these processes.
I shall define the addition and multiplication of relations of
probabilities only for certain types of such relations. But it
will be shown later that the limitation thus placed on our operations
is not of practical importance.

We define the \emph{sum} of the probable relations $ab/h$ and~$a\bar{b}/h$
as being the probable relation~$a/h$; and the \emph{product} of the probable
relations $a/bh$~and~$b/h$ as being the probable relation~$ab/h$. That
is to say:
\begin{DPgather*}
\lintertext{\indent IX\@.}
ab/h + a\bar{b}/h = ah.
\rintertext{Def.} \\
\lintertext{\indent X\@.}
ab/h = a/bh· b/h = b/ah· a/h.
\rintertext{Def.}
\end{DPgather*}

Before we proceed to the axioms which will make these symbols
operative, the definitions may be restated in more familiar
language. IX.~may be read: ``The sum of the probabilities
of `both $a$~and~$b$' and of `$a$~but not~$b$,' relative to the same
hypothesis, is equal to the probability of~`$a$' relative to this hypothesis.''
%% -----File: 147.png---Folio 136-------
X.~may be read: ``The probability of `both $a$~and~$b$,'
assuming~$h$, is equal to the product of the probability of~$b$, assuming~$h$,
and the probability of~$a$, assuming both $b$~and~$h$.'' Or in
the current terminology\footnote
  {\Eg\ Bertrand, \textit{Calcul des probabilités}, p.~26.}
\index{Bertrand!on multiplication}%
we should have: ``The probability
that both of two events will occur is equal to the probability of
the first multiplied by the probability of the second, assuming
the occurrence of the first.'' It is, in fact, the ordinary rule for
the multiplication of the probabilities of events which are not
`independent.' It has, however, a much more central position
in the development of the theory than has been usually recognised.

Subtraction and division are, of course, defined as the inverse
operations of addition and multiplication:

XI\@. If $PQ = R$, $P = \dfrac{R}{Q}$.\hfill Def.

XII\@. If $P + Q = R$, $P = R - Q$.\hfill Def.

Thus we have to introduce as definitions what would be axioms
if the meaning of addition and multiplication were already defined.
In this latter case we should have been able to apply the ordinary
processes of addition and multiplication without any further
axioms. As it is, we need axioms in order to make these symbols,
to which we have given our own meaning, operative. When
certain properties are associated, it is often more or less arbitrary
which we take as defining properties and which we associate
with these by means of axioms. In this case I have found it
more convenient, for the purposes of formal development, to
reverse the arrangement which would come most natural to
\DPtypo{commonsense}{common sense}, full of preconceptions as to the meaning of addition
and multiplication. I define these processes, for the theory of
probability, by reference to a comparatively unfamiliar property,
and associate the more familiar properties with this one by means
of axioms. These axioms are as follows:

(iv.)\ If $P$,~$Q$,~$R$ are relations of probability such that the
products $PQ$,~$PR$ and the sums $P + Q$, $P + R$ exist, then:

(iv.\textit{a}) If $PQ$~exists, $QP$~exists, and $PQ = QP$. If $P + Q$ exists,
$Q + P$ exists and $P + Q = Q + P$.

(iv.\textit{b}) $PQ < P$ unless $Q = 1$ or $P=0$; $P + Q > P$ unless $Q = 0$.

\PadTxt{(iv.\textit{b})}{} $PQ = P$ \PadTxt{unless}{if} $Q = 1$ or $P=0$; $P + Q = P$ \PadTxt{unless}{if} $Q = 0$.

(iv.\textit{c}) If $PQ \lesseqqgtr PR$, then $Q\lesseqqgtr R$ unless $P = 0$. If $P + Q\lesseqqgtr P + R$,
then $Q \lesseqqgtr R$ and conversely.
%% -----File: 148.png---Folio 137-------

A meaning has not been given, it is important to notice, to
the signs of addition and multiplication between probabilities
\emph{in all cases}. According to the definitions we have given, $P + Q$
and~$PQ$ have not an interpretation whenever $P$~and~$Q$ are
relations of probability, but in certain conditions only. Furthermore,
if $P + Q = R$ and $Q = S + T$, it does not follow that
$P + S + T = R$, since no meaning has been assigned to such an
expression as $P + S + T$. The equation must be written $P + (S + T)
= R$, and we cannot infer from the foregoing axioms that
$(P + S) + T = R$. The following axioms allow us to make this
and other inferences in cases in which the sum~$P+S$ exists, \ie\
when $P + S = A$ and $A$~is a relation of probability.
\begin{DPalign*} %[** TN: Reformatting]
\lintertext{\indent (v.)}
[±P±Q] + [±R±S]   &= [±P±R] - [\mp Q\mp S] \\
&= [±P±R] + [±Q±S] \\
&= [±P±Q] - [\mp R\mp S]
\end{DPalign*}
in every case in which the probabilities $[±P±Q]$, $[±R±S]$,
$[±P±R]$, etc., exist, \ie, in which these sums satisfy the conditions
necessary in order that a meaning may be given to them
in the terms of our definition.

(vi.)\ $P(R±S) = PR ± PS$, if the sum~$R±S$ and the products
$PR$~and~$PS$ exist as probabilities.

\Paragraph{7.} From these axioms it is possible to derive a number of
propositions respecting the addition and multiplication of probabilities.
They enable us to prove, for instance, that if $P + Q =
R + S$ then $P - R = S - Q$, provided that the differences $P-R$~and~$S-Q$
exist; and that $(P + Q)(R + S) = (P + Q)R + (P + Q)S =
[PR + QR] + [PS + QS] = [PR + QS] + [QR + PS]$, provided that
the sums and products in question exist. In general any rearrangement
which would be legitimate in an equation between
arithmetic quantities is also legitimate in an equation between
probabilities, provided that our initial equation and the equation
which finally results from our symbolic operations can both be
expressed in a form which contains only products and sums which
have an interpretation as probabilities in accordance with the
definitions. If, therefore, this condition is observed, we need not
complicate our operations by the insertion of brackets at every
stage, and no result can be obtained as a result of leaving them
out, if it is of the form prescribed above, which could not be
obtained if they had been rigorously inserted throughout. We
can only be interested in our final results when they deal with
actually existent and intelligible probabilities---for our object is,
%% -----File: 149.png---Folio 138-------
\index{Independence, for knowledge!definition of}%
always, to compare one probability with another---and we are
not incommoded, therefore, in one symbolic operations by the
circumstance that sums and products do not exist between
every pair of probabilities.

\Paragraph{8.} \textit{Independence}:

XIII\@. If $a_1/a_2h = a_1/h$ and $a_{2}/a_{1}h=a_{2}/h$, the probabilities
$a_1/h$~and~$a_2/h$ are \emph{independent}. \hfill Def.

Thus the probabilities of two arguments having the same
premisses are independent, if the addition to the premisses of the
conclusion of either leaves them unaffected.

\textit{Irrelevance}:\index{Irrelevance!definition of}\footnote
  {This is repeated for convenience of reference from \Chapref{IV}. §\;14. It is
  only necessary here to take account of \emph{irrelevance on the whole}, not of the more
  precise sense.}

XIV\@. If $a_1/a_2h = a_1/h$, $a_2$~is \emph{irrelevant on the whole}, or, for
short, \emph{irrelevant} to~$a_1/h$. \hfill Def.
%% -----File: 150.png---Folio 139-------
\index{De Morgan!inference@{and inference}}%
\index{Probability, and relevant knowledge!negative}%


\Chapter{XIII}{The Fundamental Theorems of Necessary Inference}
\index{Inference!necessary}%

\Paragraph{1.} \First{In} this chapter we shall be mainly concerned with deducing
the existence of relations of certainty or impossibility, given other
relations of certainty or impossibility,---with the rules, that is to
say, of \emph{Certain} or, as De~Morgan termed it, of \emph{Necessary} Inference.
But it will be convenient to include here a few theorems dealing
with intermediate degrees of probability. Except in one or two
important cases I shall not trouble to translate these theorems
from the symbolism in which they are expressed, since their
interpretation presents no difficulty.

\Paragraph{2.} (1) $a/h + \bar{a}/h = 1$.
\begin{DPgather*}
\lintertext{For}
  ab/h + \bar{a}b/h = b/h
  \rintertext{by IX.,}\\
%
  a/bh · b/h + \bar{a}/bh · b/h = b/h
  \rintertext{by X.}\\
%
\lintertext{Put}
  b/h = 1, \text{ then }a/bh + \bar{a}/bh = 1
  \rintertext{by (iv.~\textit{b}),}\\
%
\lintertext{since}
  b/h = 1,\quad bh\equiv h
  \rintertext{by (iii.).}\\
%
\lintertext{Thus}
  a/h + \bar{a}/h = 1
  \rintertext{by (ii.).}
\end{DPgather*}

(1.1) If $a/h = 1$, $\bar{a}/h = 0$,
\begin{DPgather*}
a/h + \bar{a}/h = 1
  \rintertext{by (1),}\\
%
\therefore a/h + \bar{a}/h = a/h = a/h + 0
  \rintertext{by (iv.~\textit{b}),}\\
%
\therefore \bar{a}/h = 0
  \rintertext{by (iv.~\textit{c}).}
\end{DPgather*}

(1.2) Similarly, if $\bar{a}/h=1$, $a/h=0$.

(1.3) If $a/h=0$, $\bar{a}/h=1$,
\begin{DPgather*}
  a/h + \bar{a}/h = 1
  \rintertext{by (1),}\\
%
\therefore 0 + \bar{a}/h = 0 + 1
  \rintertext{by (iv.~\textit{b}),}\\
%
\therefore \bar{a}/h = 1
  \rintertext{by (iv.~\textit{c}).}
\end{DPgather*}

(1.4) Similarly, if $\bar{a}/h = 0$, $a/h = 1$.
\begin{DPgather*}
\lintertext{\indent(2)}
  a/h < 1 \text{ or } a/h = 1
  \rintertext{by IV.}\\
%
\lintertext{\indent(3)}
  a/h > 0 \text{ or } a/h = 0
  \rintertext{by V.,}
\end{DPgather*}
\ie\ there are no negative probabilities.
%% -----File: 151.png---Folio 140-------
\begin{DPgather*}
\lintertext{\indent(4)}
  \text{$ab/h < b/h$ or $ab/h = b/h$}
  \rintertext{by X. and (iv.~\textit{b}).}
\end{DPgather*}
If $P$~and~$Q$ are relations of probability and $P + Q = 0$,
then $P=0$ and $Q=0$.
\begin{DPgather*}
\text{$P+Q > P$ unless $Q = 0$}
  \rintertext{by (iv.~\textit{b}),}\\
%
\lintertext{and}
  \text{$P>0$ unless $P = 0$}
  \rintertext{by V.}\\
%
\text{$\therefore P+Q>0$ unless $Q = 0$.}
\end{DPgather*}
Hence, if $P + Q = 0$, $Q = 0$ and similarly $P = 0$.

(6)~If $PQ = 0$, $P = 0$ or $Q = 0$,
\begin{DPgather*}
\text{$Q > 0$ unless $Q = 0$}
  \rintertext{by V.}\\
%
\lintertext{Hence}
  \text{$PQ > P· 0$ unless $Q = 0$ or $P=0$}
  \rintertext{by (iv.~\textit{c}),}\\
%
\lintertext{\ie}
  \text{$PQ > 0$ unless $Q = 0$ or $P = 0$}
  \rintertext{by (iv.~\textit{b}).}\\
%
\intertext{Whence, if $PQ = 0$, the result follows.}
%
\intertext{\indent(7)~If $PQ=1$, $P=1$ and $Q=1$,}\\
%
\text{$PQ < P$ unless $P = 0$ or $Q = 1$}
  \rintertext{by (iv.~\textit{b}),}\\
%
\text{$PQ = P$ if $P = 0$ or $Q = 1$}
  \rintertext{by (iv.~\textit{b}),}\\
%
\lintertext{and}
  \text{$P < 1$ unless $P = 1$}
  \rintertext{by IV.,}\\
%
\text{$\therefore PQ < 1$ unless $P = 1$.} \\
%
\intertext{Hence $P = 1$; similarly $Q = 1$.}
\end{DPgather*}

(8)~If $a/h = 0$, $ab/h = 0$ and $a/bh = 0$ if $bh$ is not inconsistent.
\begin{DPgather*}
\lintertext{For}
  \text{$ab/h = b/ah · a/h = a/bh · b/h$}
  \rintertext{by X.,}\\
%
\lintertext{\PadTxt[l]{and since}{and since $a/h = 0$,}}
  \text{$b/ah · a/h = 0$}
  \rintertext{by (iv.~\textit{b}),}\\
%
\text{$\therefore ab/h = 0$ and $a/bh · b/h = 0$,}\\
\text{$\therefore$ unless $b/h = 0$, $a/bh = 0$}
  \rintertext{by (5),}
\end{DPgather*}
whence the result by~VI\@.

Thus, if a conclusion is impossible, we may add to the conclusion
or add consistently to the premisses without affecting the
argument.

(9)~If $a/h = 1$, $a/bh = 1$ if $bh$ is not inconsistent.
\begin{DPgather*}
\lintertext{Since $a/h = 1$,}
  \bar{a}/h = 0
  \rintertext{by (1.1),}\\
%
\intertext{$\therefore \bar{a}/bh = 0$ by~(8) if $bh$ is not inconsistent,}\\
\lintertext{whence}
  a/bh = 1
  \rintertext{by (1.4).}
\end{DPgather*}

Thus we may add to premisses, which make a conclusion
certain, any other premisses not inconsistent with them, without
affecting the result.

(10)~If $a/h = 1$, $ab/h = b/ah = b/h$,
\begin{DPgather*}
ab/h = b/ah · a/h = a/bh · b/h
  \rintertext{by X.}\\
%
\intertext{Since $a/h = 1$, $a/bh = 1$ by~(9) unless $b/h = 0$,}\\
%
\text{$\therefore b/ah · a/h = b/ah$ and $a/bh · b/h = b/h$}
  \rintertext{by (iv.~\textit{b}),}
\end{DPgather*}
whence the result, unless $b/h = 0$.
%% -----File: 152.png---Folio 141-------
\index{Equivalence, definition of!principle of}%
If $b/h = 0$, the result follows from (8).

(11)~If $ab/h = 1$,  $a/h = 1$.
\begin{DPgather*}
\lintertext{For}   ab/h = b/ah · a/h                  \rintertext{by X.,} \\
                   \therefore\: a/h = 1                        \rintertext{by (7).}
\end{DPgather*}

(12)~If $(a \equiv b)/h = 1$,  $a/h = b/h$,
\begin{DPgather*}
                   b/ah · a/h = a/bh · b/h   \rintertext{by X.}\\
\lintertext{and}   b/ah = 1, a/bh = 1                          \rintertext{by VIII.,}\\
                   \therefore a/h= b/h                         \rintertext{by (iv.~b).}
\end{DPgather*}

(12.1)~If $(a \equiv b)/h = 1$ and $hx$ is not inconsistent,
\begin{DPgather*}
                   a/hx = b/hx.\\
                   a/hx· x/h = x/ah · a/h,\\
\lintertext{and}   b/hx · x/h = x/bh · b/h   \rintertext{by X.,}\\
                   x/ah = x/bh                                 \rintertext{by (ii.),}\\
\lintertext{and}   a/h  = b/h                                  \rintertext{by (12),}\\
                   \therefore a/hx = b/hx\text{ unless }x/h = 0.
\end{DPgather*}

This is the \emph{principle of equivalence}. In virtue of it and of
axiom (ii.), if $(a \equiv b)/h = 1$, we can substitute $a$~for~$b$ and \textit{vice versa},
wherever they occur in a probability whose premisses include $h$.

(13)~$a/a= 1$, unless $a$ is inconsistent.
\begin{DPgather*}
\lintertext{For}   a/a = aa/a = a/aa· a/a             \rintertext{by (iii.), (12), and X.,}
\end{DPgather*}
whence $a/aa = 1$ by (ii.), unless $a/a = 0$,
\begin{DPgather*}
\lintertext{\ie} a/a = 1, \text{ unless $a$ is inconsistent} \rintertext{by (iii.), (12), and VI.}
\end{DPgather*}

(13.1)~$\bar{a}/a = 0$, unless $a$ is inconsistent. This follows from
(13)~and~(1.1).

(13.2)~$a/\bar{a} = 0$, unless $\bar{a}$ is inconsistent. This follows from
(iii.)\ by writing $\bar{a}$ for $a$ in (13.1).

(14)~If $a/b = 0$ and $a$~is not inconsistent, $b/a = 0$.

Let $f$ be the group of assumptions, common to $a$~and~$b$, which
we have supposed to be included in every real group;
\begin{DPgather*}
\lintertext{then}     a/b = a/bf \text{ and } b/a = b/af             \rintertext{by (iii.)\ and (12),}\\
\lintertext{and}      a/bf · b/f = b/af · a/f      \rintertext{by X.}\\
\lintertext{Since}    a/bf = 0 \text{ by hypothesis,}\\
\lintertext{and}      a/f \neq 0, \text{ since $a$ is not inconsistent,}\\
                      \therefore b/af = 0,\\
\lintertext{whence}   b/a = 0.
\end{DPgather*}
Thus, if $a$ is impossible given~$b$, then $b$~is impossible given~$a$.

(15)~If $h_1/h_2 = 0$, $h_1h_2/h = 0$,
\begin{DPgather*}
  h_1/h_2/h = h_1/h_2h · h_2/h  \rintertext{by X.,}
\end{DPgather*}
and since $h_1/h_2 = 0$, $h/h_2h = 0$ by~(8), unless $h/h_2 = 0$, whence
the result by~(iv.~b), unless $h/h_2 = 0$.
%% -----File: 153.png---Folio 142-------
\begin{DPgather*}
\lintertext{\indent If}
h/h_2 = 0,\quad h_2/h = 0
  \rintertext{by~(14),}\\
\intertext{since we assume that $h$~is not inconsistent, and hence}
h_1h_2/h = 0
  \rintertext{by~(8).}
\end{DPgather*}
Thus, if $h_1$ is impossible given~$h_2$, $h_1h_2$~is always impossible and is
excluded from every group.

(15.1) If $h_1h_2/h = 0$ and $h_2h$~is not inconsistent, $h_1/h_2h = 0$.
This, which is the converse of~(15), follows from X.~and~(6).

(16) If $h_1/h_2 = 1$, $(h_1 + \bar{h}_2)/h = 1$,
\begin{DPgather*}
\bar{h}_1/h_2 = 0
  \rintertext{by~(1),}\\
\therefore \bar{h}_1h_2/h = 0
  \rintertext{by~(15),}\\
\therefore \overline{h_1 h_2}/h = 1
  \rintertext{by~(1.3),}\\
\therefore (h_1 + \bar{h}_2)/h = 1
  \rintertext{by (12)~and~(iii.).}
\end{DPgather*}

(16.1) We may write~(16):

If $h_1/h_2 = 1$, $(h_2 \supset h_1)/h = 1$, where `$\supset$'~symbolises `implies.'
Thus if $h_1$~follows from~$h_2$, then it is always certain that
$h_2$~implies~$h_1$.

(16.2) If $(h_1 + \bar{h}_2)/h = 1$ and $h_2h$~is not inconsistent,
$h_1/h_2h = 1$.
\begin{DPgather*}
\bar{h}_1h_2/h = 0,\quad \text{as in~(16),}\\
\therefore \bar{h}_1/h_2h = 0\quad \text{by~(15.1), since $h_2h$~is not inconsistent,}\\
\therefore h_1/h_2h = 1
  \rintertext{\llap{by~(1.4).}}
\end{DPgather*}
This is the converse of~(14).

(16.3) We may write~(16.2):

If $(h_2 \supset h_1)/h = 1$ and $h_2h$~is not inconsistent, $h_1/h_2h = 1$.
Thus, if we define a `group' as a set of propositions, which follow
from and are certain relatively to the proposition which specifies
them, this proposition proves that, if $h_2 \supset h_1$ and~$h_2$ belong to a
group~$h_2h$, then $h_1$~also belongs to this group.

(17) If $(h_1 \supset: a \equiv b)/h = 1$ and $h_1h$~is not inconsistent, $a/h_1h
= b/h_1h$. This follows from (16.3)~and~(12).

(18) $a/a = 1$ or $\bar{a}/\bar{a} = 1$.
\begin{DPgather*}
\bar{a}/a = 1,\text{ unless $a$~is inconsistent,}
  \rintertext{by~(13).}\\
\intertext{\indent If $a$ is inconsistent, $a/h = 0$, where $h$~is not inconsistent, and therefore}
\bar{a}/h = 1
  \rintertext{by~(1.3).}\\
\intertext{Thus unless $a$ is inconsistent, $\bar{a}$~is not inconsistent, and therefore}
\bar{a}/\bar{a} = 1
  \rintertext{by~(13).}\\
\lintertext{\indent (19) \rlap{$a\bar{a}/h = 0$,}} \\
\bar{a}/\bar{a} = 1 \text{ or } a/a = 1
  \rintertext{by~(18),}\\
\therefore a/\bar{a} = 0 \text{ or } \bar{a}/a = 0
  \rintertext{\llap{by (1.1)~and~(1.2).}}
\end{DPgather*}
In either case $a\bar{a}/h = 0$ by~(15).
%% -----File: 154.png---Folio 143-------
\index{Excluded Middle, Law of}%

Thus it is impossible that both $a$ and its contradictory
should be true. This is the Law of Contradiction.
\index{Contradiction}%

(20) $(a + \bar{a})/h = 1$.
\begin{DPgather*}
\lintertext{Since}
(a\bar{a} \equiv \overline{a + \bar{a}})/h = 1
  \rintertext{by~(iii.),} \\
%
\overline{a + \bar{a}}/h = 0
  \rintertext{by (19)~and~(12),} \\
%
\therefore (a + \bar{a})/h = 1
  \rintertext{by~(1.3).}
\end{DPgather*}
Thus it is certain that either $a$~or its contradictory is true. This
is the Law of Excluded Middle.

(21) If $a/h_1 = 1$ and $a/h_2 = 0$, $h_1h_2/h = 0$.
\begin{DPgather*}
\lintertext{For}
a/h_1h_2 · h_1/h_2 = h_1/ah_2 · ah_2, \\
%
\lintertext{and}
\bar{a}/h_1h_2 · h_2/h_1 = h_2/\bar{a}h_1 · \bar{a}/h_1
  \rintertext{by~X.,} \\
%
\therefore a/h_1h_2 · h_1/h_2 = 0 \text{ and } \bar{a}/h_1h_2 · h_2/h_1 = 0, \\
\intertext{since, by hypothesis and~(1), $\bar{a}/h_1 = 0$ and $a/h_2 = 0$,}
%
\therefore a/h_1h_2 = 0 \text{ or } h_1/h_2 = 0, \\
\lintertext{and}
a/h_1h_2 = 1 \text{ or } h_2/h_1 = 0, \\
%
\therefore h_1/h_2 = 0 \text{ or } h_2/h_1 = 0.
\end{DPgather*}
In either case $h_1h_2/h = 0$ by~(15).

Thus, if a proposition is certain relatively to one set of
premisses, and impossible relatively to another set, the two sets
are incompatible.

(22) If $a/h_1 = 0$ and $h_1/h = 1$, $a/h = 0$,
\begin{gather*}
ah_1/h = 0 \text{ by~(15),}\quad \therefore h_1/ah · a/h = 0, \\
h_1/ah = 1 \text{ by~(9), unless } a/h = 0. \\
\therefore \text{ in any case $a/h = 0$.}
\end{gather*}

(23) If $b/a = 0$ and $b/\bar{a} = 0$, $b/h = 0$.
\begin{DPgather*}
ab/h = 0 \text{ and } \bar{a}b/h = 0
  \rintertext{by~(15),} \\
%
\therefore a/bh = 0 \text{ or } b/h = 0, \\
\lintertext{and}
\bar{a}/bh = 0 \text{ or } b/h = 0
  \rintertext{by II.~and~(iv.),} \\
%
\lintertext{whence}
b/h = 0
  \rintertext{by~(1.4).}
\end{DPgather*}
%% -----File: 155.png---Folio 144-------
\index{Addition, of probabilities!Theorem of}%


\Chapter{XIV}{The Fundamental Theorems of Probable Inference}

\Paragraph{1.} \First{I shall} give proofs in this chapter of most of the fundamental
theorems of Probability, with very little comment. The bearing
of some of them will be discussed more fully in \Chapref{XVI}\@.

\Paragraph{2.} \textit{The Addition Theorems}:

(24) $(a + b)/h = a/h + b/h - ab/h$.

In~IX. write $(a + b)$ for~$a$, and $\bar{a}b$ for~$b$.
\begin{DPgather*}
\lintertext{Then}
  (a + b) \bar{a}b/h + (a + b) \overline{\bar{a}b}/h = (a + b)/h, \\
%
\lintertext{whence}
  \bar{a}b/h + (a + b)(a + \bar{b})/h = (a + b)/h
  \rintertext{by~(iii.),}\\
%
\bar{a}/bh · b/h + a/h = (a + b)/h
  \rintertext{\llap{by (iii.)\ and~IX.}}
\end{DPgather*}
\begin{DPalign*}
\lintertext{That is to say,}
(a + b)/h
  &= a/h + (1 - a/bh) · b/h,\\
  &= a/h + b/h - ab/h.
\end{DPalign*}

In accordance with the principles of \Chapref{XII}. §\;6, this
should be written, strictly, in the form $a/h + (b/h - ab/h)$, or in
the form $b/h + (a/h - ab/h)$. The argument is valid, since the
probability $(b/h - ab/h)$ is equal to $\bar{a}b/h$, as appears from the
preceding proof, and, therefore, exists. This important theorem
gives the probability of `$a$~or~$b$' relative to a given hypothesis
in terms of the probabilities of `$a$,'~`$b$,' and `$a$~and~$b$' relative to
the same hypothesis.

(24.1) If $ab/h = 0$, \ie\ if $a$~and~$b$ are exclusive alternatives
relative to the hypothesis, then
\[
(a + b)/h = a/h + b/h.
\]
This is the ordinary rule for the addition of the probabilities of
exclusive alternatives.

(24.2) $ab/h + \bar{a}b/h = b/h$,
\begin{DPalign*}
\lintertext{since}
  &ab + \bar{a}b \equiv b
  \rintertext{by (iii.),}\\
%
\lintertext{and}
  &a\bar{a}b/h = 0
  \rintertext{by (19)~and~(8).}
\end{DPalign*}

(24.3) $(a + b)/h = a/h + b\bar{a}/h$. This follows from (24)~and~(24.2).
%% -----File: 156.png---Folio 145-------
\begin{DPalign*}[m]
\lintertext{\rlap{\indent(24.4)}}
(a + b + c)/h &= (a + b)/h + c/h - (ac + bc)/h\\
              &= a/h + b/h + c/h \\ %[** TN: Added another line break]
              &\qquad - ab/h - bc/h - ca/h + abc/h.
\end{DPalign*}

(24.5) And in general
\begin{multline*}
(p_1 + p_2 + \ldots + p_n)/h
  = \Sum p_r/h - \Sum p_s p_t/h
  + \Sum p_rp_sp_t/h \ldots \\
  + (-1)^n - 1 p_1p_2 \ldots p_n/h.
\end{multline*}

(24.6) If $p_s p_t/h = 0$ for all pairs of values of $s$~and~$t$, it follows
by repeated application of~X. that
\[
(p_1 + p_2 + \ldots + p_n)/h = \Sum_1^np_r/h.
\]

(24.7) If $p_s p_t/h = 0$, etc., and $(p_1 + p_2 + \ldots + p_n)/h = 1$, \ie\
if $p_1p_2 \ldots p_n$ form, relatively to~$h$, a set of exclusive and
exhaustive alternatives, then
\[
\Sum_1^n p_r/h = 1.
\]

(25) If $p_1p_2 \ldots p_n$ form, relative to~$h$, a set of exclusive
and exhaustive alternatives,
\[
a/h = \Sum_1^n p_r a/h.
\]
Since $(p_1 + p_2 + \ldots + p_n)/h = 1$ by hypothesis,
\[
\therefore (p_1 + p_2 + \ldots + p_n)/ah = 1\quad
  \text{ by~(9) if $ah$ is not inconsistent;}
\]
and since $p_s p_t/h = 0$ by hypothesis,
\[
\therefore p_s p_t/ah = 0\quad
  \text{by~(9), if $ah$ is not inconsistent.}
\]
\begin{DPalign*}
\lintertext{Hence}
  \Sum_1^n p_r/ah &= (p_1 + p_2 + \ldots + p_n)/ah
  \rintertext{by~(24.6)}\\
  &=1 \\
%[** TN: Continuing the alignment, not as in original]
\lintertext{Also}
p_r a/h &= p_r/ah · a/h.\\
%
\lintertext{Summing}
\Sum_1^n p_r a/h &= a/h · \Sum_1^n p_r/ah,
\end{DPalign*}
\[
\therefore a/h = \Sum_1^n p_r a/h,\quad \text{if $ah$ is not inconsistent}.
\]

If $ah$ is inconsistent, \ie\ if $a/h = 0$ (for $h$~is by hypothesis consistent),
the result follows at once by~(8).

(25.1) If $p_ra/h = X_r$, the above may be written
\[
p_r/ah = \frac{X_r}{\Sum_1^n X_r}.
\]
%% -----File: 157.png---Folio 146-------
\index{Independence, for knowledge!Theorem of}%

(26)  $a/h = (a + \bar{h})/h$.
\begin{DPalign*}
\lintertext{\indent For}
(a + \bar{h})/h &= a/h + \bar{h}/h - a\bar{h}/h
  \rintertext{by~(24),}\\
%
  &= a/h
  \rintertext{\llap{by (13.1)~and~(8).}}
\end{DPalign*}

(26.1) This may be written
\[
a/h = (h\supset a)/h.
\]

(27) If $(a + b)/h = 0$, $a/h = 0$.
\begin{DPgather*}[m]
a/h + [b/h - ab/h] = 0, \rintertext{\llap{by~(24) and hypothesis}}\\
\therefore a/h = 0      \rintertext{by~(5)}.
\end{DPgather*}

(27.1) If $a/h = 0$ and $b/h = 0$, $(a + b)/h = 0$. This follows
from~(24).

(28) If $a/h = 1$, $(a + \bar{b})/h = 1$,
\begin{DPgather*}
(a + \bar{b})/h = a/h + \bar{b}\bar{a}/h \rintertext{by~(24.3)},
\end{DPgather*}
whence $(a +\bar{b})/h = a/h = 1$ by (1.1)~and~(8), together with the
hypothesis. That is to say, a certain proposition is implied by
every proposition.

(28.1) If $a/h = 0$, $(\bar{a}+ b)/h = 1$ by substituting~$\bar{a}$ for~$a$ and~$b$
for~$\bar{b}$ in~(28). That is to say, a certainly false proposition
implies every proposition.

(29) If $a/(h_1 + h_2) = 1$, $a/h_1 = 1$, $a/h_2 = 1$.
\begin{DPgather*}
\bar{a}/(h_1 + h_2) = 0, \\
\lintertext{and}
  \therefore \bar{a}(h_1 + h_2)/h_1 = 0
  \rintertext{by~(15).}\\
%
\lintertext{Hence}
\bar{a}h_1/h_1 = 0
  \rintertext{by~(27),}
\end{DPgather*}
whence the result.

(29.1) $If a/h_1 = 1$ and $a/h_2 = 1$, $a/(h_1 + h_2) = 1$.
\begin{DPgather*}
\lintertext{As in~(20)}
\bar{a}h_1/(h_1 + h_2) = 0 \text{ and } \bar{a}h_2/(h_1 + h_2) = 0.\\
%
\lintertext{Hence}
\bar{a}(h_1 + h_2)/(h_1 + h_2) = 0
  \rintertext{by~(27.1),}
\end{DPgather*}
whence the result.

(29.2) If $a/(h_1 + h_2) = 0$, $a/h_1 = 0$. This follows from~(29).

(29.3) If $a/h_1 = 0$ and $a/h_2 = 0$, $a/(h_1 + h_2) = 0$. This follows
from~(29.1).

\Paragraph{3.} \textit{Irrelevance and Independence}:
\index{Irrelevance!Theorem of}%

(30) If $a/h_1h_2 = a/h_1$, then $a/h_1\bar{h}_2 = a/h_1$, if $h_1\bar{h}_2$ is not inconsistent.
\begin{DPalign*}
a/h_1 &= ah_2/h_1 + a\bar{h}_2/h_1 \rintertext{by~(24.2),}\\
      &= a/h_1h_2 · h_2/h_1 + a/h_1\bar{h}_2 · \bar{h}_2/h_1,\\
      &= a/h_1 · h_2/h_1 + a/h_1\bar{h}_2 · \bar{h}_2/h_1,
\end{DPalign*}
\[
\therefore a/h_1 · \bar{h}_2/h_1 = a/h_1\bar{h}_2 · \bar{h}_2/h_1,
\]
whence $a/h_1 = a/h_1\bar{h}_2$, unless $\bar{h}_2/h_1 = 0$, \ie\ if $h_1\bar{h}_2$ is not inconsistent.
%% -----File: 158.png---Folio 147-------
\index{Relevance, judgments of!theorems of}%

Thus, if a proposition is irrelevant to an argument, then the
contradictory of the proposition is also irrelevant.

(31)~If $a_2/a_1h = a_2/h$ and~$a_2h$ is not inconsistent, $a_1/a_2h = a_1/h$.

This follows by (iv.~\textit{c}), since $a_2/a_1h · a_1/h = a_1/a_2h · a_2/h$ by~X.
If, that is to say, $a_1$~is irrelevant to the argument~$a_2/h$ (see~XIV.),
and $a_2$~is not inconsistent with~$h$: then $a_2$~is irrelevant
to the argument~$a_1/h$; and $a_1/h$~and~$a_2/h$ are independent
(see~XIII.).

\Paragraph{4.}\Pagelabel{147} \textit{Theorems of Relevance:}

(32)~If $a/hh_1 > a/h$, $h_1/ah > h_1/h$. \\
$ah$~is consistent since, otherwise, $a/hh_1 = a/h = 0$.
\begin{DPgather*}
\lintertext{Therefore}
  a/h · h_1/ah = a/hh_1 · h_1/h
  \rintertext{by~X.,}\\
%
> a/h · h_1/h
  \rintertext{by hypothesis;}\\
%
\lintertext{so that}
  h_1/ah > h_1/h.
\end{DPgather*}

Thus if $h_1$~is favourably relevant to the argument~$a/h$, $a$~is
favourably relevant to the argument~$h_1/h$.

This constitutes a formal demonstration of the generally
accepted principle that if a hypothesis helps to explain a
phenomenon, the fact of the phenomenon supports the reality
of the hypothesis.

In the following theorems $p$~will be said to be more
favourable to~$a/h$, than $q$~is to~$b/h$, if $\dfrac{a/ph}{a/h} > \dfrac{b/qh}{b/h}$, \ie~if, in the
language of §\;8 below, the coefficient of influence of~$p$ on~$a/h$
is greater than the coefficient of influence of~$q$ on~$b/h$.

(33) If $x$~is favourable to~$a/h$, and $h_1$~is not more favourable
to~$a/hx$ than $x$~is to~$a/hh_1$, then $h_1$~is favourable to~$a/h$.

For $a/hh_1 = a/h · \dfrac{a/hx}{a/h} · \dfrac{a/hh_1x}{a/hx} · \dfrac{a/hh_1}{a/hh_1x}$; and by hypothesis the
second term on the right is greater than unity and the product
of the third and fourth terms is greater than or equal
to unity.

(33.1) \textit{A~fortiori}, if $x$~is favourable to~$a/h$ and not favourable
to~$a/hh_1$, and if $h_1$~is not unfavourable to~$a/hx$, then $h_1$~is
favourable to~$a/h$.

(34) If $x$~is favourable to~$a/h$, and $h_1$~is not less favourable
to~$x/ha$ than $x$~is to~$h_1/ha$, then $h_1$~is favourable to~$a/h$.

This follows by the same reasoning as~(33), since by an
application of the Multiplication Theorem
%% -----File: 159.png---Folio 148-------
\[
\frac{a/hh_1x}{a/hx} · \frac{a/hh_1}{a/hh_1x}
=\frac{x/hh_1a}{x/ha} · \frac{h_1/ha}{h_1/hax}.
\]

(35)~If $x$ is favourable to~$a/h$, but not more favourable to it
than $h_1x$~is, and not less favourable to it than to~$a/hh_1$, then
$h_1$ is favourable to~$a/h$.

\begin{DPgather*}[m]
\lintertext{\indent For}
a/hh_1
= a/h · \left\{\frac{a/h}{a/hx} · \frac{a/hh_1x}{a/h}\right\}
      · \left\{\frac{a/hx}{a/h} · \frac{a/hh_1}{a/hh_1x}\right\}.
\end{DPgather*}

This result is a little more substantial than the two
preceding. By judging the influence of $x$~and~$h_1x$ on the
arguments $a/h$~and~$a/hh_1$, we can infer the influence of~$h_1$ by
itself on the argument~$a/h$.

\Paragraph{5.} \textit{The Multiplication Theorems:}
\index{Multiplication!theorems of}%

(36)~If $a_1/h$~and~$a_2/h$ are independent, $a_1a_2/h=a_1/h · a_2/h$.
\begin{DPgather*}
\lintertext{\indent For}
a_1a_2/h
= a_1/a_2h · a_2/h=a_2/a_1h · a_1/h     \rintertext{by X.,}\\
\intertext{and since $a_1/h$ and $a_2/h$ are independent,}
                         a_1/a_2h=a_1/h \text{ and } a_2/a_1h=a_2/h   \rintertext{by XIII.}\\
\lintertext{Therefore}   a_1a_2/h=a_1/h· a_2/h.
\end{DPgather*}
Hence, when $a_1/h$~and~$a_2/h$ are independent, we can arrive at the
probability of $a_1$~and~$a_2$ jointly on the same hypothesis by simple
multiplication of the probabilities $a_1/h$~and~$a_2/h$ taken separately.

(37)~If $p_1/h=p_2/p_1h=p_3/p_1p_2h=\ldots$,
\[
p_1p_2p_3\ldots p_n/h=\left\{p_1/h\right\}^n.
\]

For $p_1p_2p_3\ldots /h=p_1/h · p_2/p_1h · p_3/p_1p_2h\ldots$ by repeated
applications of~X.

\Paragraph{6.} \textit{The Inverse Principle:}

(38)~$\dfrac{a_1/bh}{a_2/bh}=\dfrac{b/a_1h}{b/a_2h}· \dfrac{a_1/h}{a_2/h}$, provided $bh$, $a_1h$, and~$a_2h$ are
each consistent.
\begin{DPgather*}
\lintertext{For}   a_1/bh · b/h=b/a_1h · a_1/h,\\
\lintertext{and}   a_2/bh · b/h=b/a_2h · a_2/h     \rintertext{by X.,}
\end{DPgather*}
whence the result follows, since $b/h\neq 0$, unless $bh$ is inconsistent.

(38.1)~If \quad$a_1/h=p_1$,\quad $a_2/h=p_2$,\quad $b/a_1h=q_1$,\quad $b/a_2h=q_2$,\quad and
$a_1/bh+a_2/bh=1$ then it easily follows that
\begin{DPalign*}
a_1/bh &= \frac{p_1q_1}{p_1q_1+p_2q_2},\\
%% -----File: 160.png---Folio 149-------
\index{Inverse Probability}%
\index{Probability, and relevant knowledge!Inverse}%
\lintertext{and} a_2/bh &= \frac{p_2q_2}{p_1q_1+p_2q_2}.
\end{DPalign*}

(38.2)~If $a_1/h=a_2/h$ the above reduces to
\begin{DPalign*}
                 a_1/bh  &=\frac{q_1}{q_1+q_2},\\
\lintertext{and} a_2/bh  &=\frac{q_2}{q_1+q_2},
\end{DPalign*}
since $a_1/h\neq 0$, unless $a_1h$ is inconsistent.

The proposition is easily extended to the cases in which the
number of~$a$'s is greater than two.

It will be worth while to translate this theorem into familiar
language. Let $b$~represent the occurrence of an event~$B$, $a_1$~and~$a_2$
the hypotheses of the existence of two possible causes
$A_1$~and~$A_2$ of~$B$, and $h$~the general data of the problem. Then $p_1$~and~$p_2$
are the \textit{à~priori} probabilities of the existence of $A_1$~and~$A_2$
respectively, when it is not known whether or not the event~$B$
has occurred; $q_1$~and~$q_2$ the probabilities that each of the causes
$A_1$~and~$A_2$, if it exists, will be followed by the event~$B$. Then
$\dfrac{p_1q_1}{p_1q_1+p_2q_2}$ and $\dfrac{p_2q_2}{p_1q_1+p_2q_2}$ are the probabilities of the existence
of $A_1$~and~$A_2$ respectively \emph{after} the event, \ie\ when, in addition
to our other data, we know that the event~$B$ has occurred. The
initial condition, that $bh$ must not be inconsistent, simply ensures
that the problem is a possible one, \ie\ that the occurrence of the
event~$B$ is on the initial data at least possible.

The reason why this theorem has generally been known as
the Inverse Principle of Probability is obvious. The causal
problems to which the Calculus of Probability has been applied
\index{Calculus of Probability}%
are naturally divided into two classes---the direct in which, given
the cause, we deduce the effect; the indirect or inverse in which,
given the effect, we investigate the cause. The Inverse Principle
has been usually employed to deal with the latter class of
problem.

\Paragraph{7.} \textit{Theorems on the Combination of Premisses:}
\index{Combination of premisses}%

The Multiplication Theorems given above deal with the combination
of \emph{conclusions}; given $a/h_1$~and~$a/h_2$ we considered the
relation of~$a_1a_2/h$ to these probabilities. In this paragraph the
corresponding problem of the combination of \emph{premisses} will be
%% -----File: 161.png---Folio 150-------
\index{Johnson, W. E.!cumulative@{and cumulative formula}}%
treated; given $a/h_1$~and~$a/h_2$ we shall consider the relation of~$a/h_1h_2$
to these probabilities.
\begin{DPalign*}
\lintertext{\indent(39)}
a/h_1h_2h
  &= \frac{ah_1h_2/h}{h_1h_2/h}
   = \frac{ah_1h_2/h}{ah_1h_2/h + \bar ah_1h_2/h}
   \rintertext{by X. and (24.2)}\\
  &= \frac{u}{u + v},
\end{DPalign*}
where $u$ is the \textit{à~priori} probability of the conclusion~$a$ and both
hypotheses $h_1$~and~$h_2$ jointly, and $v$~is the \textit{à~priori} probability
of the contradictory of the conclusion and both hypotheses $h_1$~and~$h_2$ jointly.
\begin{DPalign*}[m]
\lintertext{\indent(40)} a/h_1h_2 = \frac{ah_1/h_2}{ah_1/h_2+\bar ah_1/h_2} &=
       \frac{h_1/ah_2·q}{h_1/ah_2·q+h_1/\bar ah_2·(1-q)},\\
    &= \frac{h_2/ah_1·p}{h_2/ah_1·p + h_2/\bar ah_1·(1-p)},
\end{DPalign*}
where $p=a/h_1$ and $q=a/h_2$.
\begin{DPalign*}
\lintertext{\indent(40.1)~If $p = \frac{1}{2}$,} a/h_1h_2 &
    = \frac{h_2/ah_1}{h_2/ah_1+h_2/\bar ah_1},\\
\lintertext{and increases with} &\phantom{=~} \frac{h_2/ah_1}{h_2/\bar ah_1}.
\end{DPalign*}

These results are not very valuable and show the need of an
original method of reduction. This is supplied by Mr.~W.~E.
Johnson's \textit{Cumulative Formula}, which is at present unpublished
\index{Cumulative Formula}%
but which I have his permission to print below.\footnote
  {The substance of propositions (41)~to~(49) below is derived in its entirety
  from his notes,---the exposition only is mine.}

\Paragraph{8.} It is first of all necessary to introduce a new symbol. Let
us write
\begin{DPgather*}
\lintertext{\indent XV.}    a/bh = \{a^hb\}a/h   \rintertext{Def.}
\end{DPgather*}
We may call $\{a^hb\}$ \emph{the coefficient of influence} of $b$ upon~$a$ on
hypothesis~$h$.
\begin{DPalign*}
\lintertext{\indent XVI.}   \{a^hb\} · \{ab^hc\}      &=\{a^hb^hc\}  \rintertext{Def.}\\
\lintertext{and similarly}  \{a^hb\} · \{ab^hcd^he\}  &=\{a^hb^hcd^he\}.
\end{DPalign*}
These coefficients thus belong by definition to a general class of
operators, which we may call \emph{separative factors}.
\noindent
\begin{DPgather*}
\lintertext{\indent (41)}  ab/h=\{a^hb\} · a/h · b/h,\\
\lintertext{since}         ab/h=a/bh · b/h.
\end{DPgather*}
%% -----File: 162.png---Folio 151-------
Thus we may also call $\{a^{h}b\}$ \emph{the coefficient of dependence} between
$a$~and~$b$ on hypothesis~$h$.
\begin{DPalign*}
\lintertext{\indent(41.1)}  abc/h & = \{a^{h}b^{h}c\} · a/h · b/h · c/h.   \\
\lintertext{For}            abc/h & = \{ab^{h}c\}ab/h · c/h                                                  \rintertext{by (41),}\\
                                  & = \{ab^{h}c\} · \{a^{h}b\} · a/h · b/h · c/h  \rintertext{by (41).}
\end{DPalign*}

(41.2)~And in general
\begin{DPalign*}
abcd \ldots /h = \{a^{h}b^{h}c^{h}d^{h} \ldots \}
  &{} · a/h · b/h · c/h · d/h \ldots \\
\lintertext{\indent(42)}
\{a^{h}b\} & = \{b^{h}a\},            \\
\lintertext{since}
a/bh · b/h & = b/ah · a/h.   \\
\lintertext{\indent(42.1)}
\{a^{h}b^{h}c\} &= {a^{h}c^{h}b},         \\
\lintertext{since}
a/h · b/h · c/h & = a/h · c/h · b/h.
\end{DPalign*}

(42.2)~And in general we have \emph{a commutative rule}, by which
the order of the terms may be always commuted---
\begin{DPalign*}
\lintertext{\eg} \{a^{h}bc^{h} def^{h} g\} & = \{bc^{h}a^{h}g^{h} def\} \\
                 \{a^{h}bc^{h} def^{h} g\} & = \{a^{h}cb^{h} fed^{h} g\}.
\end{DPalign*}

(43)~As a multiplier the separative factor operates so as to
separate the terms that may be associated (or joined) in the
multiplicand.

\begin{DPalign*}
\lintertext{Thus}
  & \{ab^{h}cd^{h}e\} · \{a^{h}b\} = \{a^{h}b^{h}cd^{h}e\}, \\
\lintertext{for}
abcde/h
  & =  \{ab^{h}cd^{h}e\} · ab/h · cd/h · e/h \\
  & =  \{ab^{h}cd^{h}e\} · \{a^{h}b\} · a/h · b/h · cd/h · e/h, \\
\lintertext{and \rlap{also}}
abcde/h
  & =  \{a^{h}b^{h}cd^{h}e\} · a/h · b/h · cd/h · e/h.
\end{DPalign*}
Similarly (for example)
\begin{DPgather*}
\{abc^{h}d^{h}ef\} · \{ab^{h}c\} · \{a^{h}b\}
  = \{a^{h}b^{h}c^{h}d^{h}ef\}.\\
\lintertext{(44)}
\{a^{h}b\} · \{ab\} = \{a^{h}b\}.\\
\lintertext{For}
ab/h = \{ab\}ab/h.
\end{DPgather*}
By a symbolic convention, therefore, we may put $\{ab\} = 1$.

(44.1)~If $\{a^{h}b\} = 1$, it follows that $a/h$~and~$b/h$ are independent
arguments; and conversely.

(45)~Rule of Repetition  $\{aa^{h}b\} = \{a^{h}b\}$.
\begin{DPgather*}
\lintertext{For}  aab/h = ab/h  \rintertext{by (vi.)\ and (12).}
\end{DPgather*}

(46) \textit{The Cumulative Formula:}
{\setlength{\multlinegap}{0pt}
\begin{multline*}
x/ah  :  x'/ah  :  x''/ah  :  \ldots \\
 = x/h · a/xh  :  x'/h · a/x'h  :  x''/h · a/x''h  :  \ldots   \qquad\text{by (38).}
\end{multline*}
}
Take $n + 1$ propositions $a, b, c \ldots$ \quad Then by repetition
{\setlength{\multlinegap}{0pt}
\begin{multline*}
x/ah · x/bh · x/ch \ldots : x'/a · \DPtypo{x'b/}{x'/b}
· x'/c \ldots  :  x''/a · x''/b · x''/c \ldots :  \ldots \\
\shoveleft{ = (x/h)^{n + 1} a/xh · b/xh \ldots :  (x'/h)^{n + 1}a/x'h · b/x'h \ldots} \\
 : (x''/h)^{n + 1} a/x''h · b/x''h \ldots
\end{multline*}
}%
which may be written
%% -----File: 163.png---Folio 152-------
\index{Mathematicians, and probability!cumulative formula@{and cumulative formula}}%
{\setlength{\multlinegap}{0pt}
\begin{multline*}
\Prod^{n+1} x/ah :  \Prod^{n+1} x'/ah : \Prod^{n+1} x''/ah: \ldots {}\\
  = (x/h)^{n+1}     \Prod^{n+1}  a/xh : (x'/h)^{n+1} \Prod^{n+1} a/x'h: \ldots
\end{multline*}
}
Now
{\setlength{\multlinegap}{0pt}
\begin{multline*}
x/habc \ldots: x'/habc \ldots: x''/habc \ldots \\
  = x/h · (abc \ldots) /xh : x'/h ·  (abc \ldots) /x'h: \ldots \text{by (38),}
\end{multline*}
}
and
\begin{DPgather*}
abc \ldots /xh = \{a^{xh}b^{xh}c \ldots\} \Prod^{n+1}a/xh \rintertext{\; by (41.2),}
\end{DPgather*}
\begin{multline*}
\therefore
(x/h)^{n} · x/habc \ldots :
(x'/h)^{n} · x'/habc \ldots:
(x''/h)^{n} · x''/habc \ldots: \ldots \\
  = \{a^{xh}b^{xh}c \ldots\} x/ah · x/bh · x/ch \ldots:
    \{a^{x'h}b^{x'h}c \ldots\} x'/ah · x'/bh \\
                         {} · x'/ch \ldots : \ldots
\end{multline*}
which may be written
\[
(x/h)^{n}· x/habc \ldots \propto\{a^{xh}b^{xh}c \ldots\}· x/ah· x/bh· x/ch\ldots
\]
where variations of~$x$ are involved.

The cumulative formula is to be applied when, having accumulated
the evidence $a, b, c \ldots$, we desire to know the comparative
probabilities of the various possible inferences $x, x' \ldots$ which
may be drawn, and already know determinately the force of
each of the items $a, b, c \ldots$ separately as evidence for $x, x' \ldots$.

Besides the factors $x/ah$, $x/bh$, etc., we require to know two
other sets of values, viz.: (1)~$x/h$, etc., \ie\ the \textit{à~priori}
probabilities of~$x$, etc., and (2)~$\{a^{xh}b^{xh}c \ldots\}$, etc., \ie\ the
coefficients of dependence between $a$,~$b$, and~$c\ldots$ on hypotheses~$xh$,
etc. It may be remarked that the values $\{a^{xh}b^{xh}c \ldots\}$,
$\{a^{x'h}b^{x'h}c \ldots\} \ldots$ are not in any way related, even when $x' \equiv \bar{x}$.

What corresponds to the cumulative formula has been employed,
sometimes, by mathematicians in a simplified form
which is, except under special conditions, incorrect. First, it
has been tacitly assumed that $\{a^{xh}b^{xh}c \ldots\}$, $\{a^{x'h}b^{x'h}c \ldots\} \ldots$
are all unity: so that
\[
(x/h)^{n}x/habc \ldots \propto x/ah · x/bh · x/ch \ldots
\]
Secondly, the factor $(x/h)^{n}$ has been omitted, so that
\[
x/habc \ldots \propto x/ah · x/bh · x/ch \ldots
\]

It is this second incorrect statement of the formula which
leads to the fallacious rule for the combination of the testimonies
of independent witnesses ordinarily given in the text-books.\footnote
  {See \Pageref{180} below.}

(46.1). If $abc \ldots /xh = \{a^{xh}b^{xh}c \ldots\} a/xh ·  b/xh · c/xh \ldots$
\begin{DPgather*}
\lintertext{then}  x/habc \ldots \propto \{a^{xh}b^{xh}c \ldots\} x/ah · x/bh · x/ch \ldots\DPtypo{}{.}
\end{DPgather*}
%% -----File: 164.png---Folio 153-------
\index{Johnson, W. E.!cumulative@{and cumulative formula}}%
This result is exceedingly interesting. Mr.~Johnson is the first to
arrive at the simple relation, expressed above, between the direct
and the inverse formulæ: viz.\ that the \emph{same} coefficient is required
for correcting the simple formulæ of multiplication in
both cases. As he remarks, however, while the direct formula
gives the required probability directly by multiplication, the
inverse formula gives only the \emph{comparative} probability.

(46.2) If $x, x', x'' \ldots$ are exclusive and exhaustive alternatives,
\begin{DPgather*}
x/habc\ldots = \frac
  {(x/h)^{-n} · \{a^{xh}b^{xh}c \ldots\}\Prod\limits^{n-1} x/ah}
  {\Sum\left[(x'/h)^{-n}·\{a^{x'h}b^{x'h}c \ldots\}\Prod\limits^{n-1}x'/ah\right]},\\
%
\lintertext{since}  x/habc \ldots\propto (x/h)^{-n}\{a^{xh}b^{xh}c \ldots\}\Prod\limits^{n-1}x/ah,\\
%
\lintertext{and}    \Sum x'/habc \ldots = 1 \rintertext{\llap{by (24.7).}}
\end{DPgather*}
\begin{DPalign*}[m]
\lintertext{\indent(47).}
\frac{x/habc \ldots}{x/h}
  &= \frac{a/h · b/h · c/h \ldots}{abc \ldots/h} \\
  &\qquad{} · \frac{abc \ldots /xh}{a/xh · b/xh · c/xh \ldots}
  · \left[\frac{x/ah}{x/h} · \frac{x/bh}{x/h} \ldots\right].
\end{DPalign*}
\begin{DPgather*}
\lintertext{For}  abc \ldots x/h = x/h · abc \ldots/xh,
\end{DPgather*}
\begin{multline*}
\therefore \frac{abc \ldots x/h}{abc \ldots/h· x/h}
  = \frac{abc \ldots /xh}{abc \ldots /h}
  = \frac{a/h · b/h · c/h \ldots}{abc \ldots /h} \\
  {} · \frac{abc \ldots /xh}{a/xh · b/xh · c/xh\ldots}
     · \left[\frac{a/xh}{a/h} · \frac{b/xh}{b/h}\ldots\right],
\end{multline*}
whence the result, since $\dfrac{a/xh}{a/h} = \dfrac{x/ah}{x/h}$, etc.

(47.1) The above formula may be written in the condensed
form
\[
\{abc \ldots ^{h}x\}
  = \frac{1}{\{a^{h}b^{h}c^{h} \ldots\}}·
    \{a^{xh}b^{xh}c^{xh} \ldots\} ·
    [\{a^{h}x\} · \{b^{h}x\} · \{c^{h}x\} \ldots].
\]
\begin{DPgather*}[m]
\lintertext{\indent(48.)}
\frac{\{x/h\}^{n}x/habc \ldots}{\{\bar{x}/h\}^{n}\bar{x}/habc \ldots}
  = \frac{\{a^{xh}b^{xh}c^{xh} \ldots\}}
         {\{a^{\bar{x}h}b^{\bar{x}h}c^{\bar{x}h} \ldots\}}
  · \frac{x/ah · x/bh · x/ch \ldots}
             {\bar{x}/ah · \bar{x}/bh · \bar{x}/ch \ldots}.
\end{DPgather*}
This follows at once from~(46.2), since $x$~and~$\bar{x}$ are exclusive and
exhaustive alternatives. (It is assumed that $xh$,~$\bar{x}h$, and~$ah$,
etc., are not inconsistent.)
%% -----File: 165.png---Folio 154-------

This formula gives $x/habc \ldots$ in terms of $x/ah$, $x/bh$, etc.,
together with the three values $x/h$, $\{a^{xh}b^{xh}c^{xh} \ldots\}$, and
$\{a^{\bar{x}h}b^{\bar{x}h}c^{\bar{x}h} \ldots\}$.
\begin{DPgather*}[m]
\lintertext{\indent(48.1)} \dfrac{x/habcd \ldots}{\bar{x}/habcd \ldots} : \dfrac{x/hbcd \ldots}{\bar{x}/hbcd \ldots}
= \dfrac{\{a^{xh}bcd \ldots\} · x/ah}{\{a^{\bar{x}h}bcd \ldots\} · \bar{x}/ah} : \dfrac{x/h}{\bar{x}/h}.
\end{DPgather*}
This gives the effect on the odds ($\text{prob.\ } x : \text{prob.\ } \bar{x}$) of the extra
knowledge~$a$.

(49) When several data co-operate as evidence in favour of a
proposition, they continually strengthen their own mutual
probabilities, on the assumption that when the proposition
is known to be true or to be false the data jointly are not
counterdependent.

\Ie\ if $\{a^{xh}b^{xh}c \ldots\}$ and $\{a^{\bar{x}h}b^{\bar{x}h}c \ldots\}$ are not less than
unity, and $x/kh > x/h$ where $k$ is any of the data $a, b, c \ldots$, then
$\{a^hb^hc^hd \ldots\}$ beginning with unity, continually increases, as
the number of its terms is increased.
\begin{DPalign*}[m]
abc \ldots/h
  & = xabc \ldots/h + \bar{x}abc \ldots/h
\rintertext{\llap{by (24.2).}} \\
  & = x/h · abc \ldots/xh + \bar{x}/h · abc \ldots/\bar{x}h.\\
  & \geq x/h · \Prod a/xh · b/xh \ldots
    + \bar{x}h\Prod a/\bar{x}h · b/\bar{x}h \ldots \\
\intertext{\centering(since $\{a^{xh}b^{xh}c \ldots\}$ and $\{a^{\bar{x}h}b^{\bar{x}h}c \ldots\}$ are not less than unity),}
  & \geq x/h ·
  \Prod\left[\frac{ax/h}{x/h}
       · \frac{bx/h}{x/h} \ldots\right]
  + \bar{x}/h ·
  \Prod \left[\frac{a\bar{x}/h}{\bar{x}/h}
        · \frac{b\bar{x}/h}{\bar{x}/h} \ldots\right],
\end{DPalign*}
\begin{multline*}
\therefore \frac{abc \ldots/h}{\Prod[a/h · b/h \ldots]}
  \geq x/h · \Prod\left[\frac{x/ah}{x/h}
       · \frac{x/bx}{x/h} \ldots\right] \\ %[** TN: Moved line break]
     + \bar{x}/h · \Prod\Big[\frac{\bar{x}/ah}{\bar{x}/h}
       · \frac{\bar{x}/bh}{\bar{x}/h} \ldots\Big].
\end{multline*}

We can show that each additional piece of evidence $a, b, c \ldots$
increases the value of this expression. For let $x/h · G + \bar{x}/h · G'$ be
its value when all the evidence up to~$k$ exclusive is taken, so that
\[
x/kh · G + \bar{x}/kh · G'
\]
is its value when $k$~is taken. Now $G > G'$ since $x/ah > x/h$, etc.,
and $\bar{x}/ah < \bar{x}/h$, etc., by the hypothesis that the evidence
favours~$x$; and for the same reason $x/kh - x/h$, which is equal
to $\bar{x}/h - \bar{x}/kh$, is positive.
\begin{DPalign*}
\therefore G(x/kh - x/h) & > G'(\bar{x}/h - \bar{x}/kh),\\
\lintertext{\ie}
x/kh · G + \bar{x}/kh · G'
  & > x/h · G + \bar{x}/h · G',
\end{DPalign*}
whence the result.
%% -----File: 166.png---Folio 155-------
\index{Johnson, W. E.!cumulative@{and cumulative formula}}%
\index{McColl, and symbolic probability}%
\index{Middle Term, Fallacy of}%

(49.1) The above proposition can be generalised for the
case of exclusive alternatives $x, x', x'' \ldots$ (in place of $x$,~$\bar{x}$).
\begin{DPalign*}
\lintertext{\rlap{For $\{a^h b^h c^h \ldots\}$}}\\
&\indent = x/h . \{a^{xh} b^{xh} c \ldots\} \{a^h x\} \{b^h x\} \{c^h x\} \ldots\\
&\indent + x'/h . \{a^{x'h} b^{x'h} c \ldots\} \{a^h x'\} \{b^h x'\} \{c^h x'\} \ldots\\
&\indent + x''/h . \{a^{x''h} b^{x''h} c \ldots\} \{a^h x''\} \{b^h x''\} \{c^h x''\} \ldots + \ldots;
\end{DPalign*}
from which, it follows that, if $\{a^{xh} b^{xh} c \ldots\} \text{etc.} \nless 1$, and if
$\DPtypo{\{a^h x\} - 1}{\{a^hx - 1\}}$, $\{b^h x - 1\}$, $\{c^h x - 1\}$, etc., have the same sign, then
$\{a^h b^h c \ldots\}$ is increasing (with the number of letters) from unity.

Mr.~Johnson describes this result as a generalisation of
the corrected ``middle term fallacy'' (see \Chapref[Chap.]{V}. §\;4).


\Appendix{ON SYMBOLIC TREATMENTS OF PROBABILITY}

\First{The} use of the symbol~$0$ for impossibility and $1$~for certainty was
first introduced by Leibnitz in a very early pamphlet, entitled
\textit{Specimen certitudinis seu demonstrationum in jure, exhibitum in
doctrina conditionum}, published in 1665 (\textit{vide} Couturat, \textit{Logique de
Leibnitz}, p.~553). Leibnitz represented intermediate degrees of
probability by the sign~$\frac{1}{2}$, meaning, however, by this symbol a
\emph{variable} between $0$~and~$1$.

Several modern writers have made some attempt at a symbolic
treatment of Probability. But with the exception of Boole, whose
\index{Boole!symbolic probability@{and symbolic probability}}%
methods I have discussed in detail in Chapters \Chapref[]{XV}., \Chapref[]{XVI}., and
\Chapref[]{XVII}., no one has worked out anything very elaborate.

Mr.~McColl published a number of brief notes on Probability of
considerable interest---see especially his \textit{Symbolic Logic}, \textit{Sixth Paper
on the Calculus of Equivalent Statements}, and \textit{On the Growth and Use
of a Symbolical Language}. The conception of probability as a relation
between propositions underlies his symbolism, as it does mine.\footnote
  {I did not come across these notes until my own method was considerably
  developed. Mr.~McColl has been the first to use the fundamental symbol of
  Probability.}
The probability of $a$, relative to the \textit{à~priori} premiss~$h$, he writes~$\dfrac{a}{\epsilon}$; and
the probability, given $b$~in addition to the \textit{à~priori} premiss, he writes~$\dfrac{a}{b}$.
Thus $\dfrac{a}{\epsilon} = \dfrac{a}{h}$, and $\dfrac{a}{b} = a/bh$. The difference $\dfrac{a}{b} - \dfrac{a}{\epsilon}$, \ie\ the change
in the probability of~$a$ brought about by the addition of~$b$ to the
evidence, he calls `the dependence of the statement $a$ upon the statement~$b$,'
%% -----File: 167.png---Folio 156-------
\index{Gilman, B. I., and symbolic probability}%
\index{Lammel@{Lämmel}!symbolic probability@{and symbolic probability}}%
and denotes it by~$\delta\dfrac{a}{b}$. Thus $\delta\dfrac{a}{b}=0$, where, in my terminology,
$b$ is \emph{irrelevant} to~$a$ on evidence~$h$. The multiplication and
addition formulæ he gives as follows:
$\dfrac{ab}{\epsilon} = \dfrac{a}{\epsilon}·\dfrac{b}{a}
                      = \dfrac{b}{\epsilon}·\dfrac{a}{b}$.
\begin{DPgather*}
\frac{a+b}{\epsilon}
  = \frac{a}{\epsilon} + \frac{b}{\epsilon} - \frac{ab}{\epsilon}.\\
\lintertext{Also}
\delta\frac{a}{b}
  = \frac{A}{B}\delta \frac{b}{a}, \text{ where } A = \frac{a}{\epsilon}.
\end{DPgather*}

It is surprising how little use he succeeds in making of these good
results. He arrives, however, at the inverse formula in the shape---
\[
\frac{c_r}{v}
  = \frac{\dfrac{c_r}{\epsilon}\dfrac{v}{c_r}}
         {\Sum_{r=1}^{r=n}\dfrac{c_r}{\epsilon}·\dfrac{v}{c_r}},
\]
where $c_{1} \ldots c_{n}$ are a series of mutually exclusive causes of the event~$v$
and include all possible causes of it; reaching it as a generalisation
of the proposition
\[
\frac{a}{b} = \frac{\dfrac{a}{\epsilon}·\dfrac{b}{a}}
                   {\dfrac{a}{\epsilon}·\dfrac{b}{a}+\dfrac{\bar{a}}{\epsilon}·\dfrac{b}{\bar{a}}}
\]

In a paper entitled ``Operations in Relative Number with Applications
to the Theory of Probabilities,''\footnote
  {Published in the volume of Johns Hopkins \textit{Studies in Logic}.}
Mr.~B.~I. Gilman attempted
a symbolic treatment based on a frequency theory similar to Venn's,
but made more precise and more consistent with itself: ``Probability
has to do, not with individual events, but with classes of events; and
not with one class, but with a pair of classes,---the one containing,
the other contained. The latter being the one with which we are
principally concerned, we speak, by an ellipsis, of its probability
without mentioning the containing class; but in reality probability
is a ratio, and to define it we must have both correlates given.'' But
Mr.~Gilman's symbolic treatment leads to very little. More recently
R.~Laemmel, in his \textit{Untersuchungen über die Ermittlung von Wahrscheinlichkeiten},
made a beginning on somewhat similar lines; but
in his case also the symbolic treatment leads to no substantial results.

Apart from the writers mentioned above, there are a few who
have incidentally made use of a probability symbol. It will be
\index{Czuber!symbolic probability@{and symbolic probability}}%
sufficient to cite Czuber.\footnote
  {\textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ pp.~43--48.}
He denotes the probability of an event~$E$
%% -----File: 168.png---Folio 157-------
\index{Poretzki, Platon S., and symbolic!probability}%
\index{Schröder and symbolic probability}%
by~$W(E)$, and the probability of the event~$E$ given the occurrence of
an event~$F$ by~$W_{F}(E)$. He uses this symbol to give $W_{F}(E) = W_{\bar{F}}(E)$
as the criterion of the independence of the events $E$~and~$F$ ($\bar{F}$ denoting
the non-occurrence of~$F$); $W_{F}(E)=1$, as the expression of the fact
that $E$ is a necessary consequence of~$F$; and one or two other similar
results.

Finally there is in the \textit{Bulletin of the Physico-mathematical Society
of Kazan} for 1887 a memoir in Russian by Platon S. Porotzki entitled
``A Solution of the General Problem of the Theory of Probability by
Means of Mathematical Logic.'' I have seen it stated that Schröder
intended to publish ultimately a symbolic treatment of Probability.
Whether he had prepared any manuscript on the subject before his
death I do not know.
%% -----File: 169.png---Folio 158-------
\index{Addition, of probabilities!measurement@{and measurement}}%
\index{Measurement of Probability}%


\Chapter{XV}{Numerical Measurement and Approximation of Probabilities}

\Paragraph{1.} \First{The} possibility of numerical measurement, mentioned at
the close of \Chapref{III}., arises out of the Addition Theorem~(24.1).
In introducing the definitions and the axiom, which are
required in order to make the convention of numerical measurement
operative, we may appear, as in the case of the original
definitions of Addition and Multiplication, to be arguing in an
artificial way. This appearance is due, here as in \Chapref{XII}.,
to our having given the names of addition and multiplication to
certain processes of compounding probabilities \emph{in advance of}
postulating that the processes in question have the properties
commonly associated with these names. As common sense is
hasty to impute the properties as soon as it hears the names, it
may overlook the necessity of formally introducing them.

\Paragraph{2.} The definitions and the axiom which are needed in order
to give a meaning to numerical measurement are the following:---
\begin{DPalign*}[m]
\lintertext{\indent XVII.}
  & a/h + \left\{a/h + \left[a/h + (a/h + \ldots\  r \text{ terms})\right]\right\}
  = r · a/h.
  \rintertext{Def.}\\
%
\lintertext{\rlap{\indent XVIII.}}
  &\text{If $r · a/h = b/f$, then $a/h = \dfrac{1}{r} · b/f$.}
  \rintertext{Def.}\\
%
\lintertext{\indent XIX.}
  &\text{If $b/f = q · c/g$, then $\dfrac{1}{r} · b/f = \dfrac{q}{r}\, c/g$.}
  \rintertext{Def.}
\end{DPalign*}
Thus if $b/h = a/h + a/h + \ldots$ to $r$~terms, then the probability
$b/h$ is said to be $r$~times the probability~$a/h$; hence if $ab/h=0$ and
$a/h = b/h$, the probability $(a+b)/h$ is \emph{twice} the probability~$a/h$.
If $a$~and~$b$ are exhaustive as well as exclusive alternatives relatively
to~$h$, so that $(a+b)/h = 1$, since we take the relation of
certainty as our unit, then $a/h = b/h = \frac{1}{2}$.

We also need the following axiom postulating the existence of
relations  of probability corresponding to all proper fractions:
%% -----File: 170.png---Folio 159-------

(vii.) If $q$~and~$r$ are any finite integers and $q < r$, there exists
a relation of probability which can be expressed, by means of the
convention of the foregoing definitions, as~$\dfrac{q}{r}$.

\Paragraph{3.} From these axioms and definitions combined with those
of \Chapref{XII}., it is easy to show (certainty being represented
by unity and impossibility by zero) that we can manipulate
according to the ordinary laws of arithmetic the ``numbers''
which by means of a special convention we have thus introduced
to represent probabilities. Of the kind of proofs necessary
for the complete demonstration of this the following is given as
an example:
\begin{DPgather*}
\lintertext{\indent(50)}
  \text{If $a/f = \dfrac{1}{m}$ and $b/h = \dfrac{1}{n}$, $a/f + b/h = \dfrac{m + n}{mn}$.}
\end{DPgather*}

Let the probability $\dfrac{1}{mn} = P$, which exists by~(vii.),
\begin{DPalign*}
\lintertext{then}
  n · P &= \frac{1}{m} = a/f
  \rintertext{by~(XIX.),}\\
%
\lintertext{and}
  m · P &= \frac{1}{n} = b/h,
\end{DPalign*}
\begin{DPalign*}
\therefore a/f + b/h
  &= n · P + m · P, \text{ if this probability exists,}\\
  &= P + P \ldots \text{ to $n$~terms} + P + P\ldots \text{ to $m$~terms,}\\
  &= P + P \ldots \text{ to $m+n$~terms,}\\
  &= (m+n)P = \frac{m+n}{mn}
  \rintertext{\PadTxt[r]{}{by~(XIX.).}}
\end{DPalign*}
This probability exists in virtue of~(vii.).

\Paragraph{4.} Many probabilities---in fact all those which are equal to
the probability of some other argument which has the same
premiss and of which the conclusion is incompatible with that
of the original argument---are numerically measurable in the
sense that there is \emph{some} other probability with which they are
comparable in the manner described above. But they are not
numerically measurable in the most usual sense, unless the probability
with which they are thus comparable is the relation
of certainty. The conditions under which a probability $a/h$ is
numerically measurable and equal to~$\dfrac{q}{r}$ are easily seen. It
%% -----File: 171.png---Folio 160-------
\index{Probability, and relevant knowledge!comparison of}%
is necessary that there should exist probabilities $a_1/h_1$, $a_2/h_2 \ldots$,
$a_q/h_q \ldots a_r/h_r$, such that
\begin{gather*}
a_1/h_1 = a_2/h_2 = \ldots = a_q/h_q = \ldots = a_r/h_r, \\
a/h = \textstyle\Sum_1^q a_s/h_s, \text{ and }
      \textstyle\Sum_1^r a_s/h_s = 1.
\end{gather*}

If $a/h = \dfrac{q_1}{r_1}$ and $b/h = \dfrac{q_2}{r_2}$, it follows from~(32) that $ab/h = \dfrac{q_1q_2}{r_1r_2}$
only if $a/h$~and~$b/h$ are independent arguments. Unless, therefore,
we are dealing with independent arguments, we cannot
apply detailed mathematical reasoning even when the individual
probabilities are numerically measurable. The greater part of
mathematical probability, therefore, is concerned with arguments
which are \emph{both} independent \emph{and} numerically measurable.

\Paragraph{5.} It is evident that the cases in which exact numerical
measurement is possible are a very limited class, generally
dependent on evidence which warrants a judgment of equiprobability
by an application of the Principle of Indifference.
\index{Principle of Indifference!measurement@{and measurement}}%
The fuller the evidence upon which we rely, the less likely is it to
be perfectly symmetrical in its bearing on the various alternatives,
and the more likely is it to contain some piece of relevant information
favouring one of them. In actual reasoning, therefore,
perfectly equal probabilities, and hence exact numerical measures,
will occur comparatively seldom.

The sphere of inexact numerical comparison is not, however,
quite so limited. Many probabilities, which are incapable of
numerical measurement, can be placed nevertheless \emph{between}
numerical limits. And by taking particular non-numerical
probabilities as standards a great number of comparisons or
approximate measurements become possible. If we can place
a probability in an order of magnitude with some standard probability,
we can obtain its approximate measure by comparison.

This method is frequently adopted in common discourse.
When we ask how probable something is, we often put our question
in the form---Is it more or less probable than so and so?---where
`so and so' is some comparable and better known probability.
We may thus obtain information in cases where it would
be impossible to ascribe any \emph{number} to the probability in question.
Darwin was giving a numerical limit to a non-numerical probability
%% -----File: 172.png---Folio 161-------
when he said of a conversation with Lyell that he thought
it no more likely that he should be right in nearly all points than
that he should toss up a penny and get heads twenty times
running.\footnote
  {\textit{Life and Letters}, vol.~ii.\ p.~240.}
Similar cases and others also, where the probability
which is taken as the standard of comparison is itself non-numerical
and not, as in Darwin's instance, a numerical one,
\index{Darwin!Lyell@{and Lyell}}%
will readily occur to the reader.

A specially important case of approximate comparison is that
of `practical certainty.' This differs from logical certainty since
its contradictory is not impossible, but we are in practice completely
satisfied with any probability which approaches such
a limit. The phrase has naturally not been used with complete
precision; but in its most useful sense it is essentially non-numerical---we
cannot measure practical certainty in terms of
logical certainty. We can only explain how great practical
certainty is by giving instances. We may say, for instance, that
it is measured by the probability of the sun's rising to-morrow.
The type which we shall be most likely to take will be that of a
well-verified induction.

\Paragraph{6.} Most of such comparisons must be based on the principles
of \Chapref{V}\@. It is possible, however, to develop a systematic
method of approximation which may be occasionally useful.
The theorems given below are chiefly suggested by some work
of Boole's. His theorems were introduced for a different purpose,
\index{Boole!approximation@{and approximation}}%
and he does not seem to have realised this interesting
application of them; but analytically his problem is identical
with that of approximation.\footnote
  {In Boole's \textit{Calculus} we are apt to be left with an equation of the second
  or of an even higher degree from which to derive the probability of the conclusion;
  and Boole introduced these methods in order to determine which of the
  several roots of his equation should be taken as giving the true solution of the
  problem in probability. In each case he shows that that root must be chosen
  which lies between certain limits, and that only one root satisfies this condition.
  The general theory to be applied in such cases is expounded by him in Chapter~XIX.
  of \textit{The Laws of Thought}, which is entitled ``On Statistical Conditions.''
  But the solution given in that chapter is awkward and unsatisfactory, and he
  subsequently published a much better method in the \textit{Philosophical Magazine}
  for 1854 (4th~series, vol.~viii.)\ under the title ``On the Conditions by which the
  Solutions of Questions in the Theory of Probabilities are limited.''}
This method of approximation
is also substantially the same analytically as that dealt with by
\index{Yule!approximation@{and approximation}}%
Mr.~Yule under the heading of \textit{Consistence}.\footnote
  {\textit{Theory of Statistics}, chap.~ii.}
%% -----File: 173.png---Folio 162-------

(51) $xy/h$ always lies between\footnote
  {In this and the following theorems the term `between' includes the
  limits.}
$x/h$ and $x/h + y/h - 1$ and
between $y/h$ and $x/h + y/h - 1$.
\begin{DPalign*}
\lintertext{For}
xy/h &= x/h - x\bar{y}/h
  \rintertext{by (24.2),}\\
%
     &= x/h - \bar{y}/h · x/\bar{y}/h
  \rintertext{by~X.}
\end{DPalign*}
\begin{DPgather*}
\lintertext{Now}
\text{$x/\bar{y}h$ lies between $0$~and~$1$}
  \rintertext{by (2)~and~(3),} \\
%
\text{$\therefore xy/h$ lies between $x/h$ and $x/h - \bar{y}/h$,}\\
\text{\ie\ between $x/h$ and $x/h + y/h - 1$.}
\end{DPgather*}
As $xy/h \nless 0$, the above limits may be replaced by $x/h$ and~$0$, if
$x/h + y/h - 1 < 0$.

We thus have limits for~$xy/h$, close enough sometimes to be
useful, which are available whether or not $x/h$ and~$y/h$ are \emph{independent}
arguments. For instance, if $y/h$ is nearly certain, $xy/h
= x/h$ nearly, quite independently of whether or not $x$ and~$y$ are
independent. This is obvious; but it is useful to have a simple
and general formula for all such cases.

(52) $x_1x_2 \ldots x_{n+1}/h$ is always greater than $\Sum_1^{n+1} x_r/h - n$.
\begin{DPalign*}[m]
\lintertext{For by~(51)}
x_1x_2 \ldots  x_{n+1}/h
  &> x_1x_2 \ldots x_n/h + x_{n+1}/h - 1\\
  &> x_1x_2 \ldots x_{n-1}/h + x_n/h + x_{n+1}/h - 2,
\end{DPalign*}
and so on.

(53) $xy/h + \bar{x}\bar{y}/h$ is always less than $x/h - y/h + 1$, and less
than $y/h - x/h + 1$.
\begin{DPalign*}[m]
\lintertext{\rlap{For as in~(51)}}
xy/h &= x/h - x\bar{y}/h\\
\lintertext{and}
\bar{x}\bar{y}/h &= \bar{y}/h - x\bar{y}/h,\\
\therefore xy/h + \bar{x}\bar{y}/h &= x/h - y/h + 1 - 2x\bar{y}/h,
\end{DPalign*}
whence the required result.

(54) $xy/h -\bar{x}\bar{y}/h = x/h + y/h - 1$.

This proposition, which follows immediately from the above,
is really out of place here. But its close connection with conclusions
(51)~and~(53) is obvious. It is slightly unexpected,
perhaps, that the difference of the probabilities that both of two
events will occur and that neither of them will, is independent of
whether or not the events themselves are independent.

\Paragraph{7.} It is not worth while to work out more of these results here.
Some less systematic approximations of the same kind are given
in the course of the solutions in \Chapref{XVII}\@.

In seeking to compare the degree of one probability with that
of another we may desire to get rid of one of the terms, on account
%% -----File: 174.png---Folio 163-------
of its not being comparable with any of our standard probabilities.
Thus our object in general is to eliminate a given symbol of
quantity from a set of equations or inequations. If, for instance,
we are to obtain numerical limits within which our probability
must lie, we must eliminate from the result those probabilities
which are non-numerical. This is the general problem for
solution.

(55)~A general method of solving these problems when we
can throw our equations into a linear shape so far as all symbols
of probability are concerned, is best shown in the following
example:---
\begin{DPalign*}
\lintertext{\indent\PadTxt[l]{}{Suppose we have}}
  \lambda + \nu &= a \rintertext{(i.)}\\
  \lambda + \sigma &= b \rintertext{(ii.)}\\
  \lambda + \nu + \sigma &= c \rintertext{(iii.)}\\
  \lambda + \mu + \nu + \rho &= d \rintertext{(iv.)}\\
  \lambda + \mu + \sigma + \tau &= e \rintertext{(v.)}\\
  \lambda + \mu + \nu + \rho + \sigma + \tau + \upsilon &= 1 \rintertext{(vi.)}
\end{DPalign*}
where $\lambda$, $\mu$, $\nu$, $\rho$, $\sigma$, $\tau$, $\upsilon$ represent probabilities which are to be
eliminated, and limits are to be found for~$c$ in terms of the
standard probabilities $a$,~$b$, $d$,~$e$, and~$1$.

$\lambda$,~$\mu$,~etc., must all lie between $0$~and~$1$.

From (i.)\ and~(iii.)\ $\sigma = c - a$; from (ii.)\ and~(iii.)\ $\nu = c - b$.

From (i.),~(ii.), and~(iii.)\ $\lambda = a + b - c$, \\
whence %[** TN: Not using condensed intertext]
\begin{gather*}
  c - a \eqslantgtr 0,\quad c - b \eqslantgtr 0,\quad a + b - c \eqslantgtr 0,\\
\intertext{substituting for $\sigma$,~$\nu$,~$\lambda$ in (iv.), (v.), and~(vi.)}
\mu + \rho = d - a,\quad
\mu + \tau = e - b,\quad
\mu + \rho + \tau + \upsilon = 1 - c, \\
\intertext{whence}
\rho = d - a - \mu,\quad
\tau = e - b - \mu,\quad
\upsilon = 1 - c - d + a - e + b + \mu, \\
\therefore d - a - \mu \eqslantgtr 0,\quad
  e - b - \mu \eqslantgtr 0,\quad
  1 - c - d + a - e + b + \mu \eqslantgtr 0. \\
\intertext{We have still to eliminate~$\mu$.}
\mu \eqslantgtr d - a,\quad \mu \eqslantgtr e - b, \\
\mu \eqslantgtr c + d + e - a - b - 1, \\
\text{$\therefore d - a \eqslantgtr c + d + e - a - b - 1$ and
      $e - b \eqslantgtr c + d + e - a - b - 1$.}
\end{gather*}
Hence we have:

Upper limits of~$c$:---$b + 1 - e$, $a + 1 - d$, $a + b$ (whichever is least),

Lower limits of~$c$:---$a$, $b$ (whichever is greatest).

This example, which is only slightly modified from one given
by Boole, represents the actual conditions of a well-known
problem in probability.
%% -----File: 175.png---Folio 164-------
\index{Calculus of Probability}%
\index{Causality!independence@{and independence}}%
\index{Independence, for knowledge!of events}%


\Chapter{XVI}{Observations on the Theorems of Chapter XIV. and their
Developments, including Testimony}

\Paragraph{1.} \First{In} Definition~XIII. of \Chapref{XII}. a meaning was given to
the statement that $a_1/h$ and~$a_2/h$ are independent arguments.
In Theorem~(33) of \Chapref{XIV}. it was shown that, if $a_1/h$~and~$a_2/h$
are independent, $a_1a_2/h = a_1/h · a_2/h$. Thus where on given
evidence there is independence between $a_1$~and~$a_2$, the probability
on this evidence of~$a_1a_2$ jointly is the product of the probabilities
of $a_1$~and~$a_2$ separately. It is difficult to apply mathematical
reasoning to the Calculus of Probabilities unless this condition
is fulfilled; and the fulfilment of the condition has often been
assumed too lightly. A good many of the most misleading
fallacies in the theory of Probability have been due to a use of
the Multiplication Theorem in its simplified form in cases where
this is illegitimate.

\Paragraph{2.} These fallacies have been partly due to the absence of
a clear understanding as to what is meant by \emph{Independence.}
Students of Probability have thought of the independence of
events, rather than of the independence of arguments or propositions.
The one phraseology is, perhaps, as legitimate as the
other; but when we speak of the dependence of events, we are
led to believe that the question is one of direct causal dependence,
two events being dependent if the occurrence of one is a part
cause or a possible part cause of the occurrence of the other. In
this sense the result of tossing a coin is dependent on the existence
of bias in the coin or in the method of tossing it, but it is independent
of the actual results of other tosses; immunity from
smallpox is dependent on vaccination, but is independent of
statistical returns relating to immunity; while the testimonies
of two witnesses about the same occurrence are independent,
so long as there is no collusion between them.
%% -----File: 176.png---Folio 165-------
\index{Independence, for knowledge}%

This sense, which it is not easy to define quite precisely, is
at any rate not the sense with which we are concerned when we
deal with independent probabilities. We are concerned, not with
direct causation of the kind described above, but with `dependence
for knowledge,' with the question whether the \emph{knowledge} of
one fact or event affords any rational ground for expecting the
existence of the other. The dependence for knowledge of two
events usually arises, no doubt, out of causal connection, or what
we term such, of \emph{some} kind. But two events are not independent
for knowledge merely because there is an absence of direct causal
connection between them; nor, on the other hand, are they
necessarily dependent because there is in fact a causal train which
brings them into an indirect connection. The question is whether
there is any \emph{known} probable connection, direct or indirect. A
knowledge of the results of other tossings of a coin may be hardly
less relevant than a knowledge of the bias of the coin; for a
knowledge of these results may be a ground for a probable knowledge
of the bias. There is a similar connection between the
statistics of immunity from smallpox and the causal relations
between vaccination and smallpox. The truthful testimonies
of two witnesses about the same occurrence have a common
cause, namely the occurrence, however independent (in the legal
sense of the absence of collusion) the witnesses may be. For the
purposes of probability two facts are only independent if the
existence of one is no \emph{indication} of anything which might be a
part cause of the other.

\Paragraph{3.} While dependence and independence may be thus connected
with the conception of causality, it is not convenient to
found our definition of independence upon this connection. A
partial or possible cause involves ideas which are still obscure, and
I have preferred to define independence by reference to the conception
of relevance, which has been already discussed. Whether
there really are material external causal laws, how far causal
connection is distinct from logical connection, and other such
questions, are profoundly associated with the ultimate problems
of logic and probability and with many of the topics, especially
those of \Partref{III}., of this treatise. But I have nothing useful to
say about them. Nearly everything with which I deal can be
expressed in terms of logical relevance. And the relations between
logical relevance and material cause must be left doubtful.
%% -----File: 177.png---Folio 166-------
\index{Cournot, and frequency theory!independence@{and independence}}%

\Paragraph{4.} It will be useful to give a few examples out of writers who,
as I conceive, have been led into mistakes through misapprehending
the significance of Independence.

Cournot,\footnote
  {For some account of Cournot, see Chapter~XXIV. §\;3.}
in his work on Probability, which after a long period
of neglect has come into high favour with a modern school of
thought in France, distinguishes between `subjective probability'
based on ignorance and `objective probability' based on the
calculation of `objective possibilities,' an `objective possibility'
being a chance event brought about by the combination or convergence
of phenomena belonging to \emph{independent} series. The
existence of objectively chance events depends on his doctrine
that, as there are series of phenomena causally dependent, so
there are others between the causal developments of which there
is independence. These objective possibilities of Cournot's,
whether they be real or fantastic, can have, however, small
importance for the theory of probability. For it is not known
to us what series of phenomena are thus independent. If we had
to wait until we knew phenomena to be independent in this sense
before we could use the simplified multiplication theorem, most
mathematical applications of probability would remain hypothetical.

\Paragraph{5.} Cournot's `objective probability,' depending wholly on
objective fact, bears some resemblances to the conception in the
minds of those who adopt the frequency theory of probability.
The proper definition of independence on this theory has been
\index{Yule!independence@{and independence}}%
given most clearly by Mr.~Yule\footnote
  {``Notes on the Theory of Association of Attributes in Statistics,'' \textit{Biometrika},
  vol.~ii.\ p.~125.} as follows:

``Two attributes $A$~and~$B$ are usually defined to be independent,
within any given field of observation or `universe,'
when the chance of finding them together is the product of the
chances of finding either of them separately. The physical
meaning of the definition seems rather clearer in a different
form of statement, viz.\ if we define $A$~and~$B$ to be independent
\emph{when the proportion of~$A$'s amongst the~$B$'s of the given universe is
the same as in that universe at large}. If, for instance, the question
were put, `What is the test for independence of smallpox attack
and vaccination?' the natural reply would be, `The percentage
of vaccinated amongst the attacked should be the same as in
the general population.'\ldots''
%% -----File: 178.png---Folio 167-------
\index{McColl, and symbolic probability!Boole@{and Boole}|inote}%
\index{Wilbraham, H., and Boole|inote}%

This definition is consistent with the rest of the theory
to which it belongs, but is, at the same time, open to the
general objections to it.\footnote
  {See \Chapref{VIII}\@.}
Mr.~Yule admits that $A$~and~$B$ may be
independent in the world at large but not in the world of~$C$'s.
The question therefore arises as to what world given evidence
specifies, and whether any step forward is possible when, as is
generally the case, we do not know for certain what the proportions
in a given world actually are. As in the case of Cournot's
independent series, it is in general impossible that we should
know whether $A$~and~$B$ are or are not independent in this sense.
The logical independence for knowledge which justifies our
reasoning in a certain way must be something different from
either of these objective forms of independence.

\Paragraph{6.} I come now to Boole's treatment of this subject. The
\index{Boole!independence@{and independence}}%
central error in his system of probability arises out of his giving
two inconsistent definitions of `independence.'\footnote
  {Boole's mistake was pointed out, accurately though somewhat obscurely,
  by H.~Wilbraham in his review ``On the Theory of Chances developed in Professor
  Boole's \textit{Laws of Thought}'' (\textit{Phil.\ Mag.}\ 4th~series, vol.~vii., 1854). Boole
  failed to understand the point of Wilbraham's criticism, and replied hotly,
  challenging him to impugn any individual results (``Reply to some Observations
  published by Mr.~Wilbraham,'' \textit{Phil.\ Mag.}\ 4th~series, vol.~viii., 1854). He
  returned to the same question in a paper entitled ``On a General Method in
  the Theory of Probabilities,'' \textit{Phil.\ Mag.}\ 4th~series, vol.~viii., 1854, where he
  endeavours to support his theory by an appeal to the Principle of Indifference.
  McColl, in his ``Sixth Paper on Calculus of Equivalent Statements,'' saw
  that Boole's fallacy turned on his definition of Independence; but I do
  not think he understood, at least he does not explain, where precisely Boole's
  mistake lay.}
He first wins
the reader's acquiescence by giving a perfectly correct definition:
``Two events are said to be independent when the
probability of the happening of either of them is unaffected by
our \emph{expectation} of the occurrence or failure of the other.''\footnote
  {\textit{Laws of Thought}, p.~255. The italics in this quotation are mine.}
But
a moment later he interprets the term in quite a different sense;
for, according to Boole's second definition, we must regard the
events as independent unless we are told either that they \emph{must}
concur or that they \emph{cannot} concur. That is to say, they are independent
unless we know for certain that there is, in fact, an
invariable connection between them. ``The simple events, $x$,~$y$,~$z$,
will be said to be \emph{conditioned} when they are not free to occur in
every possible combination; in other words, when some compound
event depending upon them is precluded from occurring\ldots.
%% -----File: 179.png---Folio 168-------
\index{De Morgan!independence@{and independence}}%
Simple unconditioned events are by definition independent.''\footnote
  {\textit{Op.~cit.}\ p.~258.}
In fact as long as $xz$ is \emph{possible}, $x$~and~$z$ are independent. This is
plainly inconsistent with Boole's first definition, with which he
makes no attempt to reconcile it. The consequences of his employing
the term independence in a double sense are far-reaching.
For he uses a method of reduction which is only valid when the
arguments to which it is applied are independent in the first
sense, and assumes that it is valid if they are independent in the
second sense. While his theorems are true if all the propositions
or events involved are independent in the first sense, they are not
true, as he supposes them to be, if the events are independent
only in the second sense. In some cases this mistake involves
him in results so paradoxical that they might have led him
to detect his fundamental error.\footnote
  {There is an excellent instance of this, \textit{Laws of Thought}, p.~286. Boole
  discusses the problem: Given the probability~$p$ of the disjunction `either~$Y$
  is true, or $X$~and~$Y$ are false,' required the probability of the conditional proposition,
  `If $X$~is true, $Y$~is true.' The two propositions are formally equivalent;
  but Boole, through the error pointed out above, arrives at the result $\dfrac{cp}{1 - p + cp}$,
  where $c$~is the probability of `If either $Y$~is true, or $X$~and~$Y$ false, $X$~is true.'
  His explanation of the paradox amounts to an assertion that, so long as two
  propositions, which are formally equivalent when true, are only probable, they
  are not necessarily equivalent.}
Boole was almost certainly
led into this error through supposing that the \textit{data} of a
problem can be of the form, ``Prob.~$x = p$,'' \ie~that it is
sufficient to state that the probability of a proposition is such
and such, without stating to what premisses this probability is
referred.\footnote
  {In studying and criticising Boole's work on Probability, it is very important
  to take into account the various articles which he contributed to the
  \textit{Philosophical Magazine} during 1854, in which the methods of \textit{The Laws of
  Thought} are considerably improved and modified. His last and most considered
  contribution to Probability is his paper ``On the application of the Theory of
  Probabilities to the question of the combination of testimonies or judgments,''
  to be found in the \textit{Edin.\ Phil.\ Trans.}\ vol.~xxi., 1857. This memoir contains a
  simplification and general summary of the method originally proposed in \textit{The
  Laws of Thought}, and should be regarded as superseding the exposition of that
  book. In spite of the error already alluded to, which vitiates many of his
  conclusions, the memoir is as full as are his other writings of genius and
  originality.}

It is interesting that De~Morgan should have given,
incidentally, a definition of independence almost identical
with Boole's second definition: ``Two events are independent
if the latter might have existed without the former, or the
%% -----File: 180.png---Folio 169-------
\index{Macfarlane, and independence|inote}%
former without the latter, for anything that we know to the
contrary''\footnote
  {``Essay on Probabilities'' in the \textit{Cabinet Encyclopaedia}, p.~26. De~Morgan
  is not very consistent with himself in his various distinct treatises on this
  subject, and other definitions may be found elsewhere. Boole's second definition
  of Independence is also adopted by Macfarlane, \textit{Algebra of Logic}, p.~21.}

\Paragraph{7.} In many other cases errors have arisen, not through a
misapprehension of the meaning of independence, but merely
through careless assumptions of it, or through enunciating the
Theorem of Multiplication without its qualifying condition.
Mathematicians have been too eager to assume the legitimacy
of those complicated processes of multiplying probabilities, for
which the greater part of the mathematics of probability is
engaged in supplying simplifications and approximate solutions.
Even De~Morgan was careless enough in one of his writings\footnote
  {``Theory of Probabilities'' in the \textit{Encyclopaedia Metropolitana}.}
to enunciate the Multiplication Theorem in the following form:
``The probability of the happening of two, three, or more events
is the product of the probabilities of their happening separately
(p.~398)\ldots. Knowing the probability of a compound event,
and that of one of its components, we find the probability
of the other by dividing the first by the second. This is a
mathematical result of the last too obvious to require further
proof (p.~401).''

An excellent and classic instance of the danger of wrongful
assumptions of independence is given by the problem of determining
the probability of throwing heads twice in two consecutive
tosses of a coin. The plain man generally assumes without
hesitation that the chance is~$(\frac{1}{2})^2$. For the \textit{à~priori} chance of
heads at the first toss is~$\frac{1}{2}$, and we might naturally suppose that
the two events are independent,---since the mere fact of heads
having appeared once can have no influence on the next toss.
But this is not the case unless we know for certain that the coin
is free from bias. If we do not know whether there is bias, or
which way the bias lies, then it is reasonable to put the probability
somewhat higher than~$(\frac{1}{2})^2$. The \emph{fact} of heads having appeared
at the first toss is not the cause of heads appearing at the second
also, but the \emph{knowledge}, that the coin has fallen heads already,
affects our forecast of its falling thus in the future, since heads in
the past may have been due to a cause which will favour heads
in the future. The possibility of bias in a coin, it may be noticed,
%% -----File: 181.png---Folio 170-------
\index{D'Alembert|inote}%
always favours `runs'; this possibility increases the probability
both of `runs' of heads and of `runs' of tails.

This point is discussed at some length in \Chapref{XXIX}. and
further examples will be given there. In this chapter, therefore,
I will do no more than refer to an investigation by Laplace and
\index{Laplace!independence@{and independence}}%
to one real and one supposed fallacy of Independence of a type
with which we shall not be concerned in \Chapref{XXIX}\@.

\Paragraph{8.}\Pagelabel{170} Laplace, in so far as he took account at all of the considerations
explained in §\;7, discussed them under the heading of \textit{Des
inégalités inconnues qui peuvent exister entre les chances que l'on
suppose égales}.\footnote
  {\textit{Essai philosophique}, p.~49. See also ``Mémoire sur les Probabilités,'' \textit{Mém.\
  de l'Acad.}\ p.~228, and cp.\ D'Alembert, ``Sur le calcul des probabilités,''
  \textit{Opuscules mathématiques} (1780), vol.~vii.}
In the case, that is to say, of the coin with
unknown bias, he held that the true probability of heads even
at the first toss differed from~$\frac{1}{2}$ by an amount unknown. But
this is not the correct way of looking at the matter. In the
supposed circumstances the \emph{initial} chances for heads and tails
respectively at the first toss really are equal. What is not true
is that the initial probability of `heads twice' is equal to the
probability of `heads once' squared.

Let us write `heads at first toss' $= h_1$; `heads at second toss'
$= h_2$. Then $h_1/h = h_2/h = \frac{1}{2}$, and $h_1h_2/h = h_2/h_1h · h_1/h$. Hence
$h_1h_2/h = \{h_1/h\}^2$ only if $h_2/h_1h = h_2/h$, \ie~if the knowledge that
heads has fallen at the first toss does not affect in the least the
probability of its falling at the second. In general, it is true that
$h_2/h_1h$ will not differ greatly from~$h_2/h$ (for relative to most hypotheses
heads at the first toss will \emph{not much} influence our expectation
of heads at the second), and $\frac{1}{4}$~will, therefore, give a good approximation
to the required probability. Laplace suggests an ingenious
method by which the divergence may be diminished. If we
throw two coins and define `heads' at any toss as the face thrown
by the second coin, he discusses the probability of `heads twice
running' with the first coin. The solution of this problem
involves, of course, particular assumptions, but they are of a kind
more likely to be realised in practice than the complete absence
of bias. As Laplace does not state them, and as his proof is
incomplete, it may be worth while to give a proof in detail.

Let $h_1$,~$t_1$, $h_2$,~$t_2$ denote heads and tails respectively with
the first and second coins respectively at the first toss, and
$h_1'$,~$t_1'$, $h_2'$,~$t_2'$ the corresponding events at the second toss, then
%% -----File: 182.png---Folio 171-------
the probability (with the above convention) of `heads twice running,'
\ie~agreement between the two coins twice running, is
\[
(h_2h_2' + t_2t_2')(h_1h_1' + t_1t_1')/h
  = (h_2h_2' + t_2t_2')/(h_1h_1' + t_1t_1', h) · (h_1h_1' + t_1t_1')/h.
\]
Since $h_2h_2'/(h_1h_1' + t_1t_1', h) = t_2t_2'/(h_1h_1' + t_1t_1', h)$ by the Principle
of Indifference, and $h_2h_2't_2t_2'/h = 0$.
\[
\therefore (h_2h_2' + t_2t_2')/(h_1h_1' + t_1t_1', h)
  = 2 · h_2h_2'/(h_1h_1' + t_1t_1', h)
  \text{ by~(24.1).}
\]
\begin{DPgather*}
\lintertext{Similarly}
  (h_1h_1' + t_1t_1')/h = 2h_1h_1'/h.
\end{DPgather*}

We may assume that $h_1/h_1'h = h_1/h$, \ie~that heads with one
coin is irrelevant to the probability of heads with the other; and
$h_1/h = h_1'/h = \frac{1}{2}$ by the Principle of Indifference, so that
\index{Principle of Indifference}%
\begin{align*}
(h_1h_1' + t_1t_1')/h = 2\left(\tfrac{1}{2}\right)^2
  &= \tfrac{1}{2}.\\
\therefore (h_2h_2' + t_2t_2')(h_1h_1' + t_1t_1')/h
  &= 2h_2h_2'/(h_1h_1' + t_1t_1', h) · \tfrac{1}{2}\\
  &=  h_2h_2'/(h_1h_1' + t_1t_1', h)\\
  &= \tfrac{1}{2} h_2/(h_2', h_1h_1' + t_1t_1', h),
\end{align*}
since, $(h_1h_1' + t_1t_1')$ being irrelevant to $h'_2/h$, $h'_2/(h_1h_1' + t_1t_1',\,h) =
h_2'/h = \frac{1}{2}$.

Now $h_2/(h_2', h_1h_1' + t_1t_1', h)$ is greater than~$\frac{1}{2}$, since the fact of
the coins having agreed once may be \emph{some} reason for supposing
they will agree again. But it is less than~$h_2/h_1h$: for we may
assume that $h_2/(h_2', h_1h_1' + t_1t_1', h)$ is less than $h_2/(h_2', h_1h_1', h)$,
and also that $h_2/(h_2', h_1h_1', h) = h_2/h_1h$, \ie~that heads twice
running with one coin does not increase the probability of heads
twice running with a different coin. Laplace's method of tossing,
therefore, yields with these assumptions, more or less legitimate
according to the content of~$h$, a probability nearer to~$\frac{1}{4}$ than is
$h_1h_2/h$. If $h_2/(h_2', h_1h_1' + t_1t_1', h) = \frac{1}{2}$, then the probability is
exactly~$\frac{1}{4}$.

\Paragraph{9.} Two other examples will complete this rather discursive
commentary. It has been supposed that by the Principle of
Indifference the probability of the existence of iron upon Sirius
is~$\frac{1}{2}$, and that similarly the probability of the existence there of
any other element is also~$\frac{1}{2}$. The probability, therefore, that
not one of the $68$~terrestrial elements will be found on Sirius
is~$(\frac{1}{2})^{68}$, and that at least one will be found there is $1 - \left(\frac{1}{2}\right)^{68}$ or
approximately certain. This argument, or a similar one, has
been seriously advanced. It would seem to prove also, amongst
%% -----File: 183.png---Folio 172-------
\index{Kries, von!Principle of Indifference@{and Principle of Indifference}}%
\index{Maxwell|inote}%
\index{Nitsche, A.|inote}%
\index{Stumpf|inote}%
many other things, that at least one college exactly resembling
some college at either Oxford or Cambridge will almost certainly
be found on Sirius. The fallacy is partly due, as has been pointed
out by Von~Kries and others, to an illegitimate use of the Principle
of Indifference. The probability of iron on Sirius is \emph{not}~$\frac{1}{2}$. But
the result is also due to the fallacy of false independence.
It is assumed that the known existence of $67$~terrestrial
elements on Sirius would not increase the probability of the
sixty-eighth's being found there also, and that their known
absence would not decrease the sixty-eighth's probability.\footnote
  {See Von Kries, \textit{Die Principien der Wahrscheinlichkeitsrechnung}, p.~10.
  Stumpf (\textit{Über den Begriff der mathem.\ Wahrscheinlichkeit}, pp.~71--74) argues that
  the fallacy results from not taking into account the fact that there might be as
  many metals as atomic weights, and that therefore the chance of iron is~$\dfrac{1}{z}$, where
  $z$~is the number of possible atomic weights. A.~Nitsche (\textit{Vierteljsch.\ f.~wissensch.\
  Philos.}, 1892) thinks that the real alternatives are~$0$, or only~$1$, or only~$2\ldots$ or
  $68$~terrestrial elements on Sirius, and that these are equally probable, the chance
  of each being~$\dfrac{1}{69}$.}

\Paragraph{10.} The other example is that of Maxwell's classic mistake in
\index{Maxwell!theory of gases@{and theory of gases}}%
the theory of gases.\footnote
  {I take the statement of this from Bertrand's \textit{Calcul des probabilités}, p.~30.
\index{Bertrand!Maxwell@{and Maxwell}|inote}%
  Let me here quote a precocious passage on Probability regarded as a branch of
  Logic, from a letter written by Maxwell in his nineteenth year (1850), before
  he came up to Cambridge: ``They say that Understanding ought to work
  by the rules of right reason. These rules are, or ought to be, contained in
  Logic; but the actual science of logic is conversant at present only with things
  either certain, impossible, or entirely doubtful, none of which (fortunately)
  we have to reason on. Therefore the true logic for this world is the calculus
  of Probabilities, which takes account of the magnitude of the probability
  which is, or ought to be, in a reasonable man's mind'' (\textit{Life}, page~143).}
According to this theory molecules of gas
move with great velocity in every direction. Both the directions
and velocities are unknown, but the probability that a molecule
has a given velocity is a function of that velocity and is independent
of the direction. The maximum velocity and the mean
velocity vary with the temperature. Maxwell seeks to
determine, on these conditions alone, the probability that a
molecule has a given velocity. His argument is as follows:

If $\phi(x)$ represents the probability that the component of
velocity parallel to the axis of~$X$ is~$x$, the probability that the
velocity has components $x$,~$y$,~$z$ parallel to the three axes is
$\phi(x)\phi(y)\phi(z)$. Thus if $F(v)$ represents the probability of a total
velocity~$v$, we have $\phi(x)\phi(y)\phi(z)=F(v)$, where $v^2 = x^2 + y^2 + z^2$.
It is not difficult to deduce from this (assuming that the
%% -----File: 184.png---Folio 173-------
\index{Kries, von!independence@{and independence}}%
\index{Poincaré, Henri!independence@{and independence}}%
functions are analytical) that $\phi(x)$~must be of the form
$Ge^{-k^2x^2}$.

It is generally agreed at the present time that this result is
erroneous. But the nature of the error is, I think, quite different
from what it is commonly supposed to be.

Bertrand,\index{Bertrand!independence@{and independence}}\footnote
  {\textit{Calcul des probabilités}, p.~30.}
Poincaré,\footnote
  {\textit{Calcul des probabilités} (2nd ed.), pp.~41--44.}
and Von~Kries,\footnote
  {\textit{Wahrscheinlichkeitsrechnung}, p.~199.}
all cite this argument of
Maxwell's as an illustration of the fallacy of Independence; and
argue that $\phi(x)$,~$\phi(y)$, and~$\phi(z)$ cannot, as he assumes, represent
independent probabilities, if, as he also assumes, the probability
of a velocity is a function of that velocity. But it is not in this
way that the error in the result really arises. If we do not know
\emph{what} function of the velocity the probability of that velocity is,
a knowledge of the velocity parallel to the axes of $x$~and~$y$ tells
us nothing about the velocity parallel to the axis of~$z$. Maxwell
was, I think, quite right to hold that a mere assumption that the
probability of a velocity is \emph{some} function of that velocity, does
\emph{not} interfere with the mutual independence of statements as to
the velocity parallel to each of the three axes. Let us denote
the proposition, `the velocity parallel to the axis of~$X$ is~$x$' by
$X(x)$, the corresponding propositions relative to the axes of $Y$
and~$Z$ by $Y(y)$ and~$Z(z)$, and the proposition `the total
velocity is~$v$' by~$V(v)$; and let $h$~represent our \textit{à~priori} data.
Then if $X(x)/h = \phi(x)$ it is a justifiable inference from the
Principle of Indifference that $Y(y)/h = \phi(y)$ and $Z(z)/h = \phi(z)$.
Maxwell infers from this that $X(x)Y(y)Z(z)/h = \phi(x)\phi(y)\phi(z)$.
That is to say, he assumes that $Y(y)/X(x) · h = Y(y)/h$ and
that $Z(z)/Y(y) · X(x) · h = Z(z)/h$. I do not agree with the
authorities cited above that this is illegitimate. So long as
we do not know what function of the total velocity the probability
of that velocity is, a knowledge of the velocities parallel
to the axes of $x$ and~$y$ has no bearing on the probability of a given
velocity parallel to the axis of~$z$. But Maxwell goes on to infer
that $X(x)Y(y)Z(z)/h = V(v)/h$ where $v^2 = x^2 + y^2 + z^2$. It is here,
and in a very elementary way, that the error creeps in. The
propositions $X(x)Y(y)Z(z)$ and~$V(v)$ are \emph{not} equivalent. The
latter follows from the former, but the former does not follow
from the latter. There is more than one set of values $x$,~$y$,~$z$,
%% -----File: 185.png---Folio 174-------
\index{Bayes, and Inverse Probability}%
\index{Bernoulli, Daniel, and Inverse Probability}%
\index{Price and Bayes|inote}%
which will yield the same value $v$. Thus the probability $V(v)/h$
is much greater than the probability $X(x)Y(y)Z(z)/h$. As we do
not know the direction of the total velocity $v$, there are many
ways, not inconsistent with our \textit{data}, of resolving it into components
parallel to the axes. Indeed I think it is a legitimate
extension of the preceding argument to put $V(v)/h = \phi(v)$; for
there is no reason for thinking differently about the direction
$V$ from what we think about the direction $X$.

A difficulty analogous to this occurs in discussing the problem
of the dispersion of bullets over a target---a subject round which,
on account of a curiosity which it seems to have raised in the
minds of many students of probability, a literature has grown up
of a bulk disproportionate to its importance.

\Paragraph{11.} I now pass to the Principle of Inverse Probability, a
\index{Inverse Probability}%
theorem of great importance in the history of the subject. With
various arguments which have been based upon it I shall deal
in \Chapref{XXX}\@. But it will be convenient to discuss here the
history of the Principle itself and of attempts at proving it.

It first makes its appearance somewhat late in the history of
the subject. Not until 1763, when Bayes's theorem was communicated
to the Royal Society,\footnote
  {Published in the \textit{Phil.\ Trans.}\ vol.~liii., 1763, pp.~376--398. This Memoir
  was communicated by Price after Bayes's death; there was a second Memoir
  in the following year (vol.~liv.\ pp.~298--310), to which Price himself made some
  contributions. See Todhunter's \textit{History}, pp.~299 \textit{et~seq}. Thomas Bayes was
  a dissenting minister of Tunbridge Wells, who was a Fellow of the Royal Society
  from 1741 until his death in 1761. A German edition of his contributions to
  Probability has been edited by Timerding.}
was a rule for the determination
of inverse probabilities explicitly enunciated. It is true that
solutions to inductive problems requiring an implicit and more
or less fallacious use of the inverse principle had already been
propounded, notably by Daniel Bernoulli in his investigations
into the statistical evidence in favour of inoculation.\footnote
  {``Essai d'une nouvelle analyse de la mortalité causée par la petite vérole,
  et des avantages de l'inoculation pour la prévenir,'' \textit{Hist.\ de~l'Acad.}, Paris, 1760
  (published 1766). Bernoulli argued that the recorded results of inoculation
  rendered it a probable cause of immunity. This is an inverse argument, though
  Bayes's theorem is not used in the course of it. See also D.~Bernoulli's \textit{Memoir
  on the Inclinations of the Planetary Orbits}.}
But the
appearance of Bayes's \textit{Memoir} marks the beginning of a new
stage of development. It was followed in 1767 by a contribution
\index{Michell!Inverse Probability@{and Inverse Probability}}%
from Michell\footnote
  {Michell's argument owes more, perhaps, to Daniel Bernoulli than to
  Bayes.}
to the \textit{Philosophical Transactions} on the distribution
%% -----File: 186.png---Folio 175-------
of the stars, to which further reference will be made in
\Chapref{XXV}\@. And in 1774 the rule was clearly, though not
quite accurately, enunciated by Laplace in his ``Mémoire sur
\index{Laplace!Inverse Probability@{and Inverse Probability}}%
la probabilité des causes par les évènemens'' (\textit{Mémoires
présentés à l'Académie des Sciences}, vol.~vi., 1774). He states
the principle as follows (p.~623):

``Si\Pagelabel{175} un évènement peut être produit par un nombre~$n$ de
causes différentes, les probabilités de l'existence de ces causes
prises de l'évènement sont entre elles comme les probabilités de
l'évènement prises de ces causes; et la probabilité de l'existence
de chacune d'elles est égale à la probabilité de l'évènement prise
de cette cause, divisée par la somme de toutes les probabilités
de l'évènement prises de chacune de ces causes.''

He speaks as if he intended to prove this principle, but he only
\DPtypo{give}{gives} explanations and instances without proof. The principle is
not strictly true in the form in which he enunciates it, as will be
seen on reference to theorems~(38) of \Chapref{XIV}.; and the
omission of the necessary qualification has led to a number of
fallacious arguments, some of which will be considered in \Chapref{XXX}\@.

\Paragraph{12.} The value and originality of Bayes's \textit{Memoir} are considerable,
and Laplace's method probably owes much more to
it than is generally recognised or than was acknowledged by
Laplace. The principle, often called by Bayes's name, does not
appear in his \textit{Memoir} in the shape given it by Laplace and
usually adopted since; but Bayes's enunciation is strictly correct
and his method of arriving at it shows its true logical connection
with more fundamental principles, whereas Laplace's enunciation
gives it the appearance of a \emph{new} principle specially introduced
for the solution of causal problems. The following passage\footnote
  {Quoted by Todhunter, \textit{op.~cit.}\ p.~296. Todhunter underrates the importance
\index{Todhunter!Bayes@{and Bayes}}%
  of this passage, which he finds unoriginal, yet obscure.}
gives, in my opinion, a right method of approaching the
problem: ``If there be two subsequent events, the probability
of the second~$\dfrac{b}{N}$ and the probability of both together~$\dfrac{P}{N}$, and, it
being first discovered that the second event has happened, from
hence I guess that the first event has also happened, the probability
I am in the right is~$\dfrac{P}{b}$.'' If the occurrence of the first event
%% -----File: 187.png---Folio 176-------
\index{Donkin, W. F.!Inverse Probability@{and Inverse Probability}}%
\index{Kries, von!Inverse Probability@{and Inverse Probability}}%
\index{McColl, and symbolic probability!Inverse Probability@{and Inverse Probability}}%
\index{Markoff, A. A.!Inverse Probability@{and Inverse Probability}}%
is denoted by~$a$ and of the second by~$b$, this corresponds to
$ab/h = a/bh · b/h$ and therefore $a/bh = \dfrac{ab/h}{b/h}$; for $ab/h = \dfrac{P}{N}$, $b/h = \dfrac{b}{N}$,
$a/bh = \dfrac{P}{b}$. The direct and indeed fundamental dependence of the
inverse principle on the rule for compound probabilities was not
appreciated by Laplace.

\Paragraph{13.} A number of proofs of the theorem have been attempted
since Laplace's time, but most of them are not very satisfactory,
and are generally couched in such a form that they do no more
than recommend the plausibility of their thesis. Mr.~McColl\footnote
  {``Sixth Paper on the Calculus of Equivalent Statements,'' \textit{Proc.\ Lond.\
  Math.\ Soc\DPtypo{}{.}}, 1897, vol.~xxviii.\ p.~567. See also p.~155 above.}
gave
a symbolic proof, closely resembling theorem~(38) when differences
of symbolism are allowed for; and a very similar proof
has also been given by A.~A. Markoff.\footnote
  {\textit{Wahrscheinlichkeitsrechnung}, p.~178.}
I am not acquainted with
any other rigorous discussion of it.

Von Kries\footnote
  {\textit{Die Principien der Wahrscheinlichkeitsrechnung}, pp.~117--121. The above
  account of Von Kries's argument is much condensed.}
presents the most interesting and careful example
of a type of proof which has been put forward in one shape or
another by a number of writers. We have initially, according to
this view, a certain number of hypothetical possibilities, all
equally probable, some favourable and some unfavourable to our
conclusion. Experience, or rather knowledge that the event
has happened, rules out a number of these alternatives, and we
are left with a field of possibilities narrower than that with which
we started. Only part of the original field or \textit{Spielraum} of
possibility is now admissible (\textit{zulässig}). Causes have \textit{à~posteriori}
probabilities which are proportional to the extent of their occurrence
in the now restricted field of possibility.

There is much in this which seems to be true, but it hardly
amounts to a proof. The whole discussion is in reality an
appeal to intuition. For how do we know that the possibilities
admissible \textit{à~posteriori} are still, as they were assumed to be \textit{à~priori},
equal possibilities? Von~Kries himself notices that there
is a difficulty; and I do not see how he is to avoid it, except by
the introduction of an axiom.

This was in fact the course taken by Professor Donkin in 1851,
in an article which aroused some interest in the \textit{Philosophical
%% -----File: 188.png---Folio 177-------
\index{Markoff, A. A.|inote}%
Magazine} at the time, but which has since been forgotten.
Donkin's theory is, however, of considerable interest. He laid
down as one of the fundamental principles of probability the
following:\footnote
  {``On certain Questions relating to the Theory of Probabilities,'' \textit{Phil.\ Mag\DPtypo{}{.}}\
  4th~series, vol.~i., 1851.}

``If there be any number of mutually exclusive hypotheses
$h_1h_2h_3 \ldots$ of which the probabilities relative to a particular state
of information are $p_1p_2p_3 \ldots$, and if new information be gained
which changes the probabilities of some of them, suppose of
$h_{m+1}$~and all that follow, without having otherwise any reference
to the rest, then the probabilities of these latter have the \emph{same
ratios} to one another, \emph{after} the new information, that they had
before.''\footnote
  {It is interesting to notice that an axiom, practically equivalent to this,
  has been laid down more lately by A.~A. Markoff (\textit{Wahrscheinlichkeitsrechnung},
  p.~8) under the title `Unabhängigkeitsaxiom.'}

Donkin goes on to say that the most important case is where
the new information consists in the knowledge that some of the
hypotheses must be rejected, without any further information
as to those of the original set which are retained. This is the
proposition which Von~Kries requires.

As it stands, the phrase ``without having otherwise any
reference to the rest'' obviously lacks precision. An interpretation,
however, \emph{can} be put upon it, with which the principle is
true. If, given the old information and the truth of one of the
hypotheses $h_1 \ldots h_m$ to the exclusion of the rest, the probability
of what is conveyed by the new information is the \emph{same} whichever
of the hypotheses $h_1 \ldots h_m$ has been taken, then Donkin's
principle is valid. For let $a$~be the old information, $a'$~the new,
and let $h_r/a = p_r$, $h_r/aa' = p_r'$; then
\[
p_r' = h_r/aa' = \frac{h_ra'/a}{a/'a} = \frac{a'/h_ra · p_r}{a'/a},
\]
$\therefore \dfrac{p_r'}{p_r} = p_s'/p_s$, etc., if $a'/h_ra = a'/h_sa$, which is the condition already
explained.

\Paragraph{14.} Difficulties connected with the Inverse Principle have
arisen, however, not so much in attempts to \emph{prove} the principle
as in those to \emph{enunciate} it---though it may have been the lack
%% -----File: 189.png---Folio 178-------
\index{De Morgan!Inverse Probability@{and Inverse Probability}}%
\index{Whately and combination of misses}%
of a rigorous proof that has been responsible for the frequent
enunciation of an inaccurate principle.

It will be noticed that in the formula~(38.2) the \textit{à~priori}
probabilities of the hypotheses $a_1$~and~$a_2$ drop out if $p_1 = p_2$, and
the results can then be expressed in a much simpler shape. This
is the shape in which the principle is enunciated by Laplace for
\index{Laplace!Inverse Probability@{and Inverse Probability}}%
the \emph{general} case,\footnote
  {See the passage quoted above, \Pageref{175}.}
and represents the uninstructed view expressed
with great clearness by De~Morgan:\footnote
  {``Essay on Probabilities,'' in the \textit{Cabinet Encyclopædia}, p.~27.}
``Causes are likely or unlikely,
just in the same proportion that it is likely or unlikely
that observed events should follow from them. The most
probable cause is that from which the observed event could most
easily have arisen.'' If this were true the principle of Inverse
Probability would certainly be a most powerful weapon of proof,
even equal, perhaps, to the heavy burdens which have been laid
on it. But the proof given in \Chapref{XIV}. makes plain the
necessity in general of taking into account the \textit{à~priori} probabilities
of the possible causes. Apart from formal proof this
necessity commends itself to careful reflection. If a cause is
very improbable in itself, the occurrence of an event, which
might very easily follow from it, is not necessarily, so long as
there are other possible causes, strong evidence in its favour.
Amongst the many writers who, forgetting the theoretic qualification,
have been led into actual error, are philosophers as diverse
\index{Jevons!Inverse Probability@{and Inverse Probability}}%
\index{Sigwart!Inverse Probability@{and inverse probability}}%
as Laplace, De~Morgan, Jevons, and Sigwart, Jevons\footnote
  {\textit{Principles of Science}, vol.~i.\ p.~280.}
going
so far as to maintain that the fallacious principle he enunciates
is ``that which common sense leads us to adopt almost instinctively.''

\Paragraph{15.} The theory of the combination of premisses dealt with
\index{Combination of premisses}%
in §§\;7,~8 of \Chapref{XIV}. has not often been discussed, and the
history of it is meagre. Archbishop Whately\footnote
  {\textit{Logic}, 8th~ed.\ p.~211: ``As in the case of two probable premisses, the
  conclusion is not established except upon the supposition of their being \emph{both}
  true, so in the case of two distinct and independent indications of the truth
  of some proposition, unless \emph{both} of them fail, the proposition must be true:
  we therefore multiply together the fractions indicating the probability of the
  failure of each---the chances against it---and, the result being the total chances
  against the establishment of the conclusion by these arguments, this fraction
  being deducted from unity, the remainder gives the probability \emph{for} it. \Eg~a
  certain book is conjectured to be by such and such an author, partly, 1st,~from
  its resemblance in style to his known works; partly, 2nd,~from its being attributed
  to him by some one likely to be pretty well informed. Let the probability
  of the conclusion, as deduced from one of these arguments by itself, be supposed~$\frac{2}{5}$,
  and in the other case~$\frac{3}{7}$; then the \emph{opposite} probabilities will be $\frac{3}{5}$ and~$\frac{4}{7}$, which
  multiplied together give~$\frac{12}{35}$ as the probability against the conclusion\ldots.''

  The Archbishop's error, in that a negative can always be turned into an
  affirmative by a change of verbal expression, was first pointed out by a mere
  diocesan, Bishop Terrot, in the \textit{Edin.\ Phil.\ Trans.}\ vol.~xxi. The mistake is well
  explained by Boole in the same volume of the \textit{Edin.\ Phil.\ Trans.}: ``A confusion
  may here be noted between the probability that a conclusion is proved, and the
  probability in favour of a conclusion furnished by evidence which does not prove
  it. In the proof and statement of his rule, Archbishop Whately adopts the
  former view of the nature of the probabilities concerned in the data. In the
  exemplification of it, he adopts the latter.''}
was led astray
%% -----File: 190.png---Folio 179-------
\index{De Morgan!combination@{and combination of premisses}}%
\index{Terrot, Bishop!Whately@{and Whately}|inote}%
\index{Terrot, Bishop!combination@{and combination of premisses}}%
by a superficial error, and De~Morgan, adopting the same mistaken
rule, pushed it to the point of absurdity.\footnote
  {``Theory of Probabilities,'' \textit{Encyclopædia Metropolitana}, p.~400. He shows
  by means of it that ``if any assertion appear neither likely nor unlikely in
  itself, then any logical argument in favour of it, however weak the premisses,
  makes it in some degree more likely than not---a theorem which will be readily
  admitted on its own evidence.'' He then gives an example: ``\textit{à~priori}
  vegetation on the planets is neither likely nor unlikely; suppose argument
  from analogy makes it~$\frac{3}{10}$; then the total probability is $\frac{1}{2} + \frac{1}{2}·\frac{3}{10}$ or~$\frac{13}{20}$.'' De~Morgan
  seems to accept without hesitation the conclusion to be derived from
  this, that everything which is not impossible is as probable as not.}
Bishop Terrot\footnote
  {``On the Possibility of combining two or more Probabilities of the same
  Event, so as to form one definite Probability,'' \textit{Edin.\ Phil.\ Trans}., 1856, vol.~xxi.}
\index{Boole!Whately@{and Whately}}%
\index{Boole!combination@{and combination of premisses}}%
approached the question more critically. Boole's\footnote
  {``On the Application of the Theory of Probabilities to the Question of the
  Combination of Testimonies or Judgments,'' \textit{Edin.\ Phil.\ Trans}., 1857, vol.~xxi.}
last and
most considered contribution to the subject of probability dealt
with the same topic. I know of no discussion of it during the
past sixty years.

Boole's treatment is full and detailed. He states the problem
as follows: ``Required the probability of an event~$z$, when two
circumstances $x$~and~$y$ are known to be present,---the probability
of the event~$z$, when we know only of the existence of the circumstances~$x$,
being~$p$, and the probability, when we only know of
the existence of~$y$, being~$q$.''\footnote
  {\textit{Loc.~cit.}\ p.~631. Boole's principle (\textit{loc.~cit.}\ p.~620) that ``the mean strength
  of any probabilities of an event which are founded upon different judgments
  or observations is to be measured by that supposed probability of the event
  \textit{à~priori} which those judgments or observations following thereupon would not
  tend to alter,'' is not correct if it means more than that the mean strength of
  $z/x$~and~$z/y$ is to be measured by~$z/xy$.}
His solution, however, is vitiated
by the fundamental error examined in §\;6 above. Two of his
conclusions may be mentioned for their plausibility, but neither
is valid.

``If the causes in operation, or the testimonies borne,'' he
%% -----File: 191.png---Folio 180-------
\index{Cournot, and frequency theory!on testimony}%
\index{Testimony, theory of}%
argues, ``are, separately, such as to leave the mind in a state of
equipoise as respects the event whose probability is sought,
united they will but produce the same effect.'' If, that is to say,
$a/h_1 = \frac{1}{2}$ and $a/h_2 = \frac{1}{2}$, he concludes that $a/h_1h_2 = \frac{1}{2}$. The plausibility
of this is superficial. Consider, for example, the following
instance: $h_1 = $ $A$~is black and $B$~is black or white, $h_2 = $ $B$~is black
and $A$~is black or white, $a = $ both $A$~and~$B$ are black. Boole also
\index{Boole!testimony@{and testimony}}%
concluded without valid reason that $a/h_1h_2$ increases, the greater
the \textit{à~priori} improbability of the combination~$h_1h_2$.

\Paragraph{16.}\Pagelabel{180} The theory of ``Testimony'' itself, the theory, that is to
say, of the combination of the evidence of witnesses, has occupied
so considerable a space in the traditional treatment of Probability
that it will be worth while to examine it briefly. It may, however,
be safely said that the principal conclusions on the subject set
out by Condorcet, Laplace, Poisson, Cournot, and Boole, are
\index{Condorcet!testimony@{and testimony}}%
\index{Laplace!testimony@{and testimony}}%
\index{Poisson!on testimony}%
demonstrably false. The interest of the discussion is chiefly due
to the memory of these distinguished failures.

It seems to have been generally believed by these and other
logicians and mathematicians\footnote
  {Perhaps M.~Bertrand should be registered as an honourable exception.
  At least he points out a precisely analogous fallacy in an example where two
  meteorologists prophesy the weather, \textit{Calcul des Probabilités}, p.~31.}
that the probability of two
witnesses speaking the truth, who are independent in the sense
that there is no collusion between them, is always the product
of the probabilities that each of them separately will speak the
truth.\footnote
  {\Eg,
    \begin{minipage}[t]{3in}
      Boole, \textit{Laws of Thought}, p.~279. \\
      De~Morgan, \textit{Formal Logic}, p.~195. \\
      Condorcet, \textit{Essai}, p.~4. \\
      Lacroix, \textit{Traité}, p.~248. \\
      Cournot, \textit{Exposition}, p.~354. \\
      Poisson, \textit{Recherches}, p.~323.
    \end{minipage} \\
This list could be greatly extended.}
On this basis conclusions such as the following, for
example, are arrived at:

$X$~and~$Y$ are independent witnesses (\ie\ there is no collusion
between them). The probability that $X$~will speak the truth is~$x$,
that $Y$~will speak the truth is~$y$. $X$~and~$Y$ agree in a particular
statement. The chance that this statement is true is
\[
\frac{xy}{xy + (1 - x)(1 - y)}.
\]
For the chance that they both speak the truth is~$xy$, and the
chance that they both speak falsely is~$(1-x)(1-y)$. As, in this
%% -----File: 192.png---Folio 181-------
case, our hypothesis is that they agree, these two alternatives
are exhaustive; whence the above result, which may be found
in almost every discussion of the subject.

The fallacy of such reasoning is easily exposed by a more
exact statement of the problem. For let $a_1$ stand for ``$X_1$~asserts~$a$,''
and let $a/a_1h = x_1$, where~$h$, our general data, is by itself
irrelevant to~$a$, \ie, $x_1$~is the probability that a statement is true
of which we only know that $X_1$ has asserted it. Similarly let us
write $b/b_2h = x_2$ where $b_2$~stands for ``$X_2$~asserts~$b$.'' The above
argument then assumes that, if $X_1$ and~$X_2$ are witnesses who are
causally independent in the sense there is no collusion between
them direct or indirect, $ab/a_1b_2h = a/a_1h · b/b_2h = x_1x_2$.

But $ab/a_1b_2h = a/a_1bb_2h · b/a_1b_2h$, and this is not equal to $x_1x_2$
unless $a/a_1bb_2h = a/a_1h$ and $b/a_1b_2h = b/b_2h$. It is not a sufficient
condition for this, as seems usually to be supposed, that $X_1$~and~$X_2$
should be witnesses causally independent of one another. It is
also necessary that $a$ and~$b$, \ie\ the propositions asserted by the
witnesses, should be irrelevant to one another and also each of
them irrelevant to the fact of the assertion of the other by a
witness. If a knowledge of~$a$ affects the probability either of~$b$
or of~$b_1$, it is evident that the formula breaks down. In the one
extreme case, where the assertions of the two contradict one
another, $ab/a_1b_2h = 0$. In the other extreme, where the two agree
in the same assertion, \ie\ where $a \equiv b$, $a/a_1bb_2h = 1$ and not $= a/a_1h$.

\Paragraph{17.} The special problem of the agreement of witnesses, who
make the same statement, can be best attacked as follows, a
certain amount of simplification being introduced. Let the
general data~$h$ of the problem include the hypothesis that $X_1$ and~$X_2$
are each asked and reply to a question to which there is only
one correct answer. Let $a_i = $ ``$X_i$~asserts~$a$ in reply to the question,''
and $m_i = $ ``$X_i$~gives the correct answer to the question.''
Then
\[
m_1/a_1h = x_1 \text{ and } m_2/a_2h = x_2,
\]
$x_1$ and~$x_2$ being, in the conventional language of this problem,
the ``credibilities'' of the witnesses. We have, since the witnesses
agree and since $a$~follows from~$m_ia_i$ and $m_i$~follows from~$aa_i$,
\begin{align*}
m_1/a_1a_2h &= m_1m_2/a_1a_2h = m_2/a_1a_2h;\\
a/a_ih      &= m_i/a_ih;\\
a/a_im_ih   &= 1;\quad m_i/aa_ih = 1.
\end{align*}
Also, since the witnesses are, in the ordinary sense, ``independent''
%% -----File: 193.png---Folio 182-------
witnesses, $a_2/a_1ah = a_2/ah$ and $a_2/a_1\bar{a}h = a_2/\bar{a}h$; that is to say, the
probability of $X_2$'s asserting~$a$ is independent of the fact of $X_1$'s
having asserted~$a$, given we know that $a$~is, in fact, true or false,
as the case may be.

The probability that, if the witnesses agree, their assertion is
true is
\begin{gather*}
a/a_1a_2h = m_1/a_1a_2h = \frac{m_1a_2/a_1h}{a_2/a_1h} \\
  = \frac{a_2/a_1m_1h . m_1/a_1 h}{a_2a/a_1h + a_2\bar{a}/a_1 h}
  = \frac{a_2/a_1ah . x_1}{a_2/a_1ah . x_1 + a_2/a_1\bar{a}h . (1 - x_2)}.
\end{gather*}
If this is to be equal to $\dfrac{x_1x_2}{x_1x_2 + (1 - x_1)(1 - x_2)}$, we must have
\[
\frac{a_2/a_1ah}{a_2/a_1\bar{a}h} = \frac{x_2}{1 - x_2}.
\]
\begin{DPalign*}
\lintertext{Now}
\frac{a_2/a_1ah}{a_2/a_1\bar{a}h}
  &= \frac{a_2/ah}{a_2/\bar{a}h} \text{ by the hypothesis of ``independence''}\\
  &= \frac{aa_2/h}{\bar{a}a_2/h} . \frac{\bar{a}/h}{a/h}
   = \frac{a/a_2h}{\bar{a}/a_2 h} . \frac{\bar{a}/h}{a/h}\\
  &= \frac{x_2}{1 - x_2} . \frac{\bar{a}/h}{a/h}.
\end{DPalign*}
This then is the assumption which has tacitly slipped into the
conventional formula,---that $a/h =\bar{a}/h = \frac{1}{2}$.  It is assumed, that
is to say, that any proposition taken at random is as likely as
not to be true, so that \emph{any} answer to a given question is, \textit{à~priori},
as likely as not to be correct. Thus the conventional formula
ought to be employed only in those cases where the answer
which the ``independent'' witnesses agree in giving is, \textit{à~priori}
and apart from their agreement, as likely as not.

\Paragraph{18.} A somewhat similar confusion has led to the controversy
as to whether and in what manner the \textit{à~priori} improbability
of a statement modifies its credibility in the mouth of a witness
whose degree of reliability is known. The fallacy of attaching
the same weight to a testimony regardless of the character of
what is asserted, is pointed out, of course, by Hume in the \textit{Essay
\index{Hume!testimony@{and testimony}}%
on Miracles}, and his argument, that the great \textit{à~priori} improbability
of some assertions outweighs the force of testimony
otherwise reliable, depends on the avoidance of it. The correct
is also taken by Laplace in his \textit{Essai philosophique} (pp\DPtypo{}{.}~98--102),
\index{Laplace!testimony@{and testimony}}%
%% -----File: 194.png---Folio 183-------
\index{Diderot on testimony}%
\index{Johnson, W. E.!testimony@{and testimony}}%
where he argues that a witness is less to be believed
when he asserts an extraordinary fact, declaring the opposite
view (taken by Diderot in the article on ``Certitude'' in the
\textit{Encyclopédie}) to be inconceivable before ``le simple bon sens.''

The manner in which the resultant probability is affected
depends upon the precise meaning we attach to ``degree of reliability''
or ``coefficient of credibility.'' If a witness's credibility
\index{Coefficient of Credibility}%
is represented by~$x$, do we mean that, if $a$~is the true answer,
the probability of his giving it is~$x$, or do we mean that if he
answers~$a$ the probability of $a$'s being true is~$x$? These two things
are not equivalent.

Let $a_1$ stand for ``$a$~is asserted by the witness''; $h_1$~for our
evidence bearing on the witness's veracity; and $h_2$~for other
evidence bearing on the truth of~$a$. Let $a/h_1h_2$, \ie\ the \textit{à~priori}
probability of~$a$ apart from our knowledge of the fact that the
witness has asserted it, be represented by~$p$.

Let $a/a_1h_1 = x_1$ and $a_1/ah_1 = x_2$; so that $x_1 = \dfrac{a/h_1}{a_1/h_1} · x_2$. In
general $a/h_1 \ne a_1/h_1$. Do we mean by the witness's credibility
$x_1$ or~$x_2$?

We require $\DPtypo{a/a_1h_2h_2}{a/a_1h_1h_2}$.

Let $a_1/\bar{a}h_1 = r$, \ie\ the probability, apart from our special
knowledge concerning~$a$, that, if $a$~is false, the witness will hit on
that particular falsehood.
\begin{align*}
a/a_1h_1h_2
  &= \frac{a_1/ah_1h_2 · a/h_1h_2}{a_1/h_1h_2}
   = \frac{x_2p}{a_1a/h_1h_2 + a_1\bar{a}/h_1h_2}\\
  &= \frac{x_2p}{x_2p + a_1/\bar{a}h_1h_2 · (1 - p)}
   = \frac{x_2p}{x_2p + r(1 - p)};
\end{align*}
for $a_1/ah_1h_2 = a_1/ah_1$ and $a_1/\bar{a}h_1h_2 = a_1/\bar{a}h_1$, since, given \emph{certain}
knowledge concerning~$a$, $h_2$~is irrelevant to the probability of~$a_1$.

\Paragraph{19.} Generally speaking, all problems, in regard to the combination
of testimonies or to the combination of evidence derived
from testimony with evidence derived from other sources, may
be treated as special instances of the general problem of the
combination of arguments. Beyond pointing out the above
plausible fallacies, there is little to add. Mr.~W.~E. Johnson,
however, has proposed a method of defining credibility, which
is sometimes valuable, because it regards the witness's credibility
not absolutely, but with reference to a given type of question,
%% -----File: 195.png---Folio 184-------
\index{Bicquilley and testimony|inote}%
\index{Craig and tradition}%
\index{De Morgan!tradition@{and tradition}|inote}%
\index{Lacroix|inote}%
\index{Lee and tradition|inote}%
\index{Peterson and tradition}%
so that it enables us to measure the force of the witness's testimony
under special circumstances. If $a$~represents the fact of $A$'s
testimony regarding~$x$, then we may define $A$'s credibility for~$x$
as~$\DPtypo{a}{\alpha}$, where $\DPtypo{a}{\alpha}$~is given by the equation
\[
x/ah = x/h + \DPtypo{a}{\alpha}\sqrt{x/h · \bar{x}/h};
\]
so that $\DPtypo{a}{\alpha}\sqrt{x/h · \bar{x}/h}$ measures the amount by which $A$'s~assertion
of~$x$ increases its probability.

\Paragraph{20.} One of the most ancient problems in probability is concerned
with the gradual diminution of the probability of a past
event, as the length of the tradition increases by which it is
established. Perhaps the most famous solution of it is that
propounded by Craig in his \textit{Theologiae Christianae Principia
Mathematica}, published in 1699.\footnote
  {See Todhunter's \textit{History}, p.~54. It has been suggested that the anonymous
\index{Todhunter!Craig@{and Craig}}%
  essay in the \textit{Phil.\ Trans.}\ for 1699 entitled ``A Calculation of the Credibility
  of Human Testimony'' is due to Craig. In this it is argued that, if the
  credibilities of a set of witnesses are $p_1 \ldots p_n$, then if they are
  successive the resulting probability is the product $p_1p_2 \ldots p_n$; if they are
  concurrent, it is:
  \[
  1 - (1 - p_1)(1 - p_2) \ldots (1 - p_n).
  \]
  This last result follows from the supposition that the first witness leaves an
  amount of doubt represented by $1 - p_1$; of this the second removes the fraction~$p_2$,
  and so on. See also Lacroix, \textit{Traité élémentaire}, p.~262. The above theory
  was actually adopted by Bicquilley.}
He proves that suspicions of
any history vary in the duplicate ratio of the times taken from
the beginning of the history in a manner which has been described
as a kind of parody of Newton's \textit{Principia}. ``Craig,'' says
Todhunter, ``concluded that faith in the Gospel so far as it
depended on oral tradition expired about the year 880, and that
so far as it depended on written tradition it would expire in the
year 3150. Peterson by adopting a different law of diminution
concluded that faith would expire in 1789.''\footnote
  {In the \textit{Budget of Paradoxes} De~Morgan quotes Lee, the Cambridge Orientalist,
  to the effect that Mahometan writers, in reply to the argument that the Koran
  has not the evidence derived from Christian miracles, contend that, as evidence
  of Christian miracles is daily weaker, a time must at last arrive when it will
  fail of affording assurance that they were miracles at all: whence the necessity
  of another prophet and other miracles.}
About the same
time Locke raised the matter in chap.~xvi.\ bk.~iv.\ of the
\index{Locke!on tradition}%
\textit{Essay Concerning Human Understanding}: ``Traditional testimonies
the farther removed, the less their proof\ldots. No
Probability can rise higher than its first original.'' This is
evidently intended to combat the view that the long acceptance
by the human race of a reputed fact is an additional argument
%% -----File: 196.png---Folio 185-------
\index{Cayley, and tradition}%
\index{Macfarlane, and independence!tradition@{and tradition}}%
in its favour and that a long tradition increases rather than
diminishes the strength of an assertion. ``This is certain,'' says
Locke, ``that what in one age was affirmed upon slight grounds,
can never after come to be more valid in future ages, by being
often repeated.'' In this connection he calls attention to ``a
rule observed in the law of England, which is, that though the
attested copy of a record be good proof, yet the copy of a copy
never so well attested, and by never so credible witnesses, will
not be admitted as a proof in Judicature.'' If this is still a good
rule of law, it seems to indicate an excessive subservience to the
principle of the decay of evidence.

But, although Locke affirms sound maxims, he gives no theory
that can afford a basis for calculation. Craig, however, was the
more typical professor of probability, and in attempting an
algebraic formula he was the first of a considerable family. The
last grand discussion of the problem took place in the columns
of the \textit{Educational Times}.\footnote
  {Reprinted in \textit{Mathematics from the Educational Times}, vol.~xxvii.}
Macfarlane\footnote
  {\textit{Algebra of Logic}, p.~151. Macfarlane attempts a solution of the general
  problem without success. Its solution is not difficult, if enough unknowns are
  introduced, but of very little interest.}
mentions that four
different solutions have been put forward by mathematicians
of the problem: ``$A$~says that $B$~says that a certain event took
place; required the probability that the event did take place,
$p_1$~and~$p_2$ being $A$'s~and~$B$'s respective probabilities of speaking
the truth.'' Of these solutions only Cayley's is correct.
%% -----File: 197.png---Folio 186-------


\Chapter{XVII}{Some Problems in Inverse Probability, including Averages}

\Paragraph{1.} \First{The} present chapter deals with `problems'---that is to
say, with applications to particular abstract questions of some of
the fundamental theorems demonstrated in \Chapref{XIV}\@. It
is without philosophical interest and should probably be omitted
by most readers. I introduce it here in order to show the analytical
power of the method developed above and its advantage
in ease and especially in accuracy over other methods which
have been employed.\footnote
  {Such examples as these might sometimes be set to test the wits of students.
  The problems on Probability usually given are simply problems on mathematical
  combinations. These, on the other hand, are really problems in logic.}
§\;2 is mainly based upon some problems
discussed by Boole. §§\;3--7 deal with the fundamental theory
connecting averages and laws of error. §§\;8--11 treat discursively
the Arithmetic Average, the Method of Least Squares, and
Weighting.

\Paragraph{2.} In the following paragraph solutions are given of some
problems posed by Boole in chapter~xx.\ of his \textit{Laws of Thought}.
Boole's own method of solving them is constantly erroneous,\footnote
  {For the reason given in §\;6 of \Chapref{XVI}\@. The solutions of problems
  I.--VI., for example, in the \textit{Laws of Thought}, chap.~xx., are all erroneous.}
and the difficulty of his method is so great that I do not know
of any one but himself who has ever attempted to use it. The
term `cause' is frequently used in these examples where it might
have been better to use the term `hypothesis.' For by a possible
cause of an event no more is here meant than an antecedent
occurrence, the knowledge of which is relevant to our anticipation
of the event; it does not mean an antecedent from which the
event in question \emph{must} follow.

(56) The \textit{à~priori} probabilities of two causes $A_1$~and~$A_2$
are $c_1$~and~$c_2$ respectively. The probability that if the cause~$A_1$
%% -----File: 198.png---Folio 187-------
\index{Cayley, and tradition!Challenge@{and Challenge Problem}}%
\index{Macfarlane, and independence!Challenge@{and `\textit{Challenge Problem}'}|inote}%
occur, an event~$E$ will accompany it (whether as a consequence
of~$A_1$ or not), is~$p_1$, and the probability that $E$ will accompany~$A_2$,
if $A_2$ present itself, is~$p_2$. Moreover, the event~$E$ cannot appear
in the absence of both the causes $A_1$~and~$A_2$. Required the probability
of the event~$E$.

This problem is of great historical interest and has been called
Boole's `Challenge Problem.' Boole originally proposed it for
\index{Boole!Challenge@{and Challenge Problem}}%
solution to mathematicians in 1851 in the \textit{Cambridge and Dublin
Mathematical Journal}. A result was given by Cayley\footnote
  {\textit{Phil.\ Mag}.\ 4th~series, vol.~vi.}
in the
\textit{Philosophical Magazine}, which Boole declared to be erroneous.\footnote
  {Cayley's solution was defended against Boole by Dedekind (\textit{Crelle's Journal},
\index{Dedekind and `\textit{Challenge Problem}'|inote}%
  vol.~1.\ p.~268). The difference arises out of the extreme ambiguity as to the
  meaning of the terms as employed by Cayley.}
He then entered the field with his own solution.\footnote
  {``Solution of a Question in the Theory of Probabilities,'' \textit{Phil.\ Mag}.\ 4th~series,
  vol.~vii., 1854. This solution is the same as that printed by Boole
  shortly afterwards in the \textit{Laws of Thought}, pp.~321--326. In the \textit{Phil.\ Mag}.\
  Wilbraham gave as the solution $u = c_1p_1 + c_2p_2 - z$, where $z$~is necessarily less
  than either $c_1p_1$ or~$c_2p_2$. This solution is correct so far as it goes, but is not
  complete. The problem is also discussed by Macfarlane, \textit{Algebra of Logic},
  p.~154.}
``Several
attempts at its solution,'' he says, ``have been forwarded to me,
all of them by mathematicians of great eminence, all of them
admitting of particular verification, yet differing from each other
and from the truth.''\footnote
  {In proposing the problem Boole had said: ``The motives which have
  led me, after much consideration, to adopt, with reference to this question, a
  course unusual in the present day, and not upon slight grounds to be revived,
  are the following: First, I propose the question as a test of the sufficiency of
  received methods. Secondly, I anticipate that its discussion will in some
  measure add to our knowledge of an important branch of pure analysis.''
  When printing his own solution in the \textit{Laws of Thought}, he adds, that the
  above ``led to some interesting private correspondence, but did not elicit a
  solution.''}
After calculations of considerable length
and great difficulty he arrives at the conclusion that $u$ is the
probability of the event~$E$ where $u$ is that root of the equation
\[
\frac{\left[1 - c_1(1 - p_1) - u\right]\left[1 - c_2(1 - p_2) - u\right]}{1 - u}
  = \frac{(u - c_1p_1)(u - c_2p_2)}{c_1p_1 + c_2p_2 - u}
\]
which is not less than $c_1p_1$ and~$c_2p_2$ and not greater than
$1 - c_1(1 - p_1)$, $1 - c_2(1 - p_2)$ or $c_1p_1 + c_2p_2$.

This solution can easily be seen to be wrong. For in the
case where $A_1$~and~$A_2$ cannot both occur, the solution is
$u = c_1p_1 + c_2p_2$; whereas Boole's equations do not reduce to
%% -----File: 199.png---Folio 188-------
\index{McColl, and symbolic probability!Challenge@{and `\textit{Challenge Problem}'}|inote}%
this simplified form. The mistake which Boole has made is
the one general to his system, referred to in \Chapref{XVI}., §\;6.\footnote
  {Boole's error is pointed out and a correct solution given in Mr.~M\textsuperscript{c}Coll's
  ``Sixth Article on the Calculus of Equivalent Statements'' (\textit{Proc.\ Lond.\ Math.\
  Soc.}\ vol.~xxviii.\ p.~562).}

The correct solution, which is very simple, can be reached as
follows:

Let $a_1$,~$a_2$,~$e$ assert the occurrences of the two causes and the
event respectively, and let $h$ be the \textit{data} of the problem.

Then we have $a_1/h = c_1$, $a_2/h = c_2$, $e/a_1 h = p_1$, $e/a_2 h = p_2$: we
require~$e/h$. Let $e/h = u$, and let $a_1a_2/eh = z$. Since the event
cannot occur in the absence of both the causes,
\[
e/\bar{a}_1 \bar{a}_2 h = 0.
\]
It follows from this that $\bar{a}_1 \bar{a}_2/eh = 0$, unless $e/h = 0$,
\begin{DPgather*}
\lintertext{\ie}
(a_1 + a_2)/eh = 1,\\
%
\lintertext{whence}
a_1/eh + a_2/eh = 1 + a_1 a_2/eh
  \rintertext{by~(24).}\\
\lintertext{Now}
a_1/eh = \frac{c_1 p_1}{u} \text{ and } a_2/eh = \frac{c_2 p_2}{u},\\
\therefore u = \frac{c_1 p_1 + c_2 p_2}{1 + z},
\end{DPgather*}
where $z$ is the probability after the event that \emph{both} the causes were
present.

If we write $e a_1 a_2/h = y$,
\begin{DPalign*}
y &= a_1 a_2/eh · e/h = uz\\
\lintertext{so that}
u &= (c_1 p_1 + c_2 p_2) - y.
\end{DPalign*}

Boole's solution fails by attempting to be independent of
$y$~or~$z$.

(56.1)\DPtypo{.}{} Suppose that we wish to find limits for the solution
which are independent of $y$~and~$z$: then, since $y \eqslantless 0$,
$u \eqslantless c_1 p_1 + c_2 p_2$.

Again
\[
e/h = e\bar{a}_1/h + ea_1/h
    \eqslantless \bar{a}_1/h + ea_1/h
    \eqslantless 1 - c_2 + c_2 p_2
  \quad\text{by (24.2) and~(4).}
\]
Similarly $e/h \eqslantless -c_2 + c_2p_2$. From the same equations it appears
that $e/h \eqslantless c_1 p_1$ and~$c_2 p_2$.
%% -----File: 200.png---Folio 189-------
%[** TN: In orig, above ends mid-line, but next line not indented.]

\noindent$\therefore u$ lies between
\[
\text{the greatest of }
\smash[t]{\left\{
\begin{aligned}
& c_1p_1\\
& c_2p_2
\end{aligned}
\right.}
\text{ and the least of }
\smash[t]{\left\{
\begin{aligned}
&c_1p_1 + c_2p_2\\
&1 - c_1(1 - p_1)\\
&1 - c_2(1 - p_2).
\end{aligned}
\right.}
\]

It will be seen that these numerical limits are the same as the
limits obtained by Boole for the roots of his equations.

(56.2) Suppose that the \textit{à~priori} probabilities of the causes $c_1$~and~$c_2$
are to be eliminated. The only limit we then have is
$u < p_1 + p_2$.

(56.3) Suppose that one of the \textit{à~priori} probabilities~$c_2$ is to be
eliminated. We then have limits $c_1p_1 \eqslantless u \eqslantless 1 - c_1 + c_1p_1$. If, therefore,
$c_1$~is large, $u$~does not differ widely from~$c_1p_1$.

(56.4) Suppose $p_2$ is to be eliminated. We then have
\begin{align*}
c_1p_1 \eqslantless u
  &\eqslantless c_1p_1 + c_2\\
  &\eqslantless c_1p_1 + 1 - c_1.
\end{align*}

If therefore $c_1$ is large or $c_2$ small, $u$~does not differ widely
from~$c_1p_1$.

(56.5) If $a_1/a_2h = a_1/h$, \ie\ if our knowledge of each of the
causes is independent, we have a closer approximation. For
\begin{gather*}
y = ea_1a_2/h
  = e/a_1a_2h · a_1/a_2h · a_2/h
  = e/a_1a_2h · c_1c_2, \\
%
\therefore u = c_1p_1 + c_2p_2 - c_1c_2 · e/a_1a_2h, \\
%
\therefore u > c_1p_1 + c_2p_2 - c_1c_2.
\end{gather*}

(57) We may now generalise~(56) and discuss the case of $n$~causes.
If an event can only happen as a consequence of one
\emph{or more} of certain causes $A_1$,~$A_2$, $\ldots~A_n$, and if $c_1$ is the \textit{à~priori}
probability of the cause $A_1$ and~$p_1$ the probability that, if the
cause~$A_1$ be known to exist, the event~$E$ will occur: required the
probability of~$E$.

This is Boole's problem~VI. (\textit{Laws of Thought}, p.~336). As
the result of ten pages of mathematics, he finds the solution to be
the root lying between certain limits of an equation of the $n$\ordth~degree
which he cannot solve. I know no other discussion of the
problem. The solution is as follows:
\begin{DPgather*}
e/h = e\bar{a}_1/h + ea_1/h
    = e\bar{a}_1/h + e/a_1h · a_1/h
    = e\bar{a}_1/h + c_1p_1
  \rintertext{(i.)}\\
%
e\bar{a}_1/h
    = e\bar{a}_1\bar{a}_2/h + e\bar{a}_1/a_2h · a_2/h
    = e\bar{a}_1\bar{a}_2/h + c_2 · e\bar{a}_1/a_2h, \\
%
e\bar{a}_1/a_2h
    = e/a_2h - ea_1/a_2h
    = p_2 - \frac{1}{c_2} · ea_1a_2/h,
\end{DPgather*}
%% -----File: 201.png---Folio 190-------
\begin{gather*}
\therefore e/h
  = e\bar{a}_1\bar{a}_2/h + c_1p_1 + c_2p_2 - ea_1a_2/h, \\
    e\bar{a}_1\bar{a}_2/h
  = e\bar{a}_1\bar{a}_2\bar{a}_3/h + e\bar{a}_1\bar{a}_2a_3/h,
\end{gather*}
\begin{DPalign*}
\lintertext{and}
e\bar{a}_1\bar{a}_2a_3/h
  &= e\bar{a}_1\bar{a}_2/a_3h · c_3
   = c_3\left\{e/a_3h - e\overline{\bar{a}_1\bar{a}_2}/a_3/h\right\} \\
  &= c_3p_3 - e\overline{\bar{a}_1\bar{a}_2}a_3/h,
\end{DPalign*}
\[
\therefore e/h
  = e\bar{a}_1\bar{a}_2\bar{a}_3/h + c_1p_1 + c_2p_2 + c_3p_3
  - e\bar{a}_1a_2/h - e\overline{\bar{a}_1\bar{a}_2}a_3/h.
\]
In general
\begin{align*}
e\bar{a}_1\bar{a}_2 \ldots \bar{a}_{r-1}/h
  &= e\bar{a}_1\bar{a}_2 \ldots \bar{a}_{r-1}\bar{a}_r/h
   + e\bar{a}_1\bar{a}_2 \ldots \bar{a}_{r-1}a_r/h \\
%
  &= e\bar{a}_1 \ldots \bar{a}_r/h
   + e\bar{a}_1 \ldots \bar{a}_{r-1}/a_r h · c_r \\
%
  &= e\bar{a}_1 \ldots \bar{a}_r/h
   + c_r \left\{e/a_rh - \overline{e\bar{a}_1 \ldots \bar{a}_{r-1}}/a_rh \right\} \\
%
  &= e\bar{a}_1 \ldots \bar{a}_r/h + c_rp_r
   - e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_r/h.
\end{align*}
\[
\therefore \text{ finally we have } e/h = e\bar{a}_1 \ldots \bar{a}_n/h + \Sum_1^n c_r p_r - \Sum_2^n e\overline{\bar{a} \ldots \bar{a}_{r-1}}a_r/h.
\]
But since the $n$~causes are supposed to be exhaustive
\begin{DPgather*}
e\bar{a}_1 \ldots \bar{a}_n/h = 0,\\
%
\therefore e/h = \Sum_1^n c_r p_r - \Sum_2^n e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_r/h
  \rintertext{(ii.).}\\
%
\lintertext{Let}
e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_r/h = n_r;\\
%
\lintertext{then}
e/h = \Sum_1^n c_r p_r - \Sum_2^n n_r
  \rintertext{(iii.).}
\end{DPgather*}

(57.1) If our knowledge of the several causes is independent,
if, that is to say, our knowledge of the existence of any one of
them is not relevant to the probability of the existence of any
other, so that $a_r/a_sh = a_r/h = c_r$, then
\begin{align*}
e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_r/h
  &= e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}/a_rh · c_r\\
%
  &= c_r · e\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_rh \{1 - \bar{a}_1 \ldots \bar{a}_{r-1}/a_rh\} \\
%
  &= c_r \left[1 - \Prod_1^{r-1}(1 - c_1) \ldots (1 - c_{r-1})\right]e
     /\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_rh.
\end{align*}
\begin{DPgather*}
\lintertext{Let}
e/\overline{\bar{a}_1 \ldots \bar{a}_{r-1}}a_rh = m_r, \\
\lintertext{then}
e/h = \Sum_{r=1}^{r=n} c_r p_r
    - \Sum_{r=2}^{r=n} c_r \left[1 - \Prod_{s=1}^{s=r-1}(1 - c_s)\right]m_r.
\end{DPgather*}

These results do not look very promising as they stand, but
they lead to some useful approximations on the elimination of
$m_r$~and~$n_r$ and to some interesting special cases.
%% -----File: 202.png---Folio 191-------

(57.2) From equation~(i.)\ it follows that $e/h \eqslantgtr c_1p_1$ and
$e/h \eqslantless 1 - c_1(1 - p_1)$; and from equation~(ii.)\ that $e/h \eqslantless \Sum_1^n c_r p_r$;

$\therefore e/h$ lies between
\[
\text{the greatest of }
\left\{
\begin{aligned}
&c_1p_1 \\
&\PadTo{c_1p_1}{\vdots} \\
&c_np_n
\end{aligned}
\right.
\text{ and the least of }
\left\{
\begin{aligned}
&\Sum_1^n c_rp_r \\
&1 - c_1(1 - p_1) \\
& \PadTo{1 - c_1(1 - p_1)}{\vdots} \\
&1 - c_n(1 - p_n).
\end{aligned}
\right.
\]

(57.3) Further, if the causes are independent it follows from~(57.1)
that
\[
e/h \eqslantgtr \Sum_1^n c_r p_r
  - \Sum_2^n c_r {\textstyle\left[1 - \Prod_1^{r-1}(1 - c_s)\right]},
\]
so that $e/h$ lies between
\[
\settowidth{\TmpLen}{greatest}%[** TN: Stacking text to get horizontal fit]
\parbox[c]{\TmpLen}{\centering the\\ greatest\\ of }
\left\{
\begin{aligned}
&{\textstyle\Sum_1^n c_rp_r - \Sum_2^n c_r \bigl[1 - \Prod\limits_1^{r-1}(1 - c_s)\bigr]}\\
&c_1p_1 \\
&\PadTo{c_1p_1}{\vdots} \\
&c_np_n
\end{aligned}
\right.
\settowidth{\TmpLen}{ and the}%
\parbox[c]{\TmpLen}{ and the\\ least of }
\left\{
\begin{aligned}
&{\textstyle\Sum_1^n c_r p_r} \\
&1 - c_1(1 - p_1)\\
&\PadTo{1 - c_1(1 - p_1)}{\vdots} \\
&1 - c_n(1 - p_n).
\end{aligned}
\right.
\]

(57.4) Now consider the case in which $p_1 = p_2 = \ldots = p_n = 1$,
\ie\ in which any of the causes would be sufficient, and in which
the causes are independent. Then $m_r = 1$; so that
\begin{align*}
e/h &= \Sum_{r=1}^{r=n}c_r
     - \Sum_{r=2}^{r=n}c_r \left[1 - \Prod_{s=1}^{s=r-1}(1 - c_s)\right] \\
    &= 1 - (1 - c_1)(1 - c_2) \ldots (1 - c_n).
\end{align*}

(57.5) Let $c_1$, $c_2 \ldots c_n$ be small quantities so that their
squares and products may be neglected.
\begin{DPgather*}
\lintertext{\indent Then}
e/h = \Sum c_rp_r,
\end{DPgather*}
\ie\ the smaller the probabilities of the causes the more do they
approach the condition of being mutually exclusive.\footnote
  {Boole arrives at this result, \textit{Laws of Thought}, p.~345, but I doubt his proof.}

(57.6) The \textit{à~posteriori} probability of a particular cause~$a_r$
after the event has been observed is
\begin{align*}
a_r/eh &= \frac{e/a_rh · a_r/h}{e/h} \\
       &= \frac{p_rc_r}{e/h}.
\end{align*}

(This is Boole's problem~IX., p.~357).
%% -----File: 203.png---Folio 192-------

(58) The probability of the occurrence of a certain natural
phenomenon under given circumstances is~$p$. There is also a
probability~$a$ of a permanent cause of the phenomenon, \ie\ of a
cause which would always produce the event under the circumstances
supposed. What is the probability that the phenomenon,
being observed $n$~times, will occur the~$n+1$\ordth?

This is Boole's problem~X. (\textit{Laws of Thought}, p.~358). Boole
arrives by his own method at the same result as that given below.
It is necessary first of all to state the assumption somewhat
more precisely. If $x_r$~asserts the occurrence of the event at the
$r^\text{th}$~trial and $t$~the existence of the `permanent cause' we have
\begin{DPgather*}
x_r/h = p,\quad t/h = a,\quad x_r/th = 1, \\
\lintertext{and we require}
x_{n+1}/x_1 \ldots x_nh = y_{n+1}.
\end{DPgather*}
It is also assumed that if there is \emph{no} permanent cause the probability
of~$x_s$ is not affected by the observations~$x_r$, etc.,~\ie\
\begin{DPgather*}
x_s/x_r \ldots x_t\bar{t}h = x_s/\bar{t}h,\footnotemark \\
%
x_s/\bar{t}h
  = \frac{x_s\bar{t}/h}{\bar{t}/h}
  = \frac{x_s/h - x_s t/h}{\bar{t}/h}
  = \frac{p - a}{1 - a}, \\
%
\begin{aligned}
x_r/x_1 \ldots x_{r-1}h
  &= x_r t/x_1 \ldots x_{r-1}h + x_r\bar{t}/x_1 \ldots x_{r-1}h \\
  &= t/x_1 \ldots x_{r-1}h + x_r/\bar{t}x_1 \ldots x_{r-1}h · \bar{t}/x_1 \ldots x_{r-1}h \\
  &= \frac{x_1 \ldots x_{r-1}t/h}{x_1 \ldots x_{r-1}/h}
   + \frac{p-a}{1-a}
   · \frac{x_1 \ldots x_{r-1}/\bar{t}h · \bar{t}/h}{x_1 \ldots x_{r-1}/h} \\
%
  &= \frac{a}{y_1y_2 \ldots y_{r-1}}
   + \frac{p-a}{1-a}
     \frac{\left(\dfrac{p-a}{1-a}\right)^{r-1}(1-a)}{y_1y_2\ldots y_{r-1}},
\end{aligned} \\
\lintertext{\rlap{\ie}}
y_r = \frac{a + (p-a)\left(\dfrac{p-a}{1-a}\right)^{r-1}}{y_1y_2 \ldots y_{r-1}}. \\
%
\lintertext{\rlap{Also}}
y_1 = p \text{ and } y_2 = \frac{a + (p-a)\dfrac{p-a}{1-a}}{y_1},
\end{DPgather*}
\footnotetext{This assumption, which is tacitly introduced by Boole, is not generally
justifiable. I use it here, as my main purpose is to illustrate a method. The
same problem, \emph{without} this assumption, will be discussed in dealing with Pure
Induction.}%
%% -----File: 204.png---Folio 193-------
\begin{DPgather*}
\lintertext{so that}
y_{n+1} = \frac{a + (p-a)\left(\dfrac{p-a}{1-a}\right)^n}
               {a + (p-a)\left(\dfrac{p-a}{1-a}\right)^{n-1}}.
\end{DPgather*}

(58.1)~If $p=a$, $y_n=1$; for if an event can only occur as the
result of a permanent cause, a single occurrence makes future
occurrences certain under similar conditions.

(58.2)
\[
y_{n+1} - y_n = \frac{a(p-a)\left(\dfrac{p-a}{1-a}\right)^{n-2}\left(1 - \dfrac{p-a}{1-a}\right)}
               {\left[a + (p-a)\left(\dfrac{p-a}{1-a}\right)^{n-1}\right]\left[a + (p-a)\left(\dfrac{p-1}{1-a}\right)^{n-2}\right]}
\]
(by easy algebra);

%[** TN: Paragraph break in original]
and $p$ is always $>a$ and~$<1$.

So that $(p-a)\left(\dfrac{p-a}{1-a}\right)^r$ is positive and decreases as $r$~increases,
\[
\therefore y_{n+1} > y_n.
\]

As $n$ increases $y_n=1-\epsilon$, where
\[
\epsilon = (p-a)\left[1 - \left(\dfrac{p-a}{1-a}\right)\right]\frac{\left(\dfrac{p-a}{1-a}\right)^{n-2}}{a + (p-a)\left(\dfrac{p-a}{1-a}\right)^{n-2}},
\]
so that for any positive value of~$\eta$ however small a value of~$n$
can be found such that $\epsilon<\eta$ so long as $a$~is not zero.

(58.3)~$t_n$\DPnote{** [sic] no comma} the \textit{à posteriori} probability of a permanent cause
after $n$~successful observations is
\begin{DPgather*}
t/x_1 \ldots x_nh
  = \frac{x_1 \ldots x_n/th· t/h}{x_1 \ldots x_n/h}
  = \frac{a}{y_1y_2 \ldots y_n},\\
\lintertext{\ie} t_n
  = \frac{a}{a + (p-a)\left(\dfrac{p-a}{1-a}\right)^n},\\
    t_n = 1-\epsilon'\text{, where }
\epsilon'
  = \frac{(p-a)\left(\dfrac{p-a}{1-a}\right)^n}
         {a + (p-a)\left(\dfrac{p-a}{1-a}\right)^n}.
\end{DPgather*}
%% -----File: 205.png---Folio 194-------
\index{Law of error|ifoll}%
\index{Means and laws of error|ifoll}%
So that $t_n$~approaches the limit unity as $n$~increases, so long as $a$
is not zero.

\Paragraph{3.} The following is a common type of statistical problem.\footnote
  {The substance of §§\;3--7 has been printed in the \textit{Journal of the Royal
  Statistical Society}, vol.~lxxiv.\ p.~323 (February 1911).}
We are given a series of measurements, or observations, or
estimates of the true value of a given quantity; and we wish to
determine what function of these measurements will yield us
the \emph{most probable} value of the quantity, on the basis of this evidence.
The problem is not determinate unless we have some
good ground for making an assumption as to how likely we are
in each case to make errors of given magnitudes. But such an
assumption, with or without justification, is frequently made.

The functions of the original measurements which we commonly
employ, in order to yield us approximations to the most
probable value of the quantity measured, are the various kinds
of means or averages---the arithmetic mean, for example, or
the median. The relation, which we assume, between errors of
different magnitudes and the probabilities that we have made
errors of those magnitudes, is called a \emph{law of error}. Corresponding
to each law of error which we might assume, there is some function
of the measurements which represents the most probable value
of the quantity. The object of the following paragraphs is to
discover what laws of error, if we assume them, correspond to
each of the simple types of average, and to discover this by means
of a systematic method.

\Paragraph{4.} Let us assume that the real value of the quantity is either
$b_1, \ldots b_r \ldots b_n$, and let $a_r$~represent the conclusion that the
value is, in fact,~$b_r$. Further let $x_r$~represent the evidence that
a measurement has been made of magnitude~$y_r$.

If a measurement~$y_p$ has been made, what is the probability
that the real value is~$b_s$? The application of the theorem of
inverse probability yields the following result:
\[
%[** TN: Omitting \quad-like space after · in orig.]
a_s/x_ph
  = \frac{x_p/a_sh · a_s/h}
         {\Sum^{r=n}_{r=1}x_p/a_rh · a_r/h}
\]
(the number of possible values of the quantity being~$n$), where
$h$~stands for any other relevant evidence which we may have,
in addition to the fact that a measurement~$x_p$ has been made.

Next, let us suppose that a number of measurements $y_1 \ldots y_m$
%% -----File: 206.png---Folio 195-------
\index{Independence, for knowledge!law of error@{and law of error}}%
have been made; what is now the probability that the real value
is~$b_s$? We require the value of $a_s/x_1x_2 \ldots x_mh$. As before,
\[
%[** TN: Omitting \quad-like space after · in orig.]
a_s/x_1x_2 \ldots x_mh
  = \frac{x_1 \ldots x_m/a_sh · a_s/h}
         {\Sum^{r=x}_{r=1}x_1\ldots x_m/a_rh · a_r/h}.
\]

At this point we must introduce the simplifying assumption
that, if we knew the real value of the quantity, the different
measurements of it would be \emph{independent}, in the sense that a
knowledge of what errors have actually been made in some of
the measurements would not affect in any way our estimate of
what errors are likely to be made in the others. We assume,
in fact, that $x_r/x_p \ldots x_sa_rh = x_r/a_rh$. This assumption is exceedingly
important. It is tantamount to the assumption that
our law of error is unchanged throughout the series of observations
in question. The general evidence~$h$, that is to say, which justifies
our assumption of the particular law of error which we do assume,
is of such a character that a knowledge of the actual errors made
in a number of measurements, not more numerous than those
in question, are absolutely or approximately irrelevant to the
question of what form of law we ought to assume. The law
of error which we assume will be based, presumably, on an
experience of the relative frequency with which errors of different
magnitudes have been made under analogous circumstances in
the past. The above assumption will \emph{not} be justified if the
additional experience, which a knowledge of the errors in the new
measurements would supply, is sufficiently comprehensive, relatively
to our former experience, to be capable of modifying our
assumption as to the shape of the law of error, or if it suggests
that the circumstances, in which the measurements are being
carried out, are not so closely analogous as was originally supposed.

With this assumption, \ie\ that $x_1$,~etc., are independent of
one another relatively to evidence $a_r h$,~etc., it follows from the
ordinary rule for the multiplication of independent probabilities
that
\begin{DPgather*}
x_1\ldots x_m/a_sh = \Prod \limits^{q=m}_{q=1}x_q/a_s h. \\
\lintertext{Hence}
a_s/x_1x_2 \ldots x_mh
  = \frac{a_s/h · \Prod \limits^{q=m}_{q=1}x_q/a_sh}
         {\Sum^{r=n}_{r=1}
          \left[ \Prod \limits^{q=m}_{q=1} x_q/a_rh · a_r/h \right]}.
\end{DPgather*}
%% -----File: 207.png---Folio 196-------
\index{Gauss, and laws of error|inote}%

The \emph{most probable} value of the quantity under measurement,
given the $m$~measurements $y_1$,~etc.---which is our \textit{quaesitum}---is
therefore that value which makes the above expression a maximum.
Since the denominator is the same for all values of~$b_s$,
we must find the value which makes the numerator a maximum.
Let us assume that $a_1/h = a_2/h = \ldots = a_n/h$. We assume, that
is to say, that we have no reason \textit{à~priori} (\ie\ before any measurements
have been made) for thinking any one of the possible
values of the quantity more likely than any other. We require,
therefore, the value of~$b_s$ which makes the expression $\Prod \limits^{q=m}_{q=1}x_q/a_s h$
a maximum. Let us denote this value by~$y$.

We can make no further progress without a further assumption.
Let us assume that $x_q/a_sh$---namely, the probability of a
measurement~$y_q$ assuming the real value to be~$b_s$---is an algebraic
function~$f$ of $y_q$ and~$b_s$, the same function for all values of $y_q$ and~$b_s$
within the limits of the problem.\footnote
  {Gauss, in obtaining the normal law of error, made, in effect, the more
  special assumption that $x_q/a_sh$ is a function of $e_q$~only, where $e_q$ is the error and
  $e_q = b_s - y_q$. We shall find in the sequel that all symmetrical laws of error,
  such that positive and negative errors of the same absolute magnitude are
  equally likely, satisfy this condition---the normal law, for example, and the
  simplest median law. But other laws, such as those which lead to the geometric
  mean, do not satisfy it.}
We assume, that is to say,
$x_q/a_sh = f(y_q, b_s)$, and we have to find the value of~$b_s$, namely~$y$,
which makes $\Prod \limits^{q=m}_{q=1}f(y_q, y)$ a maximum. Equating to zero the
differential coefficient of this expression with respect to~$y$, we
have $\Sum^{q=m}_{q=1}\dfrac{f'(y_q, y)}{f(y_q, y)} = 0$,\footnote
  {Since none of the measurements actually made can be impossible, none of
  the expressions $f(y_q, y)$ can vanish.}
where $f' = \dfrac{df}{dy}$. This equation may be
written for brevity in the form $\Sum \dfrac{f'_q}{f_q} = 0$.

If we solve this equation for~$y$, the result gives us the value of
the quantity under observation, which is most probable relatively
to the measurements we have made.

The act of differentiation assumes that the possible values of~$y$
are so numerous and so uniformly distributed within the range
in question, that we may, without sensible error, regard them as
continuous.

\Paragraph{5.} This completes the \textit{prolegomena} of the inquiry. We are
%% -----File: 208.png---Folio 197-------
\index{Arithmetic mean (or average)!laws of error@{and laws of error}}%
now in a position to discover what laws of error correspond to
given assumptions respecting the algebraic relation between the
measurements and the most probable value of the quantity, and
\textit{vice versa}. For the law of error determines the form of~$f(y_q,y)$.
\index{Law of error!arithmetic@{and arithmetic mean}}%
And the form $f(y_q,y)$ determines the algebraic relation $\Sum \dfrac{f'_q}{f_q} = 0$
between the measurements and the most probable value. It
may be well to repeat that $f(y_q,y)$ denotes the probability to
us that an observer will make a measurement~$y_q$ in observing a
quantity whose true value we know to be~$y$. A law of error tells
us what this probability is for all possible values of $y_q$ and~$y$
within the limits of the problem.

(i.) If the most probable value of the quantity is equal to the
arithmetic mean of the measurements, what law of error does this
imply?
\setlength{\TmpLen}{3.5in}%[** TN: Hard-coded width.]
\begin{DPalign*}[m]
\Sum\frac{f'_q}{f_q}
  &= \parbox[t]{\TmpLen}{$0$
        must be equivalent to $\Sum (y - y_q) = 0$, since the most
        probable value~$y$ must equal $\dfrac{1}{m} \Sum^{q=m}_{q=1} y_q$.} \\
%
\therefore \dfrac{f'_q}{f_q}
  &= \parbox[t]{\TmpLen}{$\phi''(y)(y - y_q)$
        where $\phi''(y)$ is some function which
        is not zero and is independent of~$y_q$.} \\
%
\intertext{Integrating,}
\log f_q
   &= \parbox[t]{\TmpLen}{$\int \phi''(y)(y - y_q)\, dy + \psi(y_q)$
        where $\psi(y_q)$ is some function
        independent of~$y$.} \\
%
  &= \phi'(y)(y - y_q) - \phi(y) + \psi(y_q). \\
\lintertext{\rlap{So that}}
f_q &= e^{\phi'(y)(y - y_q) - \phi(y) + \psi(y_q)}.
\end{DPalign*}

Any law of error of this type, therefore, leads to the arithmetic
mean of the measurements as the most probable value of the
quantity measured.

%[** TN: Reformatting/displaying next alignment]
If we put $\phi(y) = -k^2y^2$ and $\psi(y_q) = -k^2y_q^2 + \log A$, we obtain
\begin{align*}
f_q &= Ae^{-k^2(y - y_q)^2}, \text{ the form normally assumed}\DPtypo{.}{,} \\
    &= Ae^{-k^2z_q^2},
\end{align*}
where $z_q$ is the absolute magnitude of the error in
the measurement~$y_q$.

This is, clearly, only one amongst a number of possible solutions.
But with one additional assumption we can prove that
this is the only law of error which leads to the arithmetic mean.
%% -----File: 209.png---Folio 198-------
\index{Gauss, and laws of error}%
\index{M'Alister, Sir Donald, and laws of error}%
Let us assume that negative and positive errors of the same
absolute amount are equally likely.

In this case $f_q$ must be of the form $Be^{\theta(y - y_q)^2}$,
\[
\therefore \phi'(y)(y - y_q) - \phi(y) + \psi(y_q) = \theta(y - y_q)^2.
\]

Differentiating with respect to~$y$,
\[
\phi''(y) = 2\frac{d}{d(y - y_q)^2}\theta (y - y_q)^2.
\]

But $\phi''(y)$ is, by hypothesis, independent of~$y_q$.

$\therefore \dfrac{d}{d(y - y_q)^2} \theta(y - y_q)^2 = -k^2$ where $k$~is constant; integrating,
$\theta (y - y_q)^2 = -k^2(y - y_q)^2 + \log C$ and we have $f_q = Ae^{-k^2(y - y_q)^2}$ (where
$A = BC$).

(ii.) What is the law of error, if the geometric mean of the
\index{Law of error!geometric@{and geometric mean}}%
measurements leads to the most probable value of the quantity?

In this case $\Sum \dfrac{f'_q}{f_q}= 0$ must be equivalent to $\Prod \limits^{q=m}_{q=1} y_q = y^m$, \ie\ to
\[
\Sum \log\frac{y_q}{y} = 0.
\]
Proceeding as before, we find that the law of error is
\[
f_q = Ae^{\phi'(y) \log \frac{y_q}{y} + \int \frac{\phi'(y)}{y}\, dy + \psi(y_q)}.
\]
There is no solution of this which satisfies the condition that
negative and positive errors of the same absolute magnitude are
equally likely. For we must have
\begin{gather*}
\phi'(y) \log \frac{y_q}{y} + \int \frac{\phi'(y)}{y}\, dy + \psi(y_q) = \phi(y - y_q)^2 \\
\text{or } \phi''(y) \log \frac{y_q}{y} = \frac{d}{dy} \phi(y - y_q)^2,
\end{gather*}
which is impossible.

The simplest law of error, which leads to the geometric mean,
seems to be obtained by putting $\phi'(y) = -ky$, $\psi(y_q) = 0$. This
gives $f_q = A \left(\dfrac{y}{y_q}\right)^{ky} e^{-ky}$.

A law of error, which leads to the geometric mean of the
observations as the most probable value of the quantity, has been
previously discussed by Sir~Donald McAlister (\textit{Proceedings of the
Royal Society}, vol.~xxix.\ (1879) p.~365). His investigation depends
upon the obvious fact that, if the geometric mean of the
%% -----File: 210.png---Folio 199-------
observations yields the most probable value of the quantity, the
arithmetic mean of the logarithms of the observations must yield
the most probable value of the logarithm of the quantity. Hence,
if we suppose that the logarithms of the observations obey the
normal law of error (which leads to their arithmetic mean as the
\index{Law of error!normal law}%
most probable value of the logarithms of the quantity), we can
by substitution find a law of error for the observations themselves
which must lead to the geometric mean of them as the most
probable value of the quantity itself.

If, as before, the observations are denoted by $y_q$,~etc., and the
quantity by~$y$, let their logarithms be denoted by $l_q$,~etc., and by~$l$.
Then, if $l_q$,~etc., obey the normal law of error, $f(l_q, l) = Ae^{-k^2(l_q - l)^2}$.
Hence the law of error for $y_q$,~etc., is determined by
\begin{align*}
f(y_q, y)
  &= Ae^{-k^2(\log y_q - \log y)^2}\\
  &= Ae^{-k^2(\log \frac{y_q}{y})^2},
\end{align*}
and the most probable value of~$y$ must, clearly, be the geometric
mean of $y_q$,~etc.

This is the law of error which was arrived at by Sir Donald
McAlister. It can easily be shown that it is a special case of the
generalised form which I have given above of all laws of error
leading to the geometric mean. For if we put $\psi(y_q) = -k^2(\log y_q)^2$,
and $\phi'(y) = 2k^2 \log y$, we have
\begin{align*}
f_q &= Ae^{2k^2 \log y \log \frac{y_q}{y} + \int 2k^2\, \frac{\log y}{y}\, dy - k^2(\log y_q)^2}\\
    &= Ae^{2k^2 \log y \log y_q - 2k^2 (\log y)^2 + k^2(\log y)^2 - k^2 (\log y_q)^2}\\
    &= Ae^{-k^2\left(\log \frac{y_q}{y}\right)^2}.
\end{align*}

\index{Kapteyn, Prof.\ J. C.!law of error@{and law of error}}%
A similar result has been obtained by Professor J.~C. Kapteyn.\footnote
  {\textit{Skew Frequency Curves}, p.~22, published by the Astronomical Laboratory
\index{Frequency curves}%
  at Groningen (1903).}
But he is investigating frequency curves, not laws of error, and
this result is merely incidental to his main discussion. His
method, however, is not unlike a more generalised form of Sir
Donald McAlister's. In order to discover the frequency curve
of certain quantities~$y$, he supposes that there are certain other
quantities~$z$, functions of the quantities~$y$, which are given by
$z = F(y)$, and that the frequency curve of these quantities~$z$ is
\emph{normal}. By this device he is enabled in the investigation of a
type of skew frequency curve, which is likely to be met with
often, to utilise certain statistical constants corresponding to
%% -----File: 211.png---Folio 200-------
\index{Median and laws of error}%
those which have been already calculated for the normal
curve.

In fact the main advantage both of Sir Donald McAlister's
law of error and of Professor Kapteyn's frequency curves lies in
\index{Law of error!median@{and median}}%
the possibility of adapting without much trouble to unsymmetrical
phenomena numerous expressions which have been already
calculated for the normal law of error and the normal curve of
frequency.\footnote
  {It may be added that Professor Kapteyn's monograph brings forward
  considerations which would be extremely valuable in determining the types of
  phenomena to which geometric laws of error are likely to be applicable.}

This method of proceeding from arithmetic to geometric laws
of error is clearly capable of generalisation. We have dealt with
the geometric law which can be derived from the normal arithmetic
law. Similarly if we start from the simplest geometric
law of error, namely, $f_q = A\left(\dfrac{y}{y_q}\right)^{k^2y} e^{-k^2y}$, we can easily find, by
writing $\log y = l$ and $\log y_q = l_q$, the corresponding arithmetic
law, namely, $f_q = Ae^{k^2el(l - l_q) - k^2el}$, which is obtained from the
generalised arithmetic law by putting $\phi(l) = k^2e^{l}$ and $\psi(l_q) = 0$.
And, in general, corresponding to the arithmetic law
\[
f_q = Ae^{\phi'(y)(y - y_q) - \phi(y) + \psi(y_q)},
\]
we have the geometric law
\[
f_q = Ae^{\phi'_l(z) \log \frac{z_q}{z } + \int \frac{\phi_l(z)}{z}\, dz + \psi_l(z_q)},
\]
where
\[
y = \log z,\
y_q = \log z_q,\
\int \frac{\phi'_1(z)}{z}\, dz = \phi(\log z) \text{ and } \psi_l(z_q) = \psi(\log z_q).
\]

(iii.) What law of error does the harmonic mean imply?

In this case, $\Sum\dfrac{f'_q}{f_q} = 0$ must be equivalent to $\Sum\left(\dfrac{1}{y_q} - \dfrac{1}{y}\right) = 0$.

Proceeding as before, we find that $f_q = Ae^{\phi'(y)\left[\frac{1}{y_q} - \frac{1}{y}\right] - \int \frac{\phi'(y)}{y^2}\, dy + \psi(y_q)}$.
A simple form of this is obtained by putting $\phi'(y) = -k^2y^2$ and
$\psi(y_q) = -k^2y_q$. Then $f_q = Ae^{\frac{k^2}{y_q} (y - y_q)^2} = Ae^{-k^2\frac{z_q^2}{y_q}}$. With this law,
positive and negative errors of the same absolute magnitude are
not equally likely.

(iv.) If the most probable value of the quantity is equal to the
median of the measurements, what is the law of error?

The median is usually defined as the measurement which
%% -----File: 212.png---Folio 201-------
\index{Fechner, and median}%
occupies the middle position when the measurements are ranged
in order of magnitude. If the number of measurements~$m$ is odd,
the most probable value of the quantity is the $\dfrac{m+1}{2}$th, and, if the
number is even, all values between the $\dfrac{m}{2}$th and the $\left(\dfrac{m}{2}+1\right)$th are
equally probable amongst themselves and more probable than
any other. For the present purpose, however, it is necessary to
make use of another property of the median, which was known
to Fechner (who first introduced the median into use) but which
seldom receives as much attention as it deserves. \emph{If~$y$ is the
median of a number of magnitudes, the sum of the absolute differences
\emph{(\ie\ \emph{the difference always reckoned positive})} between $y$ and each of
the magnitudes is a minimum.} The median~$y$ of $y_1y_2\ldots y_m$ is
found, that is to say, by making $\Sum^m_1 |y_q - y|$ a minimum where
$|y_q - y|$ is the difference always reckoned positive between $y_q$
and~$y$.

We can now return to the investigation of the law of error
corresponding to the median.

Write $|y - y_q| = z_q$. Then since $\Sum^m_1 z_q$ is to be a minimum we
must have $\Sum^m_1 \dfrac{y - y_q}{z_q} = 0$. Whence, proceeding as before, we have
\[
f_q = Ae^{\int \frac{y - y_q}{z_q}\, \phi''(y)\, dy + \psi(y_q).}
\]

The simplest case of this is obtained by putting
\begin{DPalign*}
\phi''(y) &= -k^2, \\
\psi(y_q) &= \frac{y-y_q}{z_q}\, k^2y_q, \\
\lintertext{whence}
f_q &= Ae^{-k^2|y - y_q|} = Ae^{-k^2 z_q}.
\end{DPalign*}

This satisfies the additional condition that positive and negative
errors of equal magnitude are equally likely. Thus in this
important respect the median is as satisfactory as the arithmetic
mean, and the law of error which leads to it is as simple. It also
resembles the normal law in that it is a function of the error \emph{only},
and not of the magnitude of the measurement as well.

The median law of error, $f_q = Ae^{-k^2 z_q}$, where $z_q$~is the absolute
amount of the error always reckoned positive, is of some historical
%% -----File: 213.png---Folio 202-------
\index{Least Squares and Venn!method of}%
interest, because it was the earliest law of error to be formulated.
\index{Law of error!normal law}%
The first attempt to bring the doctrine of averages into definite
relation with the theory of probability and with laws of error was
published by Laplace in 1774 in a memoir ``sur la probabilité des
\index{Laplace!doctrine@{and doctrine of averages}}%
causes par les événemens.''\DPnote{** TN: [sic], not événements}\footnote
  {\textit{Mémoires présentés à l'Académie des Sciences}, vol.~vi.}
This memoir was not subsequently
incorporated in his \textit{Théorie analytique}, and does not represent his
more mature view. In the \textit{Théorie} he drops altogether the law
tentatively adopted in the memoir, and lays down the main lines
of investigation for the next hundred years by the introduction
of the \emph{normal} law of error. The popularity of the normal law,
with the arithmetic mean and the method of least squares as its
corollaries, has been very largely due to its overwhelming advantages,
in comparison with all other laws of error, for the purposes
of mathematical development and manipulation. And in
addition to these technical advantages, it is probably applicable
as a first approximation to a larger and more manageable group
of phenomena than any other single law. So powerful a hold
indeed did the normal law obtain on the minds of statisticians,
that until quite recent times only a few pioneers have seriously
considered the possibility of preferring in certain circumstances
other means to the arithmetic and other laws of error to the
normal. Laplace's earlier memoir fell, therefore, out of remembrance.
But it remains interesting, if only for the fact that a
law of error there makes its appearance for the first time.

Laplace sets himself the problem in a somewhat simplified
form: ``Déterminer le milieu que l'on doit prendre entre trois
observations données d'un même phénomène.'' He begins by
assuming a law of error $z = \phi(y$), where $z$~is the probability of an
error~$y$; and finally, by means of a number of somewhat arbitrary
assumptions, arrives at the result $\phi (y) = \dfrac{m}{2} e^{-my}$. If this formula
is to follow from his arguments, $y$~must denote the \emph{absolute} error,
always taken positive. It is not unlikely that Laplace was led
to this result by considerations other than those by which he
attempts to justify it.

Laplace, however, did not notice that his law of error led to
the median. For, instead of finding the most probable value,
which would have led him straight to it, he seeks the ``mean of
error''---the value, that is to say, which the true value is as likely
%% -----File: 214.png---Folio 203-------
\index{Mode, and law of error}%
to fall short of as to exceed. This value is, for the median law,
laborious to find and awkward in the result. Laplace works it
out correctly for the case where the observations are no more
than three.

\Paragraph{6.} I do not think that it is possible to find by this method a
law of error which leads to the mode. But the following general
\index{Law of error!mode@{and mode}}%
formulae are easily obtained:

(v.) If $\Sum \theta(y_q, y)$ is the law of relation between the measurements
and the most probable value of the quantity, then the law
of error $f_q(y_q, y)$ is given by $f_q = Ae^{\int \theta (y_qy)\phi''(y)\, dy + \psi(y_q)}$. Since $f_q$~lies
between $0$~and~$1$, $\int \theta (y_qy)\phi''(y)\, dy + \psi(y_q) + \log A$ must be negative
for all values of $y_q$~and~$y$ that are physically possible; and, since
the values of~$y_q$ are between them exhaustive,
\[
\Sum Ae^{\int \theta (y_qy)\phi''(y)\, dy + \psi(y_q)} = 1,
\]
where the summation is for all terms that can be formed by giving~$y_q$
every value \textit{à~priori} possible.

(vi.) The most general form of the law of error, when it is
assumed that positive and negative errors of the same magnitude
are equally probable, is $Ae^{-k^2 f(y - y_q)^2}$, where the most probable
value of the quantity is given by the equation
\[
\Sum (y - y_q) f'(y - y_q)^2 = 0,\text{ where }
f'(y - y_q)^2 = \frac{d}{d(y - y_q)^2} f(y - y_q)^2.
\]
The arithmetic mean is a special case of this obtained by putting
$f(y - y_q)^2 = (y - y_q)^2$; and the median is a special case obtained
by putting $f(y - y_q)^2 = +\sqrt{(y - y_q)^2}$.

We can obtain other special cases by putting
\[
f(y - y_q)^2 = (y - y_q)^4,
\]
when the law of error is $Ae^{-k^2(y - y_q)^2}$ and the most probable values
are the roots of $my^3 - 3y^2\Sum y_q + 3y\Sum y^2_q - \Sum y^3_q = 0$; and by putting
$f(y - y_q)^2 = \log(y - y_q)^2$, when the law of error is $\dfrac{A}{(y - y_q)} = 0$ and
the most probable values the roots of $\Sum \dfrac{1}{(y - y_q)} = 0$. In all these
cases the law is a function of the error only.

\Paragraph{7.} These results may be summarised thus. We have
assumed:

(a) That we have no reason, before making measurements, for
%% -----File: 215.png---Folio 204-------
\index{Independence, for knowledge!measurement@{and measurement}}%
supposing that the quantity we measure is more likely to have
any one of its possible values than any other.

(b) That the errors are independent, in the sense that a
\emph{knowledge} of how great an error has been made in one case does
not affect our expectation of the probable magnitude of the error
in the next.

(c) That the probability of a measurement of given magnitude,
when in addition to the \textit{à~priori} evidence the real value of the
quantity is supposed known, is an algebraic function of this
given magnitude of the measurement and of the real value of the
quantity.

(d) That we may regard the series of possible values as continuous,
without sensible error.

(e) That the \textit{à~priori} evidence permits us to assume a law of
error of the type specified in~(c); \ie\ that the algebraic function
referred to in~(c) is known to us \textit{à~priori}.

Subject to these assumptions, we have reached the following
conclusions:

(1) The most general form of the law of error is
\[
f_q = Ae^{\int \phi''(y)\theta (y_qy)\, dy + \psi(y_q)},
\]
leading to the equation $\Sum\theta (y_qy) = 0$, connecting the most probable
value and the actual measurements, where $y$~is the most probable
value and $y_q$,~etc., the measurements.

(2) Assuming that positive and negative errors of the same
absolute magnitude are equally likely, the most general form is
$f_q = Ae^{-k^2 f(y - y_q)^2}$, leading to the equation $\Sum (y - y_q) f'(y - y_q)^2 = 0$,
where $f'z = \dfrac{d}{dz}fz$. Of the special cases to which this form gives
rise, the most interesting were

(3) $f_q = Ae^{-k^2(y - y_q)^2} = Ae^{-k^2z_q^2}$, where $z_q = |y - y_q|$, leading to
the arithmetic mean of the measurements as the most probable
value of the quantity; and

(4) $f_q = Ae^{-k^2z_q}$, leading to the median.

(5) The most general form leading to the arithmetic mean is
$f_q = Ae^{\phi'(y - y_q) - \phi(y) + \psi(y_q)}$, with the special cases~(3), and

(6) $f_q = Ae^{k^2e^y (y - y_q) - k^2 e^y}$.

(7) The most general form leading to the geometric mean is
$f_q = Ae^{\phi'(y)\log \frac{y_q}{y} + \int \frac{\phi'(y)}{y}\, dy + \psi (y_q)}$, with the special cases:
%% -----File: 216.png---Folio 205-------
\index{Arithmetic mean (or average)}%
\index{Averages|ifoll}%
\index{Least Squares and Venn!method of}%

(8) $f_q = A\left(\frac{y}{y_q}\right)^{k^2y} e^{-k^2y}$, and

(9) $f_q = Ae^{-k^2\left(\log\frac{y_q}{y}\right)^2}$.

(10) The most general form leading to the harmonic mean is
$f_q = Ae^{\phi'(y)\left[\frac{1}{y_q} - \frac{1}{y}\right] - \int\frac{\phi'(y}{y^2}\DPtypo{}{\,dy} + \psi(y_q)}$, with the special case

(11) $f_q = Ae^{-k^2\frac{(y - y_q)^2}{y_q}} = Ae^{-k^2\frac{z_q^2}{y_q}}$.

(12) The most general form leading to the median is
\[
f_q = Ae^{\phi'(y)\frac{y - y_q}{z_q} + \psi(y_q)},
\]
with the special case~(4).

In each of these expressions, $f_q$~is the probability of a measurement~$y_q$,
given that the true value is~$y$.

\Paragraph{8.} The doctrine of Means and the allied theory of Least
Squares comprise so extensive a subject-matter that they cannot
be adequately treated except in a volume primarily devoted to
them. As, however, they are one of the important practical
applications of the theory of probability, I am unwilling to pass
them by entirely; and the following discursive observations,
chiefly relating to the Normal Law of Error, will serve, taken in
\index{Law of error!normal law}%
conjunction with the paragraphs immediately preceding, to
illustrate the connection between the theories of this treatise
and the general treatment of averages.

\Paragraph{9.} \textit{The Claims of the Arithmetic Average}.---By definition the
arithmetic average of a number of quantities is nothing more
than their arithmetic sum divided by their number. But the
utility of an average generally consists in our supposed right to
substitute, in certain cases, this single measure for the varying
measures of which it is a function. Sometimes this requires no
justification; the word ``average'' is in these cases used for
the sake of shortness, and merely to summarise a set of facts:
as, for instance, when we say that the birth-rate in England is
greater than the birth-rate in France.

But there are other cases in which the average makes a more
substantial claim to add to our knowledge. After a number of
examiners of equal capacity have given varying marks to a
candidate for the same paper, it may be thought fair to allow
the candidate the average of the different marks allotted: and
in general if several estimates of a magnitude have been made,
%% -----File: 217.png---Folio 206-------
\index{Arithmetic mean (or average)!Laplace on}%
\index{Arithmetic mean (or average)!Gauss on}%
\index{De Witt and arithmetic averages}%
\index{Fresnel and simplicity}%
\index{Gauss, and laws of error!arithmetic mean@{and arithmetic mean}}%
\index{Least Squares and Venn}%
\index{Least Squares and Venn!method of}%
between the accuracy of which we have no reason to discriminate,
we often think it reasonable to act as if the true magnitude were
the average of the several measurements. Perhaps De~Witt, in
his report on Annuities to the States General in 1671,\footnote
  {\textit{De vardye van de lif-renten na proportie van de \DPtypo{losrenten}{los-renten}}. The Hague, 1671.}
was the
first to use it scientifically. But as Leibniz points out: ``Our
\index{Leibniz!arithmetic average@{and arithmetic average}}%
peasants have made use of it for a long time according to their
natural mathematics. For example, when some inheritance or
land is to be sold, they form three bodies of appraisers; these
bodies are called \emph{Schurzen} in Low Saxon, and each body makes
an estimate of the property in question. Suppose, then, that
the first estimates its value to be $1000$ crowns, the second, $1400$,
the third, $1500$; the sum of these three estimates is taken, viz.\
$3900$, and because they were three bodies, the third, \ie~$1300$, is
taken as the mean value asked for. This is the axiom: \textit{aequalibus
aequalia}, equal suppositions must have equal consideration.''\footnote
  {\textit{Nouveaux Essais}. Engl.\ transl.\ p.~540.}

But this is a very inadequate axiom. Equal suppositions
would have equal consideration, if the three estimates had been
multiplied together instead of being added. The truth is that
at all times the arithmetic mean has had \emph{simplicity} to recommend
it. It is always easier to add than to multiply. But simplicity
is a dangerous criterion: ``La nature,'' says Fresnel, ``ne s'est
pas embarassée des difficultés d'analyse, elle n'a évité que la
complication des moyens.''

With Laplace and Gauss there began a series of attempts to
\index{Laplace!arithmetic mean@{and arithmetic mean}}%
\emph{prove} the worth of the arithmetic mean. It was discovered that
its use involved the assumption of a particular type of law of
error for the \textit{à~priori} probabilities of given errors. It was also
found that the assumption of this law led on to a more complicated
rule, known as the Method of Least Squares for combining
the results of observations which contain more than one
doubtful quantity. In spite of a popular belief that, whilst the
Arithmetic Mean is intuitively obvious, the Method of Least
Squares depends upon doubtful and arbitrary assumptions, it
can be demonstrated that the two stand and fall together.\footnote
  {Venn (\textit{Logic of Chance}, p.~40) thinks that the Normal Law of Error and
\index{Venn!Least Squares@{and Least Squares}|inote}%
  the Method of Least Squares ``are not only totally distinct things, but they have
  scarcely even any necessary connection with each other. The Law of Error
  is the statement of a physical fact\ldots. The Method of Least Squares, on the
  other hand, is not a law at all in the scientific sense of the term. It is simply
  a rule or direction\ldots.''}
%% -----File: 218.png---Folio 207-------
\index{Ellis, Leslie!Least Squares@{and Least Squares}|inote}%
\index{Hagen, and error}%
\index{Maclaurin, Theorem of}%
\index{Mathematicians, and probability!laws of error@{and laws of error}}%

The analytical theorems of Laplace and Gauss are complicated,
but the special assumptions upon which they are based are easily
stated.\footnote
  {For an account of the three principal methods of arriving at the Method
  of Least Squares and the Arithmetic Mean, see Ellis, \textit{Least Squares}. Gauss's
  first method is in the \textit{Theoria Motus}, and his second in the \textit{Theoria Combinationis
  Observationum}. Laplace's investigations are in chap.~iv.\ of the second
  Book of the \textit{Théorie analytique}. Laplace's method was improved by Poisson
\index{Poisson!least errors@{and least errors}}%
  in the \textit{Connaissance des temps} for 1827 and~1832.}
Gauss supposes (\textit{a})~that the probability of a given error
is a function of the error only and not also of the magnitude of
the observation, (\textit{b})~that the errors are so small that their cubes
and higher powers may be neglected. Assumption~(\textit{a}) is arbitrary,\footnote
  {It does not follow, as G.~Hagen argues (\textit{Grundzüge der Wahrscheinlichkeitsrechnung},
  p.~29), that, because a larger error is less probable than a smaller,
  \emph{therefore} the probability of a given error is a function of its magnitude
  only.}
and Gauss did not state it explicitly. These two assumptions,
together with certain others, lead us to the result. For
let $\phi(z)$~be the law of error where $z$~is the error, and let us assume,
as it always is assumed in these proofs, that $\phi(z)$ can be expanded
by Maclaurin's Theorem. Then $\phi (x) = \phi (0) + z\phi'(0) + \dfrac{z^2}{2!}\phi''(0) + \dfrac{z^3}{3!}\phi'''(0) + \ldots$.
It is also supposed that positive and negative
errors are equally probable, \ie~$\phi(z) = \phi(-z)$, so that $\phi'(0)$ and~$\phi'''(0)$
vanish. Since we may neglect~$z^4$ in comparison with~$z^2$,
$\phi{z} = \phi(0) + \frac{1}{2}z^2\phi''(0)$. But (neglecting~$z^4$ and higher powers)
$a + bz^2 = ae^{\frac{bz^2}{a}}$, so that $\phi(z) = ae^{\frac{bz^2}{a}}$.

Gauss's proof looks much more complicated than this, but he
obtains the form $ae^{\frac{bz^2}{a}}$ by neglecting higher powers of~$z$, so that
this expression is really equivalent to $a + bz^2$. By this approximation
he has reduced all the possible laws to an equivalent
form.\footnote
  {This is pointed out by Bertrand, \textit{Calcul des probabilités}, p.~267.}
It is true, therefore, that the normal law of error is, to
the second power of the error, equivalent to any law of error,
\emph{which is a function of the error only, and for which positive and
negative errors are equally probable}. Laplace also introduces
assumptions equivalent to these.

While mathematicians have endeavoured to establish the
normal law of error and the arithmetic mean as a law of logic,
%% -----File: 219.png---Folio 208-------
\index{Fechner, and median!law of sensation@{and law of sensation}}%
\index{Pearson, Karl!arithmetic mean@{and arithmetic mean}}%
others have claimed for it the testimony of experience and have
deemed it a law of nature.\footnote
  {This is, of course, a very common point of view indeed. Cf.~Bertrand,
\index{Bertrand!Law of Error@{and Law of Error}|inote}%
  \textit{op.~cit.}\ p.~183: ``Malgré les objections précédentes, la formule de Gauss doit
  être adoptée. L'observation la confirme: cela doit suffire dans les applications.''}

That this cannot be so, is evident. For suppose that $x_1x_2 \ldots x_n$
are a set of observations of an unknown quantity~$x$. Then, by
this principle, $x = \dfrac{1}{n}\Sum x_r$ gives the most probable value of~$x$. But
suppose we had wished to determine~$x^2$, our observations, assuming
that we can multiply correctly, would be $x_1^2$,~$x_2^2 \ldots x_n^2$,
and the most probable value of $x^2 = \dfrac{1}{n}\Sum x_r^2$. But $(\dfrac{1}{n}\Sum x_r)^2 = \dfrac{1}{n}\Sum x_r^2$.
And in general, $\dfrac{1}{n}\Sum f(x_r) \neq f(\dfrac{1}{n}\Sum x_r)$. Nor is this a consideration
which can safely be ignored in practice. For our ``observations''
are often the result of some manipulation, and the particular
shape in which we get them is not necessarily fixed for us. It is
not easy to say what the \emph{direct} observation is. In particular if
any such law of sensation, as that enunciated by Fechner, is true
(\ie~that sensation varies as the logarithm of the stimulus), the
arithmetic mean must break down as a \emph{practical} rule in all cases
where human sensation is part of the instrument by means of
which the observations are recorded.\footnote
  {This was noticed by Galton.}
\index{Galton!Fechner's law@{and Fechner's law}}%

Apart, however, from theoretical refutations, statisticians now
recognise that the arithmetic mean and the normal law of error
can only be applied to certain special classes of phenomena.
\index{Quetelet!arithmetic mean@{and arithmetic mean}}%
Quetelet\footnote
  {\DPtypo{E.g.}{\Eg}~\textit{Letters on the Theory of Probabilities}, p.~114.}
was, I think, the first to point this out. In England,
Galton drew attention to the fact many years ago, and Professor
Pearson\footnote
  {On ``Errors of Judgment, etc.,'' \textit{Phil.\ Trans.}~A, vol.~cxcviii.\ pp.~235--299.
  The following quotation is from his memoir \textit{On the General Theory of Skew
  Correlation and \DPtypo{Nonlinear}{Non-linear} Regression}, where further references are given.}
has shown ``that the Gaussian-Laplace normal distribution
is very far from being a general law of frequency
distribution either for errors of observation or for the distribution
of deviations from type such as occur in organic populations\ldots.
It is not even approximately correct, for example, in the distribution
of barometric variations, of grades of fertility and incidence
of disease.''
%% -----File: 220.png---Folio 209-------
\index{Ellis, Leslie!Least Squares@{and Least Squares}}%
\index{Least Squares and Venn!method of}%
\index{Merriman, Mansfield, and Least Squares}%

The Arithmetic Mean occupies, therefore, no unique position;
and it is worth while, from the point of view of probability, to
discuss the properties of other possible means and laws of error,
as, for example, on the lines indicated in the earlier part of this
chapter.

\Paragraph{10.} \textit{The Method of Least Squares.}---The problem, to which this
method is applied, is no more than the application of the same
considerations, as those which we have just been discussing, to
cases where the relation between the observed measurements and
the quantity whose most probable value we require, involves
more than one unknown.

Owing to the surprising character of its conclusions, if they
could be accepted as universally valid, and to the obscurity of
the mathematical fabric that has been reared on and about it,
this method has been surrounded by an unnecessary air of
mystery. It is true that in recent times scepticism has grown
at the expense of mystery. It is also true that just views have
been held by individuals for sixty years past, notably by Leslie
Ellis. But the old mistakes are not always corrected in the
current text-books, and even so useful and generally used a
treatise on Least Squares, as Professor Mansfield Merriman's,
opens with a series of very fallacious statements.

The controversial side of the Method of Least Squares is
purely logical; in the later developments there is much elaborate
mathematics of whose correctness no one is in doubt. What it
is important to state with the utmost possible clearness is the
precise assumptions on which the mathematics is based; when
these assumptions have been set forth, it remains to determine
their applicability in particular cases.

In dealing with averages we supposed ourselves to be presented
with a number of direct observations of some quantity
which it is desired to determine. But it is obvious that direct
observations will be in many cases either impracticable or inconvenient;
and our natural course will be to measure certain
other quantities which we know to bear fixed and invariable
relations to the unknowns we wish to determine. In surveying,
for instance, or in astronomy, we constantly prefer to take
measurements of angles or distances in which we are not interested
for their own sakes, but which bear known geometrical relationships
to the set of ultimate unknowns.
%% -----File: 221.png---Folio 210-------
\index{Astronomers and Least Squares}%
\index{Boscovitch and Least Squares}%
\index{Euler and Least Squares}%
\index{Gauss, and laws of error!Least Squares@{and Least Squares}}%
\index{Lambert and Least Squares}%
\index{Legendre and Least Squares}%
\index{Mayer and Least Squares}%
\index{Simpson and Least Squares}%

If we wish to determine the most probable values of a set of
unknowns $x_1, x_2, \ldots x_r$, instead of obtaining a number of
sets of direct observations of each, we may obtain a number of
equations of observation of the following type:
\[
\begin{array}{*{4}{r@{}}l}
a_1x_1 &{}+ a_2x_2 &{}+ \ldots &{}+ a_rx_r &{}= V_1,\\
b_1x_1 &{}+ b_2x_2 &{}+ \ldots &{}+ b_rx_r &{}= V_2,\\
\hdotsfor[10]{5}\\
k_1x_1 &{}+ k_2x_2 &{}+ \ldots &{}+ k_rx_r &{}= V_n,
\end{array}
\]
where $V_1$,~etc., are the quantities \emph{directly} observed, and the $a'$s,
$b'$s,~etc., are supposed known~($n>r$).

We have in such a case $n$~equations to determine $r$~unknowns,
and since the observations are likely to be inexact, there may be
no precise solution whatever. In these circumstances we wish to
know the most probable set of values of the~$x$'s warranted by
these observations.

The problem is precisely similar in kind to that dealt with
by averages and differs only in the degree of its complexity. It
is the problem of finding the most probable solution of such a set
of discrepant equations of observation that the Method of Least
Squares claims to solve.

By 1750 the astronomers were obtaining such equations of
observation in the course of their investigations, and the question
arose as to the proper manner of their solution. Boscovich in
Italy, Mayer and Lambert in Germany, Laplace in France, Euler
\index{Laplace!Least Squares@{and Least Squares}}%
in Russia, and Simpson in England proposed different methods
of solution. Simpson, in 1757, was the first to introduce, by way
of simplification, the assumption or axiom that positive and
negative errors are equally probable.\footnote
  {See Merriman's \textit{Method of Least Squares}, p.~181, for an historical sketch,
  from which the above is taken. In 1877 Merriman published in the \textit{Transactions
  of the Connecticut Academy} a list of writings relating to the Method of
  Least Squares and the theory of accidental errors of observation, which comprised
  408~titles---classified as 313~memoirs, 72~books, 23~parts of books.}
The Method of Least
Squares was first definitely stated by Legendre in 1805, who
proposed it as an advantageous method of adjusting observations.
This was soon followed by the `proofs' of Laplace and Gauss.
But it is easily shown that these proofs involve the normal law
of error $y = ke^{-k^2x^2}$, and the theory of Least Squares simply
develops the mathematical results of applying to equations of
observation, which involve more than one unknown, that law
%% -----File: 222.png---Folio 211-------
\index{Index numbers}%
of error which leads to the Arithmetic Mean in the case of a single
unknown.

\Paragraph{11.} \textit{The Weighting of Averages.}---It is necessary to recur to
\index{Averages!weighting of}%
\index{Weighting of averages}%
the distinction made at the beginning of §\;9 between the two
types to which our average, or, as it is generally termed in social
inquiries, our index number, may belong. The average or index
number may simply summarise a set of facts and give us the
actual value of a composite quantity, as, for example, the index
number of the cost of living. In such cases the composite
quantity, in which we are interested, need not contain precisely
the same number of units of each of the elementary quantities of
which it is composed, so that the `weights,' which denote the
numbers of each elementary quantity appropriate to the composite
quantity, are part of the definition of the composite
quantity, and can no more be dispensed with than the magnitudes
of the elementary quantities themselves. Nor in such cases is
the rejection of discordant observations permissible; if, that is
to say, some of the elementary quantities are subject to much
wider variation, or to variations of a different type than the
majority, that is no reason for rejecting them.

On the other hand, the individual items, out of which the
average is composed, may each be \emph{indications} or approximate
estimates of some \emph{one single} quantity; and the average, instead
of representing the measure of a composite quantity, may be
selected as furnishing the most probable value of the single
quantity, given, as evidence of its magnitude, the values of the
various terms which make up the average.

If this is the character of our average, the problem of weighting
depends upon what we know about the individual observations
or samples or indications, out of which our average is to be built
up. The units in question may be \emph{known} to differ in respects
relevant to the probable value of the \textit{quaesitum}. Thus there
may be reasons, quite apart from the actual results of the individual
observations or samples, for trusting some of them more
than others. Our knowledge may indicate to us, in fact, that
the constants of the laws of error appropriate to the several
instances, even if the type of the law can be assumed to be
constant, should be varied according to the data we possess about
each. It may also indicate to us that the condition of \emph{independence}
between the instances, which the method of averages
%% -----File: 223.png---Folio 212-------
\index{Independence, for knowledge!averages@{and averages}}%
\index{Jevons!index numbers@{and index numbers}}%
presumes, is imperfectly satisfied, and consequently that our
mode of combining the instances in an average must be modified
accordingly.

Some modern statisticians, who, really influenced perhaps by
practical considerations, have been inclined to deprecate the
importance of weighting on theoretical grounds, have not always
been quite clear what kind of average they supposed themselves
to be dealing with. In particular, discussions of the question of
weighting in connection with index numbers of the value of
money have suffered from this confusion. It has not been clear
whether such index numbers really represent measures of a
composite quantity or whether they are probable estimates of
the value of a single quantity formed by combining a number of
independent approximations towards the value of this quantity.
The original Jevonian conception of an index number of the
value of money was decidedly of the latter type. Modern work
on the subject has been increasingly dominated by the other
conception. A discussion of where the truth lies would lead me
too far into the field of a subject-matter alien to that of this
treatise.

Theoretical arguments against weighting have sometimes
been based on the fact that to weight the items of the average
in an irrelevant manner, or, as it is generally expressed, in a
random manner, is not likely, provided the variations between
the weights are small compared with the variations between the
items, to affect the result very much. But why should any one
wish to weight an average ``at random''? Such observations
overlook the real meaning and significance of weights. They are
probably inspired by the fact that a superficial treatment of
statistics would sometimes lead to the introduction of weights
which are irrelevant. In drawing a conclusion, for example,
from the vital statistics of various towns, the figures of population
for the different towns may or may not be relevant to our conclusion.
It depends on the character of the argument. If they
are relevant, it may be right to employ them as weights. If they
are irrelevant, it must be wrong and unnecessary to do so. The
fact that what is a more important article of consumption than
pins \emph{may}, on certain assumptions, be irrelevant to the usefulness
of variations in the price of each article as indications of variation
in the value of money. With other assumptions, it may be
%% -----File: 224.png---Folio 213-------
\index{Discordant observations, rejection of}%
extremely relevant. Or again, we may know that observations
with a particular instrument tend to be too large and must,
therefore, be weighted down. It is contrary both to theory and
to common sense to suppose that the possession of information
as to the relative reliability of different statistics is not useful.
There is no place, therefore, in my judgment, for a \emph{generalised}
argument as to the propriety or impropriety of weighting an
average.

It should be added that, where we seek to build up an index
number of a conception, which is quantitative but is not itself
numerically measurable in any defined or unambiguous sense, by
combining a number of numerical quantities, which, while they
do not measure our \textit{quaesitum} are nevertheless indications of its
quantitative variations and tend to fluctuate in the same sense,
as, for example, by means of what are sometimes called \emph{economic
barometers} of the state of business, or the prosperity of the country
or the like, some very confusing questions can arise both as to
what sort of a thing our resulting index really is, and as to the
mode of compilation appropriate to it.

These confusing questions always arise when, instead of
measuring a quantity directly, we seek an index to fluctuations
in its magnitude by combining in an average the fluctuations of
a series of magnitudes, which are, each of them in a different way,
to some extent (but only to some extent), correlated with fluctuations
in our \textit{quaesitum}. I must not burden this book with a
discussion of the problems of Index Numbers. But I venture to
think that they would be sooner cleared up if the natures and
purposes of differing index numbers were more sharply distinguished---those,
namely, which are simply descriptive of a composite
commodity, those which seek to combine results differing from
one another in a way analogous to the variations of an instrument
of precision, and those which combine results, not of the \textit{quaesitum}
itself, but of various other quantities, variations in which are
partly due to variations in the \textit{quaesitum}, but which we well
know to be also due to other distinguishable influences. Index
numbers of the third type are often treated by methods and
arguments only appropriate to those of the second type.

\Paragraph{12.} \textit{The Rejection of Discordant Observations}.---This differs
from the problem just discussed, because we have supposed so
far that our system of weighting is determined by data which we
%% -----File: 225.png---Folio 214-------
\index{Hagen, and error!discordant observations@{and discordant observations}|inote}%
\index{Independence, for knowledge!discordant observations@{and discordant observations}}%
possess prior to and apart from our knowledge of the actual
magnitude of the items of our average. The principle of the
rejection of discordant observations comes in when it is argued
that, if one or more of our observations show great discrepancies
from the results of the greater number, these ought to be partly
or entirely neglected in striking the average, even if there is no
reason, except their discrepancy from the rest, for attributing
less weight to them than to the others. By some this practice
has been thought to be in accordance with the dictates of common
sense; by others it is denounced as savouring even of forgery.\footnote
  {\Eg\ G.~Hagen's \textit{Grundzüge der Wahrscheinlichkeitsrechnung}, p.~63: ``Die
  Täuschung, die man durch Verschweigen von Messungen begeht, lässt sich
  eben so wenig entschuldigen, als wenn man Messungen fälschen oder fingiren
  wollte.''}

This controversy, like so many others in Probability, is due
to a failure to understand the meaning of `independence.' The
mathematics of the orthodox theory of Averages and Least
\index{Averages!discordant observations@{and discordant observations}}%
Squares depend, as we have seen, upon the assumption that the
observations are `independent'; but this has sometimes been
interpreted to mean a \emph{physical} independence. In point of fact,
the theory requires that the observations shall be independent,
in the sense that a \emph{knowledge} of the result of some does not affect
the probability that the others, when known, involve given
errors.

Clearly there may be initial data in relation to which this
supposition is entirely or approximately accurate. But in many
cases the assumption will be inadmissible. A knowledge of the
results of a number of observations may lead us to modify our
opinion as to the relative reliabilities of others.

The question, whether or not discordant observations should
be specially weighted down, turns, therefore, upon the nature of
the preliminary data by which we have been guided in initially
adopting a particular law of error as appropriate to the observations.
If the observations are, relevant to these data, strictly
`independent,' in the sense required for probability, then rejection
is not permissible. But if this condition is not fulfilled, a bias
against discordant observations may be well justified.
%% -----File: 226.png---Folio 215-------


\Part{III}{Induction and Analogy}
%% -----File: 227.png---Folio 216-------
%[Blank Page]
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\index{Logic, academic!Induction@{and Induction}}%


\Chapter{XVIII}{Introduction}

\begin{Quote}
Nothing so like as eggs; yet no one, on account of this apparent similarity,
expects the same taste and relish in all of them. 'Tis only after a long course
of uniform experiments in any kind, that we attain a firm reliance and security
with regard to a particular event. Now where is that process of reasoning,
which from one instance draws a conclusion, so different from that which it
infers from a hundred instances, that are no way different from that single
instance? This question I propose as much for the sake of information, as
with any intention of raising difficulties. I cannot find, I cannot imagine any
such reasoning. But I keep my mind still open to instruction, if any one will
vouchsafe to bestow it on me.---\textsc{Hume}.\footnote
  {\textit{Philosophical Essays concerning Human Understanding.}}
\end{Quote}

\Paragraph{1.} \First{I have} described Probability as comprising that part of
logic which deals with arguments which are rational but not
conclusive. By far the most important types of such arguments
are those which are based on the methods of Induction and
\index{Induction!Logic@{and Logic}}%
Analogy. Almost all empirical science rests on these. And the
decisions dictated by experience in the ordinary conduct of life
generally depend on them. To the analysis and logical justification
of these methods the following chapters are directed.

Inductive processes have formed, of course, at all times a
vital, habitual part of the mind's machinery. Whenever we learn
by experience, we are using them. But in the logic of the schools
they have taken their proper place slowly. No clear or satisfactory
account of them is to be found anywhere. Within and
yet beyond the scope of formal logic, on the line, apparently,
between mental and natural philosophy, Induction has been
admitted into the organon of scientific proof, without much help
from the logicians, no one quite knows when.

\Paragraph{2.} What are its distinguishing characteristics? What are
the qualities which in ordinary discourse seem to afford strength
to an inductive argument?
%% -----File: 229.png---Folio 218-------
\index{Analogy, principle of!induction@{and induction}}%

I shall try to answer these questions before I proceed to
the more fundamental problem---What ground have we for regarding
such arguments as rational?

Let the reader remember, therefore, that in the first of the
succeeding chapters my main purpose is no more than to state
in precise language what elements are commonly regarded as
adding weight to an empirical or inductive argument. This
requires some patience and a good deal of definition and special
terminology. But I do not think that the work is controversial.
At any rate, I am satisfied myself that the analysis of \Chapref{XIX}.
is fairly adequate.

In the next section, Chapters \Chapref[]{XX}.~and~\Chapref[]{XXI}., I continue in
part the same task, but also try to elucidate what sort of assumptions,
\emph{if} we could adopt them, lie behind and are required by the
methods just analysed. In \Chapref{XXII}. the nature of these
assumptions is discussed further, and their possible justification
is debated.

\Paragraph{3.} The passage quoted from Hume at the head of this chapter
\index{Hume!Induction@{and Induction}}%
is a good introduction to our subject. Nothing so \emph{like} as eggs,
and after a \emph{long} course of uniform experiments we can expect
with a firm reliance and security the same taste and relish in all
of them. The eggs must be like eggs, and we must have tasted
many of them. This argument is based partly upon \emph{Analogy}
and partly upon what may be termed \emph{Pure Induction}. We argue
\index{Induction!pure}%
from Analogy in so far as we depend upon the \emph{likeness} of the eggs,
and from Pure Induction when we trust the \emph{number} of the experiments.

It will be useful to call arguments \emph{inductive} which depend
in any way on the methods of Analogy and Pure Induction. But
I do not mean to suggest by the use of the term \emph{inductive} that these
methods are necessarily confined to the objects of phenomenal
experience and to what are sometimes called empirical questions;
or to preclude from the outset the possibility of their use in
abstract and metaphysical inquiries. While the term \emph{inductive}
will be employed in this general sense, the expression \emph{Pure
Induction} must be kept for that part of the argument which
arises out of the repetition of instances.

\Paragraph{4.} Hume's account, however, is incomplete. His argument
could have been improved. His experiments should not have
been too uniform, and ought to have differed from one another
%% -----File: 230.png---Folio 219-------
\index{Analogy, principle of!negative}%
as much as possible in all respects save that of the likeness of the
eggs. He should have tried eggs in the town and in the country,
in January and in June. He might then have discovered that
eggs could be good or bad, however like they looked.

This principle of varying those of the characteristics of the
instances, which we regard in the conditions of our generalisation
as non-essential, may be termed \emph{Negative Analogy}.

It will be argued later on that an increase in the \emph{number} of
experiments is \emph{only} valuable in so far as, by increasing, or possibly
increasing, the variety found amongst the non-essential characteristics
\index{Variety!induction@{and induction}}%
of the instances, it strengthens the Negative Analogy.
If Hume's experiments had been \emph{absolutely} uniform, he would
have been right to raise doubts about the conclusion. There is
no process of reasoning, which from one instance draws a conclusion
different from that which it infers from a hundred instances,
if the latter are known to be in \emph{no} way different from
the former. Hume has unconsciously misrepresented the typical
inductive argument.

When our control of the experiments is fairly complete, and
the conditions in which they take place are well known, there is
not much room for assistance from Pure Induction. If the
Negative Analogies are known, there is no need to count the
instances. But where our control is incomplete, and we do not
know accurately in what ways the instances differ from one
another, then an increase in the mere number of the instances
helps the argument. For unless we know for certain that the
instances are perfectly uniform, each new instance \emph{may} possibly
add to the Negative Analogy.

Hume might also have weakened his argument. He expects
no more than the same taste and relish from his eggs. He
attempts no conclusion as to whether his stomach will always
draw from them the same nourishment. He has conserved the
force of his generalisation by keeping it narrow.

\Paragraph{5.} In an inductive argument, therefore, we start with a
number of instances similar in some respects~$AB$, dissimilar in
others~$C$. We pick out one or more respects~$A$ in which the
instances are similar, and argue that some of the other respects~$B$
in which they are also similar are likely to be associated with
the characteristics~$A$ in other unexamined cases. The more
comprehensive the essential characteristics~$A$, the greater the
%% -----File: 231.png---Folio 220-------
\index{Analogy, principle of!positive}%
\index{Mill, and inductive correlations}%
variety amongst the non-essential characteristics~$C$, and the less
comprehensive the characteristics~$B$ which we seek to associate
with~$A$, the stronger is the likelihood or probability of the generalisation
we seek to establish.

These are the three ultimate logical elements on which the
probability of an empirical argument depends,---the Positive
and the Negative Analogies and the scope of the generalisation.

\Paragraph{6.} Amongst the generalisations arising out of empirical
argument we can distinguish two separate types. The first of
these may be termed \emph{universal induction}. Although such inductions
\index{Induction!universal}%
are themselves susceptible of any degree of probability,
they affirm \emph{invariable} relations. The generalisations which they
assert, that is to say, claim universality, and are upset if a
single exception to them can be discovered. Only in the more
exact sciences, however, do we aim at establishing universal
inductions. In the majority of cases we are content with that
other kind of induction which leads up to laws upon which
we can generally depend, but which does not claim, however
adequately established, to assert a law of more than probable
connection.\footnote
  {What Mill calls `approximate generalisations.'}
This second type may be termed \emph{Inductive Correlation}.
\index{Inductive correlation}%
If, for instance, we base upon the data, that this and that
and those swans are white, the conclusion that \emph{all} swans are white,
we are endeavouring to establish a universal induction. But if
we base upon the data that this and those swans are white and
that swan is black, the conclusion that \emph{most} swans are white,
or that the probability of a swan's being white is such and such,
then we are establishing an inductive correlation.

Of these two types, the former---universal induction---presents
both the simpler and the more fundamental problem. In
this part of my treatise I shall confine myself to it almost entirely.
In \Partref{V}., on the Foundations of Statistical Inference, I shall
discuss, so far as I can, the logical basis of inductive correlation.

\Paragraph{7.} The fundamental connection between Inductive Method
and Probability deserves all the emphasis I can give it. Many
writers, it is true, have recognised that the conclusions which we
reach by inductive argument are probable and inconclusive.
Jevons, for instance, endeavoured to justify inductive processes
by means of the principles of inverse probability. And it is true
also that much of the work of Laplace and his followers was
\index{Laplace!Induction@{and Induction}}%
%% -----File: 232.png---Folio 221-------
\index{Evidence, and measurement of Probability!Induction@{and Induction}}%
directed to the solution of essentially inductive problems. But
it has been seldom apprehended clearly, either by these writers
or by others, that the validity of every induction, strictly interpreted,
\index{Induction!validity of}%
depends, not on a matter of fact, but on the existence of
a relation of probability. An inductive argument affirms, not
that a certain matter of fact \emph{is} so, but that \emph{relative to certain
evidence} there is a probability in its favour. The validity of the
induction, relative to the original evidence, is not upset, therefore,
if, as a fact, the truth turns out to be otherwise.

The clear apprehension of this truth profoundly modifies
our attitude towards the solution of the inductive problem. The
validity of the inductive method does \emph{not} depend on the success
of its predictions. Its repeated failure in the past may, of course,
supply us with new evidence, the inclusion of which will modify
the force of subsequent inductions. But the force of the old
induction \emph{relative to the old evidence} is untouched. The evidence
with which our experience has supplied us in the past may have
proved misleading, but this is entirely irrelevant to the
question of what conclusion we ought reasonably to have
drawn from the evidence then before us. The validity and
reasonable nature of inductive generalisation is, therefore, a
question of logic and not of experience, of formal and not of
material laws. The actual constitution of the phenomenal
universe determines the character of our evidence; but it cannot
determine what conclusions \emph{given} evidence \emph{rationally} supports.
%% -----File: 233.png---Folio 222-------
\index{Analogy, principle of!induction@{and induction}}%
\index{definition of}%
\index{Jevons!Induction@{and Induction}}%
\index{Propositional function!induction@{and induction}}%


\Chapter{XIX}{The Nature of Argument by Analogy}

\begin{Quote}
All kinds of reasoning from causes or effects are founded on two particulars,
viz.\ the constant conjunction of any two objects in all past experience, and the
resemblance of a present object to any of them. Without some degree of
\index{Hume!analogy@{and analogy}}%
resemblance, as well as union, 'tis impossible there can be any reasoning.---\textsc{Hume}.\footnote
  {\textit{A Treatise of Human Nature.}}
\end{Quote}

\Paragraph{1.} \First{Hume} rightly maintains that some degree of resemblance
must always exist between the various instances upon which a
generalisation is based. For they must have this, at least, in
common, that they are instances of the proposition which
generalises them. Some element of analogy must, therefore,
lie at the base of every inductive argument. In this chapter I
shall try to explain with precision the meaning of Analogy, and
to analyse the reasons, for which, rightly or wrongly, we usually
regard analogies as strong or weak, without considering at present
whether it is possible to find a \emph{good} reason for our instinctive
principle that likeness breeds the expectation of likeness.

\Paragraph{2.} There are a few technical terms to be defined. We mean
by a \emph{generalisation} a statement that all of a certain definable class
of propositions are true. It is convenient to specify this class
in the following way. If $f(x)$~is true for all those values of~$x$ for
which $\phi(x)$~is true, then we have a generalisation about $\phi$~and~$f$
which we may write $g(\phi, f)$. If, for example, we are dealing with
the generalisation, ``all swans are white,'' this is equivalent to
the statement ``\,`$x$~is white' is true for all those values of~$x$ for
which `$x$~is a swan' is true.'' The proposition $\phi(a) · f(a)$ is an
\emph{instance} of the generalisation~$g(\phi, f)$.

By thus defining a generalisation in terms of propositional
functions, it becomes possible to deal with all kinds of generalisations
%% -----File: 234.png---Folio 223-------
\index{Analogy, principle of!negative}%
\index{Analogy, principle of!positive}%
\index{Analogy, principle of!generalisation@{and generalisation}}%
in a uniform way; and also to bring generalisation into
convenient connection with our definition of Analogy.

If some one thing is true about both of two objects, if, that is
to say, they both satisfy the same propositional function, then to
this extent there is an \emph{analogy} between them. Every generalisation
$g(\phi, f)$, therefore, asserts that one analogy is always accompanied
by another, namely, that between all objects having the
analogy~$\phi$ there is also the analogy~$f$. The set of propositional
functions, which are satisfied by both of the two objects, constitute
the \emph{positive analogy}. The analogies, which would be
disclosed by complete knowledge, may be termed the \emph{total positive
analogy}; those which are relative to partial knowledge, the
\emph{known positive analogy}.

As the positive analogy measures the resemblances, so the
negative analogy measures the differences between the two objects.
The set of functions, such that each is satisfied by one and not
by the other of the objects, constitutes the \emph{negative analogy}.
We have, as before, the distinction between the \emph{total negative
analogy} and the \emph{known negative analogy}.

This set of definitions is soon extended to the cases in which
the number of instances exceeds two. The functions which are
true of \emph{all} of the instances constitute the positive analogy of the
set of instances, and those which are true of \emph{some only}, and are
false of others, constitute the negative analogy. It is clear that
a function, which represents positive analogy for a group of
instances taken out of the set, may be a negative analogy for the
set as a whole. Analogies of this kind, which are positive for
a sub-class of the instances, but negative for the whole class, we
may term \emph{sub-analogies}. By this it is meant that there are
\index{Sub-analogies}%
resemblances which are common to some of the instances, but
not to all.

A simple notation, in accordance with these definitions, will
be useful. If there is a positive analogy~$\phi$ between a set of instances
$a_1$,~$\ldots$~$a_n$, whether or not this is the total analogy
between them, let us write this---
\[
\underset{a_1 \ldots a_n}{A}(\phi).\footnotemark
\]
\footnotetext{Hence $\underset{a_1 \ldots a_n}{A}(\phi) \equiv \phi(a_1) · \phi(a_2) \ldots \phi(a_n) \equiv \Prod \limits^{x=a_n}_{x=a_1} \phi(x)$.}%
%% -----File: 235.png---Folio 224-------

And if there is a negative analogy~$\phi'$, let us write this---
\[
\underset{a_1 \ldots a_n}{\bar{A}}(\phi').\footnotemark
\]
\footnotetext{Hence $\underset{a_1 \ldots a_n}{\bar{A}}(\phi') \equiv \Sum^{x=a_s}_{x=a_r}\phi'(x) · \Sum^{x=a_s'}_{x=a_r'} \overline{\phi'(x)}$.}%

Thus $\underset{a_1 \ldots a_n}{A}(\phi)$ expresses the fact that there is a set of
characteristics~$\phi$ which are common to all the instances, and
$\underset{a_1 \ldots a_n}{\bar{A}}(\phi')$ that there is a set of characteristics $\phi'$ which is
true of at least one of the instances and false of at least one.

\Paragraph{3.} In the typical argument from analogy we wish to generalise
from one part to another of the total analogy which experience
has shown to exist between certain selected instances. In all the
cases where one characteristic~$\phi$ has been found to exist, another
characteristic~$f$ has been found to be associated with it. We argue
from this that any instance, which is known to share the first
analogy~$\phi$, is likely to share also the second analogy~$f$. We have
found in certain cases, that is to say, that both $\phi$~and~$f$ are true
of them; and we wish to assert~$f$ as true of other cases in which
we have only observed~$\phi$. We seek to establish the generalisation
$g(\phi, f)$, on the ground that $\phi$~and~$f$ constitute between them an
observed positive analogy in a given set of experiences.

But while the argument is of this character, the grounds, upon
which we attribute more or less weight to it, are often rather
complex; and we must discuss them, therefore, in a systematic
manner.

\Paragraph{4.} According to the view suggested in the last chapter, the
value of such an argument depends partly upon the nature of the
conclusion which we seek to draw, partly upon the evidence
which supports it. If Hume had expected the same degree of
\index{Hume!analogy@{and analogy}}%
nourishment as well as the same taste and relish from all of the
eggs, he would have drawn a conclusion of weaker probability.
Let us consider, then, this dependence of the probability upon the
\emph{scope} of the generalisation $g(\phi,f)$,---upon the comprehensiveness,
that is to say, of the condition~$\phi$ and the conclusion~$f$ respectively.

The more comprehensive the condition~$\phi$ and the less comprehensive
the conclusion~$f$, the greater \textit{à~priori} probability do
we attribute to the generalisation~$g$. With every increase in~$\phi$
this probability increases, and with every increase in~$f$ it will
diminish.
%% -----File: 236.png---Folio 225-------

The condition $\phi (\equiv \phi_1\phi_2)$ is more comprehensive than the
condition~$\phi_1$, relative to the general evidence~$h$, if $\phi_2$ is a condition
independent of~$\phi_1$ relative to~$h$, $\phi_2$~being independent of~$\phi_1$, if
$g(\phi_1, \phi_2)/h\neq  1$, \ie~if, relative to~$h$, the satisfaction of~$\phi_2$ is not
inferrible from that of~$\phi_1$.

Similarly the conclusion $f(\equiv f_1 f_2)$ is more comprehensive than
the conclusion~$f_1$, relative to the general evidence~$h$, if $f_2$~is a conclusion
independent of~$f_1$, relative to~$h$, \ie~if $g(f_1, f_2)/h \neq 1$.

If $\phi \equiv \phi_1\phi_2$ and $f \equiv f_1 f_2$, where $\phi_1$~and~$\phi_2$ are independent and
$f_1$~and~$f_2$ are independent relative to~$h$, we have---
\begin{DPalign*}
g(\phi_1, f)/h
  &= g(\phi_1\phi_2, f) · g(\phi_1\bar{\phi}_2, f)/h \\
  &\eqslantless g(\phi, f)/h, \\
\lintertext{and}
g(\phi, f)/h
  &= g(\phi, f_1f_2)/h \\
  &= g(\phi f_1, f_2)/h · g(\phi, f_1)/h \\
  &\leq g(\phi, f_1)/h, \\
\lintertext{so that}
g(\phi, f_1)/h
  &\geq g(\phi, f)/h \geq g(\phi_1, f)/h.
\end{DPalign*}

This proves the statement made above. It will be noticed
that we cannot necessarily compare the \textit{à~priori} probabilities
of two generalisations in respect of more and less, unless the condition
of the first is included in the condition of the second, and
the conclusion of the second is included in that of the first.

We see, therefore, that some generalisations stand \emph{initially}
in a stronger position than others. In order to attain a given
degree of probability, generalisations require, according to their
scope, different amounts of favourable evidence to support them.

\Paragraph{5.} Let us now pass from the character of the generalisation
\textit{à~priori} to the evidence by which we support it. Since, whenever
the conclusion~$f$ is complex, \ie~resolvable into the form
$f_1f_2$ where $g(f_1, f_2)/h \neq 1$, we can express the probability of the
generalisation $g(\phi, f)$ as the product of the probabilities of the
two generalisations $g(\phi f_1, f_2)$ and~$g(\phi, f)$, we may assume in what
follows, that the conclusion~$f$ is simple and not capable of further
analysis, without diminishing the generality of our argument.

We will begin with the simplest case, namely, that which
arises in the following conditions. First, let us assume that our
knowledge of the examined instances is complete, so that we know
of every statement, which is about the examined instances,
whether it is true or false of each.\footnote
  {If $\psi(a)$ is a proposition and $\psi(a)=h · \theta(a)$, where $h$~is a proposition not
  involving~$a$, then we must regard~$\theta(a)$, not~$\psi(a)$\DPtypo{}{,} as the statement \emph{about}~$a$.}
Second, let us assume that
%% -----File: 237.png---Folio 226-------
\index{Uniformity of Nature, Law of}%
all the instances which are known to satisfy the condition~$\phi$,
are also known to satisfy the conclusion~$f$ of the generalisation.
And third let us assume that there is nothing which is true of
\emph{all} the examined instances and yet not included either in~$\phi$ or
in~$f$, \ie\ that the positive analogy between the instances is
exactly \DPchg{co-extensive}{coextensive} with the analogy~$\phi f$ which is covered by the
generalisation.

Such evidence as this constitutes what we may term a perfect
analogy. The argument in favour of the generalisation cannot
be further improved by a knowledge of additional instances.
Since the positive analogy between the instances is exactly
coextensive with the analogy covered by the generalisation, and
since our knowledge of the examined instances is complete, there
is no need to take account of the negative analogy.

An analogy of this kind, however, is not likely to have much
practical utility; for if the analogy covered by the generalisation,
covers the \emph{whole} of the positive analogy between the instances
it is difficult to see to what \emph{other} instances the generalisation can
be applicable. Any instance, about which everything is true
which is true of all of a set of instances, must be identical with
one of them. Indeed, an argument from perfect analogy can
only have practical utility, if, as will be argued later on, there are
some distinctions between instances which are \emph{irrelevant} for the
purposes of analogy, and if, in a perfect analogy, the positive
analogy, of which we must take account, need cover only those
distinctions which are relevant. In this case a generalisation
based on perfect analogy might cover instances numerically
distinct from those of the original set.

The law of the Uniformity of Nature appears to me to amount
to an assertion that an analogy which is perfect, except that mere
differences of position in time and space are treated as irrelevant,
\index{Space!uniformity@{and uniformity}}%
\index{Time!uniformity@{and uniformity}}%
is a valid basis for a generalisation, two total causes being regarded
as the \emph{same} if they only differ in their positions in time
or space. This, I think, is the whole of the importance which
this law has for the theory of inductive argument. It involves
the assertion of a generalised judgment of irrelevance, namely,
of the irrelevance of mere position in time and space to generalisations
which have no reference to particular positions in time
and space. It is in respect of such position in time or space that
`nature' is supposed `uniform.' The significance of the law
%% -----File: 238.png---Folio 227-------
and the nature of its justification, if any, are further discussed
in \Chapref{XXII}\@.

\Paragraph{6.} Let us now pass to the type which is next in order of
simplicity. We will relax the first condition and no longer assume
that the \emph{whole} of the positive analogy between the instances is
covered by the generalisation, though retaining the assumption
that our knowledge of the examined instances is complete. We
know, that is to say, that there are some respects in which the
examined instances are all alike, and yet which are not covered
by the generalisation. If $\phi_1$~is the part of the positive analogy
between the instances which is \emph{not} covered by the generalisation,
then the probability of this type of argument from analogy can
be written---
\[
g(\phi, f) \Big/ \underset{a_1 \ldots a_n}{A}(\phi \phi_1 f).
\]

The value of this probability turns on the comprehensiveness
of~$\phi_1$. There are some characteristics~$\phi_1$ common to all the
instances, which the generalisation treats as unessential, but
the less comprehensive these are the better. $\phi_1$~stands for the
characteristics in which all the instances resemble one another
outside those covered by the generalisation. To reduce these
resemblances between the instances is the same thing as to
increase the differences between them. And hence any increase
in the Negative Analogy involves a reduction in the comprehensiveness
of~$\phi_1$. When, however, our knowledge of the
instances is complete, it is not necessary to make separate
mention of the negative analogy $\underset{a_1 \ldots a_n}{\bar{A}}(\phi')$ in the above formula.
For $\phi'$~simply includes all those functions about the instances,
which are not included in~$\phi \phi_1 f$, and of which the contradictories
are not included in them; so that in stating $\underset{a_1 \ldots a_n}{A}(\phi\phi_1f)$, we
state by implication $\underset{a_1 \ldots a_n}{\bar{A}}(\phi')$ also.

The whole process of strengthening the argument in favour
of the generalisation $g(\phi, f)$ by the accumulation of further experience
appears to me to consist in making the argument
approximate as nearly as possible to the conditions of a perfect
analogy, by steadily reducing the comprehensiveness of those
resemblances~$\phi_1$ between the instances which our generalisation
disregards. Thus the advantage of additional instances, derived
%% -----File: 239.png---Folio 228-------
from experience, arises not out of their number as such, but out
of their tendency to limit and reduce the comprehensiveness of~$\phi_1$,
or, in other words, out of their tendency to increase the negative
analogy~$\phi'$, since $\phi_1 \phi'$~comprise between them whatever is not
covered by~$\phi f$. The more numerous the instances, the less comprehensive
are their superfluous resemblances likely to be. But
a single additional instance which greatly reduced~$\phi_1$ would increase
the probability of the argument more than a large number
of instances which affected~$\phi_1$ less.

\Paragraph{7.} The nature of the argument examined so far is, then, that
the instances all have some characteristics in common which
we have ignored in framing our generalisation; but it is still
assumed that our knowledge about the examined instances is
complete. We will next dispense with this latter assumption, and
deal with the case in which our knowledge of the characteristics
of the examined instances themselves is or may be incomplete.

It is now necessary to take explicit account of the known
negative analogy. For when the known positive analogy falls
short of the total positive analogy, it is not possible to infer the
negative analogy from it. Differences may be known between the
instances which cannot be inferred from the known positive
analogy. The probability of the argument must, therefore, be
written---
\[
g(\phi, f)\Big/\underset{a_1 \ldots a_n}{A}(\phi \phi_1 f)
               \underset{a_1 \ldots a_n}{\bar{A}}(\phi'),
\]
where $\phi \phi_1 f$~stands for the characteristics in which all $n$~instances
$a_1 \ldots a_n$ are \emph{known} to be alike, and $\phi'$~stands for the characteristics
in which they are \emph{known} to differ.

This argument is strengthened by any additional instance or
by any additional knowledge about the former instances which
diminishes the known superfluous resemblances~$\phi_1$ or increases the
negative analogy~$\phi'$. The object of the accumulation of further
experience is still the same as before, namely, to make the form
of the argument approximate more and more closely to that of
perfect analogy. Now, however, that our knowledge of the
instances is no longer assumed to be complete, we must take
account of the mere \emph{number}~$n$ of the instances, as well as of our
specific knowledge in regard to them; for the more numerous
the instances are, the greater the opportunity for the \emph{total}
negative analogy to exceed the \emph{known} negative analogy. But
%% -----File: 240.png---Folio 229-------
the more complete our knowledge of the instances, the less
attention need we pay to their mere number, and the more
imperfect our knowledge the greater the stress which must be
laid upon the argument from number. This part of the argument
will be discussed in detail in the following chapter on
Pure Induction.

\Paragraph{8.} When our knowledge of the instances is incomplete, there
may exist analogies which are known to be true of some of the
instances and are not known to be false of any. These sub-analogies
\index{Sub-analogies}%
(see §\;2) are not so dangerous as the positive analogies~$\phi_1$,
which are known to be true of \emph{all} the instances, but their existence
is, evidently, an element of weakness, which we must endeavour
to eliminate by the growth of knowledge and the multiplication
of instances. A sub-analogy of this kind between the instances
$a_r \ldots a_s$ may be written $\underset{a_r \ldots a_s}{A}(\psi_k)$; and the formula, if it
is to take account of all the relevant information, ought, therefore,
to be written---
\[
g(\phi,f)\Big/\underset{a_1 \ldots a_n}{A}(\phi\phi_1f)
              \underset{a_1 \ldots a_n}{\bar{A}}(\phi')
  \Prod\left\{\underset{a_r \ldots a_s}{A}(\psi_k)\right\},
\]
where the terms of $\Prod\left\{\underset{a_r \ldots a_s}{A}(\psi_k)\right\}$ stand for the various sub-analogies
between sub-classes of the instances, which are not
included in~$\phi \phi_1 f$ or in~$\phi'$.

\Paragraph{9.} There is now another complexity to be introduced. We
must dispense with the assumption that the whole of the analogy
covered by the generalisation is known to exist in all the instances.
For there may be some instances within our experience, about
which our knowledge is incomplete, but which show \emph{part} of the
analogy required by the generalisation and nothing which contradicts
it; and such instances afford some support to the
generalisation. Suppose that ${}_b\phi$~and~${}_bf$ are \emph{part} of $\phi$~and~$f$ respectively,
then we may have a set of instances $b_1 \ldots b_m$ which
show the following analogies:
\[
\underset{b_1 \ldots b_m}{A}({}_b\phi\, {}_b\phi_{1} \,{}_bf)
\underset{b_1 \ldots b_m}{\bar{A}}({}_b\phi')
\Prod\left\{\underset{b_r \ldots b_s}{A}({}_b\psi_k)\right\},
\]
where ${}_b\phi_1$~is the analogy not covered by the generalisation, and
so on, as before.
%% -----File: 241.png---Folio 230-------

The formula, therefore, is now as follows:
\[
g(\phi,f)\Big/
\Prod_{a,b\ldots}\left\{
  \underset{a_1 \ldots a_n}{A}({}_a\phi\, {}_a\phi_{1}\, {}_af)
  \underset{a_1 \ldots a_n}{\bar{A}}({}_a\phi')\right\}
  \Prod\left\{\underset{a_r\, b_s\ldots}{A}(\psi_k)\right\}.
\]
In this expression ${}_a\phi$,~${}_a f$ are the whole \emph{or} part of $\phi$,~$f$; the product
$\Prod\limits_{a,b\ldots}$ is composed of the positive and negative analogies for each
of the sets of instances $a_1 \ldots a_n$, $b_1 \ldots b_m$,~etc.; and the
product~$\Prod$ contains the various sub-analogies of different sub-classes
of all the instances $a_1 \ldots a_n$, $b_1 \ldots b_m$,~etc., regarded as
\emph{one} set.\footnote
  {Even if we want to distinguish between the sub-analogies of the $a$~set and
  the sub-analogies of the $b$~set, this information can be gathered from the product~$\Prod$.}

\Paragraph{10.} This completes our classification of the \emph{positive} evidence
which supports a generalisation; but the probability may also
be affected by a consideration of the negative evidence. We
have taken account so far of that part of the evidence only which
shows the whole or part of the analogy we require, and we have
neglected those instances of which~$\phi$, the condition of the generalisation,
or~$f$, its conclusion, or part of~$\phi$ or of~$f$ is \emph{known to be false}.
Suppose that there are instances of which $\phi$~is true and $f$~false, it
is clear that the generalisation is ruined. But cases in which we
know \emph{part} of~$\phi$ to be true and $f$~to be false, and are ignorant as
to the truth or falsity of the rest of~$\phi$, weaken it to some extent.
We must take account, therefore, of analogies
\[
\underset{a_1' \ldots a_n''}{A}({}_{a'}\phi\, {}_{a'}\bar f),
\]
%[**TN: Unclear. A formatter claims to have checked this against a hard copy.]
where~${}_{a'}\phi$, part of~$\phi$, is true of all the set, and~${}_{a'}f$, part of~$f$, is
false of all the set, while the truth or falsity of some part of $\phi$~and~$f$
is unknown. The negative evidence, however, can strengthen
as well as weaken the evidence. We deem instances favourably
relevant in which $\phi$~and~$f$ are both false together.\footnote
  {I am disposed to think that we need not pay attention to instances for
  which part of~$\phi$ is known to be false, and part of~$f$ to be true. But the
  question is a little perplexing.}

Our final formula, therefore, must include terms, similar to
those in the formula which concludes §\;9, not only for sets of
instances which show analogies~${}_a\phi\, {}_a f$ where ${}_a\phi$~and~${}_a f$ are parts
of $\phi$~and~$f$, but also for sets which show analogies ${}_a\bar\phi\, {}_a f$,
%% -----File: 242.png---Folio 231-------
or analogies~${}_a\bar{\phi}\, {}_a\bar{f}$, where ${}_a\phi$~and~${}_af$ are the whole or part of $\phi$~and~$f$,
and \DPtypo{$\bar{\phi}\,\bar{f}$}{$\bar{\phi}$, $\bar{f}$} are the contradictories of $\phi$~and~$f$.\footnote
  {Where the conclusion~$f$ is simple and not complex (see §\;5), some of these
  complications cannot, of course, arise.}

It should be added, perhaps, that the theoretical classification
of most empirical arguments in daily use is complicated by
the account which we reasonably take of generalisations previously
established. We often take account indirectly, therefore,
of evidence which supports in some degree other generalisations
than that which we are concerned to establish or refute at the
moment, but the probability of which is relevant to the problem
under investigation.

\Paragraph{11.} The argument will be rendered unnecessarily complex,
without much benefit to its theoretical interest, if we deal with
the most general case of all. What follows, therefore, will deal
with the formula of the third degree of generality, namely---
\[
g(\phi,f)\Big/\underset{a_1 \ldots a_n}{A}(\phi\phi_1f)
              \underset{a_1 \ldots a_n}{\bar{A}}(\phi')
  \Prod\left\{\underset{a_r \ldots a_s}{A}(\psi_k)\right\},
\]
in which no \emph{partial} instances occur, \ie\ no instances in which part
only of the analogy, required by the generalisation, is known to
exist. In this third degree of generality, it will be remembered,
our knowledge of the characteristics of the instances is incomplete,
there is more analogy between the instances than is
covered by the generalisation, and there are some sub-analogies
to be reckoned with. In the above formula the incompleteness
of our knowledge is implicitly recognised in that $\phi \phi_1 f \phi'$ are
not between them entirely comprehensive. It is also supposed
that all the evidence we have is positive, no knowledge is
assumed, that is to say, of instances characterised by the conjunctions
${}_a\bar{\phi}\, {}_af$,~${}_a\phi\ {}_a\bar f$, or~${}_a\bar{\phi}\, {}_a\bar f$, where ${}_a\phi$~and~${}_a f$ are part of $\phi$~and~$f$.

An argument, therefore, from experience, in which, on the
basis of examined instances, we establish a generalisation applicable
beyond these instances, can be strengthened, if we restrict our
attention to the simpler type of case, by the following means:

(1) By reducing the resemblances~$\phi_1$ known to be common to
all the instances, but ignored as unessential by the generalisation.

(2) By increasing the differences~$\phi'$ known to exist between
the instances.
%% -----File: 243.png---Folio 232-------

(3) By diminishing the sub-analogies or unessential resemblances~$\psi_k$
known to be common to some of the instances and not
known to be false of any.

These results can generally be obtained in two ways, either by
increasing the number of our instances or by increasing our knowledge
of those we have.

The reasons why these methods seem to common sense to
strengthen the argument are fairly obvious. The object of~(1) is to
avoid the possibility that $\phi_1$~as well as~$\phi$ is a necessary condition
of~$f$. The object of~(2) is to avoid the possibility that there may
be some resemblances additional to~$\phi$, common to all the instances,
which have escaped our notice. The object of~(3) is to get rid
of indications that the total value of~$\phi_1$ may be greater than the
known value. When $\phi\phi_1 f$ is the \emph{total} positive analogy between
the instances, so that the known value of~$\phi_1$ is its total value, it
is~(1) which is fundamental; and we need take account of (2)~and~(3)
only when our knowledge of the instances is incomplete.
But when our knowledge of the instances is incomplete, so that
$\phi_1$~falls short of its total value and we cannot infer~$\phi'$ from it,
it is better to regard~(2) as fundamental; in any case every
reduction of~$\phi_1$ must increase~$\phi'$.

\Paragraph{12.} I have now attempted to analyse the various ways in
which common practice seems to assume that considerations
of Analogy can yield us presumptive evidence in favour of a
generalisation.

It has been my object, in making a classification of empirical
arguments, not so much to put my results in forms closely similar
to those in which problems of generalisation commonly present
themselves to scientific investigators, as to inquire whether
ultimate uniformities of method can be found beneath the
innumerable modes, superficially differing from another, in
which we do in fact argue.

I have not yet attempted to justify this way of arguing.
After turning aside to discuss in more detail the method of Pure
Induction, I shall make this attempt; or rather I shall try to see
\emph{what sort} of assumptions are capable of justifying empirical
reasoning of this kind.
%% -----File: 244.png---Folio 233-------


\Chapter{XX}{The Value of Multiplication of Instances, or Pure
Induction}

\Paragraph{1.} \First{It} has often been thought that the essence of inductive argument
lies in the multiplication of instances. ``Where is that
\index{Multiplication!of instances|ifoll}%
process of reasoning,'' Hume inquired, ``which from one instance
\index{Hume!Induction@{and Induction}}%
draws a conclusion, so different from that which it infers from
a hundred instances, that are no way different from that single
instance?'' I repeat that by emphasising the number of the instances
Hume obscured the real object of the method. If it
were strictly true that the hundred instances are \emph{no} way different
from the single instance, Hume would be right to wonder in what
manner they can strengthen the argument. The object of increasing
the number of instances arises out of the fact that we
are nearly always aware of \emph{some} difference between the instances,
and that even where the known difference is insignificant we may
suspect, especially when our knowledge of the instances is very
incomplete, that there may be more. Every new instance \emph{may}
diminish the unessential resemblances between the instances and
by introducing a new difference increase the Negative Analogy.
\index{Analogy, principle of!negative}%
For this reason, and for this reason only, new instances are
valuable.

If our premisses comprise the body of memory and tradition
which has been originally derived from direct experience, and
the conclusion which we seek to establish is the Newtonian theory
of the Solar System, our argument is one of Pure Induction, in
so far as we support the Newtonian theory by pointing to the
great number of consequences which it has in common with the
facts of experience. The predictions of the Nautical Almanack
are a consequence of the Newtonian theory, and these predictions
are verified many thousand times a day. But even here the
%% -----File: 245.png---Folio 234-------
force of the argument largely depends, not on the mere number
of these predictions, but on the knowledge that the circumstances
in which they are fulfilled differ widely from one another in a
vast number of important respects. The \emph{variety} of the circumstances,
\index{Variety}%
in which the Newtonian generalisation is fulfilled, rather
than the number of them, is what seems to impress our reasonable
faculties.

\Paragraph{2.} I hold, then, that our object is always to increase the
Negative Analogy, or, which is the same thing, to diminish the
characteristics common to all the examined instances and yet not
taken account of by our generalisation. Our method, however,
maybe one which certainly achieves this object, or it may be one
which possibly achieves it. The former of these, which is obviously
the more satisfactory, may consist either in increasing our
definite knowledge respecting instances examined already, or in
finding additional instances respecting which definite knowledge
is obtainable. The second of them consists in finding additional
instances of the generalisation, about which, however, our definite
knowledge may be meagre; such further instances, if our
knowledge about them were more complete, would either increase
or leave unchanged the Negative Analogy; in the former case
they would strengthen the argument and in the latter case they
would not weaken it; and they must, therefore, be allowed some
weight. The two methods are not entirely distinct, because
new instances, about which we have some knowledge but not
much, may be known to increase the Negative Analogy a little
by the first method, and suspected of increasing it further by the
second.

It is characteristic of advanced scientific method to depend
on the former, and of the crude unregulated induction of ordinary
experience to depend on the latter. It is when our definite
knowledge about the instances is limited, that we must pay
attention to their number rather than to the specific differences
between them, and must fall back on what I term Pure Induction.

In this chapter I investigate the conditions and the manner
in which the mere repetition of instances can add to the force
of the argument. The chief value of the chapter, in my judgment,
is negative, and consists in showing that a line of advance,
which might have seemed promising, turns out to be a blind
alley, and that we are thrown back on known Analogy. Pure
%% -----File: 246.png---Folio 235-------
Induction will not give us any very substantial assistance in
getting to the bottom of the general inductive problem.

\Paragraph{3.} The problem of generalisation\footnote
  {In the most general sense we can regard any proposition as the generalisation
  of all the propositions which follow from it. For if $h$~is any proposition,
  and we put $\phi(x)\equiv \text{`$x$~can be inferred from~$h$'}$ and, $f(x)\equiv x$, then $g(\phi, f)\equiv h$. Since
  Pure Induction consists in finding as many instances of a generalisation as
  possible, it is, in the widest sense, the process of strengthening the probability
  of any proposition by adducing numerous instances of known truths which
  follow from it. The argument is one of Pure Induction, therefore, in so far as
  the probability of a conclusion is based upon the number of independent consequences
  which the conclusion and the premisses have in common.}
by Pure Induction can be
stated in the following symbolic form:

Let $h$~represent the general \textit{à~priori data} of the investigation;
let $g$~represent the generalisation which we seek to establish;
let $x_1x_2\ldots x_n$ represent instances of~$g$.

Then $x_1/gh=1$, $x_2/gh=1 \ldots x_n/gh=1$; given~$g$, that is to
say, the truth of each of its instances follows. The problem is
to determine the probability $g/hx_1x_2 \ldots x_n$, \ie~the probability
of the generalisation when $n$~instances of it are given. Our
analysis will be simplified, and nothing of fundamental importance
will be lost, if we introduce the assumption that there is nothing
in our \textit{à~priori data} which leads us to distinguish between the
\textit{à~priori} likelihood of the different instances; we assume, that is
to say, that there is no reason \textit{à~priori} for expecting the occurrence
of any one instance with greater reliance than any other,~\ie
\begin{DPgather*}[m]
x_1/h = x_2/h = \ldots = x_n/h. \\
\lintertext{\rlap{Write}}
g/hx_1x_2 \ldots x_n = p_n \\
\lintertext{\rlap{and}}
x_{n+1}/hx_1x_2 \ldots x_n = y_{n+1}; \\
\intertext{then}
\begin{aligned}
\frac{p_n}{p_{n-1}} = \frac{g/hx_1\ldots x_n}{g/hx_1 \ldots x_{n-1}}
  &= \frac{gx_n/hx_1 \ldots x_{n-1}}
          {g/hx_1 \ldots x_{n-1} · x_n/hx_1 \ldots x_{n-1}}\\
%
  &= \frac{x_n/ghx_1 \ldots x_{n-1}}{x_n/hx_1 \ldots x_{n-1}} \\
%
  &= \frac{1}{y_n}.
\end{aligned}
\end{DPgather*}
$\therefore \dfrac{p_n}{p_{n-1}} = \dfrac{1}{y_n}$, and hence $p_n = \dfrac{1}{y_1y_2\ldots y_n} · p_0$, where $p_0 = g/h$, \ie~$p_0$
is the \textit{à~priori} probability of the generalisation.
%% -----File: 247.png---Folio 236-------

It follows, therefore, that $p_n > p_{n-1}$ so long as $y_n > 1$.

Further,
\begin{align*}
x_1x_2 \ldots x_n/h
  &= x_n/hx_1x_2 \ldots x_{n-1} · x_1x_2 \ldots x_{n-1}/h \\
  &= y_n · x_1x_2 \ldots x_{n-1}/h \\
  &= y_n y_{n-1} \ldots y_1. \\
\therefore p_n
  &= \frac{p_0}{y_1y_2 \ldots y_n}
   = \frac{p_0}{x_1x_2 \ldots x_n/h} \\
  &= \frac{p_0}{x_1x_2 \ldots x_ng/h + x_1x_2 \ldots x_n\bar{g}/h} \\
  &= \frac{p_0}{g/h + x_1x_2 \ldots x_n/\bar{g}h · \bar{g}/h} \\
  &= \frac{p_0}{p_0 + x_1x_2 \ldots x_n/\bar{g}h(1 - p_0)}
\end{align*}

This approaches unity as a limit, if $x_1x_2 \ldots x_n/\bar{g}h · \dfrac{1}{p_0}$
approaches zero as a limit, when $n$~increases.

\Paragraph{4.} We may now stop to consider how much this argument has
proved. We have shown that if each of the instances necessarily
follows from the generalisation, then each additional instance
increases the probability of the generalisation, so long as the new
instance could not have been predicted with certainty from a
knowledge of the former instances.\footnote
  {Since $p_n > p_{n-1}$ so long as $y_n \neq 1$.}
This condition is the same
as that which came to light when we were discussing Analogy.
If the new instance were identical with one of the former instances,
a knowledge of the latter would enable us to predict it.
If it differs or may differ in analogy, then the condition required
above is satisfied.

The common notion, that each successive verification of a
doubtful principle strengthens it, is formally proved, therefore,
without any appeal to conceptions of law or of causality. \emph{But
we have not proved} that this probability approaches certainty as
a limit, or even that our conclusion becomes more likely than not,
as the number of verifications or instances is indefinitely increased.

\Paragraph{5.} What are the conditions which must be satisfied in order
that the rate, at which the probability of the generalisation
increases, may be such that it will approach certainty as a
%% -----File: 248.png---Folio 237-------
\index{Probability, and relevant knowledge!finite}%
limit when the number of independent instances of it are indefinitely
increased? We have already shown, as a basis for
this investigation, that $p_n$~approaches the limit of certainty for
a generalisation~$g$, if, as $n$~increases, $x_1x_2 \ldots x_n/\bar{g}h$ becomes
small compared with~$p_0$, \ie~if the \textit{à~priori} probability of so many
instances, assuming the falsehood of the generalisation, is small
compared with the generalisation's \textit{à~priori} probability. It
follows, therefore, that the probability of an induction tends
towards certainty as a limit, when the number of instances is
increased, provided that
\[
x_r/x_1 x_2 \ldots x_{r-1} \bar{g}h < 1 - \epsilon
\]
for all values of~$r$, and $p_0>\eta$, where $\epsilon$~and~$\eta$ are finite probabilities,
separated, that is to say, from impossibility by a value
of some finite amount, however small. These conditions appear
simple, but the meaning of a `finite probability' requires a
word of explanation.\footnote
  {The proof of these conditions, which is obvious, is as follows:
  \[
  x_1 x_2\ldots  x_n / \bar{g}h = x_{n-1}\bar{g}h · x_1 x_2 \ldots x_{n-1} / \bar{g}h < (1-\epsilon)^n,
  \]
  where $\epsilon$~is finite and $p_0 > \eta$ where $\eta$~is finite. There is always, under these
  conditions, some finite value of~$n$ such that both $(1 - \epsilon)^n$ and~$\dfrac{(1 - \epsilon)^n}{\eta}$ are less
  than any given finite quantity, however small.}

I argued in \Chapref{III}. that not all probabilities have an
exact numerical value, and that, in the case of some, one can say
no more about their relation to certainty and impossibility than
that they fall short of the former and exceed the latter. There
is one class of probabilities, however, which I called the numerical
class, the ratio of each of whose members to certainty can be
expressed by some number less than unity; and we can sometimes
compare a non-numerical probability in respect of more and less
with one of these numerical probabilities. This enables us to
give a definition of `finite probability' which is capable of application
to non-numerical as well as to numerical probabilities. I
define a `finite probability' as one which \emph{exceeds} some numerical
probability, the ratio of which to certainty can be expressed by
a finite number.\footnote
  {Hence a series of probabilities $p_1p_2 \ldots p_r$ approaches a limit~$L$, if, given
  any positive finite number~$\epsilon$ however small, a positive integer~$n$ can always be
  found such that for all values of~$r$ greater than~$n$ the difference between $L$~and~$p_r$
  is less than~$\epsilon · \gamma$, where $\gamma$~is the measure of certainty.}
The principal method, in which a probability
can be proved finite by a process of argument, arises either when
%% -----File: 249.png---Folio 238-------
its conclusion can be shown to be one of a finite number of alternatives,
which are between them exhaustive or, at any rate, have
a finite probability, and to which the Principle of Indifference
is applicable; or (more usually), when its conclusion is \emph{more}
probable than some hypothesis which satisfies this first condition.

\Paragraph{6.} The conditions, which we have now established in order
that the probability of a pure induction may tend towards
certainty as the number of instances is increased, are (1)~that
$x_r/x_1x_2 \ldots x_{r-1} \bar{g}h$ falls short of certainty by a finite amount
for all values of~$r$, and (2)~that~$p_0$, the \textit{à~priori} probability of our
generalisation, exceeds impossibility by a finite amount. It is
easy to see that we can show by an exactly similar argument that
the following more general conditions are equally satisfactory:

(1) That $x_r/x_1x_2 \ldots x_{r-1} \bar{g}h$ falls short of certainty by a finite
amount for all values of~$r$ beyond a specified value~$s$.

(2) That $p_s$, the probability of the generalisation relative to
a knowledge of these first $s$~instances, exceeds impossibility by
a finite amount.

In other words Pure Induction can be usefully employed to
strengthen an argument if, after a certain number of instances
have been examined, we have, from some other source, a finite
probability in favour of the generalisation, and, assuming the
generalisation is false, a finite uncertainty as to its conclusion
being satisfied by the next hitherto unexamined instance which
satisfies its premiss. To take an example, Pure Induction can
be used to support the generalisation that the sun will rise every
morning for the next million years, provided that with the experience
we have actually had there are finite probabilities,
however small, \emph{derived from some other source}, first, in favour of
the generalisation, and, second, in favour of the sun's \emph{not} rising
to-morrow assuming the generalisation to be false. Given these
finite probabilities, obtained otherwise, however small, then the
probability can be strengthened and can tend to increase towards
certainty by the mere multiplication of instances provided
that these instances are so far distinct that they are not
inferrible one from another.

\Paragraph{7.} Those supposed proofs of the Inductive Principle, which
are based openly or implicitly on an argument in inverse probability,
are all vitiated by unjustifiable assumptions relating
to the magnitude of the \textit{à~priori} probability~$p_0$. Jevons, for
\index{Jevons!Induction@{and Induction}}%
%% -----File: 250.png---Folio 239-------
\index{Metaphysics and certainty}%
instance, avowedly assumes that we may, in the absence of special
information, suppose any unexamined hypothesis to be as likely
as not. It is difficult to see how such a belief, if even its most
immediate implications had been properly apprehended, could
have remained plausible to a mind of so sound a practical judgment
as his. The arguments against it and the contradictions
to which it leads have been dealt with in \Chapref{IV}\@. The
demonstration of Laplace, which depends upon the Rule of
\index{Laplace!Induction@{and Induction}}%
Succession, will be discussed in \Chapref{XXX}\@.

\Paragraph{8.} The prior probability, which must always be found, before
the method of pure induction can be usefully employed to support
a substantial argument, is derived, I think, in most ordinary
cases---with what justification it remains to discuss---from considerations
of Analogy. But the conditions of valid induction
as they have been enunciated above, are quite independent of
analogy, and might be applicable to other types of argument.
In certain cases we might feel justified in assuming \emph{directly} that
the necessary conditions are satisfied.

Our belief, for instance, in the validity of a logical scheme is
based partly upon inductive grounds---on the \emph{number} of conclusions,
each seemingly true on its own account, which can be
derived from the axioms---and partly on a degree of self-evidence
in the axioms themselves sufficient to give them the initial
probability upon which induction can build. We depend upon
the initial presumption that, if a proposition appears to us to
be true, this is by itself, in the absence of opposing evidence,
\emph{some reason} for its \emph{being} as well as appearing true. We cannot
deny that what appears true is sometimes false, but, unless we
can assume some substantial relation of probability between
the appearance and the reality of truth, the possibility of
even probable knowledge is at an end.

The conception of our having \emph{some} reason, though not a
conclusive one, for certain beliefs, arising out of direct inspection,
may prove important to the theory of epistemology. The old
metaphysics has been greatly hindered by reason of its having
always demanded demonstrative certainty. Much of the cogency
of Hume's criticism arises out of the assumption of methods
\index{Hume}%
of certainty on the part of those systems against which it was
directed. The earlier realists were hampered by their not perceiving
that lesser claims in the beginning might yield them
%% -----File: 251.png---Folio 240-------
\index{Moore, G. E.|inote}%
what they wanted in the end. And transcendental philosophy
has partly arisen, I believe, through the belief that there is no
knowledge on these matters short of certain knowledge, being
combined with the belief that such certain knowledge of metaphysical
questions is beyond the power of ordinary methods.

When we allow that probable knowledge is, nevertheless, real,
a new method of argument can be introduced into metaphysical
discussions. The demonstrative method can be laid on one side,
and we may attempt to advance the argument by taking account
of circumstances which seem to give \emph{some} reason for preferring
one alternative to another. Great progress may follow if the
nature and reality of objects of perception,\footnote
  {A paper by Mr.~G.~E. Moore entitled, ``The Nature and Reality of Objects
  of Perception,'' which was published in the \textit{Proceedings of the Aristotelian Society
  for 1906}, seems to me to apply for the first time a method somewhat resembling
  that which is described above.}
for instance, can be
usefully investigated by methods not altogether dissimilar from
those employed in science and with the prospect of obtaining as
high a degree of certainty as that which belongs to some scientific
conclusions; and it may conceivably be shown that a belief in
the conclusions of science, enunciated in any reasonable manner
however restricted, involves a preference for some metaphysical
conclusions over others.

\Paragraph{9.} Apart from analysis, careful reflection would hardly lead
us to expect that a conclusion which is based on no other than
grounds of pure induction, defined as I have defined them as
consisting of repetition of instances merely, could attain in this
way to a high degree of probability. To this extent we ought
all of us to agree with Hume. We have found that the suggestions
of common sense are supported by more precise methods.
Moreover, we constantly distinguish between arguments, which
we call inductive, upon other grounds than the number of instances
upon which they are based; and under certain conditions
we regard as crucial an insignificant number of experiments. The
method of pure induction may be a useful means of strengthening
a probability based on some other ground. In the case, however,
of most scientific arguments, which would commonly be called
inductive, the probability that we are right, when we make
predictions on the basis of past experience, depends not so
much on the number of past experiences upon which we rely,
as on the degree in which the circumstances of these experiences
%% -----File: 252.png---Folio 241-------
resemble the known circumstances in which the prediction is
to take effect. Scientific method, indeed, is mainly devoted to
discovering means of so heightening the known analogy that
we may dispense as far as possible with the methods of pure
induction.

When, therefore, our previous knowledge is considerable
and the analogy is good, the purely inductive part of the argument
may take a very subsidiary place. But when our knowledge
of the instances is slight, we may have to depend upon pure
induction a good deal. In an advanced science it is a last resort,---the
least satisfactory of the methods. But sometimes it must
be our first resort, the method upon which we must depend in
the dawn of knowledge and in fundamental inquiries where
we must presuppose nothing.
%% -----File: 253.png---Folio 242-------
\index{Fermat, formula of}%


\Chapter{XXI}{The Nature of Inductive Argument Continued}

\Paragraph{1.} \First{In} the enunciation, given in the two preceding chapters, of the
Principles of Analogy and Pure Induction there has been no
reference to experience or causality or law. So far, the argument
has been perfectly formal and might relate to a set of propositions
of any type. But these methods are most commonly
employed in physical arguments where material objects or
experiences are the terms of the generalisation. We must consider,
therefore, whether there is any good ground, as some
logicians seem to have supposed, for restricting them to this
kind of inquiry.

I am inclined to think that, whether reasonably or not, we
naturally apply them to all kinds of argument alike, including
formal arguments as, for example, about numbers. When we
are told that Fermat's formula for a prime, namely, $2^{2^a}+1$~for
all values of~$a$, has been verified in every case in which verification
is not excessively laborious---namely, for $a=1$, $2$,~$3$,
and~$4$, we feel that this is \emph{some} reason for accepting it, or, at
least, that it raises a sufficient presumption to justify a
further examination of the formula.\footnote
  {This formula has, in fact, been disproved in recent times, \eg~$2^{2^5}+1=
  4,294,967,297 = 641 × 6,700,417$. Thus it is no longer so good an illustration
  as it would have been a hundred years ago.}
Yet there can be no reference
here to the uniformity of nature or physical causation. If
inductive methods are limited to natural objects, there can no
more be an appreciable ground for thinking that $2^{2^a}+1$ is a true
formula for primes, because empirical methods show that it
yields primes up to $a=4$, or \emph{even if they showed that it yielded
primes for every number up to a million million}, than there is
to think that any formula which I may choose to write down
%% -----File: 254.png---Folio 243-------
at random is a true source of primes. To maintain that there is
no appreciable ground in such a case is paradoxical. If, on the
other hand, a partial verification does raise some just appreciable
presumption in the formula's favour, then we must include
numbers, at any rate, as well as material objects amongst the
proper subjects of the inductive method. The conclusion of
the previous chapter indicates, however, that, if arguments of
this kind have force, it can only be in virtue of there being
some finite \textit{à~priori} probability for the formula based on other
than inductive grounds.

\index{Jevons!Induction@{and Induction}}%
There are some illustrations in Jevons's \textit{Principles of Science},\footnote
  {Pp.~229--231 (one volume edition). Jevons uses these illustrations, not
  for the purpose to which I am here putting them, but to demonstrate the fallibility
  of empirical laws.}
which are relevant to this discussion. We find it to be true of
the following six numbers:
\[
5,\ 15,\ 35,\ 45,\ 65,\ 95
\]
that they all end in five, and are all divisible by five without remainder.
Would this fact, by itself, raise any kind of presumption
that all numbers ending in five are divisible by five without
remainder? Let us also consider the six numbers,
\[
7,\ 17,\ 37,\ 47,\ 67,\ 97.
\]
They all end in seven and also agree in being primes. Would
this raise a presumption in favour of the generalisation that all
numbers are prime, which end in seven? We might be prejudiced
in favour of the first argument, because it would lead us to a
true conclusion; but we ought not to be prejudiced against the
second because it would lead us to a false one; for the validity
of empirical arguments as the foundation of a probability cannot
be affected by the actual truth or falsity of their conclusions.
If, on the evidence, the analogy is similar and equal, and if the
scope of the generalisation and its conclusion is similar, then the
value of the two arguments must be equal also.

Whether or not the use of empirical argument appears plausible
to us in these particular examples, it is certainly true that many
mathematical theorems have actually been discovered by such
methods. Generalisations have been suggested nearly as often,
perhaps, in the logical and mathematical sciences, as in the
%% -----File: 255.png---Folio 244-------
\index{Jevons|inote}%
\index{Newton, and induction}%
physical, by the recognition of particular instances, even where
formal proof has been forthcoming subsequently. Yet if the
suggestions of analogy have no appreciable probability in the
formal sciences, and should be permitted only in the material, it
must be unreasonable for us to pursue them. If no finite probability
exists that a formula, for which we have empirical verification,
is in fact universally true, Newton was acting fortunately,
but not reasonably, when he hit on the Binomial Theorem by
methods of empiricism.\footnote
  {See Jevons, \textit{loc.\ cit.}\ p.~231.}

\Paragraph{2.} I am inclined to believe, therefore, that, if we trust the
promptings of common sense, we have the same kind of ground
for trusting analogy in mathematics that we have in physics,
and that we ought to be able to apply any justification of the
method, which suits the latter case, to the former also. This
does not mean that the \textit{à~priori} probabilities, from some other
source than induction, which the inductive method requires as
its foundation, may not be sought and found differently in the
two types of inquiry. A reason why it has been thought
that analogy ought to be confined to natural laws may be,
perhaps, that in most of those cases, in which we could
support a mathematical theorem by a very strong analogy, the
existence of a formal proof has done away with the necessity
for the limping methods of empiricism; and because in most
mathematical investigations, while in our earliest thoughts
we are not ashamed to consult analogy, our later work will be
more profitably spent in searching for a formal proof than in
establishing analogies which must, at the best, be relatively weak.
As the modern scientist discards, as a rule, the method of pure
induction, in favour of experimental analogy, where, if he
takes account of his previous knowledge, one or two cases may
prove immensely significant; so the modern mathematician
prefers the resources of his analysis, which may yield him
certainty, to the doubtful promises of empiricism.

\Paragraph{3.} The main reason, however, why it has often been held that
we ought to limit inductive methods to the content of the particular
material universe in which we live, is, most probably, the
fact that we can easily imagine a universe so constructed that
such methods would be useless. This suggests that analogy and
induction, while they happen to be useful to us in this world,
%% -----File: 256.png---Folio 245-------
\index{Frazer, Sir J.}%
\index{Logic, academic!Induction@{and Induction}}%
\index{Primitive people and rational belief}%
cannot be universal principles of logic, on the same footing, for
instance, as the syllogism.

In one sense this opinion may be well founded. I do not deny
or affirm at present that it may be necessary to confine inductive
methods to arguments about certain kinds of objects or certain
kinds of experiences. It may be true that in every useful argument
from analogy our premisses must contain fundamental
assumptions, obtained directly and not inductively, which some
possible experiences might preclude. Moreover, the success of
induction in the past can certainly affect its probable usefulness
for the future. We may discover something about the nature
of the universe---we may even discover it by means of induction
itself---the knowledge of which has the effect of destroying the
further utility of induction. I shall argue later on that the
confidence with which we ourselves use the method does in
fact depend upon the nature of our past experience.

But this empirical attitude towards induction may, on the
other hand, arise out of either one of two possible confusions.
It may confuse, first, the reasonable character of arguments
with their practical usefulness. The usefulness of induction
depends, no doubt, upon the actual content of experience. If
there were no repetition of detail in the universe, induction
would have no utility. If there were only a single object in the
universe, the laws of addition would have no utility. But the
processes of induction and addition would remain reasonable.
It may confuse, secondly, the validity of attributing probability
to the conclusion of an argument with the question of the actual
truth of the conclusion. Induction tells us that, on the basis of
certain evidence, a certain conclusion is reasonable, \emph{not} that it is
true. If the sun does not rise to-morrow, if Queen Anne still
lives, this will not prove that it was foolish or unreasonable of us
to have believed the contrary.

\Paragraph{4.} It will be worth while to say a little more in this connection
about the not infrequent failure to distinguish the rational from
the true. The excessive ridicule, which this mistake has visited
on the supposed irrationality of barbarous and primitive peoples,
affords some good examples. ``Reflection and enquiry should
satisfy us,'' says Dr.~Frazer in the \textit{Golden Bough}, ``that to our
predecessors we are indebted for much of what we thought most
our own, and that their errors were not wilful extravagances
%% -----File: 257.png---Folio 246-------
\index{Pythagoras and `\textit{seven}'}%
or the ravings of insanity, but simply hypotheses, justifiable as
such at the time when they were propounded, but which a fuller
experience has proved to be inadequate\ldots. Therefore, in
reviewing the opinions and practices of ruder ages and races we
shall do well to look with leniency upon their errors as inevitable
slips made in the search for truth\ldots.'' The first introduction of
iron ploughshares into Poland, he tells in another passage, having
been followed by a succession of bad harvests, the farmers attributed
the badness of the crops to the iron ploughshares, and discarded
them for the old wooden ones. The method of reasoning
of the farmers is not different from that of science, and may,
surely, have had for them some appreciable probability in its
favour. ``It is a curious superstition,'' says a recent pioneer in
Borneo, ``this of the Dusuns, to attribute anything---whether
good or bad, lucky or unlucky---that happens to them to something
novel which has arrived in their country. For instance,
my living in Kindram has caused the intensely hot weather we
have experienced of late.''\footnote
  {\textit{Golden Bough}, p.~174.}
What is this curious superstition
but the Method of Difference?
\index{Method of Difference}%

The following passage from Jevons's \textit{Principles of Science} well
\index{Jevons!analogy@{and analogy}}%
illustrates the tendency, to which he himself yielded, to depreciate
the favourite analogies of one age, because the experience of
their successors has confuted them. Between things which are
the same in number, he points out, there is a certain resemblance,
namely in number; and in the infancy of science men could not
be persuaded that there was not a deeper resemblance implied
in that of number. ``Seven days are mentioned in Genesis;
infants acquire their teeth at the end of seven months; they
change them at the end of seven years; seven feet was the limit
of man's height; every seventh year was a climacteric or critical
year, at which a change of disposition took place. In natural
science there were not only the seven planets, and the seven
metals, but also the seven primitive colours, and the seven tones
of music. So deep a hold did this doctrine take that we still have
its results in many customs, not only in the seven days of the
week, but the seven years' apprenticeship, puberty at fourteen
years, the second climacteric, and legal majority at twenty-one
years, the third climacteric.'' Religious systems from Pythagoras
to Comte have sought to derive strength from the virtue of seven.
\index{Comte!seven@{and `\textit{seven}'}}%
%% -----File: 258.png---Folio 247-------
\index{Hudson, W. H., and animism|inote}%
\index{Newton, and induction!ans seven@{and `\textit{seven}'}}%
``And even in scientific matters the loftiest intellects have occasionally
yielded, as when Newton was misled by the analogy
between the seven tones of music and the seven colours of his
spectrum\ldots. Even the genius of Huyghens did not prevent
\index{Huyghens!six@{and `\textit{six}'}}%
him from inferring that but one satellite could belong to Saturn,
because, with those of Jupiter and the earth, it completed the
perfect number of six.'' But is it certain that Newton and
Huyghens were only reasonable when their theories were true,
and that their mistakes were the fruit of a disordered fancy?
Or that the savages, from whom we have inherited the most
fundamental inductions of our knowledge, were always superstitious
when they believed what we now know to be
preposterous?

It is important to understand that the common sense of the
race has been impressed by very weak analogies and has attributed
to them an appreciable probability, and that a logical
theory, which is to justify common sense, need not be afraid of
including these marginal cases. Even our belief in the real
existence of other people, which we all hold to be well established,
may require for its justification the combination of
experience with a just appreciable \textit{à~priori} possibility for
Animism generally.\footnote
  {``This is animism, or that sense of something in Nature which to the
  enlightened or civilised man is not there, and in the civilised man's child, if it
  be admitted that he has it at all, is but a faint survival of a phase of the
  primitive mind. And by animism I do not mean the theory of a soul in
  nature, but the tendency or impulse or instinct, in which all myth originates,
  to \emph{animate} all things; the projection of ourselves into nature; the sense and
  apprehension of an intelligence like our own, but more powerful in all visible
  things'' (Hudson, \textit{Far Away and Long Ago}, pp.~224--5). This `tendency or
  impulse or instinct,' refined by reason and enlarged by experience, may be
  required, in the shape of an intuitive \textit{à~priori} probability, if some of those
  universal conclusions of common sense, which the most sceptical do not kick
  away, are to be supported with rational foundations.}
If we actually possess evidence which
renders some conclusion absurd, it is very difficult for us to
appreciate the relation of this conclusion to data which are
different and less complete; but it is essential that we should
realise arguments from analogy as \emph{relative to premisses}, if we are
to approach the logical theory of Induction without prejudice.

\Paragraph{5.} While we depreciate the former probability of beliefs
which we no longer hold, we tend, I think, to exaggerate the
present degree of certainty of what we still believe. The preceding
paragraph is not intended to deny that savages often greatly
%% -----File: 259.png---Folio 248-------
\index{Grimsehl|inote}%
\index{Relativity, of knowledge!doctrine of, and the Law of Uniformity|inote}%
\index{Uniformity of Nature, Law of}%
\index{Universal Causation, Law of}%
overestimate the value of their crude inductions, and are to this
extent irrational. It is not easy to distinguish between a belief's
being the most reasonable of those which it is open to us to
believe, and its being more probable than not. In the same way
we, perhaps, put an excessive confidence in those conclusions---the
existence of other people, for instance, the law of gravity, or
to-morrow's sunrise---of which, in comparison with many other
beliefs, we are very well assured. We may sometimes confuse
the practical certainty, attaching to the class of beliefs upon which
it is rational to act with the utmost confidence, with the more
wholly objective certainty of logic. We might rashly assert, for
instance, that to-morrow's sunrise is as likely to us as failure,
and the special virtue of the number seven as unlikely, even to
Pythagoras, as success, in an attempt to throw heads a hundred
times in succession with an unbiassed coin.\footnote
  {Yet if every inhabitant of the world, Grimsehl has calculated, were to toss
  a coin every second, day and night, this latter event would only occur once on
  the average in every twenty billion years.}

\Paragraph{6.} As it has often been held upon various grounds, with
reason or without, that the validity of Induction and Analogy
depends in some way upon the character of the actual world,
logicians have sought for material laws upon which these methods
can be founded. The Laws of Universal Causation and the
Uniformity of Nature, namely, that all events have \emph{some} cause
and that the same total cause always produces the same effect,
are those which commonly do service. But these principles
merely assert that there are \emph{some} data from which events posterior
to them in time could be inferred. They do not seem to yield us
much assistance in solving the inductive problem proper, or in
determining how we can infer with probability from \emph{partial} data.
It has been suggested in \Chapref{XIX}\DPtypo{}{.} that the Principle
of the Uniformity of Nature amounts to an assertion that an
argument from perfect analogy (defined as I have defined it) is
valid when applied to events only differing in their positions in
time or space.\footnote
  {Is this interpretation of the Principle of the Uniformity of Nature affected
  by the Doctrine of Relativity?}
It has also been pointed out that ordinary inductive
arguments appear to be strengthened by any evidence
which makes them approximate more closely in character to a
perfect analogy. But this, I think, is the whole extent to which
this principle, even if its truth could be assumed, would help us.
%% -----File: 260.png---Folio 249-------
\index{Atomic Uniformity}%
\index{Principle of superposition of small!effects}%
States of the universe, identical in every particular, may never
recur, and, even if identical states were to recur, we should not
know it.

The kind of fundamental assumption about the character of
material laws, on which scientists appear commonly to act,
seems to me to be much less simple than the bare principle of
Uniformity. They appear to assume something much more like
what mathematicians call the principle of the superposition of
small effects, or, as I prefer to call it, in this connection, the
\emph{atomic} character of natural law. The system of the material
universe must consist, if this kind of assumption is warranted,
of bodies which we may term (without any implication as to
their size being conveyed thereby) \emph{legal atoms}, such that each of
them exercises its own separate, independent, and invariable
effect, a change of the total state being compounded of a number
of separate changes each of which is solely due to a separate
portion of the preceding state. We do not have an invariable
relation between particular bodies, but nevertheless each has on
the others its own separate and invariable effect, which does not
change with changing circumstances, although, of course, the
total effect may be changed to almost any extent if all the other
accompanying causes are different. Each atom can, according
to this theory, be treated as a separate cause and does
not enter into different organic combinations in each of which
it is regulated by different laws.

Perhaps it has not always been realised that this atomic
uniformity is in no way implied by the principle of the
Uniformity of Nature. Yet there might well be quite different
laws for wholes of different degrees of complexity, and laws of
connection between complexes which could not be stated in
terms of laws connecting individual parts. In this case
natural law would be organic and not, as it is generally
supposed, atomic. If every configuration of the Universe were
subject to a separate and independent law, or if very small
differences between bodies---in their shape or size, for instance,---led
to their obeying quite different laws, prediction would be
impossible and the inductive method useless. Yet nature might
still be uniform, causation sovereign, and laws timeless and
absolute.

The scientist wishes, in fact, to assume that the occurrence
%% -----File: 261.png---Folio 250-------
of a phenomenon which has appeared as part of a more complex
phenomenon, may be \emph{some} reason for expecting it to be associated
on another occasion with part of the same complex. Yet if
different wholes were subject to different laws \textit{quâ}~wholes and
not simply on account of and in proportion to the differences of
their parts, knowledge of a part could not lead, it would seem,
even to presumptive or probable knowledge as to its association
with other parts. Given, on the other hand, a number of legally
atomic units and the laws connecting them, it would be possible
to deduce their effects \textit{pro~tanto} without an exhaustive knowledge
of all the coexisting circumstances.

We do habitually assume, I think, that the size of the atomic
unit is for mental events an individual consciousness, and for
material events an object small in relation to our perceptions.
These considerations do not show us a way by which we can
justify Induction. But they help to elucidate the kind of assumptions
which we do actually make, and may serve as an introduction
to what follows.
%% -----File: 262.png---Folio 251-------
\index{Necessary connection, law of}%


\Chapter{XXII}{The Justification of these Methods}

\Paragraph{1.} \First{The} general line of thought to be followed in this chapter may
be indicated, briefly, at the outset.

A system of facts or propositions, as we ordinarily conceive
it, may comprise an indefinite number of members. But the
ultimate constituents or indefinables of the system, which all
the members of it are about, are less in number than these
members themselves. Further, there are certain laws of necessary
connection between the members, by which it is meant (I do not
stop to consider whether \emph{more} than this is meant) that the truth
or falsity of every member can be inferred from a knowledge of
the laws of necessary connection together with a knowledge of the
truth or falsity of some (but not all) of the members.

The ultimate constituents together with the laws of necessary
connection make up what I shall term the \emph{independent variety}
of the system. The more numerous the ultimate constituents
and the necessary laws, the greater is the system's independent
variety. It is not necessary for my present purpose, which is
merely to bring before the reader's mind the sort of conception
which is in mine, that I should attempt a complete definition
of what I mean by a system.

Now it is characteristic of a system, as distinguished from
a collection of heterogeneous and independent facts or propositions,
that the number of its premisses, or, in other words, the
amount of independent variety in it, should be less than the
number of its members. But it is not an obviously essential
characteristic of a system that its premisses or its independent
variety should be actually finite. We must distinguish,
therefore, between systems which may be termed finite and
infinite respectively, the terms \emph{finite} and \emph{infinite} referring not to
%% -----File: 263.png---Folio 252-------
the number of members in the system but to the amount of independent
variety in it.

The purpose of the discussion, which occupies the greater
part of this chapter, is to maintain that, if the premisses of our
argument permit us to assume that the facts or propositions,
with which the argument is concerned, belong to a \emph{finite} system,
then probable knowledge can be validly obtained by means of
an inductive argument. I now proceed to approach the question
from a slightly different standpoint, the controlling idea, however,
being that which is outlined above.

\Paragraph{2.} What is our actual course of procedure in an inductive
argument? We have before us, let us suppose, a set of $n$~instances
which have $r$~known qualities, $a_1a_2\ldots a_r$ in common,
these $r$~qualities constituting the known positive analogy. From
these qualities three (say) are picked out, namely, $a_1$,~$a_2$,~$a_3$ and
we inquire with what probability \emph{all} objects having these three
qualities have also certain other qualities which we have picked
out, namely, $a_{r-1}$,~$a_r$. We wish to determine, that is to say,
whether the qualities $a_{r-1}$,~$a_r$ are \emph{bound up} with the qualities
$a_1$,~$a_2$,~$a_3$. In thus approaching this question we seem to
suppose that the qualities of an object are bound together in
a limited number of \emph{groups}, a sub-class of each group being an
infallible symptom of the coexistence of certain other members
of it also.

Three possibilities are open, any of which would prove
destructive to our generalisation. It may be the case (1)~that
$a_{r-1}$~or~$a_r$ is independent of all the other qualities of the instances---they
may not overlap, that is to say, with any other groups;
or (2)~that $a_1a_2a_3$~do not belong to the same groups as~$a_{r-1}a_r$;
or (3)~that $a_1a_2a_3$, while they belong to the same group as~$a_{r-1}a_r$,
are not sufficient to specify this group uniquely---they belong,
that is to say, to other groups also which do not include $a_{r-1}$~and~$a_r$.
The precautions we take are directed towards reducing the
likelihood, so far as we can, of each of these possibilities. We
distrust the generalisation if the terms typified by~$a_{r-1}a_r$ are
numerous and comprehensive, because this increases the likelihood
that some at least of them fall under heading~(1), and also
because it increases the likelihood of~(3). We trust it if the
terms typified by~$a_1a_2a_3$ are numerous and comprehensive,
because this decreases the likelihood both of~(2) and of~(3). If
%% -----File: 264.png---Folio 253-------
we find a new instance which agrees with the former instances in
$a_1a_2a_3a_{r-1}a_r$ but not in~$a_4$, we welcome it, because this disposes of
the possibility that it is~$a_4$, alone or in combination, that is bound
up with~$a_{r-1}a_r$. We desire to increase our knowledge of the
properties, lest there be some positive analogy which is escaping us,
and when our knowledge is incomplete we multiply instances,
which we do not know to increase the negative analogy for
certain, in the hope that they may do so.

If we sum up the various methods of Analogy, we find, I
think, that they are all capable of arising out of an underlying
assumption, that if we find two sets of qualities in coexistence
there is a finite probability that they belong to the same group,
and a finite probability also that the first set specifies this group
uniquely. Starting from this assumption, the object of the
methods is to increase the finite probability and make it large.
Whether or not anything of this sort is explicitly present to our
minds when we reason scientifically, it seems clear to me that we
do act exactly as we should act, if this were the assumption from
which we set out.

In most cases, of course, the field is greatly simplified from
the first by the use of our pre-existing knowledge. Of the
properties before us we generally have good reason, derived
from prior analogies, for supposing some to belong to the same
group and others to belong to different groups. But this does
not affect the theoretical problem confronting us.

\Paragraph{3.} What kind of ground could justify us in assuming the
existence of these finite probabilities which we seem to require?
If we are to obtain them, not directly, but by means of argument,
we must somehow base them upon a finite number of exhaustive
alternatives.

The following line of argument seems to me to represent, on
the whole, the kind of assumption which is obscurely present to
our minds. We suppose, I think, that the almost innumerable
apparent properties of any given object all arise out of a finite
number of generator properties, which we may call~$\phi_1\phi_2\phi_3\ldots$.
\index{Generator properties}%
Some arise out of $\phi_1$~alone, some out of~$\phi_1$ in conjunction with~$\phi_2$,
and so on. The properties which arise out of $\phi_1$~alone form one
group; those which arise out of~$\phi_1\phi_2$ in conjunction form another
group, and so on. Since the number of generator properties is
finite, the number of groups also is finite. If a set of apparent
%% -----File: 265.png---Folio 254-------
properties arise (say) out of three generator properties~$\phi_1\phi_2\phi_3$,
\index{Generator properties!plurality of}%
then this set of properties may he said to specify the group~$\phi_1\phi_2\phi_3$.
Since the total number of apparent properties is assumed
to be greater than that of the generator properties, and since the
number of groups is finite, it follows that, if two sets of apparent
properties are taken, there is, in the absence of evidence to the
contrary, a finite probability that the second set will belong
to the group specified by the first set.

There is, however, the possibility of a plurality of generators.
The first set of apparent properties may specify more than one
group,---there is more than one group of generators, that is to
say, which are competent to produce it; and some only of these
groups may contain the second set of properties. Let us, for
the moment, rule out this possibility.

When we argue from an analogy, and the instances have
two groups of characters in common, namely $\phi$~and~$f$, either $f$~belongs
to the group~$\phi$ or it arises out of generators partly distinct
from those out of which $\phi$~arises. For the reason already explained
there is a finite probability that $f$~and~$\phi$ belong to the
same group. If this is the case, \ie\ if the generalisation~$g(\phi f)$
is valid, then $f$~will certainly be true of all other cases in which
$\phi$~is true; if this is not the case, then $f$~will not always be true
when $\phi$~is true. We have, therefore, the preliminary conditions
necessary for the application of pure induction. If $x_r$,~etc., are
the instances,
\begin{DPgather*}
g/h = p_0, \text{ where $p_0$ is finite},\\
x_r/gh = 1, \text{ etc.}, \\
\lintertext{and}
x_r/x_1x_2\ldots x_{r-1}\bar{g}h = 1 - \epsilon, \text{ where $\epsilon$ is finite}.
\end{DPgather*}
And hence, by the argument of \Chapref{XX}., the probability of a
generalisation, based on such evidence as this, is capable, under
suitable conditions, of tending towards certainty as a limit, when
the number of instances is increased.

If $\phi$~is complex and includes a number of characters which
are not always found together, it must include a number of
separate generator properties and specify a large group; hence
the initial probability that $f$~belongs to this group is relatively
large. If, on the other hand, $f$~is complex, there will be, for the
same reasons \textit{mutatis mutandis}, a relatively smaller initial probability
than otherwise that $f$~belongs to any other given group.
%% -----File: 266.png---Folio 255-------
\index{Uniformity of Nature, Law of}%

When the argument is mainly by analogy, we endeavour to
obtain evidence which makes the initial probability~$p_0$ relatively
high; when the analogy is weak and the argument depends for
its strength upon pure induction, $p_0$~is small and~$p_m$, which is
based upon numerous instances, depends for its magnitude upon
their number. But an argument from induction must always
involve some element of analogy, and, on the other hand, few
arguments from analogy can afford to ignore altogether the
strengthening influence of pure induction.

\Paragraph{4.} Let us consider the manner in which the methods of
analogy increase the initial likelihood that two characters belong
to the same group. The numerous characters of an object which
are known to us may be represented by $a_1a_2\ldots a_n$. We select
two sets of these, $a_r$~and~$a_s$, and seek to determine whether $a_s$~always
belongs to the group specified by~$a_r$. Our previous knowledge
will enable us, in general, to rule out many of the object's
characters as being irrelevant to the groups specified by $a_r$~and~$a_s$,
although this will not be possible in the most fundamental inquiries.
We may also know that certain characters are always
associated with $a_r$~or with~$a_s$. But there will be left a residuum
of whose connection with $a_r$~or~$a_s$ we are ignorant. These
characters, whose relevance is in doubt, may be represented by
$a_{r+1}\ldots a_{s-1}$. If the analogy is perfect, these characters are
eliminated altogether. Otherwise, the argument is weakened
in proportion to the comprehensiveness of these doubtful characters.
For it may be the case that some of $a_{r+1}\ldots a_{s-1}$ are
necessary as well as~$a_r$, in order to specify all the generators
which are required to produce~$a_s$.

\Paragraph{5.} We may possibly be justified in neglecting certain of the
characters $a_{r+1}\ldots a_{s-1}$ by \emph{direct} judgments of irrelevance.
\index{Irrelevance}%
There are certain properties of objects which we rule out from
the beginning as wholly or largely independent and irrelevant to
all, or to some, other properties. The principal judgments of
this kind, and those alone about which we seem to feel much
confidence, are concerned with absolute position in time and
\index{Time}%
space, this class of judgments of irrelevance being summed up,
\index{Space}%
I have suggested, in the Principle of the Uniformity of Nature.
We judge that \emph{mere} position in time and space cannot possibly
affect, as a determining cause, any other characters; and this
belief appears so strong and certain, although it is hard to see
%% -----File: 267.png---Folio 256-------
\index{Generator properties!plurality of}%
how it can be based on experience, that the judgment by which
we arrive at it seems perhaps to be direct. A further type of
instance in which some philosophers seem to have trusted direct
judgments of relevance in these matters arises out of the relation
between mind and matter. They have believed that no mental
event can possibly be a \emph{necessary} condition for the occurrence of
a material event.

The Principle of the Uniformity of Nature, as I interpret it,
supplies the answer, if it is correct, to the criticism that the
instances, on which generalisations are based, are all alike in
being past, and that any generalisation, which is applicable to
the future, must be based, for this reason, upon imperfect analogy.
We judge directly that the resemblance between instances, which
consists in their being past, is in itself irrelevant, and does not
supply a valid ground for impugning a generalisation.

But these judgments of irrelevance are not free from difficulty,
and we must be suspicious of using them. When I say that position
is irrelevant, I do not mean to deny that a generalisation, the
premiss of which specifies position, may be true, and that the
same generalisation without this limitation might be false. But
this is because the generalisation is incompletely stated; it
happens that objects so specified have the required characters,
and hence their position supplies a sufficient criterion. Position
may be relevant as a sufficient condition but never as a \emph{necessary}
condition, and the inclusion of it can only affect the truth of a
generalisation when we have left out some other essential condition.
A generalisation which is true of one instance must be
true of another which \emph{only} differs from the former by reason of
its position in time or space.

\Paragraph{6.} Excluding, therefore, the possibility of a plurality of
generators, we can justify the method of perfect analogy, and
other inductive methods in so far as they can be made to
approximate to this, by means of the assumption that the
objects in the field, over which our generalisations extend, do
not have an infinite number of independent qualities; that, in
other words, their characteristics, however numerous, cohere
together in groups of invariable connection, which are finite
in number. This does not limit the number of entities which
are only \emph{numerically} distinct. In the language used at the
beginning of this chapter, the use of inductive methods can be
%% -----File: 268.png---Folio 257-------
\index{Broad, C.~D.|inote}%
\index{Generator properties!plurality of}%
justified if they are applied to what we have reason to suppose
a finite system.\footnote
  {Mr.~C.~D. Broad, in two articles ``On the Relation between Induction and
  Probability'' (\textit{Mind}, 1918 and~1920), has been following a similar line of
  thought.}

\Paragraph{7.} Let us now take account of a possible plurality of
generators. I mean by this the possibility that a given character
can arise in more than one way, can belong to more than
one distinct group, and can arise out of more than one generator.
$\phi$~might, for instance, be sometimes due to a generator~$\DPtypo{a}{\alpha}_1$, and
$\DPtypo{a}{\alpha}_1$~might invariably produce~$f$. But we could not generalise
from $\phi$~to~$f$, if $\phi$~might be due in other cases to a different
generator~$\DPtypo{a}{\alpha}_2$ which would \emph{not} be competent to produce~$f$.

If we were dealing with inductive correlation, where we do
\index{Inductive correlation}%
not claim universality for our conclusions, it would be sufficient
for us to assume that the number of distinct generators, to which
a given property~$\phi$ can be due, is always finite. To obtain validity
for universal generalisations it seems necessary to make the more
comprehensive and less plausible assumption that a finite probability
always exists that there is \emph{not}, in any given case, a plurality
of causes. With this assumption we have a valid argument from
pure induction on the same lines, nearly, as before.

\Paragraph{8.} We have thus two distinct difficulties to deal with, and we
require for the solution of each a separate assumption. The
point may be illustrated by an example in which only one of the
difficulties is present. There are few arguments from analogy of
which we are better assured than the existence of other people.
We feel indeed so well assured of their existence that it has been
thought sometimes that our knowledge of them must be in some
way direct. But analogy does not seem to me unequal to the
proof. We have numerous experiences in our own person of
acts which are associated with states of consciousness, and we
infer that similar acts in others are likely to be associated with
similar states of consciousness. But this argument from analogy
is superior in one respect to nearly all other empirical arguments,
and this superiority may possibly explain the great confidence
which we feel in it. We do seem in this case to have
direct knowledge, such as we have in no other case, that our
states of consciousness are, sometimes at least, causally connected
with some of our acts. We do not, as in other cases,
%% -----File: 269.png---Folio 258-------
\index{Analogy, principle of!logical foundation of}%
\index{Inductive correlation}%
merely observe invariable sequence or coexistence between consciousness
and act; and we do believe it to be vastly improbable
in the case of some at least of our own physical acts that they
could have occurred without a mental act to support them.
Thus, we seem to have a special assurance of a kind not usually
available for believing that there is \emph{sometimes} a necessary connection
between the conclusion and the condition of the
generalisation; we doubt it only from the possibility of a
plurality of causes.

The objection to this argument on the ground that the analogy
is always imperfect, in that all the observed connections of
consciousness and act are alike in being \emph{mine}, seems to me to be
invalid on the same ground as that on which I have put on one
side objections to future generalisations, which are based on the
fact that the instances which support them are all alike in being
\emph{past}. If direct judgments of irrelevance are ever permissible,
there seems some ground for admitting one here.

\Paragraph{9.} As a logical foundation for Analogy, therefore, we seem to
need some such assumption as that the amount of variety in the
\index{Variety!limitation of}%
universe is limited in such a way that there is no one object so
complex that its qualities fall into an infinite number of independent
groups (\ie~groups which might exist independently
as well as in conjunction); or rather that none of the objects
about which we generalise are as complex as this; or at least
that, though some objects may be infinitely complex, we sometimes
have a finite probability that an object about which we
seek to generalise is not infinitely complex.

To meet a possible plurality of causes some further assumption
is necessary. If we were content with Inductive Correlations
and sought to prove merely that there was a probability in favour
of \emph{any} instance of the generalisation in question, without inquiring
whether there was a probability in favour of \emph{every} instance,
it would be sufficient to suppose that, while there may be more
than one sufficient cause of a character, there is not an infinite
number of distinct causes competent to produce it. And this
involves no new assumption; for if the aggregate variety of the
system is finite, the possible plurality of causes must also be finite.
If, however, our generalisation is to be universal, so that it breaks
down if there is a single exception to it, we must obtain, by some
means or other, a finite probability that the set of characters,
%% -----File: 270.png---Folio 259-------
\index{Measurement of Probability!induction@{and induction}}%
which condition the generalisation, are \emph{not} the possible effect of
more than one distinct set of fundamental properties. I do not
know upon what ground we could establish a finite probability
to this effect. The necessity for this seemingly arbitrary hypothesis
strongly suggests that our conclusions should be in the
form of inductive correlations, rather than of universal generalisations.
Perhaps our generalisations should always run: `It is
probable that any given~$\phi$ is~$f$,' rather than, `It is probable that
all~$\phi$ are~$f$.' Certainly, what we commonly seem to hold with conviction
is the belief that the sun will rise \emph{to-morrow}, rather than
the belief that the sun will \emph{always} rise so long as the conditions
explicitly known to us are fulfilled. This will be matter for
further discussion in \Partref{V}., when Inductive Correlation is
specifically dealt with.

\Paragraph{10.} There is a vagueness, it may be noticed, in the number of
instances, which would be required on the above assumptions
to establish a given numerical degree of probability, which
corresponds to the vagueness in the degree of probability which
we do actually attach to inductive conclusions. We assume
that the necessary number of instances is finite, but we do not
know what the number is. We know that the probability of a
well-established induction is great, but, when we are asked to
name its degree, we cannot. Common sense tells us that some
inductive arguments are stronger than others, and that some
are very strong. But how much stronger or how strong we
cannot express. The probability of an induction is only
numerically definite when we are able to make definite assumptions
about the number of independent equiprobable influences
at work. Otherwise, it is non-numerical, though bearing relations
of greater and less to numerical probabilities according to the
approximate limits within which our assumption as to the possible
number of these causes lies.

\Paragraph{11.} Up to this point I have supposed, for the sake of simplicity,
that it is necessary to make our assumptions as to the limitation
of independent variety in an absolute form, to assume, that is to
say, the finiteness of the system, to which the argument is applied,
\emph{for certain}. But we need not in fact go so far as this.

If our conclusion is~$C$ and our empirical evidence is~$E$, then,
in order to justify inductive methods, our premisses must include,
in addition to~$E$, a general hypothesis~$H$ such that~$C/H$, the
%% -----File: 271.png---Folio 260-------
\textit{à~priori} probability of our conclusion, has a finite value. The
effect of~$E$ is to increase the probability of~$C$ above its initial
\textit{à~priori} value, $C/HE$~being greater than~$C/H$. But the method
of strengthening~$C/H$ by the addition of evidence~$E$ is valid quite
apart from the particular content of~$H$. If, therefore, we have
another general hypothesis~$H'$ and other evidence~$E'$, such that
$H/H'$ has a finite value, we can, without being guilty of a circular
argument, use evidence~$E'$ by the same method as before to
strengthen the probability~$H/H'$. If we call~$H$, namely, the
absolute assertion of the finiteness of the system under consideration,
the \emph{inductive hypothesis}, and the process of strengthening~$C/H$
\index{Inductive hypothesis}%
by the addition~$E$ the \emph{inductive method}, it is not circular to
\index{Inductive method}%
use the inductive method to strengthen the inductive hypothesis
itself, relative to some more primitive and less far-reaching assumption.
If, therefore, we have any reason~($H'$) for attributing
\textit{à~priori} a finite probability to the Inductive Hypothesis~($H$), then
the actual conformity of experience \textit{à~posteriori} with expectations
based on the assumption of~$H$ can be utilised by the inductive
method to attribute an enhanced value to the probability of~$H$.
To this extent, therefore, we can support the Inductive Hypothesis
by experience. In dealing with any particular question we can
take the Inductive Hypothesis, not at its \textit{à~priori} value, but at
the value to which experience in general has raised it. What
we require \textit{à~priori}, therefore, is not the certainty of the Inductive
Hypothesis, but a finite probability in its favour.\footnote
  {I have implicitly assumed in the above argument that if $H'$~supports~$H$, it
  strengthens an argument which $H$ would strengthen. This is not \emph{necessarily}
  the case for the reasons given on pp.\ \Pageref[]{68}~and~\Pageref[]{147}. In these passages the
  necessary conditions for the above are elucidated. I am, therefore, assuming
  that in the case now in question these conditions actually are fulfilled.}

Our assumption, in its most limited form, then, amounts to
this, that we have a finite \textit{à~priori} probability in favour of
the Inductive Hypothesis as to there being some limitation
of independent variety (to express shortly what I have already
\index{Variety!limitation of}%
explained in detail) in the objects of our generalisation. Our
experience might have been such as to diminish this probability
\textit{à~posteriori}. It has, in fact, been such as to increase it. It is
because there has been so much repetition and uniformity in our
experience that we place great confidence in it. To this extent
the popular opinion that Induction depends upon experience for
its validity is justified and does not involve a circular argument.
%% -----File: 272.png---Folio 261-------

\Paragraph{12.} I think that this assumption is adequate to its purpose
and would justify our ordinary methods of procedure in inductive
argument. It was suggested in the previous chapter that our
theory of Analogy ought to be as applicable to mathematical
as to material generalisations, if it is to justify common sense.
The above assumptions of the limitation of independent variety
sufficiently satisfy this condition. There is nothing in these
assumptions which gives them a peculiar reference to material
objects. We believe, in fact, that all the properties of numbers
can be derived from a \emph{limited} number of laws, and that the same
set of laws governs all numbers. To apply empirical methods to
such things as numbers renders it necessary, it is true, to make
an assumption about the nature of numbers. But it is the same
kind of assumption as we have to make about material objects,
and has just about as much, or as little, plausibility. There is
no new difficulty.

The assumption, also, that the system of Nature is finite is
in accordance with the analysis of the underlying assumption of
scientists, given at the close of the previous chapter. The
hypothesis of atomic uniformity, as I have called it, while not
formally equivalent to the hypothesis of the limitation of independent
variety, amounts to very much the same thing. If the
fundamental laws of connection changed altogether with variations,
for instance, in the shape or size of bodies, or if the laws
governing the behaviour of a complex had no relation whatever
to the laws governing the behaviour of its parts when belonging
to other complexes, there could hardly be a limitation of independent
variety in the sense in which this has been defined. And,
on the other hand, a limitation of independent variety seems
necessarily to carry with it some degree of atomic uniformity.
The underlying conception as to the character of the System of
Nature is in each case the same.

\Paragraph{13.} We have now reached the last and most difficult stage of
the discussion. The logical part of our inquiry is complete, and
it has left us, as it is its business to leave us, with a question of
epistemology. Such is the premiss or assumption which our
\index{Epistemology!inductive hypothesis@{and inductive hypothesis}}%
logical processes need to work upon. What right have we to
make it? It is no sufficient answer in philosophy to plead that
the assumption is after all a very little one.

I do not believe that any conclusive or perfectly satisfactory
%% -----File: 273.png---Folio 262-------
answer to this question can be given, so long as our knowledge
\index{Knowledge!direct and indirect}%
of the subject of epistemology is in so disordered and undeveloped
a condition as it is in at present. No proper answer has yet been
given to the inquiry---of what sorts of things are we capable of
direct knowledge? The logician, therefore, is in a weak position,
when he leaves his own subject and attempts to solve a particular
instance of this general problem. He needs guidance as to what
\emph{kind} of reason we could have for such an assumption as the use
of inductive argument appears to require.

On the one hand, the assumption may be absolutely \textit{à~priori}
in the sense that it would be equally applicable to all possible
objects. On the other hand, it may be seen to be applicable to
some classes of objects only. In this Case it can only arise out
of some degree of particular knowledge as to the nature of the
objects in question, and is to this extent dependent on experience.
But if it is experience which in this sense enables us to know the
assumption as true of certain amongst the objects of experience,
it must enable us to know it in some manner which we may term
direct and not as the result of an inference.

Now an assumption, that \emph{all} systems of fact are finite (in the
sense in which I have defined this term), cannot, it seems perfectly
plain, be regarded as having absolute, universal validity in the
sense that such an assumption is self-evidently applicable to every
kind of object and to all possible experiences. It is not, therefore,
in quite the same position as a self-evident \emph{logical} axiom, and does
not appeal to the mind in the same way. The most which can
be maintained is that this assumption is true of \emph{some} systems of
fact, and, further, that there are some objects about which, as
soon as we understand their nature, the mind is able to apprehend
directly that the assumption in question \emph{is} true.

In \Chapref{II}. §\;7, I wrote: ``By some mental process of
which it is difficult to give an account, we are able to pass from
direct acquaintance with things to a knowledge of propositions
about the things of which we have sensations or understand the
meaning.'' Knowledge, so obtained, I termed direct knowledge.
From a sensation of yellow and from an understanding of the
meaning of `yellow' and of `colour,' we could, I suggested,
have direct knowledge of the fact or proposition `yellow is a
colour;' we might also know that colour cannot exist without
extension, or that two colours cannot be perceived at the same
%% -----File: 274.png---Folio 263-------
\index{Causality}%
\index{Proposition, characterisation of!synthetic}%
\index{Uniformity of Nature, Law of}%
time in the same place. Other philosophers might use terms
differently and express themselves otherwise; but the substance
of what I was there trying to say is not very disputable. But
when we come to the question as to what kinds of propositions
we can come to know in this manner, we enter upon an unexplored
field where no certain opinion is discoverable.

In the case of logical terms, it seems to be generally agreed
that if we understand their meaning we can know directly propositions
about them which go far beyond a mere expression of
this meaning;---propositions of the kind which some philosophers
have termed \emph{synthetic}. In the case of non-logical or
empirical entities, it seems sometimes to be assumed that our
direct knowledge must be confined to what may be regarded as
an expression or description of the meaning or sensation apprehended
by us. If this view is correct the Inductive Hypothesis
is not the kind of thing about which we can have direct knowledge
as a result of our acquaintance with objects.

I suggest, however, that this view is incorrect, and that we
are capable of direct knowledge about empirical entities which
goes beyond a mere expression of our understanding or sensation
of them. It may be useful to give the reader two examples, more
familiar than the Inductive Hypothesis, where, as it appears to
me, such knowledge is commonly assumed. The first is that of the
causal irrelevance of mere position in time and space, commonly
called the Uniformity of Nature. We do believe, and yet have
no adequate inductive reason whatever for believing, that mere
position in time and space cannot make any difference. This
belief arises directly, I think, out of our acquaintance with
the objects of experience and our understanding of the concepts
of `time' and `space.' The second is that of the Law of
Causation. We believe that every object in time has a `necessary'
connection\footnote
  {I do not propose to define the meaning of this.}
with some set of objects at a previous time.
This belief also, I think, arises in the same way. It is to be
noticed that neither of these beliefs clearly arises, in spite of the
directness which may be claimed for them, out of any one single
experience. In a way analogous to these, the validity of assuming
the Inductive Hypothesis, as applied to a particular class of
objects, appears to me to be justified.

Our justification for using inductive methods in an argument
%% -----File: 275.png---Folio 264-------
about numbers arises out of our perceiving directly, when we
understand the meaning of a number, that they are of the required
character.\footnote
  {Since numbers are logical entities, it may be thought less unorthodox to
  make such an assumption in their case.}
And when we perceive the nature of our
phenomenal experiences, we have a direct assurance that in their
case also the assumption is legitimate. We are capable, that
is to say, of direct synthetic knowledge about the nature
of the objects of our experience. On the other hand, there
may be some kinds of objects, about which we have no such
assurance and to which inductive methods are not reasonably
applicable. It may be the case that some metaphysical questions
are of this character and that those philosophers have been right
who have refused to apply empirical methods to them.

\Paragraph{14.} I do not pretend that I have given any perfectly adequate
reason for accepting the theory I have expounded, or any such
theory. The Inductive Hypothesis stands in a peculiar position
\index{Inductive hypothesis}%
in that it seems to be neither a self-evident logical axiom nor an
object of direct acquaintance; and yet it is just as difficult, as
though the inductive hypothesis were either of these, to remove
from the organon of thought the inductive method which can
only be based on it or on something like it.

As long as the theory of knowledge is so imperfectly
understood as now, and leaves us so uncertain about the grounds
of many of our firmest convictions, it would be absurd to
confess to a special scepticism about this one. I do not think
that the foregoing argument has disclosed a reason for such
scepticism. We need not lay aside the belief that this conviction
gets its invincible certainty from some valid principle darkly
present to our minds, even though it still eludes the peering
eyes of philosophy.
%% -----File: 276.png---Folio 265-------
\index{Bacon|ifoll}%
\index{Ellis, Leslie!Bacon@{and Bacon}|inote}%
\index{Mill, and inductive correlations!induction@{and induction}|ifoll}%
\index{Newton, and induction!Bacon@{and Bacon}}%
\index{Spedding and Ellis and Bacon|inote}%


\Chapter{XXIII}{Some Historical Notes on Induction}

\Paragraph{1.} \First{The} number of books, which deal with inductive\footnote
  {See note at the end of this chapter on ``The Use of the Term \emph{Induction}.''}
theory, is
extraordinarily small. It is usual to associate the subject with
the names of Bacon, Hume, and Mill. In spite of the modern
\index{Hume!Induction@{and Induction}}%
tendency to depreciate the first and the last of these, they are the
principal names, I think, with which the history of induction
ought to be associated. The next place is held by Laplace and
\index{Laplace!Induction@{and Induction}}%
Jevons. Amongst contemporary logicians there is an almost
\index{Jevons!Induction@{and Induction}}%
complete absence of constructive theory, and they content
themselves for the most part with the easy task of criticising
Mill, or with the more difficult one of following him.

That the inductive theories of Bacon and of Mill are full of
errors and even of absurdities, is, of course, a commonplace of
criticism. But when we ignore details, it becomes clear that they
were really attempting to disentangle the essential issues. We
depreciate them partly, perhaps, as a reaction from the view once
held that they helped the progress of scientific discovery. For
it is not plausible to suppose that Newton owed anything to Bacon,
or Darwin to Mill. But with the logical problem their minds
\index{Darwin!Mill@{and Mill}}%
were truly occupied, and in the history of logical theory they
should always be important.

It is true, nevertheless, that the advancement of science was
the main object which Bacon himself, though not Mill, believed
that his philosophy would promote. The \textit{Great Instauration} was
intended to promulgate an actual method of discovery entirely
different from any which had been previously known.\footnote
  {He speaks of himself as being ``in hac re plane protopirus, et vestigia
  nullius sequutus''; and in the \textit{Praefatio Generalis} he compares his method to
  the mariner's compass, until the discovery of which no wide sea could be
  crossed (see Spedding and Ellis, vol.~i.\ p.~24).}
It did
%% -----File: 277.png---Folio 266-------
\index{Ellis, Leslie!Bacon@{and Bacon}|inote}%
\index{Macaulay and Bacon}%
\index{Spedding and Ellis and Bacon|inote}%
not do this, and against such pretensions Macaulay's well-known
essay was not unjustly directed. Mill, however, expressly disclaimed
in his preface any other object than to classify and
generalise the practices ``conformed to by accurate thinkers in
their scientific inquiries.'' Whereas Bacon offered rules and
demonstrations, hitherto unknown, with which any man could
solve all the problems of science by taking pains, Mill admitted
that ``in the existing state of the cultivation of the sciences,
there would be a very strong presumption against any one
who should imagine that he had effected a revolution in the
theory of the investigation of truth, or added any fundamentally
new process to the practice of it.''

\Paragraph{2.} The theories of both seem to me to have been injured,
though in different degrees, by a failure to keep quite distinct
the three objects: (1)~of helping the scientist, (2)~of explaining
and analysing his practice, and (3)~of justifying it. Bacon was
really interested in the second as well as in the first, and was
led to some of his methods by reflecting upon what distinguished
good arguments from bad in actual investigations. To logicians
his methods were as new as he claimed, but they had their
origin, nevertheless, in the commonest inferences of science and
daily life. But his main preoccupation was with the first, which
did injury to his treatment of the third. He himself became
aware as the work progressed that, in his anxiety to provide
an infallible mode of discovery, he had put forth more than he
would ever be able to justify.\footnote
  {This view is taken in the edition of James Spedding and Leslie Ellis.
  Their introductions to Bacon's philosophical works seem to me to be very greatly
  superior to the accounts to be found elsewhere. They make intelligible, what
  seems, according to other commentaries, fanciful and without sense or reason.}
His own mind grew doubtful,
and the most critical parts of the description of the new method
were never written. No one who has reflected much upon Induction
need find it difficult to understand the progress and
development of Bacon's thoughts. To the philosopher who first
distinguished some of the complexities of empirical proof in a
generalised, and not merely a particular, form, the prospects of
systematising these methods must have seemed extraordinarily
hopeful. The first investigator could not have anticipated that
Induction, in spite of its apparent certainty, would prove so
elusive to analysis.

Mill also was led, in a not dissimilar way, to attempt a too
%% -----File: 278.png---Folio 267-------
\index{Mill, and inductive correlations!plurality of causes@{and plurality of causes}|inote}%
\index{Plurality of causes and Mill}%
simple treatment, and, in seeking for ease and certainty, to
\index{Certainty!Bacon@{and Bacon}}%
treat far too lightly the problem of justifying what he had
claimed. Mill shirks, almost openly, the difficulties; and scarcely
attempts to disguise from himself or his readers that he grounds
induction upon a circular argument.

\Paragraph{3.} Some of the most characteristic errors both of Bacon and
of Mill arise, I think, out of a misapprehension, which it has been
a principal object of this book to correct. Both believed, without
hesitation it seems, that induction is capable of establishing a
conclusion which is absolutely certain, and that an argument
is invalid if the generalisation, which it supports, admits of
exceptions in fact. ``Absolute certainty,'' says Leslie Ellis,\footnote
  {\textit{Op.~cit.}\ vol.~i.\ p.~23.} ``is
one of the distinguishing characters of the Baconian induction.''
It was, in this respect, mainly that it improved upon the older
induction \textit{per enumerationem simplicem}. ``The induction which
the logicians speak of,'' Bacon argues in the \textit{Advancement of
Learning}, ``is utterly vicious and incompetent\ldots. For to conclude
upon an enumeration of particulars, without instance
contradictory, is no conclusion but a conjecture.'' The conclusions
of the new method, unlike those of the old, are not liable to be
upset by further experience. In the attempt to justify these
claims and to obtain demonstrative methods, it was necessary
to introduce assumptions for which there was no warrant.

Precisely similar claims were made by Mill, although there
are passages in which he abates them,\footnote
  {When he deals with Plurality of Causes, for instance.}
for his own rules of procedure.
An induction has no validity, according to him as
according to Bacon, unless it is absolutely certain. The following
passage\footnote
  {Bk.~iii.\ chap.~iii.~3 (the italics are mine).}
is significant of the spirit in which the subject
was approached by him: ``Let us compare a few cases
of incorrect inductions with others which are acknowledged
to be legitimate. Some, we know, which were believed for
centuries to be correct, were nevertheless incorrect. \emph{That all
swans are white, cannot have been a good induction, since the
conclusion has turned out erroneous.} The experience, however, on
which the conclusion rested was genuine.'' Mill has not justly
apprehended the relativity of all inductive arguments to the
evidence, nor the element of uncertainty which is present, more
%% -----File: 279.png---Folio 268-------
\index{Analogy, principle of!Bacon@{and Bacon}}%
\index{Mill, and inductive correlations!probability@{and probability}|inote}%
or less, in all the generalisations which they support.\footnote
  {This misapprehension may be connected with Mill's complete failure to
  grasp with any kind of thoroughness the nature and importance of the theory of
  probability. The treatment of this topic in the \textit{System of Logic} is exceedingly
  bad. His understanding of the subject was, indeed, markedly inferior to the
  best thought of his own time.}
Mill's
methods would yield certainty, if they were correct, just as
Bacon's would. It is the necessity, to which Mill had subjected
himself, of obtaining certainty that occasions their want of
reality. Bacon and Mill both assume that experiment can
shape and analyse the evidence in a manner and to an extent
which is not in fact possible. In the aims and expectations with
which they attempt to solve the inductive problem, there is on
fundamental points an unexpectedly close resemblance \DPtypo{beween}{between}
them.

\Paragraph{4.} Turning from these general criticisms to points of greater
detail, we find that the line of thought pursued by Mill was
essentially the same as that which had been pursued by Bacon,
and, also, that the argument of the preceding chapters is, in
spite of some real differences, a development of the same fundamental
ideas which underlie, as it seems to me, the theories of
Mill and Bacon alike.

We have seen that all empirical arguments require an initial
probability derived from analogy, and that this initial probability
may be raised towards certainty by means of pure induction
or the multiplication of instances. In some arguments we depend
mainly upon analogy, and the initial probability obtained by
means of it (with the assistance, as a rule, of previous knowledge)
is so large that numerous instances are not required. In other
arguments pure induction predominates. As science advances
and the body of pre-existing knowledge is increased, we depend
increasingly upon analogy; and only at the earlier stages of our
investigations is it necessary to rely, for the greater part of our
support, upon the multiplication of instances. Bacon's great
achievement, in the history of logical theory, lay in his being the
first logician to recognise the importance of methodical analogy
to scientific argument and the dependence upon it of most well-established
conclusions. The \textit{Novum Organum} is mainly concerned
with explaining methodical ways of increasing what I
have termed the Positive and Negative Analogies, and of avoiding
false Analogies. The use of exclusions and rejections, to which
%% -----File: 280.png---Folio 269-------
\index{Ellis, Leslie!Bacon@{and Bacon}|inote}%
\index{Mill, and inductive correlations!pure induction@{and pure induction}}%
Bacon attached supreme importance, and which he held to constitute
\index{Bacon!tables of}%
the essential superiority of his method over those which
preceded it, entirely consists in the determination of what characters
(or natures as he would call them) belong to the positive
and negative analogies respectively. The first two tables with
which the investigation begins are, first, the table \textit{essentiae et
praesentiae}, which contains all known instances in which the
given nature is present, and, second, the table \textit{declinationis sive
absentiae in proximo}, which contains instances corresponding in
each case to those of the first table, but in which, notwithstanding
this correspondence, the given nature is absent.\footnote
  {Ellis, vol.~i.\ p.~33.}
The doctrine
of prerogative instances is concerned no less plainly with the
methodical determination of Analogy. And the doctrine of
idols is expounded for the avoidance of \emph{false} analogies, standing,
he says, in the same relation to the interpretation of Nature, as
the doctrine of fallacies to ordinary logic.\footnote
  {Ellis, vol.~i.\ p.~89.}
Bacon's error lay
in supposing that, because these methods were new to logic, they
were therefore new to practice. He exaggerated also their precision
and their certainty; and he underestimated the importance
of pure induction. But there was, at bottom, nothing about
his rules impracticable or fantastic, or indeed unusual.

\Paragraph{5.} Almost the whole of the preceding paragraph is equally
applicable to Mill. He agreed with Bacon in depreciating the
part played in scientific inquiry by pure induction, and in
emphasising the importance of analogy to all systematic investigators.
But he saw further than Bacon in allowing for the
Plurality of Causes, and in admitting that an element of pure
induction was therefore made necessary. ``The Plurality of
Causes,'' he says,\footnote
  {Book~iv.\ chap.~x.~2.}
``is the only reason why mere number of instances
is of any importance in inductive inquiry. The tendency
of unscientific inquirers is to rely too much on number, without
analysing the instances\ldots. Most people hold their conclusions
with a degree of assurance proportioned to the mere \emph{mass} of the
experience on which they appear to rest; not considering that
by the addition of instances to instances, all of the same kind,
that is, differing from one another only in points already recognised
as immaterial, nothing whatever is added to the evidence of
%% -----File: 281.png---Folio 270-------
\index{Mill, and inductive correlations!methods of}%
\index{Uniformity of Nature, Law of!Mill@{and Mill}}%
the conclusion. A single instance eliminating some antecedent
which existed in all the other cases, is of more value than the
greatest multitude of instances which are reckoned by their
number alone.'' Mill did not see, however, that our knowledge
of the instances is seldom complete, and that new instances, which
are not known to differ from the former in material respects, may
add, nevertheless, to the negative analogy, and that the multiplication
of them may, for this reason, strengthen the evidence.
It is easy to see that his methods of Agreement and Difference
closely resemble Bacon's, and aim, like Bacon's, at the determination
\index{Bacon!limited variety@{and limited variety}}%
of the Positive and Negative Analogies. By allowing
for Plurality of Causes Mill advanced beyond Bacon. But he
was pursuing the same line of thought which alike led to Bacon's
rules and has been developed in the chapters of this book.
Like Bacon, however, he exaggerated the precision with which
his canons of inquiry could be used in practice.

\Paragraph{6.} No more need be said respecting method and analysis.
But in both writers the exposition of method is closely intermingled
with attempts to justify it. There is nothing in Bacon
which at all corresponds to Mill's appeals to Causation or to the
Uniformity of Nature, and, when they seek for the ground of
induction, there is much that is peculiar to each writer. It is
my purpose, however, to consider in this place the details common
to both, which seem to me to be important and which exemplify
the only line of investigation which seems likely to be fruitful;
and I shall pursue no further, therefore, their numerous points
of difference.

The attempt, which I have made to justify the initial probability
which Analogy seems to supply, primarily depends upon
a certain limitation of independent variety and upon the derivation
of all the properties of any given object from a limited
number of primary characters. In the same way I have supposed
that the number of primary characters which are capable of
producing a given property is also limited. And I have argued
that it is not easy to see how a finite probability is to be obtained
unless we have in each case some such limitation in the number
of the ultimate alternatives.

It was in a manner which bears fundamental resemblances
to this that Bacon endeavoured to demonstrate the cogency of
his method. He considers, he says, ``the simple forms or difference
%% -----File: 282.png---Folio 271-------
\index{Mill, and inductive correlations!limited variety@{and limited variety}}%
of things which are few in number, and the degrees and
co-ordinations whereof make all this variety,'' And in \textit{Valerius
Terminus} he argues ``that every particular that worketh any
effect is a thing compounded more or less of diverse single natures,
more manifest and more obscure, and that it appeareth not to
which of the natures the effect is to be ascribed.''\footnote
  {Quoted by Ellis, vol.~i.\ p.~41.\index{Ellis, Leslie!Bacon@{and Bacon}|inote}}
It is indeed
essential to the method of exclusions that the matter to which it
is applied should be somehow resolvable into a finite number of
elements. But this assumption is not peculiar, I think, to
Bacon's method, and is involved, in some form or other, in every
argument from Analogy. In making it Bacon was initiating,
perhaps obscurely, the modern conception of a finite number of
laws of nature out of the combinations of which the almost boundless
variety of experience ultimately arises. Bacon's error was
double and lay in supposing, first, that these distinct elements
lie upon the surface and consist in visible characters, and second,
that their natures are, or easily can be, known to us, although
the part of the \textit{Instauration}, in which the manner of conceiving
simple natures was to be explained, he never wrote. These
beliefs falsely simplified the problem as he saw it, and led him
to exaggerate the ease, certainty, and fruitfulness of the new
method. But the view that it is possible to reduce all the
phenomena of the universe to combinations of a limited number
of simple elements---which is, according to Ellis,\footnote
  {Vol.~i.\ p.~28.}
the central
point of Bacon's whole system---was a real contribution to philosophy.

\Paragraph{7.} The assumption that every event can be analysed into a
limited number of ultimate elements, is never, so far as I am
aware, explicitly avowed by Mill. But he makes it in almost
every chapter, and it underlies, throughout, his mode of procedure.
His methods and arguments would fail immediately, if we were
to suppose that phenomena of infinite complexity, due to an
infinite number of independent elements, were in question, or
if an infinite plurality of causes had to be allowed for.

In distinguishing, therefore, analogy from pure induction,
and in justifying it by the assumption of a \emph{limited} complexity in
the problems which we investigate, I am, I think, pursuing, with
numerous differences, the line of thought which Bacon first
%% -----File: 283.png---Folio 272-------
\index{Analogy, principle of!Leibniz@{and Leibniz}}%
\index{Couturat|inote}%
pursued and which Mill popularised. The method of treatment
is dissimilar, but the subject-matter and the underlying beliefs
are, in each case, the same.

\Paragraph{8.} Between Bacon and Mill came Hume. Hume's sceptical
\index{Hume!Induction@{and Induction}}%
criticisms are usually associated with causality; but argument
by induction---inference from past particulars to future generalisations---was
the real object of his attack. Hume showed, not that
inductive methods were false, but that their validity had never
been established and that all possible lines of proof seemed
equally unpromising. The \emph{full} force of Hume's attack and the
nature of the difficulties which it brought to light were never
appreciated by Mill, and he makes no adequate attempt to
deal with them. Hume's statement of the case against induction
has never been improved upon; and the successive attempts
of philosophers, led by Kant, to discover a transcendental solution
\index{Kant!Hume@{and Hume}}%
have prevented them from meeting the hostile arguments on
their own ground and from finding a solution along lines which
might, conceivably, have satisfied Hume himself.

\Paragraph{9.} It would not be just here to pass by entirely the name
of the great Leibniz, who, wiser in correspondence and fragmentary
\index{Leibniz!Induction@{and Induction}}%
projects than in completed discourses, has left to us
sufficient indications that his private reflections on this subject
were much in advance of his contemporaries'. He distinguished
three degrees of conviction amongst opinions, logical certainty
\index{Certainty!Leibniz@{and Leibniz}}%
(or, as we should say, propositions known to be formally true),
physical certainty which is only logical probability, of which a
well-established induction, as that man is a biped, is the type,
and physical probability (or, as we should say, an inductive
correlation), as for example that the south is a rainy quarter.\footnote
  {Couturat, \textit{Opuscules et fragments inédits de Leibniz}, p.~232.}
He condemned generalisations based on mere repetition of
instances, which he declared to be without logical value, and he
insisted on the importance of \emph{Analogy} as the basis of a valid
induction.\footnote
  {Couturat, \textit{La Logique de Leibniz d'après des documents inédits}, pp\DPtypo{}{.}~262,~267.}
He regarded a hypothesis as more probable in
proportion to its \emph{simplicity} and its \emph{power}, that is to say, to the
number of the phenomena it would explain and the fewness of
the assumptions it involved. In particular a power of accurate
prediction and of explaining phenomena or experiments previously
%% -----File: 284.png---Folio 273-------
\index{Analogy, principle of!Jevons@{and Jevons}}%
untried is a just ground of secure confidence, of which
he cites as a nearly perfect example the key to a cryptogram.\footnote
  {Letter to Conring, 19th~March 1678.}

\Paragraph{10.} Whewell and Jevons furnished logicians with a storehouse
\index{Jevons!Induction@{and Induction}}%
of examples derived from the practice of scientists.
Jevons, partly anticipated by Laplace, made an important
\index{Laplace!Induction@{and Induction}}%
advance when he emphasised the close relation between
Induction and Probability. Combining insight and error, he
spoilt brilliant suggestions by erratic and atrocious arguments.
His application of Inverse Probability to the inductive problem
is crude and fallacious, but the idea which underlies it is
substantially good. He, too, made explicit the element of
Analogy, which Mill, though he constantly employed it, had
seldom called by its right name. There are few books, so
superficial in argument yet suggesting so much truth, as Jevons's
\textit{Principles of Science}.

\Paragraph{11.} Modern text-books on Logic all contain their chapters on
Induction, but contribute little to the subject. Their recognition
of Mill's inadequacy renders their exposition, which, in spite
of criticisms, is generally along his lines, nerveless and confused.
Where Mill is clear and offers a solution, they, confusedly
criticising, must withhold one. The best of them, Sigwart and
\index{Sigwart!induction@{and induction}}%
Venn, contain criticism and discussion which is interesting, but
\index{Venn!induction@{and induction}}%
constructive theory is lacking. Hitherto Hume has been master,
only to be refuted in the manner of Diogenes or Dr.~Johnson.
%% -----File: 285.png---Folio 274-------


%[** TN: Omitting italic smallcaps "Induction"]
\Notes{i}{Notes on Part III}{On the Use of the Term Induction}
\index{Induction@{`\textit{Induction}'}}%

\Paragraph{1.} \First{Induction} is in origin a translation of the Aristotelian \textgreek{>epagwg'h}.
This term was used by Aristotle in two quite distinct senses---first,
\index{Aristotle!induction@{and induction}}%
and principally, for the process by which the observation of particular
instances, in which an abstract notion is exemplified, enables us to
realise and comprehend the abstraction itself; secondly, for the type
of argument in which we generalise after the complete enumeration
and assertion of \emph{all} the particulars which the generalisation embraces.
From this second sense it was sometimes extended to cases in which
we generalise after an \emph{incomplete} enumeration. In post-Aristotelian
writers the induction \textit{per enumerationem simplicem} approximates to
induction in Aristotle's second sense, as the number of instances is
increased. To Bacon, therefore, ``the induction of which the logicians
speak'' meant a method of argument by multiplication of instances.
He himself deliberately extended the use of the term so as to cover
all the systematic processes of empirical generalisation. But he
also used it, in a manner closely corresponding to Aristotle's \emph{first} use,
for the process of forming scientific conceptions and correct notions
of  ``simple natures.''\footnote
  {See Ellis's edition of Bacon's \textit{Works}, vol.~i.\ p.~37. On the first occasion
  \index{Ellis, Leslie!Bacon@{and Bacon}|inote}%
  on which Induction is mentioned in the \textit{Novum Organum}, it is used in this
  secondary sense.}

\Paragraph{2.} The modern use of the term is derived from Bacon's. Mill
defines it as ``the operation of discovering and proving general
propositions.'' His philosophical system required that he should
define it as widely as this; but the term has really been used, both
by him and by other logicians, in a narrower sense, so as to cover
those methods of proving general propositions, which we call empirical,
and so as to exclude generalisations, such as those of mathematics,
which have been proved formally. Jevons was led, partly by the
\index{Jevons!Induction@{and Induction}}%
linguistic resemblance, partly because in the one case we proceed
from the particular to the general and in the other from the general
to the particular, to define Induction as the inverse process of
Deduction. In contemporary logic Mill's use prevails; but there
%% -----File: 286.png---Folio 275-------
\index{Cause@{`\textit{Cause}'}}%
\index{Cournot, and frequency theory!causality@{and causality}}%
is, at the same time, a suggestion---arising from earlier usage, and
because Bacon and Mill never quite freed themselves from it---of
argument by mere multiplication of instances. I have thought it
best, therefore, to use the term \emph{pure induction} to describe arguments
which are based upon the \emph{number} of instances, and to use \emph{induction}
itself for all those types of arguments which combine, in one form or
another, pure induction with analogy.\\


%[** TN: Omitting italic smallcaps "Cause"]
\NoteSec{ii}{On the Use of the Term Cause}

\Pagelabel{275}%
\Paragraph{1.} Throughout the preceding argument, as well as in \Partref{II}.,
I have been able to avoid the metaphysical difficulties which surround
the true meaning of \emph{cause}. It was not necessary that I should
inquire whether I meant by \emph{causal} connection an invariable connection
in fact merely, or whether some more intimate relation was
involved. It has also been convenient to speak of causal relations
between objects which do not strictly stand in the position of cause
and effect, and even to speak of \emph{a probable cause}, where there is no
implication of necessity and where the antecedents will sometimes
lead to particular consequents and sometimes will not. In making
this use of the term, I have followed a practice not uncommon amongst
writers on probability, who constantly use the term \emph{cause}, where
\emph{hypothesis} might seem more appropriate.\footnote
  {Cf.\ Czuber, \textit{Wahrscheinlichkeitsrechnung}, p.~139. In dealing with Inverse
\index{Czuber!cause@{and `\textit{cause}'}|inote}%
  Probability Czuber explains that he means by \emph{possible cause} the various \textit{Bedingungskomplexe}
  from which the cause \emph{can} result.}

One is led, almost inevitably, to use `cause' more widely than
`sufficient cause' or than `necessary cause,' because, the necessary
causation of particulars by particulars being rarely apparent to us,
the strict sense of the term has little utility. Those antecedent
circumstances, which we are usually content to accept as causes, are
only so in strictness under a favourable conjunction of innumerable
other influences.

\Paragraph{2.} As our knowledge is partial, there is constantly, in our use
of the term \emph{cause}, some reference implied or expressed to a limited
body of knowledge. It is clear that, whether or not, as Cournot\footnote
  {See \Chapref{XXIV}. §\;3.}
maintains, there are such things as independent series in the order
of causation, there is often a sense in which we may hold that there
is a closer intimacy between some series than between others. This
intimacy is relative, I think, to particular information, which is
actually known to us, or which is within our reach. It will be useful,
therefore, to give precise definitions of these wider senses in which
it is often convenient to use the expression \emph{cause}.
%% -----File: 287.png---Folio 276-------
\index{Causality}%
\index{Kries, von!knowledge@{and knowledge}}%
\index{Proposition, characterisation of!existential}%
\index{Uniformity of Nature, Law of}%

We must first distinguish between assertions of law and assertions
of fact, or, in the terminology of Von~Kries,\footnote
  {\textit{Die Principien der Wahrscheinlichkeitsrechnung}, p.~86.}
between nomologic and
ontologic knowledge. It may be convenient in dealing with some
\index{Knowledge!homologic and ontologic}%
questions to frame this distinction with reference to the special
circumstances. But the distinction generally applicable is between
propositions which contain no reference to \emph{particular} moments of
time, and existential propositions which cannot be stated without
reference to specific points in the time series. The Principle of the
Uniformity of Nature amounts to the assertion that natural laws
are all, in this sense, timeless. We may, therefore, divide our \textit{data}
into two portions $k$~and~$l$, such that $k$~denotes our formal and
nomologic evidence, consisting of propositions whose predication
does not involve a particular time reference, and $l$~denotes the
existential or ontologic propositions.

\Paragraph{3.} Let us now suppose that we are investigating two existential
propositions $a$~and~$b$, which refer two events $A$~and~$B$ to particular
moments of time, and that $A$~is referred to moments which are all
prior to those at which $B$~occurred. What various meanings can we
give to the assertion that $A$~and~$B$ are \emph{causally connected}?

(i.) If $b/ak=1$, $A$~is a sufficient cause of~$B$. In this case $A$~is a
cause of~$B$ in the strictest sense. $b$~can be \emph{inferred} from~$a$, and no
additional knowledge consistent with~$k$ can invalidate this.

(ii.) If $b/\bar{a}k=0$, $A$~is a necessary cause of~$B$.

(iii.) If $k$~includes all the laws of the existent universe, then $A$~is
\emph{not} a sufficient cause of~$B$ unless $b/ak=1$. The Law of Causation,
therefore, which states that every existent has to some other previous
existent the relation of effect to sufficient cause, is equivalent to the
proposition that, if $k$~is the body of natural law, then, if $b$~is true,
there is always another true proposition~$a$, which asserts existences
prior to~$B$, such that $b/ak=1$. No use has been made so far of our
existential knowledge~$l$, which is irrelevant to the definitions preceding.

(iv.) If $b/akl=1$ and~$b/kl\neq 1$, $A$~is a sufficient cause of~$B$ under
conditions~$l$.

(v.) If $b/\bar{a}kl=0$ and~$b/kl\neq 0$, $A$~is a necessary cause of~$B$ under
conditions~$l$.

(vi.) If there is any existential proposition~$h$ such that $b/ahk=1$
and~$b/hk\neq 1$, $A$~is, relative to~$k$, a possible sufficient cause of~$B$.

(vii.) If there is an existential proposition~$h$ such that $b/\bar{a}hk=0$
and~$b/hk\neq 0$, $A$~is, relative to~$k$, a possible necessary cause of~$B$.

(viii.) If $b/ahkl=1$, $b/hk\neq 1$, and~$h/akl\neq 0$, $A$~is, relative to~$k$,
a possible sufficient cause of~$B$ under conditions~$l$.

(ix.) If $b/\bar{a}hkl=0$, $b/hkl\neq0$, $h/\bar{a}kl=0$, and~$h/akl\neq 0$, $A$~is,
relative to~$k$, a possible necessary cause of~$B$ under conditions~$l$.
%% -----File: 288.png---Folio 277-------
Thus an event is a possible necessary cause of another, relative to
given nomologic data, if circumstances can arise, not inconsistent
with our existential data, in which the first event will be indispensable
if the second is to occur.

(x.) Two events are \emph{causally independent} if no part of either is,
relative to our nomologic data, a possible cause of any part of the
other under the conditions of our existential knowledge. The greater
the scope of our existential knowledge, the greater is the likelihood
of our being able to pronounce events causally dependent or independent.

\Paragraph{4.} These definitions preserve the distinction between `causally
independent' and `independent for probability,'---the distinction
between \textit{causa essendi} and \textit{causa cognoscendi}. If $b/ahkl\neq b/\bar{a}hkl$,
where $a$~and~$b$ may be any propositions whatever and are not limited
as they were in the causal definitions, we have `dependence for
probability,' and $a$~is a \textit{causa cognoscendi} for~$b$, relative to data~$kl$.
If $a$~and~$b$ are causally dependent, according to definition~(x.), $b$~is a
possible \textit{causa essendi}, relative to data~$kl$.

But, after all, the essential relation is that of `independence for
probability.' We wish to know whether knowledge of one fact
throws light \emph{of any kind} upon the likelihood of another. The theory
of causality is only important because it is thought that by means of
its assumptions light \emph{can} be thrown by the experience of one phenomenon
upon the expectation of another.
%% -----File: 289.png---Folio 278-------
\index{Psychical Research|ifoll}%
%[Blank Page]
%% -----File: 290.png---Folio 279-------


\Part[Philosophical Applications]{IV}{Some Philosophical Applications of
Probability}
%% -----File: 291.png---Folio 280-------
%[Blank Page]
%% -----File: 292.png---Folio 281-------
\index{Chance, objective}%
\index{Probability, and relevant knowledge!objective relation of}%


\Chapter{XXIV}{The Meanings of Objective Chance, and of Randomness}
\index{Randomness}%

\Paragraph{1.} \First{Many} important differences of opinion in the treatment of
Probability have been due to confusion or vagueness as to
what is meant by Randomness and by Objective Chance, as
distinguished from what, for the purposes of this chapter, may be
termed Subjective Probability. It is agreed that there is a sort
of Probability which depends upon knowledge and ignorance, and
\index{Knowledge!ignorance@{and ignorance}}%
is relative, in some manner, to the mind of the subject; but it is
supposed that there is also a more objective Probability which
is not thus dependent, or less completely so, though precisely
what this conception stands for is not plain. The relation of
Randomness to the other concepts is also obscure. The problem
of clearing up these distinctions is of importance if we are to
criticise certain schools of opinion intelligently, as well as to the
treatment of the foundations of Statistical Inference which is to
be attempted in \Partref{V}.

There are at least three distinct issues to be kept apart. There
is the antithesis between knowledge and ignorance, between
events, that is to say, which we have some reason to expect, and
events which we have no reason to expect, which gives rise to
the theory of subjective probability and subjective chance; and,
connected with this, the distinction between `random' selection
and `biassed' selection. There are next objective probability and
objective chance, which are as yet obscure, but which are commonly
held to arise out of the antithesis between `cause' and
`chance,' between events, that is to say, which are causally connected
and events which are not causally connected. And there
is, lastly, the antithesis between chance and design, between
`blind causes' and `final causes,' where we oppose a `chance'
%% -----File: 293.png---Folio 282-------
\index{Cournot, and frequency theory!chance@{and chance}}%
\index{Spinoza|inote}%
event to one, part of whose cause is a volition following on a
conscious desire for the event.\footnote
  {This is discussed in \Chapref{XXV}. §\;4.}

\Paragraph{2.} The method of this treatise has been to regard subjective
probability as fundamental and to treat all other relevant conceptions
as derivative from this. That there is such a thing as
probability in this sense has been admitted by all sensible philosophers
since the middle of the eighteenth century at least.\footnote
  {D'Alembert, collecting (largely from Hume, many passages being translated
\index{D'Alembert!chance@{and chance}}%
\index{Hume!chance@{and chance}}%
  almost \textit{verbatim}) in the \textit{Encyclopédie méthodique} the most up-to-date
  commonplaces of the subject, found it natural to write: ``Il n'y a point de
  hasard à proprement parler; mais il y a son équivalent: l'ignorance, où nous
  sommes des vraies causes des événemens, a sur notre esprit l'influence qu'on
  suppose au hasard.'' Compare also the sentences from Spinoza quoted on
  p.~117 above.}
But
there is also, many writers have supposed, something else which
may be fitly described as objective probability; and there is,
besides, a long tradition in favour of the view that it is this (whatever
it may be) which is logically and philosophically important,
subjective probability being a vague and mainly psychological
conception about which there is very little to be said.

The distinction exists already in Hume: ``Probability is of
two kinds, either when the object is really in itself uncertain,
and to be determined by chance; or when, though the object be
already certain, yet 'tis uncertain to our judgment, which finds
a number of proofs on each side of the question.''\footnote
  {\textit{A Treatise of Human Nature}, Book~ii.\ part~iii.\ section~ix.}
But the
distinction is not elucidated, and one can only infer from other
passages that Hume did not intend to imply in this passage the
existence of objective chance in a sense contradictory to a determinist
theory of the Universe. In Condorcet all is confused; and
\index{Condorcet!chance@{and chance}}%
in Laplace nearly all. In the nineteenth century the distinction
\index{Laplace!chance@{and chance}}%
begins to grow explicit in the writings of Cournot. ``Les explications
que j'ai données\ldots,'' he writes in the preface to his
\textit{Exposition}, ``sur le double sens du mot de probabilité, qui
tantôt se rapporte à une certaine mesure de nos connaissances, et
tantôt à une mesure de la possibilité des choses, indépendamment
de la connaissance que nous en avons: ces explications, dis-je,
me semblent propres à resoudre les difficultés qui ont rendu
jusqu'ici suspecte à de bons esprits toute la théorie de la probabilité
mathématique.'' It will be worth while to pause for a
moment to consider the ideas of Cournot.
%% -----File: 294.png---Folio 283-------
\index{Chance, objective!Couturat on}%
\index{Cournot, and frequency theory!chance@{and chance}}%
\index{Definitions!de la Placette, Jean, and chance}%
\index{Independence, for knowledge!chance@{and chance}}%
\index{Series of probabilities!independent}%

\Paragraph{3.} Cournot, while admitting that there is such a thing as subjective
chance, was concerned to dispute the opinion that chance
is \emph{merely} the offspring of ignorance, saying that in this case
``le calcul des chances'' is merely ``un calcul des illusions.''
The chance, upon which ``le calcul des chances'' is based, is
something different, and depends, according to him, on the combination
or convergence of phenomena belonging to \emph{independent}
series. By ``independent series'' he means series of phenomena
which develop as parallel or successive series without any causal
interdependence or link of solidarity whatever.\footnote
  {``Le mot hasard,'' Cournot writes in his \textit{Essai sur les fondemenis de nos
  connaissances}, ``n'indique pas une cause substantielle, mais une idée: cette idée
  est celle de la combinaison entre plusieurs séries de causes ou de faits qui se
  développent chacun dans sa série propre, indépendamment les uns des autres.''
  This is very like the definition given by Jean de~la~Placette in his \textit{Traité des jeux
  de hasard}, to which Cournot refers: ``Pour moi, je suis persuadé que le hasard
  renferme quelque chose de réal et de positif, savoir un concours de deux ou
  plusieurs événements contingents, chacun desquels a ses causes, mais en sorte
  que leur concours n'en a aucune que l'on connaisse.''}
No one, he
says by way of example, seriously believes that in striking the
ground with his foot he puts out the navigator in the Antipodes,
or disturbs the system of Jupiter's satellites. Separate trains of
events, that is to say, have been set going by distinct initial acts of
creation, so to speak.\footnote
  {\textit{Essai sur les fondements de nos connaissances}, i.~134: ``La nature ne se
  gouverne pas par une loi unique\ldots\ ses lois ne sont pas toutes dérivées les
  unes des autres, on dérivées toutes d'une loi supérieure par une nécessité purement
  logique\ldots\ nous devons les concevoir au contraire comme ayant pu
  étre décrétées séparément d'une infinité de manières.''}
Every event is causally connected with
previous events belonging to its own series, but it cannot be
modified by contact with events belonging to a different series.
A `chance' event is a complex due to the concurrence in time
or place of events belonging to causally independent series.

This theory, as it stands, is evidently unsatisfactory. Even
if there are series of phenomena which are independent in Cournot's
sense, it is not clear how we can know which they are, or how we
can set up a calculus which presumes an acquaintance with them.
Just as it is likely that we are all cousins if we go back far enough,
so there may be, after all, remote relationships between ourselves
and Jupiter. A remote connection or a reaction quantitatively
small is a matter of degree and not by any means the same thing
as absolute independence. Nevertheless Cournot has contributed
something, I think, to the stock of our ideas. He has
%% -----File: 295.png---Folio 284-------
\index{Chance, objective!Poincaré on}%
\index{Chance, objective!Condorcet on}%
\index{Darbon, A., and Cournot}%
\index{Kries, von!Cournot@{and Cournot}|inote}%
\index{Poincaré, Henri!chance@{and chance}}%
hinted at, even if he has not disentangled, one of the elements
in a common conception of chance; and of the notion, which he
seems to have in his mind, we must in due course take account.\footnote
  {Cournot's work on Probability has been highly praised by authorities as
  diverse and distinguished as Boole and Von~Kries, and has been made the
\index{Boole!Cournot@{and Cournot}|inote}%
  foundation of a school by some recent French philosophers (see the special
  number of the \textit{Revue de métaphysique et de morale}, devoted to Cournot and published
  in~1905, and the bibliography at the end of the present volume \textit{passim}).
  The best account with which I am acquainted, of Cournot's theory of probability,
  is to be found in A.~Darbon's \textit{Le Concept du hasard}. Cournot's philosophy of
  the subject is developed, not so much in his \textit{Exposition de la théorie des chances},
  as in later works, especially in his \textit{Essai sur les fondements de nos connaissances}.
  Cournot never touched any subject without contributing something to it, but,
  on the whole, his work on Probability is, in my opinion, disappointing. No
  doubt his \textit{Exposition} is superior to other French text-books of the period, of
  which there is so large a variety, and his work, both here and elsewhere, is not
  without illuminating ideas: but the philosophical treatment is so confused and
  indefinite that it is difficult to make much of it beyond the one specific point
  treated above.}

\Paragraph{4.} In the writings of Condorcet, I have said above, all is confused.
\index{Condorcet!chance@{and chance}}%
But in Bertrand's criticism of him a relevant distinction,
\index{Bertrand!chance@{and chance}}%
though not elucidated, is brought before the mind. ``The
motives for believing,'' wrote Condorcet, ``that, from ten million
white balls mixed with one black, it will not be the black ball
which I shall draw at the first attempt is \emph{of the same kind} as the
motive for believing that the sun will not fail to rise to-morrow.''
``The assimilation of the two cases,'' Bertrand writes in criticism
of the above,\footnote
  {\textit{Calcul des probabilités}, p.~xix.}
``is not legitimate: one of the probabilities is
objective, the other subjective. The probability of drawing
the black ball at the first attempt is~$\frac{1}{10,000,000}$, neither more nor
less. Whoever evaluates it otherwise makes a mistake. The
probability that the sun will rise varies from one mind to another.
A scientist might hold on the basis of a false theory, without being
utterly irrational, that the sun will soon be extinguished; he
would be within his rights, just as Condorcet is within his; both
would exceed their rights in accusing of error those who think
differently.'' Before commenting on this distinction, let us have
before us also some interesting passages by Poincaré.

\Paragraph{5.} We certainly do not use the term `chance,' Poincaré points
out, as the ancients used it, in opposition to determinism. For
us therefore the natural interpretation of `chance' is subjective,---`Chance
is only the measure of our ignorance. Fortuitous
phenomena are, by definition, those, of the laws of which we are
%% -----File: 296.png---Folio 285-------
ignorant.'' But Poincaré immediately adds: ``Is this definition
very satisfactory? When the first Chaldaean shepherds followed
with their eyes the movements of the stars, they did not yet
know the laws of astronomy, but would they have dreamed of
saying that the stars move by chance? If a modern physicist
is studying a new phenomenon, and if he discovers its law on
Tuesday, would he have said on Monday that the phenomenon
was fortuitous?''\footnote
  {\textit{Calcul des probabilités} (2nd~edition), p.~2. This passage also appears in an
  article in the  \textit{Revue du mois} for 1907 and in the author's \textit{Science et méthode}, of
  the English translation of which I have made use above,---at the cost of doing
  incomplete justice to Poincaré's most admirable style.}

There is also another type of case in which ``chance must be
something more than the name we give to our ignorance.'' Among
the phenomena, of the causes of which we are ignorant, there are
some, such as those dealt with by the manager of a life insurance
\index{Insurance}%
company, about which the calculus of probabilities can give real
information. Surely it cannot be thanks to our ignorance,
Poincaré urges, that we are able to arrive at valuable conclusions.
If it were, it would be necessary to answer an inquirer thus:
``You ask me to predict the phenomena that will be produced.
If I had the misfortune to know the laws of these phenomena, I
could not succeed except by inextricable calculations, and I should
have to give up the attempt to answer you; but since I am
fortunate enough to be ignorant of them, I will give you an answer
at once. And, what is more extraordinary still, my answer will
be right.'' The ignorance of the manager of the life insurance
company as to the prospects of life of his individual policy-holders
does not prevent his being able to pay dividends to his
shareholders.

Both these distinctions seem to be real ones, and Poincaré
proceeds to examine further instances in which we seem to
distinguish \emph{objectively} between events according as they are or
are not due to `chance.' He takes the case of a cone balanced
upon its tip; we know for certain that it will fall, but not on
which side---chance will determine. ``A very small cause which
escapes our notice determines a considerable effect that we cannot
fail to see, and then we say that that effect is due to chance.''
The weather, and the distribution of the minor planets on the
Zodiac, are analogous instances. And what we term `games of
chance' afford, it has always been recognised, an almost perfect
%% -----File: 297.png---Folio 286-------
\index{Chance, objective|ifoll}%
example. ``It may happen that small differences in the initial
conditions produce very great ones in the final phenomena. A
small error in the former will produce an enormous error in the
latter. Prediction becomes impossible, and we have the fortuitous
phenomenon.'' ``The greatest chance is the birth of a great
man. It is only by chance that the meeting occurs of two genital
cells of different sex that contain precisely, each on its side, the
mysterious elements, the mutual reaction of which is destined
to produce genius\ldots. How little it would have taken to make
the spermatozoid which carried them deviate from its course.
It would have been enough to deflect it a hundredth part of an
inch, and Napoleon would not have been born and the destinies
of a continent changed. No example can give a better comprehension
of the true character of chance.''

Poincaré calls attention next to another class of events, which
we commonly assign to `chance,' the distinguishing characteristic
of which seems to be that their causes are very numerous and
complex,---the motions of molecules of gas, the distribution of
drops of rain, the shuffling of a pack of cards, or the errors of
observation. Thirdly there is the type, usually connected with
one of the first two, and specially emphasised, as we have seen
above, by Cournot, in which something comes about through
the concurrence of events which we regard as belonging to distinct
causal trains,---a man is walking along the street and is killed by
the fall of a tile.

\Paragraph{6.} When we attribute such events, as those illustrated by
Poincaré, to \emph{chance}, we certainly do not mean merely to assert
that we do not know how they arose or that we had no special
reason for anticipating them \textit{à~priori}. So far from this being the
case, we mean to make a definite assertion as to the kind of way
in which they arose;---though exactly what we mean to assert
about them it is extremely difficult to say.

Now a careful examination of all the cases in which various
writers claim to detect the presence of `objective chance' confirms
the view that `subjective chance,' which is concerned with
knowledge and ignorance, is fundamental, and that so-called
`objective chance,' however important it may turn out to be
from the practical or scientific point of view, is really a special
kind of `subjective chance' and a derivative type of the latter.
For none of the adherents of `objective chance' wish to question
%% -----File: 298.png---Folio 287-------
\index{Chance, objective!definition of}%
the determinist character of natural order; and the possibility
of this objective chance of theirs seems always to depend on the
possibility that a particular kind of knowledge either is ours or
is within our powers and capacity. Let me try to distinguish as
exactly as I can the criterion of objective chance.

\Paragraph{7.} When we say that an event has happened by chance, we
do not mean that previous to its occurrence the event was, on
the available evidence, very improbable; this may or may not
have been the case. We say, for example, that if a coin falls heads
it is `by chance,' whereas its falling heads is not at all improbable.
The term `by chance' has reference rather to the state of our
information about the concurrence of the event considered and
the event premised. The fall of the coin is a chance event if
our knowledge of the circumstances of the throw is \emph{irrelevant}
to our expectation of the possible alternative results. If the
number of alternatives is very large, then the occurrence of
the event is not only subject to chance but is also very improbable.
In general two events may be said to have a chance
connection, in the subjective sense, when knowledge of the
first is irrelevant to our expectation of the second, and produces
no additional presumption for or against it; when, that is to
say, the probabilities of the propositions asserting them are
\emph{independent} in the sense defined in \Chapref{XII}. §\;8.

The above definition deals with chance in the widest sense.
What is the \textit{differentia} of the narrower group of cases to which
it is desired to apply the term `\emph{objective} chance'? The occurrence
of an event may be said to be subject to objective chance,
I think, when it is not only a chance event in the above sense,
but when we also have good reason to suppose that the addition
of further knowledge of a given kind, if it were procurable, would
not affect its chance character. We must consider, that is to say,
the probability which is relative not to \emph{actual} knowledge but to
the \emph{whole} of a \emph{certain kind} of knowledge. We may be able to
infer from our evidence that, even with certain kinds of
additions to our knowledge, the connections between the events
would still be subject to chance in the sense just defined, and
we may be able to infer this without actually having the additional
information in question. If, however complete our
knowledge of certain kinds of things might be, there would still
exist independence between the propositions, the conjunction
%% -----File: 299.png---Folio 288-------
\index{Casual@{`\textit{Casual}'}}%
of which we are investigating, then we may say there is an
\emph{objective} sense in which the actual conjunction of these propositions
is due to chance.

\Paragraph{8.} This is, I think, the right line of inquiry. It remains to
decide, \emph{what} kinds of information must be irrelevant to the
connection, in order that the presence of objective chance may
be established.

When we attribute a coincidence to objective chance, we
mean not only that we do not actually know a law of connection,
but, speaking roughly, that there is no law of connection to be
known. And when we say that the occurrence of one alternative
rather than another is due to chance, we mean not only
that we know no principle by which to choose between the
alternatives, but also that no such principle is knowable. This
use of the term closely corresponds to what Venn means by the
\index{Venn!chance@{and chance}}%
term `casual': ``We call a coincidence casual, I apprehend,
when we mean to imply that no knowledge of one of the two
\index{Knowledge!homologic and ontologic}%
elements, which we can suppose to be practically attainable,
would enable us to expect the other.''\footnote
  {\textit{Logic of Chance}, p.~245.}

To make this more precise, we must revive our distinction,\footnote
  {See \Partref{III}. Note~(ii.)\ §\;2, \Pageref{275}.}
between nomologic knowledge and ontologic knowledge,
between knowledge of laws and knowledge of facts or existence.
Given certain facts~$f(a)$ about~$a$ and certain laws of connection,~$L$,
we can infer certainly or probably other facts~$\phi(a)$ about~$a$. If
a \emph{complete} knowledge of laws of connection together with~$f(a)$
yields no appreciable probability for preferring~$\phi(a)$ to other
alternatives, then I suggest that an actual connection between $\phi$~and~$f$
in a particular instance may be said to be due to chance in
a sense which usage justifies us in calling objective. We do
not, in fact, when we speak of objective chance, always use it
in so strict a sense as this, but this is, I think, the underlying
conception to which current usage approximates. Current
usage diverges from this sense mainly for two reasons. We
speak of objective chance if in the above conditions our
grounds for preference, though appreciable, are very small; and
we are not insistent to assert the rule of chance if a comparatively
\emph{slight} addition to our ontologic knowledge would render the
probability or the grounds for preference appreciable.
%% -----File: 300.png---Folio 289-------
\index{Chance, objective!Poincaré on}%
\index{Poincaré, Henri!chance@{and chance}}%

To sum up the above, an event is due to objective chance if
in order to predict it, or to prefer it to alternatives, at present
\DPchg{equi-probable}{equiprobable}, with any high degree of probability, it would be
necessary to know a great many more facts of existence about
it than we actually do know, and if the addition of a wide
knowledge of general principles would be little use.
\index{Knowledge!chance@{and chance}}%

It must be added that we make a distinction between facts of
existence which are highly variable from case to case and those
which are constant or nearly constant over a certain field of
observation or experience. Within the limits of this field we
regard the \emph{permanent} facts of existence as being, from the standpoint
of chance, in nearly the same position as laws. A connection
is not due to chance, therefore, if a knowledge of the permanent
facts of existence could lead to their prediction.

To sum up again therefore,---if within a given field of observation
or experience a knowledge of those facts of existence which are
permanent or invariable within that field, together with a knowledge
of all the relevant fundamental causal laws or general
principles, and of a \emph{few} other facts of existence, would not
permit us, given~$f(a)$, to attribute an appreciable probability to~$\phi(a)$
(or an appreciable probability to the alternative~$\phi_1(a)$
rather than~$\phi_2(a)$); then the conjunction of~$\phi(a)$ (or of~$\phi_1(a)$
rather than $\phi_2(a)$ with~$f(a)$) is due to objective chance.

\Paragraph{9.} If we return to the examples of Poincaré, the above definition
appears to conform satisfactorily with the usages of common
sense. It is when an \emph{exact} knowledge of fact, as distinguished
from principle, is required for even approximate prediction that
the expression `objective chance' seems applicable. But
neither our definition nor usage is precise as to the \emph{amount} of
knowledge of fact which must be required for prediction, in
order that, in the absence of it, the event may be regarded as
subject to objective chance.

It may be added that the expression `chance' can be used
with reference to general statements as well as to particular facts.
We say, for example, that it is a matter of chance if a man dies
on his birthday, meaning that, as a general principle and in the
absence of special information bearing on a particular case, there
is no presumption whatever in favour of his dying on his birthday
rather than on any other day. If as a general rule there were celebrations
on such a day such as would be not unlikely to accelerate
%% -----File: 301.png---Folio 290-------
\index{Frequency theory!randomness@{and randomness}}%
death, we should say that a man's dying on his birthday was not
altogether a matter of chance. If we knew no such general rule
but did not know enough about birthdays to be assured that there
was no such rule, we could not call the chance `objective'; we
could only speak of it thus, if on the evidence before us there was a
strong presumption against the existence of any such general rule.

\Paragraph{10.} The philosophical and scientific importance of objective
chance as defined above cannot be made plain, until Part V., on
the Foundations of Statistical Inference, has been reached. There
it will appear in more than one connection, but chiefly in connection
with the application of Bernoulli's formula. In cases where
the use of this formula is valid, important inferences can be drawn;
and it will he shown that, when the conditions for objective chance
are approximately satisfied, it is probable that the conditions
for the application of Bernoulli's formula will be approximately
satisfied also.

\Paragraph{11.} The term \emph{random} has been used, it is well recognised, in
\index{Venn!random@{and `\textit{random}'}}%
several distinct senses. Venn\footnote
  {\textit{Logic of Chance}, chap.~v., ``The Conception \emph{Randomness} and its Scientific
\index{Randomness}%
  Treatment.''}
and other adherents of the
`frequency' theory have given to it a precise meaning, but one
which has avowedly very little relation to popular usage. A
\index{Peirce!randomness@{and randomness}}%
random sample, says Peirce,\footnote
  {``A Theory of Probable Inference'' (published in Johns Hopkins \textit{Studies in
  Logic}), p.~152.}
is one ``taken according to a precept
or method, which, being applied over and over again indefinitely,
would in the long run result in the drawing of any one set of instances
as often as any other set of the same number.'' The
same fundamental idea has been expressed with greater precision
by Professor Edgeworth in connection with his investigations
\index{Edgeworth!randomness@{and randomness}}%
into the law of error.\footnote
  {``Law of Error,'' \textit{Camb.\ Phil.\ Trans.}, 1904, p.~128.}
It is a fatal objection, in my opinion, to
this mode of defining randomness, that in general we can only
know whether or not we have a random sample when our knowledge
is nearly complete. Its divergence from ordinary usage is
well illustrated by the fact that there would be perfect randomness
in the distribution of stars in the heavens, as Venn explicitly points
out, if they were disposed in an exact and symmetrical pattern.\footnote
  {But it may be added that this seems inconsistent with Venn's conception
  of randomness as that of aggregate order and \emph{individual irregularity}; nor is it
  concordant with Venn's typically random diagram (p.~118). His usage, therefore,
  is sometimes nearer than his definition to the popular usage.}
%% -----File: 302.png---Folio 291-------
\index{Probability, and relevant knowledge!randomness@{and randomness}}%

I do not believe, therefore, that this kind of definition is a
useful one. The term must be defined with reference to probability,
not to what will happen ``in the long run''; though
there may be two senses of it, corresponding to subjective and
objective probability respectively.

The most important phrase in which the term is used is that
of `a random selection' or `taken at random.' When we apply
this term to a particular member of a series or collection of
objects, we may mean one of two things. We may mean that
our knowledge of the method of choosing the particular member
is such that \textit{à~priori} the member chosen is as likely to be any
one member of the series as any other. We may also mean,
not that we have \emph{no} knowledge as to which particular member
is in question, but that such knowledge as we have respecting
the particular member, as distinguished from other members of
the series, is irrelevant to the question as to whether or not
this member has the characteristic under examination. In the
first case the particular member is a random member of the
series for \emph{all} characteristics; in the second case it is a random
member for some only. As the second case is the more general,
we had better take that for the purpose of defining `random
selection.'

The point will be brought out further if we discuss the
more difficult use of the term. What exactly do we mean by
the statement: ``Any number, taken at random, is equally
likely to be odd or even''? According to the frequency theory,
this simply means that there are as many odd numbers as there
are even. Taking it in a sense corresponding to subjective
chance (and to the explanations given above), I propose as
a definition the following: $a$~is taken at random from the
class~$S$ for the purposes of the propositional function $S(x)·\phi(x)$,
\index{Propositional function!randomness@{and randomness}}%
relative to evidence~$h$, if `$x$~is~$a$' is irrelevant to the probability
$\phi(x)/S(x)· h$. Thus `the number of the inhabitants of France is
odd' is, relative to my knowledge, a random instance of the
propositional function `$x$~is an odd number,' since `$a$~is the
number of the inhabitants of France' is irrelevant to the probability
of `$a$~is odd'.\footnote
  {In the above $S(x)$ stands for `$x$~is a number', $\phi(x)$~stands for `$x$~is odd,'
  $a$~stands for `the number of inhabitants of France.'}
Thus to say that a number taken at
random is as likely to be odd as even, means that there is a
%% -----File: 303.png---Folio 292-------
\index{Selection, random}%
probability~$\frac{1}{2}$ that any instance taken at random of the
generalisation `all numbers are odd' (or of the corresponding
generalisation `all numbers are even') is true; an instance being
taken at random in respect of evenness or oddness, if our
knowledge about it satisfies the conditions defined above.
Whether or not a given instance is taken at random, depends,
therefore, upon what generalisation is in question.

\Paragraph{12.} We may or may not have reason to believe that, if we take
a series of random selections, the proportionate number of
occurrences of one particular type of result will very probably
lie within certain limits. For reasons to be explained in \Chapref{XXIX}.,
random selection relative to such information may
conveniently be termed `random selection under Bernoullian
conditions.' It is this kind of random selection which is scientifically
and statistically important. But, as this corresponds to
`objective chance,' it is convenient to have a wider definition
of `random selection' unqualified, corresponding to `subjective
chance'; and it is this wider definition which is given above.

The term opposite to `random selection' in ordinary usage
is `biassed selection.' When I use this phrase without qualification
I shall use it as the opposite of `random selection' in the
wider unqualified sense.
%% -----File: 304.png---Folio 293-------
\index{Bernoulli, Daniel, and Inverse Probability!planets@{and planets}|inote}%
\index{Chance, objective!planets@{and planets}}%
\index{Planets, movements of}%
\index{Probability, and relevant knowledge!planetary orbits@{and planetary orbits}}%


\Chapter{XXV}{Some Problems arising out of the Discussion of Chance}

\Paragraph{1.} \First{There} are two classical problems in which attempts have been
made to attribute certain astronomical phenomena to a specific
cause, rather than to objective chance in some such sense as has
been defined in the preceding chapter.

The first of these is concerned with the inclinations to the
ecliptic of the orbits of the planets of the solar system. This
problem has a long history, but it will be sufficient to take De
Morgan's statement of it.\footnote
  {Article on \textit{Probabilities} in \textit{Encyclopaedia Metropolitana}, p.~412, §\;46. De~Morgan
  takes this without acknowledgment from Laplace, \textit{Théorie analytique
\index{Laplace!planets@{and planets}|inote}%
  des probabilités} (1st~edition), pp.~257, 258. Laplace also allows for the fact
  that all the planets move in the same sense as the earth. He concludes: ``On
  verra que l'existence d'une cause commune qui a dirigé tous ces mouvemens
  dans le sens de la rotation du soleil, et sur des plans peu inclinés à celui de son
  équateur, est indiquée avec une probabilité bien supérieure à celle du plus
  grand nombre des faits historiques sur lesquels on ne se permet aucun doute.''
  Laplace had in his turn borrowed the example, also without acknowledgment,
  from Daniel Bernoulli. See also D'Alembert, \textit{Opuscules mathématiques}, vol.~iv.,
\index{D'Alembert!planets@{and planets}}%
  1768, pp.~89 and 292.}
If we suppose that each of the orbits
might have \emph{any} inclination, we obtain a vast number of combinations
of which only a small number are such that their sum is as
small or smaller than the sum of those of the actual system.
But the very existence of ourselves and our world can be shown
to imply that one of this small number has been selected, and
De~Morgan derives from this an enormous presumption that
\index{De Morgan!planets@{and planets}}%
``there was a necessary cause in the formation of the solar system
for the inclinations being what they are.''

The answer to this was pointed out by D'Alembert\footnote
  {\textit{Op.\ cit.}\ p.~292. ``Il y a certainement d'infini contre un à parier que les
  Planètes ne devraient pas se trouver dans le même plan; ce n'est pas une raison
  pour en conclure que cette disposition, si elle avoit lieu, auroit nécessairement
  d'autre cause que le hasard; car il y auroit de même l'infini contre un à parier
  que les Planètes pourroient n'avoir pas une certaine disposition déterminée à
volonté\ldots.''

  D'Alembert is employing the instance for his own purposes, in order to build
  up an \textit{ad~hominem} argument in favour of his theory concerning `runs' against
  D.~Bernoulli (see also \Pageref{317}).}
in criticising
%% -----File: 305.png---Folio 294-------
\index{Bernoulli, Daniel, and Inverse Probability!planets@{and planets}}%
\index{Boole|inote}%
\index{Forbes, J. D.|inote}%
\index{Herschell and binary stars}%
\index{Probability, and relevant knowledge!binary stars@{and binary stars}}%
\index{Stars, binary}%
\index{Todhunter|inote}%
\index{Venn|inote}%
Daniel Bernoulli. De~Morgan could have reached a similar
result \emph{whatever} the configuration might have happened to be.
\emph{Any} arbitrary disposition over the celestial sphere is vastly
improbable \textit{à~priori}, that is to say in the absence of known laws
tending to favour particular arrangements. It does not follow
from this, as De~Morgan argues, that any actual disposition
possesses \textit{à posteriori} a peculiar significance.

\Paragraph{2.} The second of these problems is known as Michell's problem
\index{Michell!binary stars@{and binary stars}}%
of binary stars. Michell's Memoir was published in the \textit{Philosophical
Transactions} for 1767.\footnote
  {See also Todhunter's \textit{History}, pp.~332--4; Venn, \textit{Logic of Chance}, p.~260;
  Forbes, ``On the Alleged Evidence for a Physical Connexion between Stars
  forming Binary or Multiple Groups, deduced from the Doctrine of Chances,''
  \textit{Phil.\ Mag}., 1850, and Boole, ``On the Theory of Probabilities and in particular
  on Michell's Problem of the Distribution of the Fixed Stars,'' \textit{Phil.\
  Mag.}, 1851.}
It deals with the question as to
whether stars which are optically double, \ie\ which are so situated
as to appear close together to an observer on the earth---are also
physically so ``either by an original act of the Creator, or in consequence
of some general law, such perhaps as gravity.'' He
argues that if the stars ``were scattered by mere chance as it
might happen~\ldots\ it is manifest~\ldots\ that every star being
as likely to be in any one situation as another, the probability that
any one particular star should happen to be within a certain
distance (as, for example, one degree) of any other given star
would be represented~\ldots\ by a fraction whose numerator would
be to its denominator as a circle of one degree radius to a circle
whose radius is the diameter of a great circle~\ldots\ that is, about
$1$~in~$13131$.'' From this beginning he derives an immense presumption
against the scattering of the several contiguous stars
that may be observed ``by mere chance as it might happen.''
And he goes on to argue that, if there are causal laws directly
tending to produce the observed proximities, we may reasonably
suppose that the proximities are actual, and not merely optical
and apparent. The fact that Michell's induction was confirmed
by the later investigations of Herschell adds interest to the
speculation. But apart from this the argument is evidently
%% -----File: 306.png---Folio 295-------
\index{Chance, objective}%
\index{Chance, objective!binary stars@{and binary stars}}%
subtler than in the first example. Michell argues that there are
more stars optically contiguous, than would be likely if there
were no special cause acting towards this end, and further that,
if such a cause is in operation, it must be \emph{real}, and not merely
optical, contiguity that results from it.

Let us analyse the argument more closely. By ``mere chance
as it might happen'' Michell cannot be supposed to mean ``uncaused.''
He is thinking of objective chance in the sense in
which I have defined this in the preceding chapter. We
speak of a chance occurrence when it is brought about by the
coincidence of forces and circumstances so numerous and complex
that knowledge sufficient for its prediction is of a kind altogether
out of our reach. Michell uses the term vaguely but means, I
think, something of this kind: An event is due to \emph{mere chance}
when it can only occur if a large number of independent\footnote
  {See §\;3 of \hyperref[note:ii]{Note~(ii.)}\ to \Partref{III}\@.}
conditions
are fulfilled simultaneously. The alternatives which
Michell is discussing are therefore these: Are binary stars merely
due to the interaction of a vast variety of stellar laws and positions
or are they the result of a few fundamental tendencies,
which might be the subject of knowledge and which would lead
us to expect such stars in relative profusion?

The existence of numerous binary stars may give a real
inductive argument in favour of their arising out of the interaction
of a relatively small number of independent causes. But
it is not possible to arrive at such precise results as Michell's.
If there is some finite probability \textit{à~priori} that binary stars,
when they arise, do arise in this way, then, since the frequent
coincidence of a given set of independent causes relatively few
in number is more likely than that of a set relatively numerous,
the observation of binary stars will raise this probability \textit{à posteriori}
to an extent which depends upon the relative profusion
in which such stars appear. If, in short, the first of the two
alternatives proposed above is assumed, there is no greater
presumption for a distribution, covering a part of the heavens,
in which binary stars appear, than for any other distribution;
if the second is assumed, there \emph{is} a greater presumption. The
observation of numerous distributions in which binary stars
appear \emph{increases}, therefore, by the inverse principle, any \textit{à~priori}
probability which may exist in favour of the second hypothesis.
%% -----File: 307.png---Folio 296-------
\index{Probability, and relevant knowledge!star drifts@{and star drifts}}%
But more than this the argument cannot justify. That Michell's
argument is, as it stands, no more valid than De~Morgan's,
becomes plain when we notice that he would still have a high
probability for his conclusion even if \emph{only one} binary star had
been observed. The valuable part of the argument must clearly
turn upon the observation of \emph{numerous} binary stars.

Let us now turn to Michell's second step. He argues that,
if binary stars arise out of the interaction of a small number of
independent forces, they must be physically and not merely
optically double. The force of this argument seems to depend
upon our possessing previous knowledge as to the nature of the
principal natural laws, and upon an assumption, arising out of
this, that there are not likely to be forces tending to arrange
stars, in reality at great distances from one another, so as to
\emph{appear} double from this particular planet. But Michell, in
arguing thus, was neglecting the possibility that the optical
connection between the stars might be due to the observer and
his means of observation. It was not impossible that there should
be a law, connected with the transmission of light for example,
which would cause stars to appear to an observer to be much
nearer together than they really are.

While, therefore, a relative profusion of binary stars constitutes
evidence favourably relevant to Michell's conclusion, the argument
is more complex and much less conclusive than he seems to
have supposed. This is a criticism which is applicable to many
such arguments. The simplicity of the evidence, which arises
out of the lack of much relevant information, is liable, unless we
are careful, to lead us into deceptive calculations and into assertions
of high numerical probabilities, upon which we should never
venture in cases where the evidence is full and complicated, but
where, in fact, the conclusion is established far more strongly.
The enormously high probability in favour of his conclusion, to
which Michell's calculations led him, should itself have caused
him to suspect the accuracy of the reasoning by which he
reached it.

\Paragraph{3.} Some more recent problems of this type seem, however, so
far as I am acquainted with them, to follow safer lines of argument.
The most important are concerned with the existence
of star drifts. It seems to me not at all impossible to possess
\index{Star drifts}%
\textit{data} on which a valid argument can be constructed from the
%% -----File: 308.png---Folio 297-------
\index{Cause, final}%
\index{Pearson, Karl!stars@{and stars}}%
\index{Probability, and relevant knowledge!final causes@{and final causes}}%
observation of optically apparent star drifts to the probability
of a real uniformity of motion amongst certain sets of stars
relatively to others.

Another problem, somewhat analogous to the preceding, has
been recently discussed by Professor Karl Pearson.\footnote
  {``On the Improbability of a Random Distribution of the Stars in Space,''
  \textit{Proceedings of Royal Society}, series~A, vol.~84, pp.~47--70, 1910.}
The title
might prove a little misleading, perhaps, until the explanation
has been reached of the sense in which the term `random' is
used in it. But Professor Pearson uses the term in a perfectly
precise sense. He defines a random distribution as one in which
spherical shells of equal volume about the sun as centre contain
the same number of stars.\footnote
  {It is, therefore, independent of direction, and the distribution is random
  even if the stars are massed in particular quarters of the heavens. The definition
  is, therefore, exceedingly arbitrary.}
He argues that the observed facts
render probable the following disjunction: Either the distribution
of stars is not random in the sense defined above, \emph{or} there is
a correlation between their distance and their brilliancy, such as
might be produced, for example, by the absorption of light in its
transmission through space, \emph{or} the space within which they all
lie is limited in volume and not spherical in form.\footnote
  {This should run more correctly, I think, ``not a sphere \emph{with the sun as
centre}.''}
But it is
useless to employ the term \emph{random} in this sense in such inquiries
as Michell's. For there is no reason to suppose that a non-*random
distribution is more likely than a random distribution
to depend upon the interaction of a small number of independent
forces, and there might even exist a presumption the other way.
This arbitrary interpretation of randomness does not help us to
\index{Randomness!Pearson's use of}%
the solution of any interesting problem.

\Paragraph{4.} The discussion of \emph{final} causes and of the argument from
design has suffered confusion from its supposed connection with
theology. But the logical problem is plain and can be determined
upon formal and abstract considerations. The argument is in all
cases simply this---an event has occurred and has been observed
which would be very improbable \textit{à~priori} if we did not know that
it had actually happened; on the other hand, the event is of such
a character that it might have been not unreasonably predicted
if we had assumed the existence of a conscious agent whose
motives are of a certain kind and whose powers are sufficient.
%% -----File: 309.png---Folio 298-------
\index{Coover, J.|inote}%
\index{Society for Psychical Research|inote}%

Symbolically: Let $h$ be our original \textit{data}, $a$~the occurrence
of the event, $b$~the existence of the supposed conscious agent.
Then $a/h$~is assumed very small in comparison with~$a/bh$; and
we require~$b/ah$, the probability, that is to say, of~$b$ after $a$~is
known. The inverse principle of probability already demonstrated
shows that $b/ah = a/bh·\dfrac{b/h}{a/h}$, and $b/ah$ is therefore not
determinate in terms of $a/bh$~and~$a/h$ alone. Thus we cannot
measure the probability of the conscious agent's existence \emph{after}
the event, unless we can measure its probability \emph{before} the event.
And it is our ignorance of this, as a rule, that we are endeavouring
to remedy. The argument tells us that the existence of the
hypothetical agent is more likely after the event than before
it; but, as in the case of the general inductive problem dealt
with in \Partref{III}., unless there is an \emph{appreciable} probability first,
there cannot be an appreciable probability afterwards. No
conclusion, therefore, which is worth having, can be based on the
argument from design \emph{alone}; like induction, this type of argument
can only strengthen the probability of conclusions, for
which there is something to be said on \emph{other} grounds. We cannot
say, for example, that the human eye is due to design more
probably than not, unless we have some reason, apart from the
nature of its construction, for suspecting conscious workmanship.
But the necessary \textit{à~priori} probability, derived from some other
source, may sometimes be forthcoming. The man who upon a
desert island picks up a watch, or who sees the symbol \textit{John
Smith} traced upon the sand, can use with reason the argument
from design. For he has other grounds for supposing that
beings, capable of designing such objects, do exist, and that
their presence on the island, now or formerly, is appreciably
possible.

\Paragraph{5.} The most important problems at the present day, in which
arguments of this kind are employed, are those which arise in
connection with psychical research.\footnote
  {The probability that a remarkable success in naming playing cards is due
  to psychic agency, was discussed by Professor Edgeworth in \textit{Metretike}. This
\index{Edgeworth!Psychical Research@{and Psychical Research}|inote}%
  was, I think, the first application of probabilities to these questions. See also
  \textit{Proceedings of the Society for Psychical Research}, Parts VIII.~and~X.; Professor
  Edgeworth's article on \textit{Psychical Research and Statistical Method}, Stat.\ Journ.\
  vol.~lxxxii.\ (1919) p.~222; and \textit{Experiments in Psychical Research at Leland
  Stanford Junior University}, by J.~Coover.}
The analysis of the `cross-correspondences,'
%% -----File: 310.png---Folio 299-------
\index{Hypothetical entities}%
\index{Logic, academic!initial probability@{and initial probability}}%
\index{Physics and initial probability}%
which have played so large a part in recent
discussions, presents many points of difficulty which are not
dissimilar to those which arise in other scientific inquiries of
great complexity in which our initial knowledge is small. An
important part of the \emph{logical} problem, therefore, is to distinguish
the \emph{peculiarity} of psychical problems and to discover what special
evidence they demand beyond what is required when we deal with
other questions. There is a certain tendency, I think, arising out
of the belief that psychical problems are in some way peculiar,
to raise sceptical doubts against them, which are equally valid
against \emph{all} scientific proofs. Without entering into any questions
of detail, let us endeavour to separate those difficulties which
seem peculiar to psychical research from those which, however
great, are not different from the difficulties which confront
students of heredity, for instance, and which are not less likely
than these to yield ultimately to the patience and the insight of
investigators.

For this purpose it is necessary to recur, briefly, to the analysis
of \Partref{III}\@. It was argued there that the methods of empirical
proof, by which we strengthen the probability of our conclusions,
are not at all dissimilar, when we apply them to the discovery
of formal truth, and when we apply them to the discovery of the
laws which relate material objects, and that they may possibly
prove useful even in the case of metaphysics; but that the
\emph{initial} probability which we strengthen by these means is differently
obtained in each class of problem. In logic it arises out
of the postulate that apparent self-evidence invests what seems
self-evident with \emph{some} degree of probability; and in physical
science, out of the postulate that there is a limitation to the
amount of \emph{independent} variety amongst the qualities of material
objects. But both in logic and in physical science we may wish
to consider hypotheses which it is not possible to invest with any
\textit{à~priori} probability and which we entertain solely on account of
the known truth of many of their consequences. An axiom
which has no self-evidence, but which it seems necessary to combine
with other axioms which are self-evident in order to deduce
\index{Axioms!non-self-evident}%
the generally accepted body of formal truth, stands in this
category. A scientific entity, such as the ether or the electron,
whose qualities have \emph{never} been observed but whose existence we
postulate for purposes of explanation, stands in it also. If the
%% -----File: 311.png---Folio 300-------
\index{Probability, and relevant knowledge!spirits@{and spirits}}%
\index{Probability, and relevant knowledge!telepathy@{and telepathy}}%
\index{Spirits, probability of}%
\index{Telepathy, probability of}%
analysis of \Partref{III}. is correct, we can never attribute a finite
probability\footnote
  {I am \emph{assuming} that there is \emph{no} argument, arising either from self-evidence
  or analogy, in addition to the argument arising from the truth of their consequences,
  in favour of the truth of such axioms or the existence of such objects;
  but I daresay that this may not certainly be the case. The reader may be reminded
  also that, when I deny a finite probability this is not the same thing as
  to affirm that the probability is infinitely small. I mean simply that it is not
  greater than some numerically measurable probability.}
to the truth of such axioms or to the existence of
such scientific entities, however many of their consequences
we find to be true. They may be \emph{convenient} hypotheses, because,
if we confine ourselves to \emph{certain classes} of their consequences,
we are not likely to be led into error; but they stand, nevertheless,
in a position altogether different from that of such generalisations
as we have reason to invest with an initial probability.

Let us now apply these distinctions to the problems of psychical
research. In the case of some of them we can obtain the initial
probability, I think, by the same kind of postulates as in physical
science, and our conclusions need not be open to a greater degree
of doubt than these. In the case of others we cannot; and these
must remain, unless some method is open to us peculiar to
psychical research, as tentative unproved hypotheses in the
same category as the ether.

The best example of the first class is afforded by telepathy.
We know that the consciousnesses which, if our hypothesis is
correct, act upon one another, do exist; and I see no \emph{logical} difference
between the problem of establishing a law of telepathy and
that of establishing the law of gravitation. There is at present a
\emph{practical} difference on account of the much narrower scope of our
knowledge, in the case of telepathy, of cognate matters. We can,
therefore, be much less certain; but there seems no reason why
we should necessarily remain less certain after more evidence
has been accumulated. It is important to remember that, in
the case of telepathy, we are merely discovering a relation between
objects \emph{which we already know to exist}.

The best example of the other class is afforded by attempts
to attribute psychic phenomena to the agency of `spirits' other
than human beings. Such arguments are weakened at present
by the fact that no phenomena are known, so far as I am aware,
which cannot be explained, though improbably in some cases,
in other ways. But even if phenomena were to be observed of
%% -----File: 312.png---Folio 301-------
\index{James, W., and spirits}%
\index{Probability, and relevant knowledge!spirits@{and spirits}}%
which no known agency could afford even an improbable explanation,
the hypothesis of `spirits' would still lie in the same
logical limbo as the hypothesis of the `ether,' in which they
might be supposed not inappropriately to move.

Such an hypothesis as the existence of `spirits' could only
become substantial if some peculiar method of knowledge were
within our power which would yield us the initial probability
which is demanded. That such a method exists, it is not infrequently
claimed. If we can directly perceive these `spirits,'
as many of those who are described in James's \textit{Varieties of
Religious Experience} think they can, the problem is, logically,
altogether changed. We have, in fact, very much the same kind
of reason, though it may be with less probability, that we have
for believing in the existence of other people. The preceding
paragraph applies only to attempts at proving the existence of
`spirits' from such evidence as is discussed by the Society for
Psychical Research.

In between these two extremes comes a class of cases, with
regard to which it is extremely difficult to come to a decision---that
of attempts to attribute psychic phenomena to the conscious
agency of the dead. I wish to discuss here, not the nature of the
existing evidence, but the question whether it is possible for
\emph{any} evidence to be convincing. In this case the object whose
existence we are endeavouring to demonstrate resembles \emph{in
many respects} objects which we know to exist. The question
of epistemology, which is before us, is this: Is it necessary, in
order that we may have an initial probability, that the object of
our hypothesis should resemble in every relevant particular
some \emph{one} object which we know to exist, or is it sufficient that we
should know instances of all its supposed qualities, though never
in combination? It is clear that \emph{some} qualities may be irrelevant---position
in time and space, for example---and that `every
\index{Space!irrelevance of}%
\index{Time!irrelevance of}%
relevant particular' need not include these. But can the initial
probability exist if our hypothesis assumes qualities, which have
plainly some degree of relevance, in \emph{new} combinations? If we
have no knowledge of consciousness existing apart from a living
body, can \emph{indirect} evidence of whatever character afford us any
probability of such a thing? Could any evidence, for example,
persuade us that a tree felt the emotion of amusement, even if
it laughed repeatedly when we made jokes? Yet the analogy
%% -----File: 313.png---Folio 302-------
\index{Calculus of Probability!Psychical Research@{and Psychical Research}}%
\index{Measurement of Probability!psychical research@{and psychical research}}%
\index{Occurrences, remarkable}%
\index{Remarkableness}%
which we demand seems to be a matter of degree; for it does not
seem unreasonable to attribute consciousness to dogs, although
this constitutes a combination of qualities unlike in many respects
to any which we \emph{know} to exist.

This discussion, however, is wandering from the subject of
probability to that of epistemology, and it will not be solved until
\index{Epistemology}%
we possess a more comprehensive account of this latter subject
than we have at present. I wish only to distinguish between those
cases in which we obtain the initial probability in the same
manner as in physical science from those in which we must get
it, if at all, in some other way. The distinctions I have made
are sufficiently summarised by a recapitulation of the following
comparisons: We compared the proof of telepathy to the proof
of gravitation, the proof of non-human `spirits' to the proof
of the ether, and, much less closely, the proof of the consciousness
of the dead to the proof of the consciousness of trees, or, perhaps,
of dogs.

Before passing to the next of the rather miscellaneous topics
of this chapter, it may be worth while to add that we should be
very chary of applying to problems of psychical research the
\emph{calculus} of probabilities. The alternatives seldom satisfy the
conditions for the application of the Principle of Indifference,
\index{Principle of Indifference!Psychical Research@{and Psychical Research}}%
and the initial probabilities are not capable of being measured
numerically. If, therefore, we endeavour to \emph{calculate} the probability
that some phenomenon is due to `abnormal' causes,
our mathematics will be apt to lead us into unjustifiable
conclusions.

\Paragraph{6.} Uninstructed common sense seems to be specially unreliable
in dealing with what are termed `remarkable occurrences.'
Unless a `remarkable occurrence' is simply one which produces
on us a particular psychological effect, that of surprise, we can
only define it as an event which \emph{before} its occurrence is very improbable
on the available evidence. But it will often occur---whenever,
in fact, our \textit{data} leave open the possibility of a large
number of alternatives and show no preference for any of them---that
\emph{every} possibility is exceedingly improbable \textit{à~priori}. It
follows, therefore, that what actually occurs does not derive any
peculiar significance merely from the fact of its being `remarkable'
in the above sense. Something further is required before we
can build with success. Yet Michell's argument and the argument
\index{Michell}%
%% -----File: 314.png---Folio 303-------
\index{Calculus of Probability}%
from design derive a good deal of their plausibility, I think,
from the `remarkable' character of the actual constitution
whether of the heavens or of the universe, in forgetfulness of the
fact that it is impossible to propound \emph{any} constitution which
would if it existed be other than `remarkable.' It is supposed
that a remarkable occurrence is specially in need of an explanation,
and that any \emph{sufficient} explanation has a high probability
in its favour. That an explanation is particularly required,
possesses a measure of truth; for it is likely that our original
\textit{data} were much lacking in completeness, and the occurrence of
the extraordinary event brings to light this deficiency. But
that we are not justified in adopting with confidence any sufficient
explanation, has been shown already.

Such arguments, however, get a part of their plausibility from
a quite different source. There is a general supposition that some
kinds of occurrences are more likely than others to be \emph{susceptible}
of an explanation \emph{by us}; and, therefore, any explanation which
deals with such cases falls in prepared soil. Results which,
judging from ourselves, conscious agents would be likely to produce
fall into this category. Results which would be probable,
supposing a direct and predominant causal dependence between
the elements whose concomitance is remarked, belong to it also.
There is, in fact, a sort of argument from analogy as to whether
certain sorts of phenomena are or are not likely to be due to
`chance.' This may explain, for example, why the particular
concurrence of atoms that go to compose the human eye, why a
series of correct guesses in naming playing cards, why special
symmetry or special asymmetry amongst the stars, seem to
require explanation in no ordinary degree. \emph{Prior} to an explanation
these particular concurrences or series or distributions are
no more improbable than any other. But the causes of such
conjunctions as these are more likely to be discoverable by the
human mind than are the causes of others, and the attempt to
explain them deserves, therefore, to be more carefully considered.
This supposition, derived by analogy or induction from those
cases in which we believe the causes to be known to us, has, perhaps,
some weight. But the direct application of the Calculus
of Probabilities can do no more in these cases than suggest matter
for investigation. The fact that a man has made a long series
of correct guesses in cases where he is cut off from the ordinary
%% -----File: 315.png---Folio 304-------
channels of communication, is a fact worthy of investigation,
because it is more likely to be susceptible of a \emph{simple} causal explanation,
which may have many applications, than a case in
which false and true guesses follow one another with no apparent
regularity.

\Paragraph{7.} In the case of empirical laws, such as Bode's law, which have
\index{Bode's Law}%
no more than a very slight connection with the general body of
scientific knowledge, it is sometimes thought that the law is more
probable if it is proposed \emph{before} the examination of some or all of
the available instances than if it is proposed after their examination.
Supposing, for example, that Bode's law is accurately
true for seven planets, it is held that the law would be more
probable if it was suggested after the examination of six and
was confirmed by the subsequent discovery of the seventh, than
it would be if it had not been propounded until after all seven
had been observed. The arguments in favour of such a conclusion
\index{Peirce}%
are well put by Peirce:\footnote
  {C.~S. Peirce, \textit{A Theory of Probable Inference}, pp.~162--167; published in
Johns Hopkins \textit{Studies in Logic}, 1883.}
``All the qualities of objects may be
conceived to result from variations of a number of continuous
variables; hence any lot of objects possesses some character in
common, not possessed by any other.'' Hence if the common
character is not predesignate we can conclude nothing. Cases
must not be used to prove a generalisation which has only been
suggested by the cases themselves. He takes the first five poets
from a biographical dictionary with their ages at death:
\begin{center}
\setlength{\TmpLen}{1.5in}
\begin{tabular}{p{\TmpLen}@{}r<{\quad}|>{\quad}p{\TmpLen}@{}r}
Aagard  \dotfill & 48 & Abunowas \dotfill & 48\\
Abeille \dotfill & 76 & Accords  \dotfill & 45\\
Abulola \dotfill & 84 &                   & \\
\end{tabular}
\end{center}

\hspace*{16pt}%[** TN: Must match Subpars item width]
``These five ages have the following characters in common:
\begin{Subpars}
\item[``1.] The difference of the two digits composing the number,
divided by three, leaves a remainder of \emph{one}.

\item[``2.] The first digit raised to the power indicated by the second,
and then divided by three, leaves a remainder of \emph{one}.

\item[``3.] The sum of the prime factors of each age, including \emph{one} as
a prime factor, is divisible by \emph{three}.''
\end{Subpars}

He compares a generalisation regarding the ages of poets based
%% -----File: 316.png---Folio 305-------
\index{Playfair, Dr.\ Lyon}%
\index{Prediction, value of}%
on this evidence to Dr.~Lyon Playfair's argument about the
specific gravities of the three allotropic forms of carbon:
\begin{center}
\setlength{\TmpLen}{2in}
\begin{tabular}{p{\TmpLen}@{}l}
Diamond  \dotfill & $3.48 = \sqrt[2]{12}$ \\
Graphite \dotfill & $2.29 = \sqrt[3]{12}$ \\
Charcoal \dotfill & $1.88 = \sqrt[4]{12}$
\end{tabular}
\end{center}
approximately, the atomic weight of carbon being~$12$. Dr.~Playfair
thinks that the above renders it probable that the specific
gravities of the allotropic forms of other elements would, if we
knew them, be found to equal the different roots of their atomic
weight.

The weakness of these arguments, however, has a different
explanation. These inductions are very improbable, because they
are out of relation to the rest of our knowledge and are based on
a very small number of instances. The apparent absurdity,
moreover, of the inductive law of Poets' Ages is increased by the
fact that we take account of the knowledge we actually possess
that the ages of poets are not in fact connected by any such law.
If we knew nothing whatever about poets' ages except what is
stated above, the induction would be as valid as any other which
is based on a very weak analogy and a very small number of
instances and is unsupported by indirect evidence.

The peculiar virtue of prediction or predesignation is altogether
imaginary. The number of instances examined and the analogy
between them are the essential points, and the question as to
whether a particular hypothesis happens to be propounded before
or after their examination is quite irrelevant. If all our inductions
had to be thought of before we examined the cases to
which we apply them, we should, doubtless, make fewer inductions;
but there is no reason to think that the few we should make
would be any better than the many from which we should be
precluded. The plausibility of the argument is derived from a
different source. If an hypothesis is proposed \textit{à~priori}, this
commonly means that there is some ground for it, arising out of
our previous knowledge, \emph{apart from} the purely inductive ground,
and if such is the case the hypothesis is clearly stronger than one
which reposes on inductive grounds only. But if it is a mere
guess, the lucky fact of its preceding some or all of the cases which
verify it adds nothing whatever to its value. It is the union of
%% -----File: 317.png---Folio 306-------
\index{Statistics, and prediction}%
prior knowledge, with the inductive grounds which arise out of
the immediate instances, that lends weight to an hypothesis, and
not the occasion on which the hypothesis is first proposed. It is
sometimes said, to give another example, that the daily fulfilment
of the predictions of the \textit{Nautical Almanack} constitutes the most
cogent proof of the laws of dynamics. But here the essence of
the verification lies in the variety of cases which can be brought
accurately under our notice by means of the \textit{Almanack}, and in
the fact that they have all been obtained on a uniform principle,
\emph{not} in the fact that the verification is preceded by a prediction.

The same point arises not uncommonly in statistical inquiries.
If a theory is first proposed and is then confirmed by the examination
of statistics, we are inclined to attach more weight to it than
to a theory which is constructed in order to suit the statistics.
But the fact that the theory which precedes the statistics is more
likely than the other to be supported by general considerations---for
it has not, presumably, been adopted for no reason at all---constitutes
the only valid ground for this preference. If it does
\emph{not} receive more support than the other from general considerations,
then the circumstances of its origin are no argument in its
favour. The opposite view, which the unreliability of some
statisticians has brought into existence,---that it is a positive
advantage to approach statistical evidence \emph{without} preconceptions
based on general grounds, because the temptation to `cook'
the evidence will prove otherwise to be irresistible,---has no
\emph{logical} basis and need only be considered when the impartiality of
an investigator is in doubt.
%% -----File: 318.png---Folio 307-------
\index{Belief, rational}%
\index{Conduct and Probability}%
\index{Ethics|ifoll}%
\index{Probability, and relevant knowledge!ethics@{and ethics}}%


\Chapter{XXVI}{The Application of Probability to Conduct}

\Paragraph{1.} \First{Given} as our basis what knowledge we actually have, the
probable, I have said, is that which it is rational for us to believe.
This is not a definition. For it is not rational for us to believe
that the probable is true; it is only rational to have a probable
belief in it or to believe it in preference to alternative beliefs. To
believe one thing \emph{in preference} to another, as distinct from believing
the first true or more probable and the second false or less probable,
must have reference to action and must be a loose way of expressing
the propriety of \emph{acting} on one hypothesis rather than
on another. We might put it, therefore, that the probable is
the hypothesis on which it is rational for us to act. It is, however,
not so simple as this, for the obvious reason that of two hypotheses
it may be rational to act on the less probable if it leads to the
greater good. We cannot say more at present than that the
probability of a hypothesis is one of the things to be determined
and taken account of before acting on it.

\Paragraph{2.} I do not know of passages in the ancient philosophers which
explicitly point out the dependence of the duty of pursuing
goods on the reasonable or probable expectation of attaining
them relative to the agent's knowledge. This means only that
analysis had not disentangled the various elements in rational
action, not that common sense neglected them. Herodotus
\index{Herodotus}%
puts the point quite plainly. ``There is nothing more profitable
for a man,'' he says, ``than to take good counsel with himself;
for even if the event turns out contrary to one's hope, still one's
decision was right, even though fortune has made it of no effect:
whereas if a man acts contrary to good counsel, although by luck
he gets what he had no right to expect, his decision was not any
the less foolish.''\footnote
  {Herod.\ vii.~10.}
%% -----File: 319.png---Folio 308-------
\index{Jesuits}%
\index{Taylor, Jeremy|inote}%

\Paragraph{3.} The first contact of theories of probability with modern
ethics appears in the Jesuit doctrine of probabilism. According
\index{Probabilism}%
to this doctrine one is justified in doing an action for which there
is \emph{any} probability, however small, of its results being the best
possible. Thus, if any priest is willing to permit an action, that
fact affords some probability in its favour, and one will not be
damned for performing it, however many other priests denounce
it.\footnote
  {Compare with this doctrine the following curious passage from Jeremy
  Taylor:---``We being the persons that are to be persuaded, we must see that
  we be persuaded reasonably. And it is unreasonable to assent to a lesser
  evidence when a greater and clearer is propounded: but of that every man for
  himself is to take cognisance, if he be able to judge; if he be not, he is not
  bound under the tie of necessity to know anything of it. That that is
  necessary shall be certainly conveyed to him: God, that best can, will certainly
  take care for that; for if he does not, it becomes to be not necessary; or if it
  should still remain necessary, and he be damned for not knowing it, and yet to
  know it be not in his power, then who can help it! There can be no further
  care in this business.''}
It may be suspected, however, that the object of this
doctrine was not so much duty as safety. The priest who permitted
you so to act assumed thereby the responsibility. The
correct application of probability to conduct naturally escaped
the authors of a juridical ethics, which was more interested in
the fixing of responsibility for definite acts, and in the various
specified means by which responsibility might be disposed of,
than in the greatest possible sum-total of resultant good.

A more correct doctrine was brought to light by the efforts of
the philosophers of the Port Royal to expose the fallacies of probabilism.
``In order to judge,'' they say, ``of what we ought to
do in order to obtain a good and to avoid an evil, it is necessary
to consider not only the good and evil in themselves, but also
the probability of their happening and not happening, and to
regard geometrically the proportion which all these things have,
taken together.''\footnote
  {\textit{The Port Royal Logic} (1662), Eng.\ Trans.\ p.~367.}
\index{Port Royal logic!probabilism@{and probabilism}}%
Locke perceived the same point, although
\index{Locke}%
not so clearly.\footnote
  {\textit{Essay concerning Human Understanding}, book~ii.\ chap.~xxi.\ §\;66.}
By Leibniz this theory is advanced more
\index{Leibniz}%
explicitly; in such judgments, he says, ``as in other estimates
disparate and heterogeneous and, so to speak, of more than one
dimension, the greatness of that which is discussed is in reason
composed of both estimates (\ie\ of goodness and of probability),
and is like a rectangle, in which there are two considerations,
viz.\ that of length and that of breadth\ldots. Thus we should
%% -----File: 320.png---Folio 309-------
\index{Butler, Bishop}%
\index{Moore, G. E.}%
still need the art of thinking and that of estimating probabilities,
besides the knowledge of the value of goods and evils, in order
properly to employ the art of consequences.''\footnote
  {\textit{Nouveaux Essais}, book~ii.\ chap.~xxi.}

In his preface to the \textit{Analogy} Butler insists on ``the absolute
and formal obligation'' under which even a low probability,
if it is the greatest, may lay us: ``To us probability is the very
guide of life.''

\Paragraph{4.} With the development of a utilitarian ethics largely concerned
with the summing up of consequences, the place of probability
in ethical theory has become much more explicit. But
although the general outlines of the problem are now clear, there
are some elements of confusion not yet dispersed. I will deal with
some of them.

In his \textit{Principia Ethica} (p.~152) Dr.~Moore argues that ``the
first difficulty in the way of establishing a probability that one
course of action will give a better total result than another, lies
in the fact that we have to take account of the effects of both
throughout an infinite future\ldots. We can certainly only pretend
to calculate the effects of actions within what may be called an
`immediate future.'\ldots\ We must, therefore, certainly have
some reason to believe that no consequences of our action in a
further future will generally be such as to reverse the balance of
good that is probable in the future which we can foresee. This
large postulate must be made, if we are ever to assert that the
results of one action will be even probably better than those of
another. Our utter ignorance of the far future gives us no justification
for saying that it is even probably right to choose the
greater good within the region over which a probable forecast
may extend.''

This argument seems to me to be invalid and to depend on
a wrong philosophical interpretation of probability. Mr.~Moore's
reasoning endeavours to show that there is not even a \emph{probability}
by showing that there is not a \emph{certainty}. We must not, of course,
have reason to believe that remote consequences will \emph{generally}
be such as to reverse the balance of immediate good. But we
need not be certain that the opposite is the case. If good is
additive, if we have reason to think that of two actions one produces
more good than the other in the near future, and if we have
no means of discriminating between their results in the distant
%% -----File: 321.png---Folio 310-------
\index{Butler, Bishop}%
\index{Goodness, organic nature of}%
future, then by what seems a legitimate application of the
Principle of Indifference we may suppose that there is a probability
\index{Principle of Indifference!ethics@{and ethics}}%
in favour of the former action. Mr.~Moore's argument
must be derived from the empirical or frequency theory of
probability, according to which we must know for certain what
will happen \emph{generally} (whatever that may mean) before we can
assert a probability.

The results of our endeavours are very uncertain, but we have
a genuine probability, even when the evidence upon which it is
founded is slight. The matter is truly stated by Bishop Butler:
``From our short views it is greatly uncertain whether this
endeavour will, in particular instances, produce an overbalance
of happiness upon the whole; since so many and distant things
must come into the account. And that which makes it our duty
is that there is some appearance that it will, and no positive
appearance to balance this, on the contrary side\ldots.''\footnote
  {This passage is from the \emph{Analogy}. The Bishop adds: ``\ldots\ and also
  that such benevolent endeavour is a cultivation of that most excellent of all
  virtuous principles, the active principle of benevolence.''}

The difficulties which exist are not chiefly due, I think, to our
ignorance of the remote future. The possibility of our knowing
that one thing rather than another is our duty depends upon the
assumption that a greater goodness in any part makes, in the
absence of evidence to the contrary, a greater goodness in the
whole more probable than would the lesser goodness of the part.
We assume that the goodness of a part is \emph{favourably} relevant to
the goodness of the whole. Without this assumption we have no
reason, not even a probable one, for preferring one action to any
other on the whole. If we suppose that goodness is always
\emph{organic}, whether the whole is composed of simultaneous or
successive parts, such an assumption is not easily justified. The
case is parallel to the question, whether physical law is organic or
atomic, discussed in \Chapref{XXI}. §\;6.

Nevertheless we can admit that goodness is partly organic
and still allow ourselves to draw probable conclusions. For the
alternatives, that \emph{either} the goodness of the whole universe
throughout time is organic \emph{or} the goodness of the universe is the
arithmetic sum of the goodnesses of infinitely numerous and
infinitely divided parts, are not exhaustive. We may suppose
that the goodness of conscious persons is organic for each distinct
%% -----File: 322.png---Folio 311-------
\index{Couturat|inote}%
\index{Law|inote}%
\index{Measurement of Probability}%
\index{Measurement of Probability!ethics@{and ethics}}%
and individual personality. Or we may suppose that, when
conscious units are in conscious relationship, then the whole
which we must treat as organic includes both units. These are
only examples. We must suppose, in general, that the units
whose goodness we must regard as organic and indivisible are
not always larger than those the goodness of which we can
perceive and judge directly.

\Paragraph{5.} The difficulties, however, which are most fundamental
from the standpoint of the student of probability, are of a different
kind. Normal ethical theory at the present day, if there can be
said to be any such, makes two assumptions: first, that degrees
of goodness are numerically measurable and arithmetically
additive, and second, that degrees of probability also are numerically
measurable. This theory goes on to maintain that what
we ought to add together, when, in order to decide between two
courses of action, we sum up the results of each, are the `mathematical
expectations' of the several results. `Mathematical
expectation' is a technical expression originally derived from the
scientific study of gambling and games of chance, and stands for
the product of the possible gain with the probability of attaining
it.\footnote
  {Priority in the conception of mathematical expectation can, I think, be
\index{Mathematical Expectation}%
  claimed by Leibniz, \textit{De incerti aestimatione,} 1678 (Couturat, \textit{Logigue de Leibniz},
  p.~248). In a letter to Placcius, 1687 (Dutens, vi.~i.~36 and Couturat, \textit{op.~cit.}\
  p.~246) Leibniz proposed an application of the same principle to jurisprudence,
  by virtue of which, if two litigants lay claim to a sum of money,
  and if the claim of the one is twice as probable as that of the other, the sum
  should be divided between them in that proportion. The doctrine, seems
  sensible, but I am not aware that it has ever been acted on\DPtypo{}{.}}
In order to obtain, therefore, a measure of what ought to
be our preference in regard to various alternative courses of action,
we must sum for each course of action a series of terms made
up of the amounts of good which may attach to each of its
possible consequences, each multiplied by its appropriate probability.

The first assumption, that quantities of goodness are duly
subject to the laws of arithmetic, appears to me to be open to a
certain amount of doubt. But it would take me too far from
my proper subject to discuss it here, and I shall allow, for the
purposes of further argument, that in some sense and to some
extent this assumption can be justified. The second assumption,
however, that degrees of probability are wholly subject to the
laws of arithmetic, runs directly counter to the view which has
%% -----File: 323.png---Folio 312-------
\index{Intuition \textit{versus} experience!ethical judgment@{and ethical judgment}}%
\index{Weight, of evidence}%
been advocated in Part~I.~of this treatise. Lastly, if both these
points be waived, the doctrine that the `mathematical expectations'
of alternative courses of action are the proper measures of
our degrees of preference is open to doubt on two grounds---first,
because it ignores what I have termed in \Partref{I}. the `weights'
of the arguments, namely, the amount of evidence upon which
each probability is founded; and second, because it ignores the
element of `risk' and assumes that an even chance of heaven
or hell is precisely as much to be desired as the certain attainment
of a state of mediocrity. Putting on one side the first of
these grounds of doubt, I will treat each of the others in turn.

\Paragraph{6.} In \Chapref{III}. of \Partref{I}. I have argued that only in a
strictly limited class of cases are degrees of probability numerically
measurable. It follows from this that the `mathematical
expectations' of goods or advantages are not always numerically
measurable; and hence, that even if a meaning can be given to
the sum of a series of non-numerical `mathematical expectations,'
not every pair of such sums are numerically comparable in respect
of more and less. Thus even if we know the degree of advantage
which might be obtained from each of a series of alternative
courses of actions and know also the probability in each case of
obtaining the advantage in question, it is not always possible by
a mere process of arithmetic to determine which of the alternatives
ought to be chosen. If, therefore, the question of right action is
under all circumstances a determinate problem, it must be in
virtue of an intuitive judgment directed to the situation as a
whole, and not in virtue of an arithmetical deduction derived
from a series of separate judgments directed to the individual
alternatives each treated in isolation.

We must accept the conclusion that, if one good is greater
than another, but the probability of attaining the first less than
that of attaining the second, the question of which it is our duty
to pursue may be indeterminate, unless we suppose it to be
within our power to make direct quantitative judgments of probability
and goodness jointly. It may be remarked, further,
that the difficulty exists, whether the numerical indeterminateness
of the probability is intrinsic or whether its numerical value
is, as it is according to the Frequency Theory and most other
theories, simply unknown.

\Paragraph{7.} The second difficulty, to which attention is called above,
%% -----File: 324.png---Folio 313-------
\index{Bernoulli, Jac.!weight of evidence}%
is the neglect of the `weights' of arguments in the conception
of `mathematical expectation.' In \Chapref{VI}. of \Partref{I}. the
significance of `weight' has been discussed. In the present
connection the question comes to this---if two probabilities are
equal in degree, ought we, in choosing our course of action, to
prefer that one which is based on a greater body of knowledge?

The question appears to me to be highly perplexing, and it is
difficult to say much that is useful about it. But the degree of
completeness of the information upon which a probability is
based does seem to be relevant, as well as the actual magnitude
of the probability, in making practical decisions. Bernoulli's
maxim,\footnote
  {\textit{Ars Conjectandi}, p.~215: ``Non sufficit expendere unum alterumve argumentum,
  sed  conquirenda sunt omnia, quae in cognitionem nostram venire
  possunt, atqne ullo modo ad probationem rei facere videntur.''}
that in reckoning a probability we must take into account
all the information which we have, even when reinforced by
\index{Locke!weight@{and weight of evidence}}%
Locke's maxim that we must get all the information we can,\footnote
  {\textit{Essay concerning Human Understanding}, book~ii.\ chap.~xxi.\ §\;67: ``He
  that judges without informing himself to the utmost that he is capable, cannot
  acquit himself of \emph{judging amiss}.''}
does not seem completely to meet the case. If, for one alternative,
the available information is necessarily small, that does not seem
to be a consideration which ought to be left out of account
altogether.

\Paragraph{8.} The last difficulty concerns the question whether, the
former difficulties being waived, the `mathematical expectation'
of different courses of action accurately measures what our
preferences ought to be---whether, that is to say, the undesirability
of a given course of action increases in direct proportion
to any increase in the uncertainty of its attaining its object, or
whether some allowance ought to be made for `risk,' its undesirability
\index{Risk!ethics@{and ethics}}%
increasing more than in proportion to its uncertainty.

In fact the meaning of the judgment, that we ought to act in
such a way as to produce most probably the greatest sum of
goodness, is not perfectly plain. Does this mean that we
ought so to act as to make the sum of the goodnesses of each of
the possible consequences of our action multiplied by its probability
a maximum? Those who rely on the conception of
`mathematical expectation' must hold that this is an indisputable
proposition. The justifications for this view most commonly
advanced resemble that given by Condorcet in his ``Réflexions
\index{Condorcet!ethics@{and ethics}}%
%% -----File: 325.png---Folio 314-------
sur la règle générale, qui prescrit de prendre pour valeur d'un
événement incertain, la probabilité de cet événement multipliée
par la valeur de l'événement en lui-même,''\footnote
  {\textit{Hist.\ de~l'Acad}., Paris, 1781.}
where he argues
from Bernoulli's theorem that such a rule will lead to satisfactory
\index{Bernoulli's Theorem}%
results if a very large number of trials be made. As, however,
it will be shown in \Chapref{XXIX}. of \Partref{V}. that Bernoulli's
theorem is not applicable in by any means every case, this
argument is inadequate as a general justification.

In the history of the subject, nevertheless, the theory of
`mathematical expectation' has been very seldom disputed.
As D'Alembert has been almost alone in casting serious doubts
\index{D'Alembert!mathematical expectation@{and mathematical expectation}}%
upon it (though he only brought himself into disrepute by doing
so), it will be worth while to quote the main passage in which he
declares his scepticism: ``Il me sembloit'' (in reading Bernoulli's
\textit{Ars Conjectandi}) ``que cette matière avoit besoin d'être traitée
d'une manière plus claire; je voyois bien que l'espérance étoit
plus grande, \Primo~que la somme espérée étoit plus grande, \Secundo~que
la probabilité de gagner l'étoit aussi. Mais je ne voyois pas avec
la même évidence, et je ne le vois pas encore, \Primo~que la probabilité
soit estimée exactement par les méthodes usitées; \Secundo~que quand
elle le seroit, l'espérance doive être proportionnelle à cette probabilité
simple, plutôt qu'à une puissance ou même à une fonction
de cette probabilité; \Tertio~que quand il y a plusieurs combinaisons
qui donnent différens avantages ou différens risques (qu'on
regarde comme des avantages négatifs) il faille se contenter
d'\emph{ajouter} simplement ensemble toutes les espérances pour avoir
l'espérance totale.''\footnote
  {\textit{Opuscules mathématiques}, vol.~iv., 1768 (extraits de lettres), pp.~284,~285.
  See also p.~88 of the same volume.}

In extreme cases it seems difficult to deny some force to
D'Alembert's objection; and it was with reference to extreme
cases that he himself raised it. Is it certain that a larger good,
which is extremely improbable, is precisely equivalent ethically
to a smaller good which is proportionately more probable? We
may doubt whether the moral value of speculative and cautious
action respectively can be weighed against one another in a
simple arithmetical way, just as we have already doubted whether
a good whose probability can only be determined on a slight
basis of evidence can be compared by means merely of the
%% -----File: 326.png---Folio 315-------
\index{Weight, of evidence!ethics@{and ethics}}%
magnitude of this probability with another good whose likelihood
is based on completer knowledge.

There seems, at any rate, a good deal to be said for the conclusion
that, other things being equal, that course of action is
preferable which involves least risk, and about the results of
\index{Risk}%
which we have the most complete knowledge. In marginal cases,
therefore, the coefficients of weight and risk as well as that
of probability are relevant to our conclusion. It seems natural
to suppose that they should exert some influence in other cases
also, the only difficulty in this being the lack of any principle for
the calculation of the degree of their influence. A high weight
and the absence of risk increase \textit{pro tanto} the desirability of the
action to which they refer, but we cannot measure the amount
of the increase.

The `risk' may be defined in some such way as follows. If
$A$~is the amount of good which may result, $p$~its probability
$(p+q=1)$, and $E$~the value of the `mathematical expectation,'
\index{Mathematical Expectation}%
so that $E=pA$, then the `risk' is~$R$, where $R = p(A-E) =
p(1-p)A = pqA = qE$. This may be put in another way: $E$~measures
the net immediate sacrifice which should be made in the
hope of obtaining~$A$; $q$~is the probability that this sacrifice will
be made in vain; so that $qE$~is the `risk.'\footnote
  {The theory of \textit{Risiko} is briefly dealt with by Czuber, \textit{Wahrscheinlichkeitsrechnung},
\index{Czuber!risk@{and risk}|inote}%
  vol.~i.\ pp.~219 \textit{et seq}. If $R$~measures the first insurance, this leads to a
  \textit{Risiko} of the second order, $R_1 = qR = q^2E$. This again may be insured against,
  and by a sufficient number of such reinsurances the risk can be completely
  shifted:
  \[
  E + R_1 + R_2 + \ldots
    = E(1 + q + q^2 + \ldots) = \frac{E}{1-q} = \frac{E}{p} = A.
  \]}
The ordinary theory
supposes that the ethical value of an expectation is a function
of~$E$ only and is entirely independent of~$R$.

We could, if we liked, define a conventional coefficient~$c$ of
weight and risk, such as $c=\dfrac{2pw}{(1+q)(1+w)}$, where $w$~measures the
`weight,' which is equal to unity when $p=1$ and $w=1$, and
to zero when $p=0$ or $w=0$, and has an intermediate value
in other cases.\footnote
  {If $pA = p'A'$, $w>w'$, and $q=q'$, then $cA>c'A'$; if $pA=p'A'$, $w=w'$, and
  $q<q'$, then $cA>c'A'$; if $pA=p'A'$, $w>w'$, and $q<q'$, then $cA>c'A'$; but if
  $pA=p'A'$, $w=w'$, and $q>q'$, we cannot in general compare $cA$ and $c'A'$.}
But if doubts as to the sufficiency of the
conception of `mathematical expectation' be sustained, it is not
likely that the solution will lie, as D'Alembert suggests, and as
has been exemplified above, in the discovery of some more
%% -----File: 327.png---Folio 316-------
\index{Apprehension, direct, and ethical judgment}%
\index{Bernoulli, Daniel, and Inverse Probability!Petersburg Paradox@{and Petersburg Paradox}}%
\index{D'Alembert!ethics@{and ethics}}%
\index{Mathematicians, and probability!ethics@{and ethics}}%
complicated function of the probability wherewith to compound
the proposed good. The judgment of goodness and the judgment
of probability both involve somewhere an element of direct
apprehension, and both are quantitative. We have raised a
doubt as to whether the magnitude of the `oughtness' of an
action can be in all cases directly determined by simply multiplying
together the magnitudes obtained in the two direct judgments;
and a new direct judgment may be required, respecting
the magnitude of the `oughtness' of an action under given
circumstances, which need not bear any simple and necessary
relation to the two former.

The hope, which sustained many investigators in the course
of the nineteenth century, of gradually bringing the moral sciences
under the sway of mathematical reasoning, steadily recedes---if
we mean, as they meant, by mathematics the introduction of
precise numerical methods. The old assumptions, that all
quantity is numerical and that all quantitative characteristics
are additive, can be no longer sustained. Mathematical reasoning
now appears as an aid in its symbolic rather than in its numerical
character. I, at any rate, have not the same lively hope as
Condorcet, or even as Edgeworth, ``éclairer les Sciences morales
\index{Condorcet!ethics@{and ethics}}%
\index{Edgeworth!ethics@{and ethics}}%
et politiques par le flambeau de l'Algèbre.'' In the present case,
even if we are able to range goods in order of magnitude, and also
their probabilities in order of magnitude, yet it does not follow
that we can range the products composed of each good and its
corresponding probability in this order.

\Paragraph{9.} Discussions of the doctrine of Mathematical Expectation,
\index{Mathematical Expectation}%
apart from its directly ethical bearing, have chiefly centred
\index{Petersburg Paradox}%
round the classic Petersburg Paradox,\Pagelabel{316}\footnote
  {For the history of this paradox see Todhunter. The name is due, he says,
\index{Todhunter!Petersburg Paradox@{and Petersburg Paradox}}%
  to its having first appeared in a memoir by Daniel Bernoulli in the \textit{Commentarii}
  of the Petersburg Academy.}
which has been treated by
almost all the more notable writers, and has been explained by
them in a great variety of ways. The Petersburg Paradox arises
out of a game in which Peter engages to pay Paul one shilling
if a head appears at the first toss of a coin, two shillings if it does
not appear until the second, and, in general, $2^{r-1}$~shillings if no
head appears until the $r$\ordth~toss.\DPnote{** TN: Ordinal not ital in orig.} What is the value of Paul's
expectation, and what sum must he hand over to Peter before
the game commences, if the conditions are to be fair?
%% -----File: 328.png---Folio 317-------
\index{Bernoulli, Daniel, and Inverse Probability!Petersburg Paradox@{and Petersburg Paradox}}%

The mathematical answer is $\Sum_{1}^{n}(\frac{1}{2})^r2^{r-1}$, if the number of tosses
is not in any case to exceed $n$~in all, and $\Sum_{1}^{\infty}(\frac{1}{2})^r2^{r-1}$ if this restriction
is removed. That is to say, Paul should pay $\dfrac{n}{2}$~shillings in the
first case, and an infinite sum in the second. Nothing, it is said,
could be more paradoxical, and no sane Paul would engage on
these terms even with an honest Peter.

Many of the solutions which have been offered will occur at
once to the reader. The conditions of the game \emph{imply} contradiction,
say Poisson and Condorcet; Peter has undertaken
\index{Condorcet}%
\index{Poisson!Petersburg Paradox@{and Petersburg Paradox}}%
engagements which he cannot fulfil; if the appearance of heads
is deferred even to the $100$th~toss, he will owe a mass of silver
greater in bulk than the sun. But this is no answer. Peter has
promised much and a belief in his solvency will strain our imagination;
but it is imaginable. And in any case, as Bertrand points
\index{Bertrand!Petersburg Paradox@{and Petersburg Paradox}}%
out, we may suppose the stakes to be, not shillings, but grains of
sand or molecules of hydrogen.

D'Alembert's principal explanations are, first, that true expectation
\index{D'Alembert!Petersburg Paradox@{and Petersburg Paradox}}%
is not necessarily the product of probability and
profit (a view which has been discussed above), and second, that
very long runs are not only very improbable, but do not occur
at all.

The\Pagelabel{317} next type of solution is due, in the first instance, to Daniel
Bernoulli, and turns on the fact that no one but a miser regards
the desirability of different sums of money as directly proportional
to their amount; as Buffon says, ``L'avare est comme le
\index{Buffon}%
mathématicien: tous deux estiment l'argent par sa quantité
numérique.'' Daniel Bernoulli deduced a formula from the
assumption that the importance of an increment is inversely
proportional to the size of the fortune to which it is added.
Thus, if $x$~is the `physical' fortune and $y$~the `moral' fortune,
\[
dy = k\, \frac{dx}{x},
\]
or $y = k\log\dfrac{x}{a}$, where $k$~and~$a$ are constants.

On the basis of this formula of Bernoulli's a considerable
%% -----File: 329.png---Folio 318-------
\index{Cramer and Petersburg Paradox}%
\index{Petersburg Paradox!psychology of}%
\index{Todhunter|inote}%
theory has been built up both by Bernoulli\footnote
  {``Specimen Theoriae Novae de Mensura Sortis,'' \textit{Comm.\ Acad.\ Petrop.}\
  vol.~v.\ for 1730 and~1731, pp.~175--192 (published 1738). See Todhunter,
  pp.~213 \textit{et~seq}.}
himself and by
\index{Laplace}%
Laplace.\footnote
  {\textit{Théorie analytique}, chap.~x.\ ``De l'espérance morale,'' pp.~432--445.}
It leads easily to the further formula---
\[
x = (a+x_1)p_1(a+x_2)p_2\ldots,
\]
where $a$ is the initial `physical' fortune, $p_1$,~etc., the probabilities
of obtaining increments $x_1$,~etc., to~$a$, and $x$~the `physical' fortune
whose present possession would yield the same `moral' fortune
as does the expectation of the various increments $x_1$,~etc. By
means of this formula Bernoulli shows that a man whose fortune
is £$1000$ may reasonably pay a £$6$~stake in order to play the
Petersburg game with £$1$~units. Bernoulli also mentions two
solutions proposed by Cramer. In the first all sums greater
than~$2^{24}$ ($16,777,116$) are regarded as `morally' equal; this
leads to~£$13$ as the fair stake. According to the other formula
the pleasure derivable from a sum of money varies as the square
root of the sum; this leads to £$2:9$s.\ as the fair stake. But
little object is served by following out these arbitrary hypotheses.

As a solution of the Petersburg problem this line of thought
is only partially successful: if increases of `physical' fortune
beyond a certain finite limit can be regarded as `morally'
negligible, Peter's claim for an infinite initial stake from Paul is,
it is true, no longer equitable, but with any reasonable law of
diminution for successive increments Paul's stake will still remain
paradoxically large. Daniel Bernoulli's suggestion is, however,
of considerable historical interest as being the first explicit
attempt to take account of the important conception known to
modern economists as the diminishing marginal utility of money,---a
\index{Marginal utility}%
conception on which many important arguments are founded
relating to taxation and the ideal distribution of wealth.

Each of the above solutions probably contains a part of the
psychological explanation. We are unwilling to be Paul, partly
because we do not believe Peter will pay us if we have good
fortune in the tossing, partly because we do not know what we
should do with so much money or sand or hydrogen if we won it,
partly because we do not believe we ever should win it, and
partly because we do not think it would be a rational act to risk
%% -----File: 330.png---Folio 319-------
\index{Bernoulli's Theorem|inote}%
\index{Bradley|inote}%
\index{Laurent and gambling}%
an infinite sum or even a very large finite sum for an infinitely
larger one, whose attainment is infinitely unlikely.

When we have made the proper hypotheses and have eliminated
these elements of psychological doubt, the theoretic dispersal
of what element of paradox remains must be brought about, I
think, by a development of the theory of risk. It is primarily
\index{Risk!Petersburg Paradox@{and Petersburg Paradox}}%
the great \emph{risk} of the wager which deters us. Even in the case
where the number of tosses is in no case to exceed a finite number,
the risk~$R$, as already defined, may be very great, and the relative
risk~$\dfrac{R}{E}$ will be almost unity. Where there is no limit to the
number of tosses, the risk is infinite. A relative risk, which
approaches unity, may, it has been already suggested, be a factor
which must be taken into account in ethical calculation.

\Paragraph{10.} In establishing the doctrine, that all private gambling
\index{Gambling}%
must be with certainty a losing game, precisely contrary arguments
are employed to those which do service in the Petersburg
problem. The argument that ``you must lose if only you go on
long enough'' is well known. It is succinctly put by Laurent:\footnote
  {\textit{Calcul des probabilités}, p.~129.}
Two players $A$~and~$B$ have $a$~and~$b$ francs respectively. $f(a)$~is
the chance that $A$~will be ruined. Thus $f(a)=\dfrac{b}{a+b}$,\footnote
  {This would possibly follow from the theorem of Daniel Bernoulli. The
  reasoning by which Laurent obtains it seems to be the result of a mistake.}
so that
the poorer a gambler is, relatively to his opponent, the more
likely he is to be ruined. But further, if $b=\infty$, $f(a)=1$, \ie~ruin
is certain. The infinitely rich gambler is the public. It is against
the public that the professional gambler plays, and his ruin is
therefore certain.

Might not Poisson and Condorcet reply, The conditions of
\index{Condorcet!gambling@{and gambling}}%
\index{Poisson!gambling@{and gambling}}%
the game \emph{imply} contradiction, for no gambler plays, as this argument
supposes, for ever?\footnote
  {Cf.\ also Mr.~Bradley, \textit{Logic}, p.~217.}
At the end of any \emph{finite} quantity of
play, the player, even if he is not the public, \emph{may} finish with
winnings of any finite size. The gambler is in a worse position if
his capital is smaller than his opponents'---at poker, for instance,
or on the Stock Exchange. This is clear. But our desire for
moral improvement outstrips our logic if we tell him that he
\emph{must} lose. Besides it is paradoxical to say that everybody
%% -----File: 331.png---Folio 320-------
individually must lose and that everybody collectively must win.
For every individual gambler who loses there is an individual
gambler or syndicate of gamblers who win. The true moral is
this, that poor men should not gamble and that millionaires
should do nothing else. But millionaires gain nothing by gambling
with one another, and until the poor man departs from the
path of prudence the millionaire does not find his opportunity.
If it be replied that in fact most millionaires are men originally
poor who departed from the path of prudence, it must be
admitted that the poor man is not doomed with certainty.
Thus the philosopher must draw what comfort he can from the
conclusion with which his theory furnishes him, that millionaires
are often fortunate fools who have thriven on unfortunate
ones.\footnote
  {From the social point of view, however, this moral against gambling may
  be drawn---that those who start with the largest initial fortunes are most likely
  to win, and that a given increment to the wealth of these benefits them, on the
  assumption of a diminishing marginal utility of money, less than it injures those
  from whom it is taken.}

\Paragraph{11.} In conclusion we may discuss a little further the conception
of `moral' risk, raised in §\;8 and at the end of §\;9. Bernoulli's
\index{Risk!moral@{`\textit{moral}'}}%
formula crystallises the undoubted truth that the value of a sum
of money to a man varies according to the amount he already
possesses. But does the value of an amount of goodness also
vary in this way? May it not be true that the addition of a given
good to a man who already enjoys much good is less good than
its bestowal on a man who has little? If this is the case, it
follows that a smaller but relatively certain good is better than
a greater but proportionately more uncertain good.

In order to assert this, we have only to accept a particular
theory of organic goodness, applications of which are common
enough in the mouths of political philosophers. It is at the root
of all principles of equality, which do not arise out of an assumed
diminishing marginal utility of money. It is behind the numerous
arguments that an equal distribution of benefits is better than a
very unequal distribution. If this is the case, it follows that, the
sum of the goods of all parts of a community taken together
being fixed, the organic good of the whole is greater the more
equally the benefits are divided amongst the individuals. If the
doctrine is to be accepted, moral risks, like financial risks, must
not be undertaken unless they promise a profit actuarially.
%% -----File: 332.png---Folio 321-------
\index{Butler, Bishop!risk@{and risk}}%

There is a great deal which could be said concerning such a
doctrine, but it would lead too far from what is relevant to the
study of Probability. One or two instances of its use, however,
may be taken from the literature of Probability. In his essay,
``Sur l'application du calcul des probabilités à l'inoculation de
la petite vérole,''\footnote
  {\textit{Opuscules mathématiques}, vol.~ii.}
D'Alembert points out that the community
\index{D'Alembert}%
would gain on the average if, by sacrificing the lives of one in five
of its citizens, it could ensure the health of the rest, but he argues
that no legislator could have the right to order such a sacrifice.
Galton, in his \textit{Probability, the Foundation of Eugenics}, employed
\index{Galton}%
an argument which depends essentially on the same point.
Suppose that the members of a certain class cause an average
detriment~$M$ to society, and that the mischiefs done by the
several individuals differ more or less from~$M$ by amounts whose
average is~$D$, so that $D$~is the average amount of the individual
deviations, all regarded as positive, from~$M$; then, Galton argued,
the smaller $D$~is, the stronger is the justification for taking such
drastic measures against the propagation of the class as would
be consonant to the feelings, if it were known that each individual
member caused a detriment~$M$. The use of such arguments
seems to involve a qualification of the simple ethical doctrine
that right action should make the sum of the benefits of the
several individual consequences, each multiplied by its probability,
a maximum.

On the other hand, the opposite view is taken in the \textit{Port Royal
Logic} and by Butler, when they argue that everything ought to
be sacrificed for the hope of heaven, even if its attainment be
thought infinitely improbable, since ``the smallest degree of
facility for the attainment of salvation is of higher value than
all the blessings of the world put together.''\footnote
  {\textit{Port Royal Logic} (Eng.\ trans.), p.~369: ``It belongs to infinite things alone,
\index{Port Royal logic}%
  as eternity and salvation, that they cannot be equalled by any temporal advantage;
  and thus we ought never to place them in the balance with any of the
  things of the world. This is why the smallest degree of facility for the attainment
  of salvation is of higher value than all the blessings of the world put
  together\ldots.''}
The argument is,
that we ought to follow a course of conduct which may with the
slightest probability lead to an infinite good, until it is logically
disproved that such a result of our action is impossible. The
Emperor who embraced the Roman Catholic religion, not because
%% -----File: 333.png---Folio 322-------
\index{Bernoulli, Jac.!second axiom of}%
\index{Probability, and relevant knowledge!truth@{and truth}}%
\index{Truth and probability}%
he believed it, but because it offered insurance against a disaster
whose future occurrence, however improbable, he could not
certainly disprove, may not have considered, however, whether
the product of an infinitesimal probability and an infinite good
might not lead to a finite or infinitesimal result. In any case the
argument does not enable us to choose between different courses
of conduct, unless we have reason to suppose that one path is
\emph{more} likely than another to lead to infinite good.

\Paragraph{12.} In estimating the risk, `moral' or `physical,' it must be
\index{Risk!moral@{`\textit{moral}'}}%
\index{Risk!physical@{`\textit{physical}'}}%
remembered that we cannot necessarily apply to individual
cases results drawn from the observation of a long series resembling
them in some particular. I am thinking of such arguments
as Buffon's when he names $\frac{1}{10,000}$ as the limit, beyond
\index{Buffon}%
which probability is negligible, on the ground that, being the
chance that a man of fifty-six \emph{taken at random} will die within a
day, it is practically disregarded by a man of fifty-six \emph{who knows
his health to be good}. ``If a public lottery,'' Gibbon truly pointed
\index{Gibbon}%
out, ``were drawn for the choice of an immediate victim, and if
our name were inscribed on one of the ten thousand tickets,
should we be perfectly easy?''

Bernoulli's second axiom,\footnote
  {See \Pageref{76}.}
that in reckoning a probability
we must take everything into account, is easily forgotten in these
cases of statistical probabilities. The statistical result is so
attractive in its definiteness that it leads us to forget the more
vague though more important considerations which may be, in a
given particular case, within our knowledge. To a stranger the
probability that I shall send a letter to the post unstamped may
be derived from the statistics of the Post Office; for me those
figures would have but the slightest bearing upon the question.

\Paragraph{13.} It has been pointed out already that no knowledge of
probabilities, less in degree than certainty, helps us to know what
conclusions are true, and that there is no direct relation between
the truth of a proposition and its probability. Probability begins
and ends with probability. That a scientific investigation
pursued on account of its probability will generally lead to truth,
rather than falsehood, is at the best only probable. The proposition
that a course of action guided by the most probable
considerations will generally lead to success, is not certainly true
and has nothing to recommend it but its probability.
%% -----File: 334.png---Folio 323-------

The importance of probability can only be derived from the
judgment that it is \emph{rational} to be guided by it in action; and a
practical dependence on it can only be justified by a judgment
that in action we \emph{ought} to act to take some account of it. It is
for this reason that probability is to us the ``guide of life,'' since
to us, as Locke says, ``in the greatest part of our concernment,
\index{Locke}%
God has afforded only the Twilight, as I may so say, of Probability,
suitable, I presume, to that state of Mediocrity and
Probationership He has been pleased to place us in here.''
%% -----File: 335.png---Folio 324-------
%[Blank Page]
%% -----File: 336.png---Folio 325-------


\Part[Statistical Inference]{V}{The Foundations of Statistical
Inference}
%% -----File: 337.png---Folio 326-------
%[Blank Page]
%% -----File: 338.png---Folio 327-------
\index{Statistical inference|ifoll}%
\index{Statistics, and prediction!descriptive and inductive}%


\Chapter{XXVII}{The Nature of Statistical Inference}
\index{Inference!statistical|ifoll}%

\Paragraph{1.} \First{The} Theory of Statistics, as it is now understood,\footnote
  {See Yule, \textit{Introduction to Statistics}, pp.~1--5, for a very interesting account
\index{Yule!statistics@{and `\textit{statistics}'}}%
  of the evolution of the meaning of the term \emph{statistics}.}
can be
divided into two parts which are for many purposes better kept
distinct. The first function of the theory is purely \emph{descriptive}.
It devises numerical and diagrammatic methods by which certain
salient characteristics of large groups of phenomena can be briefly
described; and it provides formulae by the aid of which we can
measure or summarise the variations in some particular character
which we have observed over a long series of events or instances.
The second function of the theory is \emph{inductive}. It seeks to extend
its description of certain characteristics of observed events to
the corresponding characteristics of other events which have not
been observed. This part of the subject may be called the
Theory of Statistical Inference; and it is this which is closely
bound up with the theory of probability.

\Paragraph{2.} The union of these two distinct theories in a single science
is natural. If, as is generally the case, the development of
some inductive conclusion which shall go beyond the actually
observed instances is our ultimate object, we naturally choose
those modes of description, while we are engaged in our preliminary
investigation, which are most capable of extension
beyond the particular instances which they primarily describe.
But this union is also the occasion of a great deal of confusion. The
statistician, who is mainly interested in the technical methods of
his science, is less concerned to discover the precise conditions in
which a description can be legitimately extended by induction.
\index{Induction!statistics@{and statistics}|ifoll}%
He slips somewhat easily from one to the other, and having
found a complete and satisfactory mode of description he
%% -----File: 339.png---Folio 328-------
\index{Frequency curves!statistics@{and statistics}}%
\index{definition of!from statistics}%
may take less pains over the transitional argument, which is
to permit him to use this description for the purposes of
generalisation.

One or two examples will show how easy it is to slip from
description into generalisation. Suppose that we have a series
of similar objects one of the characteristics of which is under
observation;---a number of persons, for example, whose age at
death has been recorded. We note the proportion who die at
each age, and plot a diagram which displays these facts graphically.
We then determine by some method of curve fitting a
mathematical frequency curve which passes with close approximation
through the points of our diagram. If we are given the
equation to this curve, the number of persons who are comprised
in the statistical series, and the degree of approximation (whether
to the nearest year or month) with which the actual age has been
recorded, we have a very complete and succinct account of one
particular characteristic of what may constitute a very large
mass of individual records. In providing this comprehensive
description the statistician has fulfilled his first function. But in
determining the accuracy with which this frequency curve can be
employed to determine the probability of death at a given age
in the population at large, he must pay attention to a new class
of considerations and must display a different kind of capacity.
He must take account of whatever extraneous knowledge may be
available regarding the sample of the population which came
under observation, and of the mode and conditions of the observations
themselves. Much of this may be of a vague kind, and most
of it will be necessarily incapable of exact, numerical, or statistical
treatment. He is faced, in fact, with the normal problems of
inductive science, \emph{one} of the data, which must be taken into
account, being given in a convenient and manageable form by
the methods of descriptive statistics.

Or suppose, again, that we are given, over a series of years,
the marriage rate and the output of the harvest in a certain area
of population. We wish to determine whether there is any
apparent degree of correspondence between the variations of the
two within this field of observation. It is technically difficult to
measure such degree of correspondence as may appear to exist
between the variations in two series, the terms of which are in
some manner associated in couples,---by coincidence, in this case,
%% -----File: 340.png---Folio 329-------
\index{Error, probable}%
\index{Whitehead, and frequency theory!invalid inference@{and invalid inference}|inote}%
of time and place. By the method of correlation tables and
\index{Correlation}%
correlation coefficients the descriptive statistician is able to effect
this object, and to present the inductive scientist with a highly
significant part of his data in a compact and instructive form.
But the statistician has not, in calculating these coefficients of
observed correlation, covered the whole ground of which the inductive
scientist must take cognisance. He has recorded the
results of the observations in circumstances where they cannot
be recorded so clearly without the aid of technical methods; but
the precise nature of the conditions in which the observations
took place and the numerous other considerations of one sort or
another, of which we must take account when we wish to
generalise, are not usually susceptible of numerical or statistical
expression.

The truth of this is obvious; yet, not unnaturally, the more
complicated and technical the preliminary statistical investigations
become, the more prone inquirers are to mistake the statistical
description for an inductive generalisation.\footnote
  {Cf.\ Whitehead, \textit{Introduction to Mathematics}, p.~27: ``There is no more
  common error than to assume that, because prolonged and accurate mathematical
  calculations have been made, the application of the result to some fact
  of nature is absolutely certain.''}
This tendency,
which has existed in some degree, as, I think, the whole history of
the subject shows, from the eighteenth century down to the
present time, has been further encouraged by the terminology in
ordinary use. For several statistical coefficients are given the
same name when they are used for purely descriptive purposes,
as when corresponding coefficients are used to measure the force
or the precision of an induction. The term `probable error,'
for example, is used \emph{both} for the purpose of supplementing
and improving a statistical description, \emph{and} for the
purpose of indicating the precision of some generalisation.
The term `correlation' itself is used \emph{both} to describe an
observed characteristic of particular phenomena \emph{and} in the
enunciation of an inductive law which relates to phenomena
in general.

\Paragraph{3.} I have been at pains to enforce this contrast between
statistical description and statistical induction, because the
chapters which follow are to be entirely about the latter, whereas
nearly all statistical treatises are mainly concerned with the
former. My object will be to analyse, so far as I can, the logical
%% -----File: 341.png---Folio 330-------
\index{Frequency, statistical}%
\index{Great Numbers, Law of}%
basis of statistical modes of argument. This involves a double
task. To mark down those which are invalid amongst arguments
having the support of authority is relatively easy.
The other branch of our investigation, namely, to analyse
the ground of validity in the case of those arguments the
force of which all of us do in fact admit, presents the same
kind of fundamental difficulties as we met with in the case
of Induction.

\Paragraph{4.} The arguments with which we have to deal fall into three
main classes:

(i.) Given the probability relative to certain evidence of each
of a series of events, what are the probabilities, relative to the
same evidence, of various proportionate frequencies of occurrence
for the events over the whole series? Or more briefly, how often
may we expect an event to happen over a series of occasions, given
its probability on each occasion?

(ii.) Given the frequency with which an event has occurred
on a series of occasions, with what probability may we expect it
on a further occasion?

(iii.) Given the frequency with which an event has occurred
on a series of occasions, with what frequency may we probably
expect it on a further series of occasions?

In the first type of argument we seek to infer an unknown
statistical frequency from an \textit{à~priori} probability. In the second
type we are engaged on the inverse operation, and seek to base
the calculation of a probability on an observed statistical frequency.
In the third type we seek to pass from an observed
statistical frequency, not merely to the probability of an individual
occurrence, but to the probable values of other unknown statistical
frequencies.

Each of these types of argument can be further complicated
by being applied not simply to the occurrence of a simple event
but to the concurrence under given conditions of two or more
events. When this two or more dimensional classification replaces
the one dimensional, the theory becomes what is sometimes
termed Correlation, as distinguished from simple Statistical
\index{Correlation!statistical frequency@{and statistical frequency}}%
Frequency.

\Paragraph{5.} In \Chapref{XXVIII}. I touch briefly on the observed
phenomena which have given rise to the so-called Law of
Great Numbers, and the discovery of which first set statistical
%% -----File: 342.png---Folio 331-------
investigation going. In \Chapref{XXIX}. the first type of argument,
as classified above, is analysed, and the conditions which
are required for its validity are stated. The crucial problem
of attacking the second and third types of argument is the
subject of my concluding chapters.
%% -----File: 343.png---Folio 332-------
\index{Halley and mortality statistics}%


\Chapter{XXVIII}{The Law of Great Numbers}

\begin{Quote}
Natura quidem suas habet consuetudines, natas ex reditu causarum, sed non
nisi \textgreek{<ws `ep`i t`o pol'u}. Novi morbi inundant subiande humanum genus, quodsi
ergo de mortibus quotcunque experimenta feceris, non ideo naturae rerum limites
posuisti, ut pro futuro variare non possit.---\textsc{Leibniz} \textit{in a letter to Bernoulli,
December}~3, 1703.
\end{Quote}

\Paragraph{1.} \First{It} has always been known that, while some sets of events
\emph{invariably} happen together, other sets \emph{generally} happen together.
That experience shows one thing, while not always a sign of
another, to be a usual or probable sign of it, must have been one
of the earliest and most primitive forms of knowledge. If a dog
is \emph{generally} given scraps at table, that is sufficient for him to judge
it reasonable to be there. But this kind of knowledge was slow
to be made precise. Numerous experiments must be carefully
recorded before we can know at all accurately \emph{how} usual the
association is. It would take a dog a long time to find out that
he was given scraps except on fast days, and that there was the
same number of these in every year.

The necessary kind of knowledge began to be accumulated
during the seventeenth and eighteenth centuries by the early
statisticians. Halley and others began to construct mortality
tables; the proportion of the births of each sex were tabulated;
and so forth. These investigations brought to light a new fact
which had not been suspected previously---namely, that in certain
cases of partial association the degree of association, \ie~the proportion
of instances in which it existed, shows a very surprising
regularity, and that this regularity becomes more marked the
greater the number of the instances under consideration. It was
found, for example, not merely that boys and girls are born on
the whole in about equal proportions, but that the proportion,
%% -----File: 344.png---Folio 333-------
\index{Bernoulli, Jac.!regular frequency@{and regular frequency}}%
\index{Bortkiewicz, von, and great numbers|inote}%
\index{Great Numbers, Law of|ifoll}%
\index{Lotteries|inote}%
\index{Quetelet|inote}%
\index{Süssmilch and regular frequencies}%
which is not one of complete equality, tends everywhere, when
the number of recorded instances becomes large, to approximate
towards a certain definite figure.

During the eighteenth century matters were not pushed much
further than this, that in certain cases, of which comparatively
few were known, there was this surprising regularity, increasing
in degree as the instances became more numerous. Bernoulli,
however, took the first step towards giving it a theoretical basis
by showing that, if the \textit{à~priori} probability is known throughout,
then (subject to certain conditions which he himself did not make
clear) \emph{in the long run} a certain determinate frequency of occurrence
is to be expected. Süssmilch (\textit{Die göttliche Ordnung in den
Veränderungen des menschlichen Geschlechts}, 1741) discovered a
theological interest in these regularities. Such ideas had become
sufficiently familiar for Gibbon to characterise the results of
\index{Gibbon}%
probability as ``so true in general, so fallacious in particular.''
Kant found in them (as many later writers have done) some
\index{Kant}%
bearing on the problem of Free Will.\footnote
  {In \textit{Idee zu einer allgemeinen Geschichte in weltbürgerlicher Absicht}, 1784. For
  a discussion of this passage and for the connection between Kant and Süssmilch,
  see Lottin's \textit{Quetelet}, pp.~367,~368.}

But with the nineteenth century came bolder theoretical
methods and a wider knowledge of facts. After proving his
\index{Bernoulli's Theorem}%
extension of Bernoulli's Theorem,\footnote
  {See \Pageref{345}.}
Poisson applied it to the
\index{Poisson!great numbers@{and great numbers}}%
observed facts, and gave to the principle underlying these
regularities the title of the \textit{Law of Great Numbers}. ``Les choses
de toutes natures,'' he wrote,\footnote
  {\textit{Recherches}, pp.~7--12. Von Bortkiewicz (\textit{Kritische Betrachtungen}, 1st~part,
  pp.~655--660) has maintained that Poisson intended to state his principle in a
  less general way than that in which it has been generally taken, and that he was
  misunderstood by Quetelet and others. If we attend only to Poisson's contributions
  to \textit{Comptes Rendus} in 1835 and~1836 and to the examples he gives
  there, it is possible to make out a good case for thinking that he intended his
  law to extend only to cases where certain strict conditions were fulfilled. But
  this is not the spirit of his more popular writings or of the passage quoted above.
  At any rate, it is the fashion, in which Poisson influenced his contemporaries,
  that is historically interesting; and this is certainly not represented by Von
  Bortkiewicz's interpretation.}
``sont soumises à une loi universelle
qu'on peut appeler la loi des grands nombres\ldots. De ces
exemples de toutes natures, il résulte que la loi universelle des
grands nombres est déjà pour nous un fait général et incontestable,
résultant d'expériences qui ne se démentent jamais.'' This is
the language of exaggeration; it is also extremely vague. But
%% -----File: 345.png---Folio 334-------
it is exciting; it seems to open up a whole new field to scientific
investigation; and it has had a great influence on subsequent
thought. Poisson seems to claim that, in the whole field of chance
and variable occurrence, there really exists, amidst the apparent
disorder, a discoverable system. Constant causes are always
at work and assert themselves in the long run, so that each class
of event does eventually occur in a definite proportion of cases.
It is not clear how far Poisson's result is due to \textit{à~priori} reasoning,
and how far it is a natural law based on experience; but it is
represented as displaying a certain harmony between natural
law and the \textit{à~priori} reasoning of probabilities.

Poisson's conception was mainly popularised through the
writings of Quetelet. In 1823 Quetelet visited Paris on an
\index{Quetelet}%
astronomical errand, where he was introduced to Laplace and
\index{Laplace!Quetelet@{and Quetelet}}%
came into touch with ``la grande école française.'' ``Ma jeunesse
et mon zèle,'' he wrote in later years, ``ne tardèrent pas à me
mettre en rapport avec les hommes les plus distingués de cette
époque; qu'on me permette de citer Fourier, Poisson, Lacroix,
spécialement connus, comme Laplace, par leurs excellents écrits
sux la théorie mathématique des probabilités\ldots. C'est donc
au milieu des savants, statisticiens, et économistes de ce temps
que j'ai commencé mes travaux.''\footnote
  {For the details of the life of Quetelet and for a very full discussion of his
  writings with special reference to Probability, see Lottin's \textit{Quetelet, statisticien et
  sociologue}.}
Shortly afterwards began
his long series of papers, extending down to 1873, on the application
of Probability to social statistics. He wrote a text-book
on Probability in the form of letters for the instruction of the
Prince Consort.

Before accepting in 1815 at the age of nineteen (with a view to
a livelihood) a professorship of mathematics, Quetelet had studied
as an art student and written poetry; a year later an opera, of
which he was part-author, was produced at Ghent. The character
of his scientific work is in keeping with these beginnings. There
is scarcely any permanent, accurate contribution to knowledge
which can be associated with his name. But suggestions, projects,
far-reaching ideas he could both conceive and express, and
he has a very fair claim, I think, to be regarded as the parent of
modern statistical method.

Quetelet very much increased the number of instances of the
%% -----File: 346.png---Folio 335-------
\index{Mendelism and statistics}%
Law of Great Numbers, and also brought into prominence a
slightly variant type of it, of which a characteristic example is
the law of height, according to which the heights of any considerable
sample taken from any population tend to group themselves
according to a certain well-known curve. His instances were
chiefly drawn from social statistics, and many of them were of a
kind well calculated to strike the imagination---the regularity of
the number of suicides, ``l'effrayante exactitude avec laquelle
les crimes se reproduisent,'' and so forth. Quetelet writes
\index{Quetelet}%
with an almost religious awe of these mysterious laws, and
certainly makes the mistake of treating them as being as
adequate and complete in themselves as the laws of physics,
and as little needing any further analysis or explanation.\footnote
  {Compare, for instance, the following passage from \textit{Recherches sur le penchant
  au crime}: ``Il me semble que ce qui se rattache à l'espèce humaine, considérée
  en masse, est de l'ordre des faits physiques; plus le nombre des individus est
  grand, plus la volonté individuelle s'efface et laisse prédominer la série des faits
  généraux qui dépendent des causes générales\ldots. Ce sont ces causes qu'il
  s'agit de saisir, et dès qu'on les connaîtra, on en déterminera les effets pour la
  société comme on détermine les effets par les causes dans les sciences physiques.''}
Quetelet's sensational language may have given a considerable
impetus to the collection of social statistics, but it also involved
statistics in a slight element of suspicion in the minds of some
who, like Comte, regarded the application of the mathematical
\index{Comte!statistics@{and statistics}}%
calculus of probability to social science as ``purement chimérique
\index{Calculus of Probability!Sociology@{and Sociology}}%
et, par conséquent, tout à fait vicieuse.'' The suspicion of
quackery has not yet disappeared. Quetelet belongs, it must be
admitted, to the long line of brilliant writers, not yet extinct, who
have prevented Probability from becoming, in the scientific salon,
perfectly respectable. There is still about it for scientists a
smack of astrology, of alchemy.

The progress of the conception since the time of Quetelet has
been steady and uneventful; and long strides towards this perfect
respectability have been taken. Instances have been multiplied
and the conditions necessary for the existence of statistical
stability have been to some extent analysed. While the most
fruitful applications of these methods have still been perhaps,
as at first, in social statistics and in errors of observation, a
number of uses for them have been discovered in quite recent
times in the other sciences; and the principles of Mendelism
have opened out for them a great field of application throughout
biology.
%% -----File: 347.png---Folio 336-------
\index{Statistical frequency, theory of!stability of}%

\Paragraph{2.} The existence of numerous instances of the Law of Great
Numbers, or of something of the kind, is absolutely essential for
the importance of Statistical Induction. Apart from this the more
precise parts of statistics, the collection of facts for the prediction
of future frequencies and associations, would be nearly useless.
But the `Law of Great Numbers' is not at all a good name for the
principle which underlies Statistical Induction. The `Stability
of Statistical Frequencies' would be a much better name for it.
The former suggests, as perhaps Poisson intended to suggest, but
\index{Poisson!great numbers@{and great numbers}}%
what is certainly false, that every class of event shows statistical
regularity of occurrence if only one takes a sufficient number of
instances of it. It also encourages the method of procedure, by
which it is thought legitimate to take any observed degree of
frequency or association, which is shown in a fairly numerous
set of statistics, and to assume with insufficient investigation
that, because the statistics are \emph{numerous}, the observed degree of
frequency is therefore \emph{stable}. Observation shows that some
statistical frequencies are, within narrower or wider limits, stable.
But stable frequencies are not very common, and cannot be
assumed lightly.

The gradual discovery, that there are certain classes of
phenomena, in which, though it is impossible to predict what will
happen in each individual case, there is nevertheless a regularity
of occurrence if the phenomena be considered together in successive
sets, gives the clue to the abstract inquiry upon which we
are about to embark.
%% -----File: 348.png---Folio 337-------
\index{Bernoulli's Theorem|ifoll}%
\index{Probability, and relevant knowledge!truth frequency@{and truth frequency}|ifoll}%


\Chapter{XXIX}{The Use of \textit{à~priori} Probabilities for the Prediction of
Statistical Frequency---the Theorems of Bernoulli,
Poisson, and Tchebycheff}

\begin{Quote}
Hoc igitur est illud Problema, quod evulgandum hoc loco proposui, postquam
jam per vicennium pressi, et cujus tum novitas, tum summa utilitas cum
pari conjuncta difficultate omnibus reliquis hujus doctrinae capitibus pondus
et pretium superaddere potest.---\textsc{Bernoulli}.\footnote
  {\textit{Ars Conjectandi}, p.~227.}
\end{Quote}

\Paragraph{1.} \First{Bernoulli's} Theorem is generally regarded as the central
theorem of statistical probability. It embodies the first attempt
to deduce the measures of statistical frequencies from the measures
of individual probabilities, and it is a sufficient fruit of the twenty
years which Bernoulli alleges that he spent in reaching his result,
if out of it the conception first arose of general laws amongst
masses of phenomena, in spite of the uncertainty of each particular
case. But, as we shall see, the theorem is only valid subject
to stricter qualifications, than have always been remembered,
and in conditions which are the exception, not the rule.

The problem, to be discussed in this chapter, is as follows:
Given a series of occasions, the probability\footnote
  {In the simplest cases, dealt with by Bernoulli, these probabilities are all
  supposed equal.}
of the occurrence
of a certain event at each of which is known relative to certain
initial \textit{data}~$h$, on what proportion of these occasions may we
reasonably anticipate the occurrence of the event? Given, that
is to say, the individual probability of each of a series of events
\textit{à~priori}, what statistical frequency of occurrence of these events
is to be anticipated over the whole series? Beginning with
Bernoulli's Theorem, we will consider the various solutions of
this problem which have been propounded, and endeavour to
%% -----File: 349.png---Folio 338-------
determine the proper limits within which each method has
validity.

\Paragraph{2.} Bernoulli's Theorem in its simplest form is as follows: If
the probability of an event's occurrence under certain conditions
is~$p$, then, if these conditions are present on $m$~occasions, the most
probable number of the event's occurrences is~$mp$ (or the nearest
integer to this), \ie\ the most probable \emph{proportion} of its occurrences
to the total number of occasions is~$p$: further, the probability
that the proportion of the event's occurrences will diverge from
the most probable proportion~$p$ by less than a given amount~$b$,
increases as $m$~increases, the value of this probability being
calculable by a process of approximation.

The probability of the event's occurring $n$~times and failing
$m - n$~times out of the $m$~occasions is (subject to certain conditions
to be elucidated later) $p^n q^{m-n}$ multiplied by the coefficient of
this expression in the expansion of $(p + q)^m$, where $p + q = 1$. If
we write $n = mp - h$, this term is $\dfrac{m!}{(mp - h)!(mq + h)!} p^n q^{m-n}$. It
is easily shown that this is a maximum when $h = 0$, \ie\ when $n = mp$
(or the nearest integer to this, where $mp$~is not integral). This
result constitutes the first part of Bernoulli's Theorem.

For the second part of the theorem some method of approximation
is required. Provided that $m$~is large, we can simplify
the expression $\dfrac{m!}{(mp - h)!(mq + h)!} p^n q^{m - n}$ by means of Stirling's
Theorem, and obtain as its approximate value
\[
\frac{1}{\sqrt{2\pi mpq}}e^{-\frac{h^2}{2mpq}}
\]
As before, this is a maximum when $h = 0$, \ie\ when $n = mp$.

It is possible, of course, by more complicated formulae to
obtain closer approximations than this.\footnote
  {See, \eg, Bowley, \textit{Elements of Statistics}, p.~298. The objection about to
  be raised does not apply to these closer approximations.}
But there is an objection,
which can be raised to this approximation, quite distinct
from the fact that it does not furnish a result correct to as many
places of decimals as it might. This is, that the approximation
is independent of the sign of~$h$, whereas the original expression
is not thus independent. That is to say, the approximation
implies a symmetrical distribution for different values of~$h$ about
%% -----File: 350.png---Folio 339-------
\index{Czuber|inote}%
the value for $h = 0$; while the expression under approximation
is unsymmetrical. It is easily seen that this want of symmetry
is appreciable unless $mpq$ is large. We ought, therefore, to have
laid it down as a condition of our approximation, not only that
$m$~must be large, but also that $mpq$ must be large. Unlike most
of my criticisms, this is a mathematical, rather than a logical
point. I recur to it in §\;15.

``Par une fiction qui rendra les calculs plus faciles'' (to quote
Bertrand), we now replace the integer~$h$ by a continuous variable~$z$
\index{Bertrand!Bernoulli's Theorem@{and Bernoulli's Theorem}}%
and argue that the probability that the amount of the divergence
from the most probable value~$mp$ will lie between $z$~and~$z + dz$,
is
\[
\frac{1}{\sqrt{2\pi mpq}} e^{-\frac{z^2}{2mpq}} dz .
\]
This `fiction' will do no harm so long as it is remembered that we
are now dealing with a particular kind of approximation. The
probability that the divergence~$h$ from the most probable value~$mp$
will be less than some given quantity~$a$ is, therefore,
\[
\frac{1}{\sqrt{2\pi mpq}} \int^{+a}_{-a} e^{-\frac{z^2}{2mpq}} dz .
\]
If we put $\dfrac{z}{\sqrt{2mpq}} = t$, this is equal to
\[
\frac{2}{\sqrt{\pi}} \int^{\frac{a}{\sqrt{2mpq}}}_{0} e^{-t^2} dt .
\]
Thus, if we write $a = \sqrt{2mpq} \gamma$, the probability\footnote
  {The replacement of the integer~$h$ by the continuous variable~$z$ may render
  the formula rather deceptive. It is certain, for example, that the error does not
  lie between $h$~and~$h + 1$.}
that the
number of occurrences will lie between
\[
mp + \sqrt{2mpq}\gamma \text{ and }
mp - \sqrt{2mpq}\gamma
\]
is measured by\footnote
  {The\Pagelabel{339} above proof follows the general lines of Bertrand's (\textit{Calcul des probabilités},
  chap.~iv.). Some writers, using rather more precision, give the result as
  \[
  \frac{2}{\sqrt{\pi}}
  \int^{\gamma}_{0} e^{-t^2}\, dt + \frac{e^{-\gamma^2}}{\sqrt{2\pi mpq}}
  \]
  (\eg\ Laplace, by the use of Euler's Theorem, and more recently Czuber,
  \textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ p.~121). As the whole formula is approximate,
  the simpler expression given in the text is probably not less satisfactory in
  practice. See also Czuber, \textit{Entwicklung}, pp.~76,~77, and Eggenberger, \textit{Beiträge
  zur Darstellung des Bernoullischen Theorems}.}
$\displaystyle\frac{2}{\sqrt{\pi}} \int^{\gamma}_{0} e^{-t^2} dt$. This same expression measures
%% -----File: 351.png---Folio 340-------
\index{Eggenberger|inote}%
the probability that the \emph{proportion} of occurrences will lie
between
\[
p + \sqrt\frac{2pq}{m}\gamma \text{ and }
p - \sqrt\frac{2pq}{m}\gamma.
\]
The different values of the integral $\dfrac{2}{\sqrt{\pi}}\displaystyle\int_0^te^{-t^2}dt=\Theta(t)$ are given
in tables.\footnote
  {A list of the principal tables is given by Czuber, \textit{loc.\ cit.}\ vol.~i.\ p.~122.}
\index{Czuber!Bernoulli's Theorem@{and Bernoulli's Theorem}|inote}%

The probability that the proportion of occurrences will lie
between given limits varies with the magnitude of~$\sqrt{\dfrac{2pq}{m}}$, and
this expression is sometimes used, therefore, to measure the
`precision' of the series. Given the \textit{à~priori} probabilities, the
precision varies inversely with the \emph{square root} of the number of
instances. Thus, while the probability that the \emph{absolute} divergence
will be less than a given amount~$a$ decreases, the probability
that the corresponding \emph{proportionate} divergence (\ie\ the absolute
divergence divided by the number of instances) will be less than
a given amount~$b$, increases, as the number of instances increases.
This completes the second part of Bernoulli's Theorem.

\Paragraph{3.} Bernoulli himself was not acquainted with Stirling's
theorem, and his proof differs a good deal from the proof outlined
in §\;2. His final enunciation of the theorem is as follows: If in
each of a given series of experiments there are $r$~contingencies
favourable to a given event out of a total number of contingencies~$t$,
so that $\dfrac{r}{t}$ is the probability of the event at each experiment,
then, given any degree of probability~$c$, it is possible to make such
a number of experiments that the probability, that the proportionate
number of the event's occurrences will lie between
$\dfrac{r+1}{t}$ and $\dfrac{r-1}{t}$, is greater than~$c$.\footnote
  {\textit{Ars Conjectandi}, p.~236 (I have translated freely). There is a brief account
  of Bernoulli's proof in Todhunter's \textit{History}, pp.~71,~72. The problem is dealt
\index{Todhunter!Bernoulli's Theorem@{and Bernoulli's Theorem}|inote}%
  with by Laplace, \textit{Théorie analytique}, livre~ii.\ chap.~iii. For an account of
\index{Laplace!Bernoulli's Theorem@{and Bernoulli's Theorem}}%
  Laplace's proof see Todhunter's \textit{History}, pp.~548--553.}

%% -----File: 352.png---Folio 341-------
\index{Ellis, Leslie!Bernoulli's Theorem@{and Bernoulli's Theorem}}%

\Paragraph{4.} We seem, therefore, to have proved that, if the \textit{à~priori}
probability of an event under certain conditions is~$p$, the proportion
of times most probable \textit{à~priori} for the event's occurrence
on a series of occasions where the conditions are satisfied is also~$p$,
and that if the series is a long one the proportion is very unlikely
to differ widely from~$p$. This amounts to the principle
which Ellis\footnote
  {\textit{On the Foundation of the Theory of Probabilities}: ``If the probability of a
  given event be correctly determined, the event will on a long run of trials tend
  to recur with frequency proportional to this probability. This is generally
  proved mathematically. It seems to me to be true \textit{à~priori}\ldots. I have been
  unable to sever the judgment that one event is more likely to happen than
  another from the belief that in the long run it will occur more frequently.''}
and Venn have employed as the defining axiom of
\index{Venn!Bernoulli@{and Bernoulli}}%
probability, save that if the series is `long enough' the proportion,
\index{Laplace!Bernoulli's Theorem@{and Bernoulli's Theorem}}%
according to them, will \emph{certainly} be~$p$. Laplace\footnote
  {\textit{Essai philosophique}, p.~53: ``On peut tirer du théorème précédent cette
  conséquence qui doit être regardée comme une loi générale, savoir, que les
  rapports des effets de la nature, sont à fort peu près constans, quand ces effets
  sont considérés en grand nombre.''}
believed that the
theorem afforded a demonstration of a general law of nature, and
in his second edition published in 1814 he replaces\footnote
  {Introduction, pp.~liii, liv.}
the eloquent
dedication, \textit{A Napoléon-le-Grand}, which prefaces the edition of
1812, by an explanation that Bernoulli's Theorem must always
bring about the eventual downfall of a great power which, drunk
with the love of conquest, aspires to a universal domination,---``c'est
encore un résultat du calcul des probabilités, confirmé
par de nombreuses et funestes expériences.''

\Paragraph{5.} Such is the famous Theorem of Bernoulli which some have
believed\footnote
  {Even by Mr.~Bradley, \textit{Principles of Logic}, p.~214. After criticising Venn's
\index{Bradley!Bernoulli's Theorem@{and Bernoulli's Theorem}|inote}%
  view he adds: ``It is false that the chances must be realised in a series. It is,
  however, true that they most probably will be, and true again that this probability
  is increased, the greater the length we give to our series.''}
to have a universal validity and to be applicable to \emph{all}
`properly calculated' probabilities. Yet the theorem exhibits
algebraical rather than logical insight. And, for reasons about
to be given, it will have to be conceded that it is only true of a
special class of cases and requires conditions, before it can be
legitimately applied, of which the fulfilment is rather the exception
than the rule. For consider the case of a coin of which
it is given that the two faces are either both heads or both tails:
at every toss, provided that the results of the other tosses are
unknown, the probability of heads is~$\frac{1}{2}$ and the probability of
tails is~$\frac{1}{2}$; yet the probability of $m$~heads and $m$~tails in $2m$~tosses
%% -----File: 353.png---Folio 342-------
is zero, and it is certain \textit{à~priori} that there will be either $2m$~heads
or none. Clearly Bernoulli's Theorem is inapplicable to
such a case. And this is but an extreme case of a normal
condition.

For the first stage in the proof of the theorem assumes that,
if $p$~is the probability of one occurrence, $p^r$~is the probability of $r$~occurrences
running. Our discussion of the theorems of multiplication
\index{Multiplication!theorems of}%
will have shown how considerable an assumption this
involves. It assumes that a \emph{knowledge} of the fact that the event
has occurred on every one of the first $r-1$~occasions does not in
any degree affect the probability of its occurrence on the~$r$th.
Thus Bernoulli's Theorem is only valid if our initial \textit{data} are of
such a character that additional knowledge, as to the proportion
of failures and successes in one part of a series of cases is altogether
irrelevant to our expectation as to the proportion in another
part. If, for example, the initial probability of the occurrence
of an event under certain circumstances is one in a million, we
may only apply Bernoulli's Theorem to evaluate our expectation
over a million trials, if our original \textit{data} are of such a character
that, even after the occurrence of the event in every one of the
first million trials, the probability in the light of this additional
knowledge that the event will occur on the next occasion is still
no more than one in a million.

Such a condition is very seldom fulfilled. If our initial probability
is partly founded upon experience, it is clear that it is
liable to modification in the light of further experience. It is,
in fact, difficult to give a concrete instance of a case in which the
conditions for the application of Bernoulli's Theorem are completely
fulfilled. At the best we are dealing in practice with a
good approximation, and can assert that no realised series of
moderate length can much affect our initial probability. If we
wish to employ the expression $\displaystyle\frac{2}{\sqrt \pi}\int_0^\gamma e^{-t^2}dt$ we are in a worse
position. For this is an approximate formula which requires for
its validity that the series should be \emph{long}; whilst it is precisely
in this event, as we have seen above, that the use of Bernoulli's
Theorem is more than usually likely to be illegitimate.

\Paragraph{6.} The conditions, which have been described above, can be
expressed precisely as follows:
%% -----File: 354.png---Folio 343-------

Let $_mx_n$ represent the statement that the event has occurred
on $m$ out of $n$ occasions and has not occurred on the others; and
let $_1x_1/h = p$, where $h$ represents our \textit{à~priori data}, so that $p$ is the
\textit{à~priori} probability of the event in question. Bernoulli's Theorem
then requires a series of conditions, of which the following is
typical: $_{m+1}x_{n+1}/_mx_n· h = _1x_1/h$, \ie\ the probability of the event
on the $n+1$th occasion must be unaffected by our knowledge of
its proportionate frequency on the first $n$~occasions, and must be
exactly equal to its \textit{à~priori} probability before the first occasion.

Let us select one of these conditions for closer consideration.
If $y_r$ represents the statement that the event has occurred on each
of $r$ successive occasions, $y_r/h = y_r/y_{r-1}h· y_{r-1}/h$ and so on, so
that $y_r/h = \Prod\limits_{s=1}^{s=r}y_s/y_{s-1}h$. Hence if we are to have $y_r/h=p^r$, we
must have $y_s/y_{s-1}h=p$ for all values of~$s$ from $1$ to~$r$. But in
many particular examples $y_s/y_{s-1}h$ increases with~$s$, so that
$y_r/h>p^r$. Bernoulli's Theorem, that is to say, tends, if it is
carelessly applied, to exaggerate the rate at which the probability
of a given divergence from the most probable decreases as the
divergence increases. If we are given a penny of which we have
no reason to doubt the regularity, the probability of heads at
the first toss is~$\frac{1}{2}$; but if heads fall at every one of the first 999
tosses, it becomes reasonable to estimate the probability of heads
at the thousandth toss at much more than~$\frac{1}{2}$. For the \textit{à~priori}
probability of its being a conjurer's penny, or otherwise biassed
so as to fall heads almost invariably, is not usually so infinitesimally
small as $(\frac{1}{2})^{1000}$. We can only apply Bernoulli's Theorem
with rigour for a prediction as to the penny's behaviour over a
series of a thousand tosses, if we have \textit{à~priori} such exhaustive
knowledge of the penny's constitution and of the other conditions
of the problem that $999$~heads running would not cause
us to modify in any respect our prediction \textit{à~priori}.

\Paragraph{7.} It seldom happens, therefore, that we can apply Bernoulli's
Theorem with reference to a long series of natural events. For
in such cases we seldom possess the exhaustive knowledge which
is necessary. Even where the series is short, the perfectly
rigorous application of the Theorem is not likely to be legitimate,
and some degree of approximation will be involved in
utilising its results.

Not so infrequently, however, artificial series can be devised
%% -----File: 355.png---Folio 344-------
in which the assumptions of Bernoulli's Theorem are relatively
legitimate.\footnote
  {In the discussion in \Chapref{XVI}., \Pageref{170}, of the probability of a divergence
  from an equality of heads and tails in coin-tossing, an example has been
  given of the construction of an artificial series in which the application of
  Bernoulli's Theorem is more legitimate than in the natural series.}
Given, that is to say, a proposition~$a_1$, \emph{some} series
$a_1a_2\ldots$ can be found, which satisfies the conditions:
\begin{align*}
\text{(i.) }&a_1/h = a_2/h\ldots = a_r/h.\\
\text{(ii.) }&a_r/a_s\ldots\bar a_t\ldots h = a_r/h.
\end{align*}
Adherents of the Frequency Theory of Probability, who use the
\index{Frequency theory!Bernoulli's Theorem@{and Bernoulli's Theorem}}%
principal conclusion of Bernoulli's Theorem as the defining property
of \emph{all} probabilities, sometimes seem to mean no more than
that, relative to given evidence, every proposition belongs to
\emph{some} series, to the members of which Bernoulli's Theorem is
rigorously applicable. But the \emph{natural} series, the series, for
example, in which we are most often interested, where the $a$'s
are \emph{alike} in being accompanied by certain specified conditions~$c$,
is not, as a rule, rigorously subject to the Theorem. Thus `the
probability of~$a$ in certain conditions~$c$ is~$\frac{1}{2}$' is \emph{not} in general
equivalent, as has sometimes been supposed, to `It is $500$~to~$1$
that in $40,000$~occurrences of~$c$, $a$~will not occur more than $20,200$~times,
and $500$~to~$1$ that it will not occur less than $19,800$~times.'

\Paragraph{8.} Bernoulli's Theorem supplies the simplest formula by
which we can attempt to pass from the \textit{à~priori} probabilities of
each of a series of events to a prediction of the statistical frequency
of their occurrence over the whole series. We have seen that
Bernoulli's Theorem involves two assumptions, one (in the form
in which it is usually enunciated) tacit and the other explicit.
It is assumed, first, that a knowledge of what has occurred at
some of the trials would not affect the probability of what may
occur at any of the others; and it is assumed, secondly, that these
probabilities are all \emph{equal} \textit{à~priori}. It is assumed, that is to say,
that the probability of the event's occurrence at the $r$th~trial is
equal \textit{à~priori} to its probability at the $n$th~trial, and, further, that
it is unaffected by a knowledge of what may actually have
occurred at the $n$th~trial.

A formula, which dispenses with the explicit assumption of
equal \textit{à~priori} probabilities at every trial, was proposed by
\index{Poisson!Theorem of}%
Poisson,\footnote
  {\textit{Recherches}, pp.~246 \textit{et~seq.}}
and is usually known by his name. It does \emph{not} dispense,
%% -----File: 356.png---Folio 345-------
\index{Czuber|inote}%
however, with the other inexplicit assumption. The difference
between Poisson's Theorem and Bernoulli's is best shown by
reference to the ideal case of balls drawn from an urn. The
typical example for the valid application of Bernoulli's Theorem
is that of balls drawn from a single urn, containing black and
white balls in a known proportion, and replaced after each drawing,
or of balls drawn from a series of urns, each containing black
and white balls in the \emph{same} known proportion. The typical
example for Poisson's Theorem is that of balls drawn from a series
of urns, each containing black and white balls in \emph{different} known
proportions.

Poisson's\Pagelabel{345} Theorem may be enunciated as follows:\footnote
  {For the proof see Poisson, \textit{Recherches}, \textit{loc.\ cit.}, or Czuber, \textit{Wahrscheinlichkeitsrechnung},
  vol.~i.\ pp.~153--159.}
Let $s$~trials
be made, and at the $\lambda$th~trial ($\lambda=1,2\ldots s$) let the probabilities
for the occurrence and non-occurrence of the event be
$p_{\lambda}$,~$q_{\lambda}$ respectively. Then, if $\dfrac{\Sum p_{\lambda}}{s}=p$, the probability that the
number of occurrences~$m$ of the event in the $s$~trials will lie
between the limits~$sp ± l$ is given by
\[
P = \frac{2}{k\sqrt{\pi s}}\int_0^l e^{-\frac{x^2}{k^2s}}\, dx
  + \frac{e^{-\frac{l^2}{k^2s}}}{k\sqrt{\pi s}}
\]
where $k = \sqrt{\dfrac{2\Sum p_\lambda q_\lambda}{s}}$.

By substituting $\dfrac{x}{k\sqrt{s}}=t$ and $\dfrac{l}{k\sqrt{s}}=\gamma$, this may be written
in a form corresponding to that of Bernoulli's Theorem,\footnote
  {For the analogous form of Bernoulli's Theorem see \Pageref{339} (footnote).}
namely:

The probability that the number of occurrences of the event
will lie between $sp ± \gamma k\sqrt{s}$ is given by
\[
P = \frac{2}{\sqrt{\pi}} \int_0^\gamma e^{-t^2}\, dt
  + \frac{e^{-\gamma^2}}{k\sqrt{\pi s}}
\]

\Paragraph{9.} This is a highly ingenious theorem and extends the application
of Bernoulli's results to some important types of cases. It
embraces, for example, the case in which the successive terms of
a series are drawn from distinct populations known to be characterised
by differing statistical frequencies; no further complication
%% -----File: 357.png---Folio 346-------
being necessary beyond the calculation of two simple
functions of these frequencies and of the number of terms in the
series. But it is important not to exaggerate the degree to which
Poisson's method has extended the application of Bernoulli's
results. Poisson's Theorem leaves untouched all those cases in
which the probabilities of some of the terms in the series of events
can be influenced by a knowledge of how some of the other terms
in the series have turned out.

Amongst these cases two types can be distinguished. In the
first type such knowledge would lead us to discriminate between
the conditions to which the different instances are subject. If,
for example, balls are drawn from a bag, containing black and
white balls in known proportions, and not replaced, the knowledge
whether or not the first ball drawn was black affects the
probability of the second ball's being black because it tells us
how the conditions in which the second ball is drawn differ
from those in which the first ball was drawn. In the second type
such knowledge does not lead us to discriminate between the
conditions to which the different instances are subject, but it leads
us to modify our opinion as to the nature of the conditions which
apply to all the terms alike. If, for instance, balls are drawn
from a bag, which is one, but it is not certainly known which, out
of a number of bags containing black and white balls in differing
proportions, the knowledge of the colour of the first ball drawn
affects the probabilities at the second drawing, because it throws
some light upon the question as to which bag is being drawn from.

This last type is that to which most instances conform which
are drawn from the real world. A knowledge of the characteristics
of some members of a population may give us a clue to the
general character of the population in question. Yet it is this
type, where there is a change in knowledge but \emph{no change in the
material conditions} from one instance to the next, which is most
frequently overlooked.\footnote
  {Numerous instances could be quoted. To take a recent English example,
  reference may be made to Yule, \textit{Introduction to the Theory of Statistics},
\index{Yule!coin@{and coin-tossing}|inote}%
  p.~251. Mr.~Yule thinks that the condition of independence is satisfied if ``the
  \emph{result} of any one throw or toss does not affect, and is unaffected by, the results
  of the preceding and following tosses,'' and does not allow for the cases in which
  \emph{knowledge} of the result is relevant apart from any change in the physical conditions.}
It will be worth while to say something
further about each of these two types.\footnote
  {The types which I distinguish under four heads (the Bernoullian, the
  Poissonian, and the two described above) Bachelier (\textit{Calcul des probabilités},
  p.~155) classifies as follows:

  (i.) When the conditions are identical throughout, the problem has \textit{uniformité};

  (ii.) When they vary from stage to stage, but according to a law given from
  the beginning and in a manner which does not depend upon what has happened
  at the earlier stages, it has \textit{indépendance};

  (iii.) When they vary in a manner which depends upon what has happened
  at the earlier stages, it has \textit{connexité}.

  Bachelier gives solutions for each type on the assumption that the number of
  trials is very great, and that the number of successes or failures can be regarded
  as a continuous variable. This is the same kind of assumption as that made
  in the proof of Bernoulli's Theorem given in §\;2, and is open to the same objections,---or
  rather the value of the results is limited in the same way.}
%% -----File: 358.png---Folio 347-------
\index{Bachelier|inote}%
\index{Pearson, Karl!asymmetry@{and asymmetry}}%
\index{Pearson, Karl!generalised Probability@{and generalised Probability curves}}%

\Paragraph{10.} For problems of the first type, where there is physical
or material dependence between the successive trials, it is not
possible, I think, to propose any general solution; since the
probabilities of the successive trials may be modified in all kinds
of different ways. But for particular problems, if the conditions
are precise enough, solutions can be devised. The problem, for
instance, of an urn, containing black and white balls in known
proportions, from which balls are drawn successively and \emph{not
replaced},\footnote
  {It is of no consequence whether the balls are drawn successively and not
  replaced, or are drawn simultaneously.}
\index{Czuber}%
is ingeniously solved by Czuber\footnote
  {\textit{Loc.\ cit.}\ vol.~i.\ pp.~163,~164.}
with the aid of
Stirling's Theorem. If $\sigma$~is the number of balls and $s$~the number
of drawings, he reaches the interesting conclusion (assuming that
$\sigma$,~$s$ and~$\sigma-s$ are all large) that the probability of the number of
black balls lying within given limits is the same as it would be
if the balls were replaced after each drawing and the number
of drawings were $\dfrac{\sigma-s}{\sigma}s$ instead of~$s$.

In addition to the assumptions already stated, Professor
Czuber's solution applies only to those cases where the limits, for
which we wish to determine the probability, are narrow compared
with the total number of black balls~$p\sigma$. Professor Pearson\footnote
  {``Skew Variation in Homogeneous Material,'' \textit{Phil.\ Trans.}\ (1895), p.~360.}
has
worked out the same problem in a much more general manner,
so as to deal with the \emph{whole} range, \ie~the frequency or probability
of all possible ratios of black balls, even where $s>p\sigma$. The
various forms of curve, which result, according to the different
relations existing between $p$,~$s$, and~$\sigma$, supply examples of each
of the different types of frequency curve which arise out of a
%% -----File: 359.png---Folio 348-------
classification according to (i.)~skewness or symmetry, (ii.)~limitation
of range in one, both or neither direction; and he designates,
therefore, the curves which are thus obtained as \emph{generalised probability
curves}. His discussion of the properties of these curves is
interesting, however, to the student of descriptive statistics
rather than to the student of probability. The most generalised
and, mathematically, by far the most elegant treatment of this
problem, with which I am acquainted, is due to Professor
\index{Tschuprow!statistical frequency@{and statistical frequency}}%
Tschuprow.\footnote
  {``Zur Theorie der Stabilität statistischer Reihen,'' p.~216, published in
  the \textit{Skandinavisk Aktuarietidskrift} for~1919.}

\index{Poisson!statistical frequency@{and statistical frequency}}%
Poisson, in attempting a somewhat similar problem,\footnote
  {\textit{Loc.\ cit.}\ pp.~231,~232.}
arrives
at a result, which seems obviously contrary to good sense, by a
curious, but characteristic, misapprehension of the meaning of
`independence' in probability. His problem is as follows:
If $l$~balls be taken out from an urn, containing $c$~black and white
balls in known proportions, and not replaced, and if a further
number of balls~$\mu$ be then taken out, the probability that a given
proportion~$\dfrac{m}{m+n}$ of these $\mu$~balls will be black \emph{is independent of
the number and the colour of the $l$~balls originally drawn out}. For,
he argues, if $l+\mu$~balls are drawn out, the probability of a combination,
which is made up of $l$~black and white balls in given
proportions followed by $\mu$~balls, of which $m$~are white and $n$~black,
must be the same as that of a similar combination in which the
$\mu$~balls precede the $l$~balls. Hence the probability of $m$~white
balls in $\mu$~drawings, given that the $l$~balls have already been
drawn out, must be equal to the probability of the same result,
when no balls have been previously drawn out. The reader will
perceive that Poisson, thinking only of physical dependence, has
been led to his paradoxical conclusion by a failure to distinguish
between the cases where the proportion of black and white balls
amongst the $l$~balls originally drawn is \emph{known} and where it is not.
The \emph{fact} of their having been drawn in certain proportions, provided
that only the total number drawn is known and the proportions
are \emph{unknown}, does not influence the probability. Poisson
states in his conclusion that the probability is independent of the
number and colour of the $l$~balls originally drawn. If he had
added---as he ought---`provided the number of each colour is
%% -----File: 360.png---Folio 349-------
\index{Yule|inote}%
\emph{unknown},' the air of paradox disappears. This is an exceedingly
good example of the failure to perceive that a probability cannot
be influenced by the \emph{occurrence} of a material event but only by
such \emph{knowledge}, as we may have, respecting the occurrence of the
event.\footnote
  {For an attempt to solve other problems of this type see Bachelier, \textit{Calcul
\index{Bachelier!statistical frequency@{and statistical frequency}|inote}%
  des probabilités}, chap.~ix.\ \textit{(Probabilités connexes}). I think, however, that the
  solutions of this chapter are vitiated by his assuming in the course of them
  both that certain quantities are very large, and also, at a later stage, that the
  same quantities are infinitesimal. On this account, for example, his solution
  of the following difficult problem breaks down: Given an urn~$A$ with $m$~white
  and $n$~black balls and an urn~$B$ with $m'$~white and $n'$~black balls, if at each move
  a ball is taken from~$A$ and put into~$B$, and at the same time a ball is taken from~$B$
  and put into~$A$, what is the probability after $x$~moves that the urns $A$~and~$B$
  shall have a given composition?}

\Paragraph{11.} For problems of the second type, where knowledge of the
result of one trial is capable of influencing the probability at the
next apart from any change in the material conditions, there is,
likewise, no general solution. The following artificial example,
however, will illustrate the sort of considerations which are involved.

In the cases where Bernoulli's Theorem is applied to practical
questions, the \textit{à~priori} probability is generally obtained empirically
by reference to the statistical frequency of each alternative
in past experience under apparently similar conditions. Thus
the \textit{à~priori} probability of a male birth is estimated by reference
to the recorded proportion of male births in the past.\footnote
  {Cf.\ Yule, \textit{Theory of Statistics}, p.~258: ``We are not able to assign an
  \textit{à~priori} value to the chance~$p$ (\ie~of a male birth) as in the case of dice-throwing,
  but it is quite sufficiently accurate for practical purposes to use the proportion
  of male births actually observed if that proportion be based on a moderately
  large number of observations.''}
The
validity of estimating probabilities in this manner will be discussed
later. But for the purposes of this example let us assume
that the \textit{à~priori} probability has been calculated on this basis.
Thus the \textit{à~priori} probability $p\left(=\dfrac{r}{s}\right)$ of an event is based on
the observation of its occurrence $r$~times out of $s$~occasions on
which the given conditions were present. Now, according to
Bernoulli's Theorem directly applied, the probability of the
event's occurring $n$~times running is~$p^n$ or~$\left(\dfrac{r}{s}\right)^n$. But, if the
event occurs at the first trial, the probability at the second
%% -----File: 361.png---Folio 350-------
becomes $\dfrac{r+1}{s+1}$, and so on. Hence the probability~$P$, properly
calculated, of $n$~successive occurrences is
\[
\frac{r}{s}·\frac{r+1}{s+1}·\frac{r+2}{s+2}\ldots\frac{r+n-1}{s+n-1}.
\]
Hence
\begin{DPalign*}[m]
P &= \frac{(r+n-1)!\, (s-1)!}{(s+n-1)!\, (r-1)!} \\
  &= \frac{(r+n-1)^{r+n-\frac{1}{2}} e^{-(r+n-1)} s^{s-\frac{1}{2}} e^{-(s-1)}}
          {(s+n-1)^{s+n-\frac{1}{2}} e^{-(s+n-1)} r^{r-\frac{1}{2}} e^{-(r-1)}}
\rintertext{by Stirling's} \\
  &
\rintertext{\llap{Theorem, provided that $r$~and~$s$ are large;}} \\
  &= \left(\frac{r}{s}\right)^n
     \frac{\left(1 + \dfrac{n-1}{r}\right)^{r+n-\frac{1}{2}}}
          {\left(1 + \dfrac{n-1}{s}\right)^{s+n-\frac{1}{2}}}\\
  &= p^{n}Q^{n}, \text{ where }
     Q = \frac{\left(1 + \dfrac{n-1}{r}\right)^{\frac{r-\frac{1}{2}}{n} + 1.}}
              {\left(1 + \dfrac{n-1}{s}\right)^{\frac{s-\frac{1}{2}}{n} + 1.}}
\end{DPalign*}
Thus, in this case, the assumption of Bernoulli's Theorem is
approximately correct, only if $Q$~is nearly unity. This condition
is not satisfied unless $n$~is small both compared with~$r$ and compared
with~$s$. It is very important to notice that \emph{two} conditions
are involved. Not only must the experience, upon which the
\textit{à~priori} probability is based, be extensive in comparison with the
number of instances to which we apply our prediction; but also
the number of previous instances multiplied by the probability
based upon them, \ie~$sp\, (=r)$, must be large in comparison with
the number of new instances. Thus, even where the prior experience,
upon which we found the initial probability~$P$, is very
extensive, we must not, if $P$~is very small, say that the probability
of $n$~successive occurrences is approximately~$p^n$, unless $n$~is also
small. Similarly if we wish to determine, by the methods of
Bernoulli, the probability of $n$~occurrences and $m$~failures on
$m+n$~occasions, it is necessary that we should have $m$~and~$n$ small
%% -----File: 362.png---Folio 351-------
\index{Pearson, Karl|inote}%
compared with~$s$, $n$~small compared with~$r$, and $m$~small compared
with~$s-r$.\footnote
  {This paragraph is concerned with a different point from that dealt with
  in Professor Pearson's article ``On the Influence of Past Experience on Future
  Expectation,'' to which it bears a superficial resemblance. Professor Pearson's
  article which deals, not with Bernoulli's Theorem, but with Laplace's ``Rule of
\index{Laplace!Rule of Succession@{and Rule of Succession}|inote}%
  Succession,'' will be referred to in §\;16 of this chapter and in §\;12 of the next.}

The case solved above is the simplest possible. The general
problem is as follows: If an event has occurred $x$~times in the
first $y$~trials, its probability at the~$y+1$th is~$\dfrac{r+x}{s+y}$; determine the
\textit{à~priori} probability of the event's occurring $p$~times in $q$~trials.
If the \textit{à~priori} probability in question is represented by~$\phi(p,q)$, we
have %[** TN: Displaying in-line formula]
\[
\phi(p,q)
  = \frac{r + p - 1}{s + q - 1}\, \phi(p-1, q-1)
  + \frac{s + q - 1 - r - p}{s + q - 1}\, \phi(p, q-1).
\]
I know of no solution of this, even approximate. But we may
say that the conditions are those of supernormal dispersion as
compared with Bernoulli's conditions. That is to say, the probability
of a proportion differing widely from~$\dfrac{r}{s}$ is greater than
in Bernoullian conditions; for when the proportion begins to
diverge it becomes more probable that it will continue to diverge
in the same direction. If, on the other hand, the conditions of
the problem had been such, that when the proportion begins to
diverge it becomes more probable that it will recover itself and
tend back towards~$\dfrac{r}{s}$ (as when we draw balls without replacing
them from a bag of known composition), we should have subnormal
dispersion.\footnote
  {Bachelier (\textit{Calcul des probabilités}, p.~201) classifies these two kinds of conditions
\index{Bachelier!statistical frequency@{and statistical frequency}}%
  as \textit{conditions accélératrices} and \textit{conditions retardatrices}.}

\Paragraph{12.}\Pagelabel{351} The condition elucidated in the preceding paragraph is
frequently overlooked by statisticians. The following example
\index{Czuber!statistical frequency@{and statistical frequency}}%
from Czuber\footnote
  {\textit{Loc.\ cit.}\ vol.~ii.\ p.~15. I choose my example from Professor Czuber because
  he is usually so careful an exponent of theoretical statistics.}
will be sufficient for the purpose of illustration.
Czuber's argument is as follows:

In the period 1866--1877 there were registered in Austria
\[
\begin{array}{@{}r@{ }l}
\llap{$m$} = 4,311,076 & \text{ male births} \\
         n = 4,052,193 & \text{ female births} \\
\cline{1-1}
\rule{0pt}{12pt}
         s = 8,363,269\rlap{\,;} &
\end{array}
\]
%% -----File: 363.png---Folio 352-------
for the succeeding period, 1877--1899, we are given only
\[
m' = 6,533,961 \text{ male births};
\]
what conclusion can we draw as to the number~$n'$ of female
births? We can conclude, according to Czuber, that the most
probable value
\[
n_0' = \frac{nm'}{m} = 6,141,587,
\]
and that there is a probability $P = .9999779$ that $n'$~will lie
between the limits $6,118,361$ and~$6,164,813$.

It seems in plain opposition to good sense that on
such evidence we should be able with practical certainty
$\left(P=.9999779 = 1-\dfrac{1}{45250}\right)$ to estimate the number of female
births within such narrow limits. And we see that the conditions
laid down in §\;11 have been flagrantly neglected. The
number of cases, over which the prediction based on Bernoulli's
Theorem is to extend, actually \emph{exceeds} the number of cases upon
which the \textit{à~priori} probability has been based. It may be added
that for the period, 1877--1894, the actual value of~$n'$ did lie
between the estimated limits, but that for the period, 1895--1905,
it lay \emph{outside} limits to which the same method had
attributed practical certainty.

That Professor Czuber should have thought his own argument
plausible, is to be explained, I think, by his tacitly taking account
in his own mind of evidence not stated in the problem. He was
relying upon the fact that there is a great mass of evidence for
believing that the ratio of male to female births is peculiarly
stable. But he has not brought this into the argument, and he
has not used as his \textit{à~priori} probability and as his coefficient of
dispersion the values which the whole mass of this evidence would
have led him to adopt. Would not the argument have seemed
very preposterous if $m$~had been the number of males called
George, and $n$~the number of females called Mary? Would it not
have seemed rather preposterous if $m$~had been the number of
legitimate births and $n$~the number of illegitimate births? Clearly
we must take account of other considerations than the mere
numerical values of $m$~and~$n$ in estimating our \textit{à~priori} probability.
But this question belongs to the subject-matter of later chapters,
%% -----File: 364.png---Folio 353-------
\index{Tchebycheff, Theorem of}%
and, quite apart from the manner of calculation of the \textit{à~priori}
probability, the argument is invalidated by the fact than an
\textit{à~priori} probability founded on $8,363,269$ instances, without
corroborative evidence of a non-statistical character, cannot
be assumed stable through a calculation which extends over
$12,700,000$ instances.

\Paragraph{13.} Before we leave the theorems of Bernoulli and Poisson,
it is necessary to call attention to a very remarkable theorem by
Tchebycheff, from which both of the above theorems can be
derived as special cases. This result is reached rigorously and
without approximation, by means of simple algebra and without
the aid of the differential calculus. Apart from the
beauty and simplicity of the proof, the theorem is so valuable
and so little known that it will be worth while to quote it in
full:\footnote
  {From \textit{Journ.\ Liouville} (2),~xii., 1867, ``Des valeurs moyennes,'' an article
  translated from the Russian of Tchebycheff. This proof is also quoted by
  Czuber, \textit{loc.\ cit.}\ p.~212, through whom I first became acquainted with it. Most
\index{Czuber!Tchebycheff's Theorem@{and Tchebycheff's Theorem}|inote}%
  of Tchebycheff's work was published previous to 1870 and appeared originally
  in Russian. It was not easily accessible, therefore, until the publication
  at Petrograd in 1907 of the collected edition of his works in French.
  His theorems are, consequently, not nearly so well known as they deserve
  to be, although his most important theorems were reproduced from time
  to time in the Journals of Euler and Liouville. For full references see the
  Bibliography.}

Let $x, y, z\ldots$ represent certain magnitudes, of which $x$~can
take the values $x_1x_2\ldots x_k$ with probabilities $p_1p_2\ldots p_k$
respectively, $y$~the values $y_1y_2\ldots y_l$ with probabilities $q_1q_2\ldots q_l$,
$z$~the values $z_1z_2\ldots z_m$ with probabilities $r_1r_2\ldots r_m$ and so on,
so that
\begin{DPalign*}
& \Sum_1^k p=1,\quad
  \Sum_1^l q=1,\quad
  \Sum_1^m r=1, \text{ etc.} \\
\lintertext{Write}
& \Sum_1^k p_\kappa x_\kappa = a,\quad
  \Sum_1^l q_\lambda y_\lambda = b,\quad
  \Sum_1^m r_\mu z_\mu =c, \text{ etc.,} \\
\lintertext{and}
& \Sum_1^k p_\kappa x_\kappa^2 = a_1,\quad
  \Sum_1^l q_\lambda y_\lambda^2 = b_1,\quad
  \Sum_1^m r_\mu z_\mu^2 = \DPtypo{c}{c_1}, \text{ etc.,}
\end{DPalign*}
so that we can describe~$a$ as the mathematical expectation or
average value of~$x$ and $a_1$~as the mathematical expectation or
average value of $x^2$,~etc.
%% -----File: 365.png---Folio 354-------

Consider the expression:
\begin{DPalign*}
\Sum (x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c - \ldots)^2 p_\kappa q_\lambda r_\mu \ldots \\
\lintertext{Now}
\begin{aligned}[t]
\Sum_1^k (x_\kappa^2 - 2ax_\kappa + a^2)p_\kappa
  &= \Sum p_\kappa x_\kappa^2 - 2a\Sum p_\kappa x_\kappa + a^2\Sum p_\kappa \\
  &= a_1 - 2a^2 + a^2 = a_1-a^2.
\end{aligned}
\end{DPalign*}
Also $\Sum q_\lambda r_\mu \ldots = 1$ summed for all values of $\lambda$,~$\mu~\ldots$, and
\begin{DPgather*}[m]
\Sum_1^k 2(x_\kappa - a)(y_\lambda - b)p_\kappa
  = \Sum_1^k 2(x_\kappa y_\lambda - bx_\kappa - ay_\lambda + ab) p_\kappa \\
  = 2\left(y_\lambda\Sum p_\kappa x_\kappa - b\Sum p_\kappa x_\kappa
       - a y_\lambda\Sum p_\kappa + ab\Sum p_\kappa\right) \\
  = 2(ay_\lambda - ab - ay_\lambda + ab) = 0. \\
\lintertext{\rlap{Therefore}}
\Sum(x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c\ldots)^2 p_\kappa q_\lambda r_\mu\ldots \\
  = a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots, \\
\lintertext{whence}
\frac{\Sum(x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c\ldots)^2 p_\kappa q_\lambda r_\mu\ldots}
     {\alpha^2(a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots)}
  = \frac{1}{\alpha^2},
\end{DPgather*}
where the summation extends over all values of $\kappa$,~$\lambda$,~$\mu~\ldots$ and
$\alpha$~is some arbitrary number greater than unity.

If we omit those terms of the sum on the left-hand side of
the above equation for which
\[
\frac{(x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c\ldots)^2}
     {\alpha^2(a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots)} < 1,
\]
and write unity for this expression in the remaining terms, both
these processes diminish the magnitude of the left-hand side.
Hence $\Sum p_\kappa q_\lambda r_\mu \ldots < \dfrac{1}{\alpha^2}$, where the summation covers those sets
of values only for which
\[
\frac{(x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c\ldots)^2}
     {\alpha^2(a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 \ldots)} \geq 1.
\]

If $P$~is the probability that
\[
\frac{(x_\kappa + y_\lambda + z_\mu + \ldots - a - b - c\ldots)^2}
     {\alpha^2(a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots)}
\]
is equal to or less than unity, it follows that
%% -----File: 366.png---Folio 355-------
\index{Tchebycheff, Theorem of}%
\begin{DPgather*}
1-P < \frac{1}{\alpha ^2} \\
\lintertext{\ie}  P > 1 - \frac{1}{\alpha ^2}
\end{DPgather*}
Hence the probability that the sum
\begin{DPgather*}
x_\kappa + y_\lambda + z_\mu \ldots
\rintertext{\llap{lies between the limits}} \\
a + b + c + \ldots
  - \alpha\sqrt{a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots} \\
\lintertext{and}
a + b + c + \ldots
  + \alpha\sqrt{a_1 + b_1 + c_1 + \ldots - a^2 - b^2 - c^2 - \ldots}
\end{DPgather*}
is greater than $1-\dfrac{1}{\alpha ^2}$, where $\alpha$~is some number greater than
unity.

This result constitutes Tchebycheff's Theorem. It may also
be written in the following form:

Let $n$ be the number of the magnitudes $x, y, z\ldots$, and
write $\alpha = \dfrac{\sqrt{n}}{t}$; then the probability that the arithmetic
mean $\dfrac{x_\kappa + y_\lambda + z_\mu+\ldots}{n}$ lies between the limits
\[
\frac{a + b + c+ \ldots}{n}
  ± \frac{1}{t}\sqrt{\frac{a_1 + b_1 + c_1 + \ldots}{n}
  - \frac{a^2 + b^2 + c^2 + \ldots}{n}}
\]
is greater than $1-\dfrac{t^2}{n}$.

It is also easy to show\footnote
  {For a proof see Czuber, \textit{loc.\ cit.}\ vol.~i.\ p.~216.}
\index{Czuber!Tchebycheff's Theorem@{and Tchebycheff's Theorem}|inote}%
as a deduction from Tchebycheff's
Theorem that, if an amount~$A$ is won when an event of probability
$p\,[p=1-q]$ occurs and an amount~$B$ lost when it fails, then in
$s$~trials the probability that the total winnings (or losses) will lie
between the limits
\[
s(pA - qB) ± \alpha(A + B)\sqrt{spq}
\]
is greater than $1-\dfrac{1}{\alpha^2}$.

\Paragraph{14.} From this very general result for the probable limits of
a sum composed of a number of independently varying magnitudes,
Bernoulli's Theorem is easily derived. For let there be
%% -----File: 367.png---Folio 356-------
$s$~observations or trials, and $s$ magnitudes $x_1x_2\ldots x_s$ corresponding,
such that $x=1$ when the event under consideration
occurs, and $x=0$ when it fails. If the probability of the events
occurrence is~$p$, we have $a=p$, $b=p$, etc., and $a_1=p$, $b_1=p$, etc.
Hence the probability~$P$ that the number of the event's occurrences
will lie between the limits $sp ± \alpha \sqrt{sp - sp^2}$, \ie\ between
the limits $sp ± \alpha\sqrt{spq}$ where $q=1-p$, is $>1-\dfrac{1}{\alpha^2}$. If we
compare this formula with the formula for Bernoulli's
Theorem already given, we find that, where this formula
gives $P > 1 - \dfrac{1}{\alpha^2}$, Bernoulli's Theorem with greater precision
gives $P = \Theta\left(\dfrac{\alpha}{\sqrt{2}}\right)$. The degree of superiority in the matter
of precision supplied by the latter can be illustrated by the
following table:
\[
\begin{array}{|>{\quad}r<{\quad}|>{\quad}l<{\quad}|>{\quad}l<{\quad}|}
\hline
\rule[-12pt]{0pt}{32pt}
\alpha^2. &
%[** TN: Added parentheses to heading]
\multicolumn{1}{c|}{\Theta\left(\frac{\alpha}{\sqrt{2}}\right).} &
\multicolumn{1}{c|}{1-\frac{1}{\alpha^2}.} \\
\hline
\rule{0pt}{20pt}
1.5             &.7788   &.333 \\
2\phantom{.5}   &.8427   &.5  \\
4.5             &.9661   &.7778  \\
8\phantom{.5}   &.9953   &.875  \\
12.5            &.9996   &.92 \\
\rule[-12pt]{0pt}{12pt}
18\phantom{.5}  &.99998  &.9445 \\
\hline
\end{array}
\]
Thus when the limits are narrow and $\alpha$~is small, Bernoulli's
formula gives a value of~$P$ very much in excess of $1-\dfrac{1}{\alpha^2}$. But
Bernoulli's formula involves a process of approximation which is
only valid when $s$~is large. Tchebycheff's formula involves no
such process and is equally valid for all values of~$s$. We have
seen in §\;11 that there are numerous cases in which for a
different reason Bernoulli's formula exaggerates the results,
and, therefore, Tchebycheff's more cautious limits may sometimes
prove useful.

The deduction of a corresponding form of Poisson's Theorem
from Tchebycheff's general formula obviously follows on similar
lines. For we put\footnote
  {I am using the same notation as that used for Poisson's Theorem in §\;8.}
$a=p_1$, $b=p_2$, etc., and $a_1=p_1$, $b_1=p_2$, etc.,
%% -----File: 368.png---Folio 357-------
\index{Markoff, A. A.!Tchebycheff's Theorem@{and Tchebycheff's Theorem}}%
\index{Tchebycheff!Poisson's Theorem@{and Poisson's Theorem}}%
and find that the probability that the number of the event's
occurrences will lie between the limits
\[
\Sum_1^\lambda p_\lambda ± \alpha \sqrt{\Sum_1^\lambda p_\lambda
  - \Sum_1^\lambda p_\lambda^2},
\]
\begin{DPgather*}
\lintertext{\rlap{\ie\ between the limits}}
sp ± \alpha\sqrt{\Sum^\lambda p_\lambda q_\lambda}, \\
\lintertext{\rlap{\ie\ between the limits}}
sp ± \sqrt{2}\,\alpha k\sqrt{s},
\end{DPgather*}
is greater than $t-\dfrac{1}{\alpha^2}$.

In \textit{Crelle's Journal}\footnote
  {Vol.~33 (1846), \textit{Démonstration élémentaire d'une proposition générale de la
  théorie des probabilités}.}
Tchebycheff proves Poisson's Theorem
\index{Poisson!Tchebycheff@{and Tchebycheff}}%
directly by a method similar to his general method, and also
obtains several supplementary results such as the following:

I\@. If the chances of an event~$E$ in $\mu$~consecutive trials are
$p_1p_2\ldots p_\mu$ respectively, and their sum is~$s$, the probability that
$E$~will occur at least $m$~times is less than
\[
\frac{1}{2(m-s)} \sqrt\frac{m(\mu - m)}{\mu}
  \left(\frac{s}{\mu}\right)^m
  \left(\frac{\mu - s}{\mu - m}\right)^{\mu - m + 1}
\]
\begin{flushright}
provided that $m>s+1$;
\end{flushright} %[** TN: [sic] no \par]
II\@. and the probability that $E$~will not occur more than $n$~times
is less than
\[
\frac{1}{2(s-n)} \sqrt\frac{\mu(\mu - n)}{\mu}
  \left(\frac{\mu - s}{\mu - n}\right)^{\mu - n}
  \left(\frac{s}{n}\right)^{n + 1}
\]
\begin{flushright}
provided that $n<s-1$.
\end{flushright}
III\@. Hence the probability that $E$~will occur less than $m$~times
and more than~$n$ is greater than
\begin{align*}
1 &- \frac{1}{2(m-s)}\sqrt\frac{m(\mu -m)}{\mu}\left(\frac{s}{m}\right)^m
     \left(\frac{\mu -s}{\mu -m}\right)^{\mu -m+1}\\
  &- \frac{1}{2(s-n)}\sqrt\frac{n(\mu -n)}{\mu}\left(\frac{s}{n}\right)^{n+1}
     \left(\frac{\mu -s}{\mu -n}\right)^{n-\mu}
\end{align*}
\begin{flushright}
provided $m>s+1$, $n<s-1$.
\end{flushright}

\Paragraph{15.} Tchebycheff's methods have been set out and his results
admirably extended by A.~A. Markoff.\footnote
  {The reader is referred to Markoff's \textit{Wahrscheinlichkeitsrechnung}, and particularly
  to p.~67, for a striking development, along mathematical lines, of
  Tchebycheff's leading idea. Further references to later memôirs,
  which, being in the Russian language, are inaccessible to me, will
  be found in the Bibliography.}
And some developments
%% -----File: 369.png---Folio 358-------
\index{Asymmetry, and Bernoulli's Theorem|ifoll}%
\index{Laplace!school of}%
along the same lines by Tschuprow (``Zur Theorie der
\index{Tschuprow}%
Stabilität statistischer Reihen,'' \textit{Skandinavisk Aktuarietidskrift},
1919) have convinced me that Tchebycheff's discovery is far
more than a technical device for solving a special problem, and
points the way to the fundamental method for attacking these
questions on the mathematical side. The Laplacian mathematics,
although it still holds the field in most text-books, is
really obsolete, and ought to be replaced by the very beautiful
work which we owe to these three Russians.

\Paragraph{16.} There is one other investigation relating to Bernoulli's
Theorem which deserves remark. I have already pointed out,
in §\;2, that the dispersion about the most probable value, even
when the conditions for the applicability of Bernoulli's Theorem
\index{Bernoulli's Theorem!asymmetry@{and asymmetry}|ifoll}%
in its non-approximate form are strictly fulfilled, is unsymmetrical.
The fact, that the usual approximation for the probability
of a divergence~$h$ from the most probable number of
occurrences (the notation is that of §\;2 above) takes the form
$\dfrac{1}{\sqrt{2\pi mpq}}\, e^{-\frac{h^2}{2mpq}}$, which is the same for~$+h$ as for~$-h$, has led
to this want of symmetry being very generally overlooked;
and it is not uncommon to assume that the probability of a
given divergence less than~$pm$ is equal to that of the same divergence
in excess of~$pm$, and, in general, that the probability of
the frequency's exceeding~$pm$ in a set of $m$~trials is \emph{equal} to that
of its falling short of~$pm$.

That this is not strictly the case is obvious. If a die is cast
$60$~times, the most probable number of appearances of the ace
is~$10$; but the ace is more likely to appear $9$~times than $11$~times;
and much more likely (about $5$~times as likely) not to appear at
all than to appear exactly $20$~times. That this must be so will
be clear to the reader (without his requiring to trouble himself
with the algebra), when he reflects that the ace cannot appear
less often than not at all, whereas it may well appear more than
$20$~times, so that the smallness of the possible divergence in
defect from the most probable value~$10$, as compared with the
possible divergence in excess, must be made up for by the greater
%% -----File: 370.png---Folio 359-------
\index{Lexis, and asymmetry of statistical frequency|inote}%
\index{Pearson, Karl!asymmetry@{and asymmetry}|inote}%
\index{Rule of Succession|inote}%
\index{Simmons and asymmetry in Bernoulli's!Theorem}%
frequency of any given defection as compared with the corresponding
excess. Thus the actual frequency in a series of trials
of an event, of which the probability at each trial is less than~$\frac{1}{2}$,
is likely to fall short of its most probable value more often than
it exceeds it. What is in fact true is that the mathematical
expectation of deficiency is equal to the mathematical expectation
of excess, \ie\ that the sum of the possible deficiencies each
multiplied by its probability is equal to the sum of the possible
excesses each multiplied by its probability.

The actual measurement of this want of symmetry and the
determination of the conditions, in which it can be safely
neglected, involves laborious mathematics, of which I am only
acquainted with one direct investigation, that published in the
\textit{Proceedings of the London Mathematical Society} by Mr.~T.~C.
Simmons.\footnote
  { ``A New Theorem in Probability.'' Mr.~Simmons claimed novelty for
  his investigation, and so far as I know this claim is justified; but recent
  investigations obtaining closer approximations to Bernoulli's Theorem by means
  of the Method of Moments are essentially directed towards the same problem.

  A somewhat analogous point has, however, been raised by Professor Pearson
  in his article (\textit{Phil.\ Mag.}, 1907) on ``The Influence of Past Experience on Future
  Expectation.'' He brings out an exactly similar want of symmetry in the
  probabilities of the various possible frequencies about the most probable frequency,
  when the calculation is based, not on Bernoulli's Theorem as in Mr.~Simmons's
  investigation, but on Laplace's rule of succession (see next chapter).
\index{Laplace!Rule of Succession@{and Rule of Succession}|inote}%
  The want of symmetry has also been pointed out by Professor Lexis (\textit{Abhandlungen},
  p. 120).}

For the details of the proof I must refer the reader to Mr.~Simmons's
article. His principal theorem\footnote
  {I am not giving his own enunciation of it.}
is as follows: If
$\dfrac{1}{a+1}$~is the probability of the event at each trial and $n(a+1)$ the
number of trials, $n$~and~$a$ being integers,\footnote
  {Mr.~Simmons does not seem to have been able to remove this restriction
  on the generality of his theorem, but there does not seem much reason to doubt
  that it can be removed.}
the probability that the
frequency of occurrence will fall short of~$n$ is always greater than
the probability that it will exceed~$n$; the difference between the
two probabilities being a maximum when $n=1$, constantly
diminishing as $n$~increases, lying always between $\dfrac{1}{3}\,\dfrac{a-1}{a+1}$~times the
greatest term in $\left(\dfrac{a}{a+1}+\dfrac{1}{a+1}\right)^{n(a+1)}$ and $\dfrac{1}{3}\,\dfrac{a-1}{a+1}$ times the
%% -----File: 371.png---Folio 360-------
greatest term in $\left(\dfrac{a}{a+1} + \dfrac{1}{a+1}\right)^{(n+1)(a + 1)}$, and being approximately
equal, when $n$~is very large, to $\dfrac{1}{3}\,\dfrac{a-1}{\sqrt{2\pi na(a+1)}}$.

The following table gives the value of the excess~$\Delta$ of the
probability of a frequency less than~$pm$ over the probability of
a frequency greater than~$pm$ for various values of~$p$ the probability
and $m$~the number of trials $\left[p = \dfrac{1}{a+1},\ m=n(a+1)\right]$, as
calculated by Mr.~Simmons:
\[
\renewcommand{\arraystretch}{1.25}%
\begin{array}{|>{\quad}c<{\quad}|>{\quad}r<{\quad}|>{\quad}l<{\quad}|}
\hline
p.    &  \multicolumn{1}{c|}{m.}   &  \multicolumn{1}{c|}{\Delta.} \\
\hline
\frac{1}{3}    &    3 & .037037 \\
\frac{1}{3}    &   15 & .02243662 \\
\frac{1}{3}    &   24 & .0182706 \\
\frac{1}{4}    &    4 & .054687 \\
\frac{1}{4}    &   20 & .03201413 \\
\frac{1}{10}   &   10 & .084777 \\
\frac{1}{10}   &   20 & .068673713 \\
\frac{1}{100}  &  100 & .101813 \\
\frac{1}{100}  &  200 & .081324387 \\
\frac{1}{1000} & 1000 & .103454\\
\hline
\end{array}
\]
Thus unless not only $m$ but $mp$~also is large the want
of symmetry is likely to be appreciable. Thus it is easily found
that in $100$~sets of $4$~trials each, where $p=\dfrac{1}{4}$, the actual frequency
is likely to exceed the most probable $26$~times and to fall short of
it $31$~times; and in $100$~sets of $10$~trials each, where $p=\dfrac{1}{10}$, to
exceed $26$~times and to fall short $34$~times.

Mr.~Simmons was first directed to this investigation through
%% -----File: 372.png---Folio 361-------
\index{Dice-tossing|ifoll}%
\index{Mode, and law of error!asymmetry about}%
\index{Yule|inote}%
noticing in the examination of sets of random digits that ``each
digit presented itself, with unexpected frequency, \emph{less} than $\dfrac{1}{10}$~of
the number of times. For instance, in $100$~sets of $150$~digits each,
I found that a digit presented itself in a set more frequently under
$15$~times than over $15$~times; similarly in the case of $80$~sets each
of $250$~digits, and also in other aggregations.'' Its possible
bearing on such experiments with dice and roulette, as are
\index{Roulette}%
described at the end of this chapter, is clear. But apart from
these artificial experiments, it is sometimes worth the statistician's
while to bear in mind this appreciable want of symmetry
in the distribution about the mode or most probable value in
many even of those cases in which Bernoullian conditions are
strictly fulfilled.

\Paragraph{17.} I will conclude this chapter by an account of some of the
attempts which have been made to verify \textit{à~posteriori} the conclusions
of Bernoulli's Theorem. These attempts are nearly
\index{Bernoulli's Theorem!empirical verification of|ifoll}%
useless, first, because we can seldom be certain \textit{à~priori} that the
conditions assumed in Bernoulli's Theorem are fulfilled, and,
secondly, because the theorem predicts not what will happen
but only what is, on certain evidence, likely to happen. Thus
even where our results do not verify Bernoulli's Theorem, the
theorem is not thereby discredited. The results have bearing
on the conditions in which the experiments took place, rather
than upon the truth of the theorem. In spite, therefore, of the
not unimportant place which these attempts have in the history
of probability, their scientific value is very small. I record them,
because they have a good deal of historical and psychological
interest, and because they satisfy a certain idle curiosity from
which few students of probability are altogether free.\footnote
  {Mr.~Yule (\textit{Introduction to Statistics}, p. 254) recommends its indulgence:
\index{Yule!coin@{and coin-tossing}|inote}%
  ``The student is strongly recommended to carry out a few series of such experiments
  personally, in order to acquire confidence in the use of the theory.''
  Mr.~Yule himself has indulged moderately.}

\Paragraph{18.} The \textit{data} for these investigations have been principally
drawn from four sources---coin-tossing, the throw of dice, lotteries,
\index{Lotteries}%
and roulette; for in such cases as these the conditions for
Bernoulli's Theorem seem to be fulfilled most nearly. The earliest
recorded experiment was carried out by Buffon,\footnote
  {\textit{Essai d'arithmètique morale} (see Bibliography), published
  1777, said to have been composed about 1760.}
who, assisted
%% -----File: 373.png---Folio 362-------
\index{De Morgan!pupil of}%
\index{Edgeworth|inote}%
\index{Petersburg Paradox!Buffon@{and Buffon}}%
\index{Poisson|inote}%
\index{Weldon and dice}%
\index{Wolf and dice}%
by a child tossing a coin into the air, played $2048$~\textit{partis} of the
Petersburg game, in which a coin is thrown successively until
the \textit{parti} is brought to an end by the appearance of heads. The
same experiment was repeated by a young pupil of De~Morgan's
`for his own satisfaction.'\footnote
  {\textit{Formal Logic}, p.~185, published 1847. De~Morgan gives Buffon's results,
\index{Buffon!coin@{and coin-tossing}}%
  as well as his pupil's, in full. Buffon's results are also investigated by Poisson,
  \textit{Recherches}, pp.~132--135.}
In Buffon's trials there were $1992$
tails to $2048$ heads; in Mr.~H.'s (De~Morgan's pupil) $2044$ tails to
$2048$ heads. A further experiment, due to Buffon's example,
\index{Quetelet!balls@{and balls}}%
was carried out by Quetelet\footnote
  {\textit{Letters on the Theory of Probabilities} (Eng.\ trans.), p.~37.}
in 1837. He drew $4096$ balls from
an urn, replacing them each time, and recorded the result at
different stages, in order to show that the precision of the result
tended to increase with the number of the experiments. He
drew altogether $2066$ white balls and $2030$ black balls. Following
\index{Jevons!coin@{and coin-tossing}}%
in this same tradition is the experiment of Jevons,\footnote
  {\textit{Principles of Science} (2nd~ed.), p.~208.}
who made
$2048$ throws of ten coins at a time, recording the proportion of
heads at each throw and the proportion of heads altogether. In
the whole number of $20,480$ single throws, he obtained heads
$10,353$ times; More recently Weldon\footnote
  {Quoted by Edgeworth, ``Law of Error'' (\textit{Ency.\ Brit.}\ 10th~ed.), and by
  Yule, \textit{Introduction to Statistics}, p.~254.}
threw twelve dice $4096$
times, recording the proportion of dice at each throw which
showed a number greater than three.

All these experiments, however, are thrown completely into
the shade by the enormously extensive investigations of the Swiss
astronomer Wolf, the earliest of which were published in 1850
and the latest in~1893.\footnote
  {See Bibliography. Of the earliest of these investigations I have no first-hand
  knowledge and have relied upon the account given by Czuber, \textit{loc.\ cit.}\
\index{Czuber!verification@{and verification of Bernoulli}|inote}%
  vol.~i.\ p.~149. For a general account of empirical verifications of Bernoulli's
  Theorem reference may be made to Czuber, \textit{Wahrscheinlichkeitsrechnung}, vol.~i.\
  pp\DPtypo{}{.}~139--152, and Czuber, \textit{Entwicklung der Wahrscheinlichkeitstheorie}, pp.~88--91.}
In his first set of experiments Wolf
completed $1000$ sets of tosses with two dice, each set continuing
until every one of the $21$~possible combinations had occurred at
least once. This involved altogether $97,899$ tosses, and he then
completed a total of $100,000$. These \textit{data} enabled him to work
out a great number of calculations, of which Czuber quotes the
following, namely a proportion of~$.83533$ of unlike pairs, as against
the theoretical value $.83333$, \ie~$\dfrac{5}{6}$. In his second set of experiments
%% -----File: 374.png---Folio 363-------
\index{Meissner, Otto, and dice-throwing}%
Wolf used two dice, one white and one red (in the first set
the dice were indistinguishable), and completed $20,000$ tosses, the
details of each result being recorded in the \textit{Vierteljahrsschrift der
Naturforschenden Gesellschaft in Zürich}. He studied particularly
the number of sequences with each die, and the relative frequency
of each of the $36$~possible combinations of the two dice. The
sequences were somewhat fewer than they ought to have been,
and the relative frequency of the different combinations very
different indeed from what theory would predict.\footnote
  {Czuber quotes the principal results (\textit{loc.\ cit.}\ vol.~i.\ pp.~149--151). The
  frequencies of only~$4$, instead of~$18$, out of the $36$~combinations lay within the
  probable limits, and the standard deviation was~$76.8$ instead of~$23.2$.}
The explanation
of this is easily found; for the records of the relative
frequency of each face show that the dice must have been very
irregular, the six face of the white die, for example, falling $38$~per
cent more often than the four face of the same die. This,
then, is the sole conclusion of these immensely laborious experiments,---that
Wolf's dice were very ill made. Indeed the experiments
could have had no bearing except upon the accuracy
of his dice. But ten years later Wolf embarked upon one more
series of experiments, using \emph{four} distinguishable dice,---white,
yellow, red, and blue,---and tossing this set of four $10,000$ times.
Wolf recorded altogether, therefore, in the course of his life
$280,000$ results of tossing individual dice. It is not clear that
Wolf had any well-defined object in view in making these
records, which are published in curious conjunction with various
astronomical results, and they afford a wonderful example of the
pure love of experiment and observation.\footnote
  {The latest experiment of the kind, of which I am aware, is that of Otto
  Meissner (``Würfelversuche,'' \textit{Zeitschrift für Math.\ und Phys.}\ vol.~62 (1913), pp.~149--156),
  who recorded $24$~series of $180$~throws each with four distinguishable
  dice.}

\Paragraph{19.} Another series of calculations have been based upon the
ready-made \textit{data} provided by the published results of lotteries
\index{Lotteries!published results of}%
\index{Roulette!published results of|inote}%
and roulette.\footnote
  {For the publication of such returns there has always been a sufficient
  demand on the part of gamblers. An \textit{Almanach romain sur la loterie royale de
  France} was published at Paris in~1830, which contained all the drawings of the
  French lottery (two or three a month) from 1758~to~1830. Players at Monte
  Carlo are provided with cards and pins with which to record the results of
  successive coups, and the results at the tables are regularly published in \textit{Le
  Monaco}. Gamblers study these returns on account of the belief, which they
  usually hold, that as the number of cases is increased the \emph{absolute} deviation from
  the most probable proportion becomes less, whereas at the best Bernoulli's
  Theorem shows that the \emph{proportionate} deviation decreases while the absolute
  deviation \emph{increases}. Cf.~Houdin's \textit{Les Tricheries des Grecs dévoilées}: ``In a
  game of chance, the oftener the same combination has occurred in succession, the
  nearer we are to the certainty that it will not recur at the next cast or turn-up.
  This is the most elementary of the theories on probabilities; it is termed the
  \emph{maturity of the chances}.'' Laplace (\textit{Essai philosophique}, p.~142) quotes an
  amusing instance of the same belief not drawn from the annals of gambling:
  ``J'ai vu des hommes désirant ardemment d'avoir un fils, n'apprendre qu'avec
  peine les naissances des garçons dans le mois où ils allaient devenir pères.
  S'imaginant que le rapport de ces naissances à celles des filles devait être le
  même à la fin de chaque mois, ils jugaient que les garçons déjà nés rendaient
  plus probables les naissances prochaines des filles.''

  The literature of gambling is very extensive, but, so far as I am acquainted
  with it, excessively lacking in variety, the maturity of the chances and the
  martingale continually recurring in one form or another. The curious reader
  will find tolerable accounts of such topics in Proctor's \textit{Chance and Luck}, and
  Sir Hiram Maxim's \textit{Monte Carlo Facts and Fallacies}.}
%% -----File: 375.png---Folio 364-------
\index{Houdin|inote}%
\index{Laplace!birth proportions@{and birth proportions}}%
\index{Lotteries|ifoll}%
\index{Maxim, Sir Hiram|inote}%
\index{Pearson, Karl!roulette@{and roulette}}%
\index{Proctor|inote}%

\index{Czuber!lotteries@{and lotteries}}%
Czuber\footnote
  {\textit{Zum Gesetz der grossen Zahlen}. The results are summarised in his \textit{Wahrscheinlichkeitsrechnung},
  vol.~i.\ p.~139.}
has made calculations based on the lotteries
of Prague ($2854$~drawings) and Brünn ($2703$~drawings) between
\index{Brunn and lotteries@{Brünn and lotteries}}%
the years 1754~and~1886, in which the actual results agree
\index{Fechner, and median!lotteries@{and lotteries}}%
very well with theoretical predictions. Fechner\footnote
  {\textit{Kollektivmasslehre}, p.~229. These results also are summarised by Czuber,
  \textit{loc.\ cit.}}
employed the
lists of the ten State lotteries of Saxony between the years 1843
and~1852. Of a rather more interesting character are Professor
Karl Pearson's investigations\footnote
  {\textit{The Chances of Death}, vol.~i.}
into the results of Monte Carlo
\index{Monte Carlo}%
Roulette as recorded in \textit{Le Monaco} in the course of eight weeks.
\index{Roulette}%
Applying Bernoulli's Theorem, on the hypothesis of the equiprobability
of all the compartments throughout the investigation,
he found that the actually recorded proportions of red and black
were not unexpected, but that alternations and long runs were
so much in excess that, on the assumption of the exact accuracy
of the tables, the \textit{à~priori} odds were at least a thousand millions
to one against some of the recorded deviations. Professor
Pearson concluded, therefore, that Monte Carlo Roulette is not
objectively a game of chance in the sense that the tables on which
it is played are absolutely devoid of bias. Here also, as in the
case of Wolf's dice, the conclusion is solely relevant, not to the
theory or philosophy of Chance, but to the material shapes of
the tools of the experiment.

Professor Pearson's investigations into Roulette, which dealt
with $33,000$ Monte Carlo coups, have been overshadowed, just
%% -----File: 376.png---Folio 365-------
\index{Bortkiewicz, von, and great numbers!Marbe@{and Marbe}|inote}%
\index{Bromse and Marbel@{Brömse and Marbe}|inote}%
\index{Bruns and Marbe|inote}%
\index{D'Alembert|inote}%
\index{Grunbaum and Marbe@{Grünbaum and Marbe}|inote}%
\index{Lexis, and asymmetry of statistical frequency!Marbe@{and Marbe}|inote}%
\index{Marbe, Dr.\ Karl, and roulette}%
as all other tosses of coins and dice have been outdone by Wolf,
by Dr.~Karl Marbe,\footnote
  {\textit{Naturphilosophische Untersuchungen zur Wahrscheinlichkeitstheorie}.}
who has examined $80,000$ coups from Monte
Carlo and elsewhere. Dr.~Marbe arrived at exactly opposite
conclusions; for he claims to have shown that long runs, so far
from being in excess, were greatly in defect. Dr.~Marbe introduces
this experimental result in support of his thesis that the
world is so constituted that long runs do not as a matter of fact
occur in it.\footnote
  {Dr.~Marbe's monograph has given rise in Germany to a good deal of discussion,
  not directed towards showing what a preposterous method this is for
  demonstrating a natural law, but because the experimental result itself does not
  really follow from the \textit{data} and is due to a somewhat subtle error in Marbe's
  reasoning, by which he has been led into an incorrect calculation of the probable
  proportions \text{à~priori} of the various sequences. The problem is discussed by
  Von Bortkiewicz, Brömse, Bruns, Grimsehl, and Grünbaum (for exact references
\index{Grimsehl!Marbe@{and Marbe}|inote}%
  to these see the Bibliography), and by Lexis (\textit{Abhandlungen}, pp.~222--226) and
  Czuber (\textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ pp.~144--149). Largely as a result
\index{Czuber!Marbe@{and Marbe}}%
  of this controversy, Von Bortkiewicz has lately devoted a complete treatise
  (\textit{Die Iterationen}) to the mathematics of `runs.' Dr.~Marbe has been given
  far more attention by his colleagues in Germany than he conceivably deserves.}
Not merely are long runs very improbable. They
do not, according to him, occur at all. But we may doubt
whether roulette can tell us very much either of the laws of logic
or of the constitution of the universe.

Dr.~Marbe's main thesis is identical, as he himself recognises,
\index{D'Alembert!Marbe@{and Marbe}}%
with one of the heterodox contentions of D'Alembert.\footnote
  {D'Alembert's principal contributions to Probability are most accessible in
  the volumes of his \textit{Opuscules mathématiques} (1761). Works on Probability
  usually contain some reference to D'Alembert, but his sceptical opinions, rejected
  rather than answered by the orthodox school of Laplace, have not always
\index{Laplace!school of}%
  received full justice. D'Alembert has three main contentions to which in his
  various papers he constantly recurs:

  (1) That a probability very small mathematically is really zero;

  (2) That the probabilities of two successive throws with a die are not
  independent;

  (3) That `mathematical expectation' is not properly measured by the
  product of the probability and the prize.

  The first and third of these were partly advanced in explanation of the
  Petersburg paradox (see \Pageref{316}). The second is connected with the first, and
  was also used to support his incorrect evaluation of the probability of heads
  twice running; but D'Alembert, in spite of many of his results being wrong,
  does not altogether deserve the ridicule which he has suffered at the hands of
  writers, who accepted without sceptical doubts the hardly less incorrect conclusions
  of the orthodox theory of that time.}
But this
principle of variety, precisely opposite to the usual principle of
Induction, can have no claim to be accepted \textit{à~priori} and, as a
\emph{general} principle, there is no adequate evidence to support it from
experience. Its origin is to be found, perhaps, in the fact that
%% -----File: 377.png---Folio 366-------
in a certain class of cases, especially where conscious human
agency comes in, it may contain some element of truth. The
fact of an act's having been done in a particular way once may
be a special reason for thinking that it will not be performed on
the next occasion in precisely the same manner. Thus in many
so-called random events some slight degree of causal and material
dependence between successive occurrences may, nevertheless,
exist. In these cases `runs' may be fewer and shorter than those
which we should predict, if a complete absence of such dependence
is assumed. If, for example, a pack of cards be dealt, collected,
and shuffled, to the extent that card-players do as a rule shuffle,
there may be a greater presumption against the second hand's
being identical with the first than against any other particular
distribution. In the case of croupiers long experience might
possibly suggest some psychological generalisation,---that they
are very mechanical, giving an excess of numbers belonging to a
particular section of the wheel, or, on the other hand, that when
a croupier sees a run beginning, he tends to vary his spin more than
usual, thus bringing runs to an end sooner than he ought.\footnote
  {A good roulette table is, however, so delicate an instrument that no probable
  degree of regularity of habit on the part of the spinner could be sufficient
  to produce regularity in the result.}
At any
rate, it is worth emphasising once more that from such experiments
as these this is the only \emph{kind} of knowledge which we can
hope to obtain,---knowledge of the material construction of a
die or of the psychology of a croupier.
%% -----File: 378.png---Folio 367-------
\index{Probability, and relevant knowledge!from statistics|ifoll}%


\Chapter{XXX}{The Mathematical use of Statistical Frequencies for
the Determination of Probability \textit{à posteriori}---the
Methods of Laplace}

\begin{Quote}
Utilissima est aestimatio probabilitatum, quanquam in exemplis juridicis
politicisque plerumque non tam subtili calculo opus est, quam accurata
omnium circumstantiarum enumeratione.---\textsc{Leibniz}.
\end{Quote}

\Paragraph{1.} \First{In} the preceding chapter we have assumed that the probability
of an event at each of a series of trials is given, and have considered
how to infer from this the probabilities of the various possible
frequencies of the event over the whole series, without discussing
in detail by what method the initial probability had been determined.
In statistical inquiries it is generally the case that this
initial probability is based, not upon the Principle of Indifference,
\index{Principle of Indifference!statistics@{and statistics}}%
but upon the statistical frequencies of similar events
which have been observed previously. In this chapter, therefore,
we must commence the complementary part of our inquiry,---namely,
into the method of deriving a measure of probability
from an observed statistical frequency.

I do not myself believe that there is any direct and simple
method by which we can make the transition from an observed
numerical frequency to a numerical measure of probability.
The problem, as I view it, is part of the general problem of founding
judgments of probability upon experience, and can only be
dealt with by the general methods of induction expounded in
\Partref{III}\@. The nature of the problem precludes any other method,
and direct mathematical devices can all be shown to depend
upon insupportable assumptions. In the next chapters we will
consider the applicability of general inductive methods to this
problem, and in this we will endeavour to discredit the mathematical
charlatanry by which, for a hundred years past, the basis
of theoretical statistics has been greatly undermined.
%% -----File: 379.png---Folio 368-------
\index{Bernoulli, Jac.}%

\Paragraph{2.} Two direct methods have been commonly employed,
theoretically inconsistent with one another, though not in every
case noticeably discrepant in practice. The first and simplest of
these may be termed the Inversion of Bernoulli's Theorem, and
\index{Bernoulli's Theorem!Inverse of|ifoll}%
the other Laplace's Rule of Succession.
\index{Laplace!Rule of Succession@{and Rule of Succession}}%
\index{Rule of Succession}%

The earliest discussion of this problem is to be found in the
\index{Leibniz}%
Correspondence of Leibniz and Jac.\ Bernoulli,\footnote
  {For the exact references see \Bibref.}
and its true
nature cannot be better indicated than by some account of the
manner in which it presented itself to these very illustrious
philosophers. The problem is tentatively proposed by Bernoulli
in a letter addressed to Leibniz in the year 1703. We can determine
from \textit{à~priori} considerations, he points out, by how much it
is more probable that we shall throw~$7$ rather than~$8$ with two dice,
but we cannot determine by such means the probability that a
young man of twenty will outlive an old man of sixty. Yet is it
not possible that we might obtain this knowledge \textit{à~posteriori}
from the observation of a great number of similar couples, each
consisting of an old man and a young man? Suppose that the
young man was the survivor in $1000$~cases and the old man in $500$~cases,
might we not conclude that the young man is twice as likely
as the old man to be the survivor? For the most ignorant
persons seem to reason in this way by a sort of natural instinct,
and feel that the risk of error is diminished as the number of
observations is increased. Might not the solution tend asymptotically
to some determinate degree of probability with the
increase of observations? \textit{Nescio, Vir Amplissime, an speculationibus
istis soliditatis aliquid inesse Tibi videatur.}

Leibniz's reply goes to the root of the difficulty. The calculation
of probabilities is of the utmost value, he says, but in statistical
inquiries there is need not so much of mathematical subtlety
as of a precise statement of all the circumstances. The possible
contingencies are too numerous to be covered by a finite number
of experiments, and exact calculation is, therefore, out of the
question. Although nature has her habits, due to the recurrence
of causes, they are general, not invariable. Yet empirical calculation,
although it is inexact, may be adequate in affairs of practice.\footnote
  {Leibniz's actual expressions (in a letter to Bernoulli, December~3, 1703) are
  as follows: Utilissima est aestimatio probabilitatum, quanquam in exemplis
  juridicis politicisque plerumque non tam subtili calculo opus est, quam accurata
  omnium circumstantiarum enumeratione. Cum empirice aestimamus probabilitates
  per experimenta successuum, quaeris an ea via tandem aestimatio
  perfecte obtineri possit. Idque a Te repertum scribis. Difficultas in eo mihi
  inesse videtur, quod contingentia seu quae infinitis pendent circumstantiis, per
  finita experimenta determinari non possunt; natura quidem suas habet consuetudines,
  natas ex reditu causarum, sed non nisi \textgreek{<ws `ep`i t`o pol'u}. Novi morbi
  inundant subinde humanum genus, quodsi ergo de mortibus quotcunque experimenta
  feceris, non ideo naturae rerum limites posuisti, ut pro futuro variare
  non possit. Etsi autem empirice non posset haberi perfecta aestimatio, non
  ideo minus empirica aestimatio in praxi utilis et sufficiens foret.}
%% -----File: 380.png---Folio 369-------
\index{Bernoulli, Jac.}%
\index{Inverse Probability!statistics@{and statistics}}%

Bernoulli in his answer fell back upon the analogy of balls
drawn from an urn, and maintained that without estimating
each separate contingency we might determine within narrow
limits the \emph{proportion} favouring each alternative. If the true
proportion were~$2:1$, we might estimate it with moral certainty
\textit{à~posteriori} as lying between $201:100$ and $199:100$. ``Certus
sum,'' he concluded the controversy, ``Tibi placituram demonstrationem,
cum publicavero.'' But whether he was impressed by
the just caution of Leibniz, or whether death intercepted him,
he advances matters no further in the \textit{Ars Conjectandi}. After
dealing with some of Leibniz's objections\footnote
  {The relevant passages are on pp.~224--227 of the \textit{Ars Conjectandi}.}
and seeming to
promise some mode of estimating probabilities \textit{à~posteriori} by an
inversion of his theorem, he proves the direct theorem only and
the book is suddenly at an end.

\Paragraph{3.} In dealing with the correspondence of Leibniz and Bernoulli,
I have not been mainly influenced by the historical interest
of it. The view of Leibniz, dwelling mainly on considerations
of analogy, and demanding ``not so much mathematical subtlety
as a precise statement of all the circumstances,'' is, substantially,
the view which will be supported in the following chapters.
The desire of Bernoulli for an exact formula, which would derive
from the numerical frequency of the experimental results a
numerical measure of their probability, preludes the exact
formulas of later and less cautious mathematicians, which will be
examined immediately.

\Paragraph{4.} During the greater part of the eighteenth century there is
no trace, I think, of the explicit use of the Inversion of Bernoulli's
Theorem. The investigations carried out by D'Alembert, Daniel
\index{D'Alembert}%
Bernoulli, and others relied upon the type of argument examined
in \Chapref{XXV}\@. They showed, that is to say, that certain
observed series of events would have been very improbable, if
we had supposed independence between some two factors or if
%% -----File: 381.png---Folio 370-------
\index{De Morgan!Inverse@{and Inverse of Bernoulli's Theorem}|inote}%
\index{Inverse Probability!statistics@{and statistics}|inote}%
\index{Munro|inote}%
\index{Todhunter|inote}%
some occurrence had been assumed to be as likely as not, and they
inferred from this that there was in fact a measure of dependence
or that the occurrence had probability in its favour. But they
did not endeavour to pass from the observed frequency of occurrence
to an exact measure of the probability. With the advent
of Laplace more ambitious methods took the field.
\index{Laplace!Bernoulli's Theorem@{and Bernoulli's Theorem}}%
\index{Laplace!unknown probabilities@{and unknown probabilities}}%

Laplace began by assuming without proof a direct inversion
of Bernoulli's Theorem. Bernoulli's Theorem, in the form in
which Laplace proved it, states that, if $p$~is the probability \textit{à~priori},
there is a probability~$P$ that the proportion of times $\dfrac{m}{m+n}$
of the event's occurrence in $\mu\,(=m+n)$ trials will lie between
$p±\gamma\sqrt{\dfrac{2pq}{\mu}}$, where $P = \displaystyle\frac{2}{\sqrt{\pi}}\int_0^\gamma e^{-t^2}\, dt + \frac{1}{\sqrt{2\pi\mu pq}}e^{-\gamma^2}$. The inversion
of the theorem, which he assumes without proof,
states that, if the event is observed to happen $m$~times
in $\mu$~trials, there is a probability~$P$ that the probability
of the event~$p$ will lie between $\dfrac{m}{\mu} ± \gamma\sqrt{\dfrac{2mn}{\mu^3}}$, where
$P = \displaystyle\frac{2}{\sqrt{\pi}} \int_0^\gamma e^{-t^2}\, dt + \frac{1}{\sqrt{2\pi\mu\dfrac{m}{\mu^2}}}e^{-\gamma^2}$. The same result is also given
\index{Poisson!inverse@{and inverse of Bernoulli's Theorem}}%
by Poisson.\footnote
  {For an account of the treatments of this topic both by Laplace and by
  Poisson, see Todhunter's \textit{History}, pp.~554--557. Both of them also obtain a
  formula slightly different from that given above by a method analogous to the
  first part of the proof of Laplace's Rule of Succession; \ie~by an application of
  the inverse principle of probability to the assumption that the probability of
  the probability's lying within any interval is proportional to the length of the
  interval. This discrepancy has given rise to some discussion. See Todhunter,
  \textit{loc.\ cit.}; De~Morgan, \textit{On a Question in the Theory of Probabilities}; Monro, \textit{On the
  Inversion of Bernoulli's Theorem in Probabilities}; and Czuber, \textit{Entwicklung},
\index{Czuber!Inverse@{and Inverse of Bernoulli's Theorem}|inote}%
  pp.~83,~84. But this is not the important distinction between the two mathematical
  methods by which this question has been approached, and this minor
  point, which is of historical interest mainly, I forbear to enter into.}
Thus, given the frequency of occurrence in $\mu$~trials,
these writers infer the probability of occurrence at
subsequent trials within certain limits, just as, given the
\textit{à~priori} probability, Bernoulli's Theorem would enable them
to predict the frequency of occurrence in $\mu$~trials within corresponding
limits.
%% -----File: 382.png---Folio 371-------

If the number of trials is at all numerous, these limits are
narrow and the purport of the inversion of Bernoulli's Theorem
may therefore be put briefly as follows. By the direct theorem,
if $p$~measures the probability, $p$~also measures the most probable
value of the frequency; by the inversion of the theorem, if $\dfrac{m}{m+n}$
measures the frequency, $\dfrac{m}{m+n}$ also measures the most probable
value of the probability. The simplicity of the process has recommended
it, since the time of Laplace, to a great number of
writers. Czuber's argument, criticised on \Pageref{351}, with reference
to the proportions of male and female births in Austria, is based
upon an unqualified use of it. But examples abound throughout
the literature of the subject, in which the theorem is employed in
circumstances of greater or less validity.

The theorem was originally given without proof, and is indeed
incapable of it, unless some illegitimate assumption has been
introduced. But, apart from this, there are some obvious objections.
We have seen in the preceding chapter that Bernoulli's
Theorem itself cannot be applied to all kinds of \textit{data} indiscriminately,
but only when certain rather stringent conditions are fulfilled.
Corresponding conditions are required equally for the
inversion of the theorem, and it cannot possibly be inferred from
a statement of the number of trials and the frequency of occurrence
merely, that these have been satisfied. We must know,
for instance, that the examined instances are similar in the main
relevant particulars, both to one another and to the unexamined
instances to which we intend our conclusion to be applicable.
An unanalysed statement of frequency cannot tell us this.

This method of passing from statistical frequencies to probabilities
is not, however, like the method to be discussed in a
moment, radically false. With due qualifications it has its place
in the solution of this problem. The conditions in which an
inversion of Bernoulli's Theorem is legitimate will be elucidated
in \Chapref{XXXI}\@. In the meantime we will pass on to Laplace's
second method, which is more powerful than the first and has
obtained a wider currency. The more extreme applications of
it are no longer ventured upon, but the theory which underlies
it is still widely adopted, especially by French writers upon
probability, and seldom repudiated.
%% -----File: 383.png---Folio 372-------
\index{Probability, and relevant knowledge!unknown@{`\textit{unknown},' and Laplace}}%
\index{Rule of Succession}%

\index{Venn!Rule of Succession@{and Rule of Succession}}%
\Paragraph{5.} The formula in question, which Venn\footnote
  {\textit{Logic of Chance}, p~190.}
has called the \textit{Rule
of Succession}, declares that, if we know no more than that an
event has occurred $m$~times and failed $n$~times under given conditions,
then the probability of its occurrence when those conditions
are next fulfilled is $\dfrac{m+1}{m+n+2}$. It is necessary, however,
before we examine the proof of this formula, to discuss in detail
the reasoning which leads up to it.

This preliminary reasoning involves the Laplacian theory of
`unknown probabilities.' The postulate, upon which it depends,
\index{Unknown probabilities}%
is introduced to supplement the Principle of Indifference, and
\index{Principle of Indifference!Laplace@{and Laplace}}%
is in fact the extension of this principle from the probabilities
of arguments, when we know nothing about the arguments, to the
probabilities that the probabilities of arguments have certain
values, when we know nothing about the probabilities. Laplace's
enunciation is as follows: ``Quand la probabilité d'un événement
simple est inconnue, on peut lui supposer également toutes les
valeurs depuis zéro jusqu'à l'unité. La probabilité de chacune
de ces hypothèses tirée de l'événement observé est \ldots\ une
fraction dont le numérateur est la probabilité de l'événement dans
cette hypothèse, et dont le dénominateur est la somme des probabilités
semblables relatives à toutes les hypothèses\ldots.''\footnote
  {\textit{Essai philosophique}, p.~16.}

Thus when the probability of an event is unknown, we may
suppose all possible values of the probability between $0$~and~$1$ to
be equally likely \textit{à~priori}. The probability, \emph{after} the event has
occurred, that the probability \textit{à~priori} was~$\dfrac{1}{r}$ (say), is measured
by a fraction of which $\dfrac{1}{r}$~is the numerator and the sums of all the
possible \textit{à~priori} values the denominator. The origin of this rule
is evident. If we consider the problem in which a ball is drawn
from a bag containing an infinite number of black and white balls
in unknown proportions, we have hypotheses, corresponding to
each of the possible constitutions of the bag, the assumption of
which yields in turn every value between $0$~and~$1$ as the \textit{à~priori}
probability of drawing a white ball. If we could assume that
these constitutions are equally probable \textit{à~priori}, we should
obtain probabilities for each of them \textit{à~posteriori} according to
Laplace's rule.
%% -----File: 384.png---Folio 373-------
\index{Unknown probabilities}%

On the analogy of this Laplace assumes in general that, where
everything is unknown, we may suppose an infinite number of
possibilities, each of which is equally likely, and each of which
leads to the event in question with a \emph{different} degree of probability,
so that for every value between $0$~and~$1$ there is one and only one
hypothetical constitution of things, the assumption of which
invests the event with a probability of that value.

\Paragraph{6.} It might be an almost sufficient criticism of the above to
point out that these assumptions are entirely baseless. But the
theory has taken so important a place in the development of
probability that it deserves a detailed treatment.

What, in the first place, does Laplace mean by an \emph{unknown}
probability? He does not mean a probability, whose value is in
fact unknown \emph{to us}, because we are unable to draw conclusions
which \emph{could be drawn} from the \textit{data}; and he seems to apply the
term to any probability whose value, according to the argument
of \Chapref{III}., is numerically indeterminate. Thus he assumes
that \emph{every} probability has a numerical value and that, in those
cases where there seems to be no numerical value, this value is
not non-existent but unknown; and he proceeds to argue that
where the numerical value is unknown, or as I should say where
there is \emph{no} such value, every value between $0$~and~$1$ is equally
probable. With the possible interpretations of the term `unknown
probability,' and with the theory that every probability
can be measured by one of the real numbers between $0$~and~$1$,
I have dealt, as carefully as I can, in \Chapref{III}\@. If the view
taken there is correct, Laplace's theory breaks down immediately.
But even if we were to answer these questions, not as they have
been answered in \Chapref{III}., but in a manner favourable to
Laplace's theory, it remains doubtful whether we could legitimately
attribute a value to the probability of an unknown probability's
having such and such a value. If a probability is
unknown, surely the probability, relative to the same evidence,
that this probability has a given value, is also unknown; and we
are involved in an infinite regress.

\Paragraph{7.} This point leads on to the second objection; Laplace's
theory requires the employment of both of two inconsistent
methods. Let us consider a number of alternatives $a_1$,~$a_2$,~etc.,
having probabilities $p_1$,~$p_2$,~etc.; if we do not know anything
about~$a_1$, we do not know the value of its probability~$p_1$, and we
%% -----File: 385.png---Folio 374-------
must consider the various possible values of~$p_1$, namely $b_1$,~$b_2$,~etc.,
the probabilities of these possible values being $q_1$,~$q_2$,~etc.\ respectively.
There is no reason why this process should ever stop.
For as we do not know anything about~$b_1$, we do not know the
value of its probability~$q_1$, and we must consider the various
possible values of~$q_1$ namely $c_1$,~$c_2$,~etc., the probabilities of these
possible values being $r_1$,~$r_2$,~etc., respectively; and so on. This
method consists in supposing that, when we do not know anything
about an alternative, we must consider all the possible values of
the probability of the alternative; these possible values can form
in their turn a set of alternatives, and so on. But this method
\emph{by itself} can lead to no final conclusion. Laplace superimposes
on it, therefore, his other method of determining the probabilities
of alternatives about which we know nothing,---namely, the
Principle of Indifference. According to this method, when
\index{Principle of Indifference!Laplace@{and Laplace}}%
we know nothing about a set of alternatives, we suppose the
probabilities of each of them to be \emph{equal}. In some parts of
his writings---and this is true also of most of his followers---he
applies this method from the beginning. If, that is to say, we
know nothing about~$a_1$, since $a_1$~and its contradictory form a pair
of exhaustive alternatives two in number, the probability of these
alternatives is \emph{equal} and each is~$\dfrac{1}{2}$. But in the reasoning which
leads up to the Law of Succession he chooses to apply this method
at the second stage, having used the other method at the first
stage. If, that is to say, we know nothing about~$a_1$, its probability~$p_1$
may have any of the values $b_1$,~$b_2$,~etc.\ where $b_1$~is any
fraction between $0$~and~$1$; and, as we know nothing about the
probabilities $q_1$,~$q_2$,~etc.\ of these alternatives $b_1$,~$b_2$,~etc., we may
by the Principle of Indifference suppose them to be \emph{equal}. This
account may seem rather confused; but it is not easy to give
a lucid account of so confused a doctrine.

\Paragraph{8.} Turning aside from these considerations, let us examine
the theory, for a moment, from another side. When we reach the
Rule of Succession, it will be seen that the hypothetical \textit{à~priori}
\index{Rule of Succession}%
probabilities are treated as if they were possible \emph{causes} of the
event. It is assumed, that is to say, that the number of possible
sets of antecedent conditions is proportional to the number of
real numbers between $0$~and~$1$; and that these fall into equal
groups, each group corresponding to one of the real numbers
%% -----File: 386.png---Folio 375-------
\index{De Morgan!Rule of Succession@{and Rule of Succession}}%
between $0$~and~$1$, this number measuring the degree of probability
with which we could predict the event, if we knew that an antecedent
condition belonging to that group was fulfilled. It is
then assumed that all of these possible antecedent conditions are
\textit{à~priori} equally likely. The argument has arisen by false analogy
from the problem in which a ball is drawn from an urn containing
an infinite number of black and white balls. But for the assumption
that we have \emph{in general} the kind of knowledge which is
necessary about the possible antecedents, no reasonable foundation
has been suggested.

De~Morgan endeavoured to deal with the difficulty in much
the same way in the following passage:\footnote
  {\textit{Cabinet Encyclopaedia}, p.~87.}
``In determining the
chance which exists (under known circumstances) for the happening
of an event a number of times which lies between certain
limits, we are involved in a consideration of some difficulty,
namely, the \emph{probability of a probability}, or, as we have called it,
the presumption of a probability. To make this idea more clear,
remember that any state of probability may be immediately
made the expression of the result of a set of circumstances, which
being introduced into the question, the difficulty disappears.
The word presumption refers distinctly to an act of the mind, or a
state of the mind, while in the word probability we feel disposed
rather to think of the external arrangements on the knowledge
of which the strength of our presumption ought to depend, than
of the presumption itself.'' The point of this explanation lies
in the assumption that ``any state of probability may be immediately
made the expression of the result of a set of circumstances.''
It cannot be allowed that this is generally true;\footnote
  {For instance, it is not true even in the standard instance of balls drawn from
  an urn containing black and white in unknown proportions, unless the number
  of balls is infinite.}
and even in
those cases in which it is true we are thrown back on the \textit{à~priori}
probabilities of the various sets of circumstances which need not
be, as De~Morgan assumes, either equal or exhaustive alternatives.

\Paragraph{9.} The proof of the Rule of Succession, which is based upon
\index{Rule of Succession!proof of}%
this theory of unknown probabilities, is, briefly, as follows:
\index{Unknown probabilities}%

If $x$~stands for the \textit{à~priori} probability of an event in given
conditions, then the probability that the event will occur $m$~times
and fail $n$~times in these conditions is~$x^m(1-x)^n$. If,
however, $x$~is unknown, all values of it between $0$~and~$1$
%% -----File: 387.png---Folio 376-------
\index{Whittaker, E. T., and Rule of Succession|inote}%
are \textit{à~priori} equally probable. It follows from these two
sets of considerations that, if the event has been observed
to occur $m$ times out of $m+n$, the probability \textit{à posteriori} that
$x$ lies between $x$ and $x+dx$ is proportional to $x^m(1-x)^ndx$,
and is equal, therefore, to $Ax^m(1-x)^ndx$ where $A$ is a constant.
Since the event has in fact occurred, and since $x$ must have
one of its possible values, $A$ is determined by the equation
\[
\int_0Ax^m(1-x)^ndx=1\quad\therefore A=\dfrac{\Gamma(m+n+2)}{\Gamma(m+1)\Gamma(n+1)}.
\]
Hence the probability that the event will occur at the $(m+n+1)$th
trial, when we know that it has occurred $m$ times in $m+n$
trials, is
\[
A\int_0^1 x^{m+1}(1-x)^ndx.
\]
If we substitute the value of A found above, this is equal to
$\dfrac{m+1}{m+n+2}$.\footnote
  {The theorem is sometimes enunciated by contemporary writers in a much
  more guarded form, \eg\ by Czuber, \textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ p.~197,
\index{Czuber!Rule of Succession@{and Rule of Succession}|inote}%
  and by Bachelier, \textit{Calcul des probabilités}, p.~487. Bachelier, instead of assuming
\index{Bachelier!Rule of Succession@{and Rule of Succession}|inote}%
  that the \textit{à~priori} probabilities of all possible values of the probability of the
  event are equal, writes $\hat\omega(y)dy$ as the \textit{à~priori} probability that the probability is~$y$,
  so that after $m$~occurrences \DPtypo{is}{in} $m+n$~trials the probability that the probability
  lies between $y$~and~$y+dy$ is $\dfrac{y^m(1-y)^n\hat\omega(y)dy}{\int y^m(1-y)^n\hat\omega(y)dy}$. If one has no idea of $\hat\omega$ \textit{à~priori},
  he suggests that the simplest hypothesis is to put $\hat\omega=1$, which leads, as
  above, to Laplace's Law of Succession. He also proposes the hypothesis
  $\hat\omega(y)=a+a_1y+a_2y^2+\ldots$, in which case the denominator is a series of Eulerian
  integrals. There is a discussion of the Law of Succession, and of the contradictions
  and paradoxes to which it leads, by E.~T. Whittaker and others in
  Part~VI. vol.~viii.\ (1920) of the \textit{Transactions of the Faculty of Actuaries in
  Scotland}.}

The class of problem to which the theorem is supposed to
apply is the following: There are certain conditions such that we
are ignorant \textit{à~priori} as to whether they do or do not lead to the
occurrence of a particular event; on $m$ out of $m+n$ occasions,
however, on which these conditions have been observed, the
event has occurred; what is the probability in the light of this
experience that the event will occur on the next occasion? The
answer to all such problems is $\dfrac{m+1}{m+n+2}$. In the cases where
$n=0$, \ie\ when the event has invariably occurred, the formula
%% -----File: 388.png---Folio 377-------
yields the result $\dfrac{m + 1}{m + 2}$. In the case where the conditions have
been observed once only and the event has occurred on that
occasion, the result is~$\dfrac{2}{3}$. If the conditions have \emph{never} been met
with at all, the probability of the event is~$\dfrac{1}{2}$. And even in the
case where on the only occasion on which the conditions were
observed, the event did \emph{not} occur, the probability is~$\dfrac{1}{3}$.

Some of the flaws in this proof have been already explained.
One minor objection may be pointed out in addition. It is
assumed that, if $x$~is the \textit{à~priori} probability of the event's happening
once, then $x^n$~is the \textit{à~priori} probability of its happening $n$~times
in succession, whereas by the theorem's own showing the
knowledge that the event has happened once modifies the probability
of its happening a second time; its successive occurrences
are not, therefore, independent. If the \textit{à~priori} probability of the
event is~$\dfrac{1}{2}$, and if, after it has been observed once, the probability
that it will occur a second time is~$\dfrac{2}{3}$, then it follows that the \textit{à~priori}
probability of its occurring twice is not $\dfrac{1}{2} × \dfrac{1}{2}$, but $\dfrac{1}{2} × \dfrac{2}{3}$,
\ie~$\dfrac{1}{3}$; and in general the \textit{à~priori} probability of its happening
n times in succession is not $\left(\dfrac{1}{2}\right)^n$ but~$\dfrac{1}{n+1}$.

\Paragraph{10.} But refinements of disproof are hardly needed. The
principle's conclusion is inconsistent with its premisses. We
begin with the assumption that the \textit{à~priori} probability of an event,
about which we have no information and no experience, is unknown,
and that all values between 0 and 1 are equally probable.
We end with the conclusion that the \textit{à~priori} probability of
such an event is~$\dfrac{1}{2}$. It has been pointed out in §\;7 that this
contradiction was latent, as soon as the Principle of Indifference
\index{Principle of Indifference!Rule of Succession@{and Rule of Succession}}%
was superimposed on the principle of unknown probabilities.

The theorem's conclusions, moreover, are a \textit{reductio ad
absurdum} of the reasoning upon which it is based. Who could
suppose that the probability of a purely hypothetical event, of
%% -----File: 389.png---Folio 378-------
whatever complexity, in favour of which no positive argument
exists, the like of which has \emph{never} been observed, and which has
failed to occur on the one occasion on which the hypothetical
conditions were fulfilled, is no less than~$\dfrac{1}{3}$? Or if we do suppose it,
we are involved in contradictions,---for it is easy to imagine more
than three \emph{incompatible} events which satisfy these conditions.

\Paragraph{11.} The theorem was first suggested by the problem of the urn
which contains black and white balls in unknown proportions:
$m$ white and $n$ black balls have been successively drawn and
replaced; what is the probability that the next draw will yield
a white ball? It is supposed that all compositions of the urn are
equally probable, and the proof then proceeds precisely as in the
case of the more general rule of succession. The rule of succession
\index{Rule of Succession!frequency theory@{and frequency theory}}%
has been, sometimes, directly deduced from the case of the urn,
by assimilating the occurrence of the event to the drawing of a
white ball and its non-occurrence to the drawing of a black ball.

On the hypothesis that all compositions of the urn are equally
probable, an hypothesis to which in general there is nothing corresponding,
and on the further hypothesis that the number of balls
is infinite, this solution is correct.\footnote
  {This second condition is often omitted (\eg\ Bertrand, \textit{Calcul des probabilités},
  p.~172).}
But the rule of succession
does not apply, as it is easy to demonstrate, even to the case of
balls drawn from an urn, if the number of balls is finite.\footnote
  {The correct solution for the case of a finite number of balls, on the hypothesis
  that each possible ratio is equally likely, is as follows: The probability
  of a black ball at a further trial, after black balls have been successively withdrawn
  and replaced $p$~times, is $\dfrac{1}{n}\,\dfrac{s_{p+1}}{s_p}$ where there are $n$~balls and $s_r$~represents
  the sum of the $r$th~powers of the first $n$~natural numbers. This reduces to
  $\dfrac{p+1}{p+2}$---the solution usually given,---when $n$~is infinite. More generally, if
  $p$~black balls and $q$~white balls have been drawn and replaced, the chance
  that the next ball will be black is
  \[ %[** TN: Displaying in-line formula.]
  \frac{1}{n}\,
  \frac{ \Sum^{r=n}_{r=0} r^{p+1}(n-r)^q}{\Sum^{r=n}_{r=0} r^p (n-r)^q}.
  \]}

\Paragraph{12.} If the Rule of Succession is to be adopted by adherents of
\index{Frequency theory!Rule of Succession@{and Rule of Succession}}%
the Frequency Theory of Probability,\footnote
  {See \Chapref{VIII}\@.}
it is necessary that they
should make some modification in the preliminary reasoning on
which it is based. By Dr.~Venn, however, the rule has been
\index{Venn!Rule of Succession@{and Rule of Succession}}%
%% -----File: 390.png---Folio 379-------
\index{Bayes, and Inverse Probability!Theorem of}%
\index{Pearson, Karl!Rule of Succession@{and Rule of Succession}}%
explicitly rejected on the ground that it does not accord with
experience.\footnote
  {\textit{Logic of Chance}, p.~197.}
But Professor Karl Pearson, who accepts it, has
made the necessary restatement,\footnote
  {``On the Influence of Past Experience on Future Expectation,'' \textit{Phil.\
  Mag.}\ 1907, pp.~365--378. The quotations given below are taken from this
  article.}
and it will be worth while to
examine the reasoning when it is put in this form. Professor
Pearson's proof of the Rule of Succession is as follows:

``I start, as most mathematical writers have done, with `the
equal distribution of ignorance,' or I assume the truth of Bayes'
Theorem. I hold this theorem not as rigidly demonstrated, but
\index{Edgeworth}%
I think with Edgeworth\footnote
  {This reference is, no doubt, to Edgeworth's ``Philosophy of Chance''
  (\textit{Mind}, 1884, p.~230), when he wrote: ``The assumption that any probability-constant
  about which we know nothing in particular is as likely to have one value
  as another is grounded upon the rough but solid experience that such constants
  do, as a matter of fact, as often have one value as another.'' See also \Chapref{VII}.
  §\;6, above.}
that the hypothesis of the equal distribution
of ignorance is, within the limits of practical life, justified
by our experience of statistical ratios, which \textit{à~priori} are
unknown, \ie\ such ratios do not tend to cluster markedly round
any particular value. `Chances' lie between $0$~and~$1$, but our
experience does not indicate any tendency of actual chances to
cluster round any particular value in this range. The ultimate
basis of the theory of statistics is thus not mathematical but
observational. Those who do not accept the hypothesis of the
equal distribution of ignorance and its justification in observation
are compelled to produce definite evidence of the clustering of
chances, or to drop all application of past experience to the judgment
of probable future statistical ratios\ldots.

``Let the chance of a given event occurring be supposed to lie
between $x$~and~$x + dx$, then if on $n = p + q$ trials an event has been
observed to occur $p$~times and fail $q$~times, the probability that
the true chance lies between $x$~and~$x + dx$ is, on the equal
distribution of our ignorance,
\[
P_z = \frac{x^p (1-x)^q\, dx}{\int^1_0 x^p (1-x)^q\, dx}.
\]

``This is Bayes' Theorem\ldots.\footnote
  {Professor Pearson's use of this title for the above formula is not, I think,
  historically correct. Bayes' Theorem is the Inverse Principle of Probability
  itself, and not this extension of it.}
%% -----File: 391.png---Folio 380-------

``Now suppose that a second trial of $m=r + s$ instances be
made, then the probability that the given event will occur $r$~times
and fail~$s$, is on the \textit{à~priori} chance being between $x$~and~$x+dx$
\[
= P_x\frac{\Gamma m}{\Gamma r\Gamma s}n^r(1-x)^s,
\]
and accordingly the total chance~$C_r$, whatever $x$~may be of the
event occurring $r$~times in the second series, is
\[
C_r = \frac{\Gamma m}{\Gamma r\Gamma s}\,
  \dfrac{\int_0\DPtypo{}{^1} x^{p+r}(1-x)^{q+s}\, dx}
        {\int_0^1 x^p(1-x)^{q}\, dx}.
\]

This is, with a slight correction, Laplace's extension of Bayes'
\index{Laplace!Bayes' Theorem@{and Bayes' Theorem}}%
Theorem.''\footnote
  {The rest of the article is concerned with the determination of the probable
  error when Laplace's Rule of Succession is used not simply to yield the probability
\index{Rule of Succession!Pearson@{and Pearson}|inote}%
  of a single additional occurrence, but to predict the probable limits within
  which the frequency will lie in a considerable series of additional trials. Professor
  Pearson's method applies more rigorous methods of approximation to
  the fundamental formulae given above than have been sometimes used. As
  my main purpose in this chapter is to dispute the general validity of the fundamental
  formulae, it is not worth while to consider these further developments
  here. If the validity of the fundamental formula were to be granted, Professor
  Pearson's methods of approximation would, I think, be satisfactory.}

\Paragraph{13.} This argument can be restated as follows. Of all the
objects which satisfy~$\phi(x)$, let us suppose that a proportion~$p$
also satisfy~$f(x)$. In this case $p$~measures the probability that
any object, of which we know only that it is~$\phi$, is in fact also~$f$.
Now if we do not know the value of~$p$ and have no relevant information
which bears upon it, we can assume \textit{à~priori} that all
values of~$p$ between $0$~and~$1$ are equally likely. This assumption,
which is termed the `equal distribution of ignorance,' is justified
by our experience of statistical ratios. Our experience, that is
to say, leads us to suppose that of all the theories, which could be
propounded, there are just as many which are always true as
there are which are always false, just as many which are true once
in fifty times as there are which are true once in three times, and
so on. Professor Pearson challenges those who do not accept
this assumption to produce definite evidence to the contrary.

The challenge is easily met. It would not be difficult to produce
$10,000$ positive theories which are always false corresponding
to every one which is always true, and $10,000$ correlations of positive
%% -----File: 392.png---Folio 381-------
qualities which hold less often than once in three times for
every one we can name which holds more often than once in three
times. And the converse is the case for negative theories and
correlations between negative qualities; for corresponding to
every positive theory which is true there is a negative theory
which is false, and so on. Thus experience, if it shows anything,
shows that there is a very marked clustering of statistical ratios
in the neighbourhoods of zero and unity,---of those for positive
theories and for correlations between positive qualities in the
neighbourhood of zero, and of those for negative theories and for
correlations between negative qualities in the neighbourhood of
unity. Moreover, we are seldom in so complete a state of ignorance
regarding the nature of the theory or correlation under
investigation as not to know whether or not it is a positive theory
or a correlation between positive qualities. In general, therefore,
whenever our investigation is a practical one, experience, if it
tells us anything, tells us not only that the statistical ratios cluster
in the neighbourhood of zero and unity, but in which of these two
neighbourhoods the ratio in this particular case is most likely
\textit{à~priori} to be found. If we seek to discover what proportion of
the population suffer from a certain disease, or have red hair, or
are called Jones, it is preposterous to suppose that the proportion
is as likely \textit{à~priori} to exceed as to fall short of (say) fifty per cent.
As Professor Pearson applies this method to investigations where
it is plain that the qualities involved are positive, he seems to
maintain that experience shows that there are as many positive
attributes which are shared by more than half of any population
as there are which are shared by less than half.

It is also worthwhile to point out that it is formally impossible
that it should be true of all characters, simple and complex, that
they are as likely to have any one frequency as any other. For let
us take a character $c$ which is compound of two characters $a$~and~$b$,
between which there is no association, and let us suppose that
a has a frequency~$x$ in the population in question and that $b$~has
a frequency~$y$, so that, in the absence of association, the frequency~$z$
of~$c$ is equal to~$xy$. Then it is easy to show that, if all values of
$x$~and~$y$ between $0$~and~$1$ are equally probable, all values of~$z$
between $0$~and~$1$ are \emph{not} equally probable. For the value~$\dfrac{1}{2}$
is more probable than any other, and the possible values of~$z$
%% -----File: 393.png---Folio 382-------
\index{De Morgan!Rule of Succession@{and Rule of Succession}}%
\index{Pearson, Karl!Rule of Succession@{and Rule of Succession}}%
become increasingly improbable as they differ more widely
from~$\dfrac{1}{2}$.

It may be added that the conclusions, which Professor
Pearson himself derives from this method, provide a \textit{reductio
ad absurdum} of the arguments upon which they rest. He considers,
for example, the following problem: A sample of~$100$ of a
population shows $10$~per cent affected with a certain disease.
What percentage may be reasonably expected in a second sample
of~$100$? By approximation he reaches the conclusion that the
percentage of the character in the second sample is as likely to
fall inside as outside the limits, $7.85$~and~$13.71$.\DPnote{** TN: Original uses centered dot.} Apart from the
preceding criticisms of the reasoning upon which this depends,
it does not seem reasonable upon general grounds that we should
be able on so little evidence to reach so certain a conclusion. The
argument does not require, for example, that we have any knowledge
of the manner in which the samples are chosen, of the
positive and negative analogies between the individuals, or indeed
anything at all beyond what is given in the above statement.
The method is, in fact, much too powerful. It invests any positive
conclusion, which it is employed to \emph{support}, with far too high
a degree of probability. Indeed this is so foolish a theorem
that to entertain it is discreditable.

\Paragraph{14.} The Rule of Succession has played a very important part
in the development of the theory of probability. It is true that
\index{Boole!Rule of Succession@{and Rule of Succession}}%
it has been rejected by Boole\footnote
  {\textit{Laws of Thought}, p.~369.}
on the ground that the hypotheses
on which it is based are arbitrary, by Venn\footnote
  {\textit{Logic of Chance}, p.~197.}
on the ground that it
\index{Bertrand!Rule of Succession@{and Rule of Succession}}%
does not accord with experience, by Bertrand\footnote
  {\textit{Calcul des probabilités}, p.~174.}
because it is
ridiculous, and doubtless by others also. But it has been very
widely accepted,---by De~Morgan,\footnote
  {Article in \emph{Cabinet Encyclopaedia}, p\DPtypo{}{.}~64.}
\index{Jevons!Rule of Succession@{and Rule of Succession}}%
by Jevons,\footnote
  {\textit{Principles of Science}, p.~297.}
\index{Lotze!Rule of Succession@{and Rule of Succession}}%
by Lotze,\footnote
  {\textit{Logic}, pp.~373,~374; Lotze propounds a ``simple deduction'' ``as convincing''
  to him ``as the more obscure analysis, by which it is usually obtained.''
  The proof is among the worst ever conceived, and may be commended to those
  who seek instances of the profound credulity of even considerable thinkers.}
by
\index{Czuber!Rule of Succession@{and Rule of Succession}}%
Czuber,\footnote
  {\textit{Wahrscheinlichkeitsrechnung}, vol.~i.\ p.~199,---though much more guardedly
  and with more qualifications than in the form discussed above.}
and by Professor Pearson,\footnote
  {\textit{Loc.~cit.}}%
---to name some representative
writers of successive schools and periods. And, in any case, it
%% -----File: 394.png---Folio 383-------
\index{Bobek and Rule of Succession}%
is of interest as being one of the most characteristic results of a
way of thinking in probability introduced by Laplace, and never
thoroughly discarded to this day. Even amongst those writers
who have rejected or avoided it, this rejection has been due
more to a distrust of the particular applications of which the law
is susceptible than to fundamental objections against almost
every step and every presumption upon which its proof depends.

Some of these particular applications have certainly been
surprising. The law, as is evident, provides a numerical measure
of the probability of any simple induction, provided only that our
ignorance of its conditions is sufficiently complete, and, although,
when the number of cases dealt with is small, its results are incredible,
there is, when the number dealt with is large, a certain
plausibility in the results it gives. But even in these cases
paradoxical conclusions are not far out of sight. When Laplace
proves that, account being taken of the experience of the human
race, the probability of the sun's rising to-morrow is $1,826,214$ to~$1$,
this large number may seem in a kind of way to represent our
state of mind about the matter. But an ingenious German,
Professor Bobek,\footnote
  {\textit{Lehrbuch der Wahrscheinlichkeitsrechnung}, p.~208.}
has pushed the argument a degree further, and
proves by means of these same principles that the probability of
the sun's rising every day for the next $4000$ years, is not more,
approximately, than two-thirds,---a result less dear to our natural
prejudices.
%% -----File: 395.png---Folio 384-------
\index{Bortkiewicz, von, and great numbers!method of}%
\index{Lexis, and asymmetry of statistical frequency!method of}%


\Chapter{XXXI}{The Inversion of Bernoulli's Theorem}

\Paragraph{1.} \First{I conclude}, then, that the application of the mathematical
methods, discussed in the preceding chapter, to the general
problem of statistical inference is invalid. Our state of knowledge
about our material must be positive, not negative, before
we can proceed to such definite conclusions as they purport to
justify. To apply these methods to material, unanalysed in
respect of the circumstances of its origin, and without reference
to our general body of knowledge, merely on the basis of arithmetic
and of those of the characteristics of our material with
which the methods of descriptive statistics are competent to
deal, can only lead to error and to delusion.

But I go further than this in my opposition to them. Not
only are they the children of loose thinking, and the parents of
charlatanry. Even when they are employed by wise and competent
hands, I doubt whether they represent the most fruitful
form in which to apply technical and mathematical methods to
statistical problems, except in a limited class of special cases.
The methods associated with the names of Lexis, Von Bortkiewicz,
and Tschuprow (of whom the last named forms a link, to some
\index{Tschuprow!method of}%
extent, between the two schools), which will be briefly described
in the next chapter, seem to me to be much more clearly consonant
with the principles of sound induction.

\Paragraph{2.} Nevertheless it is natural to suppose that the fundamental
ideas, from which these methods have sprung, are not wholly
\textit{égarés}. It is reasonable to presume that, subject to suitable conditions
and qualifications, an inversion of Bernoulli's Theorem
must have validity. If we \emph{knew} that our material could be
likened to a game of chance, we might expect to infer chances
from frequencies, with the same sort of confidence as that with
%% -----File: 396.png---Folio 385-------
which we infer frequencies from chances. This part of our
inquiry will not be complete, therefore, until we have endeavoured
to elucidate the conditions for the validity of an Inversion of
Bernoulli's Theorem.
\index{Bernoulli's Theorem!Inverse of|ifoll}%

\Paragraph{3.} The problem is usually discussed in terms of the happening
of an event under certain conditions, that is to say, of the coexistence
of the conditions, as affecting a particular event, with
that event. The same problem can be dealt with more generally
and more conveniently as an investigation of the correlation
between two characters $A(x)$~and~$B(x)$, which, as in \Partref{III}.,
are propositional functions which may be said to concur or coexist
when they are both true of the same argument~$x$. Given
that, within the field of our knowledge, $B(x)$~is true for a certain
proportion of the values of~$x$ for which $A(x)$~is true, what is the
probability for a further value~$a$ of~$x$ that, if $A(a)$~holds, $B(a)$~will
hold also?

Let us suppose that the occurrence of an instance of~$A(x)$ is a
sign of one of the events $e_{1}(x), e_{2}(x)\ldots$ or $e_{m}(x)$, and that these
are exhaustive, exclusive, and ultimate alternatives. By \emph{exhaustive}
it is meant that, whenever there is an instance of~$A(x)$,
one of the~$e$'s is present; by \emph{exclusive}, that the presence of one
of the~$e$'s is not a sign of the presence of any other, but not that
the concurrence of two or more of the~$e$'s is in fact impossible;
by \emph{ultimate}, that no one of the~$e$'s is a disjunction of two or more
alternatives which might themselves be members of the~$e$'s.
Let us assume that these alternatives are initially and \emph{throughout
the argument} equally probable, which, subject to the above conditions,
is justified by the Principle of Indifference. We have no
reason, that is to say, and no part of our evidence ever gives us
one, for thinking that $A(a)$~is more likely to be a sign of one of the~$e$'s
than of any other, or even for thinking that some~$e$'s, although
we do not know which, are more likely to occur than others.
Let us also assume that, out of $e_{1}(x), e_{2}(x) \ldots e_{m}(x)$, the set
$e_{1}(x), e_{2}(x) \ldots e_{l}(x)$, and these only, are signs or occasions of~$B(x)$;
and further that we have no evidence bearing on the actual
magnitude of the integers $l$~and~$m$, so that the \emph{ratio}~$l/m$ is the
only factor of which the probability varies as the evidence
accumulates. Let us assume, lastly, that our knowledge of the
several instances of~$B(x)$ is adequate to establish a perfect analogy
between them; the instances~$a$, etc., of~$B(x)$, that is to say, must
%% -----File: 397.png---Folio 386-------
not have anything in common except~$B$, unless we have reason
to know that the additional resemblances are immaterial. Even
by these considerable simplifications not every difficulty has
been avoided. But a development along the usual lines with
the assistance of Bernoulli's Theorem is now possible.

Let $l/m = q$. If the value of~$q$ were known, the problem would
be solved. For this numerical ratio would represent the probability
that $A$~is, in any random instance, a sign of~$B$; and no
further evidence, which satisfies the conditions of the preceding
hypothesis, can possibly modify it. But in the inverse problem
$q$~is not known; and our problem is to determine whether evidence
can be forthcoming of such a kind, that, as this evidence is increased
in quantity, the probability that $A$~will be in any instance
a sign of~$B$, tends to a limit which lies between two determinate
ratios, just as the probability of an inductive generalisation may
tend towards certainty, when the evidence is increased in a
manner satisfying given conditions.

Let $f(q)$ represent the proposition that $q$~is the true value of~$l/m$.
Let $q'$~represent the ratio of the number of instances actually
before us in which $A$~has been accompanied by~$B$ to that of the
instances in which $A$~has not been accompanied by~$B$; and let
$f'(q')$ be the proposition which asserts this. Now if the ratio~$q$
is known, then, subject to the assumptions already stated, the
number~$q$ must also represent the \textit{à~priori} probability in any
instance, both before and after the results of other instances are
known, that~$A$, if it occurs, will be accompanied by~$B$. We have,
in fact, the conditions as set forth in \Chapref{XXIX}., in which
Bernoulli's Theorem can be validly applied, so that this theorem
enables us to give a numerical value, for all numerical values of
$q$~and~$q'$, to the probability $f'(q')/h· f(q)$,---which expression represents
the likelihood \textit{à~priori} of the frequency~$q'$, given~$q$.

An application of the inverse formula allows us to infer from
the above the \textit{à posteriori} probability of~$q$, given~$q'$, namely:
\[
\frac{f(q)/h · f(q')/h · f(q)}
{\Sum f(q)/h · f(q')/h · f(q)}
\]
where the summation in the denominator covers all possible
values of~$q$. In rough applications of this inverse of Bernoulli's
Theorem it has been usual to suppose that $f(q)/h$~is constant for
all values of~$q$,---that, in other words, all possible values of the
%% -----File: 398.png---Folio 387-------
ratio~$q$ are \textit{à~priori} equally likely. If this supposition were
legitimate, the formula could be reduced to the algebraical expression
\[
\frac{f(q')/h· f(q)}{\Sum f(q')/h· f(q)},
\]
all the terms of which can be determined numerically by Bernoulli's
Theorem. It is easy to show that it is a maximum when
$q=q'$, \ie\ that $q'$~is the most probable value of~$l/m$, and that,
when the instances are very numerous, it is very improbable that
$l/m$~differs from $q'$ widely. If, therefore, the number of instances
is increased in such a manner that the ratio continues in the
neighbourhood of~$q'$, the probability that the true value of~$l/m$
is nearly~$q'$ tends to certainty; and, consequently, the probability,
that $A$~is in any instance a sign of~$B$, also tends to a
magnitude which is measured by~$q'$.

I see, however, no justification for the assumption that all
possible values of the ratio~$q$ are \textit{à~priori} equally likely. It is
not even equivalent to the assumptions that all integral values
of $l$~and~$m$ respectively are equally probable. I am not satisfied
\emph{either} that different values of~$q$, or that different values of~$m$,
satisfy the conditions which have been laid down in \Partref{I}. for
alternatives which are equal before the Principle of Indifference.
There seem, for instance, to be relevant differences between the
statement that $A$~can arise in exactly two ways and the statement
that it can arise in exactly a thousand ways. We must,
therefore, be content with some lesser assumption and with a
less precise form for our final conclusion.

\Paragraph{4.} Since, in accordance with our hypothesis, $m$~cannot exceed
some finite number, and since $l$~must necessarily be less than~$m$,
the possible values of~$m$, and therefore of~$q$, are finite in number.
Perhaps we can assume, therefore, as one of our fundamental
assumptions, that there is \textit{à~priori} a finite probability in favour
of each of these possible values. Let $\mu$~be the finite number
which $m$~cannot exceed. Then there is a \emph{finite} probability for
each of the intervals\footnote
  {The intervals are supposed to include their lower but not their upper
  limit.}
\[
\frac{1}{\mu} \text{ to } \frac{2}{\mu}, \quad
\frac{2}{\mu} \text{ to } \frac{3}{\mu}, \ \ldots \
\frac{\mu - 1}{\mu} \text{ to } 1
\]
%% -----File: 399.png---Folio 388-------
\index{Measurement of Probability!induction@{and induction}}%
that $q$~lies in this interval; but we cannot assume that there is
an \emph{equal} probability for each interval.

We must now return to the formula
\[
\frac{f{q}/h · f(q')/hf(q)}{\Sum f(q)/h · f(q')/hf(q)},
\]
which represents the \textit{à posteriori} probability of~$q$, given~$q'$. Since
by sufficiently increasing the number of instances, the sum of
terms $f(q')/hf(q)$ for possible values of~$q$ within a certain finite
interval in the neighbourhood of~$q'$ can be made to exceed the
other terms by any required amount, and since the sum of the
values of $f(q)/h$ for possible values of~$q$ within this interval is
finite, it clearly follows that a finite number of instances can
make the probability, that $q$~lies in an interval of magnitude
$1/\mu$ in the neighbourhood of~$q'$, to differ from certainty by less
than any finite amount however small.

\Paragraph{5.} We have, therefore, reached the main part of the conclusion
after which we set out---namely, that as the number of instances
is increased the probability, that $q$~is in the neighbourhood of~$q'$,
tends towards certainty; and hence that, subject to certain
specified conditions, if the frequency with which $B$~accompanies~$A$
is found to be~$q'$ in a great number of instances, then the
probability that $A$~will be accompanied by~$B$ in any further
instance is also approximately~$q'$. But we are left with the same
vagueness, as in the case of generalisation, respecting the value
of~$\mu$ and the number of instances that we require. We know
that we can get as near certainty as we choose by a finite number
of instances, but what this number is we do not know. This is
not very satisfactory, but it accords very well, I think, with
what common sense tells us. It would be very surprising, in
fact, if logic could tell us exactly how many instances we want,
to yield us a given degree of certainty in empirical arguments.

Nobody supposes that we can measure exactly the probability
of an induction. Yet many persons seem to believe that in the
weaker and much more difficult type of argument, where the
association under examination has been in our experience, not
invariable, but merely in a certain proportion, we can attribute
a definite measure to our future expectations and can claim
practical certainty for the results of predictions which lie within
relatively narrow limits. Coolly considered, this is a preposterous
%% -----File: 400.png---Folio 389-------
\index{Universal Induction and statistical!methods}%
claim, which would have been universally rejected long ago,
if those who made it had not so successfully concealed themselves
from the eyes of common sense in a maze of mathematics.

\Paragraph{6.} Meantime we are in danger of forgetting that, in order to
reach even our modified conclusion, material assumptions have
been introduced. In the first place, we are faced with exactly
the same difficulties as in the case of universal induction dealt
with in \Partref{III}., and our original starting-point must be the
same. We have the same difficulty as to how our \emph{initial} probability
is to be obtained; and I have no better suggestion to offer
in this than in the former case---namely, the supposed principle
of a limitation of independent variety in experience. We have
to suppose that if $A$~and~$B$ occur together (\ie\ are true of the
same object), this is some just appreciable reason for supposing
that in \emph{this} instance they have a common cause; and that, if
$A$~occurs again, this is a just appreciable reason for supposing
that it is due to the \emph{same} cause as on the former occasion. But
in addition to the usual inductive hypothesis, the argument has
rested on two particularly important assumptions, first, that we
have no reason for supposing that some of the events of which
$A$~may be a sign are more likely to be exemplified in some of the
particular instances than in others, and secondly, that the analogy
amongst the examined~$B$'s is perfect. The first assumption
amounts, in the language of statisticians, to an assumption of
\emph{random sampling} from amongst the~$A$'s. The second assumption
corresponds precisely to the similar condition which we discussed
fully in connection with inductive generalisation. The instances
\index{Generalisation}%
of $A(x)$ may be the result of \emph{random sampling}, and yet it may
still be the case that there are material circumstances, common
to all the examined instances of~$B(x)$, yet not covered by the
statement $A(x)B(x)$. In so far as these two assumptions are not
justified, an element of doubt and vagueness, which is not easily
measured, assails the argument. It is an element of doubt
precisely similar to that which exists in the case of generalisation.
But we are more likely to forget it. For having overcome
the difficulties peculiar to correlation,\footnote
  {I am here using this term in distinction to \emph{generalisation}; that is to say,
  I call the statement that $A(x)$~is always accompanied by~$B(x)$ a \emph{generalisation},
  and the statement that $A(x)$~is accompanied by~$B(x)$ in a certain proportion
  of cases a \emph{correlation}. This is not quite identical with its use by modern
  statisticians.}
it is, possibly, not unnatural
%% -----File: 401.png---Folio 390-------
for a statistician to feel as if he had overcome \emph{all} the
difficulties.

In practice, however, our knowledge, in cases of correlation
\index{Correlation}%
just as in cases of generalisation, will seldom justify the assumption
of perfect analogy between the~$B$'s; and we shall be faced
by precisely the same problems of analysing and improving our
knowledge of the instances, as in the general case of induction
already examined. If $B$~has invariably accompanied~$A$ in $100$~cases,
we have all kinds of difficulties about the exact character
of our evidence before we can found on this experience a valid
generalisation. If $B$~has accompanied~$A$, not invariably, but
only $50$~times in the $100$~cases, clearly we have just the same
kind of difficulties to face, and more too, before we can announce a
valid correlation. Out of the mere unanalysed statement that $B$~has
accompanied~$A$ as often as not in $100$~cases, without precise
particulars of the cases, or even if there were $1,000,000$ cases
instead of~$100$, we can conclude very little indeed.
%% -----File: 402.png---Folio 391-------
\index{Analogy, principle of!statistics@{and statistics}}%


\Chapter{XXXII}{The Inductive use of Statistical Frequencies for the
Determination of Probability \textit{à~posteriori}---the
Methods of Lexis}

\Paragraph{1.} \First{No} one supposes that a good induction can be arrived at
merely by counting cases. The business of strengthening the
argument chiefly consists in determining whether the alleged
association is \emph{stable}, when the accompanying conditions are
varied. This process of improving the Analogy, as I have called
it in \Partref{III}., is, both logically and practically, of the essence of
the argument.

Now in statistical reasoning (or inductive correlation) that
\index{Correlation!Quantitative}%
part of the argument, which corresponds to counting the cases
in inductive generalisation, may present considerable technical
difficulty. This is especially so in the particularly complex cases
of what in the next chapter (§\;9) I shall term \emph{Quantitative Correlation},
which have greatly occupied the attention of
English statisticians in recent years. But clearly it would be an error to
suppose that, when we have successfully overcome the mathematical
or other technical difficulties, we have made any greater
progress towards establishing our conclusion than when, in the
case of inductive generalisation, we have counted the cases but
have not yet analysed or compared the descriptive and non-numerical
differences and resemblances. In order to get a good
scientific argument we still have to pursue precisely the same
scientific methods of experiment, analysis, comparison, and
differentiation as are recognised to be necessary to establish any
scientific generalisation. These methods are not reducible to a
precise mathematical form for the reasons examined in \Partref{III}.
of this treatise. But that is no reason for ignoring them, or for
pretending that the calculation of a probability, which takes into
%% -----File: 403.png---Folio 392-------
\index{Bernoulli, Jac.!statistical series@{and statistical series}}%
\index{Graunt|inote}%
\index{Statistical frequency, theory of!stability of|(}%
\index{Statistical frequency, theory of!fluctuation of}%
account nothing whatever except the numbers of the instances,
is a rational proceeding. The passage already quoted from
Leibniz (\textit{In exemplis juridicis politicisque plerumque non tamen
\index{Leibniz}%
subtili calculo opus est, quam accurata omnium circumstantiarum
enumeratione}) is as applicable to scientific as to political inquiries.

Generally speaking, therefore, I think that the business of
statistical technique ought to be regarded as strictly limited to
preparing the numerical aspects of our material in an intelligible
form, so as to be ready for the application of the usual inductive
methods. Statistical technique tells us how to `count the cases'
when we are presented with complex material. It must not
proceed also, except in the exceptional case where our evidence
furnishes us from the outset with data of a particular kind, to
turn its results into probabilities; not, at any rate, if we mean
by probability a measure of rational belief.

\Paragraph{2.} There is, however, one type of technical, statistical investigation
not yet discussed, which seems to me to be a valuable
aid to inductive correlation. This method consists in breaking
\index{Inductive correlation}%
up a statistical series, according to appropriate principles, into
a number of sub-series, with a view to analysing and measuring,
not merely the frequency of a given character over the aggregate
series, but the \emph{stability} of this frequency amongst the sub-series;
that is to say, the series as a whole is divided up by some
principle of classification into a set of sub-series, and the \emph{fluctuation}
of the statistical frequency under examination between the
various sub-series is then examined. It is, in fact, a technical
method of increasing the Analogy between the instances, in the
sense given to this process in \Partref{III}\@.

\Paragraph{3.} The method of analysing statistical series, as opposed to
the Laplacian or \emph{mathematical} method, one might designate the
\emph{inductive} method. Independently of the investigations of
Bernoulli or Laplace, practical statisticians began at least as early
\index{Laplace!statistical series@{and statistical series}}%
as the end of the seventeenth century\footnote
  {Graunt in his \textit{Natural and Political Observations upon the Bills of Mortality}
  has been quoted as one of the earliest statisticians to pay attention to these
  considerations.}
to pay attention to the
\emph{stability} of statistical series when analysed in this manner.
Throughout the eighteenth century, students of mortality
statistics, and of the ratio of male to female births (including
Laplace himself), paid attention to the degree of constancy of the
%% -----File: 404.png---Folio 393-------
\index{Bortkiewicz, von, and great numbers!Lexis@{and Lexis}|ifoll}%
\index{Lexis, and asymmetry of statistical frequency!method of|ifoll}%
ratios over different parts of their series of instances as well as
to their average value over the whole series. And in the early
part of the nineteenth century, Quetelet, as we have already
\index{Quetelet!statistical stability@{and statistical stability}}%
noticed, widely popularised the notion of the stability of various
social statistics from year to year. Quetelet, however, sometimes
asserted the existence of stability on insufficient evidence, and
involved himself in theoretical errors through imitating the
methods of Laplace too closely; and it was not until the last
quarter of the nineteenth century that a school of statistical
theory was founded, which gave to this way of approaching the
problem the system and technique which it had hitherto lacked,
and at the same time made explicit the contrast between this
analytical or inductive method and the prevailing mathematical
theory. The sole founder of this school was the German economist,
Wilhelm Lexis, whose theories were expounded in a series
of articles and monographs published between the years 1875
and~1879. For some years Lexis's fundamental ideas did not
attract much notice, and he himself seems to have turned his
attention in other directions. But more recently a considerable
literature has grown up round them in Germany, and their full
purport has been expressed with more clearness than by Lexis
himself---although no one, with the exception of Ladislaus von
Bortkiewicz, has been able to make additions to them of any
great significance.\footnote
  {A list of Lexis's principal writings on these topics will be found in the
  Bibliography. There is little of first-rate importance which is not contained
  either in the volume, \textit{Zur Theorie der Massenerscheinungen in der menschlichen
    Gesellschaft}, or in the \textit{Abhandlungen zur Theorie der Bevölkerungs- und Moral-Statistik}.
  In this latter volume the two important articles on ``Die Theorie der
  Stabilität statistischer Reihen'' and on ``Das Geschlechtsverhältnis der
  Geborenen und die Wahrscheinlichkeitsrechnung,'' originally published in Conrad's
  \textit{Jahrbüche},\DPnote{** TN: Jahrbücher?} are reprinted.}
Lexis devised his theory with an immediate
view to its practical application to the problems of sex ratio and
mortality. The fact that his general theory is so closely intermingled
with these particular applications of it is, probably, a
part explanation of the long interval which elapsed before the
general theoretical importance of his ideas was widely realised.
I cannot help doubting how fully Lexis himself realised it in the
first instance. It would certainly be easy to read his earlier
contributions to the question without appreciating their generalised
significance. After 1879 Lexis added nothing substantial to
his earlier work, and later developments are mainly due to Von
%% -----File: 405.png---Folio 394-------
\index{Kries, von!School of Lexis@{and School of Lexis}}%
Bortkiewicz. Those of the latter's writings, which have an
important bearing on the relation between probability and
statistics, are given in the Bibliography.\footnote
  {The reader may be specially referred to the \textit{Kritische Betrachtungen zur
  theoretischen Statistik} (first instalment---the later instalments being of less interest
to the student of Probability), the \textit{Anwendungen der Wahrscheinlichkeitsrechnung
  auf Statistik}, and \textit{Homogeneität und Stabilität in der Statistik}. Of other German
  and Russian writers it will be sufficient to mention here Tschuprow, who in
\index{Tschuprow!statistical frequency@{and statistical frequency}|inote}%
  ``Die Aufgaben der Theorie der Statistik'' (Schmoller's \textit{Jahrbuch}, 1905) and ``Zur
  Theorie der Stabilität statistischer Reihen'' (\textit{Skandinavisk Aktuarietidskrift}) gives
  by far the best and most lucid general accounts that are available of the doctrines
  of the school, he alone amongst these authors writing in a style from which
  the foreign reader can derive pleasure, and Czuber, who in his \textit{Wahrscheinlichtkeitsrechnung}
\index{Czuber!statistical frequency@{and statistical frequency}}%
  (vol.~ii.\ part iv.\ section~1) supplies a useful mathematical
  commentary.}

On the logic and philosophy of Probability writers of the
school of Lexis are in general agreement with Von Kries; but this
seems to be due rather to the reaction which is common both to
him and to them against the Laplacian tradition, than to any
very intimate theoretical connection between Von Kries's main
contributions to Probability and those of Lexis, though it is true
that both show a tendency to find the ultimate basis of Probability
in physical rather than in logical considerations. I am not
acquainted with much work, which has been appreciably influenced
by Lexis, written in other languages than German (including
with Germans, that is to say, those Russians, Austrians, and Dutch
who usually write in German, and are in habitual connection with
\index{Dormoy}%
the German scientific world). In France Dormoy\footnote
  {\textit{Journal des actuaires français}, 1874, and \textit{Théorie mathématique des assurances
  sur la vie}, 1878; on the question of priority see Lexis, \textit{Abhandlungen}, p.~130.}
published
independently and at about the same time as Lexis some not
dissimilar theories, but subsequent French writers have paid
little attention to the work of either. Such typical French
treatises as that of Bertrand, or, more recently, that of Borel,
contain no reference to them.\footnote
  {Though both these writers touch on closely cognate matters, where Lexis's
  investigations would be highly relevant---Bertrand, \textit{Calcul}, pp.~312--314; Borel,
  \textit{Éléments}, p.~160.}
In Italy there has been some
discussion recently on the work of Von Bortkiewicz. Among
Englishmen Professor Edgeworth has shown a close acquaintance
\index{Edgeworth!German statisticians@{and German statisticians}}%
with the work of the German school,\footnote
  {See especially his ``Methods of Statistics'' in the \textit{Jubilee Volume of the
  Stat.\ Journ.}, 1885, and ``Application of the Calculus of Probabilities to
  Statistics,'' \textit{International Statistical Institute Bulletin}, 1910.}
he providing for nearly forty
years past, on this as on other matters where the realms of
%% -----File: 406.png---Folio 395-------
Statistics and Probability overlap, almost the only connecting
link between English and continental thought.

Nevertheless, an account in English of the main doctrines of
this school is still lacking. It would be outside the plan of the
present treatise to attempt such an account here. But it may
be useful to give a short summary of Lexis's fundamental ideas.
After giving this account I shall find it convenient, in proceeding
to my own incomplete observations on the matter, to approach
it from a rather different standpoint from that of Lexis or of
Von Bortkewicz, though not for that reason the less influenced
or illuminated by their eminent contributions to this problem.

\Paragraph{4.} It will be clearer to begin with some analysis due to Von~Bortkiewicz,\footnote
  {What follows is a free rendering of some passages in his \textit{Kritiscke
  Betrachungen}.}
and then to proceed to the method of Lexis himself,
although the latter came first in point of time.

A group of observations may be made up of a number of subgroups,
to which different frequencies for the character under
investigation are properly applicable. That is to say, a proportion~$\dfrac{z_1}{z}$
of the observations may belong to a group, for which, given
the frequency, the \textit{à~priori} probability of the character under
observation in a particular instance would be~$p_1$, a proportion~$\dfrac{z_2}{z}$
may belong to a second group for which~$p_2$ is the probability, and
so on. In this case, given the frequencies for the \DPchg{sub-groups}{subgroups},
the probability $p$ for the group as a whole would be made up as
follows:
\[
p = \frac{z_1}{z}\, p_1 + \frac{z_2}{z}\, p_2 + \ldots.
\]

We may call $p$ a \emph{general probability}, and~$p_1$, etc., \emph{special probabilities}.
But the special probabilities may in their turn be
general probabilities, so that there may be more than one way
of resolving a general probability into special probabilities.

If $p_{1} = p_{2} = \ldots = p$, then~$p$, for that particular way of resolving
the total group into partial groups, is, in Bortkiewicz's terminology,
\emph{indifferent}. If $p$~is indifferent for all conceivable resolutions
into partial groups,\footnote
  {This is clearly a very loose statement of what Bortkiewicz really means.}
then, borrowing a phrase from Von~Kries,
Bortkiewicz says of it that it has a \emph{definitive interpretation}. In
%% -----File: 407.png---Folio 396-------
dealing with \textit{à~priori} probabilities, we can resolve a total probability
until we reach the special probabilities of each individual
case; and if we find that all these special probabilities are equal,
then, clearly, the general probability satisfies the condition for
definitive interpretation.

So far we have been dealing with \textit{à~priori} probabilities. But
the object of the analysis has been to throw light on the inverse
problem. We want to discover in what conditions we can regard
an observed frequency as being an adequate approximation to a
definitive general probability.

If $p'$ is the empirical value of~$p$ (or, as I should prefer to call it,
the frequency) given by a series of $n$~observations, we may
have
\[
p' = \frac{n_1}{n}\, p_1' + \frac{n_2}{n}\, p_2' + \ldots.
\]
Even if this particular way of resolving the series of observations
is indifferent, the \emph{actually observed} frequencies $p_1', p_2'$,~etc., may
nevertheless be unequal, since they may fluctuate round the
norm~$p'$ through the operation of `chance' influences. If,
however, $n_1, n_2$,~etc., are large, we can apply the usual Bernoullian
formula to discover whether, \emph{if} there was a norm~$p'$, the divergences
of $p_1', p_2'$,~etc., from it are within the limits reasonably attributable
on Bernoullian hypotheses to `chance' influences. We
can, however, only base a sound argument in favour of the
existence of a `definitive' probability~$p'$ by resolving our
aggregate of instances into sub-series in a great variety of ways,
and applying the above calculations each time. Even so, some
measure of doubt must remain, just as in the case of other
inductive arguments.

Bortkiewicz goes on to say that probabilities having definitive
interpretation (\emph{definitive} \textit{Bedeutung}) may be designated elementary
probabilities (\textit{Elementarwahrscheinlichkeiten}). But the
probabilities which usually arise in statistical inquiries are not
of this type, and may be termed \emph{average probabilities} (\textit{Durchschnittswahrscheinlichkeiten}).
That is to say, a series of observed
frequencies (or, as he calls them, empirical probabilities) does not,
as a rule, group itself as it would if the series was in fact subject
to an elementary probability.

\Paragraph{5.} This exposition is based on a philosophy of Probability
different from mine; but the underlying ideas are capable of
%% -----File: 408.png---Folio 397-------
\index{Lexis, and asymmetry of statistical frequency!method of|ifoll}%
translation. Suppose that one is endeavouring to establish an
inductive correlation, \eg\ that the chance of a male birth is~$m$.
\index{Inductive correlation}%
The conclusion, which we are seeking to establish, takes no
account of the place or date of birth or the race of the parents,
and assumes that these influences are irrelevant. Now, if we had
statistics of birth ratios for all parts of the world throughout the
nineteenth century, and added them all up and found that the
average frequency of male births was~$m$, we should not be justified
in arguing from this that the frequency of male births in England
next year is very unlikely to diverge widely from~$m$. For this
would involve the unwarranted assumption, in Bortkiewicz's
terminology, that the empirical probability~$m$ is elementary for
any resolution dependent on time or place, and is not an average
probability compounded out of a series of groups, relating to
different times or places, to each of which a distinct special
probability is applicable. And, in my terminology, it would
assume that variations of time and place were irrelevant to the
correlation, without any attempt having been made to employ
the methods of positive and negative Analogy to establish this.

We must, therefore, break up our statistical material into
groups by date, place, and any other characteristic which our
generalisation proposes to treat as irrelevant. By this means
we shall obtain a number of frequencies $m_1', m_2', m_3', \ldots$ $m_1'',
m_2'', m_3'', \ldots$ etc., which are distributed round the average
frequency~$m$. For simplicity let us consider the series of frequencies
$m_1', m_2', m_3', \ldots$ obtained by breaking up our
material according to the \emph{date} of the birth. If the observed
divergences of these frequencies from their mean are not significant,
we have the beginnings of an inductive argument for
regarding \emph{date} as being in this connection irrelevant.

\Paragraph{6.} At this point Lexis's fundamental contribution to the
problem must be introduced. He concentrated his attention on
the nature of the dispersion of the frequencies $m_1', m_2', m_3'\ldots$
round their mean value~$m$; and he sought to devise a technical
method for measuring the degree of stability displayed by the series of sub-frequencies, which are yielded by the various possible
criteria for resolving the aggregate statistical material into a
number of constituent groups.

For this purpose he classified the various types of dispersion
which could occur. It may be the case that some of the sub-frequencies
%% -----File: 409.png---Folio 398-------
show such wide and discordant variations from the
mean as to suggest that some significant Analogy has been overlooked.
In this event the lack of symmetry, which characterises
the oscillations, may be taken to indicate that some of the subgroups
are subject to a relevant influence, of which we must take
account in our generalisation, to which some of the other subgroups
are not subject.

But amongst the various types of dispersion Lexis found one
class clearly distinguishable from all the others, the peculiarity
of which is that the individual values fluctuate in a `purely
chance' manner about a constant fundamental value. This
type he called typical (\textit{typische}) dispersion. He meant by this
that the dispersion conformed approximately to the distribution
which would be given by some normal law of error.
\index{Law of error!Lexis and}%

The next stage of Lexis's argument\footnote
  {I am here following fairly closely his paper, ``\textit{Über die Theorie der Stabilität
  statisticher Reihen},'' reprinted in his \textit{Abhandlungen zur Theorie der Bevölkerungsund
  Moral-Statistik}, pp.~170--212.}
was to point out that
series of frequencies which are typical in character may have as
their foundation either a constant probability,\footnote
  {This mode of expression, which is not in accurate conformity with my
  philosophy of Probability, is Lexis's, not mine. His meaning is intelligible.}
or one which is
itself subject to chance variations about a mean. The first case
is typified by the example of a series of sets of drawings of balls,
each set being drawn from a similar urn; the second case by the
example of a series of sets of drawings, the urns from which each
set is drawn being not similar, but with constitutions which vary
in a chance manner about a mean.

As his \emph{measure} of dispersion Lexis introduces a formula, which
is evidently in part conventional (as is the case with so many
other statistical formulae, the particular shape of which is often
determined by mathematical convenience rather than by any
more fundamental criterion). He expresses himself as follows.
Where the underlying probability is constant, the probable error
in a particular frequency \textit{à~priori} is $r = \rho\sqrt{\dfrac{2v(1-v)}{g}}$, where
$\rho = .4769$, $v$~is the underlying probability, and $g$~is the number of
instances to which the frequency refers. This follows from the
usual Bernoullian assumptions. Now let $R$ be the corresponding
expression derived \textit{à posteriori} by reference to the actual deviations
of a series of observed frequencies from their mean, so that
%% -----File: 410.png---Folio 399-------
\index{Series of probabilities!organic}%
\index{Tschuprow|inote}%
$R = \rho\sqrt{\dfrac{2[\delta^2]}{n-1}}$, where $[\delta^2]$~is the sum of the squares of the deviations
of the individual frequencies from their mean and $n$~is their
number. Now, if the observed facts are due to merely chance
variations about a constant~$v$, we must have approximately
$R = r$, though, if $g$~is small, comparatively wide deviations between
$R$~and~$r$ will not be significant. If, on the other hand, $v$~itself
is not constant but is subject to chance variations, the case
stands differently. For the fluctuations of the observed frequencies
are now due to two components. The one which would
be present, even if the underlying probability were constant,
Lexis terms the ordinary or unessential component; the other
he terms the physical component. If $p$~is the probable deviation
of the various values of~$v$ from their mean, then, on the same
assumptions and as a deduction from the same theory as before,
$R$~will tend to equal not~$r$ but $\sqrt{r^2 + p^2}$. In this event $R$~cannot
be less than~$r$. If, therefore, $R < r$, one must suppose that the
individual instances of each several series on which each frequency
is based are not independent of one another. Such a series
Lexis terms an organic or dependent (\textit{gebundene}) series, and
explains that it cannot be handled by purely statistical methods.

Since,\Pagelabel{399} therefore, we have three types of series, differing
fundamentally from one another according as $R = r$, $>r$, or~$<r$,
Lexis puts $\dfrac{R}{r} = Q$, and takes $Q$~as his measure of dispersion.\footnote
  {In Tschuprow's notation (\textit{Die Aufgaben der Theorie der Statistik}, p.~45),
  $Q = P/C$, where $P$~(the Physical modulus) $= \sqrt{\dfrac{2\Sum^{k=n}_{k=1} (p_k-p)^2}{n}}$ and $C$~(the Combinatorial
  modulus) $=\sqrt{\dfrac{2p(1-p)}{M}}$, $M$~being the number of instances in each
  set, $n$~the number of sets, $p_k$~the frequency for set~$k$, and $p$~the mean of the
  $n$~frequencies.}
If
$Q = 1$, we have normal dispersion; if $Q > 1$, we have supernormal
dispersion; and if $Q < 1$, we have subnormal dispersion, which is
an indication that the series is `organic.'

If the number of instances on which the frequencies are based
is very great, $r$~becomes negligible in comparison with~$p$ (the
physical component), and, therefore, $R = \sqrt{r^2 + p^2}$ becomes
approximately $R = p$. On the other hand, if $p$~is not very large
and the base number of instances is small, $p$~becomes negligible
%% -----File: 411.png---Folio 400-------
in comparison with~$r$, and we have a delusive appearance of
normal dispersion.\footnote
  {This is part of the explanation of Bortkiewicz's \emph{Law of Small Numbers.}
  See also \Pageref{401}.}
Lexis well illustrates the former point by
the example that the statistics of the ratio of male to female
births for the forty-five registration districts of England over the
years 1859--1871 approximately satisfy the relation $R = r$. But
if we take the figures for all England over those thirteen years,
although the extreme limits of the fluctuation of the ratio about
its mean~$1.042$ are $1.035$ and~$1.047$, nevertheless $R = 2.6$ and $r = 1.6$,
so that $Q = 1.625$; the explanation being that the base number
of instances, namely $730,000$, is so large that $r$~is very small, with
the result that it is swamped by the physical component~$p$. And
he illustrates the latter point by the assertion that, if in $20$~or $30$~series
each of $100$~draws from an urn containing black and white
balls equally, the number of black balls drawn each time were
only to vary between $49$~and~$51$, he would have confidence that
the game was in some way falsified and that the draws were not
independent. That is to say, undue regularity is as fatal to the
assumption of Bernoullian conditions as is undue dispersion.

\Paragraph{7.} In a characteristic passage\footnote
  {``On Methods of Statistics,'' \textit{Jubilee Volume of the Royal Statistical Society},
  p.~211.}
Professor Edgeworth has applied
\index{Edgeworth}%
these theories to the frequency of dactyls in successive extracts
from the \textit{Aeneid}. The mean for the line is~$1.6$, exclusive of the
fifth foot, thus sharply distinguishing the Virgilian line from the
Ovidian, for which the corresponding figure is~$2.2$. But there is
also a marked stability. ``That the Mean of any five lines
should differ from the general Mean by a whole dactyl is proved
to be an exceptional phenomenon, about as rare as an Englishman
measuring $5$~feet, or $6$~feet $3$~inches. An excess of two dactyls
in the Mean of five lines would be as exceptional as an Englishman
measuring $6$~feet $10$~inches.'' But not only so---the stability is
\emph{excessive}, and the fluctuation is less ``than that which is obtained
upon the hypothesis of pure sortition. If we could imagine
dactyls and spondees to be mixed up in the poet's brain in the
proportion of $16$~to~$24$ and shaken out at random, the modulus
in the number of dactyls would be~$1.38$, whereas we have constantly
obtained a smaller number, on an average (the square
root of the average fluctuation)~$1.2$.'' On Lexian principles
these statistical results would support the hypothesis that the
%% -----File: 412.png---Folio 401-------
\index{Bortkiewicz, von, and great numbers!Law of Small Numbers@{and Law of Small Numbers}|ifoll}%
\index{Lexis, and asymmetry of statistical frequency!Edgeworth@{and Edgeworth}}%
\index{Poetry and statistics}%
\index{Small Numbers, Law of|ifoll}%
series under investigation is `organic' and not subject to
Bernoullian conditions, an hypothesis in accordance with our
ideas of poetry. That Edgeworth should have put forward
this example in criticism of Lexis's conclusions, and that Lexis\footnote
  {``Über die Wahrscheinlichkeitsrechnung,'' p.~444 (see \Bibref).}
should have retorted that the explanation was to be found in
Edgeworth's series' not consisting of an adequate number of
separate observations, indicates, if I do not misapprehend them,
that these authorities are at fault in the principles, if not of
Probability, of Poetry.

The dactyls of the Virgilian hexameter are, in fact, a very
good example of what has been termed \textit{connexité}, leading to \DPchg{sub-normal}{subnormal}
dispersion. The quantities of the successive feet are not
independent, and the appearance of a dactyl in one foot \emph{diminishes}
the probability of another dactyl in that line. It is like the case
of drawing black and white balls out of an urn, where the balls
are not replaced. But Lexis is wrong if he supposes that a \emph{supernormal}
dispersion cannot also arise out of \textit{connexité}, or organic
connection between the successive terms. It might have been
the case that the appearance of a dactyl in one foot \emph{increased}
the probability of another dactyl in that line. He should, I
think, have contemplated the result $R > r$ as possibly indicating
a non-typical, organic series, and should not have assumed that,
where $R$~is greater than~$r$, it is of the form $\sqrt{r^{2} + p^{2}}$.\Pagelabel{411}

In short, Lexis has not pushed his analysis far enough, and he
has not fully comprehended the character of the underlying
conditions. But this does not affect the fact that it was he who
made the vital advance of taking as the unit, not the single
observation, but the frequency in given conditions, and of conceiving
the nature of statistical induction as consisting in the
examination, and if possible the measurement, of the stability
of the frequency when the conditions are varied.

\Paragraph{8.}\Pagelabel{401} There is one special piece of work illustrative of the above
methods, due to Von Bortkiewicz, which must not be overlooked,
and which it is convenient to introduce in this place---the so-called
\emph{Law of Small Numbers}.\footnote
  {There are numerous references to this phenomenon in periodical literature;
  but it is sufficient to refer the reader to Von Bortkiewicz's \textit{Das Gesetz der kleinen
  Zahlen}.}

Quetelet, as we have seen in \Chapref{XXVIII}., called attention
\index{Quetelet}%
%% -----File: 413.png---Folio 402-------
\index{Bortkiewicz, von, and great numbers!Quetelet@{and Quetelet}}%
to the remarkable regularity of comparatively \emph{rare} events. Von
Bortkiewicz has enlarged Quetelet's catalogue with modern
instances out of the statistical records of bureaucratic Germany.
The classic instance, perhaps, is the number of Prussian cavalrymen
killed each year by the kick of a horse. The \hyperref[table:1]{table} is worth
giving as a statistical curiosity. (The period is from 1875 to
1894; $G$~stands for the Corps of Guards, and I.--XV.~for the
$15$~Army Corps.)
\begin{sidewaystable}[hp]
\phantomsection\label{table:1}
\footnotesize\renewcommand{\arraystretch}{1.5}%
\begin{tabular}{|r|*{20}{c|}}
\hline
     & 75 & 76 & 77 & 78 & 79 & 80 & 81 & 82 & 83 & 84 & 85 & 86 & 87 & 88 & 89 & 90 & 91&  92 & 93 & 94 \\
\hline
G.   & .. &  2 &  2 &  1 & .. & .. &  1 &  1 & .. &  3 & .. &  2 &  1 & .. & .. &  1 & .. &  1 & .. &  1\rule{0em}{1.5em}\\
I.   & .. & .. & .. &  2 & .. &  3 & .. &  2 & .. & .. & .. &  1 &  1 &  1 & .. &  2 & .. &  3 &  1 & ..\\
II.  & .. & .. & .. &  2 & .. &  2 & .. & .. &  1 & 1  & .. & .. &  2 &  1 &  1 & .. & .. &  2 & .. & ..\\
III. & .. & .. & .. &  1 &  1 &  1 &  2 & .. &  2 & .. & .. & .. &  1 & .. &  1 &  2 &  1 & .. & .. & ..\\
IV.  & .. &  1 & .. &  1 &  1 &  1 &  1 & .. & .. & .. & .. &  1 & .. & .. & .. & .. &  1 &  1 & .. & ..\\
V.   & .. & .. & .. & .. &  2 &  1 & .. & .. &  1 & .. & .. &  1 & .. &  1 &  1 &  1 &  1 &  1 &  1 & ..\\
VI.  & .. & .. &  1 & .. &  2 & .. & .. &  1 &  2 & .. &  1 &  1 &  3 &  1 &  1 &  1 & .. &  3 & .. & ..\\
VII. &  1 & .. &  1 & .. & .. & .. &  1 & .. &  1 &  1 & .. & .. &  2 & .. & .. &  2 &  1 & .. &  2 & ..\\
VIII.&  1 & .. & .. & .. &  1 & .. & .. &  1 & .. & .. & .. & .. &  1 & .. & .. & .. &  1 &  1 & .. &  1\\
IX.  & .. & .. & .. & .. & .. &  2 &  1 &  1 &  1 & .. &  2 &  1 &  1 & .. &  1 &  2 & .. &  1 & .. & ..\\
X.   & .. & .. &  1 &  1 & .. &  1 & .. &  2 & .. &  2 & .. & .. & .. & .. &  2 &  1 &  3 & .. &  1 &  1\\
XI.  & .. & .. & .. & .. &  2 &  4 & .. &  1 &  3 & .. &  1 &  1 &  1 &  1 &  2 &  1 &  3 &  1 &  3 &  1\\
%[** TN: [sic] No XII. and XIII.]
XIV. &  1 &  1 &  2 &  1 &  1 &  3 & .. &  4 & .. &  1 & .. &  3 &  2 &  1 & .. &  2 &  1 &  1 & .. & ..\\
XV.  & .. &  1 & .. & .. & .. & .. & .. &  1 & .. &  1 &  1 & .. & .. & .. &  2 &  2 & .. & .. & .. & ..\\
\hline
\end{tabular}
\end{sidewaystable}

The agreement of this table with the theoretical results of a
random distribution of the total number of casualties is remarkably
close:\footnote
  {Bortkiewicz, \textit{op.\ cit}.\ p.~24.}
\begin{center}
\begin{tabular}{|*{3}{c|}}
\hline
\settowidth{\TmpLen}{Casualties in a}%
\parbox[c]{\TmpLen}{\centering Casualties in a\\ Year.} &
\multicolumn{2}{c|}{%
  \settowidth{\TmpLen}{Number of Occasions on which the Annual}%
  \parbox[c]{\TmpLen}{\medskip\centering%
    Number of Occasions on which the Annual \\
    Casualties in a Corps reach the Figure \\
    in Column~1.\medskip}} \\
\hline
\rule{0pt}{12pt} & Actual. & Theoretical. \\
0          &    144  &     143.1    \\
1          &   \Z91  &    \Z92.1    \\
2          &   \Z32  &    \Z33.3    \\
3          &   \Z11  &   \Z\Z8.9    \\
4          &   \Z\Z2 &   \Z\Z2.0    \\
5 and more &     ..  &   \Z\Z0.6    \\
\hline
\end{tabular}
\end{center}

Other instances are furnished by the numbers of child suicides
in Prussia, and the like.

It is Von Bortkiewicz's thesis that these observed regularities
%% -----File: 414.png---Folio 403-------
have a good theoretical explanation behind them, which he
dignifies with the name of the \emph{Law of Small Numbers}.

The reader will recall that, according to the theory of Lexis,
his measure of stability~$Q$ is, in the more general case, made up
of two components $r$~and~$p$, combined in the expression $\sqrt{r^{2} + p^{2}}$,
of which one is due to fluctuations from the average of the conditions
governing all the members of a series, which furnishes us
with one of our observed frequencies, and of which the other is
due to fluctuations in the individual members of the series about
the true norm of the series. Bortkiewicz carries the same
analysis a little further, and shows that Lexis's~$Q$ is of the form
$\sqrt{1 + (n - 1)c^{2}}$, where $n$~is the number of times that the event
occurs in each series.\footnote
  {I refer the reader to the original, \textit{op.\ cit.}\ pp.~29--31, for the interpretation
  of~$c$ (which is a function of the mean square errors arising in the course of the
  investigation) and for the mathematical argument by which the above result
  is justified.}
That is to say, $Q$~increases with~$n$, and,
when $n$~is small, $Q$~is likely to exceed unity to a less extent than
when $n$~is large. To postulate that $n$~is small, is, when we are
dealing with observations drawn from a wide field, the same
thing as to say that the event we are looking for is a comparatively
rare one. This, in brief, is the mathematical basis of the Law
of Small Numbers.

In his latest published work on these topics,\footnote
  {``Homogeneität und Stabilität in der Statistik,'' published in the \textit{Skandinavisk
  Aktuarielidskrift}, 1918. Those readers, who look up my references,
  will, I think, agree with me that Von Bortkiewicz does not get any less
  obscure as he goes on. The mathematical argument is right enough, and
  often brilliant. But what it is all really about, what it all really amounts to,
  and what the premisses are, it becomes increasingly perplexing to decide.}
Von Bortkiewicz
builds his mathematical structure considerably higher, without,
however, any further underpinning of the logical foundations
of it. He has there worked out further statistical constants,
arising out of the conceptions on which Lexis's~$Q$ is based (the
precise bearing of which is not made any clearer by his calling
them \emph{coefficients of syndromy}), which are explicitly dependent
on the value of $n$; and he elaborately compares the theoretical
value of the coefficients with the observed value in certain actual
statistical material. He concludes with the thesis, that Homogeneity
and Stability (defined as he defines them) are opposed
conceptions, and that it is not correct to premise, that the larger
statistical mass is as a rule more stable than the smaller, unless
%% -----File: 415.png---Folio 404-------
we also assume that the larger mass is less homogeneous. At this
point, it would have helped, if Von Bortkiewicz, excluding from
his vocabulary homogeneity, paradromy,~$\gamma_M'$, and the like, had
stopped to tell in plain language where his mathematics had led
him, and also whence they had started. But like many other
students of Probability he is eccentric, preferring algebra to earth.

\Paragraph{9.} Where, then, though an admirer, do I criticise all this? I
think that the argument has proceeded so far from the premisses,
that it has lost sight of them. If the limitations prescribed by
the premisses are kept in mind, I do not contest the mathematical
accuracy of the results. But many technical terms have been
introduced, the precise signification and true limitations of which
will be misunderstood if the conclusion of the argument is allowed
to detach itself from the premisses and to stand by itself. I will
illustrate what I mean by two examples from the work of Von
Bortkiewicz described above.

Von Bortkiewicz enunciates the seeming paradox that the
larger statistical mass is only, as a rule, more stable if it is less
homogeneous. But an illustration which he himself gives shows
how misleading his aphorism is. The opposition between
stability and homogeneity is borne out, he says, by the judgment
of practical men. For actuaries have always maintained that
their results average out better, if their cases are drawn from a
wide field subject to \emph{variable} conditions of risk, whilst they are
chary of accepting too much insurance drawn from a single
\index{Insurance}%
homogeneous area which means a concentration of risk. But
this is really an instance of Von Bortkiewicz's own distinction
between a general probability~$p$ and special probabilities $p_{1}$~etc.,
where
\[
p = \frac{z_1}{z}\, p_1 + \frac{z_2}{z}\, p_2 + \ldots\DPtypo{}{.}
\]
If we are basing our calculations on~$p$ and do not know $p_1, p_2$,
etc., then these calculations are more likely to be borne out by
the result if the instances are selected by a method which spreads
them over all the groups $1, 2$, etc., than if they are selected by a
method which concentrates them on group~$1$. In other words,
the actuary does not like an undue proportion of his cases to be
drawn from a group which may be subject to a common relevant
influence \emph{for which he has not allowed}. If the \textit{à~priori} calculations
are based on the average over a field which is not homogeneous
%% -----File: 416.png---Folio 405-------
in all its parts, greater stability of result will be obtained if the
instances are drawn from all parts of the non-homogeneous
total field, than if they are drawn now from one homogeneous
\DPchg{sub-field}{subfield} and now from another. This is not at all paradoxical.
Yet I believe, though with hesitation, that this is all that Von
Bortkiewicz's elaborately supported mathematical conclusion
really amounts to.

My second example is that of the Law of Small Numbers.
Here also we are presented with an apparent paradox in the
statement that the regularity of occurrence of rare events is more
stable than that of commoner events. Here, I suspect, the
paradoxical result is really latent in the particular measure of
stability which has been selected. If we look back at the figures,
which I have quoted above, of Prussian cavalrymen killed by
the kick of a horse, it is evident that a measure of stability could
be chosen according to which exceptional instability would be
displayed by this particular material; for the frequency varies
from $0$~to~$4$ round a mean somewhat less than unity, which is a
very great \emph{percentage} fluctuation. In fact, the particular measure
of stability which Von Bortkiewicz has adopted from Lexis has
about it, however useful and convenient it may be, especially for
mathematical manipulation, a great deal that is arbitrary and
conventional. It is only one out of a great many possible
formulae which might be employed for the numerical measurement
of the conception of stability, which, quantitatively at
least, is not a perfectly precise one. The so-called Law of Small
Numbers is, therefore, little more than a demonstration that,
where rare events are concerned, the Lexian measure of stability
does not lead to satisfactory results. Like some other formulae
which involve a use of Bernoullian methods in an approximative
form, it does not lead to reliable results in all circumstances,
I should add that there is one other element which may contribute
to the total psychological reaction of the reader's mind to the
Law of Small Numbers, namely, the surprising and \emph{piquant}
examples which are cited in support of it. It is startling and
even amusing to be told that horses kick cavalrymen with the
same sort of regularity as characterises the rainfall. But our
surprise at this particular example's fulfilling the Law of Great
Numbers has little or nothing to do with the exceptional stability
about which the Law of Small Numbers purports to concern itself.
%% -----File: 417.png---Folio 406-------
\index{Statistical inference!induction|ifoll}%
\index{Universal Induction and statistical!methods|(}%


\Chapter{XXXIII}{Outline of a Constructive Theory}

\Paragraph{1.} \First{There} is a great difference between the proposition. ``It is
probable that \emph{every} instance of this generalisation is true'' and
the proposition ``It is probable of \emph{any} instance of this generalisation
taken at random that it is true.'' The latter proposition
may remain valid, even if it is certain that some instances of the
generalisation are false. It is more likely than not, for example,
that any number will be divisible either by two or by three, but
it is not more likely than not that all numbers are divisible either
by two or by three.

The first type of proposition has been discussed in \Partref{III}.~under
 the name of \emph{Universal Induction}. The latter belongs to
\index{Induction!universal}%
\index{Induction!statistical|ifoll}%
\emph{Inductive Correlation} or \emph{Statistical Induction}, an attempt at the
\index{Correlation!Inductive}%
\index{Inductive correlation}%
logical analysis of which must be my final task.

\Paragraph{2.} What advocates of the Frequency Theory of Probability
wrongly believe to be characteristic of \emph{all} probabilities, namely,
that they are essentially concerned not with single instances but
with series of instances, is, I think, a true characteristic of
statistical induction. A statistical induction either asserts the
probability of an instance \emph{selected at random} from a series of
propositions, or else it assigns the probability of the assertion,
that the truth frequency of a series of propositions (\ie\ the
\index{Truth frequency}%
proportion of true propositions in the series) is in the neighbourhood
of a given value. In either case it is asserting a characteristic
of a \emph{series} of propositions, rather than of a particular
proposition.

Whilst, therefore, our unit in the case of Universal Induction
is a single instance which satisfies both the condition and the
conclusion of our generalisation, our unit in the case of Statistical
%% -----File: 418.png---Folio 407-------
\index{Analogy, principle of!statistics@{and statistics}}%
Induction is not a single instance, but a set or series of instances,
all of which satisfy the condition of our generalisation but
which satisfy the conclusion only in a certain proportion of cases.
And whilst in Universal Induction we build up our argument by
examining the known positive and negative Analogy shown in a
series of single instances, the corresponding task in Statistical
Induction consists in examining the Analogy shown in a \emph{series of
series} of instances.

\Paragraph{3.} We are presented, in problems of Statistical Induction, with
a set of instances all of which satisfy the conditions of our generalisation,
and a proportion~$f$ of which satisfy its conclusion; and
we seek to generalise as to the probable proportion in which
further instances will satisfy the conclusion.

Now it is useless merely to pay attention to the proportion (or
frequency) $f$ discovered in the aggregate of the instances. For
any collection whatever, comprising a definite number of objects,
must, if the objects be classified with reference to the presence
or absence of any specified characteristic whatever, show some
definite proportion or statistical frequency of occurrence; so that
a mere knowledge of what this frequency is can have no appreciable
bearing on what the corresponding frequency will be for
some other collection of objects, or on the probability of finding
the characteristic in an object which does not belong to the
original collection. We should be arguing in the same sort of
way as if we were to base a universal induction as to the
concurrence of two characteristics on a single observation of this
concurrence, and without any analysis of the accompanying
circumstances.

Let the reader be clear about this. To argue from the \emph{mere}
fact that a given event has occurred invariably in a thousand
instances under observation, without any analysis of the circumstances
accompanying the individual instances, that it is likely
to occur invariably in future instances, is a feeble inductive
argument, because it takes no account of the Analogy. Nevertheless
an argument of this kind is not entirely worthless, as we have
seen in \Partref{III}\@. But to argue, without analysis of the instances,
from the mere fact that a given event has a frequency of $10$~per
cent in the thousand instances under observation, or even in a
million instances, that its probability is~$1/10$ for the next instance,
or that it is likely to have a frequency near to~$1/10$ in a further
%% -----File: 419.png---Folio 408-------
set of observations, is a far feebler argument; indeed it is hardly
an argument at all. Yet a good deal of statistical argument is not
free from this reproach;---though persons of common sense often
conclude better than they argue, that is to say, they select for
credence, from amongst arguments similar in form, those in
favour of which there is in fact other evidence tacitly known to
them though not explicit in the premisses as stated.

\Paragraph{4.} The analysis of statistical induction is not fundamentally
different from that of universal induction already attempted in
\Partref{III}\@. But it is much more intricate; and I have experienced
exceptional difficulty, as the reader may discover for himself in
the following pages, both in clearing up my own mind about it
and in expounding my conclusions precisely and intelligibly. I
propose to begin with a few examples of what commonly impresses
us as good arguments in this field, and also of the attendant
circumstances which, if they were known to exist, might be held
to justify such a mode of reasoning; and, having thus attempted
to bring before the reader's mind the character of the subject-matter,
to proceed to an abstract analysis.

\textit{Example One}.---Let us investigate the generalisation that the
proportion of male to female births is~$m$. The fact that the
aggregate statistics for England during the nineteenth century
yield the proportion~$m$ would go no way at all towards justifying
the statement that the proportion of male births in Cambridge
next year is likely to approximate to~$m$. Our argument would
be no better if our statistics, instead of relating to England during
the nineteenth century, covered all the descendants of Adam.
But if we were able to break up our aggregate series of instances
into a series of sub-series, classified according to a great variety
of principles, as for example by date, by season, by locality, by
the class of the parents, by the sex of previous children, and so
forth, and if the proportion of male births throughout these sub-series
showed a significant stability in the neighbourhood of $m$,
then indeed we have an argument worth something. Otherwise
we must either abandon our generalisation, amplify its conditions,
or modify its conclusion.

\textit{Example Two}.---Let us take a series of objects~$s$ all alike in
some specified respect, this resemblance constituting membership
of the class~$F$; let us determine of how many members of the
series a certain property~$\phi$ is true, the frequency of which is to be
%% -----File: 420.png---Folio 409-------
the subject of our generalisation; and if a proportion~$f$ of the
series~$s$ have the property~$\phi$ we may say that the series~$s$ has a
frequency~$f$ for the property~$\phi$.

Now if the whole field~$F$ has a finite number of constituents,
it must have some determinate frequency~$p$, and if, therefore,
we increase the comprehensiveness of $s$ until eventually it
includes the whole field, $f$~must come in the end to be equal
to~$p$. This is obvious and without interest and not what we
mean by the law of great numbers and the stability of statistical
frequency.

Let us now divide up the field~$F$, according to some determinate
principle of division~$D$, into subfields $F_1, F_2$,~etc.; and
let the series~$s_1$ be taken from~$F_1$, $s_2$~from~$F_2$, and so on. Where
$F_1, F_2$,~etc., have a finite number of constituents, $s_1, s_2$~etc., may
possibly coincide with them; if $s_1, s_2$~etc., do not coincide with
$F_1, F_2$,~etc., but are chosen from them, let us suppose that they are
chosen according to some principle of random or unbiassed
selection---$s_1$, that is to say, will be a random sample from~$F_1$.
Now it may happen that the frequencies $f_1, f_2$,~etc., of the series
$s_1, s_2$,~etc., thus selected cluster round some mean frequency~$f$. If
the frequencies show this characteristic (the measurement and precise
determination of which I am not now considering), then the
series of series $s_1, s_2$,~etc., has a stable frequency for the classification~$D$.
`Great numbers' only come in because it is difficult to
ascertain the existence of stable frequency unless the series $s_1, s_2$,~etc.,
are themselves numerous and unless each of these comprises
numerous individual instances.

Let us then apply a different principle of division~$D'$, leading
to series $s_1', s_2'$,~etc., and to frequencies $f_1', f_2'$,~etc.; and then again
a third principle of division~$D''$ leading to frequencies $f_1'', f_2''$,~etc.;
and so on, to the full extent that our knowledge of the differences
between the individual instances permits us. If the frequencies
$f_1, f_2$,~etc., $f_1', f_2'$,~etc., $f_1'', f_2''$,~etc., and so on are all stable about~$f$,
we have an inductive ground of some weight for asserting a
statistical generalisation.

Let the field~$F$, for example, comprise all Englishmen in their
sixtieth year, and let the property~$\phi$, about the frequency of
which we are generalising, be their death in that year of their age.
Now the field~$F$ can be divided into subfields $F_1, F_2$,~etc., on innumerable
different principles. $F_1$~might represent Englishmen
%% -----File: 421.png---Folio 410-------
in their sixtieth year in 1901, $F_2$~in 1902, and so on; or we might
classify them according to the districts in which they live; or
according to the amount of income tax they pay; or according as
they are in workhouses, in hospitals, in asylums, in prisons, or at
large. Let us take the second of these classifications and let the
subfields $F_1, F_2$,~etc., be constituted by the districts in which they
live. If we take large random selections $s_1, s_2$,~etc., from $F_1, F_2$,~etc.,
respectively, and find that the frequencies, $f_1, f_2$,~etc., fluctuate
closely round a mean value~$f$, this can be expressed by the
statement that there is a stable frequency~$f$ for death in the
sixtieth year in different English districts. We might also find
a similar stability for all the other classifications. On the other
hand, for the third and fourth classifications we might find no
stability at all, and for the first a greater or less degree of stability
than for the second. In the latter case the form of our statistical
generalisation must be modified or the argument in its favour
weakened.

\textit{Example Three}.---Let us return to the example given in \Chapref{XXVII}.
of the dog which is fed sometimes by scraps at table
and so judges it reasonable to be there. From one year to another,
let us assume, the dog gets scraps on a proportion of days more
or less stable. What sorts of explanation might there be of
this? First, it might be the case that he was fed on the movable
feasts of the Church; there would be the same number of these
in each year, but it would not be easy for any one who had not
the clue to discover any regularity in the occasions of their
individual occurrence. Second, it might be the case that he
was given scraps whenever he looked thin, and that the scraps
were withheld whenever he looked fat, so that if he was given
scraps on one day, this diminished the likelihood of his getting
scraps on the next day, whilst if they were withheld this would
increase the likelihood; the dog's constitution remaining constant,
the number of days for scraps would tend to fluctuate from
year to year about a stable value. Third, it might be the case
that the company at table varied greatly from day to day, and
that some days people were there of the kind who give dogs
scraps and other days not; if the set of people from whom
the company was drawn remained more or less the same from
year to year, and it was a matter of chance (in the objective sense
defined in §\;8 of \Chapref{XXIV}. above) which of them were
%% -----File: 422.png---Folio 411-------
there from day to day, the proportion of days for scraps might
again show some degree of stability from year to year. Lastly,
a combination between the first and third type of circumstance
gives rise to a variant deserving separate mention. It might be
the case that the dog was only given scraps by his master, that
his master generally went away for Saturday and Sunday, and
was at home the rest of the week unless something happened
to the contrary, and that ``chance'' causes would sometimes
intervene to keep him at home for the week-end and away in
the week; in this case the frequency of days for scraps would
probably fluctuate in the neighbourhood of five-sevenths. In
circumstances of this third type, however, the degree of stability
would probably be less than in circumstances of the first two
types; and in order to get a really stable frequency it might
be necessary to take a longer period than a year as the basis
for each series of observations, or even to take the average for
a number of dogs placed in like circumstances instead of one
dog only.

It has been assumed so far that we have an opportunity of
observing what happens on \emph{every} day of the year. If this is
not the case and we have knowledge only of a random sample
from the days of each year, then the stability, though it will be
less in degree, may be nevertheless observable, and will increase
as the number of days included in each sample is increased.
This applies equally to each of the three types.

\Paragraph{5.} What is the correct logical analysis of this sort of reasoning?
If an inductive generalisation is a true one, the conclusion which
it asserts about the instance under inquiry is, so far as it goes,
definite and final, and cannot be modified by the acquisition of
more detailed knowledge about the particular instance. But a
statistical induction, when applied to a particular instance, is
not like this; for the acquisition of further knowledge might
render the statistical induction, though not in itself less probable
than before, \emph{inapplicable} to that particular instance.

This is due to the fact that a statistical induction is not really
about the particular instance at all, but has its subject, about
which it generalises, a \emph{series}; and it is only applicable to the
particular instance, in so far as the instance is relative to our
knowledge, a \emph{random member} of the series. If the acquisition of
new knowledge affords us additional relevant information about
%% -----File: 423.png---Folio 412-------
\index{Randomness}%
\index{Variables in Probability|inote}%
the particular instance, so that it ceases to be a random member
of the series, then the statistical induction ceases to be applicable;
but the statistical induction does not for that reason become
any less probable than it was---it is simply no longer indicated
by our data as being the statistical generalisation appropriate
to the instance under inquiry. The point is illustrated by the
familiar example that the probability of an unknown individual
posting a letter unaddressed can be based on the statistics of
the Post Office, but \emph{my} expectation that \emph{I} shall act thus, cannot
be so determined.

Thus a statistical generalisation is always of the form: `The
probability, that an instance taken at random from the series~$S$
will have the characteristic~$\phi$, is~$p$;' or, more precisely, if $a$~is
a random member of~$S(x)$, the probability of~$\phi (a)$ is~$p$.

It will be convenient to recapitulate from \Chapref{XXIV}. §\;11
the definition of `an instance taken at random': Let $\phi (x)$
stand for `$x$~has the characteristic~$\phi$,' and $S(x)$~for `$x$~is a member
of the class~$S$'; then, on evidence~$h$, $a$~is a random member
of the class~$S$ for characteristic~$\phi$, if `$x$~is~$a$' is irrelevant to
$\phi(x) / S(x)· h$,\footnote
  {The use of variables in probability, as has been pointed out on \Pageref{58}, is
  very dangerous. It might therefore be better to enunciate the above: $a$~is a
  random member of~$S$ for characteristic~$\phi$, if $\phi(a)/S(a)· h = \phi(b)/S(b)· h$ where
$S(b)· h$ contains no information about~$b$, except that $b$~is a member of~$S$\@.}
\ie~if we have no information about $a$ relevant
to~$\phi(a)$ except~$S(a)$.

Or alternatively we might express our definition as follows:
Consider a particular instance~$a$, where the object of our inquiry
is the probability of $\phi (a)$ relative to evidence~$h$. Let us discard
that part of our knowledge~$h(a)$ which is irrelevant to~$\phi (a)$,
leaving us with relevant knowledge~$h'(a)$. Let the class of
instances $a_1, a_2$,~etc., which satisfy~$h'(x)$ be designated by~$S$\@. Then,
relative to evidence~$h$, $a$~is a random member of the class or
series~$S$ for the characteristic~$\phi$.

Let us denote the proposition `$x$~is, on evidence~$h$, a random
member of~$S$ for characteristic~$\phi$' by $R(x, S, \phi, h)$; then our
statistical generalisation is of the form $\phi(x)/R(x, S, \phi, h)· h = p$.

If $R (a, S, \phi, h)$ holds, then, on evidence~$h$, $S$~is the appropriate
statistical series to which to refer $a$ for the purposes of the characteristic~$\phi$.

It is not always the case that the evidence indicates any
series at all as `appropriate' in the above sense. In particular,
%% -----File: 424.png---Folio 413-------
if evidence~$h$ indicates $S$~as the appropriate series, and evidence~$h'$
indicates~$S'$ as the appropriate series, then relative to evidence~$hh'$
(assuming these to be not incompatible), it may be the case
that no determinate series is indicated as appropriate. In this
case the method of statistical induction fails us as a means of
determining the probability under inquiry.

\Paragraph{6.} We can now remove our attention from the individual
instance~$a$ to the properties of the series~$S$\@. What sort of evidence
is capable of justifying the conclusion that $p$~is the probability
that a random member of the series~$S$ will have the characteristic~$\phi$?

In the simplest case, $S$~is a finite series of which we know the
truth frequency for the characteristic~$\phi$, namely~$f$.\footnote
  {\Ie\ if $f$~is the proportion of the members of the series for which $\phi(x)$~is true.}
Then by a
straightforward application of the Principle of Indifference we
have $p = f$, so that
$\phi(x)/R(x, S, \phi, h)· h = f$.

In another important type~$S$ is a series, with an indefinite
number of members which, however, group themselves in such
a way that for every member of which $\phi(x)$~is true, there corresponds
a determinate number of members of which $\phi(x)$~is
false. The series, that is to say, contains an indefinite number
of atoms, but each atom is made up of a set of molecules of
which $\phi(x)$~is true and false respectively in fixed and determinate
proportions. If this determinate proportion is known to be~$f$, we
have, as before, $p = f$. The typical instance of this type is afforded
by games of chance. Every possible state of affairs which might
lead to a divergence in one direction is balanced by another
probability leading in the opposite direction; and these alternative
possibilities are of a kind to which the Principle of Indifference
is applicable. Thus for every poise of the dice box which leads
to the fall of the six-face, there is a corresponding poise which
leads to the fall of each of the other faces; so that if $S$ is the
series of possible poises, we may equate~$p$ to~$\frac{1}{6}$ where $\phi$~is the fall
of the six-face. It is not necessary, in order to obtain this
result, to assert that $S$~is a finite series with an actual determinate
frequency~$f$ for the fall of each face.

So far no inductive element enters in. But in general we do
not know the constitution of~$S$ for certain, and can only infer it
inductively from its resemblance to other series of which we know
the constitution. This presents a normal inductive problem---the
%% -----File: 425.png---Folio 414-------
determination by an analysis of the positive and negative
analogies as to whether the respects in which $S$~differs or may
differ from the other series is or is not relevant in the particular
context~$\phi$; and it involves the same sort of considerations as
those discussed in \Partref{III}\@.

There is, however, a further difficulty to be introduced before
we have reached the typical statistical problem. In the case
now to be considered our actual data do not consist of positive
knowledge of the constitutions either of $S$~itself or of other series
more or less resembling~$S$, but only of the frequency of the
characteristic in actually observed sets of \emph{selections}, great or
small, either from $S$~itself or from other series more or less
resembling~$S$\@.

Thus in the most general case our inquiry falls into two parts.
We are given the observed frequency in statistical sets \emph{selected}
from $S_1, S_2$,~etc., respectively. The first part of our inquiry is
the problem of arguing from these observed frequencies to the
probable constitutions of $S_1, S_2$,~etc., \ie\ of determining the values
of $\phi(x)/R(x, S_1, \phi, h)· h$, etc.; we may call this part the statistical
problem. The second part of our inquiry is the problem of
arguing from the probable constitutions of $S_1, S_2$,~etc., to the
probable constitution of~$S$, where $S, S_1, S_2$ resemble one another
more or less, and we have to determine whether the differences
are or are not relevant to our inquiry; we may call this part the
inductive problem.

Now if the observed statistical sets are made up of random
instances of $S_1, S_2$,~etc., we can argue in certain conditions from
the observed frequencies to the probable constitutions of the
series, out of which the random selections have been made, by
an inverse application of Bernoulli's Theorem on the lines explained
in \Chapref{XXXI}\@. Moreover, if the series $S_1, S_2$,~etc.,
are finite series and the observed selections cover a great part
of their members, we can reach an at least approximate conclusion
without raising all the theoretical difficulties or satisfying
all the conditions of \Chapref{XXXI}\@. The commonly received
opinions as to the bearing of the observed frequencies in a
random sample on the constitution of the universe out of which
the sample is drawn, though generally stated too precisely and
without sufficient insistence on the assumptions they involve,
our actual evidence not warranting in general more than an
%% -----File: 426.png---Folio 415-------
\index{Analogy, principle of!negative}%
\index{Analogy, principle of!positive}%
\index{Analogy, principle of!statistics@{and statistics}|ifoll}%
\index{Lexis, and asymmetry of statistical frequency!statistical stability@{and statistical stability}}%
approximate result, are not, I think, fundamentally erroneous.
The most usual error in modern method consists in treating too
lightly what I have termed above the \emph{inductive} problem, \ie\ the
problem of passing from the series $S_1, S_2$,~etc., of which we
have observed samples, to the series~$S$ of which we have not
observed samples.

Let us, then, assume that we have ascertained $p_1, p_2$,~etc., with
more or less exactness, by examining either all the instances of
the series $S_1, S_2$,~etc., or random selections from them, \ie\ $\phi(x)/R
(x, S_1, \phi, h)· h = p_1$, etc. This can be expressed for short by saying
that the series $S_1, S_2$,~etc., are subject to probable-frequencies
$p_1, p_2$,~etc., for the characteristic~$\phi$. Our problem is to infer from
this the probable-frequency~$p$ of the unexamined series~$S$\@. The
class characteristics of the series $S_1, S_2$,~etc., will be partly the same
and partly different. Using the terminology of \Partref{III}. we
may term the class characteristics which are common to all of
them the Positive Analogy, and the class characteristics which
are not common to all of them the Negative Analogy.

Now, if the observed or inferred probable-frequencies of
the series $S_1, S_2$, are to form the basis of a statistical induction,
they must show a \emph{stable} value; that is to say, either we must
have $p_1 = p_2 =$~etc., or at least $p_1, p_2$,~etc., must be stably grouped
about their mean value. Our next task, therefore, must be
to discover whether the probable-frequencies $p_1, p_2$,~etc., display
a significant stability. It is the great merit of Lexis that he was
the first to investigate the problem of stability and to attempt its
measurement. For, until a \textit{primâ facie} case has been established
for the existence of a stable probable-frequency, we have but
a flimsy basis for any statistical induction at all; indeed we are
limited to the class of case where the instance under inquiry is
a member of identically the \emph{same} series as that from which our
samples were drawn, \ie\ where $S = S_1$, which in social and scientific
inquiries is seldom the case.

What is the meaning of the assertion that $p_1, p_2$,~etc., are
\emph{stably} grouped about their mean value? The answer is not
simple and not perfectly precise. We could propound various
formulae for the measurement of stability and dispersion, respectively,
and the problem of translating the conception of stability,
which is not quantitatively precise, into a numerical formula
involves an arbitrary or approximative element. For practical
\index{Statistical frequency, theory of!stability of|)}%
%% -----File: 427.png---Folio 416-------
purposes, however, I doubt if it is possible to improve on Lexis's
measure of stability~$Q$, the mathematical definition of which
has been given above on \Pageref{399}. Lexis describes the stability
as subnormal, normal, or supernormal according as $Q$~is less than,
equal to, or greater than~$1$. This is too precise, and it is better
perhaps to say that the stability about the mean is normal if
the dispersion is such as would not be improbable \textit{à~priori}, if
we had assumed that the members of $S_1, S_2$,~etc., were obtained
by random selection out of a single universe~$U$, that it is subnormal
if the dispersion is less than one would have expected on
the same hypothesis, and that it is supernormal if the dispersion
is greater than one would have expected.

Let us suppose that we find that on this definition $p_1, p_2$,~etc.,
are stable about~$p$, and let us postpone consideration of the cases
of subnormal or supernormal dispersion. This is equivalent to
saying that the frequencies of $S_1, S_2$,~etc., are within limits which
we should expect \textit{à~priori}, if we had knowledge relative to which
their members were chosen at random from a universe~$U$ of which
the frequency was~$p$ for the characteristic under inquiry. We
next seek to extend this result to the unexamined series~$S$ and to
justify anticipations about it on the basis of the members of~$S$
also being chosen at random from the universe~$U$. This leads us
to the strictly inductive part of our inquiry.

The class characteristics of the several series $S_1, S_2$,~etc., will be
partly the same and partly different, those that are the same
constituting the positive analogy and those that are different
constituting the negative analogy, as stated above. The series~$S$
will share part of the positive analogy. The argument for
assimilating the properties of~$S$, in relation to the characteristic
under inquiry, to the properties of $S_1, S_2$,~etc., in relation to this
characteristic depends on the differences between $S, S_1, S_2$,~etc.,
being \emph{irrelevant} in this particular connection. The method of
strengthening this argument seems to me to be the same as the
general inductive method discussed in \Partref{III}. and to present
the same, but not greater, difficulties.

In general this inductive part of our inquiry will be best
advanced by classifying the aggregate series of instances with
which we are presented in such a way as to analyse most clearly
the significant positive and negative analogies, to group them,
that is to say, into sub-series $S_1, S_2$,~etc., which show the most
%% -----File: 428.png---Folio 417-------
marked and definite class characteristics. Our knowledge of the
differences between the particular observed instances which
constitute our original data will suggest to us one or more
principles of classification, such that the members of each sub-series
all have in common some set of positive or negative characteristics,
not all of which are shared in common by all the
members of any of the other sub-series. That is to say, we
classify our whole set of instances into a series of series $S_1, S_2$,~etc.,
which have frequencies $f_1, f_2$,~etc., for the characteristic under
inquiry; and then again we classify them by another principle or
criterion of classification into a second series of series $S_1', S_2'$,~etc.,
with frequencies $f_1', f_2'$,~etc.; and so on, so far as our knowledge of
the possible relevant differences between the instances extends;
the whole result being then summed up in a statement of the
positive and negative analogies of the series of series. If we then
find that all the frequencies $f_1, f_2$,~etc., $f_1', f_2'$~etc., are stable about
a value~$p$, and if, on the basis of the above positive and negative
analogies, we have a normal inductive argument for assimilating
the unexamined series~$S$ to the examined series $S_1, S_2$,~etc., $S_1', S_2'$,~etc.,
in respect of the characteristic under inquiry, in this case we
have, not conclusive grounds, but grounds of some weight for
asserting the probability~$p$, that an instance taken at random
from~$S$ will have the characteristic in question.

Let me recapitulate the two essential stages of the argument.
We first find that the observed frequencies in a set of
series are such as would have been not improbable \textit{à~priori} if,
relative to our knowledge, these series had all been made up of
random members of the same universe~$U$; and we next argue
that the positive and negative analogies of this set of series
furnish an inductive argument of some weight for supposing that
a further unexamined series~$S$ resembles the former series in
having a frequency for the characteristic under inquiry such as
would have been not improbable \textit{à~priori} if, relative to our knowledge,
$S$~was also made up of random members of the hypothetical
universe~$U$.

\Paragraph{7.} It is very perplexing to decide how far an argument of
this character involves any new and theoretically distinct
difficulties or assumptions, beyond those already admitted
as inherent in Universal Induction. I believe that the foregoing
\index{Induction!universal}%
analysis is along the right lines and that it carries the
\index{Universal Induction and statistical!methods|)}%
%% -----File: 429.png---Folio 418-------
\index{Chance, objective}%
inquiry a good deal further than it has been carried hitherto.
But it is not conclusive, and I must leave to others its more
exact elucidation.

There is, however, a little more to be said about the half-felt
reasons which, in my judgment, recommend to common sense
some at least of the scientific (or semi-scientific) arguments
which run along the above lines. In expressing these reasons I
shall be content to use language which is not always as precise as
it ought to be.

I gave in \Chapref{XXIV}. §§\;7--9 an interpretation of what is
meant by an `objectively chance' occurrence, in the sense in
which the results of a game, such as roulette, may be said to be
governed by `objective chance.' This interpretation was as
follows: ``An event is due to objective chance if in order to
predict it, or to prefer it to alternatives, at present \DPchg{equi-probable}{equiprobable},
with any high degree of probability, it would be necessary to
know a great many more facts of existence about it than we
actually do know, and if the addition of a wide knowledge of
general principles would be little use.'' The ideal instance of
this is the game of chance; but there are other examples afforded
by science in which these conditions are fulfilled with more or
less perfection. Now the field of statistical induction is the class
of phenomena which are due to the combination of two sets of
influences, one of them constant and the other liable to vary in
accordance with the expectations of objective chance,---Quetelet's
\index{Quetelet}%
`permanent causes' modified by `accidental causes.' In social
and physical statistics the ultimate alternatives are not as a rule
so perfectly fixed, nor the selection from them so purely random,
as in the ideal game of chance. But where, for example, we find
stability in the statistics of crime, we could explain this by
supposing that the population itself is stably constituted, that
persons of different temperaments are alive in proportions more
or less the same from year to year, that the motives for crime are
similar, and that those who come to be influenced by these
motives are selected from the population at large in the same
kind of way. Thus we have stable causes at work leading to the
several alternatives in fixed proportions, and these are modified
by random influences. Generally speaking, for large classes of
social statistics we have a more or less stable population including
different kinds of persons in certain proportions and on the other
%% -----File: 430.png---Folio 419-------
\index{Lexis, and asymmetry of statistical frequency!statistical stability@{and statistical stability}|inote}%
\index{Mendelism and statistics}%
hand sets of environments; the proportions of the different
kinds of persons, the proportions of the different kinds of environments,
and the manner of allotting the environments to the
persons vary in a \emph{random} manner from year to year (or, it may be,
from district to district). In all such cases as these, however,
prediction beyond what has been observed is clearly open to
sources of error which can be neglected in considering, for
example, games of chance;---our so-called `permanent' causes
are always changing a little and are liable at any moment to
radical alteration.

Thus the more closely that we find the conditions in scientific
examples assimilated to those in games of chance, the more
confidently does common sense recommend this method. The
rather surprising frequency with which we find apparent stability
in human statistics may possibly be explained, therefore, if the
biological theory of Mendelism can be established. According to
this theory the qualities apparent in any generation of a given
race appear in proportions which are determined by methods
very closely analogous to those of a game of chance. To take a
specific example (I am giving not the correct theory of sex but an
artificially simplified form of it), suppose there are two kinds of
spermatozoa and two kinds of ova and of the four possible kinds
of union two produce males and two females, then if the kinds of
spermatozoa and ova exist in equal numbers and their union is
determined by random considerations in precisely the same sense
in which a game of chance such as roulette depends upon random
considerations, we should expect the observed proportions to
vary from equality, as indeed they do, in the same manner as
variations from equality of red and black occur at roulette.\footnote
  {The fluctuations in the proportion of the sexes which, as is well known,
  is not in fact one of equality, correspond, as Lexis has shown, to what one
  would expect in a game of chance with an astonishing exactitude. But
  it is difficult to find any other example, amongst natural or social phenomena,
  in which his criteria of stability are by any means as equally well satisfied.}
If
the sphere of influence of Mendelian considerations is wide, we
have both an explanation in part of what we observe and also a
large opportunity in future of using with profit the methods of
statistical analysis.

This is all familiar. This is the way in which in fact we do
think and argue. The inquiry as to how far it is covered by the
abstract analysis of the preceding paragraphs, and by what
%% -----File: 431.png---Folio 420-------
\index{Series of probabilities!independent}%
\index{Series of probabilities!organic}%
logical principle the use of this analysis can be justified as rational,
I have pushed as far as I can. It deserves a profounder study
than logicians have given it in the past.

\Paragraph{8.} Two subsidiary questions remain to be mentioned. The
first of these relates to the character of series which, in the
terminology of Lexis, show a subnormal or supernormal stability;
for I have pressed on to the conclusion of the argument on the
assumption that the stabilities are normal. Subnormal stability
conceals two types: the one in which there is really no stability
at all and the results are in fact chaotic; and the other in which
there is mutual dependence between the successive instances of
such a kind that they tend to resemble one another so that any
divergence from the normal tends to accentuate itself. Super-*normal
stability corresponds in the other direction to the second
of these two types; that is to say, there is mutual dependence of
a regulative kind between the successive instances which tends
to prevent the frequency from swinging away from its mean
value. The case, where the dog was fed with scraps when he
looked thin and not fed when he looked fat, illustrated this.
The typical example of this type is where balls are drawn from
urns, containing black and white balls in certain proportions and
\emph{not} replaced; so that every time a black ball is drawn the next
ball is more likely than before to be white, and there is a tendency
to redress any excess of either colour beyond the proper proportions.
Possibly the aggregate annual rainfall may afford a
further illustration.

Where there is no stability at all and the frequencies are chaotic,
the resulting series can be described as `non-statistical.' Amongst
`statistical series,' we may term `independent series' those of
which the instances are independent and the stability normal,
and `organic series,' those of which the instances are mutually
dependent and the stability abnormal, whether in excess or in
defect. `Organic series' have been incidentally discussed elsewhere
in this volume. I shall not pursue them further now,
because I do not think that they introduce any new \emph{theoretical}
difficulty into the general problem of statistical inference;
although the problem of fitting them into the general theoretical
scheme is not easy.\footnote
  {The following more precise definitions bring these ideas into line with what
  has gone before: consider the terms $a_1, a_2, \ldots a_n$ of a series~$s(x)$; let `$a_r$~is~$g$'
  $\equiv g_r$ and let $g_r/h=p_r$, where $h$~is our data. Then, if $g_r/g_s \ldots g_t \ldots h=p_r$ for all
  values of $r, s, \ldots, t \ldots$, the terms of the series are \emph{independent} relative to~$h$. If
  $p_1=p_2= \ldots =p$ the terms are \emph{uniform}. If the terms are both independent and
  uniform, the series may be called an \emph{independent Bernoullian series}, subject to
  a \emph{Bernoullian probability}~$p$. If the terms are independent but not uniform, the
  series may be called an \emph{independent compound series}, subject to a \emph{compounded
  probability} $1/n\Sum p_r$. If the terms are not independent, the series is an \emph{organic
  series}.

  The same terminology can then be applied to the series $S_1, S_2, \ldots S_n$, regarded
  as members of the series of series~$S(x)$. Let the frequencies of the series for the
  characteristic under inquiry be $x_1, x_2, \ldots x_n$, and let $x_1/h=\theta_1(x_1)$, \ie~$\theta_1(x_1)$ is the
  probability of a frequency~$x_1$ in the first series. Then if $x_r/x_s \ldots h =\theta_r(x_r)$ for all
  values of $r$,~$s$,~etc., the frequencies are \emph{independent}; and if $\theta_1(x)= \theta_2(x_2)= \dots \theta (x)$,
  the frequencies are \emph{stable}. If the frequencies are stable and independent, the
  series of series may be called \emph{Gaussian}. If the frequencies are stable and
  independent, and if in addition each individual series is subject to a Bernoullian
  probability, the probable dispersion of the frequency is normal and symmetrical.
  If the individual series are organic, the dispersion of the frequencies may be
  normal, subnormal, or supernormal. If the series of series is Gaussian, and the
  individual series Bernoullian, we have the type of the perfect statistical series.}
%% -----File: 432.png---Folio 421-------
\index{Coefficient of Credibility!of Correlation|ifoll}%
\index{Series of probabilities!Gaussian|inote}%

\Paragraph{9.} The second question is concerned with the relation between
the Inductive Correlation, which has been the subject-matter of
\index{Correlation!coefficient|ifoll}%
this chapter, and the Correlation Coefficient or, as I should prefer
to call it, the \emph{Quantitative Correlation}, with which recent English
statistical theory has chiefly occupied itself. I do not propose
to discuss this theory in detail, because I suspect that it is much
more concerned, at any rate in its present form, with statistical
description than with statistical induction. The transition from
defining the `correlation coefficient' as an algebraical expression
to its employment for purposes of inference is very far from
clear even in the work of the best and most systematic writers
on the subject, such as Mr.~Yule and Professor Bowley.
\index{Bowley}%
\index{Yule!correlation@{and correlation}}%

In the notation employed in the earlier part of this chapter I
have classified each examined instance~$a$ according as it did or
did not possess the characteristic~$\phi$, \ie~satisfy the propositional
function~$\phi (x)$, or, in other words, according as $\phi (a)$~was true or
false. Thus only two possible alternatives were contemplated,
and $\phi$~was not considered as a quantitative characteristic which
the instance could satisfy in greater or less degree. Equally the
common element in all the instances, required to constitute them
as instances for the purpose of our statistical generalisation (or,
as I have sometimes put it, required to satisfy the \emph{condition} of the
generalisation), was regarded as definite and unique and not
capable of quantitative variation. That is to say, all the instances
satisfied a function~$\psi (x)$, and the question was, what proportion
%% -----File: 433.png---Folio 422-------
of them also satisfied the function~$\phi(x)$. A typical example was
that of sex-ratio,---$\psi (x)$ being the birth of a child and $\phi (x)$~its
sex, where there is no question of \emph{degree} in either $\psi (x)$~or~$\phi(x)$.

It might be the case, however; that the characteristics under
examination were capable of degree or quantitative variation;
for example $\psi (x)$~might be the age of the mother and $\phi(x)$~the
weight of the child at birth, in this case we should have a series
$\psi_1(x), \psi_2(x)$,~etc., corresponding to the various age-periods of the
mothers, and a series $\phi_1(x),~\phi_2(x)$,~etc., corresponding to the various
weights of the children. Now if we concentrated our attention
on $\psi_1(x)$~and~$\phi_1(x)$ alone, \ie~on mothers of a particular age and
the proportions of their children which had a particular weight
at birth, we have a one-dimensional problem of the same kind as
before; out of all the instances which satisfy~$\psi_1(x)$ a certain
proportion satisfy $\psi_1(x)$ also. But clearly we can push our
observations further and we can take note what proportion of the
instances which satisfy $\psi_1(x)$ satisfy $\phi_2(x), \phi_3(x)$, and so on, respectively;
and then we can do the same as regards the instances
which satisfy $\psi_2(x), \psi_3(x)$,~etc. The total results of this two-dimensional
set of observations can then be tabulated in what is
called a twofold correlation table. Thus if $f_{rs}$~is the proportion
of instances satisfying~$\psi_s(x)$ which also satisfy~$\phi_{r}(x)$ we have a
table as follows:
\[
\renewcommand{\arraystretch}{1.5}
\begin{array}{|*{5}{>{\ }c<{\ }|}}
\hline
          & \psi_1(x)& \psi_2(x) & \psi_3(x) & \ldots\\
\hline
\phi_1(x) & f_{11}   & f_{12}    & f_{13} & \\
\hline
\phi_2(x) & f_{21}   & f_{22}    & f_{23} & \\
\hline
\phi_3(x) & f_{31}   & f_{32}    & f_{33} & \\
\hline
\vdots    & \vdots   & \vdots    & \vdots & \\
\hline
\end{array}
\]

We could, further, increase the complexity and completeness
of our observations to any required degree. For example we
might take account also of~$\theta(x)$, the age of the father, and construct
a threefold table where $f_{rst}$~is the proportion of instances
satisfying $\phi_{r}(x), \psi_{s}(x), \theta_{t}(x)$; and so on up to an $n$-fold table.

Clearly it is not necessary for the construction of tables of
%% -----File: 434.png---Folio 423-------
this kind that $\phi(x)$~and~$\psi(x)$ should stand for degrees of the same
quantitative characteristic; they might be any set of exclusive
alternatives; for example, $\psi(x)$~might be the colour of the baby's
eyes, and $\phi(x)$~its Christian name.

But in order that the correlation table may be of any
practical interest for the purposes of inference, it is necessary---and
this, I think, is one of the critical assumptions of correlation---that
$\psi_{1}(x), \psi_{2}(x), \ldots$ and also $\phi_{1}(x), \phi_{2}(x), \ldots$ should
be arranged in an order that is \emph{significant}, \ie~such that we have
some \textit{à~priori} reason for expecting some connection to exist
between the \emph{order} of the~$\psi$'s and the \emph{order} of the~$\phi$'s. The point
of this will be illustrated by concentrating our attention on the
simplest type of case where $\psi(x)$~and~$\phi(x)$ are quantitative
characteristics arranged in order of magnitude. Now suppose
it were the case that the younger mothers tended to bear heavier
babies, then, if $\psi_{1}(x)~\psi_{2}(x)$ are the ages increasing upwards and
$\phi_1(x)~\phi_{2}(x)$ the weights diminishing downwards, $f_{11}$~would probably
be the greatest of the~$f_{r1}$'s and, generally speaking, $f_{r1}$~would be
greater than~$f_{r+1,1}$; also $f_{22}$~might be the greatest of the~$f_{r2}$'s, and
so on; so that the frequencies lying on the diagonal of the table
would be the greatest and the frequencies would tend to be less
the farther they lay from the diagonal. If we had some reason
\textit{à~priori} (\ie~based on our pre-existing knowledge), if only a
slight one, for supposing that there might be some connection
between the age of the mother and the weight of the baby, then,
if in a particular set of instances the frequencies were grouped
about the diagonal as suggested above, this might be taken as
affording some inductive support for the hypothesis.

Now the theory of correlation, as it is expounded in the
text-books, is almost entirely concerned with measuring how
nearly the observed frequencies are grouped about the diagonal
of the table (though the complete theory is not, of course, so
restricted as this). The `coefficient of correlation' is an algebraical
formula which may be regarded as measuring this phenomenon
in a way that is sufficiently satisfactory for all ordinary purposes.
If it is defined thus, it is simply a statistical description of a
particular set of observations arranged in a particular order.
How can we make use of this coefficient for the purposes of
inference?

Dr.~Bowley faces this problem a little more definitely than do
\index{Bowley|ifoll}%
%% -----File: 435.png---Folio 424-------
most statistical writers. Mr.~Yule warns the student that the
\index{Yule!correlation@{and correlation}}%
problem exists,\footnote
  {\textit{Introduction to the Theory of Statistics}, p.~191: ``The coefficient of correlation,
  like an average or a measure of dispersion, only exhibits in a summary
  and comprehensible form one particular aspect of the facts on which it is based,
  and the real difficulties arise in the interpretation of the coefficient when
  obtained.''}
but he does not himself attack it systematically
or do more than apply common sense to particular problems.
So much greater emphasis, however, has been laid hitherto on
the mathematical complications, that many statistical students
hazily float from defining the correlation coefficient as a statistical
description to employing it as a measure of the probability of a
statistical generalisation as to the association between quantitative
variations of $\phi(x)$~and~$\psi(x)$ respectively. If, for example,
it is found in a particular set of observations of
mothers' ages and babies' weights that the frequencies are
closely ranged about the diagonal, this is considered a sufficiently
good reason for attributing probability to a generalisation as to
the `correlation' (\ie~tendency to quantitative correspondence)
between the age of the mother and the weight of the baby.

Dr.~Bowley's line of thought is as follows. He begins by
defining the correlation coefficient~$r$ merely as a statistical description
(\textit{Elements of Statistics}, p.~354). He then shows (p.~355),
as an illustration of the nature of~$r$, that if $x$~and~$y$ are two
variable quantities which depend (more strictly, \emph{are known} to
depend) on other variables $U$,~$V$,~$W$ in such a way that
\begin{align*}
X_t &= {}_1U_t + {}_2U_t + \ldots + {}_pU_t + {}_1V_t + {}_2V_t + \ldots + {}_qV_t \\
Y_t &= {}_1U_t + {}_2U_t + \ldots + {}_pU_t + {}_1W_t + {}_2W_t + \ldots \DPtypo{}{+} {}_qW_t
\end{align*}
where ${}_1U_t,~{}_2U_t \ldots$ ${}_1V_t,~{}_2V_t \ldots$ ${}_1W_t,~{}_2W_t \ldots$ are selected
at random each from an independent group of quantities (more
strictly, are \emph{relative to our data}, random members of independent
groups); then, if we know \textit{à~priori} certain statistical coefficients
descriptive of the constitution of these groups, the value of~$r$
will probably tend towards a certain value. So far we are on
fairly safe, but not very fruitful, ground. We have no basis
for arguing backwards from the observed value of~$r$; but,
provided we have rather extensive and peculiar knowledge
\textit{à~priori} as to how $X_t$~and~$Y_t$ are constituted, then we have
calculable expectations as to the limits within which the value
%% -----File: 436.png---Folio 425-------
of~$r$, namely the correlation coefficient between $X$~and~$Y$, will
probably turn out to lie, when we have observed it.

Dr.~Bowley's next move is more dubious. If the constitutions
of the independent groups are similar in a certain, statistical
respect (\ie~if they have the same standard deviations), then,
Dr.~Bowley concludes, $r = \dfrac{p}{(p + q)}$, which ``expressed in words
shows that the correlation coefficient tends to be the ratio of
the number of causes common in the genesis of two variables
to the whole number of independent causes on which each
depends.'' By this time the student's mind, unless anchored
by a more than ordinary scepticism, will have been well launched
into a vague, fallacious sea.

Neglecting, however, the \textit{dictum} just quoted, we find that the
second stage of the argument consists in showing that, \emph{if} we
have a certain sort of knowledge \textit{à~priori} as to how our variables
are constituted, then the various possible values for the coefficients
of correlation, which would be yielded by actual sets of observations
made in prescribed conditions, will have, \textit{à~priori}, and
before the observations have been made, calculable probabilities,
certain ranges of values being probable and others improbable.

As a rule, however, we are not arguing from knowledge about
the variables to anticipations about their correlation coefficient;
but the other way round, that is from observations of their
correlation coefficients to theories about the nature of the variables.
Dr.~Bowley perceives that this involves a third stage
of the argument, and appeals accordingly (p.~409) to ``the
difficult and elusive theory of inverse probability.'' He apprehends
\index{Inverse Probability!Bowley@{and Bowley}}%
the difficulty but he does not pursue it; and, like Mr.~Yule,
he really falls back for practical purposes on the criteria
of common sense, an expedient well enough in his case, but not
a universal safeguard.

The general argument from inverse probability to which Dr.~Bowley
makes his vague appeal is doubtless on the following
lines: If there is no causal connection between the two sets of
quantities, then a close grouping of the frequencies about the
diagonal would be \textit{à~priori} improbable (and the greater the
number of the individual observations, the greater the improbability
since, if the quantities are independent, there is, then, all
the more opportunity for `averaging out'); therefore, inversely,
%% -----File: 437.png---Folio 426-------
if the frequencies do group themselves about the diagonal, we
have a presumption in favour of a causal connection between
the two sets of quantities.

But if the reader recalls our discussion of the principle of
inverse probability, he will remember that this conclusion cannot
be reached unless \textit{à~priori}, and quite apart from the observations
in question, we have some reason for thinking that there may be
such a causal connection between the quantities. The argument
can only strengthen a pre-existing presumption; it cannot
create one. And in the absence of reasons peculiar to the
particular inquiry, we have no choice but to fall back on the
general methods and the general presumptions of induction.

It is apparent that, where the correlation argument seems
\index{Correlation!Quantitative}%
plausible, some tacit assumption must have slipped in, if we return
to the case where our correlation table relates to the weights of
the babies and their Christian names. Either by accident or
because we had arranged the order of the Christian names to
suit, it might happen with a particular set of observations, even
a fairly numerous set, that the correlation coefficient was large.
Yet on that evidence alone we should hardly assert a generalisation
connecting the weights of babies with their Christian names.

The truth is that sensible investigators only employ the
correlation coefficient to test or confirm conclusions at which
they have arrived on other grounds. But that does not validate
the crude way in which the argument is sometimes presented,
or prevent it from misleading the unwary,---since not all investigators
are sensible.

If we abandon the method of inverse probability in favour of
the less precise but better founded processes of induction,
`quantitative correlation,' as I should like to term this particular
branch of statistical induction, is more complicated than, but not
theoretically distinct from, the kind of arguments which have
occupied the earlier paragraphs of this chapter. The character
of the additional complication can be described by saying that
we are presented with a two-dimensional problem instead of a
one-dimensional problem. The mere existence of a particular
correlation coefficient as descriptive of a group of observations,
even of a large group, is not in itself a more conclusive or significant
argument than the mere existence of a particular frequency
coefficient would be. Of course if we have a considerable body
%% -----File: 438.png---Folio 427-------
\index{Lucretius}%
of pre-existing knowledge relevant to the particular inquiry, the
calculation of a small number of correlation coefficients may be
crucial. But otherwise we must proceed as in the case of frequency
coefficients; that is to say we must have before us, in
order to found a satisfactory argument, many sets of observations,
of which the correlation coefficients display a significant
stability in the midst of variation in the non-essential class
characteristics (\ie~those class characteristics which our generalisation
proposes to neglect) of the different sets of observations.

\Paragraph{10.} I am now at the conclusion of an inquiry in which,
beginning with fundamental questions of logic, I have endeavoured
to push forward to the analysis of some of the actual arguments
which impress us as rational in the progress of knowledge and the
practice of empirical science. In writing a book of this kind the
author must, if he is to put his point of view clearly, pretend sometimes
to a little more conviction than he feels. He must give
his own argument a chance, so to speak, nor be too ready to
depress its vitality with a wet cloud of doubt. It is a heavy task
to write on these problems; and the reader will perhaps excuse
me if I have sometimes pressed on a little faster than the difficulties
were overcome, and with decidedly more confidence than
I have always felt.

In laying the foundations of the subject of Probability, I have
departed a good deal from the conception of it which governed
the minds of Laplace and Quetelet and has dominated through
\index{Laplace}%
\index{Quetelet}%
their influence the thought of the past century,---though I believe
that Leibniz and Hume might have read what I have written with
\index{Hume}%
\index{Leibniz}%
sympathy. But in taking leave of Probability, I should like to
say that, in my judgment, the practical usefulness of those modes
of inference, here termed Universal and Statistical Induction,
on the validity of which the boasted knowledge of modern science
depends, can only exist---and I do not now pause to inquire
again whether such an argument \emph{must} be circular---if the universe
of phenomena does in fact present those peculiar characteristics
of atomism and limited variety which appear more and more
\index{Variety!limitation of}%
clearly as the ultimate result to which material science is tending:
\begin{center}
\settowidth{\TmpLen}{materiem quoque \textit{finitis} differre figuris.}%
\begin{minipage}{\TmpLen}%
  \begin{flushright}
    fateare necessest\\
    materiem quoque \textit{finitis} differre figuris.
  \end{flushright}
\end{minipage}
\end{center}
The physicists of the nineteenth century have reduced matter to
%% -----File: 439.png---Folio 428-------
\index{Calculus of Probability}%
\index{Mendelism and statistics}%
the collisions and arrangements of particles, between which the
ultimate qualitative differences are very few; and the Mendelian
biologists are deriving the various qualities of men from the
collisions and arrangements of chromosomes. In both cases the
analogy with the perfect game of chance is really present; and
the validity of some current modes of inference may depend on the
assumption that it is to material of this kind that we are applying
them. Here, though I have complained sometimes at their want
of logic, I am in fundamental sympathy with the deep underlying
conceptions of the statistical theory of the day. If the contemporary
doctrines of Biology and Physics remain tenable, we may
have a remarkable, if undeserved, justification of some of the
methods of the traditional Calculus of Probabilities. Professors
of probability have been often and justly derided for arguing as
if nature were an urn containing black and white balls in fixed
proportions. Quetelet once declared in so many words---``l'urne
\index{Quetelet}%
que nous interrogeons, c'est la nature.'' But again in the
history of science the methods of astrology may prove useful to
the astronomer; and it may turn out to be true---reversing
Quetelet's expression---that ``La nature que nous interrogeons,
c'est une urne.''
%% -----File: 440.png---Folio 429-------

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\Bibliography

\Section{INTRODUCTION}

\begin{Quote}
There is no opinion, however absurd or incredible, which has not been
maintained by some one of our philosophers.---\textsc{Descartes}.
\end{Quote}

\First{The} following Bibliography does not pretend to be complete,
but it contains a much longer list of what has been written
about Probability than can be found elsewhere. I have
hesitated a little before burdening this volume with the titles
of many works, so few of which are still valuable. But I was
myself much hampered, when first I embarked on the study of
this subject, by the absence of guide-posts to the scattered but
extensive literature of the subject; and a list which I drew up
for my own convenience, without much attention to bibliographical
nicety or to exact uniformity in the style of entry,
may be useful to others.

It is rather an arbitrary matter to decide what to include
and what to exclude. Probability overlaps many other topics,
and some of the most important references to it are to be
found in books, the main topic of which is something else. On
the other hand it would be absurd to include every casual
reference; and no useful purpose would have been served by
cataloguing the very numerous volumes dealing with Insurance,
Games of Chance, Statistics, Errors of Observation, and Least
Squares, which treat in detail these various applications of the
Theory of Probability. It has been a matter of some difficulty,
therefore, to know precisely where to draw the line. Where
the main subject of a book or paper is Probability proper, I
have included it, nearly regardless of my own view as to its
importance, and have not attempted to act as censor; but
where Probability is not the main subject or where an application
of Probability is concerned, the chief interest of which is
%% -----File: 443.png---Folio 432-------
solely in the application itself, I have only included the entry
where I think it important, intrinsically or historically or
from the celebrity of the author. In particular, the existence
of Professor Mansfield Merriman's very extensive bibliography,
published in the \textit{Transactions of the Connecticut Academy} for
1877, has made it possible to deal very lightly (and to the
extent of but few entries) with the inordinately large literature
of Least Squares. This list comprises 408~titles of writings
relating to the Method of Least Squares and the theory of
accidental errors of observation, and is sufficiently exhaustive
so far as relates to memoirs on this topic published before
1877.

Of bibliographical sources for Probability proper, Todhunter's
\textit{History of the Mathematical Theory of Probability}
and Laurent's \textit{Calcul des probabilités} are alone important. Of
\emph{mathematical} works published before the time of Laplace,
Todhunter's list, and also his commentary and analysis, are
complete and exact,---a work of true learning, beyond criticism.
The bibliographical catalogue at the conclusion of Laurent's
\textit{Calcul} (published in 1873) is the longest list published hitherto
of general works on Probability. But it is unduly swollen by
the inclusion of numerous items on Insurance and Errors of
Observation, the bearing of which on Probability is very
slight;\footnote
  {Laurent's list contains 310~titles, of which I have excluded~174 from my
  list as being insufficiently relevant.}
it is chiefly mathematical in bias; and it is now
nearly fifty years old.

I have not read all these books myself, but I have read
more of them than it would be good for any one to read again.
There are here enumerated many dead treatises and ghostly
memoirs. The list is too long, and I have not always successfully
resisted the impulse to add to it in the spirit of a
collector. There are not above a hundred of these which it
would be worth while to preserve,---if only it were securely
ascertained which these hundred are. At present a bibliographer
takes pride in numerous entries; but he would be a
more useful fellow, and the labours of research would be
lightened, if he could practise deletion and bring into existence
an accredited \textit{Index Expurgatorius}. But this can only be
accomplished by the slow mills of the collective judgment of
%% -----File: 444.png---Folio 433-------
the learned; and I have already indicated my own favourite
authors in copious footnotes to the main body of the text.

The list is long; yet there is, perhaps, no subject of equal
importance and of equal fascination to men's minds on which
so little has been written. It is now fifty-five years since
Dr.~Venn, still an accustomed figure in the streets and courts
of Cambridge, first published his \textit{Logic of Chance}; yet amongst
systematic works in the English language on the logical foundations
of Probability my Treatise is next to his in chronological
order.

The student will find many famous names here recorded.
The subject has preserved its mystery, and has thus attracted
the notice, profound or, more often, casual, of most speculative
minds. Leibniz, Pascal, Arnauld, Huygens, Spinoza, Jacques
and Daniel Bernoulli, Hume, D'Alembert, Condorcet, Euler,
Laplace, Poisson, Cournot, Quetelet, Gauss, Mill, Boole,
Tchebychef, Lexis, and Poincaré, to name those only who are
dead, are catalogued below.

\begin{center}\rule{10em}{.5pt}\end{center}

\begin{Biblio}

\Bibsect[noskip]{A}

\BibItem[Abbott, T.~K.] ``On the Probability of Testimony and Arguments.'' Phil.\
Mag.\ (4), vol.~27, 1864.

\BibItem[Adrain, R.] ``Research concerning the Probabilities of the Errors which happen in making Observations.'' The Analyst or Math.\ Museum, vol.~1,
pp.~93--109, 1808.

\Bibnote[This paper, which contains the first deduction of the normal law of error, was partly reprinted by Abbé with historical notes in Amer.\ Journ.\
Sci.\ vol.~i.\ pp.~411--415, 1871.]

\BibItem[Ammon, O.] ``Some Social Applications of the Doctrine of Probability.''
Journ.\ Pol.\ Econ.\ vol.~7, 1899.

\BibItem[Ampère.] Considérations sur la théorie mathématique du jeu. Pp.~63. 4to. Lyon, 1802.

\BibItem[Ancillon.] ``Doutes sur les bases du calcul des probabilités.'' Mém.\ Ac.\ Berlin, pp.~3--32, 1794--5.

\BibItem[Arbuthnot, J.] Of the Laws of Chance, or a Method of Calculation of the
Hazards of Game plainly Demonstrated. 16mo. London, 1692.

\Bibnote[Contains a translation of Huygens, De ratiociniis in ludo aleae.]

\BibItem[\bysame] 4th~edition revised by John Hans. By whom is added a demonstration of
the gain of the banker in any circumstance of the game call'd Pharaon, etc.
Sm.~8vo. London, 1738.

\Bibnote[For a full account of this book and discussion of the authorship, see
Todhunter's History, pp.~48--53.]

\BibItem[\bysame] ``An Argument for Divine Providence, taken from the constant Regularity
observ'd in the Births of both Sexes.'' Phil.\ Trans, vol.~27, pp.~186--190
(1710--12).

\Bibnote[Argues that the excess of male births is so invariable, that we may conclude
that it is not an even chance whether a male or female be born.]
%% -----File: 445.png---Folio 434-------

\BibItem[Aristotle.] Anal.\ Prior.\ ii.~27, 70\textsuperscript{a}~3.
Rhet.\ i.~2, 1357~a 34. %[** TN: Semantic re-breaking]

\Bibnote[See Zeller's \textit{Aristotle} for further references.]

\BibItem[Arnauld.] (The Port Royal Logic.) La Logique ou l'Art de penser. 12mo.
Paris, 1662. Another ed.\ C.~Jourdain, Hachette, 1846. Transl.\ into
Eng.\ with introduction by T.~S. Baynes. London, 1851. xlvii~+~430.
See especially pp.~351--370.

\Bibsect{B}

\BibItem[Babbage, C.] An Examination of some Questions connected with Games of
Chance. 4to. 25~pp. Trans.\ R.~Soc.\ Edin., 1820.

\BibItem[Bachelier, Louis.] Calcul des probabilités. Tome~i. 4to. Pp.~vii~+~517.
Paris, 1912.

\BibItem[\bysame] Le Jeu, la chance, et le hasard. Pp.~320. Paris, 1914.

\BibItem[[Bailey, Samuel.]] Essays on the pursuit of truth, on the progress of knowledge
and on the fundamental principle of all evidence and expectation.
Pp.~xii~+~302. London, 1829.

\BibItem[Baldwin.] Dictionary of Philosophy. Bibliographical volumes; \textit{s.v.}~``Probability.''

\BibItem[Baniol, A.] ``Le Hasard.'' Revue Internationale de Sociologie. Pp.~16. 1912.

\BibItem[Barbeyrac.] Traité du jeu. 1st~ed.\ 1709. 2nd~ed.\ 1744.

\Bibnote[Todhunter states (p.~196) that Barbeyrac is said to have published a
discourse ``Sur la nature du sort.'']

\BibItem[Bayes, Thomas.] An Essay towards solving a Problem in the Doctrine of
Chances. Phil.\ Trans.\ vol.~liii.\ pp.~370--418, 1763. A demonstration,
etc. Phil.\ Trans.\ vol.~liv.\ pp.~296--325, 1764.

\Bibnote[Both the above were communicated by the Rev.\ Richard Price, and
the second is partly due to him.]

\BibItem[\bysame] German transl. Versuch zur Lösung eines Problems der Wahrscheinlichkeitsrechnung.
Herausgegeben von H.~E. Timerding. Sm. 8vo.
Leipzig, 1908. Pp.~57.

\BibItem[Béguelin.] ``Sur les suites ou séquences dans le loterie de Gênes.'' Hist.\ de
l'Acad. Pp.~231--280. Berlin, 1765.

\BibItem[\bysame] `` Sur l'usage du principe de la raison suffisante dans le calcul des probabilités.''
Hist.\ de l'Acad. Pp.~382--412. Berlin, 1767. (Publ.~1769.)

\BibItem[Bellavitis.] ``Osservazioni sulla theoria delle probabilità.'' Atti del Instituto
Veneto di Scienze, Lettere, ed Arti, Venice, 1857.

\BibItem[Benard.] ``Note sur une question de probabilités.'' Journal de l'École
royale politechnique. Vol.~15, Paris, 1855.

\BibItem[Bentham, J.] Rationale of Judicial Evidence. \\
See Introductory View, chap.~xii., and Bk.~i, chaps.\ v.,~vi.,~vii.

\BibItem[Bernoulli, Daniel.] ``Specimen theoriae novae de mensura sortis.'' Comm.\
Acad.\ Sci.\ Imp.\ Pet.\ vol.\ v.~pp.~175--192, 1738.

\BibItem[\bysame] Germ.~transl.~1896, by A.~Pringsheim: Die Grundlage der modernen
Wertlehre. Versuch einer neuen Theorie der Wertbestimmung von Glücksfällen
(Einleitung von Ludvig Fick). Pp.~60. Leipzig, 1896.

\BibItem[\bysame] ``Recueil des pièces qui ont remporté le prix de l'Académie Royale des
Sciences.'' 1734. iii.\ pp.~95--144.

\BibItem[\bysame] [On ``La cause physique de l'inclinaison des plans des orbites des planètes
par rapport au plan de l'équateur de la révolution du soleil autour de son
axe.'']

\BibItem[\bysame] ``Essai d'une nouvelle analyse de la mortalité causée par la petite
vérole.'' Hist.\ de l'Acad.\ pp.~1--45. Paris, 1760.

\BibItem[\bysame] De usu algorithmi infinitesimalis in arte conjectandi specimen. Novi
Comm.\ Petrop., 1766. xii.\ pp.~87--98. A 2nd~memoir. Petrop., 1766.
xii.\ pp.~99--126. See a oriticism by Trembley, Mem.\ de l'Acad., Berlin,
1799.
%% -----File: 446.png---Folio 435-------

%\BibItem[Bernoulli, Daniel.]---\emph{continued}.

\BibItem[\bysame] Disquisitiones analytiquae de novo problemate conjecturali. Novi
Comm.\ Petrop.\ xiv.\ pp.~1--25, 1769. A 2nd~memoir, Petrop.\ xiv.\ pp.~26--45, 1769.

\BibItem[\bysame] ``Dijudicatio maxime probabilis plurium observationum discrepantium
atque verisimillima inductio inde formanda.'' Acta Acad., pp.~3--23.
Petrop., 1777. Crit.\ by Euler, pp.~24--33\DPtypo{}{.}

\BibItem[Bernoulli, Jac.] Ars conjectandi, opus posthumum. Pp.~ii~+~306~+~35.
Sm. 4to, Basileae, 1713.

\Bibnote[Published by N.~Bernoulli eight years after Jac.\ Bernoulli's death.]

\BibItem[\bysame] Part~I\@. Reprint with notes and additions of Huygens, De ratiociniis in
ludo aleae.

\BibItem[\bysame] Part~II\@. Doctrina de permutationibus et combinationibus.

\BibItem[\bysame] Part~III\@. Explicans usum praecedentis doctrinae in variis sortitionibus
et ludis aleae. [Twenty-four problems.]

\BibItem[\bysame] Part~IV\@. Tradens usum et applicationem praecedentis doctrinae in
civilibus, moralibus et oeconomicis.

\BibItem[\bysame] Tractatus de seriebus infinitis. [Not connected with the subject of
Probability.]

\BibItem[\bysame] Lettre à un amy, sur les partis du jeu de paume.

\Bibnote[The most important sections, including Bernoulli's Theorem, are in
Part~IV\@. For a very full account of the whole volume see Todhunter's
\textit{History}, chap.~vii.]

\BibItem[\bysame]%[** TN: Retaining inconsistent capitalization of "transl."]
Engl.\ Transl.\ of Part~II. only, vide \textit{Maseres}.

\BibItem[\bysame] Fr.\ transl.\ of Part~I. only, vide \textit{Vastel}.

\BibItem[\bysame] Germ.\ transl.: Wahrscheinlichkeitsrechnung. 4~Teile mit dem Anhange:
Brief an einem Freund über das Ballspiel, übers.\ u.~hrsg.\ v.~R. Haussner.
2~vols. Sm.~8vo. 1899.

\Bibnote[See also \textit{Leibniz}.]

\BibItem[Bernoulli, John.] De alea, sive arte conjectandi, problemata quaedam.
Collected ed.\ vol.~iv.\ pp.~28--33. 1742.

\BibItem[Bernoulli, John (grandson).] ``Sur les suites ou séquences dans la loterie de
Gènes.'' Hist.\ de l'Acad., pp.~234--253. Berlin, 1769.

\BibItem[\bysame] ``Mémoire sur un problème de la doctrine du hasard.'' Hist.\ de l'Acad.,
pp.~384--408. Berlin, 1768.

\BibItem[Bernoulli, Nicholas.] Specimina artis conjectandi, ad quaestiones juris
applicatae. Basel, 1709. Repr.\ Act.\ Erud.\ Suppl., pp.~159--170, 1711.

\BibItem[Bertrand, J.] Calcul des probabilités. Pp.~lvii~+~332. Paris, 1889.

\BibItem[\bysame] ``Sur l'application du calcul des probabilités à la théorie des jugements.''
Comptes rendus, 1887.

\BibItem[\bysame] ``Les Lois du hasard.'' Rev.\ des Deux Mondes, p.~758. Avril 1884.

\BibItem[Bessel.] ``Untersuchung über die Wahrscheinlichkeit der Beobachtungsfehler.''
Astr.\ Nachrichten, vol.~xv.\ pp.~369--404, 1838.

\BibItem[\bysame] Also Abhandl.\ von Bessel, vol.~ii.\ pp.~372--391. Leipzig, 1875.

\BibItem[Bicquilley, C.~F.~de.] Du calcul des probabilités. 164~pp., 1783. 2nd~ed.\ 1805.

\BibItem[\bysame] Germ.\ transl.\ by C.~F. Rüdiger. Leipzig, 1788.

\BibItem[Bienaymé, J.] ``Sur un principe que Poisson avait cru découvrir et qu'il avait
appelé loi des grands nombres.'' Comptes rendus de l'Acad.\ des Sciences
morales, 1855.

\Bibnote[Reprinted in Journal de la Soc.\ de Statistiques de Paris, pp.~199--204,
1876.]

\BibItem[\bysame] ``Probabilité de la constance des causes conclue des effets observés.''
Procès-verbaux de la Soc.\ Philomathique, 1840.

\BibItem[\bysame] ``Sur la probabilité des résultats moyens des observations, etc.'' Sav.\
Étrangers, v.,~1838.
%% -----File: 447.png---Folio 436-------

% \BibItem[Bienaymé, J.]---\emph{continued}.

\BibItem[\bysame] ``Théorème sur la probabilité des résultats moyens des observations.''
Procès-verbaux de la Soc.\ Philomathique, 1839.

\BibItem[\bysame] ``Considérations à l'appui de la découverte de Laplace sur la loi de probabilité
dans la méthode des moindres carrés.'' Comptes rendus des
séances de l'Académie des Sciences, vol.~xxxvii., 1853.

\Bibnote[Reprinted in Journal de Liouville, 2nd~series, vol.~xii., 1867, pp.~158--176.]

\BibItem[\bysame] Remarques sur les différences qui distinguent l'interpolation de Cauchy
de la méthode des moindres carrés.'' Comptes rendus, 1853.

\BibItem[\bysame] ``Probabilité des erreurs dans la méthode des moindres carrés.'' Journ.\ Liouville, vol.~xvii., 1852.

\BibItem[Binet.] ``Recherches sur une question de probabilité'' (Poisson's Theorem).
Comptes rendus, 1844.

\BibItem[Blaschke, E.] Vorlesungen über mathematische Statistik. Pp.~viii~+~268.
Leipzig, 1906.

\BibItem[Bobek, K.~J.]  Lehrbuch der Wahrscheinlichkeitsrechnung. Nach System
Kleyer. Pp.~296. Stuttgart 1891.

\BibItem[Bohlmann, G.] ``Die Grundbegriffe der Wahrscheinlichkeitsrechnung in ihrer
Anwendung auf die Lebensversicherung.'' Atti del IV~Congr.\ intern.\ dei
matematici, Rome, 1909.

\BibItem[Boole, G.] Investigations of Laws of Thought on which are founded the
Mathematical Theories of Logic and Probabilities. Pp.~ix~+~424. London,
1854.

\BibItem[\bysame] ``Proposed Questions in the Theory of Probabilities.'' Cambridge and
Dublin Math.\ Journal, 1852.

\BibItem[\bysame] ``On the Theory of Probabilities, and in particular on Michell's Problem
of the Distribution of the Fixed Stars.''  Phil.\ Mag., 1851.

\BibItem[\bysame] ``On a General Method in the Theory of Probabilities.''  Phil.\ Mag.,
1852.

\BibItem[\bysame] ``On the Solution of a Question in the Theory of Probabilities.''  Phil.\ Mag., 1854.

\BibItem[\bysame] ``Reply to some Observations published by Mr.~Wilbraham in the Phil.\
Mag.~vii.\ p.~465, on Boole's `Laws of Thought.'\,''  Phil.\ Mag., 1854.

\BibItem[\bysame] ``Further Observations in reply to Mr.~Wilbraham.'' Phil.\ Mag., 1854.

\BibItem[\bysame] ``On the Conditions by which the Solutions of Questions in the Theory
of Probabilities are limited.'' Phil.\ Mag., 1854.

\BibItem[\bysame] ``On certain Propositions in Algebra connected with the Theory of
Probabilities.'' Phil.\ Mag., 1855.

\BibItem[\bysame] ``On the Application of the Theory of Probabilities to the Question of
the Combination of Testimonies or Judgments.'' Edin.\ Phil.\ Trans, vol.~xxi.\ pp.~597--652, 1857.

\BibItem[\bysame] ``On the Theory of Probabilities.'' Roy.\ Soc.\ Proc.\ vol.~xii.\ pp.~179--184,
1862--1863.

\BibItem[Borchardt, B.] Einführung in die Wahrscheinlichkeitslehre. vi~+~86.
Berlin, 1889.

\BibItem[Bordoni, A.] Sulle probabilità. 4to. Giorn.\ dell'  I.~R. Instit.\ Lombardo di
Scienze. T.~iv. Nuova Serie. Milano, 1852.

\BibItem[Borel, E.] Éléments de la théorie des probabilités. 8vo, pp.~vii~+~191.
Paris, 1909. 2nd~ed.\ 1910.

\BibItem[\bysame] Le Hasard. Pp.~iv~+~312. Paris, 1914.

\BibItem[\bysame] ``Le Calcul des probabilités et la méthode des majorités.'' L'Année
psychologique, vol.~14, pp.~125--151. Paris, 1908.

\BibItem[\bysame] ``Les Probabilités dénombrables et leurs applications arithmétiques.''
Rendiconti del Circolo matematico di Palermo, 1909.

\BibItem[\bysame] ``Le Calcul des probabilités et la mentalité individualiste.'' Revue du
Mois, vol.~6, pp.~641--650, 1908.
%% -----File: 448.png---Folio 437-------

%\BibItem[Borel, E.]---\emph{continued}.

\BibItem[\bysame]
``La Valeur practique du calcul des probabilités.'' Revue du Mois, vol.~1, pp.~424--437, 1906.

\BibItem[\bysame] ``Les Probabilités et M.~le Dantec.'' Revue du Mois, vol.~12, pp.~77--91,
1911.

\BibItem[Bortkiewicz, L.~von.] Das Gesetz der kleinen Zahlen. 8vo, pp.~viii~+~52,
Leipzig, 1898.

\BibItem[\bysame] ``Anwendungen der Wahrscheinlichkeitsrechnung auf Statistik.'' Encyklopädie
der mathematischen Wissenschaften, Band~1, Heft~6.

\BibItem[\bysame] ``Wahrscheinlichkeitstheorie und Erfahrung.'' Zeitschrift für Philosophie
und philosophische Kritik, vol.~121, pp.~71--81. Leipzig, 1903.

\Bibnote [With reference to Marbe, Brömse, and Grimsehl, \textit{q.v.}]

\BibItem[\bysame] ``Kritische Betrachtungen zur theoretischen Statistik.'' Jahrb.\ f.~Nationalök.\
u.~Stat.~(3), vol.~8, pp.~641--680, 1894; vol.~10, pp.~321--360, 1895; vol.~11, pp.~671--705, 1896.

\BibItem[\bysame] ``Die erkenntnistheoretischen Grundlagen der Wahrscheinlichkeitsrechnung.''
Jahrb.\ f.~Nationalök.\ u.~Stat.~(3), vol.~17, pp.~230--244,
1899.

\Bibnote [Criticised by Stumpf, \textit{q.v.}, who is answered by Bortkiewicz, \textit{loc.\ cit.},
vol.~18, pp.~239--242, 1899.]

\BibItem[\bysame] ``Zur Verteidigung des Gesetzes der kleinen Zahlen.'' Jahrb.\ f.~Nationalök.\
u.~Stat.~(3), vol.~39, pp.~218--236, 1910.

\Bibnote [The literature of this topic is not fully dealt with in this Bibliography,
but very full references to it will be found in the above article.]

\BibItem[\bysame] ``Über den Präzisionsgrad des Divergenzkoeffizientes.'' Mitteil.\ des Verbandes
der österr.\ und ungar.\ Versicherungstechniker, vol.~5.

\BibItem[\bysame] ``Realismus und Formalismus in der mathematischen Statistik.'' Allg.\
Stat.\ Archiv, vol.~ix.\ pp.~225--256.  Munich, 1915.

\BibItem[\bysame] Die Iterationen: ein Beitrag zur Wahrscheinlichkeitstheorie. Pp.~xii~+~205.
Berlin, 1917.

\BibItem[\bysame] Die radioaktive Strahlung als Gegenstand wahrscheinlichkeitstheoretischer
Untersuchungen. Pp.~84. Berlin, 1913.

\BibItem[\bysame] ``Wahrscheinlichkeitstheoretische Untersuchungen über die Knabenquote
bei Zwillings Gebieten.'' Sitzungsber.\ der Berliner Math.\ Ges., vol.~xvii.\ pp.~8--14, 1918.

\BibItem[\bysame] Homogeneität und Stabilität in der Statistik. Pp.~81. (Extracted from
the Skandinavisk Aktuarietidskrift.) Uppsala, 1918.

\BibItem[Bostwick, A.~E.]  ``The Theory of Probabilities.'' Science,~iii., 1896,
p.~66.

\BibItem[Boutroux, Pierre.] ``Les Origines du calcul des probabilités.''  Revue du
Mois, vol.~5, pp.~641--654, 1908.

\BibItem[Bowley, A.~L.] Elements of Statistics. Pp.~xi~+~459. 4th~ed. London,
1920.

\BibItem[Bradley, T.~H.] The Principles of Logic. Bk.~i.\ chap.~8, §§\;32--63, pp.~201--20.
London, 1883.

\BibItem[Bravais.] ``Analyse mathématique sur les probabilités des erreurs de situation
d'un point.'' Mém.\ Sav.\ vol.~9, pp.~255--332, Paris, 1846.

\BibItem[Brendel.] Wahrscheinliclikeitsrechnung mit Einschluss der Anwendungen.
Göttingen, 1907.

\BibItem[Broad, C.~D.] ``The Relation between Induction and Probability.'' Mind,
vol.~xxvii.\ (1918). Pp.~389--404, and vol.~xxix.\ (1920) pp.~11--45.

\BibItem[\DPtypo{Bromse}{Brömse}, H.] Untersuchungen zur Wahrscheinlichkeitslehre. (Mit besonderer
Beziehung auf Marbes Schrift (\textit{q.v.}).)

\BibItem[\bysame] Zeitschrift für Philosophie und philosophische Kritik. Band~118.\
Leipzig, 1901. Pp.~145--153.

\Bibnote (See also Marbe, Grimsehl, and v.~Bortkiewicz.)
%% -----File: 449.png---Folio 438-------

\BibItem[\DPtypo{Brunn}{Brünn}, Dr.\ Hermann.] ``Über ein Paradoxon der Wahrscheinlichkeitsrechnung.''
Sitzungsberichte der philos.-philol. Klasse der K.~bayrische
Akademie, pp.~692--712, 1892.

\BibItem[Bruns, H.] Wahrscheinlichkeitsrechnung und Kollektivmasslehre. 8vo.
Pp.~viii~+ 310~+~18. Leipzig, 1906.

\BibItem[\bysame] ``Das Gruppenschema für zufällige Ereignisse.'' Abhandl.\ d.~Leipz.\
Ges.\ d.~Wissensch.\ vol.~xxix.\ pp.~579--628, 1906.

\BibItem[Bryant, Sophie.] ``On the Failure of the Attempt to deduce inductive Principles
from the Mathematical Theory of Probabilities.'' Phil.\ Mag.\ S.~5,
No.~109, Suppl.\ vol.~17.

\BibItem[Buffon.] ``Essai d'arithmétique morale.'' Supplément à l'Histoire Naturelle,
vol.~4, 103~pp. 4to. 1777. Hist.\ Ac.\ Par.\ pp.~43--45, 1733.

\BibItem[Bunyakovski.] Osnovaniya, etc. (Principles of the Mathematical Theory of
Probabilities.) Petersburg, 1846.

\BibItem[Burbury, S.~H.] ``On the Law of Probability for a System of correlated
variables.'' Phil.\ Mag.~(6), vol.~17, pp.~1--28, 1909.

\Bibsect{C}

\BibItem[Campbell, R.] ``On a Test for ascertaining whether an observed Degree of
Uniformity, or the reverse, in tables of Statistics is to be looked upon as
remarkable.'' Phil.\ Mag., 1859.

\BibItem[\bysame] ``On the Stability of Results based upon average Calculations.'' Journ.\
Inst.\ Act.\ vol.~9, p.~216.

\BibItem[\bysame] A popular Introduction to the Theory of Probabilities. Pp.~16, Edinburgh,
1865.

\BibItem[Cantelli, F.~P.] ``Sulla applicazione delle probabilità parziali alla statistica.''
Giornale di Matematica finanziaria, vol.~i.\ (1919), pp.~30--44.

\BibItem[Cantor, G.] Historische Notizen über die Wahrscheinlichkeitsrechnung. 4to.
8~pp. Halle, 1874.

\BibItem[Cantor, M.] Politische Arithmetik oder die Arithmetik des täglichen Lebens.
Pp.~x~+~155. Leipzig, 1898, 2nd~ed.\ 1903.

\BibItem[Canz, E.~C.] Tractatio synoptica de probabilitate juridica sive de praesumtione.
4to. Tübingen, 1751.

\BibItem[Caramuel, John.] Kybeia, quae combinatoriae genus est, de alea, et ludis
fortunae serio disputans. 1670. [Includes a reprint of Huygens, which
is attributed to Longomontanus.]

\BibItem[Cardan.] De ludo aleae.\ fo.,~15~pp. 1663. [Cardan ob.\ 1576.]

\BibItem[Carvello, E.] Le Calcul des probabilités et ses applications. 8vo. Pp.~ix~+~169.
Paris, 1912.

\BibItem[Castelnuovo, Guido.] Calcolo delle probabilità. Large 8vo. Pp.~xxiii~+~373.
Rome, 1919.

\BibItem[Catalan, E.] ``Solution d'un problème de probabilité, relatif au jeu de
rencontre.'' Journ. Liouville, vol.~ii., 1837.

\BibItem[\bysame] ``Deux problèmes de probabilités.'' Journ.\ Liouville, vol.~vi.

\BibItem[\bysame] Problèmes et théorèmes de probabilités. 4to. 1884.

\BibItem[Cauchy.] Sur le système de valeurs qu'il faut attribuer à divers éléments
déterminés par un grand nombre d'observations. 4to. Paris, 1814.

\BibItem[Cayley, A.] ``On a Question in the Theory of Probabilities.'' Phil.\ Mag., 1853.

\BibItem[Cesàro, E.] ``Considerazioni sul concetto di probabilità.'' Periodico di
Matematica,~vi., 1891.

\BibItem[Charlier, C.~V.~L.] Researches into the Theory of Probability. Publ.\ in
Engl.\ in Meddelanden from Lund's Astronom. Observatorium, Series~ii.,
No.~24. 4to. 51~pp. Lund, 1906.

\BibItem[\bysame] ``Contributions to the Mathematical Theory of Statistics,'' Arkiv för
matematik, astronomi och fysik, vols.\ 7,~8,~9,~\textit{passim}.

\BibItem[\bysame] Vorlesungen über die Grandzüge der mathematischen Statistik. Sm.\
4to. Pp.~125. Lund, 1920.
\end{Biblio}
%% -----File: 450.png---Folio 439-------
\begin{Biblio}

\BibItem[Charpentier, T.~V.] ``Sur la nécessité d'instituer la logique du probable.''
Comptes rendus de l'Acad.\ des Sciences morales, vol.~i.\ p.~103, 1875.

\BibItem[\bysame] ``La Logique du probable.'' Rev.\ phil.\ vol.~vi.\ pp.~23--38, 146--163, 1878.

\BibItem[Chrystal, G.] On some Fundamental Principles in the Theory of Probability.
London, 1891.

\BibItem[Clark, Samuel.] The Laws of Chance: or a Mathematical Investigation of
the Probability arising from any proposed Circumstance of Play, etc.
Pp.~ii~+~204, 1758.

\BibItem[Cohen, J.] Chance: A Comparison of 4~Facts with the Theory of Probabilities.
Pp.~47. London, 1905.

\BibItem[Condorcet, Marquis de.] Essai sur l'application de l'analyse à la probabilité
des décisions rendues à la pluralité des voix. 4to. Pp.~cxci~+~304.
Paris, 1785. Another edition, 1804.

\BibItem[\bysame] ``Sur les événements futurs.'' Acad.\ des Sc., 1803.

\BibItem[\bysame] Memoir on Probabilities in six parts:

\BibItem[\bysame] 1. ``Réflexions sur la règle générale qui prescrit de prendre pour valeur
d'un événement incertain la probabilité de cet événement, multipliée par
la valeur de l'événement en lui-même.'' Hist.\ de l'Acad.\ pp.~707--728.
Paris, 1781.

\BibItem[\bysame] 2. ``Application de l'analyse à cette question: Déterminer la probabilité
qu'un arrangement régulier est l'effet d'une intention de le produire.''
Hist.\ de l'Acad., Paris, 1781. With Part~i.

\BibItem[\bysame] 3. Sur l'évaluation des droits éventuels. 1782, pp.~674--691.

\BibItem[\bysame] 4. Réflexions sur la méthode de déterminer la probabilité des événements
futurs, d'après l'observation des événements passés. 1783, pp.~539--559.

\BibItem[\bysame] 5. Sur la probabilité des faits extraordinaires. 1783, with Part~4.

\BibItem[\bysame] 6. Application des principes de l'article précédent à quelques questions
de critique. 1784, pp.~454--468.

\BibItem[Coover, J.] Experiments in Psychical Research at Leland Stanford Junior
University. Pp.~641. Stanford University, California, 1917.

\Bibnote [See Psychical Research and Statistical Method by F.~Y. Edgeworth,
Stat.\ JL., vol.~lxxxii. (1919), p.~222.]

\BibItem[Corbaux, F.] Essais métaphysiques et mathématiques sur le hasard. 8vo.
Paris, 1812.

\BibItem[Costa.] Probabilité du tir. 8vo. Paris, 1825.

\BibItem[\bysame] ``Question de probabilité applicable aux décisions rendues par les
jurés.'' Liouv.\ J.~(1), vii., 1842.

\BibItem[Courcy, Alph.\ de.] Essai sur les lois du hasard suivi d'étendus sur les assurances.
8vo. Paris, 1862.

\BibItem[Cournot, A.] Revue de Métaphysique et de Morale, May 1905. Numéro
spécialement consacré à Cournot. See especially:

\BibItem[\bysame] F. Faure: ``Les Idées de Cournot sur la statistique,'' pp.~395--411.

\BibItem[\bysame] D. Parodi: ``Le Criticisme de Cournot,'' pp.~451--484.

\BibItem[\bysame]
F. Mentré: ``Les Racines historiques du probabilisme rationnel de
Cournot,'' pp.~485--508.

\BibItem[\bysame]
Art.\ ``Probabilités.'' Dictionnaire de Franck.

\BibItem[\bysame]
``Sur la probabilité des jugements et la statistique.'' Journal de Liouville,
t.~iii p.~257.

\BibItem[\bysame] ``Mémoire sur les applications du calcul des chances à la statistique
judiciaire.'' Liouv.\ J.~(1) iii., 1838.

\BibItem[\bysame]
Exposition de la théorie des chances et des probabilités. Pp.~viii~+~448.
Paris, 1843.

\BibItem[\bysame]
German translation by C.~H. Schnuse. 8vo. Braunschweig, 1849.

\BibItem[Couturat, L.] La Logique de Leibniz d'après des documents inédits.
Pp~xiv.~+~608. Paris, 1901.
%% -----File: 451.png---Folio 440-------

%\BibItem[Couturat, L.]---\emph{continued}.

\Bibnote [See especially chap.~vi.\ for references to Leibniz's views on Probability.]

\BibItem[\bysame] Opuscules et fragments inédits de Leibniz. Paris, 1903.

\BibItem[Craig.] Theologiae Christianae principia mathematica. 4to. London, 1699.
Reprinted Leipzig, 1755.

\BibItem[[Craig] (?).]  ``A Calculation of the Credibility of Human Testimony.'' Phil.\
Trans.\ vol.~xxi.\ pp.~359--365, 1699.

\Bibnote [Also attributed to \textsc{Halley}.]

\BibItem[Crakanthorpe, R.] Logica. 1st~ed.\ London, 1622. 2nd~ed.\ London, 1641
(auctior et emendatior). 3rd~ed.\ Oxon., 1677.

\Bibnote [Book~v.\ ``De syllogismo probabili.'']

\BibItem[Crofton, M.~W.] ``On the Theory of Local Probability, applied to Straight
Lines drawn at random in a Plane.'' Phil.\ Trans.\ vol.~158, pp.~181--199,
1869.

\Bibnote [Summarised in Proc.\ Lond.\ Math.\ Soc.\ vol.~2, pp.~55--57, 1868.]

\BibItem[\bysame] ``Probability.''  Encycl.\ Brit.\ 9th~\ ed., 1885.

\BibItem[\bysame] ``Geometrical Theorems relating to Mean Values.'' Proc.\ Lond.\ Math.\
Soc.\ vol.~8, pp.~304--309, 1877.

\BibItem[Czuber, E.] Zum Gesetz der grossen Zahlen. Prag, 1889.

\BibItem[\bysame] Geometrische Wahrscheinlichkeiten und Mittelwerte. Pp.~vii~+~244.
Leipzig, 1884.

\BibItem[\bysame] Theorie der Beobachtungsfehler. Pp.~xiv~+~418. Leipzig, 1891.

\BibItem[\bysame] Die Entwicklung der Wahrscheinlichkeitstheorie und ihrer Anwendungen.
Pp.~viii~+~279. Leipzig, 1899.

\BibItem[\bysame] Wahrscheinlichkeitsrechnung und ihre Anwendung auf Fehlerausgleichung,
Statistik und Lebensversicherung. Leipzig, 1903.

\BibItem[\bysame] Ditto. 2~vols, 8vo. \DPtypo{}{pp.}~x~+~410~+~x~+~470. Leipzig, 1908--10. Second
edition, revised and enlarged. Vol.~i. Warscheinlichkeitstheorie, Fehlerausgleichung,
Kollektivmasslehre, 1908. Vol.~ii. Mathematische
Statistik, mathematische Grundlagen der Lebensversicherung, 1910.

\Bibsect{D}

%[** TN: Not exactly matching original indentation of these items.]
\BibItem[D'Alembert.] Opuscules mathématiques: Paris, 1761--1780.

\BibItem[\bysame] [Réflexions sur le calcul des probabilités, ii.\ pp.~1--25, 1761. \\
Sur l'application du c.~des~p.\ à l'inoculation, ii.\ pp.~26--95. \\
Sur le calcul des probabilités, etc., iv.\ pp.~73--105; iv.\ pp.~283--341;
v.\ pp.~228--231; v.\ pp.~508--510; vii.\ pp.~39--60.]

\BibItem[\bysame] Mélanges de littérature, d'histoire et de philosophie. Amsterdam, 1770.

\BibItem[\bysame] [Doutes et questions sur le calcul des probabilités, vol.~v.\ pp.~223--246. \\
Réflexions sur l'inoculation. Vol.~v. (These two papers were reprinted
in the first volume of D'Alembert's collected works published at Paris in
1821 (pp.~451--514).)]

\BibItem[\bysame] Articles in Encyclopédie ou Dictionnaire raisonné:

\BibItem[\bysame] ``Croix ou Pile,'' 1754.

\BibItem[\bysame] ``Gageure,'' 1757.

\BibItem[\bysame] Article in Encyclopédie méthodique: ``Cartes.''

\BibItem[D'Anières.] ``Réflexions sur les jeux de hasard.'' Mém.\ de l'Acad.\ pp.~391--398.
Berlin, 1784.

\BibItem[Dantec, Félix le.] ``Le Hasard et la question d'échelle.'' Revue du Mois,
vol.~4, pp.~257--288, 1907.

\BibItem[\bysame] Le Chaos et l'harmonie universelle. Paris, 1911.

\BibItem[Darbyshire, A.~D.] Some Talks illustrating Statistical Correlation. (Reprinted
from Memoirs of the Manchester literary and Philosophical Society.)
21~pp.\ and plates. 8vo. 1907.

\BibItem[Darbon, A.] Le Concept du hasard dans la philosophie de Cournot. Étude
critique. Pp.~60. Paris, 1911.

\BibItem[Davenport, C.~B.] Statistical Methods. 1904.
%% -----File: 452.png---Folio 441-------

\BibItem[De Moivre, A.] ``De mensura sortis, seu, de probabilitate eventuum in ludis
a casu fortuito pendentibus.'' Phil.\ Trans.\ vol.~xxvii.\ pp.~213--264, 1711.

\BibItem[\bysame] Doctrine of Chances, or A Method of Calculating the Probabilities of
Events in Play. 1st~ed. 4to. Pp.~xiv~+~175. 1718. 2nd~ed. Large
4to. Pp.~xiv~+~258. 1738. 3rd~ed. Large 4to. Pp.~xii~+~348. 1756.

\BibItem[\bysame] La dottrina d.~azzardi applic.\ ai problemi d.~probabilità di vita, di pensi,
ecc., trad.\ da R.~Gaeta e G.~Fontana. Milan, 1776.

\BibItem[\bysame] Miscellanea analytica de seriebus et quadraturis. 4to. Pp.~250~+~22.
London, 1730.

\BibItem[De Morgan, A.] Essay on Probabilities and their Application to life Contingencies
and Insurance Offices. 1838.

\BibItem[\bysame] Formal Logic: or the Calculus of Inference Necessary and Probable.
1847.

\BibItem[\bysame] Theory of Probabilities. 4to. 1849.

\Bibnote [From the Encyclopaedia Metropolitana.]

\BibItem[\bysame] On the Structure of the Syllogism and on the Application of the Theory
of Probabilities to Questions of Argument and Authority. 4to. Camb.\
Phil.\ Soc.\ pp.~393--405, 1847 (read Nov.~9, 1846).

\BibItem[\bysame] On the Symbols of Logic, the Theory of the Syllogism, and in particular
of the Copula, and the Application of the Theory of Probabilities to some
Questions of Evidence. 4to. Camb.\ Phil.\ Soc.\ vol.~ix.\ pp.~116--125, 1851.

\BibItem[De Witt, John.] De vardye van de lif-renten na proportie van de los-renten.
La\ Haye, 1671.

\BibItem[\bysame] English transl.: Contributions to the History of Insurance, by Frederick
Hendriks in the Assurance Magazine, vol.~2, p.~231 (1852).

\BibItem[\bysame] [For an abstract see N.~Struyck, Inleiding tot het algemeine geography,
etc. 4to. Amsterdam, 1740. P.~345.]

\BibItem[Dedekind, R.] Bemerkungen zu einer Aufgabe der Wahrscheinlichkeitsrechnung.
Pp.~268--271. Crelle~J.\ vol.~1., 1855.

\BibItem[Degen, C.~F.] Tabularum ad faciliorem probabilitatis computationem utilem
Enneas. Kiobenhavn, 1824.

\BibItem[Diderot.] Art.\ ``Probabilité'' in the Encyclopédie.

\BibItem[Didion, J.] Calcul des probabilités appliqué au tir des projectiles. 8vo. 1858.

\BibItem[Dodson, James.] Mathematical Repository. 3~vols. 1753. Vol.~ii.\ pp.~82--136.

\BibItem[Donkin, W.~F.] ``Sur la théorie de la combinaison des observations.'' Liouv.\ J.~(1),
vol.~xv. 1850.

\BibItem[\bysame] ``On Certain Questions relating to the Theory of Probabilities.'' Phil.\
Mag., May 1851.

\BibItem[Dormoy, E.] Théorie mathématique des assurances sur la vie. 2~vols. Paris,
1878.

\BibItem[Drobisch, A.] ``Über die nach der Wahrscheinlichkeitsrechnung zu erwartende
Dauer der Ehen.'' Berichte über die Verhandlungen der Königl.\ Sächsischen
Gesellschaft der Wissenschaften mathem.-physik. 1880.

\BibItem[Drobisch, M.~W.] Neue Darstellung der Logik. 2nd~ed.\ Leipzig, 1851. 3rd~ed.\
1863. 4th~ed.\ 1875. 5th~ed.\ 1887.

\Bibnote [Probability, pp.~181--209, §§\;145--157 (references to 4th~ed).]

\Bibsect{E}

\BibItem[Edgeworth, F.~Y.] ``Calculus of Probability applied to Psychical Research.''
Proceedings of Soc.\ for Psych.\ Res. Parts viii.~and~x.

\BibItem[\bysame] `` On the Method of ascertaining a Change in the Value of Gold.'' Roy.\
Stat.\ Soc.\ J.~xlvi.\ pp.~714--718. 1883.

\BibItem[\bysame] ``Law of Error.'' Phil.\ Mag.~(5) vol.~xvi.\ pp.~300--309, 1883.

\BibItem[\bysame] ``Method of least Squares.'' Phil.\ Mag.~(5) vol.~xvi.\ pp.~360--375, 1883.

\BibItem[\bysame] ``Physical Basis of Probability.'' Phil.\ Mag.\ vol.~xvi.\ pp.~433--435,
1883.
%% -----File: 453.png---Folio 442-------

%\BibItem[Edgeworth, F.\ Y.]---\emph{continued}.

\BibItem[\bysame] `` Chance and Law.'' Hermathene (Dublin), 1884.

\BibItem[\bysame] ``On the Reduction of Observations.'' Phil.\ Mag.~(5) vol.~xvii.\ pp.~135--141,
1884.

\BibItem[\bysame] ``Philosophy of Chance.'' Mind, April 1884.

\BibItem[\bysame] ``\textit{A~priori} Probabilities.'' Phil.\ Mag.~(5) vol.~xviii.\ pp.~209--210, 1884.

\BibItem[\bysame] ``On Methods of Statistics.'' Stat.\ Journ.\ Jub.~vol.\ pp.~181--217, 1885.

\Bibnote [Criticised by Bortkiewicz and defended by Edgeworth, Jahrb.\ f.~nat.\
Ök.\ u.~Stat.~(3), vol.~10, pp.~343--347; vol.~11, pp.~274--277, 701--705,
1896.]

\BibItem[\bysame] `` Observations and Statistics.'' Phil.\ Soc. 1885.

\BibItem[\bysame] ``Law of Error and Elimination of Chance.'' Phil.\ Mag., 1886, vol.~xxi.\ pp.~308--324.

\BibItem[\bysame] ``Problems in Probabilities.'' Phil.\ Mag., 1886, vol.~xxii.\ pp.~371--384,
and 1890, vol.~xxx.\ pp.~171--188.

\BibItem[\bysame] Metretike: or the Method of Measuring Probability and Utility. 8vo.
1887.

\BibItem[\bysame] ``On Discordant Observations.'' Phil.\ Mag.~(5) vol.~xxiii.\ pp.~\DPtypo{}{364--375,} 1887. %[** TN: Page numbers found in google excert of http://www.jstor.org/pss/2335027 on April 24, 2010]

\BibItem[\bysame] ``The Empirical Proof of the Law of Error.'' Phil.\ Mag.~(5) vol.~xxiv.\
pp.~330--342, 1887.

\BibItem[\bysame] ``The Element of Chance in Competitive Examinations.'' Roy.\ Stat.\
Soc.\ Journ.~liii.\ pp.~460--475 and 644--663, 1890.

\BibItem[\bysame] ``The Law of Error and Correlated Averages.'' Phil.\ Mag.~(5) vol.~xxxv.\
pp.~63--64, 1893.

\BibItem[\bysame] ``Statistical Correlation between Social Phenomena.'' Roy.\ Stat.\ Soc.\
Journ.~lvi.\ pp.~670--675, 1893.

\BibItem[\bysame] ``The Asymmetrical Probability-Curve.'' 1896. Phil.\ Mag.\ vol~xli.\
pp.~90--99.

\BibItem[\bysame] ``Miscellaneous Applications of the Calculus of Probabilities.'' Roy.\
Stat.\ Soc. Journ.~lx.\ pp.~681--698, 1897; lxi.\ pp.~119--131 and 534--544,
1898.

\BibItem[\bysame] ``Law of Error.'' Phil.\ Trans.\ vol.~xx.

\BibItem[\bysame] ``The Generalised Law of Error.'' Stat.\ Journ.\ vol.~lxix., 1906.

\BibItem[\bysame] ``On the Probable Errors of Frequency-Constants.'' Stat.\ Journ.\ vol.~lxxi.\
pp.~381--397, 499--512, 651--678, 1908; and vol.~lxxii.\ pp.~81--90, 1909.

\BibItem[\bysame] ``On the Application of the Calculus of Probabilities to Statistics.''
Bulletin xviii.\ of the International Statistical Institute, Paris, 1910, 32~pp.

\BibItem[\bysame] ``Applications of Probabilities to Economics.'' Economic Journal, vol.~xx.\
pp.~284--304, 441--465, 1910.

\BibItem[\bysame] ``Probability.'' Encyclopaedia Britannica, 11th~ed.\ vol.~22, pp.~376--403,
1911.

\BibItem[\bysame] ``On the Application of Probabilities to the Movement of Gas-Molecules.''
Phil.\ Mag., vol.~xl., pp.~249--272, 1920.

\BibItem[\bysame] Molecular Statistics.'' Roy.\ Stat.\ Soc.\ Journ., vol.~lxxxiv.\ pp.~71--89,
1921.

\BibItem[Eggenberger, J.] ``Beiträge zur Darstellung des bernoullischen Theorems.''
Berner Mitth.\ vol.~50 (1894); and Zeitschr.\ f.~Math.\ u.~Ph.~45 (1900), p.~43.

\BibItem[Elderton, W.~P.] Frequency-Curves and Correlation. 8vo. London, 1907.
xii~+~172.

\Bibnote [Contains a useful list of papers on Correlation, p.~163.]

\BibItem[Ellis, R.~L.] ``On the Foundations of the Theory of Probability.'' 4to.
Camb.\ Phil.\ Soc.\ vol.~viii., 1843.

\Bibnote [Reprinted in ``Mathematical and other Writings,'' 1863.]

\BibItem[\bysame]
``On a Question in the Theory of Probabilities.'' Camb.\ Math.\ Journ.\
No.~xxi.\ vol~iv., 1844.

\Bibnote [Reprinted in ``Mathematical and other Writings,'' 1863.]
%% -----File: 454.png---Folio 443-------

%\BibItem[ Ellis, R.~L.]---\emph{continued}.

\BibItem[\bysame] ``On the Method of Least Squares.'' Trans.\ Camb.\ Phil.\ Soc.\ vol.~viii.,
1844.

\Bibnote [Reprinted in ``Mathematical and other Writings,'' 1863.]

\BibItem[\bysame] ``Remarks on an alleged Proof of the `Method of Least Squares.'\,''
Phil.\ Mag.~(3) vol.~xxxvii., 1850.

\Bibnote [Reprinted in ``Mathematical and other Writings,'' 1863.]

\BibItem[\bysame] ``Remarks on the Fundamental Principle of the Theory of Probabilities.''
Trans.\ Camb.\ Phil.\ Soc.\ vol.~ix., 1854.

\Bibnote [Reprinted in ``Mathematical and other Writings,'' 1863.]

\BibItem[Elsas, A.] ``Kritische Betrachtungen über die Wahrscheinlichkeitsrechnung.''
Philos.\ Monatssch.\ vol.~xxv.\ pp.~557--584, 1889.

\BibItem[Emerson, William.] Miscellanies, 1776. [See espec.\ pp.~1--48.]

\BibItem[Encke, J.~F.] Methode der kleinsten Quadrate. Fehler theoret.\ Untersuchungen.
Berlin, 1888.

\BibItem[Engel, G.] ``Über Möglichkeit und Wirklichkeit.'' Philos.\ Monatssch.\ vol.~v.\
pp.~241--271, 1875.

\BibItem[Ermakoff, W.~P.] Wahrscheinlichkeitslehre (in Russian).

\BibItem[Euler.] ``Calcul de la probabilité dans le jeu de rencontre.'' Hist.\ Ac.\ Berl.\
(1751), pp.~255--270, 1753.

\BibItem[\bysame] ``Sur l'avantage du banquier au jeu de pharaon.'' Hist.\ Ac.\ Berl.\
(1764), pp.~144--164, 1766.

\BibItem[\bysame] ``Sur la probabilité des séquences dans la loterie génoise.'' Hist.\ Ac.\
Berl.\ (1765), pp.~191--230, 1767.

\BibItem[\bysame]
``Solution d'une question très difficile dans le calcul des probabilités.''
Hist.\ Ac.\ Berl.\ (1769), pp.~285--302, 1771.

\BibItem[\bysame] ``Solutio quarundam quaestionum difficiliorum in calculo probabilium.''
Opuscula analytica, vol.~ii.\ pp.~331--346, 1785.

\BibItem[\bysame] ``Solutio quaestionis ad calculum probabilitatis pertinentis: Quantum
duo conjuges persolvere debeant, ut suis haeredibus post utriusque mortem
certa argenti summa persolvatur.'' Opuscula analytica, vol.~ii, pp.~315--330,
1785.

\BibItem[\bysame] ``Wahrscheinlichkeitsrechnung.'' Opera omnia, ser.~1,~A, vol.~iv.\
Leipzig.

\Bibsect{F}

\BibItem[Fahlbeck.] ``La Régularité dans les choses humaines, ou les types statistiques
et leurs variations.'' Journ.\ Soc.\ Stat.\ de Paris, pp.~188--200, 1900.

\BibItem[Fechner, G.~Th.] Kollektivmasslehre. (Edited by G.~F. Lipps.) 1897.

\BibItem[Fick, A.] Philosophischer Versuch über die Wahrscheinlichkeiten. Pp.~46.
Würzburg, 1883.

\BibItem[Fisher, A.] The Mathematical Theory of Probabilities. Translated from the
Danish. Pp.~xx~+~171 New York, 1915.

\BibItem[Forbes, J.~D.] ``On the alleged Evidence for a Physical Connexion between
Stars forming Binary or Multiple Groups, deduced from the Doctrine of
Chances.'' Phil.\ Mag., Dec.\ 1850. (See also Phil.\ Mag., Aug.\ 1849.)

\BibItem[Forncey.] The Logic of Probabilities. Transl.\ from the French. 8vo.
London, n.d.~(?~1760.)

\BibItem[Förster, W.] Wahrheit und Wahrscheinlichkeit. Pp.~40. Berlin, 1875.

\BibItem[Fries, J.~J.] Versuch einer Kritik der Principien der Wahrscheinlichkeitsrechnung.
Braunschweig, 1842.

\BibItem[Frömmichen.] Über Lehre der Wahrscheinlichkeit. 4to. Braunschweig,
1773.

\BibItem[Fuss, N.] ``Recherches sur un problème du calcul des probabilités.'' Act.\ Ac.\
Petr.\ (1779), pars posterior, pp.~81--92, 1783.

\BibItem[\bysame] ``Supplément au mémoire sur un problème du calcul des probabilités.''
Act.\ Ac.\ Petr.\ (1780), pars posterior, pp.~91--96, 1784.
%% -----File: 455.png---Folio 444-------

\Bibsect{G}

\BibItem[Galileo, G.] ``Considerazioni sopra il giuoci dei dadi.'' Opere, vol.~iii.\ pp.~119--121,
1718. Also, Opere, vol.~xiv.\ pp.~293--296. Firenze, 1855.

\BibItem[\bysame] ``Lettere intorno le stima di un cavallo.'' Opere, vol.~xiv.\ pp.~231--284.
Firenze, 1855.

\BibItem[Galloway, T.]  A Treatise on Probability. 8vo. Edinburgh, 1839. (From
the 7th~edition of the Encyclopaedia Britannica.)

\BibItem[Galton, F.] ``Correlations and their Measurement.'' Proc.\ Roy.\ Soc., vol.~xlv.\
pp.~136--145.

\BibItem[\bysame] Probability, the Foundation of Eugenics. Herbert Spencer Lecture,
1907. (Reprinted---Essays in Eugenics. 8vo. ii~+~109~pp. London, 1909.)

\BibItem[Gardon, C.] Antipathies des 90~nombres, probabilités, et observations comparatives,
sur les loteries de France et de Bruxelles. 8vo. Paris, 1801.

\BibItem[\bysame] Traité élémentaire des probabilités, etc. Paris, 1805.

\BibItem[\bysame] L'investigateur des chances \ldots\ pour obtenir souvent des succès aux
loteries impériales de France. Paris.

\BibItem[Garve, C.] De nonnullis quae pertinent ad logicam probabilium. 4to. Halae,
1766.

\BibItem[Gataker, T.] On the Nature and Use of Lots. 4to. 1619.

\BibItem[Gauss, C. F.] Theoria motus corporum coelestium. 4to. Hamburg, 1809.

\BibItem[\bysame] ``Theoria combinationis observationum erroribus minimis obnoxiae.''
Comm.\ Soc.\ Göttingen, vol.~v.\ pp.~33--90. 1823.

\BibItem[\bysame] Méthode des moindres carrés. Traduit en français par J.~Bertrand.
8vo. 1855.

\Bibnote [A translation of part of the above.]

\BibItem[\bysame] Wahrscheinlichkeitsrechnung. Werke, vol.~iv.\ pp.~1--53. 4to. Göttingen,
1873.

\BibItem[Geisenheimer, L.] Über Wahrscheinlichkeitsrechnung. 8vo. Berlin, 1880.

\BibItem[Gilman, B.~I.] ``Operations in Relative Number with Applications to Theory of
Probability,'' Johns Hopkins Studies in Logic, 1883.

\BibItem[Gladstone, W.~E.] ``Probability as a Guide to Conduct.'' Nineteenth Cent.\
vol.~v.\ pp.~908--934, 1879; and in ``Gleanings,'' vol.~ii.\ pp.~153--200.

\BibItem[Glaisher, J.~W.~L.] ``On the Rejection of Discordant Observations.'' Monthly
Notices R.~Astr.~S. vol.~xxiii., 1873.

\BibItem[\bysame] ``On the Law of Facility of Errors of Observation, and on the Method
of Least Squares.'' Mem.\ R.~Astr.~S. vol.~xxxix., 1872.

\BibItem[Goldschmidt, L.] ``Wahrscheinlichkeit und Versicherung.'' Bull.\ du Comité
permanent des Congrès Internationaux d'Actuaires, 1897.

\BibItem[\bysame] Die Wahrscheinlichkeitsrechnung: Versuch einer Kritik. Pp.~279.
Hamb., 1897.

\Bibnote [Cf.\ Zeitschr.\ f.~Philos.\ u.~phil.~Kr., cxiv., pp.~116--119.]

\BibItem[Gonzalez, T.] Fundamentum theologiae moralis, id est tractatus theologicus
de recto usu opinionum probabilium. 4to. Dillingen, 1689. Naples, 1694.

\Bibnote [An abridgement entitled: Synopsis tract.\ theol.\ de recto usu opin.\
prob., concinnata a theologo quodam Soc.\ Jesu: cui accessit logistica
probabilitatum. 3rd~ed. 8vo. Venice, 1696. See Migne, Theol.\ Cur.\
Compl., vol.~xi., p.~1397.]

\BibItem[Gourand, Ch.] Histoire du calcul des probabilités depuis ses origines jusqu'à
nos jours. 8vo. Paris, 1848, 148~pp.

\Bibnote [His history seems to be a portion of a very extensive essay in 3~folio
volumes containing 1929~pp., written when he was very young, in competition
for a prize proposed by the Fr.\ Acad.\ on a subject entitled ``Théorie
de la certitude''; see Séances et Travaux de l'Académie des Sciences
morales et politiques, vol.~x.\ pp.~372,~382, vol.~xi.\ p.~137. See \textsc{Todhunter}.]

\BibItem[Gravesande, W.~J.~'S.] Introductio ad philosophiam, metaphysicam et logicam
continens. 8vo. Venetiis, 1737.
%% -----File: 456.png---Folio 445-------

% \BibItem[Gravesande, W.~J.~'S]---\emph{continued}.

\BibItem[\bysame] {\OE}uvres philosophiques et mathématiques. 4to. Amsterdam, 1774,
2~vols. 4to. ii.\ pp.~82--93, 221--248.

\BibItem[Grellings, K.] ``Die philosophischen Grundlagen der Wahrscheinlichkeitsrechnung.''
Abhandlungen der Friesschen Schule, N.~F., vol.~iii., 1910.

\BibItem[Grimsehl, E.] ``Untersuchungen zur Wahrscheinlichkeitslehre. (Mit besonderer
Beziehung auf Marbes Schrift (\textit{q.v.}).)'' ``Zeitschrift für Philosophie und
philosophische Kritik. Band~118, pp.~154--167. Leipzig, 1901.

\Bibnote [See also \textsc{Brömse, Marbe}, and \textsc{v.~Bortkiewicz}.]

\BibItem[Grolous] ``Sur une question de probabilité appliquée à la théorie des
nombres.'' Journal de l'Institut, 1872.

\BibItem[Groschius, J.~A.]  Logica probabilium in artium practicarum subsidium
adornata. Sm.\ 8vo. Halae, 1764. Pp.~xvi~+~352.

\BibItem[Grünbaum, H.] Isolierte und reine Gruppen und die Marbesche Zahl~``$p$.''
Würzburg, 1904.

\BibItem[Guibert, A.] ``Solution d'une question relative à la probabilité des jugements
rendus à une majorité quelconque.'' Liouv.\ J.~(1) vol.~iii., 1838.

\Bibsect{H}

\BibItem[Hack.] Wahrscheinlichkeitsrechnung. Leipzig, 1911.

\BibItem[Hagen, G.~F.] Meditationes philosophicae de methodo mathematico. Norimbergae,
1734.

\BibItem[\bysame] Fortsetzung einiger aus der Mathematic abgenommenen Regeln, nach
welchen sich der menschliche Verstand bei Erfindung der Wahrheiten
richtet. Halle, 1737.

\BibItem[Hagen, G.] Grundzüge der Wahrscheinlichkeitsrechnung. Berlin, 1837.
(2nd~ed.\ 1867, 3rd~ed.\ 1882.)

\BibItem[\bysame] Der constante wahrscheinliche Fehler: Nachtrag zur 3ten Auflage der
Grundzüge der Wahrscheinlichkeitsrechnung. 38~pp. Berlin, 1884.

\BibItem[Halley.] See \textsc{Craig}.

\BibItem[Hans, John.] See \textsc{J.~Arbuthnot}.

\BibItem[Hansdorff, F.] ``Beiträge zur Wahrscheinlichkeitsrechnung.'' Leipz.\ Ber.,
vol.~53, pp.~152--178, 1901.

\BibItem[\bysame] ``Das Risiko bei Zufallsspielen.'' Leipz.\ Ber., vol~49, pp.~497--548, 1897.

\BibItem[Hansen, P.~A.] ``Über die Anwendung der Wahrscheinlichtkeitsrechnung auf
geodätische Vermessungen.'' Astr.~N. vol.~ix.\ 1831.

\BibItem[Hartmann, E.~von.]\DPnote{** TN: "von" not small-capped in orig} ``Die Grundlage der Wahrscheinlichkeitsurteils.''
Vierteljahrsschr.\ f.~wiss.\ Phil.\ u.~Soz., vol.~xxviii., 1904.

\BibItem[Hauteserve, Gauthier~d'.] Traité élémentaire sur les probabilités. Paris,
1834.

\BibItem[\bysame] Application de l'algèbre élémentaire au calcul des probabilités. Paris,
1840.

\BibItem[Hélie] Mémoire sur la probabilité du tir. 8vo. 1854.

\BibItem[Helm.] ``Eine Anwendung der Theorie des Tauschwerthes auf die Wahrscheinlichtkeitsrechnung.''
Zeitschr.\ f.~Math.\ u.~Phys., vol.~38, pp.~374--376.
Leipzig, 1893.

\BibItem[\bysame] ``Die Wahrscheinlichkeitslehre als Theorie der Kollektiv-begriffe.''
Annalen der Naturphilosophie, vol.~1.

\BibItem[Henry, Charles.] La Loi des petits nombres. Recherches sur le sens de
l'écart probable dans les chances simples à la roulette, au trente-et-quarante
etc., en général dans les phénomènes dépendant de causes purement
accidentales. 72~pp. 8vo. Paris, 1908.

\BibItem[Herschel, W.]  ``On the Theory of Probabilities.'' Journal of Actuaries,
1869.

\BibItem[\bysame] ``Quetelet on Probabilities.'' Edin.\ Rev., 1850.

\Bibnote [Reprinted in Quetelet's Physique Sociale, vol.~i.\ pp.~1--89, 1869.]

\BibItem[\bysame] ``On an Application of the Rule of Succession.'' Edin.\ Rev., 1850.
%% -----File: 457.png---Folio 446-------

\BibItem[Herz, N.] Wahrscheinlichkeits- und Ausgleichungsrechnung. Pp.~iv~+~381.
Leipzig, 1900.

\BibItem[Hibben, J.~G.] Inductive Logic. London, 1896.

\Bibnote [See chaps.\ xv.,~xvi.]

\BibItem[Hobhouse, L.~T.] Theory of Knowledge.

\Bibnote [See Part~II., chaps.\ x.,~xi.]

\BibItem[Hoyle.] An Essay towards making the Doctrine of Chances easy to those who
understand vulgar Arithmetic only. Pp.~viii~+~73, 1754, 1758, 1764.

\BibItem[Huberdt, A.] Die Principien der Wahrscheinlichkeitsrechnung. 4to. Berlin,
1845.

\BibItem[Hume, David.] Treatise on Human Nature. 1st~ed.\ 1739.

\Bibnote [See especially Part~III.]

\BibItem[\bysame] An Enquiry concerning Human Understanding.

\Bibnote [See specially Section~vi.]

\BibItem[\bysame] Essays, Part~I.,~XIV\@. On the Rise and Progress of the Arts and Sciences,
 pp.~115,~116, 1742.

\BibItem[Huygens, Ch.] ``De ratiociniis in ludo aleae.'' Schooten's Exercitat.\ math.\
pp.~519--534. 4to. Lugd.\ Bat., 1657.

\Bibnote [Written by Huygens in Dutch and translated into Latin by Schooten.]

\BibItem[\bysame] Engl.\ transl.\ by W.~Browne. Sm.\ 8vo, pp.~24. London, 1714.

\Bibnote [See also \textsc{Jac.\ Bernoulli, Arbuthnot} (Engl.\ Transl.), and \textsc{Vastel} (Fr.\ Transl.).]

\Bibsect{J}

\BibItem[Jahn, G.~A.] Die Wahrscheinlichkeitsrechnung und ihre Anwendung auf das
wissenschaftliche und praktische Leben. Leipzig, 1839.

\BibItem[Janet.] La Morale. Paris, 1874. [See Bk.~iii.\ chap.~3 for Probabilism.]
Engl.\ transl. The Theory of Morals. New York, 1883, pp.~292--308.

\BibItem[Jevons, W.~S.] Principles of Science, 2~vols. 1874.

\BibItem[Jordan, C.] ``De quelques formules de probabilité (sur les causes).'' Comptes
rendus, 1867.

\BibItem[Jourdain, P.~E.~B.] ``Causality, Induction, and Probability.'' Mind, vol.~xxviii.\
pp.~162--179, 1919.

\Bibsect{K}

\BibItem[Kahle, L.~M.] Elementa logicae probabilium methodo mathematica, in usu
scientiarum et vitae adornata. Pp.~10~+~xxii~+~245. Sm.\ 8vo. Halae,
1735.

\BibItem[Kanner, M.] ``Allgemeine Probleme der Wahrscheinlichkeitsrechnung und ihre
Anwendung auf Fragen der Statistik.'' Journ.\ des Collegiums für Lebens-Versicherungs-Wissenschaft.
Berlin, 1870.

\BibItem[Kaufmann, Al.] Theorie und Methoden der Statistik. [Translated from the
Russian.] Pp.~xii~+~540. Tübingen, 1913.

\BibItem[Kepler, J.] ``De stella nova in pede serpentarii.'' 1606. See J.~Kepler's
Astr.\ Op.\ Omn.\ edidit Frisch, ii.\ pp.~714--716.

\BibItem[Kirchmann, J.~H.~von.] Über die Wahrscheinlichkeit. Pp.~60. Leipzig,
1878.

\BibItem[Knapp.] ``Quetelet als Theoretiker.'' Jahrb.\ f.~nat. Ök.\ und~Stat. (New Series),
vol.~xviii.

\BibItem[Kozak, Josef.] Grundlehren der Wahrscheinlichkeitsrechnung als Vorstufe für
das Studium der Fehlerausgleichung, Schiesstheorie, und Statistik. Vienna, 1912.

\BibItem[\bysame] Theorie des Schiesswesens auf Grundlage der Wahrscheinlichkeitsrechnung
und Fehlertheorie. Vienna, 1908.

\BibItem[Kries, J.~von.] Die Principien der Wahrscheinlichkeitsrechnung. Eine
logische Untersuchung. Pp.~298. 8vo. Freiburg, 1886.

\Bibnote [See also \textsc{Lexis, Meinong} and \textsc{Sigwart}.]
%% -----File: 458.png---Folio 447-------

\Bibsect{L}

\BibItem[Lacroix, S.~F.] Traite élémentaire du calcul des probabilités. Pp.~viii~+~299.
8vo. Paris, 1816.

\Bibnote [2nde~éd., revue et augmentée, 1822; 4th~éd.\ 1864.]

\Bibnote [Translated into German: E.~S. Unger, Erfurt, 1818.]

\BibItem[Lagrange.] ``Mémoire sur l'utilité de la méthode de prendre le milieu entre
les résultats de plusieurs observations, dans lequel on examine les avantages
de cette méthode par le calcul des probabilités, et où l'on résout
différents problèmes relatifs à cette matière.'' Misc.\ Taurinensia, vol.~5,
pp.~167--232, 1770--1773. {\OE}uvres complètes, vol.~2, Paris, 1867--1877.

\BibItem[\bysame] ``Recherches sur les suites recurrentes \ldots\ et sur l'usage de ces équations
dans la théorie des hasards.'' Nouv.\ Mém.\ Ac.\ Berl.\ (1775), pp.~183--272,
1777. {\OE}uvres complètes, vol.~4. Paris, 1867--1877.

\BibItem[Laisant, C.~A.] Algèbre. Théorie des nombres, probabilités, géométrie de
situation. Paris, 1895.

\BibItem[Lambert, J.~H.] ``Examen d'une espèce de superstition ramenée au calcul
des probabilités.'' Nouv.\ Mém.\ Ac.\ Berl., 1771, pp.~411--420.

\BibItem[Lämmel, R.] Untersuchungen über die Ermittelung von Wahrscheinlichkeiten.
(Inaug.-Dissert.) Pp.~80. Zürich, 1904.

\BibItem[Lampe, E.] ``Über eine Aufgabe aus der Wahrscheinlichkeitsrechnung.'' Grun.\
Arch., vol.~70, 1884.

\BibItem[Lange, F.~A.] Logische Studien.

\BibItem[Laplace.] Essai philosophique sur les probabilités. (Printed as introduction
to Théorie analytique des probabilités, from 2nd~ed.\ of the latter onwards.)
4to. Paris, 1814.

\BibItem[\bysame] German translation by Tönnies. Heidelberg, 1819. German translation
by N.~Schwaiger. Leipzig, 1886.

\BibItem[\bysame] A Philosophical Essay on Probabilities: transl.\ from the 6th~French
ed.\ by E.~W. Truscott and F.~L. Emory. 8vo. New York, 1902, 196~pp.

%[** TN: Next entry contains full-stop spaces after "ed.", not consistent with other entries; fixed.]
\BibItem[\bysame] Théorie analytique des probabilités.
1st~ed. 4to. Paris, 1812, 1st~and 2nd~Suppl., 1812--1820. 2nd~ed.
4to. cxi~+~506~+~2, Paris, 1814. 3rd~Suppl.\ 1820. 3rd~ed. Paris, 1820.
4th~Suppl.\ after 1820. {\OE}uvres complètes, vol.~7, pp.~cxcv~+~691, Paris,
1847. {\OE}uvres complètes, vol.~7, pp.~832, Paris, 1886.

\BibItem[\bysame] ``Recherches sur l'intégration des équations différentielles aux différences
finies, et sur leur usage dans la théorie des hasards.'' Mém.\ prés.\
à~l'Acad.\ des~Sc., pp.~113--163, 1773.

\BibItem[\bysame] ``Mémoire sur les suites récurro-récurrentes et sur leurs usages dans la
théorie des hasards,'' Mém.\ prés.\ à~l'Acad.\ des~Sc., vol.~6, pp.~353--371,
1774.

\BibItem[\bysame] ``Mémoire sur la probabilité des causes par les événements.'' Mém.\
prés.\ à~l'Acad.\ des~Sc., vol.~6, pp.~621--656, 1774.

\BibItem[\bysame] ``Mémoire sur les probabilités.'' Mém.\ prés.\ à~l'Acad.\ des~Sc., pp.~227--332,
1780.

\BibItem[\bysame] ``Mémoire sur les approximations des formules qui sont fonctions de
très grands nombres, et sur leurs applications aux probabilités.'' Mém.\
de l'Inst., pp.~353--415, 539--565, 1810.

\BibItem[\bysame] ``Mémoire sur les intégrales définies, et leur application aux probabilités.''
Mém.\ de l'Inst., pp.~279--347, 1810.

\Bibnote [The above memoirs are reprinted in {\OE}uvres complètes, vols.\ 8,~9, and~12,
Paris, 1891--1898.]

\BibItem[\bysame]
Sur l'application du calcul des probabilités appliqué à la philosophie
naturelle. Conn.\ des temps. {\OE}uvres complètes, vol.~13. Paris, 1904.

\BibItem[\bysame] ``Applications du calcul des probabilités aux observations et spécialement
aux opérations du nivellement.'' Annales de Chimie. {\OE}uvres
complètes, vol.~14, Paris, 1913.

\BibItem[La Placette, J.] Traité des jeux de hasard. 18mo. 1714.
%% -----File: 459.png---Folio 448-------

\BibItem[Laurent, H.] Traité du calcul des probabilités. Paris, 1873.

\BibItem[\bysame] [A la fin une liste des principaux ouvrages (320) ou mémoires publiés
sur le calcul des probabilités.]

\BibItem[\bysame] ``Application du calcul des probabilités à la vérification des répartitions.''
Journ.\ des Actuaires français, vol.~i.

\BibItem[\bysame] ``Sur le théorème de J.~Bernoulli.'' Journ.\ des Actuaires français, vol.~i.

\BibItem[Lechalas, G.] ``Le Hasard.'' Rev. Néo-scolastique, 1903.

\BibItem[\bysame] ``A propos de Cournot: hasard et déterminisme.'' Rev.\ de~Mét.\ et
de~Mor., 1906.

\BibItem[Legendre.] ``Méthode des moindres carrés.'' Mém.\ de l'Inst., 1810, 1811.

\BibItem[\bysame] Nouvelles méthodes pour la détermination des orbites des comètes.
Paris. 1805--6.

\BibItem[Lehr.] ``Zur Frage der Wahrscheinlichkeit von weiblichen Geburten und von
Totgeburten.'' Zeitschrift f.~des ges.\ Staatsw., vol.~45, p.~172, and p.~524, 1889.

\BibItem[Leibniz.] Nouveaux Essais. Liv.~ii.\ chap.~xxi.; liv.~iv.\ chaps.~ii.\ §\;14, xv.,~xvi.,
xviii.,~xx.

\BibItem[\bysame] Opera omnia, ed.\ Dutens, v.~17, 22,~28,~29, 203,~206; vi.\ pt.~i., 271,
304, 36,~217; iv.\ pt.~iii.~264.

\BibItem[\bysame] Correspondence between Leibnitz and Jac. Bernoulli. L.'s~Gesammelte
Werke (ed.\ Pertz and Gerhardt), vol.~3, pp.~71--97, \textit{passim}. Halle, 1855.

\Bibnote [These letters were written between 1703 and~1705.]

\BibItem[\bysame] See also s.v.~\textsc{Couturat}.

\BibItem[Lemoine, E.] ``Solution d'un problème sur les probabilités.'' Bulletin de la
Soc.\ math.\ de~Paris, 1873.

\BibItem[\bysame] Questions de probabilités et valeurs relatives des pièces du jeu des
échecs. 8vo. 1880.

\BibItem[\bysame] ``Quelques questions de probabilités résolues géométriquement.'' Bull.\
de~la Soc.\ math.\ de~France, 1883.

\BibItem[\bysame] ``Divers problèmes de probabilité.'' Ass.\ française pour l'Avancement
des Sciences, 1885.

\BibItem[Lexis, W.] Abhandlungen zur Theorie der Bevölkerungs- und Moral-statistik.
Pp.~253. Jena, 1903.

\BibItem[\bysame] Zur Theorie der Massenerscheinungen in der menschlichen Gesellschaft.
Pp.~95. Freiburg, 1877.

\BibItem[\bysame]
``Über die Wahrscheinlichkeitsrechnung und deren Anwendung auf die
Statistik.\DPtypo{}{''} Jahrb.\ f.~nat.\ Ök.\ u.~Stat.~(2), vol.~13, pp.~433--450, 1886.

\Bibnote [Contains a review of v.~Kries's ``Principien.'']

\BibItem[\bysame] ``Über die Theorie der Stabilität statistischer Reihen.'' Jahrb.\ f.~nat.\ Ök.\ u.~Stat.~(1),
vol.~32, p.~604, 1879.

\Bibnote [Reprinted in Abhandlungen.]

\BibItem[\bysame] ``Das Geschlechtsverhältnis der Geborenen und die Wahrscheinlichkeitsrechnung.''
Jahrb.\ f.~nat.\ Ök.\ u.~Stat.~(1), vol.~27, p.~209, 1876.

\Bibnote [Reprinted in Abhandlungen.]

\BibItem[\bysame] Einleitung in die Theorie der Bevölkerungsstatistik. Strassburg, 1875.

\BibItem[Liagre, J.~B.~J.] Calcul des probabilités et théorie des erreurs avec des applications
aux sciences d'observation en général et à la géodésie en particulier.
416~pp. Brussels, 1852. 2nd~ed. 8vo. 1879.

\BibItem[\bysame] ``Sur la probabilité d'une cause d'erreur régulière, etc.'' Bull.\ de l'Acad.\
de Belgique, 1855.

\BibItem[Liapounoff, A.] ``Sur une proposition de la théorie des probabilités.'' Bull.\
de l'Acad.\ des~Sc.\ de~Saint-Pét., v.~série, vol.~xiii.

\BibItem[\bysame] ``Nouvelle Forme du théorème sur la limite de probabilité.'' Mém.\ de
l'Acad.\ des~Sc.\ de~Saint-Pét., viii.~série, vol.~xiii. (1901).

\BibItem[Liebermeister, C.] ``Über Wahrscheinlichkeitsrechnung in Anwendung auf
therapeutische Statistik.'' Sammlung klinische Vorträge, Nr.~110. 1877.
%% -----File: 460.png---Folio 449-------

\BibItem[Lilienfeld, J.] ``Versuch einer strengen Fassung des Begriffs der mathematischen
Wahrscheinlichkeit.'' Zeitschr.\ f.~Philos.\ u.~phil.\ Kr., vol.~cxx,
pp.~58--65, 1902.

\BibItem[Lipps, G.~F.] Kollectivmasslehre. 1897.

\BibItem[Littrow, J.~J.] Die Wahrscheinlichkeitsrechnung in ihrer Anwendung auf das
wissenschaftliche und praktische Leben. 8vo. Wien, 1833.

\BibItem[Lobatchewsky, N.~J.] ``Probabilité des résultats moyens tirés d'observations
répétées.'' Crelle~J.\ 1824.

\BibItem[\bysame] Reprinted. Liouv.~J. vol.~24. 1842.

\BibItem[Lottin, J.] Le Calcul des probabilités et les régularités statistiques. 32~pp.
8vo. Louvain, 1910. (Originally published in the Revue Néo-scolastique,
Feb.~1910.)

\BibItem[\bysame] Quetelet, statisticien et sociologue. Louvain, 1912. Pp.~xxx~+~564.

\Bibnote [Contains a very full discussion of Quetelet's Work on Probability.]

\BibItem[Lotze, H.] Logik. 1st~ed.\ 1874, 2nd~ed.\ 1880.

\BibItem[\bysame] Engl.\ transl.\ by B.~Bosanquet. Oxford, 1884.

\Bibnote [See Bk.~ii.\ chap.~ix.: Determination of Single Facts and Calculus of
Chances.]

\BibItem[Lourié, S.] Die Prinzipien der Wahrscheinlichkeitsrechnung. Tübingen, 1910.

\BibItem[Lubbock, J.~W. \textrm{and} Drinkwater.] Treatise on Probability. [Library of
Useful Knowledge.]

\Bibnote [Often wrongly ascribed to \textsc{De Morgan}.]

\Bibsect{M}

\BibItem[Macalister, Donald.] The Law of the Geometric Mean. Phil.\ Trans., 1879.

\BibItem[McColl, Hugh.] Symbolic Logic. 1906. [Especially chaps.\ xvii.,~xviii.]

\BibItem[\bysame] The Calculus of Equivalent Statements. Proc.\ Lond.\ Math.\ Soc. Six
papers.

\Bibnote [See particularly 1877, vol.~ix.\ pp.~9--20; 1880, xi.~113--121, 4th~paper;
1897, xxviii.~p.~556, 6th~paper.]

\BibItem[\bysame] ``Growth and Use of a Symbolical Language.'' Memoirs Manchester
Lit.\ Phil.\ Soc.\ series~iii.\ vol.~7, 1881.

\BibItem[\bysame] ``Symbolical or Abbreviated Language with an Application to Mathematical
Probability.'' Math.\ Questions, vol.~28, pp.~20--23.

\BibItem[\bysame] Various Papers in Mathematical Questions from the Journal of Education,
vols.\ 29,~33,~etc.

\BibItem[\bysame] ``A Note on Prof.\ C.~S. Peirce's Probability Notation of 1867.'' Proc.\
Lond.\ Math.\ Soc.\ vol~xii.\ p.~102.

\BibItem[Macfarlane, Alexander.] Principles of the Algebra of Logic.

\Bibnote [See especially chaps.\ ii.,~iii.,~v., xx.,~xxi, xxii.,~xxiii., and the examples.]

\BibItem[\bysame] Various Papers in Mathematical Questions from the Journal of Education,
vols.\ 32,~36,~etc.

\BibItem[MacMahon, P.~A.] ``On the Probability that the Successful Candidate at an
Election by Ballot may never at any time have fewer Votes than the one
who is unsuccessful, etc.'' Phil.\ Trans.~(A), vol.~209, pp.~153--175, 1909.

\BibItem[Maldidier, Jules.] ``Le Hasard.'' Rev.\ Philos.~xliii., 1897, pp.~561--588.

\BibItem[Malfatti, G.~F.] ``Esame critico di un problema di probabilità del Sig.\ Daniele
Bernoulli, e~soluzione d'un altro problema analogo al bernuiliano.'' Memorie
di Matematica e~Fisica della Società Italiana, vol.~I, pp.~768--824, 1782.

\BibItem[Mallet.] ``Sur le calcul des probabilités.'' Act.\ Helv.\ Basileae, 1772,
vii.\ pp.~133--163.

\BibItem[Mansions, P.] ``Sur la portée objective du calcul des probabilités.'' Bulletin
de l'Académie de Belgique (Classe des sciences), pp.~1235--1294, 1903.

\BibItem[Marbe, Dr.\ Karl.] Naturphilosophische Untersuchungen zur Wahrscheinlichkeitslehre.
50~pp. Leipzig, 1899.

\BibItem[\bysame] Die Gleichförmigkeit in der Welt\DPtypo{}{.} Munich, 1916.
%% -----File: 461.png---Folio 450-------

\BibItem[Markoff, A.~A.] ``Über die Wahrscheinlichkeit \textit{à~posteriori}'' (in Russian)
Mitteilungen der Charkowv Math.\ Gesell. 2~Serie, vol.~iii. 1900.

\BibItem[\bysame] ``Untersuchung eines wichtigen Falles abhängiger Proben'' (in Russian).
Abh.\ der K.\ Russ.\ Ak.\ d.~W., 1907.

\BibItem[\bysame] ``Über einige Fälle der Theoreme vom Grenzwert der mathematischen
Hoffnungen und vom Grenzwert der Wahrscheinlichkeiten'' (in Russian).
Abh.\ der K.\ Russ.\ Ak.\ d.~W., 1907.

\BibItem[\bysame] ``Erweiterung des Gesetzes der grossen Zahlen auf von einander
abhängige Grössen'' (in Russian). Mitt.\ d.~phys.-math.\ Ges.\ Kazan, 1907.

\BibItem[\bysame] ``Über einige Fälle des Theorems vom Grenzwert der Wahrscheinlichkeiten''
(in Russian). Abh.\ der K.\ Russ.\ Ak.\ d.~W., 1908.

\BibItem[\bysame] ``Erweiterung gewisser Sätze der Wahrscheinlichkeitsrechnung auf eine
Summe verketteter Grössen'' (in Russian). Abh.\ der K.\ Russ.\ Ak.\ d.~W.,
1908.

\BibItem[\bysame] ``Untersuchung des allgemeinen Falles verketteter Ereignisse'' (in
Russian). Abh.\ der K.\ Russ.\ Ak.\ d.~W., 1910.

\BibItem[\bysame] ``Über einen Fall von Versuchen, die eine komplizierte \DPtypo{zusammenhängendes}{zusammenhängende}
Kette bilden,'' and ``Über zusammenhängende Grössen, die
keine echte Kette bilden'' (both in Russian). Bull.\ de l'Acad.\ des Sciences.
Petersburg, 1911\DPtypo{}{.}

\BibItem[\bysame] Wahrscheinlichkeitsrechnung. Transl.\ from 2nd~Russian edition by H.~Liebmann.
Leipzig, 1912. Pp.~vii~+~318.

\BibItem[\bysame] Démonstration du second théorème---limite du calcul des probabilités par
la méthode des moments. Saint-Pétersbourg, 1913. Pp.~66.

\Bibnote [Supplement to the 3rd~Russian edition of Wahrscheinlichkeitsrechnung,
in honour of the bicentenary of the Law of Great Numbers, with a Portrait
of Jacques Bernoulli.]

\BibItem[Masaryk, T.~G.] David Hume's Skepsis und die Wahrscheinlichkeitsrechnung.
Wien, 1884.

\BibItem[Maseres, F.] The Doctrine of Permutations and Combinations, being an
Essential and Fundamental Part of the Doctrine of Chances: As it is
delivered by Mr.~James Bernoulli, in his excellent Treatise on the Doctrine
of Chances, intitled, Ars conjectandi \ldots\ 8vo. London, 1795.

\BibItem[Meinong, A.] Review of Von Kries's ``Die Principien der Wahrscheinlichkeitsrechnung.''
Göttingische Gelehrte Anzeigen, vol.~2,\ pp.~56--75, 1890.

\BibItem[\bysame] Über Möglichkeit und Wahrscheinlichkeit: Beiträge zur Gegenstandstheorie
und Erkenntnistheorie. Pp.~xvi~+~760. Leipzig, 1915.

\BibItem[Meissner (Otto).] Wahrscheinlichkeitsrechnung: I.~Grundlehren; II.~Anwendungen.
Leipzig, 1912; 2nd~ed., 1919. Pp.~56~+~52.

\Bibnote [An elementary primer.]

\BibItem[Mendelssohn, Moses.] Philos.\ Schriften, 2~Tle. 12mo. Pp.~xxii~+~278~+~283.
Berlin, 1771. (\textit{Vide} especially vol.~ii.\ pp.~243--283, entitled ``Ueber die
Wahrscheinlichkeit.'')

\BibItem[Mentrè, F.] ``Rôle du hasard dans les inventions et découvertes.'' Rev.\
de Phil., 1904.

\BibItem[\bysame] ``Les Racines historiques du probabilisme rationnel de Cournot.'' Rev.\
de Métaphysique et de Morale, pp.~485--508, May 1905.

\BibItem[\bysame] Cournot et la renaissance du probabilisme au xixe\DPnote{** TN: Ordinal, no special formatting in orig}~siècle. Paris, 1908.

\BibItem[Merriman, M.] A Text-book of the Method of Least Squares. New York,
1884. Pp.~vii~+~198. 6th~ed., 1894.

\BibItem[\bysame] ``List of Writings relating to the Method of Least Squares, with Historical
and Critical Notes.'' Trans.\ Connecticut Acad.\ vol.~4, pp.~151--232, 1877.

\BibItem[Mertz.] Die Wahrscheinlichkeitsrechnung und ihre Anwendung, etc. Frankfort,
1854.

\BibItem[Messina, I.] ``Intorno a un nuovo teorema di calcolo delle probabilità.'' 20~pp.\ 4to.
Giornale di Matematiche di Battaglini, vol.~lvi.\ (1918). Naples.
%% -----File: 462.png---Folio 451-------

%\BibItem[Messina, I.]---\emph{continued}.

\Bibnote [Described Stat.\ Jl.\ vol.~lxxxii. (1919), p.~612.]

\BibItem[\bysame] ``Su di un nuovo teorema di calcolo delle probabilità, sul teorema di
Bernoulli e sui postulati empirici per la loro applicazione.'' Boll.\ del Lavoro
et della Presidenza, vol.~xxxiii. (1920).

\BibItem[Meyer, A.] Essai sur une exposition nouvelle de la théorie analytique des
probabilités \textit{à~posteriori}. 4to. Pp.~122. Liége, 1857.

\BibItem[\bysame] Cours de calcul des probabilités fait à l'université de Liége de 1849 à~1857.
Publié sur les mss.\ de l'auteur par F.~Folie. Bruxelles, 1874.

\BibItem[\bysame] Vorlesungen über Wahrscheinlichkeitsrechnung. (Translation of the
above by E.~Czuber.) Pp.~xii~+~554. Leipzig, 1879.

\BibItem[Michell.] ``An Inquiry into the Probable Parallax and Magnitude of the Fixed
Stars, from the Quantity of light which they afford us, and the particular
Circumstances of their Situation.'' Phil.\ Trans.\ vol.~57, pp.~234--264,
1767.

\BibItem[Milhaud, G.] ``Le Hasard chez Aristote et chez Cournot.'' Revue de Méta.\
et de Mor.\ vol.~x.\ pp.~667--681, 1902.

\BibItem[Mill, J.~S.] System of Logic. Bk.~iii.\ chaps.\ 18,~23.

\BibItem[Mondésir.] ``Solution d'une question qui se présente dans le calcul des probabilités.''
Liouville Journ.\ vol.~ii.

\BibItem[Monro, C.~J.] ``Note on the Inversion of Bernoulli's Theorem in Probabilities.''
Proc.\ Lond.\ Math.\ Soc.\ vol.~5, pp.~74--78 and~145, 1874.

\BibItem[Montessus, R.~de.] Leçons élémentaires sur le calcul des probabilités. Pp.~191.
Paris, 1908. (Reviewed Stat.\ Journ., 1909, p.~113.)

\BibItem[\bysame] ``Le Hasard.'' Rev.\ du Mois, March 1907.

\BibItem[Montessus, R.~de, \textrm{and} Lechalas, G.] ``Un Paradoxe du calcul des probabilités.''
Nouv.\ Ann.\ iv.~(3), 1903.

\BibItem[Montmort, P.~de.] Essai d'analyse sur les jeux de hasard. 4to. Pp.~xxiv~+~189.
Paris, 1708.

\BibItem[\bysame] Ditto. 4to. \DPtypo{pp}{Pp}.~414. Paris, 1714. (The 2nd~ed.\ is increased by a
treatise on Combinations, and the correspondence between M.~and Nicholas
Bernoulli.)

\BibItem[Montuola, J.~T.] Histoire des mathématiques. 4~vols. 4to. Paris, 1799--1802.

\BibItem[\bysame] Vol.~iii.\ pp.~380--426.

\Bibsect{N}

\BibItem[Newcomb, Simon.] A Statistical Inquiry into the Probability of Causes of the
Production of Sex in Human Offspring. (Published by the Carnegie
Institution of Washington.) Pp.~34. 8vo. Washington, 1904.

\BibItem[Nicole, F.] ``Examen et résolution de quelques questions sur les jeux.'' Hist.\
Ac.\ Par.\ pp.~45--56, 331--344, 1730.

\BibItem[Nieuport, C.~F.~de.] Un peu detort ou amusemens d'un sexagenaire. 8vo.
Bruxelles, 1818. Containing ``Conversations sur la théorie des probabilités.''

\BibItem[Nitsche, A.] ``Die Dimensionen der Wahrscheinlichkeit und die Evidenz der
Ungewissheit.'' Vierteljahrsschr.\ f.~wissensch.\ Philos.\ vol.~16, pp.~20--35,
1892.

\BibItem[Nixon, J.~W.] ``An Experimental Test of the Normal Law of Error.'' Stat.\
Journ.\ vol.~76, pp.~702--706, 1913.

\Bibsect{O}

\BibItem[Oettinger, L.] Die Wahrscheinlichkeitslehre. 4to. Berlin, 1852.

\Bibnote [Reprinted from Crelle\DPtypo{,}{}~J., vols.\ 26,~30, 34,~36, under the title, Untersuchungen
über Wahrscheinlichkeitsrechnung.]

\BibItem[Ostrogradsky.] ``Probabilité des jugements.'' Acad.\ de St-Pétersbourg, 1834.

\BibItem[\bysame] ``Sur la probabilité des hypothèses.'' Mélanges math.\ et astr., 1859.
%% -----File: 463.png---Folio 452-------

\Bibsect{P}

\BibItem[Pagano, F.] Logica dei probabili. Napoli, 1806.

\BibItem[Parisot, S.~A.] Traité du calcul conjectural ou l'art de raisonner sur les choses
futures et inconnues. 4to. Paris, 1810.

\BibItem[Pascal, B.] ``Letters to Fermat.'' Varia opera mathematica D.~Petri de
Fermat.\ pp.~179--188, Toulouse, 1678.

\BibItem[\bysame] {\OE}uvres, vol.~4, pp.~360--388, Paris, 1819.

\BibItem[Patavio.] Probabilismus methodo mathematico demonstratus. 1840.

\BibItem[Paulhan, Fr.] ``L'erreur et la sélection.'' Rev.\ Philos.\ vol.~viii.\ pp.~72--86,
179--190, 290--306, 1879.

\BibItem[Peabody, A.~P.] ``Religious Aspect of the Logic of Chance and Probability.''
Princeton Rev.\ vol.~v.\ pp.~303--320, 1880.

\BibItem[Pearson, K.] ``On a Form of Spurious Correlation which may arise when
Indices are used, etc.'' Proc.\ Roy.\ Soc.\ vol.~lx.\ pp.~489--498.

\BibItem[\bysame] ``On the Criterion that a given System of Deviations from the Probable
in the case of a Correlated System of Variables is such that it can be
reasonably supposed to have arisen from Random Sampling.'' Phil.\ Mag.~(5),
vol.~50, pp.~157--160, 1900.

\BibItem[\bysame] ``On some Applications of the Theory of Chance to Racial Differentiation.''
Phil.\ Mag.~(6), vol.~1, pp.~110--124, 1901.

\BibItem[\bysame] Contributions to the Mathematical Theory of Evolution.

\Bibnote [The main interest of the twelve elaborate memoirs published in the
Phil.\ Trans.\ under the above title is in every case statistical. References
are given below to those of them which have most reference to the theory
of Probability and in which Professor Pearson's general theory is mainly
developed.]

\BibItem[\bysame] II. ``Skew Variation in Homogeneous Material.'' Phil.\ Trans.~(A),
vol.~186, Part~i.\ pp.~343--414, 1895.

\BibItem[\bysame] III. ``Regression, Heredity, and Panmixia.'' Phil.\ Trans.~(A), vol.~187,
pp.~253--318, 1897.

\BibItem[\bysame] V. ``On the Probable Errors of Frequency Constants and on the
Influence of Random Selection on Variation and Correlation.'' Phil.\
Trans.~(A), vol.~191, pp.~229--311, 1898. (With L.~N.~G. Filon.)

\BibItem[\bysame] VII. ``On the Correlation of Characters not quantitatively measurable.''
Phil.\ Trans.~(A), vol.~195, pp.~1--47, 1901.

\BibItem[\bysame] ``Mathematical Contributions to the Theory of Evolution.'' Roy.\ Stat.\
Soc.\ Journ.\ lvi.,~1893, pp.~675--679; lix.,~1896, pp.~398--402; lx.,~1897, pp.~440--449.

\BibItem[\bysame] ``On the Mathematical Theory of Errors of Judgment, with special
reference to the Personal Equation.'' Phil.\ Trans.~(A), vol.~198, pp.~235--299,
1902.

\BibItem[\bysame] On the Theory of Contingency and its relation to Association and
Normal Correlation. Pp.~35. 4to. London, 1904.

\BibItem[\bysame] On the General Theory of Skew Correlation and Non-linear Regression.
Pp.~54. 4to. London, 1905.

\BibItem[\bysame] On further Methods of determining Correlation. London, 1907. (Reviewed
by G.~U. Yale Journ.\ Roy.\ Stat.\ Soc., Dec.\ 1907.)

\BibItem[\bysame] ``On the Influence of Past Experience on Future Expectation.'' Phil.\
Mag.~(6), vol.~13, pp.~365--378, 1907.

\BibItem[\bysame] ``The Fundamental Problem of Practical Statistics.'' Biometrika, vol.~xiii.\
pp.~1--16, 1920.

\Bibnote [On Inverse Probability.]

\BibItem[\bysame] ``Notes on the History of Correlation.'' Biometrika, vol.~xiii.\ pp.~25--45,
1920.

\BibItem[\bysame] ``The Chances of Death'' and other essays. 2~vols. 8vo, London,
1897.

\BibItem[\bysame] The Grammar of Science. London, 1892.
%% -----File: 464.png---Folio 453-------

\BibItem[Peirce, C.~S.] ``A Theory of Probable Inference.'' Johns Hopkins ``Studies in
Logic,'' 1883.

\BibItem[\bysame] ``On an Improvement in Boole's Calculus of Logic.'' Proc.\ Amer.\ Acad.\
Arts and Sci.\ vol.~vii.\ pp.~250--261, 1867. Pp.~62. Camb., 1870.

\BibItem[Perozzo.] ``Nuove applicazioni del calcolo delle probabilità allo studio dei
fenomeni statistici.'' Proceedings of Academia dei Lincei, 1881--82.

\BibItem[\bysame] Germ.\ transl.\ by O.~Elb. Neue Anwendungen der Wahrscheinlichkeitsrechnung
in der Statistik. Pp.~33. 4to. Dresden, 1883.

\BibItem[Pièron, H.] ``Essai sur le hasard. La Psychologie d'un concept.'' Rev.\ de
Méta.\ et~de Mor.\ vol.~x.\ pp.~682--693, 1902.

\BibItem[Pinard, H.] ``Sur la Convergence des Probabilités.'' Rev.\ Néo-Schol.\ de
Phil.\ No.~84 (1919) and No.~85 (1920).

\BibItem[Pincherle, S.] ``Il calcolo delle probabilità e~l'intuizione.'' Scientia, vol.~xix.\
pp.~417--426, 1916.

\BibItem[Pizzetti, P.] I fondamenti matematici per la critica dei risultati sperimentali.
Atti della R.~Univ., Genova, 1892.

\BibItem[Plaats, J.~D. van~der.] Over de toepassing der waarschijnlijkheidsrekening
op medische statistick. 1895.

\BibItem[Plana, G.] ``Mémoire sur divers problèmes de probabilité.'' Mémoires de
l'Académie de Turin for 1811--12, vol.~xx.\ pp.~355--408, 1813.

\BibItem[\DPtypo{Poincarè}{Poincaré}, H.] Calcul des probabilités. Pp.~274. Paris, 1896.

\BibItem[\bysame] 2nd~edition (with additions). Pp.~333. Paris, 1912.

\BibItem[\bysame] Science et hypothèse. Paris.

\BibItem[\bysame] Engl.\ transl., London, 1905.

\BibItem[\bysame] Science et méthode. Paris. (Includes a chapter on ``Le Hasard.'')

\BibItem[\bysame] Eng.\ transl.\ (by F.~Maitland). Pp.~288. London, 1914.

\BibItem[\bysame] ``Le Hasard.'' Rev.\ du~Mois, March 1907.

\BibItem[Poisson, S.~D.] Recherches sur la probabilité des jugements en matière
criminelle et en matière civile, précédés des règles générales du calcul des
probabilités. 4to. Pp.~ix~+~415. Paris, 1837.

\BibItem[\bysame] Lehrbuch der Wahrscheinlichkeitsrechnung. German translation of the
above by H.~Schnuse. Braunschweig. 8vo. 1841.

\BibItem[\bysame] ``Sur la probabilité des résultats moyens des observations.'' Conn.\
des Temps. Pp.~273--302, 1827. Pp.~3--22, 1832.

\BibItem[\bysame] ``Formules relatives aux probabilités qui dépendent de très grand
nombres.'' Compt.\ Rend., Acad.\ Paris, vol.~2, pp.~603--613, 1836.

\BibItem[\bysame] ``Sur le jeu de trente et quarante,'' Annal.\ de Gergonne,~xv.

\BibItem[\bysame] ``Solution d'un problème de probabilité.'' Liouv.~J.~(1), vol.~2, 1837.

\BibItem[\bysame] ``Mémoire sur la proportion des naissances des filles et des garçons.''
Mém.\ Acad.\ Paris, vol.~9, pp.~239--308, 1830.

\BibItem[Pondra \textrm{et} Hossard.] Question de probabilité résolue par la géométrie. 8vo.
Paris, 1819.

\BibItem[Poretzki, Platon.~S.] ``Solution of the general Problem of the Theory of
Probability by means of Mathematical Logic.'' (In Russian.) Bull.\ of
the physico-mathematical Academy of Kasan, 1887.

\BibItem[Prevost, P.] ``Sur les principes de la théorie des gains fortuits.'' Nouv.\ Mém.\
Pp.~430--472. Berlin, 1780.

\BibItem[Prevost, P., \textrm{and} Lhuilier, S.~A.] ``Sur les probabilités.'' Mém.\ Ac.\ Berl.\
(1796), pp.~117--142, 1799.

\BibItem[\bysame] ``Sur l'art d'estimer la probabilité des causes par les effets.'' Mém.\ Ac.\
Berl.\ (1796), pp.~3--24, 1799.

\BibItem[\bysame] ``Remarques sur l'utilité et l'étendue du principe par lequel on estime
la probabilité des causes.'' Mém.\ Ac.\ Berl.\ (1796), pp.~25--41, 1799.

\BibItem[\bysame] Note on last. Mém.\ Ac.\ Berl.\ (1797), p.~152, 1800.

\BibItem[\bysame] ``Mémoire sur l'application du calcul des probabilités à la valeur du
témoignage.'' Mém.\ Ac.\ Berl.\ (1797), pp.~120--151, 1800.
%% -----File: 465.png---Folio 454-------

\BibItem[Price, R.] See \textsc{Bayes}.

\BibItem[Pringsheim, A.] See \textsc{Daniel Bernoulli}.

\BibItem[\bysame] ``Weiteres zur Geschichte des Petersburger Problems.'' Grunert, Archiv,
77, 1881.

\BibItem[Proctor, R.~A.] Chance and Luck. A Discussion of the Laws of Luck, Coincidences,
Wagers, Lotteries, and the Fallacies of Gambling, with Notes on
Poker and Martingales. Pp.~vii~+~263. London, 1887.

\BibItem[Protimalethes.] Miracle \textit{versus} Nature: being an Application of Certain Propositions
in the Theory of Chances to the Christian Miracles. 8vo. Cambridge,
1847.

\Bibsect{Q}

\BibItem[Quetelet, A.] Instructions populaires sur le calcul des probabilités. 12mo.
Bruxelles, 1828.

\BibItem[\bysame] Engl.\ transl.: Popular Instructions on the Calculation of Probabilities,
transl.\ with notes by R.~Beamish. 1839.

\BibItem[\bysame] Dutch transl.\ by H.~Strootman. Breda, 1834.

\BibItem[\bysame] Lettres sur la théorie des probabilités appliquée aux sciences, morales
et politiques. Bruxelles, 1846.

\BibItem[\bysame] Engl.\ transl.: Letters on the Theory of Probabilities as applied to the
Moral and Political Sciences, transl.\ by O.~G. Downes. 8vo. 1849.

\BibItem[\bysame] ``Sur la possibilité de mesurer l'influence des causes qui modifient les
\DPtypo{élémens}{éléments} sociaux.'' Corresp.\ mathém.\ et~phys.\ vol.~vii.\ pp.~321--346.
Bruxelles, 1832.

\BibItem[\bysame] ``Sur la constance qu'on observe dans le nombre des crimes qui se committent.''
Corresp.\ mathém.\ et phys.\ vol.~vi.\ pp.~214--217. Brussels, 1830.

\BibItem[\bysame] ``Théorie des probabilités.'' (In the Encycl.\ populaire.) Brussels, 1853.

\BibItem[\bysame] ``Sur le calcul des probabilités appliqué à la science de l'homme.'' Bull.\
de l'Acad.\ roy.\ vol.~xxvi.\ pp.~19--32. Brussels, 1873.

\Bibnote [For a full bibliography and discussion of Quetelet's writings on these
topics see Lottin's Quetelet.]

\Bibsect{R}

\BibItem[Rayleigh, Lord.] ``On James Bernouilli's Theorem in Probabilities.'' Phil.\
Mag.~(5), vol.~47, pp.~246--251, 1890.

\BibItem[Regnault.] Calcul des chances et philosophie de la bourse. 8vo. Paris,
1863.

\BibItem[Renouvier, Ch.] L'Homme: la raison, la passion, la liberté, la certitude, la
probabilité morale. 8vo. 1859.

\BibItem[Revel, P.~Camille.] Esquisse d'un système de la nature fondé sur la loi du
hasard. 1890. 2nd~ed.\ (corrigée), 1892.

\BibItem[\bysame] Le Hasard, sa loi et ses conséquences dans les sciences et en philosophie.
Paris, 1905. 2nd~ed.\ (corrigée et augmentee). Pp.~249. Paris, 1909.

\BibItem[Rizzetti, J.] ``Ludorum scientia, sive artis conjectandi elementa ad alias
applicata.'' Act.\ Erud.\ Suppl.\ vol.~9, pp.~215--229, 295--307. Leipzig,
1729.

\BibItem[Roberts, Hon.~Francis.] ``An Arithmetical Paradox concerning the Chances
of Lotteries.'' Phil.\ Trans.\ vol.~xvii.\ pp.~677--681, 1693.

\BibItem[Roger.] ``Solution d'un problème de probabilité.'' Liouv.~J.~(1), vol.~17,
1852.

\BibItem[Rouse, W.] Doctrine of Chances, or the Theory of Gaming made easy to every
Person---Lotteries, Cards, Horse-Racing, Dice, etc. 1814.

\BibItem[Rudiger, Andreas.] De sensu falsi et veri libri~iv. [Lib.~i.\ cap.~xii.\ et~lib.~iii.]
Editio Altera. 4to. Lipsiae, 1722.

\BibItem[Ruffini.] Critical Reflexions on the Essai philosophique of Laplace (in
Italian). Modena, 1821.
%% -----File: 466.png---Folio 455-------

\Bibsect{S}

\BibItem[Sabudski-Eberhard.] Die Wahrscheinlichkeitsrechnung, ihre Anwendung auf
das Schiessen und auf die Theorie des Einschiessens. Stuttgart, 1906.

\BibItem[Sawitsch, A.] Die Anwendung der Wahrscheinlichkeitstheorie auf die Berechnung
der Beobachtungen und geodätischen Messungen oder die Methode
der kleinsten Quadrate. (Translated into German from the Russian by
Lais.) Leipzig, 1863.

\BibItem[Schell, W.] Über Wahrscheinlichkeit. 8vo.

\BibItem[Schnuse, H.] Vid.\ \textsc{Poisson}.

\BibItem[Schweigger, F.] Berechnung der Wahrscheinlichkeit beim Würfeln.

\BibItem[Scott, John.] The Doctrine of Chance: the Arithmetic of Gambling. 56~pp.\
8vo. 1908.

\BibItem[Segueri, Paolo.] Lettere sulla materia del probabile. 12mo. Colonia, 1732.

\BibItem[Sextus Empiricus.] Works.

\BibItem[Sheldon, W.~H.] ``Chance.'' Journal of Phil., Psych., and Sci.\ Meth., vol.\ ix.\
pp.~281--290. 1912.

\BibItem[Sheppard, W.~F.] ``On the Application of the Theory of Error to Cases of
Normal Distribution and Normal Correlation.'' Phil.\ Trans.~A.\ vol.~192,
pp.~101--167, 1899.

\BibItem[\bysame] ``On the Calculation of the most Probable Values of the Frequency
Constants for Data arranged according to Equidistant Divisions of a Scale.''
Proc.\ Lond.\ Math.\ Soc.\ vol.~xxix.\ pp.~353--380.

\BibItem[\bysame] ``Normal Correlation.'' Camb.\ Phil.\ Soc.\ vol.~xix.

\BibItem[\bysame] ``Normal Distribution and Correlation.\DPtypo{}{''} Roy.\ Soc.\ Trans., 1898.

\BibItem[Sigwart, C.] Review of von Kries in Vierteljahrsschr.\ für Wiss.\ Phil.~xiv.\
p.~90.

\BibItem[\bysame] Logik. Tübingen, 1878.

\BibItem[\bysame] 2nd~ed. Freiburg, i.~B., 1893. English~ed., 1895.

\BibItem[\bysame] Vol,~ii.\ Part~3, chap.~3, §\;85, Die Wahrscheinlichkeitsrechnung; 5,~§\;102.
Die Wahrscheinlichkeit auf statischem Boden.

\Bibnote References in English ed.:

\BibItem[\bysame] Probability, vol.~ii.\ pp.~216--230, 261--271 (errors of observation), 303--309
(induction), 504--507 (statistics).

\BibItem[Simmons, T.~C.] ``A New Theorem in Probability.'' Proc.\ Lond.\ Math.\ Soc.\
vol.~26, pp.~290--323, 1895.

\BibItem[\bysame] ``Sur la probabilité des événements composés.'' Ass.\ Franc.\ pour
l'Avancement des Sciences. 1896.

\BibItem[Simon.] ``Exposition des principes du calcul des probabilités.'' Journ.\ des
Actuaires français,~i.

\BibItem[Simpson, T.] ``A Letter to the Right Honourable George, Earl of Macclesfield,
President of the Royal Society, as to the Advantage of taking the Mean
of a Number of Observations in Practical Astronomy.'' Phil.\ Trans.\ vol.~xlix.\
pp.~82--93, 1755.

\BibItem[\bysame] ``An Attempt to show the Advantage arising by taking the Mean of a
Number of Observations in Practical Astronomy.'' (Miscellaneous tracts
on some curious subjects, pp.~64--75). London, 4to, 1757.

\Bibnote [A reprint of the above with some new matter. The probability, assuming
positive and negative errors to be equally likely, that the mean is
nearer to the truth than a single observation taken at random, is here
investigated for the first time.]

\BibItem[\bysame] Treatise on the Nature and Laws of Chance. 4to. London, 1740.

\BibItem[\bysame] Another edition. 8vo. 1792.

\BibItem[Sorel, G.] ``Le Calcul des probabilités et l'expérience.'' Rev.\ Philos.\ vol.~xxiii.\
pp.~50--66, 1887.

\BibItem[Spehr, F.~W.] Vollständiger Lehrbegriff der reinen Combinationslehre mit
Anwendungen derselben auf Analysis und  Wahrscheinlichkeitsrechnung. 2.~wohlfeile
Ausg. 4to. Braunschweig, 1840.
%% -----File: 467.png---Folio 456-------

\BibItem[Spinoza.] ``Letter to Jan van der Meer.'' Opera ed.\ Van Vleten and Land,
vol.~ii.\ pp.~145--149, Ep.~38 (in Latin and Dutch).

\BibItem[\bysame] See also Spinoza's Briefwechsel in J.~H. v.~Kirchmann's Philos.\ Bibliothek,
vol.~xlvi.\ pp.~145--147.

\BibItem[Sprague, T.~B.] On Probability and Chance and their Connexion with the
Business of Insurance. 8vo. 1892.

\BibItem[Stamkart, F.~J.] Over de waarschijnlijkheidsrekening. 8vo.

\BibItem[Sterzinger, O.] Zur Logik und Naturphilosophie der Wahrscheinlichkeitslehre.
Leipzig, 1911.

\BibItem[Stewart, Dugald.] ``On the Calculus of Probabilities, in reference to the
Preceding Argument for the Existence of God, from Final Causes.'' Philosophy
of the Moral Powers, vol.~ii.\ pp.~108--119. (Sir W.~Hamilton's ed.,
Edin., 1860.) 1st~ed., 1828.

\BibItem[Stieda, L.] ``Über die Anwendung der Wahrscheinlichkeitsrechnung in der
anthropologischen Statistik.\ Arch.\ f.~Anthrop., 1882.
2nd~ed.\ 8vo. Braunschweig, 1892.

\BibItem[Streeter, T.~E.] The Elements of the Theory of Probabilities. 31~pp.\ 8vo.
1908.

\BibItem[Struve.] Catalogus novus stellarum duplicium et multiplicium. Dorpati,
1827, pp.~xxxvii--xlviii.

\BibItem[Stumpf, C.] ``Bemerkung zur Wahrscheinlichkeitslehre.'' Jahrb.\ f.~national.
Ök.\ u.~Stat.~(3), vol.~17, pp.~671,~672, 1899; vol.~18, p.~243, 1899.

\Bibnote [In criticism of Bortkiewicz, \textit{q.v.}]

\BibItem[Stumpf, K.] ``Über den Begriff der mathematischen Wahrscheinlichkeit.''
Ber.\ bayr.\ Ak.\ (Phil.\ Cl.), pp.~37--120, 1892.

\BibItem[\bysame] ``Über die Anwendung des mathematischen Wahrscheinlichkeitsbegriffes
auf Teile eines Continuums.'' Ber.\ bayr.\ Ak.\ (Phil.\ Cl.), pp.~681--691,
1892.

\BibItem[Suppantschitsch.] Einführung in die Wahrscheinlichkeitsrechnung. Leipzig.

\Bibsect{T}

\BibItem[Tait, P.~G.] ``Law of Frequency of Error.'' Edin.\ Phil.\ Trans.\ vol.~4, 1865.

\BibItem[\bysame] On a Question of Arrangement and Probabilities. 1873.

\BibItem[Tchebychef, P.~L.] Essai d'analyse élémentaire de la théorie des probabilités.
4to. Moscow, 1845 (in Russian, degree thesis). Pp.~ii~+~61~+~iii.

\BibItem[\bysame] ``Démonstration élémentaire d'une proposition générale de la théorie
des probabilités.'' Crelle~J.\ vol.~33, pp.~259--267, 1846.

\BibItem[\bysame] ``Des valeurs moyennes.'' Liouv.~J.~(2), vol.~12, pp.~177--184, 1867.
(Extrait du Recueil des Sciences mathématiques, vol.~ii.)

\BibItem[\bysame] ``Sur deux théorèmes relatifs aux probabilités.'' Petersb.\ Abh.\ vol.~55,
1887. (In Russian.) French translation by J. Lyon: Act.\ Math.\
Petr.\ vol.~14, pp.~305--315, 1891.

\BibItem[\bysame] {\OE}uvres. 2~vols. 4to. St-Pétersbourg, 1907.

\Bibnote (The three memoirs preceding are here reprinted in French.)

\BibItem[Terrot, Bishop.] ``Summation of a Compound Series and its Application to a
Problem in Probabilities.'' Edin.\ Phil.\ Trans., 1853, vol.~xx.\ pp.~541--545.

\BibItem[\bysame] ``On the Possibility of combining two or more Probabilities of the same
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vol.~xxi.\ pp.~369--376.

\BibItem[Thiele, T.~N.] Theory of Observations. Pp.~6~+~143. 4to. London, 1903.

\BibItem[Thomson, Archbishop.] Laws of Thought. §\;124, Syllogisms of Chance (13~pp.).

\BibItem[Thubeuf.] Élémens\DPnote{** TN: [sic] Appears not to be a typo for Éléments} et principes de la royale arithmétique aux jettons, etc.\
12mo. Paris, 1661.

\BibItem[Timerding.] Die Analyse des Zufalls. Pp.~ix~+~168. Braunschweig, 1915.

\BibItem[Todhunter, I.] ``On the Method of Least Squares.'' Camb.\ Phil.\ Trans.\ vol.~ii.\

\BibItem[\bysame] A History of the Mathematical Theory of Probability from the Time of
Pascal to that of Laplace. Lge.\ 8vo. pp.~xvi~+~624, Camb.\ and~Lond., 1865.
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\BibItem[Tozer, J.] On the Measure of the Force of Testimony in Cases of Legal Evidence.
4to. Camb.\ Phil.\ Soc.\ vol.~viii. Part~II. 16~pp.\ (read Nov.~27,
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\BibItem[Trembley.] ``Observations sur le calcul d'un jeu de hasard.'' Mém.\ Ac.\ Berl.\
(1802), pp.~86--102.

\BibItem[\bysame] ``Recherches sur une question relative au calcul des probabilités.''
Mém.\ Ac.\ Berl.\ (1794--5), pp.~69--108, 1799.

\BibItem[\bysame] (On Euler's memoir, ``Solutio quarundam quaestionum difficiliorum in
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\BibItem[\bysame] ``De probabilitate causarum ab effectibus oriunda.'' Comm.\ Soc.\ Reg.\
Gott.\ (1795--8), vol.~13, pp.~64--119, 1799.

\BibItem[\bysame] ``Observations sur la méthode de prendre les milieux entre les observations.''
Mem.\ Ac.\ Berl.\ (1801), pp.~29--58, 1804.

\BibItem[\bysame] ``Disquisitio elementaris circa calculum probabilium.'' Comm.\ Soc.\
Reg.\ Gott.\ (1793--4), vol.~12, pp.~99--136, 1796.

\BibItem[Tschuprow, A.~A.] ``Die Aufgaben der Theorie der Statistik.'' Jahrb.\ f.~gesetzg.\
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\BibItem[\bysame] ``Zur Theorie der Stabilität statistischer Reihen.''  Skandinavisk
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\Bibsect{V}

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\Bibnote [Translation of Part~I. only of Bernoulli's Ara Conjectandi (\textit{q.v.})\ containing
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%% -----File: 469.png---Folio 458-------

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\end{Biblio}
%% -----File: 470.png---Folio 459-------

\cleardoublepage
\phantomsection
\pdfbookmark[0]{Index}{Index}
\printindex

\iffalse
Acquaintance, direct 12

Addition, of probabilities 37, 135
  definition of 120
  Theorem of 104, 121, 144
  and measurement 158

Analogy, principle of 68
  and induction 218, 222
  negative 219, 223, 233, 415
  positive 220, 223, 415
  and generalisation 223
  logical foundation of 258
  and Bacon 268
  and Leibniz 272
  and Jevons 273
  and statistics 391, 407
  and statistics|ifoll 415

Ancillon|inote#Ancillon 5

Ancillon 82

Apprehension, direct, and ethical judgment 316

Argument 13

Aristotle 80, 92
  and induction 274

Arithmetic mean (or average) 205
  and laws of error 197
  Laplace on 206
  Gauss on 206

Astronomers and Least Squares 210

Asymmetry, and Bernoulli's Theorem|ifoll 358

Atomic Uniformity 249

Averages|ifoll 205

Averages
  weighting of 211
  and discordant observations 214

Axioms|ifoll 135

Axioms
  non-self-evident 299

Bachelier|inote 347

Bachelier
  and statistical frequency|inote 349
  and statistical frequency 351
  and Rule of Succession|inote 376

Bacon|ifoll 265

Bacon
  tables of 269
  and limited variety 270

Bayes, and Inverse Probability 174
  Theorem of 379

Belief, rational|ifoll 4

Belief, rational 10, 16, 307
  degrees of 11

Bentham, measurement of Probability 20

Bernoulli, Daniel, and Inverse Probability 174
  and planets|inote 293
  and planets 294
  and Petersburg Paradox 316, 317

Bernoulli, Jac.|inote 15

Bernoulli, Jac. 41, 76, 81, 83, 86, 368, 369
  weight of evidence 313
  second axiom of 322
  and regular frequency 333
  and statistical series 392

Bernoulli's Theorem|ifoll 337

Bernoulli's Theorem|inote 319

Bernoulli's Theorem 109, 314, 333
  and asymmetry|ifoll 358
  empirical verification of|ifoll 361
  Inverse of|ifoll 368, 385

Bertrand|inote 48

Bertrand 49
  on multiplication 136
  and Maxwell|inote 172
  and independence 173
  and Law of Error|inote 208
  and chance 284
  and Petersburg Paradox 317
  and Bernoulli's Theorem 339
  and Rule of Succession 382

Bicquilley and testimony|inote 184

Bobek and Rule of Succession 383

Bode's Law 304

Boole|inote 43, 50, 294

Boole 84
  and German logicians 87
  and relation of Probability 90
  and symbolic probability 155
  and approximation 161
  and independence 167
  and Whately 179
  and combination of premisses 179
%% -----File: 471.png---Folio 460-------
%\item Boole (\textit{contd.})---
  and testimony 180
  and Challenge Problem 187
  and Cournot|inote 284
  and Rule of Succession 382

Borel|inote 47

Borel 48

Bortkiewicz, von, and great numbers|inote 333

Bortkiewicz, von, and great numbers
  and Marbe|inote 365
  method of 384
  and Lexis|ifoll 393
  and Law of Small Numbers|ifoll 401
  and Quetelet 402

Boscovitch and Least Squares 210

Bowley|ifoll 424

Bowley 421, 423

Bradley|inote 319

Bradley
  and relativity of Probability 91
  and Bernoulli's Theorem|inote 341

Broad, C.~D.|inote 257

Brömse and Marbe|inote 365

Brünn and lotteries 364

Bruns and Marbe|inote 365

Buffon 317, 322
  and coin-tossing 362

Butler, Bishop 79, 80, 309, 310
  and risk 321

Calculus of Probability|inote 83

Calculus of Probability 149, 164, 303, 428
  and Psychical Research 302
  and Sociology 335

Casual@{`\textit{Casual}'} 288

Causality 263, 276
  and independence 164

Cause@{`\textit{Cause}'} 275

Cause, final 297

Cayley, and tradition 185
  and Challenge Problem 187

Certainty 10, 127, 128
  and truth 15
  Kahle and|inote 90
  definition of 120
  relation of 134
  and Bacon 267
  and Leibniz 272

Chance, objective|ifoll 286

Chance, objective 281, 295, 418
  Couturat on 283
  Poincaré on 284, 289
  Condorcet on 284
  definition of 287
  and planets 293
  and binary stars 295

Coefficient of Credibility 183
  of Correlation|ifoll 421

Combination of premisses 149, 178

Comte
  and `\textit{seven}'#seven 246
  and statistics 335

Condorcet|inote 83

Condorcet 317
  and testimony 180
  and chance 282, 284
  and ethics 313, 316
  and gambling 319

Conduct and Probability 307

Consistence and group theory 124

Contradiction 143

Coover, J.|inote 298

Correlation 329, 390
  and statistical frequency 330
  Quantitative 391, 426
  Inductive 406
  coefficient|ifoll 421

Cournot, and frequency theory 92
  and independence 166
  on testimony 180
  and causality 275
  and chance 282, 283

Couturat|inote 272, 311

Craig and tradition 184

Cramer and Petersburg Paradox 318

Crofton|inote 47

Cumulative Formula 150
  Johnson and 121

Czuber|inote 47, 339, 345

Czuber 78, 82, 86, 347
  and symbolic probability 156
  and cause@{and `\textit{cause}'}|inote 275
  and risk|inote 315
  and Bernoulli's Theorem|inote 340
  and statistical frequency 351, 394
  and Tchebycheff's Theorem|inote 353, 355
  and verification of Bernoulli|inote 362
  and lotteries 364
  and Marbe 365
  and Inverse of Bernoulli's Theorem|inote 370
  and Rule of Succession|inote 376
  and Rule of Succession 382

D'Alembert|inote 170, 365

D'Alembert 82, 321, 369
  and chance 282
  and planets 293
  and mathematical expectation 314
  and ethics 316
  and Petersburg Paradox 317
  and Marbe 365

Darbon, A., and Cournot 284

Darwin 108
  and Lyell 161
  and Mill 265

Dedekind and `\textit{Challenge Problem}'|inote#Dedekind 187
%% -----File: 472.png---Folio 461-------

Definitions|ifoll 134

Definitions
  summary of 120
  de la Placette, Jean, and chance 283

De Morgan 21, 74, 83
  and inference 139
  and independence 168
  and Inverse Probability 178
  and combination of premisses 179
  and tradition|inote 184
  and planets 293
  pupil of 362
  and Inverse of Bernoulli's Theorem|inote 370
  and Rule of Succession 375, 382

De Witt and arithmetic averages 206

Dice-tossing|ifoll 361

Diderot on testimony 183

Discordant observations, rejection of 213

Donkin, W. F. 20
  and Inverse Probability 176

Dormoy 394

Edgeworth|inote 29, 362

Edgeworth 84, 85, 379, 400
  use of `\textit{Probability}'|inote 96
  and randomness 290
  and Psychical Research|inote 298
  and ethics 316
  and German statisticians 394

Eggenberger|inote 340

Ellis, Leslie 84, 85
  and frequency theory 92
  and Least Squares|inote 207
  and Least Squares 209
  and Bacon|inote 265, 266, 269, 271, 274
  and Bernoulli's Theorem 341

Empirical School 85, 86

Epistemology 302
  and inductive hypothesis 261

Equiprobability 41, 63, 65

Equivalence, definition of 120, 134
  axiom of 135
  principle of 141

Error, probable 329

Ethics|ifoll 307

Euler and Least Squares 210

Event, probability of 5

Evidence, and measurement of Probability 7, 35
  relevant and irrelevant 53, 54
  independent and complementary 55
  external 57
  addition of 66, 68
  weight of 71
  and Induction 221

Excluded Middle, Law of 143

Experience and the Principle of
  Indifference 100

Fechner, and median 201
  and law of sensation 208
  and lotteries 364

Fermat, formula of 242

Forbes, J. D.|inote 20, 294

Forbes, J. D. 21

Frazer, Sir J. 245

Frequency curves 199
  and statistics 328

Frequency, statistical 330

Frequency theory|ifoll 92

Frequency theory
  and randomness 290
  and Bernoulli's Theorem 344
  and Rule of Succession 378

Fresnel and simplicity 206

Fries|inote 15

Galton 321
  and Fechner's law 208

Gambling 319

Gauss, and laws of error|inote 196

Gauss, and laws of error 198
  and arithmetic mean 206
  and Least Squares 210

Generalisation 389

definition of 222
  from statistics 328

Generator properties 253
  plurality of 254, 256, 257

Geometrical probability 47, 62

German logicians 87

Gibbon 29, 322, 333

Gilman, B. I., and symbolic probability 156

Goldschmidt|inote 29

Goodness, organic nature of 310

Graunt|inote 392

Great Numbers, Law of|ifoll 333

Great Numbers, Law of 82, 330
% \item Greville, Fulke, 466

Grimsehl|inote 248

Grimsehl
  and Marbe|inote 365

Groups, of propositions 117, 124
  definition of 120, 125
  real and hypothetical 129

Grünbaum and Marbe|inote 365

Hagen, and error 207
  and discordant observations|inote 214

Halley and mortality statistics 332

Herodotus 307

Herschell and binary stars 294

Houdin|inote 364

Hudson, W. H., and animism|inote 247

Hume 52, 70, 80, 81, 82, 83, 239, 427
  and testimony 182
%% -----File: 473.png---Folio 462-------
%\item Hume (\textit{contd.})---
  and Induction 218, 233, 265, 272
  and analogy 222, 224
  and chance 282

Huyghens 82
  and six@{and `\textit{six}'}#six 247

Hypothesis 7

Hypothetical entities 299

Implication 124

Impossibility 15
  definition of 120
  relation of 134

Inconsistency, definition of 120

Independence, for knowledge 107, 165
  definition of 120, 138
  Theorem of 121, 146
  of events 164
  and law of error 195
  and measurement 204
  and averages 212
  and discordant observations 214
  and chance 283

Index numbers 211

Induction@{`\textit{Induction}'}#induction 274

Induction 97
  Principle of 68
  and frequency theory 98, 99, 107
  and Logic 217
  pure 218
  universal 220, 406, 417
  validity of 221
  and statistics|ifoll 327
  statistical|ifoll 406

Inductive correlation 220, 257, 258, 392, 397, 406

Inductive hypothesis 260, 264

Inductive method 260

Inference 129
  necessary 120, 139
  hypothetical and assertoric 130
  statistical|ifoll 327

Insurance 22, 285, 404

Intuition \textit{versus} experience 86
  and ethical judgment 312

Inverse Probability 149, 174
  and Venn 100
  and frequency theory 106
  Theorem of 121
  and statistics|inote 370
  and statistics 369
  and Bowley 425

Irrelevance 255
  judgments of 54
  definition of 55, 120, 138
  Theorem of 121, 146

James, W., and spirits 301

Jesuits 308

Jevons|inote 244

Jevons
  and equiprobability|inote 42
  and Inverse Probability 178
  and index numbers 212
  and Induction 222, 238, 243, 265, 273, 274
  and analogy 246
  and coin-tossing 362
  and Rule of Succession 382

Johnson, W. E. 116
  and propositions|inote 11
  and added evidence 68
  and cumulative formula 121, 150, 153, 155
  and groups 124
  and testimony 183

Judgments 54
  of preference and relevance 65
  direct 70
  disjunctive 77

Kahle and the Probability relation 90

Kant 333
  and Hume 272

Kapteyn, Prof.\ J. C.#Kapteyn
  and law of error 199

Knowledge 10
  kinds of 3, 4
  direct and indirect 12, 262
  incomplete and proper 13
  of logical relations 14
  probable and vague 17
  relativity of 17
  vague and distinct 53
  homologic and ontologic 276, 288
  and ignorance 281
  and chance 289

Kries, von|inote 44, 45, 46, 67

Kries, von 42, 50, 84
  and equiprobability 87
  and Principle of Indifference 172
  and independence 173
  and Inverse Probability 176
  and knowledge 276
  and Cournot|inote 284
  and School of Lexis 394

Lacroix|inote 184

Lambert and Least Squares 210

Lämmel|inote 47

Lämmel
  and symbolic probability 156

Laplace|inote 15, 28

Laplace 31, 82, 83, 84, 318, 427
  school of 44, 51, 86, 358, 365
%% -----File: 474.png---Folio 463-------
%\item Laplace (\textit{contd.})---
  and relation of Probability 91
  and independence 170
  and Inverse Probability 175, 178
  and testimony 180, 182
  and doctrine of averages 202
  and arithmetic mean 206
  and Least Squares 210
  and Induction 220, 239, 265, 273
  and chance 282
  and planets|inote 293
  and Quetelet 334
  and Bernoulli's Theorem 340, 341, 370
  and Rule of Succession|inote 351, 359
  and Rule of Succession 368
  and birth proportions 364
  and unknown probabilities 370
  and Bayes' Theorem 380
  and statistical series 392

Laurent and gambling 319

Law|inote 311

Law of error|ifoll 194

Law of error
  and arithmetic mean 197
  and geometric mean 198
  and median 200
  and mode 203
  normal law 199, 202, 205
  Lexis and 398

Least Squares and Venn 206
  method of 202, 205, 206, 209

Lee and tradition|inote 184

Legendre and Least Squares 210

Leibniz|inote 24

Leibniz 308, 368, 392, 427
  and arithmetic average 206
  and Induction 272

Lexis, and asymmetry of statistical frequency|inote 359

Lexis, and asymmetry of statistical frequency
  and Marbe|inote 365
  method of|ifoll 393, 397
  method of 384
  and Edgeworth 401
  and statistical stability|inote 419
  and statistical stability 415

Locke 76, 80, 82, 83, 308, 323
  on tradition 184
  and weight of evidence 313

Logic, academic 3
  of probability 8
  of implication 58
  and Induction 217, 245
  and initial probability 299

Logical priority 129

Lotteries|ifoll 364

Lotteries|inote 333

Lotteries 361
  published results of 363

Lotze 89
  and Rule of Succession 382

Lucretius 427

M'Alister, Sir Donald, and laws of error 198

Macaulay and Bacon 266

McColl, and symbolic probability 155
  and Boole|inote 167
  and Inverse Probability 176
  and Challenge@{and `\textit{Challenge Problem}'}|inote#Challenge 188

Macfarlane, and independence|inote 169

Macfarlane, and independence
  and tradition 185
  and Challenge@{and `\textit{Challenge Problem}'}|inote#Challenge 187

Maclaurin, Theorem of 207

Marbe, Dr.\ Karl, and roulette 365

Marginal utility 318

Markoff, A. A.|inote 177

Markoff, A. A.
  and Inverse Probability 176
  and Tchebycheff's Theorem 357

Mathematical Expectation 311, 315, 316

Mathematicians, and probability 84
  and cumulative formula 152
  and laws of error 207
  and ethics 316

Maxim, Sir Hiram|inote 364

Maxwell|inote 172

Maxwell
  and theory of gases 172

Mayer and Least Squares 210

Means and laws of error|ifoll 194

Measurement of Probability 34, 158, 311
  and frequency theory 94
  and induction 259, 388
  and psychical research 302
  and ethics 311

Median and laws of error 200

Meinong 78

Meissner, Otto, and dice-throwing 363

Memory 14

Mendelism and statistics 335, 419, 428

Merriman, Mansfield, and Least Squares 209

Metaphysics and certainty 239

Method of Difference 246

Michell 302
  and Inverse Probability 174
  and binary stars 294

Middle Term, Fallacy of 68, 155

Mill, and inductive correlations 220
  and induction|ifoll 265
  and plurality of causes|inote 267
  and probability|inote 268
  and pure induction 269
  methods of 270
  and limited variety 271

Modality and probability|inote 16
%% -----File: 475.png---Folio 464-------
%\item Modality (\textit{contd.})---

Modality and probability
  Venn and 98

Mode, and law of error 203
  asymmetry about 361

Monte Carlo 364

Moore, G. E.|inote 240

Moore, G. E. 19, 309

Morgan, \textit{vide} De Morgan 0

Multiplication 135
  definition of 120
  theorems of 121, 148, 342
  of instances|ifoll 233

Munro|inote 370

Necessary connection, law of 251

Newton, and induction 244
  ans seven@{and `\textit{seven}'}#seven 247
  and Bacon 265

Nitsche, A.|inote 45, 50, 172

Nitsche, A. 78

Occurrences, remarkable 302

Pascal 82

Pearson, Karl|inote 351

Pearson, Karl 84
  and frequency theory 100
  and arithmetic mean 208
  and stars 297
  and asymmetry|inote 359
  and asymmetry 347
  and generalised Probability curves 347
  and roulette 364
  and Rule of Succession 379, 382

Peirce|inote 50

Peirce 304
  and randomness 290

Petersburg Paradox 316
  psychology of 318
  and Buffon 362

Peterson and tradition 184

Physics and initial probability 299

Planets, movements of 293

Playfair, Dr.\ Lyon 305

Plurality of causes and Mill 267

Poetry and statistics 401

Poincaré, Henri 48, 84
  and independence 173
  and chance 284, 289

Poisson|inote 51, 362

Poisson
  on testimony 180
  and least errors 207
  and Petersburg Paradox 317
  and gambling 319
  and great numbers 333, 336
  Theorem of 344
  and statistical frequency 348
  and Tchebycheff 357
  and inverse of Bernoulli's Theorem 370

Poretzki, Platon S., and symbolic
  probability 157

Port Royal logic 70, 80, 321
  and probabilism 308

Prediction, value of 305

Price and Bayes|inote 174

Primitive people and rational belief 245

Principle of compelling reason 86

Principle of Indifference|ifoll 83

Principle of Indifference 42, 81, 87, 104, 107, 171
  analysis of 53
  modification of 55, 58
  and induction 99
  and measurement 160
  and Psychical Research 302
  and ethics 310
  and statistics 367
  and Laplace 372, 374
  and Rule of Succession 377

Principle of Non-Sufficient Reason 41, 85

Principle of superposition of small
  effects 249

Probabilism 308

Probability@{`\textit{Probability}'} 8
  Venn's use of 95
  Edgeworth's use of|inote 96

Probability, and relevant knowledge 4
  objective relation of 5, 8, 281
  mathematical 6
  dependent on evidence 7
  philosophical definition of 8
  three senses of 11
  measurement of|ifoll 20
  measurement of 37
  and law 24
  and similarity 28, 36
  comparison of 34, 66, 160
  series of 35, 38
  geometrical@{`\textit{geometrical}'} 47, 48, 62
  and rational belief 97
  and statistical frequency 98
  and truth frequency|ifoll 101, 337
  Inverse 106, 149
  and truth 116, 322
  negative 139
  finite 237
  and randomness 291
  and planetary orbits 293
  and binary stars 294
  and star drifts 296
  and final causes 297
  and spirits 300, 301
  and telepathy 300
  and ethics 307
%% -----File: 476.png---Folio 465-------
%\item Probability (\emph{contd}.)---
  from statistics|ifoll 367
  unknown@{`\textit{unknown},' and Laplace}#Laplace 372

Probability relation 4, 8, 13, 134

intuition of 52

Probable error 74

Proctor|inote 364

Proposition, characterisation of 3, 4
  primary and secondary 11, 13
  knowledge of 12
  self-evident 17
  classes of|ifoll 101
  groups of 117, 124
  sub-groups of 126, 129 %[** TN: Regularized to subgroups]
  disjunction and conjunction of 134
  synthetic 263
  existential 276

Propositional function 56
  and induction 222
  and randomness 291

Psychical Research|ifoll 278

Psychology and probability 52

Pythagoras and `\textit{seven}' 246

Quetelet|inote 333

Quetelet 334, 335, 401, 418, 427, 428
  and arithmetic mean 208
  and balls 362
  and statistical stability 393

Randomness 281, 290, 412
  Pearson's use of 297

Relation, of probability 6
  of `\textit{between}'#between 35, 39

Relativity, of knowledge 17
  of probabilities 102
  doctrine of, and the Law of Uniformity|inote 248

Relevance, judgments of 54
  and frequency theory 104
  theorems of 147

Remarkableness 302

Requirement 129

Risk 315
  and ethics 313
  and Petersburg Paradox 319
  `\textit{moral}'#moral 320, 322
  `\textit{physical}'#physical 322

Roulette 361, 364
  published results of|inote 363

Rule of Succession|inote 359

Rule of Succession 368, 372, 374
  proof of 375
  and frequency theory 378
  and Pearson|inote 380

Russell, Bertrand|inote 124

Russell, Bertrand 19, 115, 126
  and inference 117
  and implication 124

Schematisation 67

Schröder and symbolic probability 157

Selection, random 292

Series of probabilities 35, 38
  and frequency theory 93
  independent 283, 420
  organic 399, 420
  Gaussian|inote 421

Sigwart 88
  and inverse probability 178
  and induction 273

Simmons and asymmetry in Bernoulli's
  Theorem 359

Simpson and Least Squares 210

Small Numbers, Law of|ifoll 401

Society for Psychical Research|inote 298

Space 255
  and uniformity 226
  irrelevance of 301

Spedding and Ellis and Bacon|inote 265, 266

Spielräume, doctrine of 88

Spinoza|inote 116, 282

Spirits, probability of 300

Star drifts 296

Stars, binary 294

Statistical frequency, theory of|ifoll 93

Statistical frequency, theory of
  generalisation of 101
  criticism of 103
  stability of 336, 392-415
  fluctuation of 392

Statistical inference|ifoll 327

Statistical inference
  induction|ifoll 406

Statistics, and prediction 306
  descriptive and inductive 327

Stumpf|inote 44, 50, 172

Sub-analogies 223, 229

Sub-groups of propositions 126, 129 %[** TN: Regularized to subgroups]

Succession, Law of 82
  \textit{See} Rule of 0

Süssmilch and regular frequencies 333

Taylor, Jeremy|inote 308

Tchebycheff, Theorem of 353, 355
  and Poisson's Theorem 357

Telepathy, probability of 300

Terrot, Bishop|inote 43

Terrot, Bishop
  and Whately|inote 179
  and combination of premisses 179

Testimony, theory of 180
%% -----File: 477.png---Folio 466-------

Time 255
  and uniformity 226
  irrelevance of 301

Todhunter|inote 294, 318, 370

Todhunter
  and Bayes 175
  and Craig 184
  and Petersburg Paradox 316
  and Bernoulli's Theorem|inote 340

Truth and probability|inote 116

Truth and probability 322

Truth frequency 101, 406

Tschuprow|inote 399

Tschuprow 358
  and statistical frequency|inote 394
  and statistical frequency 348
  method of 384

Uniformity of Nature, Law of 226, 248, 255, 263, 276
  and Mill 270

Universal Causation, Law of 248

Universal Induction and statistical
  methods 389, 406-417

Universe of reference 117, 129, 130

Unknown probabilities 372, 373, 375

Variables in Probability|inote 412

Variables in Probability 58, 123

Variety 234
  and induction 219
  limitation of 258, 260, 427

Venn|inote 106, 294

Venn 84
  and experience 85
  and Bernoulli 86, 341
  and frequency theory|ifoll 93
  and inverse probability 100
  and Least Squares|inote 206
  and induction 273
  and chance 288
  and `\textit{random}'#random 290
  and Rule of Succession 372, 378

Weight, of evidence 312
  and ethics 315

Weighting of averages 211

Weldon and dice 362

Whately and combination of misses 178

Whitehead, and frequency theory
  and invalid inference|inote 329

Whittaker, E. T., and Rule of Succession|inote 376 %[** TN: "cession" in orig]

Wilbraham, H., and Boole|inote 167

Wolf and dice 362

Yule|inote 349, 361

Yule
  and approximation 161
  and independence 166
  and `\textit{statistics}'#statistics 327
  and coin-tossing|inote 346, 361
  and correlation 421, 424
\fi

%[** TN: index environment prints this at end]
\iffalse
\begin{center}
\begin{minipage}{0.55\linewidth}{\footnotesize O False and treacherous Probability,\\
Enemy of truth, and friend to wickednesse;\\
With whose bleare eyes Opinion learnes to see,\\
Truth's feeble party here, and barrennesse.}
\end{minipage} \\
\small THE END\rule{0em}{10em}\\
\textsc{\footnotesize PRINTED BY R. \& R. CLARK, LTD., EDINBURGH\rule{0em}{12em}}
\end{center}
\fi
%% -----File: 478.png---Folio 467-------
%[Blank Page]

\cleardoublepage

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