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Full text of "Science and hypothesis"











J. LARMOR, D.Sc., SEC. R.S., 

Liicasian Professor of Mathematics in the University of Cambridge, 

Condon and Hewcastlc-on-Cyne: 












































THE translator wishes to express his indebted 
ness to Professor Larmor, for kindly consenting 
to introduce the author of Science and Hypothesis 
to English readers; to Dr. F. S. Macaulay and 
Mr. C. S. Jackson, M.A., who have read the whole 
of the proofs and have greatly helped by sugges 
tions; also to Professor G. H. Bryan, F.R.S., who 
has read the proofs of Chapter VIII., and whose 
criticisms have been most valuable. 

\V. J. G. 

February 1905. 


IT is to be hoped that, as a consequence of the 
present active scrutiny of our educational aims 
and methods, and of the resulting encouragement 
of the study of modern languages, we shall not 
remain, as a nation, so much isolated from 
ideas and tendencies in continental thought and 
literature as we have been in the past. As things 
are, however, the translation of this book is 
doubtless required; at any rate, it brings vividly 
before us an instructive point of view. Though 
some of M. Poincare s chapters have been collected 
from well-known treatises written several years 
ago, and indeed are sometimes in detail not quite 
up to date, besides occasionally suggesting the 
suspicion that his views may possibly have been 
modified in the interval, yet their publication in 
a compact form has excited a warm welcome in 
this country. 

It must be confessed that the English language 


hardly lends itself as a perfect medium for the 
rendering of the delicate shades of suggestion 
and allusion characteristic of M. Poincare s play 
around his subject ; notwithstanding the excel 
lence of the translation, loss in this respect is 

There has been of late a growing trend of 
opinion, prompted in part by general philosophical 
views, in the direction that the theoretical con 
structions of physical science are largely factitious, 
that instead of presenting a valid image of the 
relations of things on which further progress can 
be based, they are still little better than a mirage. 
The best method of abating this scepticism is to 
become acquainted with the real scope and modes 
of application of conceptions which, in the popular 
language of superficial exposition and even in 
the unguarded and playful paradox of their 
authors, intended only for the instructed eye 
often look bizarre enough. But much advantage 
will accrue if men of science become their own 
epistemologists, and show to the world by critical 
exposition in non-technical terms of the results 
and methods of their constructive work, that more 
than mere instinct is involved in it: the com 
munity has indeed a right to expect as much as 


It would be hard to find any one better 
qualified for this kind of exposition, either 
from the profundity of his own mathematical 
achievements, or from the extent and freshness 
of his interest in the theories of physical science, 
than the author of this book. If an appreciation 
might be ventured on as regards the later chapters, 
they are, perhaps, intended to present the stern 
logical analyst quizzing the cultivator of physical 
ideas as to what he is driving at, and w r hither he 
expects to go, rather than any responsible attempt 
towards a settled confession of faith. Thus, when 
M. Poincare allows himself for a moment to 
indulge in a process of evaporation of the 
Principle of Energy, he is content to sum up: 
" Eh bien, quelles que soient les notions nouvelles 
que les experiences futures nous donneront sur le 
monde, nous sommes surs d avance qu il y aura 
quelque chose qui demeurera constant et que nous 
pourrons appeler cncrgic" (p. 166), and to leave 
the matter there for his readers to think it out. 
Though hardly necessary in the original French, it 
may not now be superfluous to point out that 
independent reflection and criticism on the part 
of the reader are tacitly implied here as else 

An interesting passage is the one devoted to 


Maxwell s theory of the functions of the sether, 
and the comparison of the close-knit theories of 
the classical French mathematical physicists with 
the somewhat loosely-connected corpus of ideas by 
which Maxwell, the interpreter and successor of 
Faraday, has (posthumously) recast the whole 
face of physical science. How many times has 
that theory been re-written since Maxwell s day ? 
and yet how little has it been altered in essence, 
except by further developments in the problem of 
moving bodies, from the form in which he left it! 
If. as M. Poincare remarks, the French instinct 
for precision and lucid demonstration sometimes 
finds itself ill at ease with physical theories of 
the British school, he as readily admits (pp. 223, 
224), and indeed fully appreciates, the advantages 
on the other side. Our ow r n mental philosophers 
have been shocked at the point of view indicated 
by the proposition hazarded by Laplace, that a 
sufficiently developed intelligence, if it were made 
acquainted with the positions and motions of the 
atoms at any instant, could predict all future 
history: no amount of demur suffices sometimes 
to persuade them that this is not a conception 
universally entertained in physical science. It 
was not so even in Laplace s own day. From 
the point of view of the study of the evolution 


of the sciences, there are few episodes more 
instructive than the collision between Laplace 
and Young with regard to the theory of capil 
larity. The precise and intricate mathematical 
analysis of Laplace, starting from fixed pre 
conceptions regarding atomic forces which were 
to remain intact throughout the logical develop 
ment of the argument, came into contrast with the 
tentative, mobile intuitions of Young ; yet the 
latter was able to grasp, by sheer direct mental 
force, the fruitful though partial analogies of this 
recondite class of phenomena with more familiar 
operations of nature, and to form a direct picture 
of the way things interacted, such as could only 
have been illustrated, quite possibly damaged or 
obliterated, by premature effort to translate it 
into elaborate analytical formulas. The apcrgus 
of Young were apparently devoid of all cogency 
to Laplace; while Young expressed, doubtless in 
too extreme a way, his sense of the inanity of the 
array of mathematical logic of his rival. The 
subsequent history involved the Nemesis that the 
fabric of Laplace was taken down and recon 
structed in the next generation by Poisson; while 
the modern cultivator of the subject turns, at any 
rate in England, to neither of those expositions 
for illumination, but rather finds in the partial 


and succinct indications of Young the best start 
ing-point for further effort. 

It seems, however, hard to accept entirely 
the distinction suggested (p. 213) between the 
methods of cultivating theoretical physics in 
the two countries. To mention only two 
transcendent names which stand at the very 
front of two of the greatest developments of 
physical science of the last century, Carnot and 
Fresnel, their procedure was certainly not on the 
lines thus described. Possibly it is not devoid of 
significance that each of them attained his first 
effective recognition from the British school. 

It may, in fact, be maintained that the part 
played by mechanical and such-like theories 
analogies if you will is an essential one. The 
reader of this book will appreciate that the human 
mind -has need of many instruments of comparison 
and discovery besides the unrelenting logic of the 
infinitesimal calculus. The dynamical basis which 
underlies the objects of our most frequent ex 
perience has now been systematised into a great 
calculus of exact thought, and traces of new real 
relationships may come out more vividly when 
considered in terms of our familiar acquaintance 
with dynamical systems than when formulated 
under the paler shadow of more analytical abstrac- 


tions. It is even possible for a constructive 
physicist to conduct his mental operations entirely 
by dynamical images, though Helmholtz, as well 
as our author, seems to class a predilection in this 
direction as a British trait. A time arrives when, 
as in other subjects, ideas have crystallised out 
into distinctness ; their exact verification and 
development then becomes a problem in mathe 
matical physics. But whether the mechanical 
analogies still survive, or new terms are now 
introduced devoid of all naive mechanical bias, 
it matters essentially little. The precise de 
termination of the relations of things in the 
rational scheme of nature in which we find 
ourselves is the fundamental task, and for its 
fulfilment in any direction advantage has to be 
taken of our knowledge, even when only partial, 
of new aspects and types of relationship which 
may have become familiar perhaps in quite 
different fields. Nor can it be forgotten that the 
most fruitful and fundamental conceptions of 
abstract pure mathematics itself have often been 
suggested from these mechanical ideas of flux 
and force, where the play of intuition is our 
most powerful guide. The study of the historical 
evolution of physical theories is essential to the 
complete understanding of their import. It is in 



the mental workshop of a Fresnel, a Kelvin, or 
a Helmholtz, that profound ideas of the deep 
things of Nature are struck out and assume 
form; when pondered over and paraphrased by 
philosophers we see them react on the conduct 
of life : it is the business of criticism to polish 
them gradually to the common measure of human 
understanding. Oppressed though we are w r ith 
the necessity of being specialists, if we are 
to know anything thoroughly in these days of 
accumulated details, we may at any rate pro 
fitably study the historical evolution of knowledge 
over a field wider than our own. 

The aspect of the subject which has here been 
dw r elt on is that scientific progress, considered 
historically, is not a strictly logical process, and 
does not proceed by syllogisms. New ideas 
emerge dimly into intuition, come into con 
sciousness from nobody knows where, and become 
the material on which the mind operates, forging 
them gradually into consistent doctrine, which 
can be welded on to existing domains of know 
ledge. But this process is never complete : a 
crude connection can always be pointed to by a 
logician as an indication of the imperfection of 
human constructions. 

If intuition plays a part which is so important, 


it is surely necessary that we should possess a firm 
grasp of its limitations. In M. Poincare s earlier 
chapters the reader can gain very pleasantly a 
vivid idea of the various and highly complicated 
ways of docketing our perceptions of the relations 
of external things, all equally valid, that were 
open to the human race to develop. Strange to 
say, they never tried any of them ; and, satisfied 
with the very remarkable practical fitness of the 
scheme of geometry and dynamics that came 
naturally to hand, did not consciously trouble 
themselves about the possible existence of others 
until recently. Still more recently has it been 
found that the good Bishop Berkeley s logical 
jibes against the Newtonian ideas of fluxions and 
limiting ratios cannot be adequately appeased in 
the rigorous mathematical conscience, until our 
apparent continuities are resolved mentally into 
discrete aggregates which we only partially 
apprehend. The irresistible impulse to atomize 
everything thus proves to be not merely a disease 
of the physicist ; a deeper origin, in the nature 
of knowledge itself, is suggested. 

Everywhere want of absolute, exact adaptation 
can be detected, if pains are taken, between the 
various constructions that result from our mental 
activity and the impressions which give rise to 


them. The bluntness of our unaided sensual 
perceptions, which are the source in part of the 
intuitions of the race, is well brought out in this 
connection by M. Poincare. Is there real con 
tradiction ? Harmony usually proves to be re 
covered by shifting our attitude to the phenomena. 
All experience leads us to interpret the totality of 
things as a consistent cosmos undergoing evolu 
tion, the naturalists will say in the large-scale 
workings of which we are interested spectators 
and explorers, while of the inner relations and 
ramifications we only apprehend dim glimpses. 
When our formulation of experience is imperfect 
or even paradoxical, we learn to attribute the 
fault to our point of view, and to expect that 
future adaptation will put it right. But Truth 
resides in a deep well, and we shall never get 
to the bottom. Only, while deriving enjoyment 
and insight from M. Poincare s Socratic exposi 
tion of the limitations of the human outlook on 
the universe, let us beware of counting limitation 
as imperfection, and drifting into an inadequate 
conception of the wonderful fabric of human 



To the superficial observer scientific truth is un 
assailable, the logic of science is infallible ; and if 
scientific men sometimes make mistakes, it is 
because they have not understood the rules of 
the game. Mathematical truths are derived from 
a few self-evident propositions, by a chain of 
flawless reasonings ; they are imposed not only on 
us, but on Nature itself. By them the Creator is 
fettered, as it were, and His choice is limited to 
a relatively small number of solutions. A few 
experiments, therefore, will be sufficient to enable 
us to determine what choice He has made. From 
each experiment a number of consequences will 
follow by a series of mathematical deductions, 
and in this way each of them will reveal to us a 
corner of the universe. This, to the minds of most 
people, and to students who are getting their first 
ideas of physics, is the origin of certainty in 
science. This is what they take to be the role of 


experiment and mathematics. And thus, too, it 
was understood a hundred years ago by many 
men of science who dreamed of constructing the 
world with the aid of the smallest possible amount 
of material borrowed from experiment. 

But upon more mature reflection the position 
held by hypothesis was seen ; it was recognised that 
it is as necessary to the experimenter as it is to the 
mathematician. And then the doubt arose if all 
these constructions are built on solid foundations. 
The conclusion was drawn that a breath would 
bring them to the ground. This sceptical attitude 
does not escape the charge of superficiality. To 
doubt everything or to believe everything are two 
equally convenient solutions ; both dispense with 
the necessity of reflection. 

Instead of a summary condemnation we should 
. examine with the utmost care the role of hypo 
thesis ; we shall then recognise not only that it is 
necessary, but that in most cases it is legitimate. 
We shall also see that there are several kinds of 
hypotheses; that some are verifiable, and when 
once confirmed by experiment become truths of 
great fertility; that others may be useful to us in 
fixing our ideas; and finally, that others are 
hypotheses only in appearance, and reduce to 
definitions or to conventions in disguise. The 


latter are to be met with especially in mathematics , 
and in the sciences to which it is applied. From 
them, indeed, the sciences derive their rigour ; 
such conventions are the result of the unrestricted 
activity of the mind, which in this domain recog-/ 
nises no obstacle. For here the mind may affirms 
because it lays down its own la\vs ; but let us 
clearly understand that while these laws are 
imposed on our science, which otherwise could 
not exist, they are not imposed on Nature. Are^ ; 
they then arbitrary? No; for if they were, they 
would not be fertile. Experience leaves us our 
freedom of choice, but it guides us by helping us to 
discern the most convenient path to follow. Our 
laws are therefore like those of an absolute 
monarch, who is wise and consults his council of 
state. Some people have been struck by this 
characteristic of free convention w^hich may be 
recognised in certain fundamental principles of 
the sciences. Some have set no limits to their 
generalisations, and at the same time they have 
forgotten that there is a difference between liberty 
and the purely arbitrary. So that they are com 
pelled to end in what is called nominalism; they 
have asked if the savant is not the dupe of his 
own definitions, and if the world he thinks he has 
discovered is not simply the creation of his own 


caprice. 1 Under these conditions science would 
retain its certainty, but would not attain its object, 
and would become powerless. Now, we daily see 
what science is doing for us. This could not be 
unless it taught us something about reality; the 
aim of science is not things themselves, as the 
dogmatists in their simplicity imagine, but the 
relations between things; outside those relations 
there is no reality knowable. 

Such is the conclusion to which we are led; but 
to reach that conclusion we must pass in review 
the series of sciences from arithmetic and 
geometry to mechanics and experimental physics. 
What is the nature of mathematical reasoning ? 
Is it really deductive, as is commonly supposed ? 
Careful analysis shows us that it is nothing of the 
kind ; that it participates to some extent in the 
nature of inductive reasoning, and for that reason 
it is fruitful. But none the less does it retain its 
character of absolute rigour ; and this is what 
must first be shown. 

When we know more of this instrument which 
is placed in the hands of the investigator by 
mathematics, we have then to analyse another 
fundamental idea, that of mathematical magni- 

1 Cf. M. le Roy: "Science et Philosophic," Revue de Afe/a- 
pkysique et de Morale , 1901. 


tude. Do we find it in nature, or have we our 
selves introduced it ? And if the latter be the 
case, are we not running a risk of coming to 
incorrect conclusions all round ? Comparing the 
rough data of our senses with that extremely com 
plex and subtle conception \vhich mathematicians 
call magnitude, we are compelled to recognise a 
divergence. The framework into which \ve wish 
to make everything fit is one of our own construc 
tion ; but w r e did not construct it at random, we 
constructed it by measurement so to speak; and 
that is \vhy w r e can fit the facts into it without 
altering their essential qualities. 

Space is another framework which we impose 
on the world. Whence are the first principles of 
geometry derived ? Are they imposed on us by 
logic ? Lobatschewsky, by inventing non-Euclid 
ean geometries, has shown that this is not the case. 
Is space revealed to us by our senses ? No ; for 
the space revealed to us by our senses is absolutely 
different from the space of geometry. Is geometry 
derived from experience ? Careful discussion will 
give the answer no ! We therefore conclude that 
the principles of geometry are only conventions ; 
but these conventions are not arbitrary, and if 
transported into another w ; orld (w 7 hich I shall 
call the non-Euclidean world, and which I shall 


endeavour to describe), we shall find ourselves 
compelled to adopt more of them. 

In mechanics we shall be led to analogous con 
clusions, and we shall see that the principles of 
this science, although more directly based on 
experience, still share the conventional character 
of the geometrical postulates. So far, nominalism 
triumphs ; but we now come to the physical 
sciences, properly so called, and here the scene 
changes. We meet with hypotheses of another 
kind, and we fully grasp ho\v fruitful they are. 
No doubt at the outset theories seem unsound, 
and the history of science show s us how ephemeral 
they are ; but they do not entirely perish, and of 
each of them some traces still remain. It is these 
traces which we must try to discover, because in 
them and in them alone is the true reality. 
The method of the physical sciences is based 
\upon the induction which leads us to expect the 
recurrence of a phenomenon when the circum 
stances which give rise to it are repeated. If all 
the circumstances could be simultaneously re 
produced, this principle could be fearlessly applied ; 
but this never happens; some of the circumstances 
will always be missing. Are we absolutely certain 
that they are unimportant ? Evidently not ! It 
may be probable, but it cannot be rigorously 


certain. Hence the importance of the role that is 
played in the physical sciences by the law of 
probability. The calculus of probabilities is there 
fore not merely a recreation, or a guide to the 
baccarat player; and we must thoroughly examine 
the principles on which it is based. In this con 
nection I have but very incomplete results to lay 
before the reader, for the vague instinct w r hich 
enables us to determine probability almost defies 
analysis. After a study of the conditions under 
which the work of the physicist is carried on, I 
have thought it best to show him at work. For 
this purpose I have taken instances from the 
history of optics and of electricity. We shall thus 
see how the ideas of Fresnel and Maxwell took 
their rise, and what unconscious hypotheses were 
made by Ampere and the other founders of 





THE very possibility of mathematical science seems 
an insoluble contradiction. If this science is only 
deductive in appearance, from whence is derived 
that perfect rigour which is challenged by none? 
If, on the contrary, all the propositions which it 
enunciates may be derived in order by the rules 
of formal logic, how is it that mathematics is 
not reduced to a gigantic tautology? The syllo 
gism can teach us nothing essentially new, and 
if everything must spring from the principle of 
identity, then everything should be capable of 
being reduced to that principle. Are we then to 
admit that the enunciations of all the theorems 


with which so many volumes are filled, are only 
indirect ways of saying that A is A ? 

No doubt we may refer back to axioms which 
are at the source of all these reasonings. If it is 
felt that they cannot be reduced to the principle of 
contradiction, if we decline to see in them any 
more than experimental facts which have no part 
or lot in mathematical necessity, there is still one 
resource left to us: we may class them among 
a priori synthetic views. But this is no solution 
of the difficulty it is merely giving it a name; and 
even if the nature of the synthetic views had no 
longer for us any mystery, the contradiction would 
not have disappeared ; it would have only been 
shirked. Syllogistic reasoning remains incapable 
of adding anything to the data that are given it ; 
the data are reduced to axioms, and that is all we 
should find in the conclusions. 

No theorem can be new unless a new axiom 
intervenes in its demonstration ; reasoning can 
only give us immediately evident truths borrowed 
from direct intuition; it would only be an inter 
mediary parasite. Should we not therefore have 
reason for asking if the syllogistic apparatus serves 
only to disguise what we have borrowed ? 

The contradiction will strike us the more if we 
open any book on mathematics; on every page the 
author announces his intention of generalising some 
proposition already known. Does the mathematical 
method proceed from the particular to the general, 
and, if so, how can it be called deductive ? 


Finally, if the science of number were merely 
analytical, or could be analytically derived from a / 
few synthetic intuitions, it seems that a sufficiently / 
powerful mind could with a single glance perceive 
all its truths ; nay, one might even hope that some 
day a language would be invented simple enough 
for these truths to be made evident to any person 
of ordinary intelligence. 

Even if these consequences are challenged, it 
must be granted that mathematical reasoning has 
of itself a kind of creative virtue, and is therefore to 
be distinguished from the syllogism. The difference 
must be profound. We shall not, for instance, 
find the key to the mystery in the frequent use of 
the rule by which the same uniform operation 
applied to two equal numbers will give identical 
results. All these modes of reasoning, whether or 
not reducible to the syllogism, properly so called, 
retain the analytical character, and ipso facto, lose 
their power. 


The argument is an old one. Let us see how 
Leibnitz tried to show that two and two make 
four. I assume the number one to be defined, and 
also the operation A +I i.e., the adding of unity 
to a given number x. These definitions, whatever 
they may be, do not enter into the subsequent 
reasoning. I next define the numbers 2, 3, 4 by 
the equalities : 

(i) 1 + 1 = 2; (2) 2 + 1 = 3; (3) a + 1^4 and in 


the same way I define the operation x + 2 by the 
relation; (4) ,t+2 = (*+i)+ I. 
Given this, we have : 

2+2 = (2+i) + i; (def. 4). 
(2+0 + 1=3+1 (def. 2). 

3 + 1=4 (def. 3). 

whence 2 + 2 = 4 Q.E.D. 

It cannot be denied that this reasoning is purely 
analytical. But if we ask a mathematician, he will 
reply: "This is not a demonstration properly so 
called; it is a verification." We have confined 
ourselves to bringing together one or other of two 
purely conventional definitions, and we have verified 
their identity ; nothing new has been learned. 
\Verification differs from proof precisely because it 
Is analytical, and because it leads to nothing. It 
leads to nothing because the conclusion is nothing 
but the premisses translated into another language. 
A real proof, on the other hand, is fruitful, because 
the conclusion is in a sense more general than the 
premisses. The equality 2 + 2 = 4 can be verified 
because it is particular. Each individual enuncia 
tion in mathematics may be always verified in 
the same way. But if mathematics could be 
reduced to a series of such verifications it 
would not be a science. A chess-player, for 
instance, does not create a science by winning a 
piece. There is no science but the science of the 
general. It may even be said that the object of 
the exact sciences is to dispense with these direct 



Let us now see the geometer at work, and try 
to surprise some of his methods. The task is 
not without difficulty; it is not enough to open a 
book at random and to analyse any proof we may 
come across. First of all, geometry must be ex 
cluded, or the question becomes complicated by 
difficult problems relating to the role of the 
postulates, the nature and the origin of the idea 
of space. For analogous reasons we cannot 
avail ourselves of the infinitesimal calculus. We 
must seek mathematical thought where it has 
remained pure i.e., in Arithmetic. But we 
still have to choose ; in the higher parts of 
the theory of numbers the primitive mathemati 
cal ideas have already undergone so profound 
an elaboration that it becomes difficult to analyse 

It is therefore at the beginning of Arithmetic 
that we must expect to find the explanation we 
seek ; but it happens that it is precisely in the 
proofs of the most elementary theorems that the 
authors of classic treatises have displayed the least 
precision and rigour. We may not impute this to 
them as a crime ; they have obeyed a necessity. 
Beginners are not prepared for real mathematical 
rigour ; they would see in it nothing but empty, 
tedious subtleties. It would be waste of time to 
try to make them more exacting ; they have to 
pass rapidly and without stopping over the road 


which was trodden slowly by the founders of the 

Why is so long a preparation necessary to 
habituate oneself to this perfect rigour, which 
it would seem should naturally be imposed on 
all minds ? This is a logical and psychological 
problem which is well worthy of study. But we 
shall not dwell on it ; it is foreign to our subject. 
All I wish to insist on is, that we shall fail in our 
purpose unless we reconstruct the proofs of the 
elementary theorems, and give them, not the rough 
form in which they are left so as not to weary the 
beginner, but the form which will satisfy the skilled 


I assume that the operation x+i has been 
denned; it consists in adding the number I to a 
given number x. Whatever may be said of this 
definition, it does not enter into the subsequent 

We now have to define the operation x + a, which 
consists in adding the number a to any given 
number x. Suppose that we have defined the 
operation x+(a-i); the operation x + a will be 
defined by the equality : (i) x + a = [x + (a - i)] + i. 
We shall know what x + a is when we know what 
x+(a-i) is, and as I have assumed that to start 
with we know what x+i is, we can define 
successively and " by recurrence " the operations 
x + 2, x + 3, etc. This definition deserves a moment s 


it is of a particular nature which 
distinguishes it even at this stage from the purely 
logical definition; the equality (i), in fact, contains 
an infinite number of distinct definitions, each 
having only one meaning when we know the 
meaning of its predecessor. 


Associative. I say that a-\-(b-\-c) = (a-\-b)-\-c; in 
fact, the theorem is true for c = i. It may then be 
written a-\-(b-\-i) = (a-{-b}-\-i; which, remembering 
the difference of notation, is nothing but the equality 
(i) by which I have just defined addition. Assume 
the theorem true for c=y, I say that it will be true for 
c = y+i. Let (a+b)+y=a+(b+y), it follows that 
i=[>+(& + y)]+i; or by def. (i)- 
(y + I )= a +(b + y + i)=a + [b+ (y + i)J , 
which shows by a series of purely analytical deduc 
tions that the theorem is true for y + i. Being 
true for c = i, we see that it is successively true for 
c = 2, c = 3, etc. 

Commutative. (i) I say that a + i = i + a. The 
theorem is evidently true for a = i ; we can verify 
by purely analytical reasoning that if it is true for 
a --= y it will be true for a = y + i. 1 Now, it is true for 
a=i, and therefore is true for a 2, a = 3, and so 
on. This is what is meant by saying that the 
proof is demonstrated " by recurrence." 

(2) I say that a + b^b + a. The theorem has just 

1 For (7+ i) | - i-(i +7)+ i = i -I- (7-1- 1}. [TR.] 


been shown to hold good for b=i, and it may be 
verified analytically that if it is true for b=ft } it 
will be true for b=fi+i. The proposition is thus 
established by recurrence. 


We shall define multiplication by the equalities: 
(i) aXi=a. (2) axb=[ax(b-i)]+a. Both of 
these include an infinite number of definitions; 
having defined aXi, it enables us to define in 
succession aX2, aX3, and so on. 


Distributive. I say that (a-\-b)Xc = (aXc) + 
(bXc). We can verify analytically that the theorem 
is true for c = i; then if it is true for c = y, it will be 
true for c = y-\-i. The proposition is then proved 
by recurrence. 

Commutative. (i) I say that aXi = iXa. The 
theorem is obvious for a = i. We can verify 
analytically that if it is true for a a, it will be 
true for <? -|- 1. 

(2) I say that aXb = bXa. The theorem has 
just been proved for b=i. We can verify analy 
tically that if it be true for &=/? it will be true for 


This monotonous series of reasonings may now 
be laid aside; but their very monotony brings 
vividly to light the process, which is uniform, 


and is met again at every step. The process is 
proof by recurrence. We first show that a 
theorem is true for ;z = i; we then show that if 
it is true for n I it is true for n, and we conclude 
that it is true for all integers. We have no\v seen 
how it may be used for the proof of the rules of 
addition and multiplication that is to say, for the 
rules of the algebraical calculus. This calculus 
is an instrument of transformation which lends 
itself to many more different combinations than 
the simple syllogism ; but it is still a purely analy 
tical instrument, and is incapable of teaching us 
anything new. If mathematics had no other in 
strument, it would immediately be arrested in its 
development; but it has recourse anew to the 
same process i.e., to reasoning by recurrence, and 
it can continue its forward march. Then if we 
look carefully, \ve find this mode of reasoning at 
every step, either under the simple form which we 
have just given to it, or under a more or less modi 
fied form. It is therefore mathematical reasoning 
par excellence, and we must examine it closer. 


The essential characteristic of reasoning by re 
currence is that it contains, condensed, so to 
speak, in a single formula, an infinite number of 
syllogisms. We shall see this more clearly if we 
enunciate the syllogisms one after another. They 
follow one another, if one may use the expression, 
in a cascade. The following are the hypothetical 


syllogisms: The theorem is true of the number I. 
Now, if it is true of i, it is true of 2; therefore it is 
true of 2. Now, if it is true of 2, it is true of 3; 
hence it is true of 3, and so on. We see that the 
conclusion of each syllogism serves as the minor 
of its successor. Further, the majors of all our 
syllogisms may be reduced to a single form. If 
the theorem is true of n - i, it is true of n. 

We see, then, that in reasoning by recurrence 
we confine ourselves to the enunciation of the 
minor of the first syllogism, and the general 
formula which contains as particular cases all the 
majors. This unending series of syllogisms is thus 
reduced to a phrase of a few lines. 

It is now easy to understand why every par 
ticular consequence of a theorem may, as I have 
above explained, be verified by purely analytical 
processes. If, instead of proving that our theorem 
is true for all numbers, we only wish to show that 
it is true for the number 6 for instance, it will be 
enough to establish the first five syllogisms in our 
cascade. We shall require 9 if we wish to prove 
it for the number 10; for a greater number we 
shall require more still; but however great the 
number may be we shall always reach it, and the 
analytical verification will always be possible. 
But however far we went we should never reach 
the general theorem applicable to all numbers, 
which alone is the object of science. To reach 
it we should require an infinite number of syllo 
gisms, and we should have to cross an abyss 


which the patience of the analyst, restricted to the 
resources of formal logic, will never succeed in 

I asked at the outset why we cannot conceive of 
a mind powerful enough to see at a glance the 
whole body of mathematical truth. The answer is 
now easy. A chess-player can combine for four or 
five moves ahead; but, however extraordinary a 
player he may be, he cannot prepare for more than 
a finite number of moves. If he applies his facul 
ties to Arithmetic, he cannot conceive its general 
truths by direct intuition alone; to prove even the 
smallest theorem he must use reasoning by re 
currence, for that is the only instrument which 
enables us to pass from the finite to the infinite. 
This instrument is always useful, for it enables us 
to leap over as many stages as we wish; it frees 
us from the necessity of long, tedious, and 
monotonous verifications which would rapidly 
become impracticable. Then when we take in 
hand the general theorem it becomes indispens 
able, for otherwise we should ever be approaching 
the analytical verification without ever actually 
reaching it. In this domain of Arithmetic we may 
think ourselves very far from the infinitesimal 
analysis, but the idea of mathematical infinity is 
already playing a preponderating part, and without 
it there would be no science at all, because there 
would be nothing general. 



The views upon which reasoning by recurrence 
is based may be exhibited in other forms; we may 
say, for instance, that in any finite collection of 
different integers there is always one which is 
smaller than any other. We may readily pass from 
one enunciation to another, and thus give our 
selves the illusion of having proved that reason 
ing by recurrence is legitimate. But we shall 
always be brought to a full stop we shall always 
come to an indemonstrable axiom, which will at 
bottom be but the proposition we had to prove 
translated into another language. We cannot there- 
(fore escape the conclusion that the rule of reason 
ing by recurrence is irreducible to the principle of 
contradiction. Nor can the rule come to us from 
i experiment. Experiment may teach us that the 
I rule is true for the first ten or the first hundred 
, numbers, for instance; it will not bring us to the 
indefinite series of numbers, but only to a more or 
less long, but always limited, portion of the series. 
Now, if that were all that is in question, the 
principle of contradiction would be sufficient, it 
would always enable us to develop as many 
syllogisms as we wished. It is only when it is a 
question of a single formula to embrace an infinite 
number of syllogisms that this principle breaks 
down, and there, too, experiment is powerless to 
rLfaid. This rule, inaccessible to analytical proof 
and to experiment, is the exact type of the a priori 


synthetic intuition. On the other hand, we 
cannot see in it a convention as in the case of the 
postulates of geometry. 

Why then is this view imposed upon us with 
such an irresistible weight of evidence ? It is 
because it is only the affirmation of the power of 
the mind which knows it can conceive of the 
indefinite repetition of the same act, when the act 
is once possible. The mind has a direct intuition 
of this power, and experiment can only be for it an 
opportunity of using it, and thereby of becoming 
conscious of it. 

But it will be said, if the legitimacy of reasoning 
by recurrence cannot be established by experiment 
alone, is it so with experiment aided by induction ? 
We see successively that a theorem is true of the 
number I, of the number 2, of the number 3, and 
so on the law is manifest, we say, and it is so on 
the same ground that every physical law is true 
which is based on a very large but limited number 
of observations. 

It cannot escape our notice that here is a 
striking analogy with the usual processes of 
induction. But an essential difference exists. 
Induction applied to the physical sciences is 
always uncertain, because it is based on the be 
lief in a general order of the universe, an order 
which is external to us. Mathematical induction 
i.e., proof by recurrence is, on the contrary, 
necessarily imposed on us, because it is only the 
affirmation of a property of the mind itself. 



Mathematicians, as I have said before, always 
endeavour to generalise the propositions they have 
obtained. To seek no further example, we have 
just shown the equality, a+i = i + a, and we then 
used it to establish the equality, a + b^b + a, which 
is obviously more general. Mathematics may, 
therefore, like the other sciences, proceed from the 
particular to the general. This is a fact which 
might otherwise have appeared incomprehensible 
to us at the beginning of this study, but w r hich has 
no longer anything mysterious about it, since we 
have ascertained the analogies between proof by 
recurrence and ordinary induction. 

No doubt mathematical recurrent reasoning and 
physical inductive reasoning are based on different 
foundations, but they move in parallel lines and in 
the same direction namely, from the particular 
to the general. 

Let us examine the case a little more closely. 

To prove the equality a + 2 = 2 + a (i), we need 

only apply the rule a + i =-- 1 + a, twice, and write 
a + 2 = a+ I + 1 = 1 + + 1 = 1 + i + a = 2 + a (2). 

The equality thus deduced by purely analytical 
means is not, however, a simple particular case. It 
is something quite different. We may not therefore 
even say in the really analytical and deductive 
part of mathematical reasoning that we proceed 
from the general to the particular in the 
ordinary sense of the words. The two sides of 


the equality (2) are merely more complicated 
combinations than the two sides of the equality 
(i), and analysis only serves to separate the ele 
ments which enter into these combinations and to 
study their relations. 

Mathematicians therefore proceed "by construc 
tion," they " construct " more complicated combina 
tions. When they analyse these combinations, 
these aggregates, so to speak, into their primitive 
elements, they see the relations of the elements 
and deduce the relations of the aggregates them 
selves. The process is purely analytical, but it is 
not a passing from the general to the particular, 
for the aggregates obviously cannot be regarded as 
more particular than their elements. 

Great importance has been rightly attached to 
this process of " construction," and some claim 
to see in it the necessary and sufficient condi 
tion of the progress of the exact sciences. 
Necessary, no doubt, but not sufficient ! For a 
construction to be useful and not mere waste of 
mental effort, for it to serve as a stepping-stone to 
higher things, it must first of all possess a kind of 
unity enabling us to see something more than the 
juxtaposition of its elements. Or more accurately, 
there must be some advantage in considering the 
construction rather than the elements themselves. 
What can this advantage be ? Why reason on a 
polygon, for instance, which is always decom 
posable into triangles, and not on elementary 
triangles ? It is because there are properties of 


pol} 7 gons of any number of sides, and they can be 
immediately applied to any particular kind of 
polygon. In most cases it is only after long efforts 
that those properties can be discovered, by directly 
studying the relations of elementary triangles. If 
the quadrilateral is anything more than the juxta 
position of two triangles, it is because it is of the 
polygon type. 

A construction only becomes interesting when 
it can be placed side by side with other analogous 
constructions for forming species of the same 
genus. To do this we must necessarily go back 
from the particular to the general, ascending one 
or more steps. The analytical process " by 
construction" does not compel us to descend, but 
it leaves us at the same level. We can only 
ascend by mathematical induction, for from it 
alone can we learn something new. Without the 
aid of this induction, which in certain respects 
differs from, but is as fruitful as, physical in 
duction, construction would be powerless to create 

Let me observe, in conclusion, that this in 
duction is only possible if the same operation can 
be repeated indefinitely. That is why the theory 
of chess can never become a science, for the 
different moves of the same piece are limited and 
do not resemble each other. 



IF we want to know what the mathematicians 
mean by a continuum, it is useless to appeal to 
geometry. The geometer is always seeking, more 
or less, to represent to himself the figures he is 
studying, but his representations are only instru 
ments to him ; he uses space in his geometry just 
as he uses chalk ; and further, too much import 
ance must not be attached to accidents which are 
often nothing more than the whiteness of the 

The pure analyst has not to dread this pitfall. 
He has disengaged mathematics from all extra 
neous elements, and he is in a position to answer 
our question : " Tell me exactly what this con 
tinuum is, about which mathematicians reason." 
Many analysts who reflect on their art have 
already done so -M. Tannery, for instance, in 
his Introduction a la theorie des Fonctiom d une 

Let us start with the integers. Between any 
two consecutive sets, intercalate one or more inter 
mediary sets, and then between these sets others 


again, and so on indefinitely. We thus get an 
unlimited number of terms, and these will be the 
numbers which we call fractional, rational, or 
commensurable. But this is not yet all ; between 
these terms, which, be it marked, are already 
infinite in number, other terms are intercalated, 
and these are called irrational or incommensurable. 

Before going any further, let me make a pre 
liminary remark. The continuum thus conceived 
is no longer a collection of individuals arranged in 
a certain order, infinite in number, it is true, but 
external the one to the other. This is not the 
ordinary conception in which it is supposed that 
between the elements of the continuum exists an 
intimate connection making of it one whole, in 
which the point has no existence previous to the 
line, but the line does exist previous to the point. 
Multiplicity alone subsists, unity has disappeared 
"the continuum is unity in multiplicity/ accord 
ing to the celebrated formula. The analysts have 
even less reason to define their continuum as they 
do, since it is always on this that they reason w r hen 
they are particularly proud of their rigour. It 
is enough to warn the reader that the real 
mathematical continuum is quite different from 
that of the physicists and from that of the 

It may also be said, perhaps, that mathematicians 
who are contented with this definition are the 
dupes of words, that the nature of each of these 
sets should be precisely indicated, that it should 


be explained how they are to be intercalated, and 
that it should be shown how it is possible to do it. 
This, however, would be wrong; the only property 
of the sets which comes into the reasoning is that of 
preceding or succeeding these or those other sets; 
this alone should therefore intervene in the defini 
tion. So we need not concern ourselves with the 
manner in which the sets are intercalated, and 
no one will doubt the possibility of the operation 
if he only remembers that " possible " in the 
language of geometers simply means exempt from 
contradiction. But our definition is not yet com 
plete, and we come back to it after this rather long 

Definition of Incommensurable^. The mathe 
maticians of the Berlin school, and Kronecker 
in particular, have devoted themselves to con 
structing this continuous scale of irrational and 
fractional numbers without using any other 
materials than the integer. The mathematical 
continuum from this point of view would be a 
pure creation of the mind in .which experiment 
would have no part. 

The idea of rational number not seeming to 
present to them any difficulty, they have confined 
their attention mainly to defining incommensurable 
numbers. But before reproducing their definition 
here, I must make an observation that will allay 
the astonishment which this will not fail to provoke 
in readers who are but little familiar with the 
habits of geometers. 


Mathematicians do not study objects, but the 
relations between objects; to them it is a matter 
of indifference if these objects are replaced by 
others, provided that the relations do not change. 
Matter does not engage their attention, they are 
interested by form alone. 

If we did not remember it, we could hardly 
understand that Kronecker gives the name of 
incommensurable number to a simple symbol 
that is to say, something very different from the 
idea we think we ought to have of a quantity 
which should be measurable and almost tangible. 

Let us see no\v what is Kronecker s definition. 
Commensurable numbers may be divided into 
classes in an infinite number of ways, subject 
to the condition that any number whatever 
of the first class is greater than any number 
of the second. It may happen that among the 
numbers of the first class there is one which is 
smaller than all the rest ; if, for instance, we 
arrange in the first class all the numbers greater 
than 2, and 2 itself, and in the second class all the 
numbers smaller than 2, it is clear that 2 will be 
the smallest of all the numbers of the first class. 
The number 2 may therefore be chosen as the 
symbol of this division. 

It may happen, on the contrary, that in the 
second class there is one which is greater than all 
the rest. This is what takes place, for example, 
if the first class comprises all the numbers greater 
than 2, and if, in the second, are all the numbers 


less than 2, and 2 itself. Here again the 
number 2 might be chosen as the symbol of this 

But it may equally well happen that we can find 
neither in the first class a number smaller than all 
the rest, nor in the second class a number greater 
than all the rest. Suppose, for instance, we 
place in the first class all the numbers whose 
squares are greater than 2, and in the second all 
the numbers whose squares are smaller than 2. 
We know that in neither of them is a number whose 
square is equal to 2. Evidently there will be in 
the first class no number which is smaller than all 
the rest, for however near the square of a number 
may be to 2, we can always find a commensur 
able whose square is still nearer to 2. From 
Kronecker s point of view, the incommensurable 
number v/2 is nothing but the symbol of this 
particular method of division of commensurable 
numbers ; and to each mode of repartition corre 
sponds in this way a number, commensurable or 
not, which serves as a symbol. But to be satisfied 
with this would be to forget the origin of these 
symbols; it remains to explain how we have been 
led to attribute to them a kind of concrete 
existence, and on the other hand, does not the 
difficulty begin with fractions ? Should we have 
the notion of these numbers if we did not previously 
know a matter which we conceive as infinitely 
divisible i.e., as a continuum ? 

The Physical Continuum. We are next led to ask 


if the idea of the mathematical continuum is not 
simply drawn from experiment. If that be so, the 
rough data of experiment, which are our sensations, 
could be measured. We might, indeed, be tempted 
to believe that this is so, for in recent times there 
has been an attempt to measure them, and a law 
has even been formulated, known as Fechner s 
law, according to which sensation is proportional 
to the logarithm of the stimulus. But if we 
examine the experiments by which the endeavour 
has been made to establish this law, we shall be 
led to a diametrically opposite conclusion. It has, 
for instance, been observed that a weight A of 10 
grammes and a weight B of n grammes produced 
identical sensations, that the weight B could no 
longer be distinguished from a weight C of 12 
grammes, but that the weight A was readily 
distinguished from the weight C. Thus the rough 
results of the experiments may be expressed by 
the following relations: A = B, B C, A < C, which 
may be regarded as the formula of the physical 
continuum. But here is an intolerable disagree 
ment with the law of contradiction, and the 
necessity of banishing this disagreement has com 
pelled us to invent the mathematical continuum. 
We are therefore forced to conclude that this 
notion has been created entirely by the mind, but 
it is experiment that has provided the opportunity. 
We cannot believe that two quantities which are 
equal to a third are not equal to one another, and 
we are thus led to suppose that A is different from 


B, and B from C, and that if we have not been 
aware of this, it is due to the imperfections of our 

The Creation of the Mathematical Continuum: First 
Stage. So far it would suffice, in order to account 
for facts, to intercalate between A and B a small 
number of terms which would remain discrete. 
What happens now if we have recourse to some 
instrument to make up for the weakness of our 
senses ? If, for example, we use a microscope ? 
Such terms as A and B, which before were 
indistinguishable from one another, appear now 
to be distinct : but between A and B, which are 
distinct, is intercalated another new term D, 
which we can distinguish neither from A nor from 
B. Although we may use the most delicate 
methods, the rough results of our experiments 
will always present the characters of the physical 
continuum with the contradiction which is inherent 
in it. We only escape from it by incessantly 
intercalating new T terms between the terms already 
distinguished, and this operation must be pursued 
indefinitely. We might conceive that it would be 
possible to stop if we could imagine an instrument 
powerful enough to decompose the physical con 
tinuum into discrete elements, just as the telescope 
resolves the Milky Way into stars. But this we 
cannot imagine ; it is always with our senses that 
we use our instruments ; it is with the eye that we 
observe the image magnified by the microscope, 
and this image must therefore always retain the 


characters of visual sensation, and therefore those 
of the physical continuum. 

Nothing distinguishes a length directly observed 
from half that length doubled by the microscope. 
The whole is homogeneous to the part ; and there 
is a fresh contradiction or rather there would be 
one if the number of the terms were supposed 
to be finite ; it is clear that the part containing 
less terms than the whole cannot be similar to the 
whole. The contradiction ceases as soon as the 
number of terms is regarded as infinite. There is 
nothing, for example, to prevent us from regarding 
the aggregate of integers as similar to the aggregate 
of even numbers, which is however only a part 
of it; in fact, to each integer corresponds another 
even number which is its double. But it is not 
only to escape this contradiction contained in the 
empiric data that the mind is led to create the 
concept of a continuum formed of an indefinite 
number of terms. 

Here everything takes place just as in the series 
of the integers. We have the faculty of conceiving 
that a unit may be added to a collection of units. 
Thanks to experiment, we have had the opportunity 
of exercising this faculty and are conscious of 
it ; but from this fact we feel that our power is 
unlimited, and that we can count indefinitely, 
although we have never had to count more than 
a finite number of objects. In the same way, as 
soon as we have intercalated terms between two 
consecutive terms of a series, we feel that this 


operation may be continued without limit, and 
that, so to speak, there is no intrinsic reason for 
stopping. As an abbreviation, I may give the 
name of a mathematical continuum of the first 
order to every aggregate of terms formed after the 
same law as the scale of commensurable numbers. 
If. then, we intercalate new sets according to tru: 
laws of incommensurable numbers, we obtain 
what may be called a continuum of the second 

Second Stage. We have only taken our first 
step. We have explained the origin of con 
tinuums of the first order ; we must now see why 
this is not sufficient, and why the incommensurable 
numbers had to be invented. 

If we try to imagine a line, it must have the 
characters of the physical continuum that is to 
say, our representation must have a certain 
breadth. Two lines will therefore appear to us 
under the form of two narrow bands, and if we 
are content with this rough image, it is clear 
that where two lines cross they must have so mo 
common part. But the pure geometer makes one 
further effort ; without entirely renouncing the 
aid of his senses, he tries to imagine a line without 
breadth and a point without size. This he can 
do only by imagining a line as the limit towards 
which tends a band that is growing thinner and 
thinner, and the point as the limit towards which 
is tending an area that is growing smaller and 
smaller. Our two bands, however narrow they 


may be, will always have a common area ; the 
smaller they are the smaller it will be, and its 
limit is what the geometer calls a point. This is 
why it is said that the two lines which cross 
must have a common point, and this truth seems 

But a contradiction would be implied if we 
conceived of lines as continuums of the first order 
i.e., the lines traced by the geometer should only 
give us points, the co-ordinates of which are 
rational numbers. The contradiction would be 
manifest if we were, for instance, to assert the 
existence of lines and circles. It is clear, in fact, 
that if the points whose co-ordinates are com 
mensurable were alone regarded as real, the 
in-circle of a square and the diagonal of the 
square would not intersect, since the co-ordinates 
of the point of intersection are incommensurable. 

Even then we should have only certain incom 
mensurable numbers, and not all these numbers. 

But let us imagine a line divided into two half- 
rays (demi-droites). Each of these half-rays will 
appear to our minds as a band of a certain breadth; 
these bands will fit close together, because there 
must be no interval between them. The common 
part will appear to us to be a point which will still 
remain as we imagine the bands to become thinner 
and thinner, so that we admit as an intuitive truth 
that if a line be divided into two half-rays the 
common frontier of these half-rays is a point. 
Here we recognise the conception of Kronecker, 


in which an incommensurable number was regarded 
as the common frontier of two classes of rational 
numbers. Such is the origin of the continuum of 
the second order, which is the mathematical con 
tinuum properly so called. 

Summary. To sum up, the mind has the faculty^ 
of creating symbols, and it is thus that it has con 
structed the mathematical continuum, which is 
only a particular system of symbols. The only 
limit to its power is the necessity of avoiding all 
contradiction ; but the mind only makes use of it 
when experiment gives a reason for it. 

In the case with which we are concerned, the 
reason is given by the idea of the physical con 
tinuum, drawn from the rough data of the senses. 
But this idea leads to a series of contradictions 
from each of which in turn we must be freed. 
In this way we are forced to imagine a more 
and more complicated system of symbols. That 
on which we shall dwell is not merely exempt 
from internal contradiction, it was so already at 
all the steps we have taken, but it is no longer in 
contradiction with the various propositions which 
are called intuitive, and which are derived from 
more or less elaborate empirical notions. 

Measurable Magnitude. So far we have not 
spoken of the measure of magnitudes; we can tell 
if any one of them is greater than any other, 
but we cannot say that it is two or three times 
as large. 

So far, I have only considered the order in which 


the terms are arranged ; but that is not sufficient 
for most applications. We must learn how to 
compare the interval which separates any two 
terms. On this condition alone will the con 
tinuum become measurable, and the operations 
of arithmetic -be applicable. This can only be 
done by the aid of a new and special con 
vention ; and this convention is, that in such a 
case the interval between the terms A and B is 
equal to the interval which separates C and D. 
For instance, we started with the integers, and 
between two consecutive sets we intercalated ;/ 
intermediary sets ; by convention we now assume 
these new sets to be equidistant. This is one 
of the ways of denning the addition of two 
magnitudes; for if the interval AB is by definition 
equal to the interval CD, the interval AD will by 
definition be the sum of the intervals AB and AC. 
This definition is very largely, but not altogether, 
arbitrary. It must satisfy certain conditions the 
commutative and associative laws of addition, for 
instance ; but, provided the definition we choose 
satisfies these laws, the choice is indifferent, and 
we need not state it precisely. 

Remarks. We are now in a position to discuss 
several important questions. 

(i) Is the creative power of the mind exhausted 
by the creation of the mathematical continuum ? 
The answer is in the negative, and this is shown 
in a very striking manner by the work of Du Bois 


We know that mathematicians distinguish 
between infinitesimals of different orders, and that 
infinitesimals of the second order are infinitely 
small, not only absolutely so, but also in relation 
to those of the first order. It is not difficult to 
imagine infinitesimals of fractional or even of 
irrational order, and here once more we find the 
mathematical continuum which has been dealt 
with in the preceding pages. Further, there are 
infinitesimals which are infinitely small with 
reference to those of the first order, and infinitely 
large with respect to the order i + e, however 
small e may be. Here, then, are new terms inter 
calated in our series; and if I may be permitted to 
revert to the terminology used in the preceding 
pages, a terminology which is very convenient, 
although it has not been consecrated by usage, I 
shall say that we have created a kind of con 
tinuum of the third order. 

It is an easy matter to go further, but it is idle 
to do so, for we would only be imagining symbols 
without any possible application, and no one will 
dream of doing that. This continuum of the third 
order, to which we are led by the consideration of 
the different orders of infinitesimals, is in itself 
of but little use and hardly worth quoting. 
Geometers look on it as a mere curiosity. The 
mind only uses its creative faculty when experi- 
ment requires it. 

(2) When we are once in possession of the 
conception of the mathematical continuum, are 


we protected from contradictions analogous to 
those which gave it birth ? No, and the follow 
ing is an instance : 

He is a savant indeed who will not take it as 
evident that every curve has a tangent ; and, in 
fact, if we think of a curve and a straight line as 
two narrow bands, we can always arrange them in 
such a way that they have a common part without 
intersecting. Suppose now that the breadth of 
the bands diminishes indefinitely : the common 
part will still remain, and in the limit, so to speak, 
the two lines will have a common point, although 
they do not intersect i.e., they will touch. The 
geometer who reasons in this way is only doing 
what we have done when we proved that two lines 
which intersect have a common point, and his 
intuition might also seem to be quite legitimate. 
But this is not the case. We can show that there 
are curves which have no tangent, if we define 
such a curve as an analytical continuum of the 
second order. No doubt some artifice analogous 
to those we have discussed above would enable us 
to get rid of this contradiction, but as the latter is 
only met with in very exceptional cases, we need 
not trouble to do so. Instead of endeavouring to 
reconcile intuition and analysis, we are content to 
sacrifice one of them, and as analysis must be 
flawless, intuition must go to the wall. 

The Physical Continuum of several Dimensions. 
We have discussed above the physical continuum 
as it is derived from the immediate evidence of our 


senses or, if the reader prefers, from the rough 
results of Fechner s experiments ; I have shown 
that these results are summed up in the contra 
dictory formulae : A = 13, B = C, A < C. 

Let us now see how this notion is generalised, 
and how from it may be derived the concept of 
continuums of several dimensions. Consider any 
two aggregates of sensations. We can either 
distinguish between them, or we cannot; just as in 
Fechner s experiments the weight of 10 grammes 
could be distinguished from the weight of 12 
grammes, but not from the weight of n grammes. 
This is all that is required to construct the con 
tinuum of several dimensions. 

Let us call one of these aggregates of sensations 
an element. It will be in a measure analogous to 
the point of the mathematicians, but will not be, 
however, the same thing. We cannot say that 
our element has no size, for we cannot distinguish 
it from its immediate neighbours, and it is thus 
surrounded by a kind of fog. If the astronomical 
comparison may be allowed, our "elements" 
would be like nebulae, whereas the mathematical 
points would be like stars. 

If this be granted, a system of elements will 
form a continuum, if we can pass from any one of 
them to any other by a series of consecutive 
elements such that each cannot be distinguished 
from its predecessor. This linear series is to the 
line of the mathematician what the isolated element 
was to the point. 


Before going further, I must explain what is 
meant by a cut. Let us consider a continuum C, 
and remove from it certain of its elements, which 
for a moment we shall regard as no longer belong 
ing to the continuum. We shall call the aggregate 
of elements thus removed a cut. By means of this 
cut, the continuum C will be subdivided into 
several distinct continuums ; the aggregate of 
elements which remain will cease to form a single 
continuum. There will then be on C two ele 
ments, A and B, which we must look upon as 
belonging to two distinct continuums; and we see 
that this must be so, because it will be impossible 
to find a linear series of consecutive elements of C 
(each of the elements indistinguishable from the 
preceding, the first being A and the last B), unless 
one of the elements of this series is indistinguisliablc 
from one of the elements of the cut. 

It may happen, on the contrary, that the cut 
may not be sufficient to subdivide the continuum 
C. To classify the physical continuums, we must 
first of all ascertain the nature of the cuts which 
must be made in order to subdivide them. If a 
physical continuum, C, may be subdivided by a cut 
reducing to a finite number of elements, all dis 
tinguishable the one from the other (and therefore 
forming neither one continuum nor several con 
tinuums), we shall call C a continuum of one 
dimension. If, on the contrary, C can only be sub 
divided by cuts which are themselves continuums, 
we shall say that C is of several dimensions; if 


the cuts are continuums of one dimension, then 
we shall say that C has two dimensions ; if cuts of 
two dimensions are sufficient, we shall say that C 
is of three dimensions, and so on. Thus the 
notion of the physical continuum of several dimen 
sions is defined, thanks to the very simple fact, 
that two aggregates of sensations may be dis 
tinguishable or indistinguishable. 

The Mathematical Continuum of Several Dimensions. 
The conception of the mathematical continuum 
of n dimensions may be led up to quite naturally 
by a process similar to that which we discussed at 
the beginning of this chapter. A point of such a 
continuum is defined by a system of n distinct 
magnitudes which we call its co-ordinates. 

The magnitudes need not always be measurable; 
there is, for instance, one branch of geometry 
independent of the measure of magnitudes, in 
which we are only concerned with knowing, for 
example, if, on a curve ABC, the point B is 
between the points A and C, and in which it is 
immaterial whether the arc A B is equal to or 
twice the arc B C. This branch is called Analysis 
Situs. It contains quite a large body of doctrine 
which has attracted the attention of the greatest 
geometers, and from which are derived, one from 
another, a" whole series of remarkable theorems. 
What distinguishes these theorems from those of 
ordinary geometry is that they are purely quali 
tative. They are still true if the figures are copied 
by an unskilful draughtsman, with the result that 



the proportions are distorted and the straight lines 
replaced by lines which are more or less curved. 

As soon as measurement is introduced into the 
continuum we have just defined, the continuum 
becomes space, and geometry is born. But the 
discussion of this is reserved for Part II. 




EVERY conclusion presumes premisses. These 
premisses are either self-evident and need no 
demonstration, or can be established only if based 
on other propositions ; and, as we cannot go back 
in this way to infinity, every deductive science, 
and geometry in particular, must rest upon a 
certain number of indemonstrable axioms. All 
treatises of geometry begin therefore with the 
enunciation of these axioms. But there is a 
distinction to be drawn between them. Some of 
these, for example, " Things which are equal to ) 
the same thing are equal to one another," are not 
propositions in geometry but propositions in 
analysis. I look upon them as analytical a priori 
intuitions, and they concern me no further. But 
I must insist on other axioms which are special 
to geometry. Of these most treatises explicitly^ 
enunciate three : (i) Only one line can pass 
through two points ; (2) a straight line is the 


shortest distance between two points ; (3) through 
one point only one parallel can be drawn to a 
given straight line. Although we generally dis 
pense with proving the second of these axioms, it 
would be possible to deduce it from the other two, 
and from those much more numerous axioms 
which are implicitly admitted without enuncia 
tion, as I shall explain further on. For a long 
time a proof of the third axiom known as Euclid s 
postulate was sought in vain. It is impossible to 
imagine the efforts that have been spent in pursuit 
of this chimera. Finally, at the beginning of the 
nineteenth century, and almost^ simultaneously, 
two scientists, a Russian and a Bulgxiria-n, Lobat- 
schewsky and Bolyai, show r ed irrefutably that this 
proof is impossible. They have nearly rid us of 
inventors of geometries without a postulate, and 
ever since the Academic des Sciences receives only 
about one or two new demonstrations a year. 
But the question was not exhausted, and it was 
not long before a great step was taken by the 
celebrated memoir of Riemann, entitled : Ueber 
die Hypothesen welche der Geometric zum Grunde 
liegen. This little work has inspired most of the 
recent treatises to which I shall later on refer, and 
among which I may mention those of Beltratni 
and Helmholtz. 

The Geometry of Lobatschewsky. If it were 
possible to deduce Euclid s postulate from the 
several axioms, it is evident that by rejecting 
the postulate and retaining the other axioms we 


should be led to contradictory consequences. It 
would be, therefore, impossible to found on those 
premisses a coherent geometry. Now, this is 
precisely what Lobatschewsky has done. He 
assumes at the outset that several parallels may 
be drawn through a point to a given straight line, 
and he retains all the other axioms of Euclid. 
From these hypotheses he deduces a series of 
theorems between which it is impossible to find 
any contradiction, and he constructs a geometry 
as impeccable in its logic as Euclidean geometry, N 
The theorems are very different, however, from 
those to which we are accustomed, and at first 
will be fourud a little disconcerting. For instance, 
the sum of the angles of a triangle is always less 
than two right angles, and the difference between 
that sum and two right angles is proportional to 
the area of the triangle. It is impossible to con 
struct a figure similar to a given figure but of 
different dimensions. If the circumference of a 
circle be divided into n equal parts, and tangents 
be drawn at the points of intersection, the n 
tangents will form a polygon if the radius of 
the circle is small enough, but if the radius is 
large enough they will never meet. We need not 
multiply these examples. Lobatschewsky s pro 
positions have no relation to those of Euclid, , 
but they are none the less logically interconnected. 
Riemann s Geometry. Let us imagine to our 
selves a world only peopled with beings of no 
J _nickness, and suppose these "infinitely flat" 


animals are all in one and the same plane, from 
which they cannot emerge. Let us further admit 
that this world is sufficiently distant from other 
worlds to be withdrawn from their influence, and 
while we are making these hypotheses it will not 
cost us much to endow these beings with reason 
ing power, and to believe them capable of making 
a geometry. In that case they will certainly 
attribute to space only two dimensions. But 
now suppose that these imaginary animals, \vhile. 
remaining without thickness, have the form of a 
spherical, and not of a plane figure, and are all on 
the same sphere, from which they cannot escape. 
What kind of a geometry will they construct ? In 
the first place, it is clear that they will attribute to 
space only two dimensions. The straight line to 
them will be the shortest distance from one point 
on the sphere to another that is to say, an arc of 
a great circle. In a word, their geometry will be 
spherical geometry. What they will call space 
will be the sphere on which they are confined, and 
on which take place all the phenomena with 
which they are acquainted. Their space will 
therefore be unbounded, since on a sphere one may 
always walk forward without ever being brought 

to a stop, and yet it will be finite; the end will 
never be found, but the complete tour can be 

made. Well, Riemann s geometry is spherical 
geometry extended to three dimensions. To con 
struct it, the German mathematician had first of 
all to throw overboard, not only Euclid s postulate 


but also the first axiom that only one line can pass 
through two points. On a sphere, through two 
given points, we can in general draw only one great 
circle which, as we have just seen, would be to 
our imaginary beings a straight line. But there 
was one exception. If the two given points are 
at the ends of a diameter, an infinite number of 
great circles can be drawn through them. In 
the same way, in Riemann s geometry at least in 
one of its forms through two points only one 
straight line can in general be drawn, but there are 
exceptional cases in which through two points 
an infinite number of straight lines can be drawn. 
So there is a kind of opposition between the 
geometries of Riemann and Lobatschewsky. For 
instance, the sum of the angles of a triangle is 
equal to two right angles in Euclid s geometry, 
less than two right angles in that of Lobat 
schewsky, and greater than two right angles in that 
of Riemann. The number of parallel lines that 
can be drawn through a given point to a given 
line is one in Euclid s geometry, none in Riemann s, 
and an infinite number in the geometry of Lobat- \\ 
schewsky. Let us add that Riemann s space is \ 
finite, although unbounded in the sense which we 
have above attached to these words. 

Surfaces with Constant Curvature. One objection, 
however, remains possible. There is no contradic 
tion between the theorems of Lobatschewsky and 
Riemann; but however numerous are the other 
consequences that these geometers have deduced 


from their hypotheses, they had to arrest their 
course before they exhausted them all, for the 
number would be infinite; and who can say that 
if they had carried their deductions further they 
would not have eventually reached some con- 

J ^/ ttu^tradiction ? This difficulty does not exist for 
**Riemann s geometry, provided it is limited to 
o dimensions. As we have seen, the two- 
dimensional geometry of Riemann, in fact, does 

kn, <ti" 1 **T n ot differ from spherical geometry, which is only a 
k rancn of ordinary geometry, and is therefore out- 
side all contradiction. Beltrami, by showing that 
Lobatschewsky s two-dimensional geometry was 
only a branch of ordinary geometry, has equally 
refuted the objection as far as it is concerned. 
This is the course of his argument: Let us con 
sider any figure whatever on a surface. Imagine 
this figure to be traced on a flexible and in- 
extensible canvas applied to the surface, in such 
a way that when the canvas is displaced and 
deformed the different lines of the figure change 
their form without changing their length. As a 
rule, this flexible and inextensible figure cannot be 
displaced without leaving the surface. But there 
are certain surfaces for which such a movement 
would be possible. They are surfaces of constant 
curvature. If we resume the comparison that we 
made just now, and imagine beings without thick 
ness living on one of these surfaces, they will 
regard as possible the motion of a figure all the 
lines of which remain of a constant length. Such 


a movement would appear absurd, on the other 
hand, to animals without thickness living on a 
surface of variable curvature. These surfaces of 
constant curvature are of two kinds. The 
curvature of some is positive, and they may be 
deformed so as to be applied to a sphere. The 
geometry of these surfaces is therefore reduced to 
spherical geometry- namely, Riemann s. The cur 
vature of others is negative. Beltrami has shown 
that the geometry of these surfaces is identical 
with that of Lobatschewsky. Thus the two- 
dimensional geometries of Riemann and Lobat- * 
schewsky are connected with Euclidean geometry. 
Interpretation of ^on-Euclidean Geometries. Thus 
vanishes the objection so far as two-dimensional 
geometries are concerned. It would be easy to 
extend Beltrami s reasoning to three-dimensional 
geometries, and minds which do not recoil before 
space of four dimensions will see no difficulty in 
it; but such minds are few in number. I prefer, 
then, to proceed otherwise. Let us consider a 
certain plane, which I shall call the fundamental 
plane, and let us construct a kind of dictionary by 
making a double series of terms written in two 
columns, and corresponding each to each, just as 
in ordinary dictionaries the words in two languages 
which have the same signification correspond to 
one another: 
Space The portion of space situated 

above the fundamental 



Plane ... 





Distance between 
two points 

Sphere cutting orthogonally 
the fundamental plane. 

Circle cutting orthogonally 
the fundamental plane. 




Logarithm of the anharmonic 

ratio of these two points 
and of the intersection 
of the fundamental plane 
with the circle passing 
through these two points 
and cutting it orthogon 

Let us now take Lobatschewsky s theorems and 
translate them by the aid of this dictionary, as we 
would translate a German text with the aid of 
a German - French dictionary. We shall then 
obtain the theorems of ordinary geometry. For 
instance, Lobatschewsky s theorem: "The sum of 
the angles of a triangle is less than two right 
angles," may be translated thus: "If a curvilinear 
triangle has for its sides arcs of circles which if 
produced would cut orthogonally the fundamental 
plane, the sum of the angles of this curvilinear 
triangle will be less than two right angles." Thus, 
however far the consequences of Lobatschewsky s 
hypotheses are carried, they will never lead to a 


contradiction; in fact, if two of Lobatschewsky s 
theorems were contradictory, the translations of 
these tw T o theorems made by the aid of our 
dictionary would be contradictory also. But 
these translations are theorems of ordinary 
geometry, and no one doubts that ordinary 
geometry is exempt from contradiction. Whence 
is the certainty derived, and how far is it justified? 
That is a question upon which I cannot enter 
here, but it is a very interesting question, and I 
think not insoluble. Nothing, therefore, is left of 
the objection I formulated above. But this is not 
all. Lobatschewsky s geometry being susceptible 
of a concrete interpretation, ceases to be a useless 
logical exercise, and may be applied. I have no 
time here to deal with these applications, nor 
with what Herr Klein and myself have done by 
using them in the integration of linear equations. 
Further, this interpretation is not unique, and 
several dictionaries may be constructed analogous 
to that above, which will enable us by a simple 
translation to convert Lobatschewsky s theorems 
into the theorems of ordinary geometry. 

Implicit Axioms. Are the axioms implicitly 
enunciated in our text-books the only foundation 
of geometry ? We may be assured of the contrary 
when we see that, when they are abandoned one 
after another, there are still left standing some 
propositions which are common to the geometries 
of Euclid, Lobatschewsky, and Riemann. These 
propositions must be based on premisses that 


geometers admit without enunciation. It is in 
teresting to try and extract them from the classical 

John Stuart Mill asserted 1 that every definition 
contains an axiom, because by denning we im 
plicitly affirm the existence of the object defined. 
That is going rather too far. It is but rarely in 
mathematics that a definition is given without 
following it up by the proof of the existence of the 
object defined, and when this is not done it is 
generally because the reader can easily supply 
it; and it must not be forgotten that the word 
"existence" has not the same meaning when it 
refers to a mathematical entity as when it refers to 
a material object. 

A mathematical entity exists provided there is 
no contradiction implied in its definition, either in 
itself, or with the propositions previously admitted. 
But if the observation of John Stuart Mill cannot 
be applied to all definitions, it is none the less true 
for some of them. A plane is sometimes defined 
in the following manner: The plane is a surface 
such that the line which joins any two points 
upon it lies wholly on that surface. Now, there is 
obviously a new axiom concealed in this definition. 
It is true we might change it, and that would be 
preferable, but then we should have to enunciate 
the axiom explicitly. Other definitions may give 
rise to no less important reflections, such as, for 
example, that of the equality of two figures. Two 

1 Logic > c. viii., cf. Definitions, 5-6. TR. 


figures are equal when they can be superposed. 
To superpose them, one of them must be displaced 
until it coincides with the other. But how must 
it be displaced ? If we asked that question, no 
doubt we should be told that it ought to be done 
without deforming it, and as an invariable solid is 
displaced. The vicious circle would then be evi 
dent. As a matter of fact, this definition defines 
nothing. It has no meaning to a being living in a 
world in which there are only fluids. If it seems 
clear to us, it is because we are accustomed to the 
properties of natural solids which do not much 
differ from those of the ideal solids, all of whose 
dimensions are invariable. However, imperfect as 
it may be, this definition implies an axiom. The 
possibility of the motion of an invariable figure is 
not a self-evident truth. At least it is only so in 
the application to Euclid s postulate, and not as an 
analytical a priori intuition would be. More 
over, when we study the definitions and the proofs 
of geometry, we see that we are compelled to 
admit without proof not only the possibility of 
this motion, but also some of its properties. This 
first arises in the definition of the straight line. 
Many defective definitions have been given, but 
the true one is that which is understood in all the 
proofs in which the straight line intervenes. " It 
may happen that the motion of an invariable figure 
may be such that all the points of a line belonging 
to the figure are motionless, while all the points 
situate outside that line are in. motion. Such a 


line would be called a straight line/ We have 
deliberately in this enunciation separated the 
definition from the axiom which it implies. Many 
proofs such as those of the cases of the equality of 
triangles, of the possibility of drawing a perpen 
dicular from a point to a straight line, assume pro 
positions the enunciations of which are dispensed 
with, for they necessarily imply that it is possible 
to move a figure in space in a certain way. 

The Fourth Geometry. Among these explicit 
axioms there is one which seems to me to deserve 
some attention, because when we abandon it we 
can construct a fourth geometry as coherent as 
those of Euclid, Lobatschewsky, and Riemann. 
To prove that we can always draw a perpendicular 
at a point A to a straight line A B, we consider a 
straight line A C movable about the point A, and 
initially identical with the fixed straight line A B. 
We then can make it turn about the point A until 
it lies in A B produced. Thus we assume two 
propositions first, that such a rotation is possible, 
and then that it may continue until the two lines 
lie the one in the other produced. If the first 
point is conceded and the second rejected, we are 
led to a series of theorems even stranger than those 
of Lobatschewsky and Riemann, but equally free 
from contradiction. I shall give only one of these 
theorems, and I shall not choose the least remark 
able of them. A real straight line may be perpen 
dicular to itself. 

Lie s Theorem. The number of axioms implicitly 


introduced into classical proofs is greater than 
necessary, and it would be interesting to reduce 
them to a minimum. It may be asked, in the first 
place, if this reduction is possible if the number of 
necessary axioms and that of imaginable geometries 
is not infinite? A theorem due to Sophus Lie is of 
weighty importance in this discussion. It may be 
enunciated in the following manner: Suppose the 
following premisses are admitted: (i) space has n 
dimensions; (2) the movement of an invariable 
figure is possible; (3) p conditions are necessary to 
determine the position of this figure in space. 

The number of geometries compatible with these 
premisses will be limited. I may even add that if n 
is given, a superior limit can be assigned to p. If, 
therefore, the possibility of the movement is 
granted, we can only invent a finite and even 
a rather restricted number of three-dimensional 

Riemann s Geometries. However, this result 
ssems contradicted by Riemann, for that scientist 
constructs an infinite number of geometries, and 
that to which his name is usually attached is only 
a particular case of them. All depends, he says, 
on the manner in which the length of a curve is 
defined. Now, there is an infinite number of ways 
of defining this length, and each of them may be 
the starting-point of a new geometry. That is 
perfectly true, but most of these definitions are in 
compatible with the movement of a variable figure 
such as we assume to be possible in Lie s theorem. 


These geometries of Riemann, so interesting on 
various grounds, can never be, therefore, purely 
analytical, and would not lend themselves to 
proofs analogous to those of Euclid. 

"On the Nature of Axioms. Most mathematicians 
regard Lobatschewsky s geometry as a mere logical 
curiosity. Some of them have, however, gone 
further. If several geometries are possible, they 
say, is it certain that our geometry is the one that 
is true ?^ Experiment no doubt teaches us that the 
sum of the angles of a triangle is equal to two 
right angles, but this is because the triangles we 
deal with are too small. According to Lobat- 
schewsky, the difference is proportional to the area 
of the triangle, and will not this become sensible 
when we operate on much larger triangles, and 
when our measurements become more accurate ? 
-; Euclid s geometry would thus be a provisory 
geometry. Now, to discuss this view we must 
first of all ask ourselves, what is the nature of 
geometrical axioms ? Are they synthetic a priori 
intuitions, as Kant affirmed ? They would then 
be imposed upon us with such a force that we 
could not conceive of the contrary proposition, nor 
could we build upon it a theoretical edifice. There 
would be no non-Euclidean geometry. To con 
vince ourselves of this, let us take a true synthetic 
a priori intuition the following, for instance, which 
played an important part in the first chapter: If 
a theorem is true for the number i, and if it has 
oeen proved that it is true of + i, provided it is 


true of n, it will be true for all positive integers. 
Let us next try to get rid of this, and while reject 
ing this proposition let us construct a false 
arithmetic analogous to non-Euclidean geometry. 
We shall not be able to do it. We shall be even 
tempted at the outset to look upon these intui 
tions as analytical. Besides, to take up again 
our fiction of animals without thickness, we can 
scarcely admit that these beings, if their minds 
are like ours, would adopt the Euclidean geometry, 
which would be contradicted by all their experi 
ence. Ought we, then, to conclude that the" 
axioms of geometry are experimental truths ? 
But we do not make experiments on ideal lines or 
ideal circles; w r e can only make them on material 
objects. On what, therefore, would experiments 
serving as a foundation for geometry be based ? 
The answer is easy. We have seen above that we 
constantly reason as if the geometrical figures 
behaved like solids. What geometry would borrow 
from experiment would be therefore the pro 
perties of these bodies. The properties of light 
and its propagation in a straight line have also 
given rise to some of the propositions of geometry, 
and in particular to those of projective geometry, 
so that from that point of view one would be 
tempted to say that metrical geometry is the study 
of solids, and projective geometry that of light. 
But a difficulty remains, and is unsurmountable. 
If geometry were an experimental science, it w T o 
not be an exact science. It would be subjected to ! 



continual revision. Nay, it would from that day 
forth be proved to be erroneous, for we know that 
no rigorously invariable solid exists/" The geo 
metrical axioms are therefore neither synthetic a priori 
intuitions nor experimental facts. They are conven- 
\ tions. Our choice among all possible conventions 
/is guided by experimental facts; but it remains 
free, and is only limited by the necessity of avoid 
ing every contradiction, and thus it is that pos 
tulates may remain rigorously true even when the 
experimental laws which have determined their 
adoption are only approximate. In other words, 
the axioms of geometry (I do not speak of those of 
arithmetic) are only definitions in disguise. What, 
then, are we to think of the question : Is 
Euclidean geometry true ? It has no meaning. 
We might as well ask if the metric system is true, 
and if the old weights and measures are false; if 
Cartesian co-ordinates are true and polar co 
ordinates false. jOne geometry cannot be more 
true than another; it can only be more convenient. 
| Now, Euclidean geometry is, and will remain, the 
\ most convenient: ist, because it is the simplest, 
") \ and it is not so only because of our mental habits 
, . or because of the kind of direct intuition that we 
have of Euclidean space ; it is the simplest in 
\ itself, just as a polynomial of the first degree is 
simpler than a polynomial of the second degree; 
2nd, because it sufficiently agrees with the pro- 
( * perties of natural solids, those bodies which we 
\. can compare and measure by means of our senses. 



LET us begin with a little paradox. Beings whose 
minds were made as ours, and with senses like 
ours, but without any preliminary education, 
might receive from a suitably-chosen external 
world impressions which would lead them to 
construct a geometry other than that of Euclid, 
and to localise the phenomena of this external 
world in a non-Euclidean space, or even in space 
of four dimensions. As for us, whose education 
has been made by our actual world, if we were 
suddenly transported into this new world, we 
should have no difficulty in referring phenomena 
to our Euclidean space. Perhaps somebody may 
appear on the scene some day who will devote his 
life to it, and be able to represent to himself the 
fourth dimension. 

Geometrical Space and Representative Space. It is 
often said that the images we form of external 
objects are localised in space, and even that they 
can only be formed on this condition. It is also 
said that this space, which thus serves as a kind of 
framework ready prepared for our sensations and 
representations, is identical with the space of the 


geometers, having all the properties of that space. 
To all clear-headed v men who think in this way, 
the preceding statement might well appear extra 
ordinary; but it is as well to see if they are not 
the victims of some illusion which closer analysis 
may be able to dissipate. In the first place, what 
are the properties of space properly so called ? 
I mean of that space which is the object of 
geometry, and which I shall call geometrical 
space. The following are some of the more 

ist, it is continuous; 2nd, it is infinite; 3rd, it 
is of three dimensions; 4th, it is homogeneous 
that is to say, all its points are identical one 
with another; 5th, it is isotropic. Compare this 
now with the framework of our representations 
and sensations, which I may call representative 

Visual Space. First of all let us consider a 
purely visual impression, due to an image formed 
on the back of the retina. A cursory analysis shows 
us this image as continuous, but as possessing only 
two dimensions, which already distinguishes purely 
visual from what may be called geometrical space. 
On the other hand, the image is enclosed within 
a limited framework ; and there is a no less 
important difference: this pure visual space is not 
homogeneous. All the points on the retina, apart 
from the images which may be formed, do not 
play the same role. The yellow spot can in no 
way be regarded as identical with a point on the 


edge of the retina. Not only does the same object 
produce on it much brighter impressions, but in 
the whole of the limited framework the point 
which occupies the centre will not appear identical 
with a point near one of the edges. Closer 
analysis no doubt would show us that this con 
tinuity of visual space and its two dimensions are 
but an illusion. It would make visual space even 
more different than before from geometrical space, 
but we may treat this remark as incidental. 

However, sight enables us to appreciate dis 
tance, and therefore to perceive a third dimension. 
But every one knows that this perception of thei t *) })" 
third dimension reduces to a sense of the effort of 
accommodation which must be made, and to a 
sense of the convergence of the two eyes, that 
must take place in order to perceive an object, 
distinctly. These are muscular sensations quite 
different from the visual sensations which have 
given us the concept of the two first dimensions. 
The third dimension will therefore not appear to us 
as playing the same role as the two others. What 
may be called complete visual space is not therefore 
an isotropic space. It has, it is true, exactly 
three dimensions; which means that the elements 
of our visual sensations (those at least which 
concur in forming the concept of extension) will 
be completely defined if we know three of them; 
or, in mathematical language, they will be func 
tions of three independent variables. But let us 
look at the matter a little closer. The third 


dimension is revealed to us in two different ways: 
by the effort of accommodation, and by the con 
vergence of the eyes. No doubt these two in 
dications are always in harmony; there is between 
them a constant relation; or, in mathematical 
language, the two variables which measure these 
two muscular sensations do not appear to us as 
independent. Or, again, to avoid an appeal to 
mathematical ideas which are already rather too 
refined, we may go back to the language of the 
preceding chapter and enunciate the same fact as 
follows: If two sensations of convergence A and 
B are indistinguishable, the two sensations of 
accommodation A and B which accompany them 
respectively will also be indistinguishable. But 
that is, so to speak, an experimental fact. Nothing 
prevents us a priori from assuming the contrary, 
and if the contrary takes place, if these two 
muscular sensations both vary independently, we 
must take into account one more independent 
variable, and complete visual space will appear 
to us as a physical continuum of four dimensions. 
And so in this there is also a fact of external 
experiment. Nothing prevents us from assuming 
that a being with a mind like ours, with the same 
sense-organs as ourselves, may be placed in a world 
in which light would only reach him after being 
passed through refracting media of complicated 
form. The two indications which enable us to 
appreciate distances would cease to be connected 
by a constant relation. A being educating his 


senses in such a world would no doubt attribute 
four dimensions to complete visual space. 

Tactile and Motor Space. "Tactile space" is 
more complicated still than visual space, and differs 
even more widely from geometrical space. It is 
useless to repeat for the sense of touch my remarks 
on the sense of sight. But outside the data of 
sight and touch there are other sensations which 
contribute as much and more than they do to the 
genesis of the concept of space. They are those 
which everybody knows, which accompany all our 
movements, and which we usually call muscular 
sensations. The corresponding framework con 
stitutes what may be called motor space. Each 
muscle gives rise to a special sensation which may 
be increased or diminished so that the aggregate 
of our muscular sensations will depend upon as 
many variables as we have muscles. From this 
point of view motor space would have as many dimen 
sions as we have muscles. I know that it is said 
that if the muscular sensations contribute to form 
the concept of space, it is because we have the 
sense of the direction of each movement, and that 
this is an integral part of the sensation. If this 
were so, and if a muscular sense could not be 
aroused unless it were accompanied by this geo 
metrical sense of direction, geometrical space 
would certainly be a form imposed upon our 
sensitiveness. But I do not see this at all when 
I analyse my sensations. What I do see is th-at 
the sensations which correspond to movements in 


the same direction are connected in my mind by a 
simple association of ideas. It is to this association 
that what we call the sense of direction is reduced. 
We cannot therefore discover this sense in a single 
sensation. This association is extremely complex, 
for the contraction of the same muscle may cor 
respond, according to the position of the limbs, 
to very different movements of direction. More 
over, it is evidently acquired ; it is like all 
associations of ideas, the result of a habit. This 
habit itself is the result of a very large number of 
experiments, and no doubt if the education of our 
senses had taken place in a different medium, 
where we would have been subjected to different 
impressions, then contrary habits would have been 
acquired, and our muscular sensations would have 
been associated according to other laws. 

Characteristics of Representative Space. Thus re 
presentative space in its triple form visual, 
tactile, and motor differs essentially from geo 
metrical space. It is neither homogeneous nor 
isotropic; we cannot even say that it is of three 
dimensions. It is often said that we " project " 
into geometrical space the objects of our external 
perception; that we "localise" them. Now, has 
that any meaning, and if so what is that meaning ? 
Does it mean that we represent to ourselves ex 
ternal objects in geometrical space ? Our repre 
sentations are only the reproduction of our sensa 
tions; they canSe*- tnerefore be arranged in the 
same framework that is to say, in representative 


space. It is also just as impossible for us to repre 
sent to ourselves external objects in geometrical^ 
space, as it is impossible for a painter to paint on 
a flat surface objects with their three dimensions. 
Representative space is only an image of geo 
metrical space, an image deformed by a kind of 
perspective, and we can only represent to our 
selves objects by making them obey the laws of 
this perspective. Thus we do not represent to our 
selves external bodies in geometrical space, but we 
reason about these bodies as if they were situated 
in geometrical space. When it is said, on the 
other hand, that we "localise" such an object in 
such a point of space, what does it mean ? // 
simply means that we represent to ourselves the move 
ments that must take place to reach that object. And 
it does not mean that to represent to ourselves 
these movements they must be projected into 
space, and that the concept of space must therefore 
pre-exist. When I say that we represent to our 
selves these movements, I only mean that we 
represent to ourselves the muscular sensations 
which accompany them, and which have no 
geometrical character, and which therefore in no 
way imply the pre-existence of the concept of 

Changes of State and Changes of Position. But, 
it may be said, if the concept of geometrical space 
is not imposed upon our minds, and if, on the 
other hand, none of our sensations can furnish us 
with that concept, how then did it ever come into 


existence ? This is what we have now to examine, 
and it will take some time; but I can sum up in a 
few words the attempt at explanation which I am 
going to develop. None of our sensations, if isolated, 
could have brought us to the concept of space ; we are 
brought to it solely by studying the laws by which those 

sensations succeed one another. We see at first that 
. . r- -lta ^-^^* - ~^^ 

our impressions are subject to change; but among 

the changes that we ascertain, we are very soon 
led to make a distinction. Sometimes we say that 
\ thejDbjects, the causes of these impressions, have 
changed their state, sometimes that they have 
changed their position, that they have only been 
displaced. Whether an object changes its state or 
only its position, this is always translated for us in 
the same manner, by a modification in an aggregate 
of impressions. How then have we been enabled 
to distinguish them ? If there were only change 
of position, we could restore the primitive aggre 
gate of impressions by making movements which 
would confront us with the movable object in 
the same relative situation. W T e thus correct the 
modification which was produced, and we re 
establish the initial state by an inverse modifica 
tion. If, for example, it were a question of the 
sight, and if an object be displaced before our 
eyes, we can " follow it with the eye," and retain 
its image on the same point of the retina by 
appropriate movements of the eyeball. These 
movements we are conscious of because they are 
voluntary, and because they are accompanied by 


muscular sensations. But that does not mean 
that we represent them to ourselves in geometrical 
space. So what characterises change of position, 
what distinguishes it from change of state, is that 
it can always be corrected by this means. It may 
therefore happen that we pass from the aggregate 
of impressions A to the aggregate B in two differ 
ent ways. First, involuntarily and without ex 
periencing muscular sensations which happens 
when it is the object that is displaced; secondly, 
voluntarily, and with muscular sensation which 
happens when the object is motionless, but when 
we displace ourselves in such a way that the 
object has relative motion with respect to us. If 
this be so, the translation of the aggregate A to 
the aggregate B is only a change of position. It 
follows that sight and touch could not have given 
us the idea of space without the help of the 
" muscular sense." Not only could this concept 
not be derived from a single sensation, or even from 
a series of sensations; but a motionless being could 
never have acquired it, because, not being able to 
correct by his movements the effects of the change 
of position of external objects, he would have had 
no reason to distinguish them from changes of 
state. Nor would he have been able to acquire 
it if his movements had not been voluntary, 
or if they were unaccompanied by any sensations 

Conditions of Compensation. How is such a 
compensation possible in such a way that two 


changes, otherwise mutually independent, may be 
reciprocally corrected ? A mind already familiar 
with geometry would reason as follows: If there 
is to be compensation, the different parts of the 
external object on the one hand, and the different 
organs of our senses on the other, must be in the 
same relative position after the double change. 
And for that to be the case, the different parts of 
the external body on the one hand, and the differ 
ent organs of our senses on the other, must have 
the same relative position to each other after the 
double change; and so with the different parts of 
our body with respect to each other. In other 
words, the external object in the first change must 
be displaced as an invariable solid would be dis 
placed, and it must also be so with the whole of our 
body in the second change, which is to correct the 
first. Under these conditions compensation may 
be produced. But we who as yet know nothing of 
geometry, whose ideas of space are not yet formed, 
we cannot reason in this way we cannot predict 
a priori if compensation is possible. But experi 
ment shows us that it sometimes does take place, 
and we start from this experimental fact in order 
to distinguish changes of state from changes of 

Solid Bodies and Geometry. Among surrounding 
objects there are some which frequently experience 
displacements that may be thus corrected by a 
correlative movement of our own body namely, 
solid bodies. The other objects, whose form is vari- 


able, only in exceptional circumstances undergo 
similar displacement (change of position without 
change of form). When the displacement of a 
body takes place with deformation, we can no 
longer by appropriate movements place the organs 
of our body in the same relative situation with 
respect to this body; we can no longer, therefore, 
reconstruct the primitive aggregate of impressions. 

It is only later, and after a series of new r experi 
ments, that we learn how to decompose a body of 
variable form into smaller elements such that each 
is displaced approximately according to the same 
laws as solid bodies. We thus distinguish "de 
formations" from other changes of state. In these 
deformations each element undergoes a simple 
change of position which may be corrected; but the 
modification of the aggregate is more profound, 
and can no longer be corrected by a correlative 
movement. Such a concept is very complex even 
at this stage, and has been relatively slow in 
its appearance. It would not have been conceived 
at all had not the observation of solid bodies shown 
us beforehand how to distinguish changes of 

//, then, there were no solid bodies in nature there 
would be no geometry. 

Another remark deserves a moment s attention. 
Suppose a solid body to occupy successively the 
positions a and /?; in the first position it will give 
us an aggregate of impressions A, and in the second 
position the aggregate of impressions B. Now let 


there be a second solid body, of qualities entirely 
different from the first of different colour, for 
instance. Assume it to pass from the position u, 
where it gives us the aggregate of impressions A to 
the position /?, where it gives the aggregate of 
impressions B . In general, the aggregate A will 
have nothing in common with the aggregate A , 
nor will the aggregate B have anything in common 
with the aggregate B . The transition from the 
aggregate A to the aggregate B, and that of the 
aggregate A to the aggregate B , are therefore 
two changes which in themselves have in general 
nothing in common. Yet \ve consider both 
these changes as displacements; and, further, we 
consider them the same displacement. How can 
this be ? It is simply because they may be both 
corrected by the same correlative movement of our 
body. " Correlative movement," therefore, con 
stitutes the sole connection between two phenomena 
which otherwise we should never have dreamed of 

On the other hand, our body, thanks to the 
number of its articulations and muscles, may have 
a multitude of different movements, but all are not 
capable of " correcting " a modification of external 
objects ; those alone are capable of it in which 
our whole body, or at least all those in which 
the organs of our senses enter into play are 
displaced en bloc i.e., without any variation of 
their relative positions, as in the case of a solid 


To sum up : 

1. In the first place, we distinguish two categories 
of phenomena : The first involuntary, unaccom 
panied by muscular sensations, and attributed to 
external objects they are external changes; the 
second, of opposite character and attributed to the 
movements of our own body, are internal changes. 

2. We notice that certain changes of each in 
these categories may be corrected by a correlative 
change of the other category. 

3. We distinguish among external changes those 
that have a correlative in the other category 
which we call displacements; and in the same way 
we distinguish among the internal changes those 
which have a correlative in the first category. 

Thus by means of this reciprocity is defined a 
particular class of phenomena called displace 
ments. The laws of these phenomena are the object of 

Law of Homogeneity. The first of these laws 
is the law of homogeneity. Suppose that by an 
external change we pass from the aggregate of 
impressions A to the aggregate B, and that then 
this change is corrected by a correlative 
voluntary movement ft so that we are brought 
back to the aggregate A. Suppose now r that 
another external change a brings us again from 
the aggregate A to the aggregate B. Experiment 
then shows us that this change u , like the change 
u, may be corrected by a voluntary correlative 
movement /3 , and that this movement // corre- 


spends to the same muscular sensations as the 
movement fi which corrected a. 

This fact is usually enunciated as follows : Space 
is homogeneous and isotropic. We may also say that a 
movement which is once produced may be repeated 
a second and a third time, and so on, without any 
variation of its properties. In the first chapter, in 
which \ve discussed the nature of mathematical 
reasoning, we saw the importance that should be 
attached to the possibility of repeating the same 
operation indefinitely. The virtue of mathematical 
reasoning is due to this repetition; by means of the 
law of homogeneity geometrical facts are appre 
hended. To be complete, to the law of homo 
geneity must be added a multitude of other laws, 
into the details of which I do not propose to enter, 
but which mathematicians sum up by saying that 
these displacements form a "group." 

The Non-Euclidean World. -If geometrical space 
were a framework imposed on each of our repre 
sentations considered individually, it would be 
impossible to represent to ourselves an image 
without this framework, and we should be quite 
unable to change our geometry. But this is not 
the case ; geometry is only the summary of the 
laws by which these images succeed each other. 
There is nothing, therefore, to prevent us from 
imagining a series of representations, similar in 
every way to our ordinary representations, but 
succeeding one another according to laws which 
differ from those to which we are accustomed. We 


may thus conceive that beings whose education 
has taken place in a medium in which those laws 
would be so different, might have a very different 
geometry from ours. 

Suppose, for example, a world enclosed in a large 
sphere and subject to the following laws : The ^ 
temperature is not uniform; it is greatest at the^uir" 
centre, and gradually decreases as we move towards 
the circumference of the sphere, where it is absolute 
zero. The law of this temperature is as follows : 
If R be the radius of the sphere, and r the distance 
of the point considered from the centre, the abso 
lute temperature will be proportional to R 2 r 2 . 
Further, I shall suppose that in this world all bodies 
have the same co-efficient of dilatation, so that the 
linear dilatation of any body is proportional to its 
absolute temperature. Finally, I shall assume that 
a body transported from one point to another of 
different temperature is instantaneously in thermal 
equilibrium with its new environment. There is 
nothing in these hypotheses either contradictory 
or unimaginable. A moving object will become 
smaller and smaller as it approaches the circum 
ference of the sphere. Let us observe, in the first 
place, that although from the point of view of our 
ordinary geometry this w T orld is finite, to its inhabit 
ants it will appear infinite. As they approach the 
surface of the sphere they become colder, and at 
the same time smaller and smaller. The steps 
they take are therefore also smaller and smaller, 
so that they can never reach the boundary of the 



// sphere. If to us geometry is only the study of the 
;/ laws according to which invariable solids move, to 
j| these imaginary beings it will be the study of the 
I j laws of motion of solids deformed by the differences 
j, / of temperature alluded to. 

No doubt, in our world, natural solids also ex 
perience variations of form and volume due to 
differences of temperature. But in laying the 
foundations of geometry we neglect these varia 
tions; for besides being but small they are irregular, 
and consequently appear to us to be accidental. 
In our hypothetical world this will no longer be 
the case, the variations will obey very simple and 
regular laws. On the other hand, the different 
solid parts of which the bodies of these inhabitants 
are composed will undergo the same variations of 
form and volume. 

Let me make another hypothesis: suppose that 
light passes through media of different refractive 
indices, such that the index of refraction is inversely 
proportional to R 2 r 2 . Under these conditions it 
is clear that the rays of light will no longer be 
rectilinear but circular. To justify what has been 
said, we have to prove that certain changes in the 
position of external objects may be corrected by 
correlative movements of the beings which inhabit 
this imaginary world; and in such a way as to 
restore the primitive aggregate of the impressions 
experienced by these sentient beings. Suppose, 
for example, that an object is displaced and 
deformed, not like an invariable solid, but like a 


solid subjected to unequal dilatations in exact con 
formity with the law of temperature assumed 
above. To use an abbreviation, we shall call such 
a movement a non-Euclidean displacement. 

If a sentient being be in the neighbourhood of 
such a displacement of the object, his impressions 
will be modified; but by moving in a suitable 
manner, he may reconstruct them. For this 
purpose, all that is required is that the aggregate 
of the sentient being and the object, considered as 
forming a single body, shall experience one of those 
special displacements which I have just called non- 
Euclidean. This is possible if we suppose that the 
limbs of these beings dilate according to the same 
laws as the other bodies of the world they inhabit. 

Although from the point of view of our ordinary 
geometry there is a deformation of the bodies in 
this displacement, and although their different 
parts are no longer in the same relative position, 
nevertheless we shall see that the impressions of 
the sentient being remain the same as before ; in 
fact, though the mutual distances of the different 
parts have varied, yet the parts which at first were 
in contact are still in contact. It follows that 
tactile impressions will be unchanged. On the 
other hand, from the hypothesis as to refraction 
and the curvature of the rays of light, visual im 
pressions will also be unchanged. These imaginary 
beings will therefore be led to classify the pheno 
mena they observe, and to distinguish among them 
the " changes of position," which may be corrected 


by a voluntary correlative movement, just as we 

If they construct a geometry, it will not be like 
ours, which is the study of the movements of our 
invariable solids; it will be the study of the 
changes of position which they will have thus 
distinguished, and will be " non-Euclidean dis 
placements," and this will be non-Euclidean geo 
metry. So that beings like ourselves, educated in 
such a world, will not have the same geometry as 

The World of Four Dimensions. Just as we have 
pictured to ourselves a non-Euclidean world, so we 
may picture a world of four dimensions. 

The sense of light, even with one eye, together 
with the muscular sensations relative to the move 
ments of the eyeball, will suffice to enable us to 
conceive of space of three dimensions. The images 
of external objects are painted on the retina, which 
is a plane of two dimensions; these are perspectives. 
But as eye and objects are movable, we see in 
succession different perspectives of the same body 
taken from different points of view. We find at 
the same time that the transition from one per 
spective to another is often accompanied by 
muscular sensations. If the transition from the 
perspective A to the perspective B, and that of the 
perspective A to the perspective B are accom 
panied by the same muscular sensations, we 
connect them as we do other operations of the 
same nature. Then when we study the laws 


according to which these operations are com 
bined, we see that they form a group, which has 
the same structure as that of the movements of 
invariable solids. Now, we have seen that it is 
from the properties of this group that we derive 
the idea of geometrical space and that of three 
dimensions. We thus understand how these 
perspectives gave rise to the conception of three 
dimensions, although each perspective is of only 
two dimensions, because they succeed each other 
according to certain laws. Well, in the same way 
that we draw the perspective of a three-dimen 
sional figure on a plane, so we can draw that of a 
four-dimensional figure on a canvas of three (or 
two) dimensions. To a geometer this is but child s 
play. We can even draw several perspectives of 
the same figure from several different points of 
view. We can easily represent to ourselves these 
perspectives, since they are of only three dimen 
sions. Imagine that the different perspectives of 
one and the same object to occur in succession, 
and that the transition from one to the other is 
accompanied by muscular sensations. It is under 
stood that we shall consider two of these transitions 
as two operations of the same nature when they 
are associated with the same muscular sensations. 
There is nothing, then, to prevent us from imagin 
ing that these operations are combined according 
to any law we choose for instance, by forming 
a group with the same structure as that of the 
movements of an invariable four-dimensional solid. 


In this there is nothing that we cannot represent 
to ourselves, and, moreover, these sensations are 
those which a being would experience \vho has a 
retina of two dimensions, and who may be dis 
placed in space of four dimensions. In this sense 
we may say that we can represent to ourselves the 
fourth dimension. 

Conclusions. It is seen that experiment plays a 
considerable role in the genesis of geometry; but 
it would be a mistake to conclude from that that 
geometry is, even in part, an experimental science. 
If it were experimental, it would only be ap 
proximative and provisory. And what a rough 
approximation it would be ! Geometry would be 
only the study of the movements of solid bodies; 
but, in reality, it is not concerned with natural 
solids : its object is certain ideal solids, absolutely 
invariable, which are but a greatly simplified and 
very remote image of them. The concept of these 
ideal bodies is entirely mental, and experiment is 
but the opportunity which enables us to reach the 
idea. The object of geometry is the study of a 
particular " group"; but the general concept of 
group pre-exists in our minds, at least potentially. 
It is imposed on us not as a form of our sensitive 
ness, but as a form of our understanding; only, 
from among all possible groups, we must choose 
one that will be the standard, so to speak, to 
which we shall refer natural phenomena. 

Experiment guides us in this choice, which it 
does not impose on us. It tells us not what is the 


truest, but what is the most convenient geometry. 
It will be noticed that my description of these 
fantastic worlds has required no language other 
than that of ordinary geometry. Then, were we 
transported to those worlds, there would be no 
need to change that language. Beings educated 
there would no doubt find it more convenient to 
create a geometry different from ours, and better 
adapted to their impressions; but as for us, in the 
presence of the same impressions, it is certain that 
we should not find it more convenient to make a 



1. I have on several occasions in the preceding 
pages tried to show how the principles of geometry 
are not experimental facts, and that in particular 
Euclid s postulate cannot be proved by experiment. 
However convincing the reasons already given 
may appear to me, I feel I must dwell upon them, 
because there is a profoundly false conception 
deeply rooted in many minds. 

2. Think of a material circle, measure its radius 
and circumference, and see if the ratio of the two 
lengths is equal to ~. What have we done ? We 
have made an experiment on the properties of the 
matter with which this roundness has been realised, 
and of which the measure we used is made. 

3. Geometry and Astronomy. The same question 
may also be asked in another way. If Lobat- 
schewsky s geometry is true, the parallax of a very 
distant star will be finite. If Riemann s is true, it 
will be negative. These are the results which 
seem within the reach of experiment, and it is 
hoped that astronomical observations may enable 
us to decide between the -twer geometries. But 


what we call a straight line in astronomy is simply 
the path of a ray of light. If, therefore, we were 
to discover negative parallaxes, or to prove that all 
parallaxes are higher than a certain limit, we 
should have a choice between two conclusions: 
we could give up Euclidean geometry, or modify 
the laws of optics, and suppose that light is not 
rigorously propagated in a straight line. It is 
needless to add that every one would look upon 
this solution as the more advantageous. Euclidean 
geometry, therefore, has nothing to fear from fresh 

4. Can we maintain that certain phenomena 
which are possible in Euclidean space would be 
impossible in non-Euclidean space, so that experi 
ment in establishing these phenomena would 
directly contradict the non-Euclidean hypothesis? 
I think that such a question cannot be seriously 
asked. To me it is exactly equivalent to the fol 
lowing, the absurdity of which is obvious: There 
are lengths which can be expressed in metres and 
centimetres, but cannot be measured in toises, feet, 
and inches; so that experiment, by ascertaining the 
existence of these lengths, would directly contra 
dict this hypothesis, that there are toises divided 
into six feet. Let us look at the question a little 
more closely. I assume that the straight line in 
Euclidean space possesses any two properties, 
which I shall call A and B; that in non-Euclidean 
space it still possesses the property A, but no 
longer possesses the property B; and, finally, I 


assume that in both Euclidean and non-Euclidean 
space the straight line is the only line that pos 
sesses the property A. If this were so, experiment 
would be able to decide between the hypotheses of 
Euclid and Lobatschewsky. It would be found 
that some concrete object, upon which w r e can 
experiment for example, a pencil of rays of light 
possesses the property A. We should conclude 
that it is rectilinear, and we should then endeavour 
to find out if it does, or does not, possess the pro 
perty B. But it is not so. There exists no 
property which can, like this property A, be an 
absolute criterion enabling us to recognise the 
straight line, and to distinguish it from every 
other line. Shall we say, for instance, " This pro 
perty will be the following: the straight line is a 
line such that a figure of which this line is a part 
can move without the mutual distances of its 
points varying, and in such a way that all the 
points in this straight line remain fixed"? Now, 
this is a property which in either Euclidean or 
non-Euclidean space belongs to the straight line, 
and belongs to it alone. But how can we ascer 
tain by experiment if it belongs to any particular 
concrete object ? Distances must be measured, 
and how shall we know that any concrete magni 
tude which I have measured with my material 
instrument really represents the abstract distance? 
We have only removed the difficulty a little farther 
off. In reality, the property that I have just 
enunciated is not a property of the straight line 


alone; it is a property of the straight line and of 
distance. For it to serve as an absolute criterion, 
we must be able to show, not only that it does not 
also belong to any other line than the straight line 
and to distance, but also that it does not belong 
to any other line than the straight line, and to any 
other magnitude than distance. NOW T , that is not 
true, and if we are not convinced by these con 
siderations, I challenge any one to give me a 
concrete experiment which can be interpreted in 
the Euclidean system, and which cannot be inter 
preted in the system of Lobatschewsky. As I 
am well aware that this challenge will never be 
accepted, I may conclude that no experiment will 
ever be in contradiction with Euclid s postulate; 
but, on the other hand, no experiment will ever be 
in contradiction with Lobatschewsky s postulate. 

5. But it is not sufficient that the Euclidean 
(or non- Euclidean) geometry can, ever be directly 
contradicted by experiment. Nor could it happen 
that it can only agree with experiment by a viola 
tion of the principle of sufficient reason, and of 
that of the relativity of space. Let me explain 
myself. Consider any material system whatever. 
We have to consider on the one hand the " state " 
of the various bodies of this system for example, 
their temperature, their electric potential, etc.; 
and on the other hand their position in space. 
And among the data which enable us to define 
this position we distinguish the mutual distances 
of these bodies that define their relative positions, 


and the conditions which define the absolute posi 
tion of the system and its absolute orientation in 
space. The law of the phenomena which will be 
produced in this system will depend on the state 
of these bodies, and on their mutual distances ; 
but because of the relativity and the inertia of 
space, they will not depend on the absolute posi 
tion and orientation of the system. In other 
words, the state of the bodies and their mutual 
distances at_any moment will solelyjiepend on 
the state of the^ same bodies^ ajod on their mutual 
distances at the initial moment, but w r ill in no 
way depend on the absolute initial position of 
the system and of its absolute initial orientation. 
This is what we shall call, for the sake of 
abbreviation, the law of relativity, 

So far I have spoken as a Euclidean geometer. 
But I have said that an experiment, whatever it 
may be, requires an interpretation on the Euclidean 
hypothesis; it equally requires one on the non- 
Euclidean hypothesis. Well, we have made a series 
of experiments. We have interpreted them on the 
Euclidean hypothesis, and we have recognised 
that these experiments thus interpreted do not 
violate this "law of relativity." We now interpret 
them on the non-Euclidean hypothesis. This is 
always possible, only the non-Euclidean distances 
of our different bodies in this new interpretation 
will not generally be the same as the Euclidean 
distances in the primitive interpretation. Will 
our experiment interpreted in this new manner 


be still in agreement with our " law of relativity," 
and if this agreement had not taken place, would 
we not still have the right to say that experiment 
has proved the falsity of non- Euclidean geometry? 
It is easy to see that this is an idle fear. In fact, 
to apply the law of relativity in all its rigour, it 
must be applied to the entire universe ; for if we 
were to consider only a part of the universe, and 
if the absolute position of this part were to vary, 
the distances of the other bodies of the universe 
would equally vary ; their influence on the part of 
the universe considered might therefore increase 
or diminish, and this might modify the laws of 
the phenomena which take place in it. But if 
our system is the entire universe, experiment is 
powerless to give us any opinion on its position 
and its absolute orientation in space. All that 
our instruments, however perfect they may be, 
can let us know will be the state of the different 
parts of the universe, and their mutual distances. 
Hence, our law of relativity may be enunciated as 
follows: The readings that we can make with our 
instruments at any given moment will depen 
only on the readings that we were able to make 
on the same instruments at the initial moment, 
Now such an enunciation is independent of all 
interpretation by experiments. If the law is true 
in the Euclidean interpretation, it will be also true 
in the non-Euclidean interpretation. Allow me 
to make a short digression on this point. I have 
spoken above of the data which define the position 


of the different bodies of the system. I might also 
have spoken of those which define their velocities. 
I should then have to distinguish the velocity with 
which the mutual distances of the different bodies 
are changing, and on the other hand the velocities 
of translation and rotation of the system ; that is 
to say, the velocities with which its absolute posi 
tion and orientation are changing. For the mind 
to be fully satisfied, the law ^f relativity would 
have to be enunciated as follows: The state of 
bodies and their mutual distances at any given 
moment, as well as the velocities with which 
those distances are changing at that moment, 
will depend only on the state of those bodies, 
on their mutual distances at the initial moment, 
and on the velocities with which those distances 
were changing at the initial moment. But they 
will not depend on the absolute initial position 
of the system nor on its absolute orientation, nor 
on the velocities with which that absolute posi 
tion and orientation were changing at the initial 
moment. Unfortunately, the law thus enunciated 
does not agree with experiments at least, as they 
are ordinarily interpreted. Suppose a man were 
translated to a planet, the sky of which was con 
stantly covered with a thick curtain of clouds, so 
that he could never see the other stars. On that 
planet he w r ould live as if it \vere isolated in space. 
But he w ould notice that it revolves, either by 
measuring its ellipticity (which is ordinarily done 
by means of astronomical observations, but which 


could be done by purely geodesic means), or by 
repeating the experiment of Foucault s pendulum. 
The absolute rotation of this planet might be 
clearly shown in this way. Now, here is a fact 
which shocks the philosopher, but which the 
physicist is compelled to accept. We know that 
from this fact Newton concluded the existence of 
absolute space. I myself cannot accept this way 
of looking at it. I shall explain why in Part III., 
but for the moment it is not my intention to 
discuss this difficulty. I must therefore resign 
myself, in the enunciation of the law of relativity, 
to including velocities of every kind among the 
data which define the state of the bodies. How 
ever that may be, the difficulty is the same for 
both Euclid s geometry and for Lobatschewsky s. 
I need not therefore trouble about it further, and 
I have only mentioned it incidentally. To sum 
up, whichever way we look at it, it is impossible 
to discover in geometric empiricism a rational 

6. Experiments only teach us the relations of 
bodies to one another. They do not and cannot , 
give us the relations of bodies and space, nor the ; 
mutual relations of the different parts of space. 
"Yes!" you reply, "a single experiment is not 
enough, because it only gives us one equation with 
several unknowns ; but when I have made enough 
experiments I shall have enough equations to 
calculate all my unknowns." If I know the height 
of the main-mast, that is not sufficient to enable 


me to calculate the age of the captain. When 
you have measured every fragment of wood in a 
ship you will have many equations, but you will 
be no nearer knowing the captain s age. All your 
measurements bearing on your fragments of wood 
can tell you only what concerns those fragments ; 
and similarly, your experiments, however numerous 
they may be, referring only to the relations of 
bodies with one another, \vill tell you nothing 
about the mutual relations of the different parts 
of space. 

7. Will you say that if the experiments have 
reference to the bodies, they at least have reference 
to the geometrical properties of the bodies. First, 
what do you understand by the geometrical pro- 
Arties nf frnHiesJ I assume that it is a question 
the relations of the bodies to space. These 
properties therefore are not reached by experi 
ments which only have reference to the relations 
of bodies to one another, and that is enough to 
show that it is not of those properties that there 
can be a question. Let us therefore begin by 
making ourselves clear as to the sense of the 
phrase : geometrical properties of bodies. When 
I say that a body is composed of several parts, I 
presume that I am thus enunciating a geometrical 
property, and that will be true even if I agree to 
give the improper name of points to the very 
small parts I am considering. When I say that 
this or that part of a certain body is in contact 
with this or that part of another body, I am 


enunciating a proposition which concerns the 
mutual relations of the two bodies, and not their 
relations with space. I assume that you will 
agree with me that these are not geometrical 
properties. I am sure that at least you will 
grant that these properties are independent of 
all knowledge of metrical geometry. Admitting 
this, I suppose that we have a solid body formed 
of eight thin iron rods, oa, ob, oc, od, oe, of, og, oh, 
connected at one of their extremities, o. And let 
us take a second solid body for example, a piece 
of wood, on which are marked three little spots 
of ink which I shall call P y. I now suppose 
that we find that we can bring into contact a ft y 
with ago; by that I mean a with a, and at the 
same time /3 with g, and 7 with o. Then we can 
successively bring into contact af3y with bgo, ego, 
dgo, ego, fgo, then with aho, bJw, cho, dho, cho, fho; 
and then ay successively with ab, be, cd, de, ef, fa. 
Now these are observations that can be made 
without having any idea beforehand as to the 
form or the metrical properties of space. They 
have no reference whatever to the " geometrical 
properties of bodies." These observations will 
not be possible if the bodies on which we experi 
ment move in a group having the same structure 
as the Lobatschewskian group (I mean according 
to the same laws as solid bodies in Lobatschewsky s 
geometry). They therefore suffice to prove that 
these bodies move according to the Euclidean 
group; or at least that they do not move according 



to the Lobatschewskian group. That they may 
be compatible with the Euclidean group is easily 
seen ; for we might make them so if the body 
a/3y were an invariable solid of our ordinary 
geometry in the shape of a right-angled triangle, 
and if the points abcdefgh \vere the vertices of 
a polyhedron formed of two regular hexagonal 
pyramids of our ordinary geometry having abode/ 
as their common base, and having the one g and 
the other . h as their vertices. Suppose now, 
instead of the previous observations, we note that 
we can as before apply afiy successively to ago, 
bgo, ego, dgo, ego, fgo, aJw, bho, cho, dho, eho, fho, 
and then that we can apply a/3 (and no longer ay) 
successively to ab, be, cd, dc, ef, and fa. These are 
observations that could be made if non-Euclidean 
geometry were true. If the bodies a/3y, oabcdefgh 
were invariable solids, if the former were a right- 
angled triangle, and the latter a double regular 
hexagonal pyramid of suitable dimensions. These 
new verifications are therefore impossible if the 
bodies move according to the Euclidean group; 
but they become possible if we suppose the bodies 
to move according to the Lobatschewskian group. 
They would therefore suffice to sho\v, if we carried 
them out, that the bodies in question do not move 
according to the Euclidean group. And so, with 
out making any hypothesis on the form and the 
nature of space, on the relations of the bodies 
and space, and without attributing to bodies any 
geometrical property, I have made observations 


which have enabled me to show in one case that 
the bodies experimented upon move according to 
a group, the structure of which is Euclidean, and 
in the other case, that they move in a group, the 
structure of which is Lobatschewskian. It can 
not be said that all the first observations would 
constitute an experiment proving that space is 
Euclidean, and the second an experiment proving 
that space is non-Euclidean ; in fact, it might be 
imagined (note that I use the word imagined) that 
there are bodies moving in such a manner as 
to render possible the second series of observations: 
and the proof is that the first mechanic who came 
our way could construct it if he would only take 
the trouble. But you must not conclude, however, 
that space is non-Euclidean. In the same way, 
just as ordinary solid bodies would continue 
to exist when the mechanic had constructed the 
strange bodies I have just mentioned, he would 
have to conclude that space is both Euclidean 
and non-Euclidean. Suppose, for instance, that 
we have a large sphere of radius R, and that its 
temperature decreases from the centre to the 
surface of the sphere according to the law of 
which I spoke when I was describing the non- 
Euclidean world. We might have bodies whose 
dilatation is negligeable, and which would behave 
as ordinary invariable solids; and, on the other 
hand, we might have very dilatable bodies, which 
would behave as non-Euclidean solids. We 
might have two double pyramids oabcdefgh and 


o db cd efg ti, and two triangles a /3 y and a /3 y . 
The first double pyramid would be rectilinear, and 
the second curvilinear. The triangle a/3y would 
consist of undilatable matter, and the other of very 
dilatable matter. We might therefore make our 
first observations with the double pyramid o a li 
and the triangle a {$ y . 

And then the experiment would seem to show 
first, that Euclidean geometry is true, and then 
that it is false. Hence, experiments have reference 
not to space but to bodies. 


8. To round the matter off, I ought to speak of 
a very delicate question, which will require con 
siderable development ; but I shall confine myself 
to summing up what I have written in the Revue 
de Metaphysique ct de Morale and in the Monist. 
When we say that space has three dimensions, 
what do we mean ? We have seen the importance 
of these " internal changes " which are revealed to 
us by our muscular sensations. They may serve 
to characterise the different attitudes of our body. 
Let us take arbitrarily as our origin one of these 
attitudes, A. When we pass from this initial 
attitude to another attitude B we experience a 
series of muscular sensations, and this series S of 
muscular sensations will define B. Observe, how 
ever, that we shall often look upon two series S 
and S as defining the same attitude B (since the 


initial and final attitudes A and B remaining the 
same, the intermediary attitudes of the corre 
sponding sensations may differ). How then can 
we recognise the equivalence of these two series ? 
Because they may serve to compensate for the same 
external change, or more generally, because, when 
it is a question of compensation for an external 
change, one of the series may be replaced by the 
other. Among these series we have distinguished 
those which can alone compensate for an external 
change, and which we have called " displacements." 
As we cannot distinguish two displacements which 
are very close together, the aggregate of these 
displacements presents the characteristics of a 
physical continuum. Experience teaches us that 
they are the characteristics of a physical con 
tinuum of six dimensions ; but we do not know as 
yet how many dimensions space itself possesses, so 
we must first of all answer another question. 
What is a point in space ? Every one thinks he 
knows, but that is an illusion. What we see when 
we try to represent to ourselves a point in space is 
a black spot on white paper, a spot of chalk on 
a blackboard, always an object. The question 
should therefore be understood as follows : What 
do I mean when I say the object B is at the 
point which a moment before was occupied by the 
object A ? Again, what criterion will enable 
me to recognise it ? I mean that although I have 
not moved (my muscular sense tells me this), my 
finger, which just now touched the object A, is 


now touching the object B. I might have used 
other criteria for instance, another finger or the 
sense of sight but the first criterion is sufficient. 
I know that if it answers in the affirmative all 
other criteria will give the same answer. I know 
it from experiment. I cannot know it a priori. \ 
I For the same reason I say that touch cannot 
/ be exercised at a distance ; that is another way of 
enunciating the same experimental fact. If I 
say, on the contrary, that sight is exercised at a 
distance, it means that the criterion furnished by 
sight may give an affirmative answer while the 
others reply in the negative. 

To sum up. For each attitude of my body my 
finger determines a point, and it is that and that 
only which defines a point in space. To each 
attitude corresponds in this way a point. But it 
often happens that the same point corresponds to 
several different attitudes (in this case we say that 
our finger has not moved, but the rest of our body 
has). We distinguish, therefore, among changes 
of attitude those in which the finger does not 
move. How are we led to this ? It is because we 
often remark that in these changes the object 
which is in touch with the finger remains in con 
tact with it. Let us arrange then in the same 
class all the attitudes which are deduced one from 
the other by one of the changes that we have thus 
distinguished. To all these attitudes of the same 
class will correspond the same point in space. 
Then to each class will correspond a point, and to 


each point a class. Yet it may be said that what 
we get from this experiment is not the point, but 
the class of changes, or, better still, the corre 
sponding class of muscular sensations. Thus, when 
we say that space has three dimensions, we merely 
mean that the aggregate of these classes appears to 
us with the characteristics of a physical continuum 
of three dimensions. Then if, instead of defining 
the points in space with the aid of the first finger, 
I use, for example, another finger, would the 
results be the same ? That is by no means a 
priori evident. But, as we have seen, experiment 
has shown us that all our criteria are in agree 
ment, and this enables us to answer in the 
affirmative. If we recur to what we have called 
displacements, the aggregate of which forms, as 
we have seen, a group, we shall be brought to 
distinguish those in which a finger does not move; 
and by what has preceded, those are the displace 
ments which characterise a point in space, and 
their aggregate will form a sub-group of our 
group. To each sub-group of this kind, then, will 
correspond a point in space. We might be 
tempted to conclude that experiment has taught 
us the number of dimensions of space ; but in 
reality our experiments have referred not to space, 
but to our body and its relations with neighbour 
ing objects. What is more, our experiments 
are exceeding crude. In our mind the latent idea 
of a certain number of groups pre-existed; these 
are the groups with which Lie s theory is con- 


cerned. Which shall we choose to form a kind of 
standard by which to compare natural pheno 
mena ? And when this group is chosen, which 
of the sub-groups shall we take to characterise a 
point in space ? Experiment has guided us by 
showing us what choice adapts itself best to the 
properties of our body ; but there its role ends. 




THE English teach mechanics as an experimental 
science; on the Continent it is taught always more., 
or less as a deductive and a priori science. The 
English are right, no doubt. How is it that the 
other method has been persisted in for so long; how 
is it that Continental scientists who have tried to 
escape from the practice of their predecessors have 
in most cases been unsuccessful ? On the other 
hand, if the principles of mechanics are only of 
experimental origin, are they not merely approxi 
mate and provisory ? May we not be some day 
compelled by new experiments to modify or even 
to abandon them ? These are the questions which 
naturally arise, and the difficulty of solution is 
largely due to the fact that treatises on mechanics 
do not clearly distinguish between what is experi 
ment, what is mathematical reasoning, what is 
convention, and what is hypothesis. This is not 


1. There is no absolute space, and we only 
conceive of relative motion ; and yet in most cases 
mechanical facts are enunciated as if there is an 
absolute space to which they can be referred. 

2. There is no absolute time. When we say that 
two periods are equal, the statement has no 
meaning, and can only acquire a meaning by a 

3. Not only have we no direct intuition of the 
equality of two periods, but we have not even 
direct intuition of the simultaneity of two events 
occurring in two different places. I have ex 
plained this in an article entitled " Mesure du 

4. Finally, is not our Euclidean geometry in 
itself only a kind of convention of language ? 
Mechanical facts might be enunciated with refer 
ence to a non-Euclidean space which would be 
less convenient but quite as legitimate as our 
ordinary space ; the enunciation would become 
more complicated, but it still would be possible. 

Thus, absolute space, absolute time, and even 
geometry are not conditions which are imposed on 
mechanics. All these things no more existed 
before mechanics than the French language can 
be logically said to have existed before the truths 
which are expressed in French. We might 
endeavour to enunciate the fundamental law of 
mechanics in a language independent of all these 

1 Revue de Mtlaphysique et de Morale, t. vi., pp. 1-13, January, 


conventions; and no doubt we should in this way 
get a clearer idea of those laws in themselves. 
This is what M. Andrade has tried to do, to 
some extent at any rate, in his Lecons de Mecanique 
physique. Of course the enunciation of these laws 
would become much more complicated, because all 
these conventions have been adopted for the very 
purpose of abbreviating and simplifying the enun 
ciation. As far as we are concerned, I shall ignore 
all these difficulties; not because I disregard 
them, far from it; but because they have re 
ceived sufficient attention in the first two parts, 
of the book. Provisionally, then, we shall admit 
absolute time and Euclidean geometry. 

The Principle of Inertia. A body under the 
action of no force can only move uniformly in a 
straight line. Is this a truth imposed on the mind 
a priori ? If this be so, how is it that the Greeks 
ignored it ? How could they have believed that 
motion ceases with the cause of motion ? or, again, 
that every body, if there is nothing to prevent it, 
will move in a circle, the noblest of all forms of 
motion ? 

If it be said that the velocity of a body cannot 
change, if there is no reason for it to change, may 
we not just as legitimately maintain that the 
position of a body cannot change, or that the 
curvature of its path cannot change, without the 
agency of an external cause? Is, then, the prin 
ciple of inertia, which is not an a priori truth, an 
experimental fact ? Have there ever been experi- 


merits on bodies acted on by no forces ? and, if so, 
how did we know that no forces were acting ? 
The usual instance is that of a ball rolling for a 
very long time on a marble table; but why do 
we say it is under the action of no force ? Is it 
because it is too remote from all other bodies to 
experience any sensible action ? It is not further 
from the earth than if it were thrown freely into 
the air; and we all know that in that case it 
would be subject to the attraction of the earth. 
Teachers of mechanics usually pass rapidly over 
the example of the ball, but they add that the 
principle of inertia is verified indirectly by its con 
sequences. This is very badly expressed; they 
evidently mean that various consequences may be 
verified by a more general principle, of which the 
principle of inertia is only a particular case. I 
shall propose for this general principle the 
following enunciation: The acceleration of a 
body depends only on its position and that of 
neighbouring bodies, and on their velocities. 
Mathematicians would say that the movements 
of all the material molecules of the universe 
depend on differential equations of the second 
order. To make it clear that this is really a 
generalisation of the law of inertia we may again 
have recourse to our imagination. The law of 
inertia, as I have said above, is not imposed on us 
a priori; other laws would be just as compatible 
with the principle of sufficient reason. If a body 
is not acted upon by a force, instead of supposing 


that its velocity is unchanged we may suppose 
that its position or its acceleration is unchanged. 

Let us for a moment suppose that one of these 
two laws is a law of nature, and substitute it for 
the law of inertia: what will be the natural 
generalisation? A moment s reflection will show 
us. In the first case, we may suppose that the 
velocity of a body depends only on its position and 
that of neighbouring bodies; in the second case, 
that the variation of the acceleration of a body 
depends only on the position of the body and ,of 
neighbouring bodies, on their velocities and 
accelerations; or, in mathematical terms, the 
differential equations of the motion would be of 
the first order in the first case and of the third 
order in the second. 

Let us now modify our supposition a little. 
Suppose a world analogous to our solar system, 
but one in which by a singular chance the orbits 
of all the planets have neither eccentricity nor 
inclination; and further, I suppose that the 
masses of the planets are too small for their 
mutual perturbations to be sensible. Astronomers 
living in one of these planets would not hesitate to 
conclude that the orbit of a star can only be 
circular and parallel to a certain plane; the 
position of a star at a given moment would then 
be sufficient to determine its velocity and path. 
The law of inertia which they would adopt would 
be the former of the two hypothetical laws I have 


Now, imagine this system to be some day 
crossed by a body of vast mass and immense 
velocity coming from distant constellations. All 
the orbits would be profoundly disturbed. Our 
astronomers would not be greatly astonished. 
They would guess that this new star is in itself 
quite capable of doing all the mischief; but, they 
would say, as soon as it has passed by, order will 
again be established. No doubt the distances of 
the planets from the sun will not be the same as 
before the cataclysm, but the orbits will become 
circular again as soon as the disturbing cause has 
disappeared. It would be only when the perturb 
ing body is remote, and when the orbits, instead of 
being circular are found to be elliptical, that the 
astronomers would find out their mistake, and 
discover the necessity of reconstructing their 

I have dwelt on these hypotheses, for it seems to 
me that we can clearly understand our generalised 
law of inertia only by opposing it to a contrary 

Has this generalised law of inertia been veri 
fied by experiment, and can it be so verified ? 
When Newton wrote the Principia, he certainly 
regarded this truth as experimentally acquired and 
demonstrated. It was so in his eyes, not only 
from the anthropomorphic conception to which I 
shall later refer, but also because of the work of 
Galileo. It was so proved by the laws of Kepler. 
According to those laws, in fact, the path of a 


planet is entirely determined by its initial position 
and initial velocity; this, indeed, is what our 
generalised law of inertia requires. 

For this principle to be only true in appearance 
lest we should fear that some day it must be re 
placed by one of the analogous principles which I 
opposed to it just now we must have been led 
astray by some amazing chance such as that \vhich 
had led into error our imaginary astronomers. 
Such an hypothesis is so unlikely that it need not 
delay us. No one will believe that there can be 
such chances; no doubt the probability that two 
eccentricities are both exactly zero is not smaller 
than the probability that one is o.i and the other 
0.2. The probability of a simple event is not 
smaller than that of a complex one. If, however, 
the former does occur, we shall not attribute its 
occurrence to chance; we shall not be inclined to 
believe that nature has done it deliberately to 
deceive us. The hypothesis of an error of this 
kind being discarded, we may admit that so far as 
astronomy is concerned our law has been verified 
by experiment. 

But Astronomy is not the whole of Physics. 
May we not fear that some day a new experi 
ment will falsify the law in some domain of 
physics ? An experimental la\v is always subject 
to revision ; we may always expect to see it re 
placed by some other and more exact law. But 
no one seriously thinks that the law of which we 
speak will ever be abandoned or amended. Why ? 


Precisely because it will never be submitted to a 
decisive test. 

In the first place, for this test to be complete, 
all the bodies of the universe must return with 
their initial velocities to their initial positions after 
a certain time. We ought then to find that they 
would resume their original paths. But this test 
is impossible; it can be only partially applied, and 
even when it is applied there will still be some 
bodies which will not return to their original 
positions. Thus there will be a ready explanation 
of any breaking down of the law. 

Yet this is not all. In Astronomy we sec the 
bodies whose motion we are studying, and in most 
cases we grant that they are not subject to the 
action of other invisible bodies. Under these con 
ditions, our law must certainly be either verified or 
not. But it is not so in Physics. If physical 
phenomena are due to motion, it is to the motion 
of molecules which we cannot see. If, then, the 
acceleration of bodies w r e cannot see depends on 
something else than the positions or velocities of 
other visible bodies or of invisible molecules, the 
existence of which we have been led previously 
to admit, there is nothing to prevent us from 
supposing that this something else is the position 
or velocity of other molecules of which we have 
not so far suspected the existence. The law 
will be safeguarded. Let me express the same 
thought in another form in mathematical language. 
Suppose we are observing n molecules, and find 


that their yi co-ordinates satisfy a system of 3 
differential equations of the fourth order (and 
not of the second, as required by the law of 
inertia). We know that by introducing 3^ variable 
auxiliaries, a system of 311 equations of the fourth 
order may be reduced to a system of 6n equations 
of the second order. If, then, we suppose that the 
3 auxiliary variables represent the co-ordinates of 
n invisible molecules, the result is again conform 
able to the law of inertia. To sum up, this law, 
verified experimentally in some particular cases, 
may be extended fearlessly to the most general 
cases; for we know that in these general cases 
it can neither be confirmed nor contradicted by 

The Law of Acceleration. The acceleration of a 
body is equal to the force which acts on it divided 
by its mass. 

Can this law be verified by experiment ? If so, 
we have to measure the three magnitudes men 
tioned in the enunciation : acceleration, force, 
and mass. I admit that acceleration may be 
measured, because I pass over the difficulty 
arising from the measurement of time. But how 
are we to measure force and mass ? We do not 
even know what they are. What is mass ? 
Newton replies : " The product of the volume and 
the density." " It were better to say," answer 
Thomson and Tait, " that density is the quotient 
of the mass by the volume." What is force ? 
" It is," replies Lagrange, " that which moves or 



tends to move a body." " It is," according to 
Kirchoff, "the product of the mass and the 
acceleration." Then why not say that mass is 
the quotient of the force by the acceleration ? 
These difficulties are insurmountable. 

When we say force is the cause of motion, we 
are talking metaphysics ; and this definition, if we 
had to be content with it, would be absolutely 
fruitless, would lead to absolutely nothing. For a 
definition to be of any use it must tell us how to 
measure force ; and that is quite sufficient, for it is 
by no means necessary to tell \vhat force is in 
itself, nor whether it is the cause or the effect of 
motion. We must therefore first define what is 
meant by the equality of two forces. When are 
tw r o forces equal ? We are told that it is when 
they give the same acceleration to the same mass, 
or when acting in opposite directions they are in 
equilibrium. This definition is a sham. A force 
applied to a body cannot be uncoupled and 
applied to another body as an engine is uncoupled 
from one train and coupled to another. It is 
therefore impossible to say what acceleration such 
a force, applied to such a body, would give to 
another body if it were applied to it. It is im 
possible to tell how two forces which are not 
acting in exactly opposite directions would be 
have if they were acting in opposite directions. 
It is this definition which we try to materialise, as 
it were, when we measure a force with a dyna 
mometer or with a balance. Two forces, F and 


F , which I suppose, for simplicity, to be acting 
vertically upwards, are respectively applied to two 
bodies, C and C . I attach a body weighing P 
first to C and then to C ; if there is equilibrium in 
both cases I conclude that the two forces F and 
F are equal, for they are both equal to the weight 
of the body P. But am I certain that the body P 
has kept its weight when I transferred it from the 
first body to the second ? Far from it. I am 
certain of the contrary. I know that the magni 
tude of the weight varies from one point to 
another, and that it is greater, for instance, at the 
pole than at the equator. No doubt the difference 
is very small, and we neglect it in practice ; but a 
definition must have mathematical rigour ; this 
rigour does not exist. What I say of weight 
would apply equally to the force of the spring of 
a dynamometer, which would vary according to 
temperature and many other circumstances. Nor 
is this all. We cannot say that the weight of the 
body P is applied to the body C and keeps in 
equilibrium the force F. What is applied to 
the body C is the action of the body P on the 
body C. On the other hand, the body P is 
acted on by its weight, and by the reaction R 
of the body C on P the forces F and A are 
equal, because they are in equilibrium; the forces 
A and R are equal by virtue of the principle 
of action and reaction ; and finally, the force 
R and the weight P are equal because they 
are in equilibrium. From these three equalities 


we deduce the equality of the weight P and the 
force F. 

Thus we are compelled to bring into our defini 
tion, of the equality of two forces the principle 
of the equality of action and reaction; hence this 
principle can no longer be regarded as an experimental 
law hit only as a definition. 

To recognise the equality of two forces we are 
then in possession of two rules : the equality of 
two forces in equilibrium and the equality of action 
and reaction. But, as we have seen, these are not 
sufficient, and we are compelled to have recourse 
to a third rule, and to admit that certain forces 
the weight of a body, for instance ar>5 constant in 
magnitude and direction. But this third rule is 
an experimental law. It is only approximately 
true: it is a bad definition. We are therefore 
reduced to Kirchoff s definition: force is the pro 
duct of the mass and the acceleration. This law 
of Newton in its turn ceases to be regarded as an 
experimental law, it is now only a definition. But 
as a definition it is insufficient, for we do not 
know what mass is. It enables us, no doubt, to 
calculate the ratio of two forces applied at 
different times to the same body, but it tells us 
nothing about the ratio of two forces applied to 
two different bodies. To fill up the gap we must 
have recourse to Newton s third law, the equality 
of action and reaction, still regarded not as 
an experimental law but as a definition. Two 
bodies, A and B, act on each other ; t v ie accelera- 


tion of A, multiplied by the mass of A, is equal to 
the action of B on A ; in the same way the 
acceleration of B, multiplied by the mass of B is 
equal to the reaction of A on B. As, by definition, 
the action and the reaction are equal, the masses 
of A and B arc respectively in the inverse ratio of 
their masses. Thus is the ratio of the two masses 
defined, and it is for experiment to verify that the 
ratio is constant. 

This would do very well if the two bodies were 
alone and could be abstracted from the action of 
the rest of the world ; but this is by no means 
the case. The acceleration of A is not solely due 
to the action of B, but to that of a multitude of. - 
other bodies, C, D, . . . To apply the preceding 
rule we must decompose the acceleration of A into 
many components, and find out which of these 
components is due to the action of B. The 
decomposition would still be possible if we 
suppose that the action of C on A is simply added 
to that of B on A, and that the presence of the 
body C does not in any way modify the action of 
B on A, or that the presence of B does not modify 
the action of C on A ; that is, if we admit that 
any two bodies attract each other, that their 
mutual action is along their join, and is only de 
pendent on their distance apart ; if, in a word, we 
admit the hypothesis of central forces. 

We know that to determine the masses of the 
heavenly bodies we adopt quite a different prin 
ciple. The law of gravitation teaches us that the 


attraction of two bodies is proportional to their 
masses; if r is their distance apart, m and ni their 
masses, k a constant, then their attraction will be 
knun /r 2 . What we are measuring is therefore not 
mass, the ratio of the force to the acceleration, but 
the attracting mass ; not the inertia of the body, 
but its attracting power. It is an indirect process, 
the use of which is not indispensable theoretically. 
We might have said that the attraction is in 
versely proportional to the square of the distance, 
without being proportional to the product of the 
masses, that it is equal to //r 2 and not to kinm . 
If it were so, we should nevertheless, by observing 
the relative motion of the celestial bodies, be able 
to calculate the masses of these bodies. 

But have we any right to admit the hypothesis 
of central forces ? Is this hypothesis rigorously 
accurate ? Is it certain that it will never be 
falsified by experiment ? Who will venture to 
make such an assertion ? And if we must abandon 
this hypothesis, the building which has been so 
laboriously erected must fall to the ground. 

We have no longer any right to speak of the 
component of the acceleration of A which is 
due to the action of B. We have no means of 
distinguishing it from that which is due to the 
action of C or of any other body. The rule 
becomes inapplicable in the measurement of 
masses. What then is left of the principle of 
the equality of action and reaction ? If we 
reject the hypothesis of central forces this prin- 


ciple must go too ; the geometrical resultant of 
all the forces applied to the different bodies of a 
system abstracted from all external action will be 
zero. In other words, the motion of the centre of 
gravity of this system will be uniform and in a 
straight line. Here would seem to be a means of 
defining mass. The position of the centre of 
gravity evidently depends on the values given to 
the masses ; we must select these values so that 
the motion of the centre of gravity is uniform 
and rectilinear. This will always be possible if 
Newton s third law holds good, and it will be in 
general possible only in one way. But no system 
exists which is abstracted from all external action; 
every part of the universe is subject, more or less, 
to the action of the other parts. The law of the 
Motion of the centre of gravity is only rigorously true 
when applied to the whole universe. 

But then, to obtain the values of the masses 
we must find the motion of the centre of gravity 
of the universe. The absurdity of this conclusion 
is obvious ; the motion of the centre of gravity 
of the universe will be for ever to us unknown. 
Nothing, therefore, is left, and our efforts are 
fruitless. There is no escape from the following 
definition, which is only a confession of failure : 
Masses are co-efficients which it is found convenient to 
introduce into calculations. 

We could reconstruct our mechanics by giving 
to our masses different values. The new me 
chanics would be in contradiction neither with 


experiment nor with the general principles of 
dynamics (the principle of inertia, proportion 
ality of masses and accelerations, equality of 
action and reaction, uniform motion of the centre 
of gravity in a straight line, and areas). But the 
equations of this mechanics would not be so simple. 
Let us clearly understand this. It would be only 
the first terms which would be less simple i.e., 
those we already know through experiment ; 
perhaps the small masses could be slightly altered 
without the complete equations gaining or losing 
in simplicity. 

Hertz has inquired if the principles of mechanics 
are rigorously true. " In the opinion of many 
physicists it seems inconceivable that experiment 
will ever alter the impregnable principles of 
mechanics; and yet, what is due to experiment 
may always be rectified by experiment." From 
what we have just seen these fears would appear 
to be groundless. The principles of dynamics 
appeared to us first as experimental truths, but 
we have been compelled to use them as defini 
tions. It is by definition that force is equal to 
the product of the mass and the acceleration ; 
this is a principle which is henceforth beyond 
the reach of any future experiment. Thus 
it is by definition that action and reaction are 
equal and opposite. But then it will be said, 
these unverifiable principles are absolutely devoid 
of any significance. They cannot be disproved by 
experiment, but we can learn from them nothing 


of any use to us ; \vhat then is the use of studying 
dynamics ? This somewhat rapid condemnation 
would be rather unfair. There is not in Nature any 
system perfectly isolated, perfectly abstracted from 
all external action ; but there are systems which 
are nearly isolated. If we observe such a system, 
we can study not only the relative motion of its 
different parts w r ith respect to each other, but the 
motion of its centre of gravity with respect to the 
other parts of the universe. We then find that 
the motion of its centre of gravity is nearly uniform 
and rectilinear in conformity with Newton s Third 
Law. This is an experimental fact, which cannot 
be invalidated by a more accurate experiment. 
What, in fact, would a more accurate experiment 
teach us ? It \vould teach us that the law is only 
approximately true, and we know that already. 
Thus is explained how experiment may serve as a basis 
for the principles of mechanics, and yet will never 
invalidate them. 

Anthropomorphic Mechanics. It will be said that 
Kirchoff has only followed the general tendency of 
mathematicians towards nominalism ; from this his 
skill as a physicist has not saved him. He wanted 
a definition of a force, and he took the first that 
came handy ; but we do not require a definition 
of force ; the idea of force is primitive, irreducible, 
indefinable ; we all know what it is ; of it we have 
direct intuition. This direct intuition arises from 
the idea of effort which is familiar to us from 
childhood. But in the first place, even if this 


direct intuition made known to us the real nature 
of force in itself, it would prove to be an insufficient 
basis for mechanics ; it would, moreover, be quite 
useless. The important thing is not to know 
what force is, but how to measure it. Everything 
which does not teach us how to measure it is as 
useless to the mechanician as, for instance, the 
subjective idea of heat and cold to the student of 
heat. This subjective idea cannot be translated 
into numbers, and is therefore useless ; a scientist 
whose skin is an absolutely bad conductor of heat, 
and who, therefore, has never felt the sensation 
of heat or cold, would read a thermometer in just 
the same way as any one else, and would have 
enough material to construct the whole of the 
theory of heat. 

Now this immediate notion of effort is of no use 
to us in the measurement of force. It is clear, for 
example, that I shall experience more fatigue in 
lifting a weight of 100 Ib. than a man who is 
accustomed to lifting heavy burdens. But there 
is more than this. This notion of effort does not 
teach us the nature of force ; it is definitively re 
duced to a recollection of muscular sensations, and 
no one will maintain that the sun experiences 
a muscular sensation when it attracts the earth. 
All that we can expect to find from it is a symbol, 
less precise and less convenient than the arrows 
(to denote direction) used by geometers, and quite 
as remote from reality. 

Anthropomorphism plays a considerable historic 


role ill the genesis of mechanics ; perhaps it may 
yet furnish us with a symbol which some minds 
may find convenient; but it can be the foundation 
of nothing of a really scientific or philosophical 

The Thread School. M. Andrade, in his Lccons 
de Mecanique physique, has modernised anthropo 
morphic mechanics. To the school of mechanics 
with which Kirchoff is identified, he opposes a 
school which is quaintly called the " Thread 

This school tries to reduce everything to the con 
sideration of certain material systems of negligible 
mass, regarded in a state of tension and capable 
of transmitting considerable effort to distant 
bodies systems of which the ideal type is the 
fine string, wire, or thread. A thread which 
transmits any force is slightly lengthened in the 
direction of that force; the direction of the thread 
tells us the direction of the force, and the magni 
tude of the force is measured by the lengthening of 
the thread. 

We may imagine such an experiment as the 
following : A body A is attached to a thread ; 
at the other extremity of the thread acts a force 
which is made to vary until the length of the 
thread is increased by a, and the acceleration 
of the body A is recorded. A is then detached, 
and a body B is attached to the same thread, and 
the same or another force is made to act until 
the increment of length again is a, and the 


acceleration of B is noted. The experiment is 
then renewed with both A and B until the incre 
ment of length is ft. The four accelerations 
observed should be proportional. Here we have 
an experimental verification of the law of accelera 
tion enunciated above. Again, we may consider 
a body under the action of several threads in 
equal tension, and by experiment we determine 
the direction of those threads when the body 
is in equilibrium. This is an experimental 
verification of the law of the composition of 
forces. But, as a matter of fact, what have we 
done ? We have defined the force acting on the 
string by the deformation of the thread, which is 
reasonable enough; we have then assumed that if 
a body is attached to this thread, the effort which 
is transmitted to it by the thread is equal to the 
action exercised by the body on the thread ; in 
fact, we have used the principle of action and 
reaction by considering it, not as an experimental 
truth, but as the very definition of force. This 
definition is quite as conventional as that of 
Kirchoff, but it is much less general. 

All the forces are not transmitted by the thread 
(and to compare them they would all have to be 
transmitted by identical threads). If we even 
admitted that the earth is attached to the sun by 
an invisible thread, at any rate it will be agreed 
that we have no means of measuring the increment 
of the thread. Nine times out of ten, in con 
sequence, our definition will be in default ; no 


sense of any kind can be attached to it, and we 
must fall back on that of Kirchoff. Why then go 
on in this roundabout way ? You admit a certain 
definition of force which has a meaning only in 
certain particular cases. In those cases you verify 
by experiment that it leads to the law of accelera 
tion. On the strength of these experiments you 
then take the law of acceleration as a definition of 
force in all the other cases. 

Would it not be simpler to consider the law of 
acceleration as a definition in all cases, and to 
regard the experiments in question, not as verifica 
tions of that law, but as verifications of the 
principle of action and reaction, or as proving 
the deformations of an elastic body depend only 
on the forces acting on that body ? Without 
taking into account the fact that the conditions 
in which your definition could be accepted can 
only be very imperfectly fulfilled, that a thread is 
never without mass, that it is never isolated from 
all other forces than the reaction of the bodies 
attached to its extremities. 

The ideas expounded by M. Andrade are none 
the less very interesting. If they do not satisfy our 
logical requirements, they give us a better view of 
the historical genesis of the fundamental ideas of 
mechanics. The reflections they suggest show us 
how the human mind passed from a naive 
anthropomorphism to the present conception of 

We see that we end with an experiment which 


is very particular, and as a matter of fact very 
crude, and we start with a perfectly general law, 
perfectly precise, the truth of which we regard as 
absolute. We have, so to speak, freely conferred 
this certainty on it by looking upon it as a con 

Are the laws of acceleration and of the com 
position of forces only arbitrary conventions ? 
Conventions, yes; arbitrary, no they would be 
so if we lost sight of the experiments which led the 
founders of the science to adopt them, and which, 
imperfect as they were, were sufficient to justify 
their adoption. It is well from time to time to let 
our attention dwell on the experimental origin of 
these conventions. 



The Principle of Relative Motion. Sometimes 
endeavours have been made to connect the law of 
acceleration with a more general principle. The 
movement of any system whatever ought to 
obey the same laws, whether it is referred to fixed 
axes or to the movable axes which are implied 
in uniform motion in a straight line. This is 
the principle of relative motion ; it is imposed 
upon us for two reasons: the commonest experi 
ment confirms it; the consideration of the contrary 
hypothesis is singularly repugnant to the mind. 

Let us admit it then, and consider a body under 
the action of a force. The relative motion of this 
body with respect to an observer moving with a 
uniform velocity equal to the initial velocity of the 
body, should be identical with what would be its 
absolute motion if it started from rest. We con 
clude that its acceleration must not depend upon 
its absolute velocity, and from that we attempt to 
deduce the complete law of acceleration. 

For a long time there have been traces of this 
proof in the regulations for the degree of IB. es Sc. 


It is clear that the attempt has failed. The 
obstacle which prevented us from proving the 
law of acceleration is that we have no definition 
of force. This obstacle subsists in its entirety, 
since the principle invoked has not furnished us 
wdth the missing definition. The principle of 
relative motion is none the less very interesting, 
and deserves to be considered for its own sake. 
Let us try to enunciate it in an accurate manner. 
We have said above that the accelerations of the 
different bodies which form part of an isolated 
system only depend on their velocities and their 
relative positions, and not on their velocities and 
their absolute positions, provided that the mov 
able axes to which the relative motion is referred 
move uniformly in a straight line; or, if it is pre 
ferred, their accelerations depend only on the 
differences of their velocities and the differences of 
their co-ordinates, and not on the absolute values 
of these velocities and co-ordinates. If this prin 
ciple is true for relative accelerations, or rather 
for differences of acceleration, by combining it 
with the law of reaction we shall deduce that it is 
true for absolute accelerations. It remains to be 
seen how we can prove that differences of accelera 
tion depend only on differences of velocities 
and co-ordinates; or, to speak in mathematical 
language, that these differences of co-ordinates 
satisfy differential equations of the second order. 
Can this proof be deduced from experiment or 
from a priori conditions? Remembering what we 


have said before, the reader will give his own 
answer. Thus enunciated, in fact, the principle of 
relative motion curiously resembles what I called 
above the generalised principle of inertia; it is not 
quite the same thing, since it is a question of 
differences of co-ordinates, and not of the co 
ordinates themselves. The new principle teaches 
us something more than the old, but the same 
discussion applies to it, and would lead to the 
same conclusions. We need not recur to it. 

Newton s Argument. Here we find a very im 
portant and even slightly disturbing question. I 
have said that the principle of relative motion 
was not for us simply a result of experiment; and 
that a priori every contrary hypothesis would be 
repugnant to the mind. But, then, why is the 
principle only true if the motion of the movable 
axes is uniform and in a straight line? It seems 
that it should be imposed upon us with the same 
force if the motion is accelerated, or at any rate 
if it reduces to a uniform rotation. In these two 
cases, in fact, the principle is not true. I need not 
dwell on the case in which the motion of the 
axes is in a straight line and not uniform. The 
paradox does not bear a moment s examination. 
If I am in a railway carriage, and if the train, 
striking against any obstacle whatever, is suddenly 
stopped, I shall be projected on to the opposite 
side, although I have not been directly acted upon 
by any force. There is nothing mysterious in 
that, and if I have not been subject to the action 



of any external force, the train has experienced an 
external impact. There can be nothing para 
doxical in the relative motion of two bodies being 
disturbed when the motion of one or the other is 
modified by an external cause. Nor need I dwell 
on the case of relative motion referring to axes 
which rotate uniformly. If the sky were for ever 
covered with clouds, and if we had no means of 
observing the stars, we might, nevertheless, con 
clude that the earth turns round. We should be 
warned of this fact by the flattening at the poles, 
or by the experiment of Foucault s pendulum. 
And yet, would there in this case be any meaning 
in saying that the earth turns round ? If there is 

I no absolute space, can a thing turn without turn 
ing with respect to something; and, on the other 
hand, how can we admit Newton s conclusion and 
believe in absolute space? But it is not sufficient 
to state that all possible solutions are equally 
unpleasant to us. We must analyse in each case 
the reason of our dislike, in order to make our 
choice with the knowledge of the cause. The 
long discussion which follows must, therefore, be 

Let us resume our imaginary story. Thick 
clouds hide the stars from men who cannot observe 
them, and even are ignorant of their existence. 
How will those men know that the earth turns 
round ? No doubt, for a longer period than did 
our ancestors, they will regard the soil on which 
they stand as fixed and immovable! They will 


wait a much longer time than we did for the 
coming of a Copernicus; but this Copernicus will 
come at last. How will he come? In the first 
place, the mechanical school of this world would 
not run their heads against an absolute contradic 
tion. In the theory of relative motion we observe, 
besides real forces, t\vo imaginary forces, which 
we call ordinary centrifugal force and compounded 
centrifugal force. Our imaginary scientists can 
thus explain everything by looking upon these two 
forces as real, and they would not see in this a 
contradiction of the generalised principle of inertia, 
for these forces would depend, the one on the 
relative positions of the different parts of the 
system, such as real attractions, and the other on 
their relative velocities, as in the case of real 
frictions. Many difficulties, however, would before 
long awaken their attention. If they succeeded in 
realising an isolated system, the centre of gravity 
of this system would not have an approximately 
rectilinear path. They could invoke, to explain 
this fact, the centrifugal forces which they would 
regard as real, and which, no doubt, they would 
attribute to the mutual actions of the bodies only 
they would not see these forces vanish at great 
distances that is to say, in proportion as the 
isolation is better realised. Far from it. Centri 
fugal force increases indefinitely with distance. 
Already this difficulty would seem to them suffi 
ciently serious, but it would not detain them for 
long. They would soon imagine some very subtle 


medium analogous to our ether, in which all 
bodies would be bathed, and which would exer 
cise on them a repulsive action. But that is not 
all. Space is symmetrical yet the laws of 
motion would present no symmetry. They should 
be able to distinguish between right and left. 
They would see, for instance, that cyclones always 
turn in the same direction, while for reasons of 
symmetry they should turn indifferently in any 
direction. If our scientists were able by dint of 
much hard work to make their universe perfectly 
symmetrical, this symmetry would not subsist, 
although there is no apparent reason why it 
should be disturbed in one direction more than 
in another. They would extract this from the 
situation no doubt they would invent something 
which would not be more extraordinary than the 
glass spheres of Ptolemy, and would thus go on 
accumulating complications until the long-ex 
pected Copernicus would sweep them all away 
with a single blow, saying it is much more simple 
to admit that the earth turns round. Just as 
our Copernicus said to us: " It is more convenient 
to suppose that the earth turns round, because the 
laws of astronomy are thus expressed in a more 
simple language," so he would say to them: "It 
is more convenient to suppose that the earth turns 
round, because the laws of mechanics are thus 
expressed in much more simple language. That 
does not prevent absolute space that is to say, 
the point to which we must refer the earth to 


know if it really does turn round from having 
no objective existence. And hence this affirma 
tion: "the earth turns round," has no meaning, 
since it cannot be verified by experiment; since 
such an experiment not only cannot be realised or 
even dreamed of by the most daring Jules Verne, 
but cannot even be conceived of without con 
tradiction ; or, in other words, these two proposi 
tions, "the earth turns round," and, "it is morel 
convenient to suppose that the earth turns round," | 
have one and the same meaning. There is nothing 
more in one than in the other. Perhaps they will 
not be content with this, and may find it surpris 
ing that among all the hypotheses, or rather all 
the conventions, that can be made on this subject 
there is one which is more convenient than the 
rest? But if we have admitted it without diffi 
culty when it is a question of the laws of 
astronomy, why should we object when it is a 
question of the laws of mechanics ? We have 
seen that the co-ordinates of bodies are deter 
mined by differential equations of the second 
order, and that so are the differences of these 
co-ordinates. This is what we have called the 
generalised principle of inertia, and the principle 
of relative motion. If the distances of these 
bodies were determined in the same way by 
equations of the second order, it seems that the 
mind should be entirely satisfied. How far does 
the mind receive this satisfaction, and why is it 
not content with it ? To explain this we had 


better take a simple example. I assume a system 
analogous to our solar system, but in which fixed 
stars foreign to this system cannot be perceived, 
so that astronomers can only observe the mutual 
distances of planets and the sun, and not the 
absolute longitudes of the planets. If we deduce 
directly from Newton s law the differential equa 
tions which define the variation of these distances, 
these equations will not be of the second order. I 
mean that if, outside Newton s law, we knew the 
initial values of these distances and of their de 
rivatives with respect to time that would not be 
sufficient to determine the values of these same 
distances at an ulterior moment. A datum would 
be still lacking, and this datum might be, for 
example, what astronomers call the area-constant. 
But here \ve may look at it from two different 
points of view. We may consider two kinds of 
constants. In the eyes of the physicist the world 
reduces to a series of phenomena depending, on the 
I one hand, solely on initial phenomena, and, on the 
other hand, on the laws connecting consequence 
|and antecedent. If observation then teaches us 
that a certain quantity is a constant, we shall have 
a choice of two ways of looking at it. So let us 
admit that there is a law which requires that this 
quantity shall not vary, but that by chance it has 
been found to have had in the beginning of time 
this value rather than that, a value that it has 
kept ever since. This quantity might then be 
called an accidental constant. Or again, let us 


admit on the contrary that there is a law of nature 
which imposes on this quantity this value and not 
that. We shall then have what may be called an 
essential constant. For example, in virtue of the 
laws of Newton the duration of the revolution of 
the earth must be constant, But if it is 366 and 
something sidereal days, and not 300 or 400, it is 
because of some initial chance or other. It is an 
accidental constant. If, on the other hand, the 
exponent of the distance which figures in the 
expression of the attractive force is equal to -2 
and not to -3, it is not by chance, but because it 
is required by Newton s la\v. It is an essential 
constant. I do not know if this manner of giving 
to chance its share is legitimate in itself, and if 
there is not some artificiality about this distinc 
tion; but it is certain at least that in proportion 
as Nature has secrets, she will be strictly arbitrary 
and always uncertain in their application. As far 
as the area-constant is concerned, we are accus 
tomed to look upon it as accidental. Is it certain 
that our imaginary astronomers would do the 
same ? If they were able to compare two different 
solar systems, they would get the idea that this 
constant may assume several different values. But 
I supposed at the outset, as I was entitled to do, 
that their system would appear isolated, and that 
they would see no star which was foreign to their 
system. Under these conditions they could only 
detect a single constant, which would have an 
absolutely invariable, unique value. They would 


be led no doubt to look upon it as an essential 

One word in passing to forestall an objection. 
The inhabitants of this imaginary world could 
neither observe nor define the area-constant as we 
do, because absolute longitudes escape their notice; 
but that would not prevent them from being 
rapidly led to remark a certain constant which 
would be naturally introduced into their equations, 
and which would be nothing but what we call the 
area-constant. But then what would happen ? 
If the area-constant is regarded as essential, as 
dependent upon a law of nature, then in order to 
calculate the distances of the planets at any given 
moment it would be sufficient to know the initial 
values of these distances and those of their first 
derivatives. From this new point of view, dis 
tances will be determined by differential equations 
of the second order. Would this completely 
satisfy the minds of these astronomers ? I think 
not. In the first place, they w T ould very soon see 
that in differentiating their equations so as to 
raise them to a higher order, these equations 
would become much more simple, and they would 
be especially struck by the difficulty which arises 
from symmetry. They would have to admit 
different laws, according as the aggregate of the 
planets presented the figure of a certain polyhedron 
or rather of a regular polyhedron, and these conse 
quences can only be escaped by regarding the area- 
constant as accidental. I have taken this particular 


example, because I have imagined astronomers 
who would not be in the least concerned with 
terrestrial mechanics and whose vision would be 
bounded by the solar system. But our con 
clusions apply in all cases. Our universe is more 
extended than theirs, since we have fixed stars; 
but it, too, is very limited, so we might reason on 
the whole of our universe just as these astronomers 
do on their solar system. We thus see that we 
should be definitively led to conclude that the 
equations which define distances are of an order 
higher than the second. Why should this alarm 
us why do we find it perfectly natural that the 
sequence of phenomena depends on initial values 
of the first derivatives of these distances, while we 
hesitate to admit that they may depend on the 
initial values of the second derivatives ? It can 
only be because of mental habits created in us by 
the constant study of the generalised principle of 
inertia and of its consequences. The values of the 
distances at any given moment depend upon their 
initial values, on that of their first derivatives, and 
something else. What is that something else ? If 
we do not want it to be merely one of the second 
derivatives, we have only the choice of hypotheses. 
Suppose, as is usually done, that this something 
else is the absolute orientation of the universe in 
space, or the rapidity with which this orientation 
varies; this may be, it certainly is, the most con 
venient solution for the geometer. But it is not 
the most satisfactory for the philosopher, because 


this orientation does not exist. We may assume 
that this something else is the position or the 
velocity of some invisible body, and this is what is 
done by certain persons, who have even called the 
body Alpha, although we are destined to never 
know anything about this body except its name. 
This is an artifice entirely analogous to that of 
which I spoke at the end of the paragraph con 
taining my reflections on the principle of inertia. 
But as a matter of fact the difficulty is artificial. 
Provided that the future indications of our instru 
ments can only depend on the indications which 
they have given us, or that they might have 
formerly given us, such is all we want, and with 
these conditions we may rest satisfied. 



Energetics. The difficulties raised by the classi 
cal mechanics have led certain minds to prefer a 
new system which they call Energetics. Energetics 
took its rise in consequence of the discovery of the 
principle of the conservation of energy. Helm- 
holtz gave it its definite form. We begin by de 
fining two quantities which play a fundamental 
part in this theory. They are kinetic energy, or 
vis viva, and potential energy. Every change 
that the bodies of nature can undergo is regulated 
by two experimental laws. First, the sum of the 
kinetic and potential energies is constant. This 
is the principle of the conservation of energy. 
Second, if a system of bodies is at A at the time t , 
and at B at the time 15 it always passes from the 
first position to the second by such a path that 
the mean value of the difference between the two 
kinds of energy in the interval of time which 
separates the two epochs t and t l is a minimum. 
This is Hamilton s principle, and is one of the 
forms of the principle of least action. The 
energetic theory has the following advantages 


over the classical. First, it is less incomplete 
that is to say, the principles of the conservation of 
energy and of Hamilton teach us more than the 
fundamental principles of the classical theory, and 
exclude certain motions which do not occur in 
nature and which would be compatible with the 
classical theory. Second, it frees us from the 
hypothesis of atoms, which it was almost impos 
sible to avoid with the classical theory. But in 
its turn it raises fresh difficulties. The definitions 
of the two kinds of energy would raise difficulties 
almost as great as those of force and mass in the 
first system. However, we can get out of these 
difficulties more easily, at any rate in the simplest 
cases. Assume an isolated system formed of a 
certain number of material points. Assume that 
these points are acted upon by forces depending 
only on their relative position and their dis 
tances apart, and independent of their velocities. 
In virtue of the principle of the conservation of 
energy there must be a function of forces. In this 
simple case the enunciation of the principle of the 
conservation of energy is of extreme simplicity. 
A certain quantity, which may be determined by 
experiment, must remain constant. This quantity 
is the sum of two terms. The first depends only on 
the position of the material points, and is inde 
pendent of their velocities; the second is pro 
portional to the squares of these velocities. This 
decomposition can only take place in one way. 
The first of these terms, which I shall call U, will 


be potential energy ; the second, which I shall call 
T, will be kinetic energy. It is true that if T + U 
is constant, so is any function of T + U, < (T + U). 
But this function <f> (T+U) will not be the sum of 
two terms, the one independent of the velocities, 
and the other proportional to the square of the 
velocities. Among the functions which remain 
constant there is only one which enjoys this pro 
perty. It is T + U (or a linear function of T + U), 
it matters not which, since this linear function may 
always be reduced to T + U by a change of unit 
and of origin. This, then, is what we call energy. 
The first term we shall call potential energy, and 
the second kinetic energy. The definition of the 
two kinds of energy may therefore be carried 
through without any ambiguity. 

So it is with the definition of mass. Kinetic 
energy, or vis viva, is expressed very simply by the 
aid of the masses, and of the relative velocities of all 
the material points with reference to one of them. 
These relative velocities may be observed, and 
when we have the expression of the kinetic energy 
as a function of these relative velocities, the co 
efficients of this expression will give us the masses. 
So in this simple case the fundamental ideas can 
be defined without difficulty. But the difficulties 
reappear in the more complicated cases if the 
forces, instead of depending solely on the dis 
tances, depend also on the velocities. For ex 
ample, Weber supposes the mutual action of two 
electric molecules to depend not only on their 


distance but on their velocity and on their accelera 
tion. If material points attracted each other 
according to an analogous law, U would depend 
on the velocity, and it might contain a term 
proportional to the square of the velocity. How 
can we detect among such terms those that arise 
from T or U ? and how, therefore, can we dis 
tinguish the two parts of the energy ? But there 
is more than this. How can we define energy 
itself? We have no more reason to take as our 
definition T+U rather than any other function of 
T + U, when the property which characterised 
T + U has disappeared namely, that of being the 
sum of two terms of a particular form. But that 
is not all. We must take account, not only of 
mechanical energy properly so called, but of the 
other forms of energy heat, chemical energy, 
electrical energy, etc. The principle of the con 
servation of energy must be written T+U+Q= 
a constant, where T is the sensible kinetic energy, 
U the potential energy of position, depending only 
on the position of the bodies, Q the internal 
molecular energy under the thermal, chemical, or 
electrical form. This would be all right if the 
three terms were absolutely distinct ; if T were 
proportional to the square of the velocities, U 
independent of these velocities and of the state of 
the bodies, Q independent of the velocities and of 
the positions of the bodies, and depending only on 
their internal state. The expression for the energy 
could be decomposed in one way only into three 


terms of this form. But this is not the case. Let 
us consider electrified bodies. The electro-static 
energy due to their mutual action will evidently 
depend on their charge i.e., on their state ; 
but it will equally depend on their position. 
If these bodies are in motion, they will act 
electro-dynamically on one another, and the 
electro-dynamic energy will depend not only on 
their state and their position but on their velocities. 
We have therefore no means of making the selec 
tion of the terms which should form part of T, 
and U, and Q, and of separating the three parts of 
the energy. IfT + U + Q is constant, the same is 
true of any function whatever, </> (T + U + Q). 

If T + U + Q were of the particular form that I 
have suggested above, no ambiguity would ensue. 
Among the functions </> (T + U + Q) which remain 
constant, there is only one that would be of this 
particular form, namely the one which I would 
agree to call energy. But I have said this is not 
rigorously the case. Among the functions that 
remain constant there is not one which can 
rigorously be placed in this particular form. How 
then can we choose from among them that which 
should be called energy ? We have no longer 
any guide in our choice. 

Of the principle of the conservation of energy 
there is nothing left then but an enunciation: 
There is something which remains constant. In this 
form it, in its turn, is outside the bounds of ex 
periment and reduced to a kind of tautology. It 


is clear that if the world is governed by laws 
there will be quantities which remain constant. 
Like Newton s laws, and for an analogous reason, 
the principle of the conservation of energy being 
based on experiment, can no longer be invalidated 
by it. 

This discussion shows that, in passing from the 
classical system to the energetic, an advance has 
been made ; but it shows, at the same time, that 
we have not advanced far enough. 

Another objection seems to be still more serious. 
The principle of least action is applicable to revers 
ible phenomena, but it is by no means satisfactory 
as far as irreversible phenomena are concerned. 
Helmholtz attempted to extend it to this class 
of phenomena, but he did not and could not 
succeed. So far as this is concerned all has yet to 
be done. The very enunciation of the principle of 
least action is objectionable. To move from one 
point to another, a material molecule, acted upon 
by no force, but compelled to move on a surface, 
will take as its path the geodesic line i.e., the 
shortest path. This molecule seems to know the 
point to which we want to take it, to foresee 
the time that it will take it to reach it by such 
a path, and then to know how to choose the most 
convenient path. The enunciation of the prin 
ciple presents it to us, so to speak, as a living 
and free entity. It is clear that it would be better 
to replace it by a less objectionable enunciation, 
one in which, as philosophers would say, final 


effects do not seem to be substituted for acting 

Thcr mo-dynamics. The role of the two funda 
mental principles of thermo-dynamics becomes 
daily more important in all branches of natural 
philosophy. Abandoning the ambitious theories 
of forty years ago, encumbered as they were with 
molecular hypotheses, we now try to rest on 
thermo-dynamics alone the entire edifice of 
mathematical physics. Will the two principles 
of Mayer and of Clausius assure to it founda 
tions solid enough to last for some time ? We 
all feel it, but whence does our confidence 
arise ? An eminent physicist said to me one day, 
apropos of the law of errors: every one stoutly \ 
believes it, because mathematicians imagine that 
it is an effect of observation, and observers imagine 
that it is a mathematical theorem. And this was 
for a long time the case with the principle of the 
conservation of energy. It is no longer the same 
now. There is no one who does not know that it 
is an experimental fact. But then who gives us 
the right of attributing to the principle itself more 
generality and more precision than to the experi 
ments which have served to demonstrate it? This 
is asking, if it is legitimate to generalise, as we do 
every day, empiric data, and I shall not be so 
foolhardy as to discuss this question, after so many 
philosophers have vainly tried to solve it. One 
thing alone is certain. If this permission were 
refused to us, science could not exist; or at least 



would be reduced to a kind of inventory, to the 
ascertaining of isolated facts. It would not longer 
be to us of any value, since it could not satisfy our 
need of order and harmony, and because it would 
be at the same time incapable of prediction.. As 
the circumstances which have preceded any fact 
whatever will never again, in all probability, be 
simultaneously reproduced, we already require a 
first generalisation to predict whether the fact will 
be renewed as soon as the least of these circum 
stances is changed, f But every proposition may 
be generalised in an infinite number of ways. 
Among all possible generalisations we must 
choose, and we cannot but choose the simplest. 
We are therefore led to adopt the same course 
as if a simple law were, other things being equal, 
more probable than a complex law. A century 
ago it was frankly confessed and proclaimed 
abroad that Nature loves simplicity; but Nature 
has proved the contrary since then on more than 
one occasion. We no longer confess this tendency, 
and we only keep of it what is indispensable, so 
that science may not become impossible. In 
formulating a general, simple, and formal law, 
based on a comparatively small number of not alto 
gether consistent experiments, we have only obeyed 
a necessity from which the human mind cannot 
free itself. ^But there is something more, and that 
is why I dwell on this topic. No one doubts that 
Mayer s principle is not called upon to survive all 
the particular laws from which it was deduced, in 


the same way that Newton s law has survived the 
laws of Kepler from which it was derived, and 
which are no longer anything but approximations, 
if we take perturbations into account. Now why 
does this principle thus occupy a kind of privileged 
position among physical laws? There are many 
reasons for that. At the outset we think that we 
cannot reject it, or even doubt its absolute rigour, 
without admitting the possibility of perpetual 
motion; we certainly feel distrust at such a 
prospect, and we believe ourselves less rash in 
affirming it than in denying it. That perhaps is 
not quite accurate. The impossibility of perpetual 
motion only implies the conservation of energy for 
reversible phenomena. The imposing simplicity 
of Mayer s principle equally contributes to 
strengthen our faith. In a law immediately de 
duced from experiments, such as Mariotte s law, 
this simplicity would rather appear to us a reason 
for distrust ; but here this is no longer the case. 
We take elements which at the first glance are 
unconnected; these arrange themselves in an un 
expected order, and form a harmonious whole. 
We cannot believe that this unexpected har 
mony is a mere result of chance. Our conquest 
appears to be valuable to us in proportion to the 
efforts it has cost, and we feel the more certain of 
having snatched its true secret from Nature in pro 
portion as Nature has appeared more jealous of our 
attempts to discover it. But these are only small 
reasons. Before we raise Mayer s law to the 


dignity of an absolute principle, a deeper discussion 
is necessary. But if we embark on this discussion 
we see that this absolute principle is not even easy 
to enunciate. In every particular case we clearly 
see what energy is, and we can give it at least a 
provisory definition; but it is impossible to find 
a general definition of it. If we wish to enunciate 
the principle in all its generality and apply it to 
the universe, we see it vanish, so to speak, and 
nothing is left but this there is something which 
remains constant. But has this a meaning ? In 
the determinist hypothesis the state of the uni 
verse is determined by an extremely large number 
n of parameters, which I shall call x it x. 2 , x 3 . . . x n . 
As soon as we know at a given moment the values of 
these n parameters, we also know their derivatives 
with respect to time, and we can therefore cal 
culate the values of these same parameters at an 
anterior or ulterior moment. In other words, 
these n parameters specify n differential equations 
of the first order. These equations have n-i 
integrals, and therefore there are n-i functions of 
x i> X 2> #3 . . x Mt which remain constant. If we 
say then, there is something which remains constant, 
we are only enunciating a tautology. We would 
be even embarrassed to decide which among all 
our integrals is that which should retain the name 
of energy. Besides, it is not in this sense that 
Mayer s principle is understood when it is applied 
to a limited system. We admit, then, that p of 
our n parameters vary independently so that we 


have only n -p relations, generally linear, between 
our n parameters and their derivatives. Suppose, 
for the sake of simplicity, that the sum of the 
work done by the external forces is zero, as well 
as that of all the quantities of heat given off from 
the interior: what will then be the meaning of 
our principle ? There is a combination of these n -p 
relations, of which the first member is an exact 
differential; and then this differential vanishing 
in virtue of our np relations, its integral is a 
constant, and it is this integral which we call 
energy. But how can it be that there are several 
parameters whose variations are independent ? 
That can only take place in the case of external 
forces (although \ve have supposed, for the sake 
of simplicity, that the algebraical sum of all the 
work done by these forces has vanished). If, 
in fact, the system were completely isolated from 
all external action, the values of our n parameters 
at a given moment would suffice to determine 
the state of the system at any ulterior moment 
whatever, provided that we still clung to the deter- 
minist hypothesis. We should therefore fall back 
on the same difficulty as before. If the future 
state of the system is not entirely determined 
by its present state, it is because it further depends 
on the state of bodies external to the system. 
But then, is it likely that there exist among the 
parameters % which define the state of the system of 
equations independent of this state of the external 
bodies? and if in certain cases we think we can 


find them, is it not only because of our ignorance, 
and because the influence of these bodies is too 
weak for our experiment to be able to detect it ? 
If the system is not regarded as completely 
isolated, it is probable that the rigorously exact 
expression of its internal energy will depend upon 
the state of the external bodies. Again, I have 
supposed above that the sum of all the external 
work is zero, and if we wish to be free from 
this rather artificial restriction the enunciation 
becomes still more difficult. To formulate 
Mayer s principle by giving it an absolute 
meaning, we must extend it to the whole 
universe, and then we find ourselves face to 
face with the very difficulty we have endeavoured 
to avoid. To sum up, and to use ordinary 
language, the law of the conservation of energy 
can have only one significance, because there is 
in it a property common to all possible properties; 
but in the determinist hypothesis there is only one 
possible, and then the law has no meaning. In 
the indeterminist hypothesis, on the other hand, 
it would have a meaning even if \ve wished to 
regard it in an absolute sense. It would appear 
as a limitation imposed on freedom. 

But this word warns me that I am wandering 
from the subject, and that I am leaving the 
domain of mathematics and physics. I check 
myself, therefore, and I wish to retain only one 
impression of the whole of this discussion, and 
that is, that Mayer s law is a form subtle enough 


for us to be able to put into it almost anything we 
like. I do not mean by that that it corresponds 
to no objective reality, nor that it is reduced to 
mere tautology; since, in each particular case, and 
provided we do not wish to extend it to the 
absolute, it has a perfectly clear meaning. This 
subtlety is a reason for believing that it will last 
long; and as, on the other hand, it will only 
disappear to be blended in a higher harmony, 
we may work with confidence and utilise it, 
certain beforehand that our work will not be 

Almost everything that I have just said 
applies to the principle of Clausius. What 
distinguishes it is, that it is expressed by an 
inequality. It will be said perhaps that it is 
the same with all physical laws, since their 
precision is always limited by errors of 
observation. But they at least claim to be 
first approximations, and we hope to replace 
them little by little by more exact laws. If, 
on the other hand, the principle of Clausius 
reduces to an inequality, this is not caused by 
the imperfection of our means of observation, but 
by the very nature of the question. 

General Conclusions on Part III. The prin 
ciples of mechanics are therefore presented to us 
under two different aspects. On the one hand, 
there are truths founded on experiment, and 
verified approximately as far as almost isolated 
systems are concerned ; on the other hand, 


there are postulates applicable to the whole of 
the universe and regarded as rigorously true. 
If these postulates possess a generality and a 
certainty which falsify the experimental truths 
from which they were deduced, it is because 
they reduce in final analysis to a simple con 
vention that we have a right to make, because 
we are certain beforehand that no experiment 
can contradict it. This convention, however, is 
not absolutely arbitrary; it is not the child 
of our caprice. \Ye admit it because certain 
experiments have shown us that it will be con 
venient, and thus is explained how experiment 
has built up the principles of mechanics, and 
why, moreover, it cannot reverse them. Take a 
comparison with geometry. The fundamental 
propositions of geometry, for instance, Euclid s 
postulate, are only conventions, and it is quite 
as unreasonable to ask if they are true or false 
as to ask if the metric system is true or false. 
Only, these conventions are convenient, and there 
are certain experiments which prove it to us. At 
the first glance, the analogy is complete, the role 
of experiment seems the same. We shall there 
fore be tempted to say, either mechanics must 
be looked upon as experimental science and then 
it should be the same with geometry; or, on the 
contrary, geometry is a deductive science, and 
then we can say the same of mechanics. Such 
a conclusion would be illegitimate. The experi 
ments which have led us to adopt as more 


convenient the fundamental conventions of 
geometry refer to bodies which have nothing 
in common with those that are studied by 
geometry. They refer to the properties of solid 
bodies and to the propagation of light in a straight 
line. These are mechanical, optical experiments. 
In no way can they be regarded as geometrical 
experiments. And even the probable reason why 
our geometry seems convenient to us is, that our 
bodies, our hands, and our limbs enjoy the properties 
of solid bodies. Our fundamental experiments are 
pre-eminently physiological experiments which 
refer, not to the space which is the object that 
geometry must study, but to our body that is to 
say, to the instrument which we use for that 
study. On the other hand, the fundamental 
conventions of mechanics and the experiments 
which prove to us that they are convenient, 
certainly refer to the same objects or to analogous 
objects. Conventional and general principles are 
the natural and direct generalisations of experi 
mental and particular principles. Let it not be 
said that I am thus tracing artificial frontiers 
between the sciences; that I am separating by 
a barrier geometry properly so called from the 
study of solid bodies. I might just as well 
raise a barrier between experimental mechanics 
and the conventional mechanics of general 
principles. Who does not see, in fact, that 
by separating these two sciences we mutilate 
both, and that what will remain of the conven- 


tional mechanics when it is isolated will be but 
very little, and can in no way be compared with 
that grand body of doctrine which is called 

We now understand why the teaching of 
mechanics should remain experimental. Thus 
only can we be made to understand the genesis 
of the science, and that is indispensable for 
a complete knowledge of the science itself. 
Besides, if we study mechanics, it is in order 
to apply it ; and we can only apply it if it remains 
objective. Now, as we have seen, when principles 
gain in generality and certainty they lose in 
objectivity. It is therefore especially with the 
objective side of principles that we must be 
early familiarised, and this can only be by 
passing from the particular to the general, instead 
of from the general to the particular. 

Principles are conventions and definitions in 
disguise. They are, however, deduced from 
experimental laws, and these laws have, so to 
speak, been erected into principles to which 
our mind attributes an absolute value. Some 
philosophers have generalised far too much. 
They have thought that the principles were 
the whole of science, and therefore that the 
whole of science was conventional. This para 
doxical doctrine, which is called Nominalism, 
cannot stand examination. How can a law 
become a principle ? It expressed a relation 
between two real terms, A and B; but it was 


not rigorously true, it was only approximate. 
We introduce arbitrarily an intermediate term, C, 
more or less imaginary, and C is by definition that 
which has with A exactly the relation expressed 
by the law. So our law is decomposed into an 
absolute and rigorous principle which expresses 
the relation of A to C, and an approximate experi 
mental and revisable law which expresses the: 
relation of C to B. But it is clear that however 
far this decomposition may be carried, laws will 
always remain. We shall now enter into the 
domain of laws properly so called. 




The Role of Experiment and Generalisation. 
Experiment is the sole source of truth. It alone 
can teach us something new ; it alone can give 
us certainty. These are two points that cannot 
be questioned. But then, if experiment is every 
thing, what place is left for mathematical physics ? 
What can experimental physics do with such an 
auxiliary an auxiliary, moreover, which seems 
useless, and even may be dangerous? 

However, mathematical physics exists. It has 
rendered undeniable service, and that is a fact 
which has to be explained. It is not sufficient 
merely to observe ; we must use our observations, 
and for that purpose we must generalise. This 
is what has always been done, only as the recollec 
tion of past errors has made man more and more 
circumspect, he has observed more and more and 
generalised less and less. Every age has scoffed 
at its predecessor, accusing it of having generalised 


too boldly and too naively. Descartes used to 
commiserate the lonians. Descartes in his turn 
makes us smile, and no doubt some day our 
children will laugh at us. Is there no way of 
getting at once to the gist of the matter, and 
thereby escaping the raillery which we foresee ? 
Cannot we be content with experiment alone ? 
No, that is impossible ; that would be a complete 
misunderstanding of the true character of science. 
The man of science must work with method. 
Science is built up of facts, as a house is built of 
stones ; but an accumulation of facts is no more a 
science than a heap of stones is a house. Most 
important of all, the man of science must exhibit 
foresight. Carlyle has written somewhere some 
thing after this fashion. " Nothing but facts are 
of importance. John Lackland passed by here. 
Here is something that is admirable. Here is a 
reality for which I would give all the theories in 
the world." 1 Carlyle was a compatriot of Bacon, 
and, like him, he wished to proclaim his worship 
of the God of Things as they are. 

But Bacon would not have said that. That is 
the language of the historian. The physicist 
would most likely have said : " John Lackland 
passed by here. It is all the same to me, for he 
will not pass this way again." 

We all know that there are good and bad 
experiments. The latter accumulate in vain. 
Whether there are a hundred or a thousand, 

1 V. Past and Present, end of Chapter I., Book II. [TR.] 


one single piece of work by a real master by a 
Pasteur, for example will be sufficient to sweep 
them into oblivion. Bacon w 7 ould have thoroughly 
understood that, for he invented the phrase experi- 
mentuni crucis; but Carlyle would not have under 
stood it. A fact is a fact. A student has read 
such and such a number on his thermometer. 
He has taken no precautions. It does not matter; 
he has read it, and if it is only the fact which 
counts, this is a reality that is as much entitled 
to be called a reality as the peregrinations of King 
John Lackland. What, then, is a good experiment? 
It is that which teaches us something more than 
V an isolated fact. It is that which enables us to 
predict, and to generalise. Without generalisa 
tion, prediction is impossible. The circumstances 
under which one has operated will never again 
be reproduced simultaneously. The fact observed 
will never be repeated. All that can be affirmed 
is that under analogous circumstances an analogous 
fact will be produced. To predict it, we must 
therefore invoke the aid of analogy that is to say, 
even at this stage, we must generalise. However 
timid we may be, there must be interpolation. 
Experiment only gives us a certain number of 
isolated points. They must be connected by a 
continuous line, and this is a true generalisation. 
But more is done. The curve thus traced will 
pass between and near the points observed; it 
will not pass through the points themselves. 
Thus we are not restricted to generalising our 


experiment, we correct it ; and the physicist who 
would abstain from these corrections, and really 
content himself with experiment pure and simple, 
would be compelled to enunciate very extra 
ordinary laws indeed. Detached facts cannot 
therefore satisfy us, and that is why our science 
must be ordered, or, better still, generalised. 

It is often said that experiments should be made 
without preconceived ideas. That is impossible. 
Not only would it make every experiment fruitless, 
but even if we wished to do so, it could not be 
done. Every man has his own conception of the 
world, and this he cannot so easily lay aside. We 
must, for example, use language, and our language 
is necessarily steeped in preconceived ideas. Only 
they are unconscious preconceived ideas, which 
are a thousand times the most dangerous of all. 
Shall we say, that if we cause others to intervene of 
which we are fully conscious, that we shall only 
aggravate the evil? I do not think so. I am 
inclined to think that they will serve as ample 
counterpoises I was almost going to say antidotes. 
They will generally disagree, they will enter into 
conflict one with another, and ipso facto, they will 
force us to look at things under different aspects. 
This is enough to free us. He is no longer a slave 
who can choose his master. 

Thus, by generalisation, every fact observed 
enables us to predict a large number of others ; 
only, we ought not to forget that the first alone 
is certain, and that all the others are merely 


probable. However solidly founded a prediction 
may appear to us, we are never absolutely sure that 
experiment will not prove it to be baseless if we 
set to work to verify it. But the probability of its 
accuracy is often so great that practically we may 
be content with it. It is far better to predict 
without certainty, than never to have predicted 
at all. We should never, therefore, disdain to 
verify when the opportunity presents itself. But 
every experiment is long and difficult, and the 
labourers are few, and the number of facts which 
we require to predict is enormous ; and besides 
this mass, the number of direct verifications that 
we can make will never be more than a negligible 
quantity. Of this little that we can directly attain 
we must choose the best. Every experiment must 
enable us to make a maximum number of predic 
tions having the highest possible degree of prob 
ability. The problem is, so to speak, to increase 
the output of the scientific machine. I may be 
permitted to compare science to a library which 
must go on increasing indefinitely; the librarian 
has limited funds for his purchases, and he must, 
therefore, strain every nerve not to waste them. 
Experimental physics has to make the purchases, 
and experimental physics alone can enrich the 
library. As for mathematical physics, her duty 
is to draw up the catalogue. If the catalogue is 
well done the library is none the richer for it ; but 
the reader will be enabled to utilise its riches; 
and also by showing the librarian the gaps in his 


collection, it will help him to make a judicious 
use of his funds, which is all the more important, 
inasmuch as those funds are entirely inadequate. 
That is the role of mathematical physics. It 
must direct generalisation, so as to increase what 
I called just now the output of science. By what 
means it does this, and how it may do it without 
danger, is what we have now to examine. 

The Unity oj Nature. Let us first of all observe 
that every generalisation supposes in a certain 
measure a belief in the unity and simplicity of 
Nature. As far as the unity is concerned, there 
can be no difficulty. If the different parts of the 
universe were not as the organs of the same body, 
they would not re-act one upon the other; they 
would mutually ignore each other, and we in 
particular should only know one part. We need 
not, therefore, ask if Nature is one, but how she 
is one. 

As for the second point, that is not so clear. It 
is not certain that Nature is simple. Can we 
without danger act as if she were ? 

There was a time when the simplicity of 
Mariotte s law was an argument in favour of its 
accuracy: when Fresnel himself, after having said 
in a conversation with Laplace that Nature cares 
naught for analytical difficulties, was compelled 
to explain his words so as not to give offence to 
current opinion. Nowadays, ideas have changed 
considerably ; but those who do not believe that 
natural laws must be simple, are still often obliged 



to act as if they did believe it. They cannot 
entirely dispense with this necessity without 
making all generalisation, and therefore all science, 
impossible. It is clear that any fact can be 
generalised in an infinite number of ways, and 
it is a question of choice. The choice can only 
be guided by considerations of simplicity. Let 
us take the most ordinary case, that of interpola 
tion. We draw a continuous line as regularly as 
possible between the points given by observation. 
Why do we avoid angular points and inflexions 
that are too sharp ? Why do we not make our 
curve describe the most capricious zigzags ? It 
is because we know beforehand, or think we know, 
that the law we have to express cannot be so 
complicated as all that. The mass of Jupiter 
may be deduced either from the movements of 
his satellites, or from the perturbations of the 
major planets, or from those of the minor planets. 
If we take the mean of the determinations obtained 
by these three methods, we find three numbers 
very close together, but not quite identical. This 
result might be interpreted by supposing that the 
gravitation constant is not the same in the three 
cases; the observations would be certainly much 
better represented. Why do we reject this inter 
pretation ? Not because it is absurd, but because 
it is uselessly complicated. W 7 e shall only accept 
it when we are forced to, and it is not imposed 
upon us yet. To sum up, in most cases every law 
is held to be simple until the contrary is proved. 


This custom is imposed upon physicists by the 
reasons that I have indicated, but how can it be 
justified in the presence of discoveries which daily 
show us fresh details, richer and more complex? 
How can we even reconcile it with the unity of 
nature ? For if all things are interdependent, 
the relations in which so many different objects 
intervene can no longer be simple. 

If we study the history of science we see pro 
duced two phenomena which are, so to speak, 
each the inverse of the other. Sometimes it is 
simplicity which is hidden under what is 
apparently complex ; sometimes, on the contrary, 
it is simplicity which is apparent, and which 
conceals extremely complex realities. What is 
there more complicated than the disturbed 
motions of the planets, and what more simple 
than Newton s law ? There, as Fresnel said, 
Nature playing with analytical difficulties, only 
uses simple means, and creates by their combina 
tion I know not what tangled skein. Here it is 
the hidden simplicity which must be disentangled. 
Examples to the contrary abound. In the kinetic 
theory of gases, molecules of tremendous velocity 
are discussed, whose paths, deformed by incessant 
impacts, have the most capricious shapes, and 
plough their way through space in every direction. 
The result observable is Mariotte s simple law. 
Each individual fact was complicated. The law 
of great numbers has re-established simplicity in 
the mean. Here the simplicity is only apparent, 


and the coarseness of our senses alone prevents us 
from seeing the complexity. 

Many phenomena obey a law of proportion 
ality. But why? Because in these phenomena 
there is something which is very small. The 
simple law observed is only the translation of 
the general analytical rule by which the infinitely 
small increment of a function is proportional 
to the increment of the variable. As in reality 
our increments are not infinitely small, but only 
very small, the law of proportionality is only 
approximate, and simplicity is only apparent. 
What I have just said applies to the law of the 
superposition of small movements, which is so 
fruitful in its applications and which is the founda 
tion of optics. 

And Newton s law itself? Its simplicity, so 
long undetected, is perhaps only apparent. Who 
knows if it be not due to some complicated 
mechanism, to the impact of some subtle matter 
animated by irregular movements, and if it has 
not become simple merely through the play of 
averages and large numbers? In any case, it 
is difficult not to suppose that the true law con 
tains complementary terms which may become 
sensible at small distances. If in astronomy they 
are negligible, and if the law thus regains its 
simplicity, it is solely on account of the enormous 
distances of the celestial bodies. No doubt, if our 
means of investigation became more and more 
penetrating, we should discover the simple beneath 


the complex, and then the complex from the 
simple, and then again the simple beneath the 
complex, and so on, without ever being able to 
predict what the last term will be. We must stop 
somewhere, and for science to be possible we must 
stop where we have found simplicity. That is the 
only ground on which we can erect the edifice of 
our generalisations. But, this simplicity being 
only apparent, will the ground be solid enough ? 
That is what we have now to discover. 

For this purpose let us see what part is played 
in our generalisations by the belief in simplicity. 
We have verified a simple law in a considerable 
number of particular cases. We refuse to admit 
that this coincidence, so often repeated, is a result 
of mere chance, and we conclude that the law 
must be true in the general case. 

Kepler remarks that the positions of a planet 
observed by Tycho are all on the same ellipse. 
Not for one moment does he think that, by a 
singular freak of chance, Tycho had never looked 
at the heavens except at the very moment when 
the path of the planet happened to cut that 
ellipse. What does it matter then if the simplicity 
be real or if it hide a complex truth ? Whether it 
be due to the influence of great numbers which 
reduces individual differences to a level, or to the 
greatness or the smallness of certain quantities 
which allow of certain terms to be neglected in 
no case is it due to chance. This simplicity, real 
or apparent, has always a cause. We shall there- 


fore always be able to reason in the same fashion, 
and if a simple law has been observed in several 
particular cases, we may legitimately suppose that 
it still will be true in analogous cases. To refuse 
to admit this would be to attribute an in 
admissible role to chance. However, there is a 
difference. If the simplicity were real and pro 
found it would bear the test of the increasing 
precision of our methods of measurement. If, 
then, we believe Nature to be profoundly simple, 
we must conclude that it is an approximate and 
not a rigorous simplicity. This is what was 
formerly done, but it is what we have no longer 
the right to do. The simplicity of Kepler s laws, 
for instance, is only apparent ; but that does not 
prevent them from being applied to almost all 
systems analogous to the solar system, though 
that prevents them from being rigorously exact. 

Role of Hypothesis. Every generalisation is a 
hypothesis. Hypothesis therefore plays a neces 
sary role, which no one has ever contested. Only, 
it should always be as soon as possible submitted 
to verification. It goes without saying that, if it 
cannot stand this test, it must be abandoned 
without any hesitation. This is, indeed, what 
is generally done; but sometimes with a certain 
impatience. Ah well ! this impatience is not 
justified. The physicist who has just given up 
one of his hypotheses should, on the contrary, 
rejoice, for he found an unexpected opportunity of 
discovery. His hypothesis, I imagine, had not 


been lightly adopted, It took into account all the 
known factors which seem capable of intervention 
in the phenomenon. If it is not verified, it is 
because there is something unexpected and extra 
ordinary about it, because we are on the point 
of finding something unknown and new. Has 
the hypothesis thus rejected been sterile ? Far 
from it. It may be even said that it has rendered 
more service than a true hypothesis. Not only 
has it been the occasion of a decisive experiment, 
but if this experiment had been made by chance, 
without the hypothesis, no conclusion could have 
been drawn ; nothing extraordinary would have 
been seen ; and only one fact the more would have 
been catalogued, without deducing from it the 
remotest consequence. 

Now, under what conditions is the use of 
hypothesis without danger ? The proposal to 
submit all to experiment is not sufficient. Some 
hypotheses are dangerous, first and foremost 
those which are tacit and unconscious. And 
since we make them without knowing them, 
we cannot get rid of them. Here again, there 
is a service that mathematical physics may 
render us. By the precision which is its char 
acteristic, we are compelled to formulate all the 
hypotheses that we would unhesitatingly make 
without its aid. Let us also notice that it is 
important not to multiply hypotheses indefinitely. 
If we construct a theory based upon multiple hypo 
theses, and if experiment condemns it, which of 


the premisses must be changed ? It is impossible 
to tell. Conversely, if the experiment succeeds, 
must we suppose that it has verified all these 
hypotheses at once ? Can several unknowns be 
determined from a single equation ? 
I We must also take care to distinguish between 
the different kinds of hypotheses. First of all, 
there are those w r hich are quite natural and 
( necessary. It is difficult not to suppose that the 
influence of very distant bodies is quite negligible, 
that small movements obey a linear law, and that 
effect is a continuous function of its cause. I will 
say as much for the conditions imposed by 
symmetry. All these hypotheses affirm, so to 
speak, the common basis of all the theories of 
mathematical physics. They are the last that 
should be abandoned. There is a second category 
of hypotheses which I shall qualify as indifferent. 
In most questions the analyst assumes, at the 
beginning of his calculations, either that matter is 
continuous, or the reverse, that it is formed of 
atoms. In either case, his results would have 
been the same. On the atomic supposition he has 
a little more difficulty in obtaining them that is 
all. If, then, experiment confirms his conclusions, 
will he suppose that he has proved, for example, 
the real existence of atoms ? 

In optical theories two vectors are introduced, 
one of which we consider as a velocity and the 
other as a vortex. This again is an indifferent 
hypothesis, since we should have arrived at the 


same conclusions by assuming the former to be 
a vortex and the latter to be a velocity. The 
success of the experiment cannot prove, therefore, 
that the first vector is really a velocity. It only 
proves one thing namely, that it is a vector; 
and that is the only hypothesis that has really 
been introduced into the premisses. To give it 
the concrete appearance that the fallibility of our 
minds demands, it was necessary to consider it 
either as a velocity or as a vortex. In the same 
way, it was necessary to represent it by an x or a 
y, but. the result will not prove that we were right 
or wrong in regarding it as a velocity; nor will it 
prove we are right or wrong in calling it x and 
not y. 

These indifferent hypotheses are never danger 
ous provided their characters are not misunder 
stood. They may be useful, either as artifices for 
calculation, or to assist our understanding by 
concrete images, to fix the ideas, as we say. They 
need not therefore be rejected. The hypotheses 
of the third category are real generalisations. 
They must be confirmed or invalidated by experi 
ment. Whether verified or condemned, they will 
always be fruitful; but, for the reasons I have 
given, they will only be so if they are not too 

Origin of Mathematical Physics. Let us go 
further and study more closely the conditions 
which have assisted the development of mathe 
matical physics. We recognise at the outset that 


the efforts of men of science have always tended 
to resolve the complex phenomenon given directly 
by experiment into a very large number of ele 
mentary phenomena, and that in three different 

First, with respect to time. Instead of embracing 
in its entirety the progressive development of a 
phenomenon, we simply try to connect each 
moment with the one immediately preceding. 
We admit that the present state of the world 
only depends on the immediate past, without 
being directly influenced, so to speak, by the 
recollection of a more distant past. Thanks to 
this postulate, instead of studying directly the 
whole succession of phenomena, we may confine 
ourselves to writing down its differential equation; 
for the laws of Kepler we substitute the law of 

Next, we try to decompose the phenomena in 
space. What experiment gives us is a confused 
aggregate of facts spread over a scene of consider 
able extent. We must try to deduce the element 
ary phenomenon, which will still be localised in a 
very small region of space. 

A few examples perhaps will make my meaning 
clearer. If \ve wished to study in all its com 
plexity the distribution of temperature in a cooling 
solid, we could never do so. This is simply be 
cause, if we only reflect that a point in the solid 
can directly impart some of its heat to a neigh 
bouring point, it will immediately impart that 


heat only to the nearest points, and it is but 
gradually that the flow of heat will reach other 
portions of the solid. The elementary pheno 
menon is the interchange of heat between two 
contiguous points. It is strictly localised and 
relatively simple if, as is natural, we admit that 
it is not influenced by the temperature of the 
molecules whose distance apart is small. 

I bend a rod: it takes a very complicated form, 
the direct investigation of which would be im 
possible. But I can attack the problem, however, 
if I notice that its flexure is only the resultant of 
the deformations of the very small elements of the 
rod, and that the deformation of each of these 
elements only depends on the forces which are 
directly applied to it, and not in the least on 
those which may be acting on the other elements. 

In all these examples, which may be increased 
without difficulty, it is admitted that there is no 
action at a distance or at great distances. That 
is an hypothesis. It is not always true, as the law 
of gravitation proves. It must therefore be verified. 
If it is confirmed, even approximately, it is valu 
able, for it helps us to use mathematical physics, 
at any rate by successive approximations. If it 
does not stand the test, we must seek something 
else that is analogous, for there are other means 
of arriving at the elementary phenomenon. If 
several bodies act simultaneously, it may happen 
that their actions are independent, and may be 
added one to the other, either as vectors or as scalar 


quantities. The elementary phenomenon is then 
the action of an isolated body. Or suppose, again, 
it is a question of small movements, or more 
generally of small variations which obey the well- 
known law of mutual or relative independence. 
The movement observed will then be decomposed 
into simple movements for example, sound into 
its harmonics, and white light into its monochro 
matic components. When we have discovered in 
which direction to seek for the elementary pheno 
mena, by what means may we reach it ? First, it 
will often happen that in order to predict it, or rather 
in order to predict what is useful to us, it will not 
be necessary to know its mechanism. The law of 
great numbers will suffice. Take for example the 
propagation of heat. Each molecule radiates to 
wards its neighbour we need not inquire accord 
ing to what law; and if we make any supposition 
in this respect, it will be an indifferent hypothesis, 
and therefore useless and unverifiable. In fact, 
by the action of averages and thanks to the 
symmetry of the medium, all differences are 
levelled, and, whatever the hypothesis may be, the 
result is always the same. 

The same feature is presented in the theory of 
elasticity, and in that of capillarity. The neigh 
bouring molecules attract and repel each other, we 
need not inquire by what law. It is enough for us 
that this attraction is sensible at small distances 
only, and that the molecules are very numerous, 
that the medium is symmetrical, and we have 


only to let the law of great numbers come into 

Here again the simplicity of the elementary 
phenomenon is hidden beneath the complexity of 
the observable resultant phenomenon; but in its 
turn this simplicity was only apparent and dis 
guised a very complex mechanism. Evidently the 
best means of reaching the elementary pheno 
menon would be experiment. It would be neces 
sary by experimental artifices to dissociate the 
complex system which nature offers for our in 
vestigations and carefully to study the elements as 
dissociated as possible; for example, natural white 
light would be decomposed into monochromatic 
lights by the aid of the prism, and into polarised 
lights by the aid of the polariser. Unfortunately, 
that is neither always possible nor always suffi 
cient, and sometimes the mind must run ahead of 
experiment. I shall only give one example which 
has always struck me rather forcibly. If I de 
compose white light, I shall be able to isolate a 
portion of the spectrum, but however small it may 
be, it will always be a certain width. In the same 
way the natural lights which are called mono 
chromatic give us a very fine array, but a y which 
is not, however, infinitely fine. It might be 
supposed that in the experimental study of the 
properties of these natural lights, by operating 
with finer and finer rays, and passing on at last 
to the limit, so to speak, we should eventually 
obtain the properties of a rigorously mono- 


chromatic light. That would not be accurate. 
I assume that two rays emanate from the same 
source, that they are first polarised in planes at 
right angles, that they are then brought back 
again to the same plane of polarisation, and that 
we try to obtain interference. If the light were 
rigorously monochromatic, there would be inter 
ference; but with our nearly monochromatic 
lights, there will be no interference, and that, 
however narrow the ray may be. For it to be 
otherwise, the ray would have to be several million 
times finer than the finest known rays. 

Here then we should be led astray by proceeding 
to the limit. The mind has to run ahead of the 
experiment, and if it has done so with success, it 
is because it has allowed itself to be guided by the 
instinct of simplicity. The knowledge of the ele 
mentary fact enables us to state the problem in 
the form of an equation. It only remains to de 
duce from it by combination the observable and 
verifiable complex fact. That is what we call 
integration, and it is the province of the mathe 
matician. It might be asked, why in physical 
science generalisation so readily takes the 
mathematical form. The reason is now easy to 
see. It is not only because we have to express 
numerical laws; it is because the observable 
phenomenon is due to the superposition of a large 
number of elementary phenomena which are all 
similar to each other ; and in this way differential 
equations are quite naturally introduced. It is 


not enough that each elementary phenomenon 
should obey simple laws: all those that we have 
to combine must obey the same law; then only 
is the intervention of mathematics of any use. 
Mathematics teaches us, in fact, to combine like 
with like. Its object is to divine the result of a 
combination without having to reconstruct that 
combination element by element. If we have to 
repeat the same operation several times, mathe 
matics enables us to avoid this repetition by telling 
the result beforehand by a kind of induction. 
This I have explained before in the chapter on 
mathematical reasoning. But for that purpose 
all these operations must be similar; in the con 
trary case we must evidently make up our minds 
to working them out in full one after the other, 
and mathematics will be useless. It is therefore, 
thanks to the approximate homogeneity of the 
matter studied by physicists, that mathematical 
physics came into existence. In the natural 
sciences the following conditions are no longer to 
be found: homogeneity, relative independence of 
remote parts, simplicity of the elementary fact; 
and that is why the student of natural science is 
compelled to have recourse to other modes of 



Significance of Physical Theories. The ephemeral 
nature of scientific theories takes by surprise the 
man of the world. Their brief period of prosperity 
ended, he sees them abandoned one after another ; 
he sees ruins piled upon ruins; he predicts that 
the theories in fashion to-day will in a short time 
succumb in their turn, and he concludes that they 
are absolutely in vain. This is what he calls the 
bankruptcy of science. 

His scepticism is superficial ; he does not take 
into account the object of scientific theories and 
the part they play, or he would understand that 
the ruins may be still good for something. No 
theory seemed established on firmer ground than 
Fresnel s, which attributed light to the move 
ments of the ether. Then if Maxwell s theory is 
to-day preferred, does that mean that Fresnel s 
work was in vain ? No; for Fresnel s object was 
not to know whether there really is an ether, if it 
is or is not formed of atoms, if these atoms really 
move in this way or that; his object was to 
predict optical phenomena. 

This Fresnel s theory enables us to do to- 


day as well as it did before Maxwell s time. The 
differential equations are always true, they may 
be always integrated by the same methods, and 
the results of this integration still preserve their 
value. It cannot be said that this is reducing 
physical theories to simple practical recipes ; 
these equations express relations, and if the 
equations remain true, it is because the relations 
preserve their reality. They teach us now, as they 
did then, that there is such and such a relation 
between this thing and that ; only, the something 
which we then called motion, we now call electric 
current. But these are merely names of the images 
we substituted for the real objects which Nature 
will hide for ever from our eyes. The true relations 
between these real objects are the only reality we 
can attain, and the sole condition is that the same 
relations shall exist between these objects as between 
the images we are forced to put in their place. If 
the relations are known to us, what does it matter 
if we think it convenient to replace one image by 
another ? 

That a given periodic phenomenon (an electric 
oscillation, for instance) is really due to the 
vibration of a given atom, which, behaving like 
a pendulum, is really displaced in this manner or 
that, all this is neither certain nor essential. 
But that there is between the electric oscillation, 
the movement of the pendulum, and all periodic 
phenomena an intimate relationship which corre 
sponds to a profound reality; that this relationship, 



this similarity, or rather this parallelism, is con 
tinued in the details ; that it is a consequence of 
more general principles such as that of the con 
servation of energy, and that of least action ; this 
we may affirm ; this is the truth which will ever 
remain the same in whatever garb we may see fit 
to clothe it. 

Many theories of dispersion have been proposed. 
The first were imperfect, and contained but little 
truth. Then came that of Helmholtz, and this 
in its turn was modified in different ways ; its 
author himself conceived another theory, founded 
on Maxwell s principles. But the remarkable 
thing is, that all the scientists who followed 
Helmholtz obtain the same equations, although 
their starting-points were to all appearance widely 
separated. I venture to say that these theories 
are all simultaneously truje; not merely because 
they express a true relation that between absorp 
tion and abnormal dispersion. In the premisses 
of these theories the part that is true is the part 
common to all: it is the affirmation of this or 
that relation between certain things, which some 
call by one name and some by another. 

The kinetic theory of gases has given rise to 
many objections, to which it would be difficult 
to find an answer were it claimed that the theory 
is absolutely true. But all these objections do 
not alter the fact that it has been useful, 
particularly in revealing to us one true relation 
which would otherwise have remained profoundly 


hidden the relation between gaseous and osmotic 
pressures. In this sense, then, it may be said to 
be true. 

When a physicist finds a contradiction between 
two theories which are equally dear to him, he 
sometimes says: " Let us not be troubled, but let 
us hold fast to the two ends of the chain, lest 
we lose the intermediate links." This argument 
of the embarrassed theologian would be ridiculous 
if we were to attribute to physical theories the 
interpretation given them by the man of the 
world. In case of contradiction one of them at 
least should be considered false. But this is no 
longer the case if we only seek in them what 
should be sought. It is quite possible that they 
both express true relations, and that the contra 
dictions only exist in the images we have formed 
to ourselves of reality. To those who feel that 
we are going too far in our limitations of the 
domain accessible to the scientist, I reply: These 
questions which we forbid you to investigate, 
and which you so regret, are not only insoluble, 
they are illusory and devoid of meaning. 

Such a philosopher claims that all physics can be 
explained by the mutual impact of atoms. If he 
simply means that the same relations obtain 
between physical phenomena as between ~the 
mutual impact of a large number of billiard 
balls well and good! this is verifiable, and 
perhaps is true. But he means something more, 
and we think we understand him, because we 


think we know what an impact is. Why? Simply 
because we have often watched a game of billiards. 
Are we to understand that God experiences the 
same sensations in the contemplation of His 
work that we do in watching a game of billiards ? 
If it is not our intention to give his assertion 
this fantastic meaning, and if we do not wish 
to give it the more restricted meaning I have 
already mentioned, which is the sound meaning, 
then it has no meaning at all. Hypotheses of 
this kind have therefore only a metaphorical sense. 
The scientist should no more banish them than a 
poet banishes metaphor; but he ought to know 
what they are worth. They may be useful to 
give satisfaction to the mind, and they will do 
no harm as long as they are only indifferent 

These considerations explain to us why certain 
theories, that were thought to be abandoned and 
definitively condemned by experiment, are suddenly 
revived from their ashes and begin a new life. 
It is because they expressed true relations, and 
had not ceased to do so when for some reason or 
other we felt it necessary to enunciate the same 
relations in another language. Their life had been 
latent, as it were. 

Barely fifteen years ago, was there anything 
more ridiculous, more quaintly old-fashioned, than 
the fluids of Coulomb ? And yet, here they are 
re-appearing under the name of electrons. In what 
do these permanently electrified molecules differ 


from the electric molecules of Coulomb ? It is 
true that in the electrons the electricity is sup 
ported by a little, a very little matter ; in other 
words, they have mass. Yet Coulomb did not 
deny mass to his fluids, or if he did, it was with 
reluctance. It would be rash to affirm that the 
belief in electrons will not also undergo an eclipse, 
but it was none the less curious to note this un 
expected renaissance. 

But the most striking example is Carnot s 
principle. Carnot established it, starting from 
false hypotheses. When it was found that heat 
was indestructible, and may be converted into 
work, his ideas were completely abandoned ; 
later, Clausius returned to them, and to him is 
due their definitive triumph. In its primitive 
form, Carnot s theory expressed in addition to 
true relations, other inexact relations, the debris 
of old ideas ; but the presence of the latter did 
not alter the reality of the others. Clausius had 
only to separate them, just as one lops off dead 

The result was the second fundamental law of 
thermodynamics. The relations were always the 
same, although they did not hold, at least to all 
appearance, between the same objects. This was 
sufficient for the principle to retain its value. 
Nor have the reasonings of Carnot perished on 
this account ; they were applied to an imperfect 
conception of matter, but their form i.e., the 
essential part of them, remained correct. What 


I have just said throws some light at the same 
time on the role of general principles, such as 
those of the principle of least action or of the 
conservation of energy. These principles are of 
very great value. They were obtained in the 
search for what there was in common in the 
enunciation of numerous physical laws ; they 
thus represent the quintessence of innumerable 
observations. However, from their very generality 
results a consequence to which I have called 
attention in Chapter VIII. namely, that they are 
no longer capable of verification. As we cannot 
give a general definition of energy, the principle 
of the conservation of energy simply signifies that 
there is a something which remains constant. 
Whatever fresh notions of the world may be 
given us by future experiments, we are certain 
beforehand that there is something which remains 
constant, and which may be called energy. Does 
this mean that the principle has no meaning and 
vanishes into a tautology ? Not at all. It means 
that the different things to which we give the 
name of energy are connected by a true relation 
ship ; it affirms between them a real relation. 
But then, if this principle has a meaning, it may 
be false ; it may be that we have no right to 
extend indefinitely its applications, and yet it is 
certain beforehand to be verified in the strict 
sense of the word. How, then, shall we know 
when it has been extended as far as is legitimate ? 
Simply when it ceases to be useful to us i.e., 


when we can no longer use it to predict correctly 
new phenomena. We shall be certain in such a 
case that the relation affirmed is no longer real, 
for otherwise it would be fruitful ; experiment 
without directly contradicting a new extension of 
the principle will nevertheless have condemned it. 

Physics and Mechanism. Most theorists have a 
constant predilection for explanations borrowed 
from physics, mechanics, or dynamics. Some 
\vould be satisfied if they could account for all 
phenomena by the motion of molecules attracting 
one another according to certain laws. Others 
are more exact : they would suppress attractions 
acting at a distance ; their molecules would follow 
rectilinear paths, from which they would only be 
deviated by impacts. Others again, such as Hertz, 
suppress the forces as well, but suppose their 
molecules subjected to geometrical connections 
analogous, for instance, to those of articulated 
systems; thus, they wish to reduce dynamics to a 
kind of kinematics. In a word, they all wish to 
bend nature into a certain form, and unless they 
can do this they cannot be satisfied. Is Nature 
flexible enough for this ? 

We shall examine this question in Chapter XII., 
apropos of Maxwell s theory. Every time that the 
principles of least action and energy are satisfied, 
we shall see that not only is there always a 
mechanical explanation possible, but that there 
is an unlimited number of such explanations. By 
means of a well-known theorem due to Konigs, 


it may be shown that we can explain everything 
in an unlimited number of ways, by connections 
after the manner of Hertz, or, again, by central 
forces. No doubt it may be just as easily de 
monstrated that everything may be explained by 
simple impacts. For this, let us bear in mind 
that it is not enough to be content with the 
ordinary matter of which we are aware by means 
of our senses, and the movements of which we 
observe directly. We may conceive of ordinary 
matter as either composed of atoms, whose internal 
movements escape us, our senses being able to 
estimate only the displacement of the whole ; or 
we may imagine one of those subtle fluids, which 
under the name of ether or other names, have 
from all time played so important a role in 
physical theories. Often we go further, and regard 
the ether as the only primitive, or even as the 
only true matter. The more moderate consider 
ordinary matter to be condensed ether, and 
there is nothing startling in this conception; but 
others only reduce its importance still further, 
and see in matter nothing more than the geo 
metrical locus of singularities in the ether. Lord 
Kelvin, for instance, holds what we call matter 
to be only the locus of those points at which the 
ether is animated by vortex motions. Riemann 
believes it to be locus of those points at which 
ether is constantly destroyed ; to Wiechert or 
Larmor, it is the locus of the points at which 
the ether has undergone a kind of torsion of a 


very particular kind. Taking any one of these 
points of view, I ask by what right do we apply 
to the ether the mechanical properties observed 
in ordinary matter, which is but false matter ? 
The ancient fluids, caloric, electricity, etc., were 
abandoned when it was seen that heat is not 
indestructible. But they were also laid aside 
for another reason, In materialising them, their 
individuality was, so to speak, emphasised gaps 
were opened between them ; and these gaps had 
to be filled in when the sentiment of the unity of 
Nature became stronger, and when the intimate 
relations which connect all the parts were per 
ceived. In multiplying the fluids, not only did 
the ancient physicists create unnecessary entities, 
but they destroyed real ties. It is not enough for 
a theory not to affirm false relations ; it must not 
conceal true relations. 

Does our ether actually exist ? We know the 
origin of our belief in the ether. If light takes 
several years to reach us from a distant star, it 
is no longer on the star, nor is it on the earth. 
It must be somewhere, and supported, so to speak, 
by some material agency. 

The same idea may be expressed in a more 
mathematical and more abstract form. What we 
note are the changes undergone by the material 
molecules. We see, for instance, that the photo 
graphic plate experiences the consequences of a 
phenomenon of which the incandescent mass of 
a star was the scene several vears before. Now, 


in ordinary mechanics, the state of the system 
under consideration depends only on its state at 
the moment immediately preceding; the system 
therefore satisfies certain differential equations. 
On the other hand, if we did not believe in the 
ether, the state of the material universe would 
depend not only on the state immediately pre 
ceding, but also on much older states ; the system 
would satisfy equations of finite differences. The 
ether was invented to escape this breaking down 
of the laws of general mechanics. 

Still, this would only compel us to fill the 
interplanetary space with ether, but not to 
make it penetrate into the midst of the material 
media. Fizeau s experiment goes further. By 
the interference of rays which have passed 
through the air or water in motion, it seems to 
show us two different media penetrating each 
other, and yet being displaced with respect to 
each other. The ether is all but in our grasp. 
Experiments can be conceived in which we come 
closer still to it. Assume that Newton s principle 
of the equality of action and re-action is not true 
if applied to matter alone, and that this can be 
proved. The geometrical sum of all the forces 
applied to all the molecules would no longer be 
zero. If we did not wish to change the whole of the 
science of mechanics, we should have to introduce 
the ether, in order that the action which matter 
apparently undergoes should be counterbalanced 
by the re-action of matter on something. 


Or again, suppose we discover that optical and 
electrical phenomena are influenced by the motion 
of the earth. It would follow that those pheno 
mena might reveal to us not only the relative 
motion of material bodies, but also what would 
seem to be their absolute motion. Again, it would 
be necessary to have an ether in order that these 
so-called absolute movements should not be their 
displacements with respect to empty space, but 
with respect to something concrete. 

Will this ever be accomplished ? I do not 
think so, and I shall explain why; and yet, it is 
not absurd, for others have entertained this view. 
For instance, if the theory of Lorentz, of which I 
shall speak in more detail in Chapter XIII., were 
true, Newton s principle would not apply to matter 
alone, and the difference would not be very far 
from being within reach of experiment. On the 
other hand, many experiments have been made 
on the influence of the motion of the earth. The 
results have always been negative. But if these 
experiments have been undertaken, it is because 
we have not been certain beforehand; and indeed, 
according to current theories, the compensation 
would be only approximate, and we might expect 
to find accurate methods giving positive results. 
I think that such a hope is illusory ; it was none 
the less interesting to show that a success of this 
kind would, in a certain sense, open to us a new 

And now allow me to make a digression ; I 


must explain why I do not believe, in spite of 
Lorentz, that more exact observations will ever 
make evident anything else but the relative dis 
placements of material bodies. Experiments have 
been made that should have disclosed the terms 
of the first order; the results were nugatory. 
Could that have been by chance ? No one has 
admitted this ; a general explanation was sought, 
and Lorentz found it. He showed that the terms 
of the first order should cancel each other, but 
not the terms of the second order. Then more 
exact experiments were made, which were also 
negative ; neither could this be the result of 
chance. An explanation was necessary, and was 
forthcoming ; they always are ; hypotheses are 
what we lack the least. But this is not enough. 
Who is there who does not think that this leaves 
to chance far too important a role ? Would it 
not also be a chance that this singular concurrence 
should cause a certain circumstance to destroy the 
terms of the first order, and that a totally different 
but very opportune circumstance should cause 
those of the second order to vanish? No; the 
same explanation must be found for the two 
cases, and everything tends to show that this 
explanation would serve equally well for the 
terms of the higher order, and that the mutual 
destruction of these terms will be rigorous and 

The Present State of Physics. Two opposite 
tendencies may be distinguished in the history 


of the development of physics. On the one hand, 
new relations are continually being discovered 
between objects which seemed destined to remain 
for ever unconnected ; scattered facts cease to be 
strangers to each other and tend to be marshalled 
into an imposing synthesis. The march of science 
is towards unity and simplicity. 

On the other hand, new phenomena are con 
tinually being revealed ; it will be long before 
they can be assigned their place sometimes it 
may happen that to find them a place a corner of 
the edifice must be demolished. In the same way, 
we are continually perceiving details ever more 
varied in the phenomena we know, where our 
crude senses used to be unable to detect any lack 
of unity. What we thought to be simple becomes 
complex, and the march of science seems to be 
towards diversity and complication. 

Here, then, are two opposing tendencies, each of 
which seems to triumph in turn. Which will win ? 
If the first wins, science is possible ; but nothing 
proves this a priori, and it may be that after 
unsuccessful efforts to bend Nature to our ideal of 
unity in spite of herself, we shall be submerged by 
the ever-rising flood of our new riches and com 
pelled to renounce all idea of classification to 
abandon our ideal, and to reduce science to the 
mere recording of innumerable recipes. 

In fact, we can give this question no answer. 
All that we can do is to observe the science of 
to-day, and compare it with that of yesterday. 


No doubt after this examination we shall be in a 
position to offer a few conjectures. 

Half-a-century ago hopes ran high indeed. The 
unity of force had just been revealed to us by the 
discovery of the conservation of energy and of its 
transformation. This discovery also showed that 
the phenomena of heat could be explained by 
molecular movements. Although the nature of 
these movements was not exactly known, no one 
doubted but that they would be ascertained before 
long. As for light, the work seemed entirely com 
pleted. So far as electricity was concerned, there 
was not so great an advance. Electricity had just 
annexed magnetism. This was a considerable and 
a definitive step towards unity. But how was 
electricity in its turn to be brought into the 
general unity, and how was it to be included in 
the general universal mechanism ? No one had 
the slightest idea. As to the possibility of the in 
clusion, all were agreed ; they had faith. Finally, 
as far as the molecular properties of material 
bodies are concerned, the inclusion seemed easier, 
but the details were very hazy. In a word, hopes 
were vast and strong, but vague. 

To-day, what do we see ? In the first place, a 
step in advance immense progress. The relations 
between light and electricity are now known ; the 
three domains of light, electricity, and magnetism, 
formerly separated, are now one ; and this annexa 
tion seems definitive. 

Nevertheless the conquest has caused us some 


sacrifices. Optical phenomena become particular 
cases in electric phenomena; as long as the former 
remained isolated, it was easy to explain them by 
movements which were thought to be known in 
all their details. That was easy enough ; but any 
explanation to be accepted must now cover the 
whole domain of electricity. This cannot be done 
without difficulty. 

The most satisfactory theory is that of Lorentz; 
it is unquestionably the theory that best explains 
the known facts, the one that throws into relief 
the greatest number of known relations, the one in 
which we find most traces of definitive construc 
tion. That it still possesses a serious fault I 
have shown above. It is in contradiction with 
Newton s law that action and re-action are equal 
and opposite or rather, this principle according 
to Lorentz cannot be applicable to matter alone ; 
if it be true, it must take into account the action 
of the ether on matter, and the re-action of the 
matter on the ether. Now, in the new order, it is 
very likely that things do not happen in this way. 

However this may be, it is due to Lorentz that 
the results of Fizeau on the optics of moving 
bodies, the laws of normal and abnormal dis 
persion and of absorption are connected with 
each other and with the other properties of the 
ether, by bonds which no doubt will not be 
readily severed. Look at the ease with which the 
new Zeeman phenomenon found its place, and 
even aided the classification of Faraday s magnetic 


rotation, which had defied all Maxwell s efforts. 
This facility proves that Lorentz s theory is not a 
mere artificial combination which must eventually 
find its solvent. It will probably have to be 
modified, but not destroyed. 

The only object of Lorentz was to include in a 
single whole all the optics and electro-dynamics 
of moving bodies ; he did not claim to give a 
mechanical explanation. Larmor goes further ; 
keeping the essential part of Lorentz s theory, he 
grafts upon it, so to speak, MacCullagh s ideas on 
the direction of the movement of the ether. 
MacCullagh held that the velocity of the ether 
is the same in magnitude and direction as the 
magnetic force. Ingenious as is this attempt, the 
fault in Lorentz s theory remains, and is even 
aggravated. According to Lorentz, we do not 
know what the movements of the ether are; and 
because we do not know this, we may suppose 
them to be movements compensating those of 
matter, and re-affirming that action and re-action 
are equal and opposite. According to Larmor 
we know the movements of the ether, and we 
can prove that the compensation does not take 

If Larmor has failed, as in my opinion he has, 
does it necessarily follow that a mechanical ex 
planation is impossible ? Far from it. I said 
above that as long as a phenomenon obeys the 
two principles of energy and least action, so long 
it allows of an unlimited number of mechanical 


explanations. And so with the phenomena of 
optics and electricity. 

But this is not enough. For a mechanical 
explanation to be good it must be simple ; to 
choose it from among all the explanations that are 
possible there must be other reasons than the 
necessity of making a choice. Well, we have no 
theory as yet which will satisfy this condition and 
consequently be of any use. Are we then to 
complain ? That would be to forget the end we 
seek, which is not the mechanism ; the true and 
only aim is unity. 

We ought therefore to set some limits to 
our ambition. Let us not seek to formulate a 
mechanical explanation ; let us be content to 
show that we can always find one if we wish. In 
this we have succeeded. The principle of the 
conservation of energy has always been confirmed, 
and now it has a fellow in the principle of least 
action, stated in the form appropriate to physics. 
This has also been verified, at least as far as 
concerns the reversible phenomena which obey 
Lagrange s equations in other words, which obey 
the most general laws of physics. The irreversible 
phenomena are much more difficult to bring into 
line ; but they, too, are being co-ordinated and 
tend to come into the unity. The light which 
illuminates them comes from Carnot s principle. 
For a long time thermo-dynamics was confined to 
the study of the dilatations of bodies and of their 
change of state. For some time past it has been 



growing bolder, and has considerably extended its 
domain. We owe to it the theories of the voltaic 
cell and of their thermo-electric phenomena; there 
is not a corner in physics which it has not ex 
plored, and it has even attacked chemistry itself. 
The same laws hold good ; everywhere, disguised 
in some form or other, we find Carnot s principle ; 
everywhere also appears that eminently abstract 
concept of entropy which is as universal as the 
concept of energy, and like it, seems to conceal a 
reality. It seemed that radiant heat must escape, 
but recently that, too, has been brought under the 
same laws. 

In this way fresh analogies are revealed which 
may be often pursued in detail ; electric resistance 
resembles the viscosity of fluids ; hysteresis would 
rather be like the friction of solids. In all cases 
friction appears to be the type most imitated by 
the most diverse irreversible phenomena, and this 
relationship is real and profound. 

A strictly mechanical explanation of these 
phenomena has also been sought, but, owing to 
their nature, it is hardly likely that it will be 
found. To find it, it has been necessary to 
suppose that the irreversibility is but apparent, that 
the elementary phenomena are reversible and obey 
the known laws of dynamics. But the elements 
are extremely numerous, and become blended 
more and more, so that to our crude sight all 
appears to tend towards uniformity i.e., all seems 
to progress in the same direction, and that without 


hope of return. The apparent irreversibility is 
therefore but an effect of the law of great numbers. 
Only a being of infinitely subtle senses, such as 
Maxwell s demon, could unravel this tangled skein 
and turn back the course of the universe. 

This conception, which is connected with the 
kinetic theory of gases, has cost great effort and 
has not, on the whole, been fruitful ; it may 
become so. This is not the place to examine if it 
leads to contradictions, and if it is in conformity 
with the true nature of things. 

Let us notice, however, the original ideas of 
M. Gouy on the Brownian movement. According 
to this scientist, this singular movement does not 
obey Carnot s principle. The particles which it sets 
moving would be smaller than the meshes of that 
tightly drawn net; they would thus be ready to 
separate them, and thereby to set back the course 
of the universe. One can almost see Maxwell s 
demon at work. 1 

To resume, phenomena long known are gradually 
being better classified, but new phenomena come 
to claim their place, and most of them, like the 
Zeeman effect, find it at once. Then we have the 
cathode rays, the X-rays, uranium and radium 
rays; in fact, a whole world of which none had 
suspected the existence. How many unexpected 

1 Clerk-Maxwell imagined some supernatural agency at work, 
sorting molecules in a gas of uniform temperature into (a] those 
possessing kinetic energy above the average, (/;) those possessing 
kinetic energy below the average. [Tk.] 


guests to find a place for ! No one can yet predict 
the place they will occupy, but I do not believe 
they will destroy the general unity : I think that 
they will rather complete it. On the one hand, 
indeed, the new radiations seem to be connected 
with the phenomena of luminosity; not only do 
they excite fluorescence, but they sometimes come 
into existence under the same conditions as that 
property; neither are they unrelated to the cause 
which produces the electric spark under the action 
of ultra-violet light. Finally, and most important 
of all, it is believed that in all these phenomena 
there exist ions, animated, it is true, with velocities 
far greater than those of electrolytes. All this is 
very vague, but it will all become clearer. 

Phosphorescence and the action of light on the 
spark were regions rather isolated, and consequently 
somewhat neglected by investigators. It is to be 
hoped that a new path will now be made which 
will facilitate their communications with the 
rest of science. Not only do we discover new 
phenomena, but those we think we know are 
revealed in unlooked-for aspects. In the free ether 
the laws preserve their majestic simplicity, but 
matter properly so called seems more and more 
complex ; all we can say of it is but approximate, 
and our formulae are constantly requiring new 

But the ranks are unbroken, the relations that 
we have discovered between objects we thought 
simple still hold good between the same objects 


when their complexity is recognised, and that 
alone is the important thing. Our equations 
become, it is true, more and more complicated, so 
as to embrace more closely the complexity of 
nature ; but nothing is changed in the relations 
which enable these equations to be derived from 
each other. In a word, the form of these equations 
persists. Take for instance the laws of reflection. 
Fresnel established them by a simple and attractive 
theory which experiment seemed to confirm. Sub 
sequently, more accurate researches have shown 
that this verification was but approximate; traces 
of elliptic polarisation were detected everywhere. 
But it is owing to the first approximation that the 
cause of these anomalies was found in the existence 
of a transition layer, and all the essentials of 
Fresnel s theory have remained. We cannot help 
reflecting that all these relations would never have 
been noted if there had been doubt in the first 
place as to the complexity of the objects they 
connect. Long ago it was said: If Tycho had had 
instruments ten times as precise, we would never 
have had a Kepler, or a Newton, or Astronomy. 
It is a misfortune for a science to be born too late, 
when the means of observation have become too 
perfect. That is what is happening at this moment 
with respect to physical chemistry; the founders 
are hampered in their general grasp by third and 
fourth decimal places; happily they are men of 
robust faith. As we get to know the properties 
of matter better we see that continuity reigns. 


From the work of Andrews and Van der Waals, 
we see how the transition from the liquid to the 
gaseous state is made, and that it is not abrupt. 
Similarly, there is no gap between the liquid and 
solid states, and in the proceedings of a recent 
Congress we see memoirs on the rigidity of liquids 
side by side with papers on the flow of solids. 

With this tendency there is no doubt a loss of 
simplicity. Such and such an effect was represented 
by straight lines; it is now r necessary to connect 
these lines by more or less complicated curves. 
On the other hand, unity is gained. Separate 
categories quieted but did not satisfy the mind. 

Finally, a new domain, that of chemistry, has 
been invaded by the method of physics, and we see 
the birth of physical chemistry. It is still quite 
young, but already it has enabled us to connect 
such phenomena as electrolysis, osmosis, and the 
movements of ions. 

From this cursory exposition what can we con 
clude? Taking all things into account, we have 
approached the realisation of unity. This has not 
been done as quickly as was hoped fifty years ago, 
and the path predicted has not always been 
followed; but, on the whole, much ground has 
been gained. 



No doubt the reader will be astonished to find 
reflections on the calculus of probabilities in such 
a volume as this. What has that calculus to do 
with physical science ? The questions I shall raise 
without, however, giving them a solution are 
naturally raised by the philosopher who is examin 
ing the problems of physics. So far is this the case, 
that in the two preceding chapters I have several 
times used the words "probability" and "chance." 
" Predicted facts," as I said above, " can only be 
probable." However solidly founded a predic 
tion may appear to be, we are never absolutely 
certain that experiment will not prove it false; but 
the probability is often so great that practically 
it may be accepted. And a little farther on I 
added: "See what a part the belief in simplicity 
plays in our generalisations. We have verified a 
simple law in a large number of particular cases, 
and we refuse to admit that this so-often-repeated 
coincidence is a mere effect of chance." Thus, in a 
multitude of circumstances the physicist is often 
in the same position as the gambler who reckons 
up his chances. Every time that he reasons by 


induction, he more or less consciously requires the 
calculus of probabilities, and that is why I am 
obliged to open this chapter parenthetically, and to 
interrupt our discussion of method in the physical 
sciences in order to examine a little closer what this 
calculus is worth, and what dependence we may 
place upon it. The very name of the calculus of 
probabilities is a paradox. Probability as opposed 
to certainty is what one does not know, and how 
can we calculate the unknown ? Yet many eminent 
scientists have devoted themselves to this calculus, 
and it cannot be denied that science has drawn there 
from no small advantage. How can we explain 
this apparent contradiction ? Has probability been 
defined ? Can it even be defined ? And if it can 
not, how can we venture to reason upon it ? The 
definition, it will be said, is very simple. The 
probability of an event is the ratio of the number 
of cases favourable to the event to the total number 
of possible cases. A simple example will show how 
incomplete this definition is: I throw two dice. 
What is the probability that one of the two 
at least turns up a 6 ? Each can turn up in six 
different ways; the number of possible cases is 
6 x 6 = 36. The number of favourable cases is n ; 

the probability is - 1 - That is the correct solution. 

But why cannot we just as well proceed as follows? 
-The points which turn up on the two dice form 

= 2 1 different combinations. Among these 
combinations, six are favourable ; the probability 


is Now why is the first method of calculating 

the number of possible cases more legitimate than 
the second ? In any case it is not the definition 
that tells us. We are therefore bound to complete 
the definition by saying, " ... to the total number 
of possible cases, provided the cases are equally 
probable." So we are compelled to define the 
probable by the probable. How can we know 
that two possible cases are equally probable ? 
Will it be by a convention ? If we insert at the 
beginning of every problem an explicit convention, 
well and good ! We then have nothing to do but to 
apply the rules of arithmetic and algebra, and we 
complete our calculation, when our result cannot 
be called in question. But if we wish to make the 
slightest application of this result, we must prove 
that our convention is legitimate, and we shall find 
ourselves in the presence of the very difficulty we 
thought we had avoided. It may be said that 
common-sense is enough to show us the convention 
that should be adopted. Alas ! M. Bertrand has 
amused himself by discussing the following simple 
problem : " What is the probability that a chord 
of a circle may be greater than the side of the 
inscribed equilateral triangle?" The illustrious 
geometer successively adopted two conventions 
which seemed to be equally imperative in the eyes 
of common-sense, and with one convention he finds 
J, and with the other J-. The conclusion which 
seems to follow- from this is that the calculus of 
probabilities is a useless science, that the obscure 


instinct which we call common-sense, and to which 
we appeal for the legitimisation of our conventions, 
must be distrusted. But to this conclusion we can 
no longer subscribe. We cannot do without that 
obscure instinct. Without it, science would be 
impossible, and without it we could neither discover 
nor apply a law. Have we any right, for instance, 
to enunciate Newton s law ? No doubt numerous 
observations are in agreement with it, but is not 
that a simple fact of chance ? and how do we know, 
besides, that this law which has been true for so 
many generations will not be untrue in the next ? 
To this objection the only answer you can give is: 
It is very improbable. But grant the law. By 
means of it I can calculate the position of Jupiter 
in a year from now. Yet have I any right to say 
this? Who can tell if a gigantic mass of enormous 
velocity is not going to pass near the solar system 
and produce unforeseen perturbations ? Here 
again the only answer is : It is very improbable. 
From this point of view all the sciences would only 
be unconscious applications of the calculus of prob 
abilities. And if this calculus be condemned, then 
the whole of the sciences must also be condemned. 
I shall not dwell at length on scientific problems 
in which the intervention of the calculus of prob 
abilities is more evident. In the forefront of these 
is the problem of interpolation, in which, knowing 
a certain number of values of a function, we try 
to discover the intermediary values. I may also 
mention the celebrated theory of errors of observa- 


tion, to which I shall return later; the kinetic 
theory of gases, a well-known hypothesis wherein 
each gaseous molecule is supposed to describe an 
extremely complicated path, but in which, through 
the effect of great numbers, the mean phenomena 
\vhich are all we observe obey the simple laws of 
Mariotte and Gay-Lussac. All these theories are 
based upon the laws of great numbers, and the 
calculus of probabilities would evidently involve 
them in its ruin. It is true that they have only a 
particular interest, and that, save as far as inter 
polation is concerned, they are sacrifices to which 
we might readily be resigned. But I have said 
above, it would not be these partial sacrifices that 
would be in question ; it would be the legitimacy 
of the whole of science that would be challenged. 
I quite see that it might be said: We do not know, 
and yet we must act. As for action, we have not 
time to devote ourselves to an inquiry that will 
suffice to dispel our ignorance. Besides, such an 
inquiry would demand unlimited time. We must 
therefore make up our minds without knowing. 
This must be often done whatever may happen, 
and we must follow the rules although we may 
have but little confidence in them. What I know 
is, not that such a thing is true, but that the best 
course for me is to act as if it were true. The 
calculus of probabilities, and therefore science 
itself, would be no longer of any practical value. 
Unfortunately the difficulty does not thus dis 
appear. A gambler wants to try a coup, and he 


asks my advice. If I give it him, I use the 
calculus of probabilities; but I shall not guarantee 
success. That is what I shall call subjective prob 
ability. In this case we might be content with the 
explanation of which I have just given a sketch. 
But assume that an observer is present at the play, 
that he knows of the coup, and that play goes 
on for a long time, and that he makes a summary 
of his notes. He will find that events have 
taken place in conformity with the laws of the 
calculus of probabilities. That is what I shall call 
objective probability, and it is this phenomenon 
which has to be explained. There are numerous 
Insurance Societies which apply the rules of the 
calculus of probabilities, and they distribute to 
their shareholders dividends, the objective reality 
of which cannot be contested. In order to explain 
them, we must do more than invoke our ignorance 
and the necessity of action. Thus, absolute scepti 
cism is not admissible. We may distrust, but we 
cannot condemn en bloc. Discussion is necessary. 
I. Classification of the Problems of Probability. In 
order to classify the problems which are presented 
to us with reference to probabilities, we must look at 
them from different points of view, and first of all, 
from that of generality. I said above that prob 
ability is the ratio of the number of favourable to 
the number of possible cases. What for want of a 
better term I call generality will increase with the 
number of possible cases. This number may be 
finite, as, for instance, if we take a throw of the 


dice in which the number of possible cases is 36. 
That is the first degree of generality. But if we 
ask, for instance, what is the probability that a 
point within a circle is within the inscribed square, 
there are as many possible cases as there are points 
in the circle that is to say, an infinite number. 
This is the second degree of generality. Generality 
can be pushed further still. We may ask the prob 
ability that a function will satisfy a given condi 
tion. There are then as many possible cases as one 
can imagine different functions. This is the third 
degree of generality, which we reach, for instance, 
w r hen we try to find the most probable law after a 
finite number of observations. Yet we may place 
ourselves at a quite different point of view. If we 
were not ignorant there would be no probability, 
there could only be certainty. But our ignorance 
cannot be absolute, for then there would be no 
longer any probability at all. Thus the problems 
of probability may be classed according to the 
greater or less depth of this ignorance. In mathe 
matics we may set ourselves problems in prob 
ability. What is the probability that the fifth 
decimal of a logarithm taken at random from a 
table is a 9. There is no hesitation in answering 
that this probability is i-ioth. Here we possess 
all the data of the problem. We can calculate 
our logarithm without having recourse to the 
table, but we need not give ourselves the trouble. 
This . is the first degree of ignorance. In the 
physical sciences our ignorance is already greater. 


The state of a system at a given moment depends 
on two things its initial state, and the law 
according to which that state varies. If we know 
both this law r and this initial state, we have a 
simple mathematical problem to solve, and we 
fall back upon our first degree of ignorance. 
Then it often happens that we know the law 
and do not know the initial state. It may be 
asked, for instance, what is the present distribu 
tion of the minor planets ? We know that from 
all time they have obeyed the laws of Kepler, 
but we do not know what was their initial dis 
tribution. In the kinetic theory of gases we 
assume that the gaseous molecules follow recti 
linear paths and obey the laws of impact and 
elastic bodies; yet as we know nothing of their 
initial velocities, we know nothing of their present 
velocities. The calculus of probabilities alone 
enables us to predict the mean phenomena which 
will result from a combination of these velocities. 
This is the second degree of ignorance. Finally 
it is possible, that not only the initial conditions 
but the laws themselves are unknown. We then 
reach the third degree of ignorance, and in general 
we can no longer affirm anything at all as to the 
probability of a phenomenon. It often happens 
that instead of trying to discover an event by 
means of a more or less imperfect knowledge of 
the law, the events may be known, and we want 
to find the law ; or that, instead of deducing 
effects from causes, we wish to deduce the causes 


from the effects. Now, these problems are classified 
as probability of causes, and are the most interesting 
of all from their scientific applications. I play at 
ecarte with a gentleman whom I know to be per 
fectly honest. What is the chance that he turns 
up the king ? It is -J-. This is a problem of the 
probability of effects. I play with a gentleman 
whom I do not know. He has dealt ten times, 
and he has turned the king up six times. What 
is the chance that he is a sharper ? This is a 
problem in the probability of causes. It may be 
said that it is the essential problem of the experi 
mental method. I have observed n values of x 
and the corresponding values of y. I have found 
that the ratio of the latter to the former is prac 
tically constant. There is the event ; what is 
the cause ? Is it probable that there is a general 
law according to which y would be proportional 
to x, and that small divergencies are due to errors 
of observation ? This is the type of question that 
we are ever asking, and which we unconsciously 
solve whenever we are engaged in scientific work. 
I am now going to pass in review these different 
categories of problems by discussing in succession 
what I have called subjective and objective prob 

II. Probability in Mathematics. The impossi 
bility of squaring the circle was shown in 1885, but 
before that date all geometers considered this im 
possibility as so " probable" that the Academic des 
Sciences rejected without examination the, alas ! 


too numerous memoirs on this subject that a 
few unhappy madmen sent in every year. Was 
the Academic wrong ? Evidently not, and it 
knew perfectly well that by acting in this 
manner it did not run the least risk of stifling 
a discovery of moment. The Academic could 
not have proved that it was right, but it knew 
quite well that its instinct did not deceive it. 
If you had asked the Academicians, they would 
have answered: "We have compared the prob 
ability that an unknown scientist should have 
found out what has been vainly sought for so 
long, with the probability that there is one mad 
man the more on the earth, and the latter has 
appeared to us the greater." These are very 
good reasons, but there is nothing mathematical 
about them; they are purely psychological. If 
you had pressed them further, they would have 
added: " Why do you expect a particular value of 
a transcendental function to be an algebraical 
number; if ^ be the root of an algebraical equa 
tion, why do you expect this root to be a period of 
the function sin 2x, and why is it not the same 
with the other roots of the same equation?" To 
sum up, they would have invoked the principle of 
sufficient reason in its vaguest form. Yet what 
information could they draw from it ? At most a 
rule of conduct for the employment of their time, 
which would be more usefully spent at their 
ordinary work than in reading a lucubration 
that inspired in them a legitimate distrust. But 


what I called above objective probability has 
nothing in common with this first problem. It is 
otherwise with the second. Let us consider the 
first 10,000 logarithms that we find in a table. 
Among these 10,000 logarithms I take one at 
random. What is the probability that its third 
decimal is an even number ? You will say with 
out any hesitation that the probability is J, and in 
fact if you pick out in a table the third decimals 
in these 10,000 numbers you will find nearly as 
many even digits as odd. Or, if you prefer it, let 
us write 10,000 numbers corresponding to our 
10,000 logarithms, writing down for each of these 
numbers 4- 1 if the third decimal of the correspond 
ing logarithm is even, and - i if odd; and then 
let us take the mean of these 10,000 numbers. I 
do not hesitate to say that the mean of these 
10,000 units is probably zero, and if I were to 
calculate it practically, I would verify that it is 
extremely small. But this verification is needless. 
I might have rigorously proved that this mean is 
smaller than 0.003. To prove this result I should 
have had to make a rather long calculation for 
which there is no room here, and for which I 
may refer the reader to an article that I pub 
lished in the Revue generate des Sciences, April 
I5th, 1899. The only point to which I wish to 
draw attention is the following. In this calcula 
tion I had occasion to rest my case on only two 
facts namely, that the first and second derivatives 
of the logarithm remain, in the interval considered, 



between certain limits. Hence our first conclusion 
is that the property is not only true of the 
logarithm but of any continuous function what 
ever, since the derivatives of every continuous 
function are limited. If I was certain beforehand 
of the result, it is because I have often observed 
analogous facts for other continuous functions; and 
next, it is because I went through in my mind in 
a more or less unconscious and imperfect manner 
the reasoning which led me to the preceding in 
equalities, just as a skilled calculator before finish 
ing his multiplication takes into account what it 
ought to come to approximately. And besides, 
since what I call my intuition was only an incom 
plete summary of a piece of true reasoning, it is 
clear that observation has confirmed my predic 
tions, and that the objective and subjective proba 
bilities are in agreement. As a third example I shall 
choose the following: The number u is taken at 
random and n is a given very large integer. What 
is the mean value of sin mi ? This problem has 
no meaning by itself. To give it one, a convention 
is required namely, we agree that the probability 
for the number u to lie between a and a + da is 
<j>(a)da; that it is therefore proportional to the 
infinitely small interval da, and is equal to this 
multiplied by a function </>(/i), only depending 
on a. As for this function I choose it arbitrarily, 
but I must assume it to be continuous. The value 
of sin nu remaining the same when u increases by 
2 TT, I may without loss of generality assume that 


u lies between o and 2 TT, and I shall thus be 
led to suppose that <f>(a) is a periodic function 
whose period is 2 TT. The mean value that we 
seek is readily expressed by a simple integral, 
and it is easy to show that this integral is smaller 

than ^, M K being the maximum value of the 

Kth derivative of (f>(u). We see then that if the 
Kth derivative is finite, our mean value will 
tend towards zero when n increases indefinitely, 

and that more rapidly than - . The mean 
r j w >-i 

value of sin nu when n is very large is therefore 
zero. To define this value I required a conven 
tion, but the result remains the same whatever 
that convention may be. I have imposed upon 
myself but slight restrictions when I assumed that 
the function (j>(a) is continuous and periodic, and 
these hypotheses are so natural that we may ask 
ourselves how they can be escaped. Examination 
of the three preceding examples, so different in all 
respects, has already given us a glimpse on the 
one hand of the role of what philosophers call the 
principle of sufficient reason, and on the other hand 
of the importance of the fact that certain pro 
perties are common to all continuous functions. 
The study of probability in the physical sciences 
will lead us to the same result. 

III. Probability in the Physical Sciences. We 
now come to the problems which are connected 
with what I have called the second degree of 


ignorance namely, those in which we know the 
law but do not know the initial state of the 
system. I could multiply examples, but I shall 
take only one. What is the probable present 
distribution of the minor planets on the zodiac ? 
We know they obey the laws of Kepler. We may 
even, without changing the nature of the problem, 
suppose that their orbits are circular and situated 
in the same plane, a plane which we are given. 
On the other hand, we know absolutely nothing 
about their initial distribution. However, we do 
not hesitate to affirm that this distribution is now 
nearly uniform. Why? Let b be the longitude 
of a minor planet in the initial epoch that is to 
say, the epoch zero. Let a be its mean motion. 
Its longitude at the present time i.e., at the time 
/ will be at + b. To say that the present distribu 
tion is uniform is to say that the mean value of 
the sines and cosines of multiples of at + b is zero. 
Why do we assert this ? Let us represent our 
minor planet by a point in a plane namely, the 
point whose co-ordinates are a and b. All these 
representative points will be contained in a certain 
region of the plane, but as they are very numerous 
this region will appear dotted with points. We 
know nothing else about the distribution of the 
points. Now what do we do when we apply the 
calculus of probabilities to such a question as 
this ? What is the probability that one or more 
representative points may be found in a certain 
portion of the plane ? In our ignorance we are 


compelled to make an arbitrary hypothesis. To 
explain the nature of this hypothesis I may be 
allowed to use, instead of a mathematical formula, 
a crude but concrete image. Let us suppose 
that over the surface of our plane has been 
spread imaginary matter, the density of which is 
variable, but varies continuously. We shall then 
agree to say that the probable number of repre 
sentative points to be found on a certain portion 
of the plane is proportional to the quantity of 
this imaginary matter which is found there. If 
there are, then, two regions of the plane of the 
same extent, the probabilities that a representative 
point of one of our minor planets is in one or 
other of these regions will be as the mean densities 
of the imaginary matter in one or other of the 
regions. Here then are two distributions, one 
real, in which the representative points are very 
numerous, very close together, but discrete like the 
molecules of matter in the atomic hypothesis; the 
other remote from reality, in which our representa 
tive points are replaced by imaginary continuous 
matter. We know that the latter cannot be real, 
but we are forced to adopt it through our ignorance. 
If, again, we had some idea of the real distribution 
of the representative points, we could arrange it so 
that in a region of some extent the density of this 
imaginary continuous matter may be nearly pro 
portional to the number of representative points, 
or, if it is preferred, to the number of atoms which 
are contained in that region. Even that is im- 


possible, and our ignorance is so great that we are 
forced to choose arbitrarily the function which 
defines the density of our imaginary matter. We 
shall be compelled to adopt a hypothesis from 
which we can hardly get away ; we shall sup 
pose that this function is continuous. That is 
sufficient, as we shall see, to enable us to reach our 

What is at the instant t the probable distribu 
tion of the minor planets or rather, what is the 
mean value of the sine of the longitude at the 
moment t i.e., of sin (at + b)? We made at the 
outset an arbitrary convention, but if we adopt it, 
this probable value is entirely defined. Let us 
decompose the plane into elements of surface. 
Consider the value of sin (at + b) at the centre of 
each of these elements. Multiply this value by the 
surface of the element and by the corresponding 
density of the imaginary matter. Let us then take 
the sum for all the elements of the plane. This 
sum, by definition, will be the probable mean 
value we seek, which will thus be expressed by a 
double integral. It may be thought at first that 
this mean value depends on the choice of the 
function < which defines the density of the imagin 
ary matter, and as this function </> is arbitrary, we 
can, according to the arbitrary choice which we 
make, obtain a certain mean value. But this is 
not the case. A simple calculation shows us that 
our double integral decreases very rapidly as t 
increases. Thus, I cannot tell what hypothesis to 


make as to the probability of this or that initial 
distribution, but when once the hypothesis is 
made the result will be the same, and this gets 
me out of my difficulty. Whatever the function 
</> may be, the mean value tends towards zero 
as t increases, and as the minor planets have 
certainly accomplished a very large number of 
revolutions, I may assert that this mean value is 
very small. I may give to </> any value I choose, 
with one restriction : this function must be con 
tinuous; and, in fact, from the point of view of 
subjective probability, the choice of a discontinuous 
function would have been unreasonable. What 
reason could I have, for instance, for supposing 
that the initial longitude might be exactly o, but 
that it could not lie between o and i ? 

The difficulty reappears if we look at it from the 
point of view of objective probability; if we pass 
from our imaginary distribution in which the sup 
posititious matter was assumed to be continuous, 
to the real distribution in which our representative 
points are formed as discrete atoms. The mean 
value of sin (at + b) will be represented quite 
simply by 

\ sin (at + b), 

n being the number of minor planets. Instead of 
a double integral referring to a continuous 
function, we shall have a sum of discrete terms. 
However, no one will seriously doubt that this 
mean value is practically very small. Our repre- 


sentative points being very close together, our 
discrete sum will in general differ very little from 
an integral. An integral is the limit towards 
which a sum of terms tends when the number of 
these terms is indefinitely increased. If the terms 
are very numerous, the sum will differ very little 
from its limit that is to say, from the integral, 
and what I said of the latter will still be true of 
the sum itself. But there are exceptions. If, for 

instance, for all the minor planets b = - -at, the 
longitude of all the planets at the time t would be 
, and the mean value in question would be 

evidently unity. For this to be the case at the 
time o, the minor planets must have all been 
lying on a kind of spiral of peculiar form, with 
its spires very close together. All will admit that 
such an initial distribution is extremely im 
probable (and even if it were realised, the distribu 
tion would not be uniform at the present time for 
example, on the ist January 1900 ; but it would 
become so a few years later). Why, then, do we 
think this initial distribution improbable ? This 
must be explained, for if we are wrong in rejecting 
as improbable this absurd hypothesis, our inquiry 
breaks down, and we can no longer affirm any 
thing on the subject of the probability of this or 
that present distribution. Once more we shall 
invoke the principle of sufficient reason, to which 
we must always recur. We might admit that at 
the beginning the planets were distributed almost 


in a straight line. We might admit that they 
were irregularly distributed. But it seems to us 
that there is no sufficient reason for the unknown 
cause that gave them birth to have acted along a 
curve so regular and yet so complicated, which 
would appear to have been expressly chosen so 
that the distribution at the present day would not 
be uniform. 

IV. Rouge ct Noir. The questions raised by 
games of chance, such as roulette, are, funda 
mentally, quite analogous to those we have just 
treated. For example, a wheel is divided into thirty- 
seven equal compartments, alternately red and 
black. A ball is spun round the wheel, and after 
having moved round a number of times, it stops in 
front of one of these sub-divisions. The probability 
that the division is red is obviously ^. The needle 
describes an angle 0, including several complete 
revolutions. I do not know what is the prob 
ability that the ball is spun with such a force that 
this angle should lie between and & + (!&, but I 
can make a convention. I can suppose that this 
probability is <j>(6)dQ. As for the function </>(#), I 
can choose it in an entirely arbitrary manner. I 
have nothing to guide me in my choice, but I am 
naturally induced to suppose the function to be 
continuous. Let e be a length (measured on the 
circumference of the circle of radius unity) of each 
red and black compartment. We have to calcu 
late the integral of ^(0)dB, extending it on the one 
hand to all the red, and on the other hand to all 


the black compartments, and to compare the 
results. Consider an interval 2 e comprising two 
consecutive red and black compartments. Let 
M and in be the maximum and minimum values of 
the function </>(#) in this interval. The integral 
extended to the red compartments will be smaller 
than Z Me; extended to the black it will be greater 
than Z inc. The difference will therefore be 
smaller than 21 (M - m) e . But if the function 4> is 
supposed continuous, and if on the other hand the 
interval c is very small with respect to the total 
angle described by the needle, the difference M -m 
will be very small. The difference of the two 
integrals will be therefore very small, and the 
probability will be very nearly J. We see that 
without knowing anything of the function <f> we 
must act as if the probability were J. And on 
the other hand it explains why, from the 
objective point of view, if I watch a certain 
number of coups, observation will give me almost 
as many black coups as red. All the players 
know this objective law; but it leads them into a 
remarkable error, which has often been exposed, 
but into which they are always falling. When 
the red has won, for example, six times running, 
they bet on black, thinking that they are playing 
an absolutely safe game, because they say it is 
a very rare thing for the red to win seven times 
running. In reality their probability of winning 
is still ^. Observation shows, it is true, that 
the series of seven consecutive reds is very rare, 


but series of six reds followed by a black are 
also very rare. They have noticed the rarity of 
the series of seven reds; if they have not remarked 
the rarity of six reds and a black, it is only 
because such series strike the attention less. 

V. The Probability of Causes.- We now come to 
the problems of the probability of causes, the 
most important from the point of view of 
scientific applications. Two stars, for instance, 
are very close together on the celestial sphere. Is 
this apparent contiguity a mere effect of chance ? 
Are these stars, although almost on the same 
visual ray, situated at very different distances 
from the earth, and therefore very far indeed from 
one another ? or does the apparent correspond 
to a real contiguity ? This is a problem on the 
probability of causes. 

First of all, I recall that at the outset of all 
problems of probability of effects that have 
occupied our attention up to now, we have had 
to use a convention which was more or less 
justified; and if in most cases the result was to 
a certain extent independent of this convention, 
it was only the condition of certain hypotheses 
which enabled us a priori to reject discontinuous 
functions, for example, or certain absurd con 
ventions. We shall again find something 
analogous to this when we deal with the prob 
ability of causes. An effect may be produced 
by the cause a or by the cause b. The effect 
has just been observed. We ask the probability 


that it is due to the cause a. This is an a 
posteriori probability of cause. But I could not 
calculate it, if a convention more or less justified 
did not tell me in advance what is the a priori 
probability for the cause a to come into play 
I mean the probability of this event to some one 
who had not observed the effect. To make my 
meaning clearer, I go back to the game of ecarte 
mentioned before. My adversary deals for the 
first time and turns up a king. What is the 
probability that he is a sharper ? The formulae 
ordinarily taught give -J, a result which is 
obviously rather surprising. If we look at it 
closer, we see that the conclusion is arrived at 
as if, before sitting down at the table, I had 
considered that there was one chance in two 
that my adversary was not honest. An absurd 
hypothesis, because in that case I should certainly 
not have played with him ; and this explains the 
absurdity of the conclusion. The function on 
the a priori probability was unjustified, and that 
is why the conclusion of the a posteriori probability 
led me into an inadmissible result. The import 
ance of this preliminary convention is obvious. 
I shall even add that if none were made, the 
problem of the a posteriori probability would have 
no meaning. It -must be always made either 
explicitly or tacitly. 

Let us pass on to an example of a more 
scientific character. I require to determine an 
experimental law; this law, when discovered, can 


be represented by a curve. I make a certain 
number of isolated observations, each of which 
may be represented by a point. When I have 
obtained these different points, I draw a curve 
between them as carefully as possible, giving 
my curve a regular form, avoiding sharp angles, 
accentuated inflexions, and any sudden variation 
of the radius of curvature. This curve will repre 
sent to me the probable law, and not only will 
it give me the values of the functions intermediary 
to those which have been observed, but it also 
gives me the observed values more accurately 
than direct observation does; that is why I make 
the curve pass near the points and not through 
the points themselves. 

Here, then, is a problem in the probability of 
causes. The effects are the measurements I have 
recorded; they depend on the combination of tw r o 
causes the true law of the phenomenon and errors 
of observation. Knowing the effects, we have to 
find the probability that the phenomenon shall 
obey this law or that, and that the observations 
have been accompanied by this or that error. 
The most probable law, therefore, corresponds to 
the curve we have traced, and the most probable 
error is represented by the distance of the cor 
responding point from that curve. But the 
problem has no meaning if before the observa 
tions I had an a priori idea of the probability of 
this law or that, or of the chances of error to 
which I am exposed. If my instruments are 


good (and I knew whether this is so or not before 
beginning the observations), I shall not draw the 
curve far from the points which represent the 
rough measurements. If they are inferior, I may 
draw it a little farther from the points, so that I 
may get a less sinuous curve; much will be sacri 
ficed to regularity. 

Why, then, do I draw a curve without sinu 
osities ? Because I consider a priori a law 
represented by a continuous function (or function 
the derivatives of which to a high order are small), 
as more probable than a law not satisfying those 
conditions. But for this conviction the problem 
would have no meaning ; interpolation would be 
impossible; no law could be deduced from a 
finite number of observations ; science would 
cease to exist. 

Fifty years ago physicists considered, other 
things being equal, a simple law as more probable 
than a complicated law. This principle was even 
invoked in favour of Mariotte s law as against 
that of Regnault. But this belief is now 
repudiated ; and yet, how many times are we 
compelled to act as though we still held it! 
However that may be, what remains of this 
tendency is the belief in continuity, and as we 
have just seen, if the belief in continuity were 
to disappear, experimental science would become 

VI. The Theory of Errors. We are thus brought 
to consider the theory of errors which is directly 


connected with the problem of the probability 
of causes. Here again we find effects to wit, 
a certain number of irreconcilable observations, 
and we try to find the causes which are, on the 
one hand, the true value of the quantity to be 
measured, and, on the other, the error made in 
each isolated observation. We must calculate 
the probable a posteriori value of each error, and 
therefore the probable value of the quantity to be 
measured. But, as I have just explained, we 
cannot undertake this calculation unless we admit 
a priori i.e., before any observations are made 
that there is a law of the probability of errors. 
Is there a law of errors ? The law to which 
all calculators assent is Gauss s law, that is 
represented by a certain transcendental curve 
known as the " bell." 

But it is first of all necessary to recall 
the classic distinction between systematic and 
accidental errors. If the metre with which we 
measure a length is too long, the number we get 
will be too small, and it will be no use to measure 
several times that is a systematic error. If we 
measure with an accurate metre, we may make a 
mistake, and find the length sometimes too large 
and sometimes too small, and when we take the 
mean of a large number of measurements, 
the error will tend to grow small. These are 
accidental errors. 

It is clear that systematic errors do not satisfy 
Gauss s law, but do accidental errors satisfy it ? 


Numerous proofs have been attempted, almost all 
of them crude paralogisms. But starting from 
the following hypotheses we may prove Gauss s 
law : the error is the result of a very large number 
of partial and independent errors ; each partial 
error is very small and obeys any law of prob 
ability whatever, provided the probability of a 
positive error is the same as that of an equal 
negative error. It is clear that these conditions 
will be often, but not always, fulfilled, and we 
may reserve the name of accidental for errors 
which satisfy them. 

We see that the method of least squares is not 
legitimate in every case ; in general, physicists 
are more distrustful of it than astronomers. This 
is no doubt because the latter, apart from the 
systematic errors to which they and the physicists 
are subject alike, have to contend with an 
extremely important source of error which is 
entirely accidental I mean atmospheric undula 
tions. So it is very curious to hear a discussion 
between a physicist and an astronomer about a 
method of observation. The physicist, persuaded 
that one good measurement is w r orth more than 
many bad ones, is pre-eminently concerned with 
the elimination by means of every precaution of 
the final systematic errors; the astronomer retorts : 
" But you can only observe a small number of stars, 
and accidental errors will not disappear." 

What conclusion must we draw 7 ? Must we 
continue to use the method of least squares ? 


We must distinguish. We have eliminated all 
the systematic errors of which we have any 
suspicion ; we are quite certain that there are 
others still, but we cannot detect them ; and yet 
we must make up our minds and adopt a definitive 
value which will be regarded as the probable 
value ; and for that purpose it is clear that the 
best thing we can do is to apply Gauss s law. 
We have only applied a practical rule referring 
to subjective probability. And there is no more 
to be said. 

Yet we want to go farther and say that not 
only the probable value is so much, but that the 
probable error in the result is so much. This 
is absolutely invalid : it would be true only if 
we were sure that all the systematic errors 
were eliminated, and of that we know absolutely 
nothing. We have two series of observations; by 
applying the law of least squares we find that the 
probable error in the first series is twice as small 
as in the second. The second series may, how 
ever, be more accurate than the first, because the 
first is perhaps affected by a large systematic 
error. All that we can say is, that the first series 
is probably better than the second because its 
accidental error is smaller, and that we have no 
reason for affirming that the systematic error is 
greater for one of the series than for the other, 
our ignorance on this point being absolute. 

VII. Conclusions. In the preceding lines I have 
set several problems, and have given no solution. 



I do not regret this, for perhaps they will invite 
the reader to reflect on these delicate questions. 

However that may be, there are certain points 
which seem to be well established. To undertake 
the calculation of any probability, and even for 
that calculation to have any meaning at all, we 
must admit, as a point of departure, an hypothesis 
or convention which has always something 
arbitrary about it. In the choice of this con 
vention we can be guided only by the principle 
of sufficient reason. Unfortunately, this principle 
is very vague and very elastic, and in the cursory 
examination we have just made we have seen it 
assume different forms. The form under which 
we meet it most often is the belief in continuity, 
a belief which it would be difficult to justify by 
apodeictic reasoning, but without which all science 
would be impossible. Finally, the problems to 
which the calculus of probabilities may be applied 
with profit are those in which the result is inde 
pendent of the hypothesis made at the outset, 
provided only that this hypothesis satisfies the 
condition of continuity. 



FresneVs Theory. The best example that can be 
chosen is the theory of light and its relations 
to the theory of electricity. It is owing to Fresnel 
that the science of optics is more advanced than 
any other branch of physics. The theory called the 
theory of undulations forms a complete whole, 
which is satisfying to the mind ; but we must 
not ask from it what it cannot give us. The 
object of mathematical theories is not to reveal 
to us the real nature of things; that would be 
an unreasonable claim. Their only object is to 
co-ordinate the physical laws with which physical 
experiment makes us acquainted, the enunciation 
of which, without the aid of mathematics, we 
should be unable to effect. Whether the ether 
exists or not matters little let us leave that to 
the metaphysicians; what is essential for us is, that 
everything happens as if it existed, and that this 
hypothesis is found to be suitable for the explana 
tion of phenomena. After all, have we any other 

1 This chapter is mainly taken from the prefaces of two of my 
books^ Theorie Mathematique de la lumiere (Paris: Naud, 1889), 
and Electricite et Optique (Paris: Naud, 1901). 


reason for believing in the existence of material 
objects? That, too, is only a convenient hypothesis ; 
only, it will never cease to be so, while some day, 
no doubt, the ether will be thrown aside as useless. 

But at the present moment the laws of optics, 
and the equations which translate them into the 
language of analysis, hold good at least as a first 
approximation. It will therefore be always useful 
to study a theory which brings these equations 
into connection. 

The undulatory theory is based on a molecular 
hypothesis ; this is an advantage to those who 
think they can discover the cause under the law. 
But others find in it a reason for distrust ; and 
this distrust seems to me as unfounded as the 
illusions of the former. These hypotheses play 
but a secondary role. They may be sacrificed, 
and the sole reason why this is not generally done 
is, that it would involve a certain loss of lucidity 
in the explanation. In fact, if we look at it a 
little closer we shall see that we borrow from 
molecular hypotheses but two things the principle 
of the conservation of energy, and the linear form 
of the equations, which is the general law of small 
movements as of all small variations. This ex 
plains why most of the conclusions of Fresnel 
remain unchanged when we adopt the electro 
magnetic theory of light. 

Maxwell s Theory. We all know that it was 
Maxwell who connected by a slender tie two 
branches of physics optics and electricity until 


then unsuspected of having anything in common. 
Thus blended in a larger aggregate, in a higher 
harmony, Fresnel s theory of optics did not perish. 
Parts of it are yet alive, and their mutual relations 
are still the same. Only, the language which we 
use to express them has changed ; and, on the 
other hand, Maxwell has revealed to us other 
relations, hitherto unsuspected, between the 
different branches of optics and the domain of 

The first time a French reader opens Maxwell s 
book, his admiration is tempered with a feeling of 
uneasiness, and often of distrust. 

It is only after prolonged study, and at the cost 
of much effort, that this feeling disappears. Some 
minds of high calibre never lose this feeling. Why 
is it so difficult for the ideas of this English 
scientist to become acclimatised among us? No 
doubt the education received by most enlightened 
Frenchmen predisposes them to appreciate pre 
cision and logic more than any other qualities. 
In this respect the old theories of mathematical 
physics gave us complete satisfaction. All our 
masters, from Laplace to Cauchy, proceeded along 
the same lines. Starting with clearly enunciated 
hypotheses, they deduced from them all their 
consequences with mathematical rigour, and then 
compared them with experiment. It seemed to 
be their aim to give to each of the branches 
of physics the same precision as to celestial 


A mind accustomed to admire such models is 
not easily satisfied with a theory. Not only will 
it not tolerate the least appearance of contradic 
tion, but it will expect the different parts to be 
logically connected with one another, and will 
require the number of hypotheses to be reduced 
to a minimum. 

This is not all ; there will be other demands 
which appear to me to be less reasonable. Behind 
the matter of which our senses are aware, and 
which is made known to us by experiment, such 
a thinker will expect to see another kind of matter 
the only true matter in its opinion which will 
no longer have anything but purely geometrical 
qualities, and the atoms of which will be mathe 
matical points subject to the laws of dynamics 
alone. And yet he will try to represent to 
himself, by an unconscious contradiction, these 
invisible and colourless atoms, and therefore 
to bring them as close as possible to ordinary 

Then only will he be thoroughly satisfied, and 
he will then imagine that he has penetrated the 
secret of the universe. Even if the satisfaction is 
fallacious, it is none the less difficult to give it up. 
Thus, on opening the pages of Maxwell, a French 
man expects to find a theoretical whole, as logical 
and as precise as the physical optics that is founded 
on the hypothesis of the ether. He is thus pre 
paring for himself a disappointment which I 
should like the reader to avoid ; so I will warn 


him at once of what he will find and what he will 
not find in Maxwell. 

Maxwell does not give a mechanical explanation 
of electricity and magnetism ; he confines himself 
to showing that such an explanation is possible, 
He shows that the phenomena of optics are only 
a particular case of electro-magnetic phenomena. 
From the whole theory of electricity a theory of 
light can be immediately deduced. Unfortunately 
the converse is not true ; it is not always easy to 
find a complete. explanation of electrical pheno 
mena. In particular it is not easy if we take 
as our starting-point Fresnel s theory; to do so, 
no doubt, would be impossible; but none the less 
we must ask ourselves if we are compelled to 
surrender admirable results which we thought we 
had definitively acquired. That seems a step 
backwards, and many sound intellects will not 
willingly allow of this. 

Should the reader consent to set some bounds 
to his hopes, he will still come across other 
difficulties. The English scientist does not try 
to erect a unique, definitive, and well-arranged 
building; he seems to raise rather a large number 
of provisional and independent constructions, 
between which communication is difficult and 
sometimes impossible. Take, for instance, the 
chapter in which electrostatic attractions are 
explained by the pressures and tensions of the 
dielectric medium. This chapter might be sup 
pressed without the rest of the book being 


thereby less clear or less complete, and yet 
it contains a theory which is self-sufficient, and 
which can be understood without reading a 
word of what precedes or follows. But it is 
not only independent of the rest of the book ; it 
is difficult to reconcile it with the fundamental 
ideas of the volume. Maxwell does not even 
attempt to reconcile it; he merely says: "I have 
not been able to make the next step namely, to 
account by mechanical considerations for these 
stresses in the dielectric." 

This example will be sufficient to show w r hat 
I mean ; I could quote many others. Thus, who 
would suspect on reading the pages devoted to 
magnetic rotatory polarisation that there is an 
identity between optical and magnetic pheno 
mena ? 

We must not flatter ourselves that we have 
avoided every contradiction, but we ought to 
make up our minds. Two contradictory theories, 
provided that they are kept from overlapping, and 
that we do not look to find in them the explana 
tion of things, may, in fact, be very useful instru 
ments of research ; and perhaps the reading of 
Maxwell would be less suggestive if he had not 
opened up to us so many new and divergent ways. 
But the fundamental idea is masked, as it were. 
So far is this the case, that in most works that are 
popularised, this idea is the only point which is 
left completely untouched. To show the import 
ance of this, I think I ought to explain in what this 


fundamental idea consists ; but for that purpose 
a short digression is necessary. 

The Mechanical Explanation of Physical Phenomena. 
In every physical phenomenon there is a certain 
number of parameters which are reached directly 
by experiment, and which can be measured. I 
shall call them the parameters q. Observation 
next teaches us the laws of the variations of these 
parameters, and these laws can be generally stated 
in the form of differential equations which connect 
together the parameters q and time. What can 
be done to give a mechanical interpretation to 
such a phenomenon ? We may endeavour to 
explain it, either by the movements of ordinary 
matter, or by those of one or more hypothetical 
fluids. These fluids will be considered as formed 
of a very large number of isolated molecules m. 
When may we say that we have a complete 
mechanical explanation of the phenomenon? It 
will be, on the one hand, when we know the 
differential equations which are satisfied by the 
co-ordinates of these hypothetical molecules /;/, 
equations which must, in addition, conform to the 
laws of dynamics; and, on the other hand, when we 
know the relations which define the co-ordinates 
of the molecules m as functions of the parameters 
q, attainable by experiment. These equations, as 
I have said, should conform to the principles of 
dynamics, and, in particular, to the principle of 
the conservation of energy, and to that of least 


The first of these two principles teaches us that 
the total energy is constant, and may be divided 
into two parts : 

(i) Kinetic energy, or vis viva, which depends 
on the masses of the hypothetical molecules m, 
and on their velocities. This I shall call T. (2) 
The potential energy which depends only on the 
co-ordinates of these molecules, and this I shall 
call U. It is the sum of the energies T and U that 
is constant. 

Now what are we taught by the principle of 
least action ? It teaches us that to pass from the 
initial position occupied at the instant t o to 
the final position occupied at the instant t lf the 
system must describe such a path that in the 
interval of time between the instant t o and t v 
the mean value of the action i.e., the difference 
between the two energies T and U, must be as 
small as possible. The first of these two principles 
is, moreover, a consequence of the second. If we 
know the functions T and U, this second principle 
is sufficient to determine the equations of motion. 

Among the paths which enable us to pass from 
one position to another, there is clearly one for 
which the mean value of the action is smaller than 
for all the others. In addition, there is only^such 
path ; and it follows from this, that the principle 
of least action is sufficient to determine the path 
followed, and therefore the equations of motion. 
We thus obtain what are called the equations of 
Lagrange. In these equations the independent 


variables are the co-ordinates of the hypothetical 
molecules m; but I now assume that we take for 
the variables the parameters q, which are directly 
accessible to experiment. 

The two parts of the energy should then be 
expressed as a function of the parameters q and 
their derivatives ; it is clear that it is under this 
form that they will appear to the experimenter. 
The latter will naturally endeavour to define 
kinetic and potential energy by the aid of 
quantities he can directly observe. 1 If this be 
granted, the system will always proceed from one 
position to another by such a path that the mean 
value of the action is a minimum. It matters 
little that T and U are now expressed by the aid 
of the parameters q and their derivatives ; it 
matters little that it is also by the aid of these 
parameters that we define the initial and fina 
positions; the principle of least action will always 
remain true. 

Now here again, of the whole of the paths which 
lead from one position to another, there is one and 
only one for which the mean action is a minimum. 
The principle of least action is therefore sufficient 
for the determination of the differential equations 
which define the variations of the parameters q. 
The equations thus obtained are another form of 
Lagrange s equations. 

1 We may add that U will depend only on the q parameters, that 
T will depend on them and their derivatives with respect to time, 
and will be a homogeneous polynomial of the second degree with 
respect to these derivatives. 


To form these equations we need not know the 
relations which connect the parameters q with the 
co-ordinates of the hypothetical molecules, nor the 
masses of the molecules, nor the expression of U 
as a function of the co-ordinates of these molecules. 
All we need know is the expression of U as a 
function of the parameters q, and that of T as a 
function of the parameters q and their derivatives 
i.e., the expressions of the kinetic and potential 
energy in terms of experimental data. 

One of two things must now happen. Either for 
a convenient choice of T and U the Lagrangian 
equations, constructed as we have indicated, will 
be identical with the differential equations deduced 
from experiment, or there will be no functions T 
and U for which this identity takes place. In the 
latter case it is clear that no mechanical explana 
tion is possible. The necessary condition for a 
mechanical explanation to be possible is therefore 
this : that we may choose the functions T and U so 
as to satisfy the principle of least action, and of the 
conservation of energy. Besides, this condition is 
sufficient. Suppose, in fact, that we have found a 
function U of the parameters q, which represents 
one of the parts of energy, and that the part of the 
energy which we represent by T is a function of 
the parameters q and their derivatives; that it 
is a polynomial of the second degree with respect 
to its derivatives, and finally that the Lagrangian 
equations formed by the aid of these two functions 
T and U are in conformity with the data of the 


experiment. How can we deduce from this a 
mechanical explanation ? U must be regarded as 
the potential energy of a system of which T is the 
kinetic energy. There is no difficulty as far as U 
is concerned, but can T be regarded as the vis viva 
of a material system ? 

It is easily shown that this is always possible, 
and in an unlimited number of ways. I will be 
content with referring the reader to the pages of 
the preface of my lectricite et Optiqne for further 
details. Thus, if the principle of least action 
cannot be satisfied, no mechanical explanation is 
possible; if it can be satisfied, there is not only one 
explanation, but an unlimited number, whence it 
follows that since there is one there must be an 
unlimited number. 

One more remark. Among the quantities that 
may be reached by experiment directly we shall 
consider some as the co-ordinates of our hypo 
thetical molecules, some will be our parameters </, 
and the rest will be regarded as dependent not 
only on the co-ordinates but on the velocities or 
what comes to the same thing, we look on them as 
derivatives of the parameters q, or as combinations 
of these parameters and their derivatives. 

Here then a question occurs: among all these 
quantities measured experimentally which shall we 
choose to represent the parameters q ? and which 
shall we prefer to regard as the derivatives of these 
parameters ? This choice remains arbitrary to a 
large extent, but a mechanical explanation will be 


possible if it is done so as to satisfy the principle of 
least action. 

Next, Maxwell asks : Can this choice and that of 
the two energies T and U be made so that electric 
phenomena will satisfy this principle ? Experiment 
shows us that the energy of an electro-magnetic 
iield decomposes into electro-static and electro- 
dynamic energy. Maxwell recognised that if we 
regard the former as the potential energy U, and 
the latter as the kinetic energy T, and that if on 
the other hand we take the electro-static charges 
of the conductors as the parameters q, and the in 
tensity of the currents as derivatives of other 
parameters (/under these conditions, Maxwell 
has recognised that electric phenomena satisfies the 
principle of least action. He was then certain of 
a mechanical explanation. If he had expounded 
this theory at the beginning of his first volume, 
instead of relegating it to a corner of the second, it 
would not have escaped the attention of most 
readers. If therefore a phenomenon allows of a 
complete mechanical explanation, it allows of an 
unlimited number of others, which will equally take 
into account all the particulars revealed by experi 
ment. And this is confirmed by the history of 
every branch of physics. In Optics, for instance, 
Fresnel believed vibration to be perpendicular to 
the plane of polarisation; Neumann holds that it is 
parallel to that plane. For a long time an experi- 
mcntum crucis was sought for, which would enable 
us to decide between these two theories, but in 


vain. In the same way, without going out of the 
domain of electricity, we find that the theory of 
two fluids and the single fluid theory equally 
account in a satisfactory manner for all the laws 
of electro-statics. All these facts are easily ex 
plained, thanks to the properties of the Lagrange 

It is easy now to understand Maxwell s funda 
mental idea. To demonstrate the possibility of a 
mechanical explanation of electricity we need not 
trouble to find the explanation itself; we need only 
know the expression of the two functions T and U, 
which are the two parts of energy, and to form with 
these two functions Lagrange s equations, and 
then to compare these equations with the experi 
mental laws. 

How shall we choose from all the possible 
explanations one in which the help of experiment 
will be wanting ? The day will perhaps come 
when physicists will no longer concern themselves 
with questions which are inaccessible to positive 
methods, and will leave them to the metaphy 
sicians. That day has not yet come; man does not 
so easily resign himself to remaining for ever ignor 
ant of the causes of things. Our choice cannot be 
therefore any longer guided by considerations in 
which personal appreciation plays too large a part. 
There are, however, solutions which all will reject 
because of their fantastic nature, and others which 
all will prefer because of their simplicity. As 
far as magnetism and electricity are concerned, 


Maxwell abstained from making any choice. It is 
not that he has a systematic contempt for all that 
positive methods cannot reach, as may be seen 
from the time he has devoted to the kinetic theory 
of gases. I may add that if in his magnum opus he 
develops no complete explanation, he has attempted 
one in an article in the Philosophical Magazine. 
The strangeness and the complexity of the 
hypotheses he found himself compelled to make, 
led him afterwards to withdraw it. 

The same spirit is found throughout his whole 
work. He throws into relief the essential i.e., 
what is common to all theories; everything that 
suits only a particular theory is passed over almost 
in silence. The reader therefore finds himself in 
the presence of form nearly devoid of matter, 
which at first he is tempted to take as a fugitive 
and unassailable phantom. But the efforts he is 
thus compelled to make force him to think, and 
eventually he sees that there is often something 
rather artificial in the theoretical "aggregates" 
which he once admired. 



THE history of electro-dynamics is very instructive 
from our point of view. The title of Ampere s 
immortal work is, Thcorie dcs phenomenes electro- 
dynamiqucs, uniqueinent fondee sur experience. He 
therefore imagined that he had made no hypotheses; 
but as we shall not be long in recognising, he was 
mistaken ; only, of these hypotheses he was quite 
unaware. On the other hand, his successors see 
them clearly enough, because their attention is 
attracted by the weak points in Ampere s solution. 
They made fresh hypotheses, but this time 
deliberately. How many times they had to change 
them before they reached the classic system, which 
is perhaps even now not quite definitive, we shall 

I. Ampere s Theory. In Ampere s experimental 
study of the mutual action of currents, he has 
operated, and he could operate only, with closed 
currents. This was not because he denied the 
existence or possibility of open currents. If two 
conductors are positively and negatively charged 
and brought into communication by a wire, a 
current is set up which passes from one to the 



other until the two potentials are equal. Accord 
ing to the ideas of Ampere s time, this was 
considered to be an open current ; the current was 
known to pass from the first conductor to the 
second, but they did not know it returned from the 
second to the first. All currents of this kind were 
therefore considered by Ampere to be open- 
currents for instance, the currents of discharge 
of a condenser; he was unable to experiment on 
them, their duration being too short. Another 
kind of open current may be imagined. Suppose 
we have two conductors A and B connected by a 
wire AMB. Small conducting masses in motion 
are first of all placed in contact with the conductor 
B, receive an electric charge, and leaving B are 
set in motion along a path BNA, carrying their 
charge with them. On coming into contact with A 
they lose their charge, which then returns to B 
along the wire AMB. Now here we have, in a 
sense, a closed circuit, since the electricity describes 
the closed circuit BNAMB; but the two parts of 
the current are quite different. In the wire AMB 
the electricity is displaced through a fixed conductor 
like a voltaic current, overcoming an ohmic resist 
ance and developing heat; we say that it is 
displaced by conduction. In the part BNA the 
electricity is carried by a moving conductor, and is 
said to be displaced by convection. If therefore the 
convection current is considered to be perfectly 
analogous to the conduction current, the circuit 
BNAMB is closed; if on the contrary the convec- 


tion current is not a " true current," and, for 
instance, does not act on the magnet, there is only 
the conduction current AMB, which is open. For 
example, if we connect by a wire the poles of a 
Holtz machine, the charged rotating disc transfers 
the electricity by convection from one pole to the 
other, and it returns to the first pole by conduction 
through the wire. But currents of this kind are 
very difficult to produce with appreciable intensity; 
in fact, with the means at Ampere s disposal we 
may almost say it was impossible. 

To sum up, Ampere could conceive of the exist 
ence of two kinds of open currents, but he could 
experiment on neither, because they were not 
strong enough, or because their duration was too 
short. Experiment therefore could only show him 
the action of a closed current on a closed current 
or more accurately, the action of a closed current 
on a portion of current, because a current can be 
made to describe a closed circuit, of which part may 
be in motion and the other part fixed. The displace 
ments of the moving part may be studied under the 
action of another closed current. On the other 
hand, Ampere had no means of studying the action 
of an open current either on a closed or on another 
open current. 

i. The Case of Closed Currents. In the case of 
the mutual action of two closed currents, ex 
periment revealed to Ampere remarkably simple 
laws. The following will be useful to us in the 
sequel : 


(1) If the intensity of the currents is kept constant, 
and if the two circuits, after having undergone any 
displacements and deformations whatever, return 
finally to their initial positions, the total work 
done by the electro-dynamical actions is zero. In 
other words, there is an electro-dynamical potential 
of the two circuits proportional to the product of 
their intensities, and depending on the form and 
relative positions of the circuits ; the work done 
by the electro-dynamical actions is equal to the 
change of this potential. 

(2) The action of a closed solenoid is zero. 

(3) The action of a circuit C on another voltaic 
circuit C depends only on the " magnetic field " 
developed by the circuit C. At each point in 
space we can, in fact, define in magnitude and 
direction a certain force called " magnetic force," 
which enjoys the following properties: 

(a) The force exercised by C on a magnetic 
pole is applied to that pole, and is equal to the 
magnetic force multiplied by the magnetic mass 
of the pole. 

(6) A very short magnetic needle tends to take 
the direction of the magnetic force, and the couple 
to which it tends to reduce is proportional to the 
product of the magnetic force, the magnetic 
moment of the needle, and the sine of the dip 
of the needle. 

(c) If the circuit C is displaced, the amount of 
the work done by the electro-dynamic action of 
C on C will be equal to the increment of " flow 


of magnetic force " which passes through the 

2. Action of a Closed Current on a Portion of 
Current. Ampere being unable to produce the 
open current properly so called, had only one 
way of studying the action of a closed current 
on a portion of current. This was by operating 
on a circuit C composed of two parts, one mov 
able and the other fixed. The movable part was, 
for instance, a movable wire a/3, the ends a and ft 
of which could slide along a fixed wire. In one of 
the positions of the movable wire the end a rested 
on the point A, and the end ft on the point B of 
the fixed wire. The current ran from a to ft i.e., 
from A to B along the movable wire, and then 
from B to A along the fixed wire. This current 
was therefore closed. 

In the second position, the movable wire 
having slipped, the points a and ft were respect 
ively at A and B on the fixed wire. The current 
ran from a to ft i.e., from A to B on the mov 
able wire, and returned from B to B, and 
then from B to A, and then from A to A all on 
the fixed wire. This current was also closed. 
If a similar circuit be exposed to the action of a 
closed current C, the movable part will be dis 
placed just as if it were acted on by a force. 
Ampere admits that the force, apparently acting on 
the movable part A B, representing the action of 
C on the portion aft of the current, remains the 
same whether an open current runs through a/3, 


stopping at a and /3, or whether a closed current 
runs first to ft and then returns to a through the 
fixed portion of the circuit. This hypothesis 
seemed natural enough, and Ampere innocently 
assumed it; nevertheless the hypothesis is not a 
necessity, for we shall presently see that Helmholtz 
rejected it. However that may be, it enabled 
Ampere, although he had never produced an open 
current, to lay down the laws of the action of a 
closed current on an open current, or even on an 
element of current. They are simple: 

(1) The force acting on an element of current 
is applied to that element ; it is normal to the 
element and to the magnetic force, and pro 
portional to that component of the magnetic force 
which is normal to the element. 

(2) The action of a closed solenoid on an 
element of current is zero. But the electro- 
dynamic potential has disappeared i.e., when a 
closed and an open current of constant intensities 
return to their initial positions, the total work 
done is not zero. 

3. Continuous Rotations. The most remarkable 
electro-dynamical experiments are those in which 
continuous rotations are produced, and which are 
called unipolar induction experiments. A magnet 
may turn about its axis ; a current passes first 
through a fixed wire and then enters the magnet 
by the pole N, for instance, passes through 
half the magnet, and emerges by a sliding con 
tact and re-enters the fixed wire. The magnet 


then begins to rotate continuously. This is 
Faraday s experiment. How is it possible ? If it 
were a question of two circuits of invariable form, 
C fixed and C movable about an axis, the latter 
would never take up a position of continuous 
rotation ; in fact, there is an electro-dynamical 
potential ; there must therefore be a position of 
equilibrium when the potential is a maximum. 
Continuous rotations are therefore possible only 
when the circuit C is composed of two parts 
one fixed, and the other movable about an axis, 
as in the case of Faraday s experiment. Here 
again it is convenient to draw a distinction. The 
passage from the fixed to the movable part, or 
rice versa, may take place either by simple contact, 
the same point of the movable part remaining 
constantly in contact with the same point of the 
fixed part, or by sliding contact, the same point of 
the movable part coming successively into con 
tact with the different points of the fixed part. 

It is only in the second case that there can 
be continuous rotation. This is what then 
happens : the system tends to take up a position 
of equilibrium ; but, when at the point of reaching 
that position, the sliding contact puts the moving 
part in contact with a fresh point in the fixed 
part ; it changes the connexions and therefore the 
conditions of equilibrium, so that as the position 
of equilibrium is ever eluding, so to speak, the 
system which is trying to reach it, rotation may 
take place indefinitely. 


Ampere admits that the action of the circuit on 
the movable part of C is the same as if the fixed 
part of C did not exist, and therefore as if the 
current passing through the movable part were 
an open current. He concluded that the action of 
a closed on an open current, or vice versa, that of 
an open current on a fixed current, may give rise 
to continuous rotation. But this conclusion 
depends on the hypothesis which I have enunci 
ated, and to which, as I said above, Helmholtz 
declined to subscribe. 

4. Mutual Action of Two Open Currents. As far 
as the mutual action of two open currents, and in 
particular that of two elements of current, is 
concerned, all experiment breaks down. Ampere 
falls back on hypothesis. He assumes: (i) that 
the mutual action of two elements reduces to a 
force acting along their join ; (2) that the action 
of two closed currents is the resultant of the 
mutual actions of their different elements, which 
are the same as if these elements were isolated. 

The remarkable thing is that here again Ampere 
makes two hypotheses without being aware of it. 
However that may be, these two hypotheses, 
together with the experiments on closed currents, 
suffice to determine completely the law of mutual 
action of two elements. But then, most of the 
simple laws we have met in the case of closed 
currents are no longer true. In the first place, 
there is no electro-dynamical potential ; nor" was 
there any, as we have seen, in the case of a closed 


current acting on an open current. Next, there 
is, properly speaking, no magnetic force ; and we 
have above denned this force in three different 
ways: (i) By the action on a magnetic pole; 
(2) by the director couple which orientates the 
magnetic needle; (3) by the action on an element 
of current. 

In the case with which we are immediately 
concerned, not only are these three definitions not 
in harmony, but each has lost its meaning : 

(1) A magnetic pole is no longer acted on by a 
unique force applied to that pole. We have seen, 
in fact, the action of an element of current on a 
pole is not applied to the pole but to the element ; 
it may, moreover, be replaced by a force applied to 
the pole and by a couple. 

(2) The couple which acts on the magnetic 
needle is no longer a simple director couple, for its 
moment with respect to the axis of the needle is 
not zero. It decomposes into a director couple, 
properly so called, and a supplementary couple 
which tends to produce the continuous rotation of 
which we have spoken above. 

(3) Finally, the force acting on an element of 
a current is not normal to that element. In 
other words, the unity of the magnetic force has 

Let us see in what this unity consists. Two 
systems which exercise the same action on a mag 
netic pole will also exercise the same action on an 
indefinitely small magnetic needle, or on an element 



of current placed at the point in space at which the 
pole is. Well, this is true if the two systems only 
contain closed currents, and according to Ampere 
it would not be true if the systems contained open 
currents. It is sufficient to remark, for instance, 
that if a magnetic pole is placed at A and an 
element at B, the direction of the element being 
in AB produced, this element, which will exercise 
no action on the pole, will exercise an action 
either on a magnetic needle placed at A, or on 
an element of current at A. 

5. Induction. We know that the discovery of 
electro-dynamical induction followed not long after 
the immortal work of Ampere. As long as it is 
only a question of closed currents there is no 
difficulty, and Helmholtz has even remarked that 
the principle of the conservation of energy is 
sufficient for us to deduce the laws of induction 
from the electro-dynamical laws of Ampere. But 
on the condition, as Bertrand has shown, that 
we make a certain number of hypotheses. 

The same principle again enables this deduction 
to be made in the case of open currents, although 
the result cannot be tested by experiment, since 
such currents cannot be produced. 

If we wish to compare this method of analysis 
with Ampere s theorem on open currents, we get 
results which are calculated to surprise us. In 
the first place, induction cannot be deduced from 
the variation of the magnetic field by the well- 
known formula of scientists and practical men; 


in fact, as I have said, properly speaking, there 
is no magnetic field. But further, if a circuit C 
is subjected to the induction of a variable voltaic 
system S, and if this system S be displaced and 
deformed in any way whatever, so that the 
intensity of the currents of this system varies 
according to any law whatever, then so long 
as after these variations the system eventually 
returns to its initial position, it seems natural 
to suppose that the mean electro-motive force 
induced in the current C is zero. This is true if 
the circuit C is closed, and if the system S only 
contains closed currents. It is no longer true if 
we accept the theory of Ampere, since there would 
be open currents. So that not only will induction 
no longer be the variation of the flow of magnetic 
force in any of the usual senses of the word, but 
it cannot be represented by the variation of that 
force whatever it may be. 

II. Helmholtz s Theory. I have dwelt upon the 
consequences of Ampere s theory and on his 
method of explaining the action of open currents. 
It is difficult to disregard the paradoxical and 
artificial character of the propositions to which 
we are thus led. We feel bound to think " it 
cannot be so." We may imagine then that 
Helmholtz has been led to look for something 
else. He rejects the fundamental hypothesis of 
Ampere namely, that the mutual action of two 
elements of current reduces to a force along their 
join. He admits that an clement of current is not 


acted upon by a single force but by a force and a 
couple, and this is what gave rise to the cele 
brated polemic between Bertrand and Helmholtz. 
Helmholtz replaces Ampere s hypothesis by the 
following : Two elements of current always 
admit of an electro-dynamic potential, depending 
solely upon their position and orientation; and the 
work of the forces that they exercise one on the 
other is equal to the variation of this potential. 
Thus Helmholtz can no more do without 
hypothesis than Ampere, but at least he does 
not do so without explicitly announcing it. In 
the case of closed currents, which alone are 
accessible to experiment, the two theories agree; 
in all other cases they differ. In the first place, 
contrary to what Ampere supposed, the force 
\vhich seems to act on the movable portion of 
a closed current is not the same as that acting 
on the movable portion if it were isolated and 
if it constituted an open current. Let us return 
to the circuit C , of which we spoke above, and 
which was formed of a movable wire sliding on 
a fixed wire. In the only experiment that can be 
made the movable portion a/3 is not isolated, but is 
part of a closed circuit. When it passes from 
AB to A B , the total electro-dynamic potential 
varies for two reasons. First, it has a slight incre 
ment because the potential of A B with respect 
to the circuit C is not the same as that of AB; 
secondly, it has a second increment because it 
must be increased by the potentials of the elements 


A A and B B with respect to C. It is this double 
increment which represents the work of the force 
acting upon the portion AB. If, on the contrary, 
a/3 be isolated, the potential would only have the 
first increment, and this first increment alone 
would measure the work of the force acting on 
AB. In the second place, there could be no 
continuous rotation without sliding contact, and 
in fact, that, as we have seen in the case of closed 
currents, is an immediate consequence of the 
existence of an electro-dynamic potential. In 
Faraday s experiment, if the magnet is fixed, 
and if the part of the current external to the 
magnet runs along a movable wire, that movable 
wire may undergo continuous rotation. But it 
does not mean that, if the contacts of the weir 
with the magnet were suppressed, and an open 
current were to run along the wire, the wire 
would still have a movement of continuous rota 
tion. I have just said, in fact, that an isolated 
element is not acted on in the same way as a 
movable element making part of a closed circuit. 
But there is another difference. The action of a 
solenoid on a closed current is zero according to 
experiment and according to the two theories. 
Its action on an open current would be zero 
according to Ampere, and it would not be 
zero according to Helmholtz. From this follows 
an important consequence. We have given above 
three definitions of the magnetic force. The third 
has no meaning here, since an element of current 


is no longer acted upon by a single force. Nor 
has the first any meaning. What, in fact, is a 
magnetic pole ? It is the extremity of an 
indefinite linear magnet. This magnet may be 
replaced by an indefinite solenoid. For the 
definition of magnetic force to have any mean 
ing, the action exercised by an open current on 
an indefinite solenoid would only depend on the 
position of the extremity of that solenoid i.e., 
that the action of a closed solenoid is zero. Now 
we have just seen that this is not the case. On 
the other hand, there is nothing to prevent us 
from adopting the second definition which is 
founded on the measurement of the director 
couple which tends to orientate the magnetic 
needle ; but, if it is adopted, neither the effects 
of induction nor electro-dynamic effects will 
depend solely on the distribution of the lines 
of force in this magnetic field. 

III. Difficulties raised by these Theories. Helm- 
holtz s theory is an advance on that of Ampere; 
it is necessary, however, that every difficulty 
should be removed. In both, the name " magnetic 
field " has no meaning, or, if we give it one by a 
more or less artificial convention, the ordinary 
laws so familiar to electricians no longer apply; 
and it is thus that the electro-motive force induced 
in a wire is no longer measured by the number 
of lines of force met by that wire. And our 
objections do not proceed only from the fact that 
it is difficult to give up deeply-rooted habits of 


language and thought. There is something more. 
If we do not believe in actions at a distance, 
electro-dynamic phenomena must be explained by 
a modification of the medium. And this medium 
is precisely what we call "magnetic field, and 
then the electro-magnetic effects should only 
depend on that field. All these difficulties arise 
from the hypothesis of open currents. 

IV. Maxwell s Theory. Such were the difficulties 
raised by the current theories, when Maxwell with 
a stroke of the pen caused them to vanish. To 
his mind, in fact, all currents are closed currents. 
Maxwell admits that if in a dielectric, the electric 
field happens to vary, this dielectric becomes the 
seat of a particular phenomenon acting on the 
galvanometer like a current and called the current 
of displacement. If, then, two conductors bearing 
positive and negative charges are placed in con 
nection by means of a wire, during the discharge 
there is an open current of conduction in that 
wire; but there are produced at the same time in 
the surrounding dielectric currents of displace 
ment which close this current of conduction. We 
know that Maxwell s theory leads to the explana 
tion of optical phenomena which would be due to 
extremely rapid electrical oscillations. At that 
period such a conception was only a daring hypo 
thesis which could be supported by no experiment; 
but after twenty years Maxwell s ideas received the 
confirmation of experiment. Hertz succeeded in 
producing systems of electric oscillations which 


reproduce all the properties of light, and only 
differ by the length of their wave that is to say, 
as violet differs from red. In some measure he 
made a synthesis of light. It might be said that 
Hertz has not directly proved Maxwell s funda 
mental idea of the action of the current of 
displacement on the galvanometer. That is true 
in a sense. What he has shown directly is that 
electro-magnetic induction is not instantaneously 
propagated, as was supposed, but its speed is the 
speed of light. Yet, to suppose there is no current 
of displacement, and that induction is with the 
speed of light ; or, rather, to suppose that the 
currents of displacement produce inductive effects, 
and that the induction takes place instantaneously 
comes to the same thing. This cannot be seen at 
the first glance, but it is proved by an analysis 
of which I must not even think of giving even a 
summary here. 

V. Rowland s Experiment. But, as I have said 
above, there are two kinds of open conduction 
currents. There are first the currents of discharge 
of a condenser, or of any conductor whatever. 
There are also cases in which the electric charges 
describe a closed contour, being displaced by con 
duction in one part of the circuit and by convec 
tion in the other part. The question might be 
regarded as solved for open currents of the first 
kind; they were closed by currents of displace 
ment. For open currents of the second kind the 
solution appeared still more simple. 


It seemed that if the current were closed it 
could only be by the current of convection itself. 
For that purpose it was sufficient to admit that a 
" convection current " i.e., a charged conductor in 
motion could act on the galvanometer. But ex 
perimental confirmation was lacking. It appeared 
difficult, in fact, to obtain a sufficient intensity 
even by increasing as much as possible the charge 
and the velocity of the conductors. Rowland, an 
extremely skilful experimentalist, was the first to 
triumph, or to seem to triumph, over these diffi 
culties. A disc received a strong electrostatic 
charge and a very high speed of rotation. An 
astatic magnetic system placed beside the disc 
underwent deviations. The experiment was made 
twice by Rowland, once in Berlin and once at Balti 
more. It was afterwards repeated by Himstedt. 
These physicists even believed that they could 
announce that they had succeeded in making 
quantitative measurements. For twenty years 
Rowland s law was admitted without objection 
by all physicists, and, indeed, everything seemed 
to confirm it. The spark certainly does produce a 
magnetic effect, and does it not seem extremely 
likely that the spark discharged is due to particles 
taken from one of the electrodes and transferred 
to the other electrode with their charge ? Is not 
the very spectrum of the spark, in which we 
recognise the lines of the metal of the electrode, 
a proof of it ? The spark would then be a real 
current of induction. 


On the other hand, it is also admitted that in 
an electrolyte the electricity is carried by the ions 
in motion. The current in an electrolyte would 
therefore also be a current of convection; but it 
acts on the magnetic needle. And in the same 
way for cathodic rays; Crooks attributed these 
rays to very subtle matter charged with negative 
electricity am! moving with very high velocity. 
He looked upon them, in other words, as currents 
of convection. * Now, these cathodic rays are 
deviated by the magnet. In virtue of the 
principle of action and re-action, they should in 
their turn deviate the magnetic needle. It is 
true that Hertz believed he had proved that the 
cathodic rays do not carry negative electricity, and 
that they do not act on the magnetic needle; but 
Hertz was wrong. First of all, Perrin succeeded 
in collecting the electricity carried by these rays 
electricity of which Hertz denied the existence; the 
German scientist appears to have been deceived 
by the effects due to the action of the X-rays, 
which were not yet discovered. Afterwards, and 
quite recently, the action of the cathodic rays on 
the magnetic needle has been brought to light. 
Thus all these phenomena looked upon as currents 
of convection, electric sparks, electrolytic currents, 
cathodic rays, act in the same manner on the 
galvanometer and in conformity to Rowland s 

VI. Loventz s Theory. We need not go much 
further. According to Lorentz s theory, currents 


of conduction would themselves be true convection 
currents. Electricity would remain indissolubly 
connected with certain - material particles called 
electrons. The circulation of these electrons 
through bodies would produce voltaic currents, 
and what would .distinguish conductors from 
insulators would be that the one could be traversed 
by these electrons, while the others would check 
the movement of the electrons. Lorentz s theory 
is very attractive. It gives a very simple explana 
tion of certain phenomena, which the earlier 
theories even Maxwell s in its primitive form- 
could only deal with in an unsatisfactory manner; 
for example, the aberration of light, the partial 
impulse of luminous waves, magnetic polarisation, 
and Zeeman s experiment. 

A few objections still remained. The pheno 
mena of an electric system seemed to depend on 
the absolute velocity of translation of the centre 
of gravity of this system, which is contrary to 
the idea that we have of the relativity of space. 
Supported by M. Cremieu, M. Lippman has pre 
sented this objection in a very striking form. 
Imagine two charged conductors with the same 
velocity of translation. They are relatively at 
rest. However, each of them being equivalent 
to a current of convection, they ought to attract 
one another, and by measuring this attraction 
we could measure their absolute velocity. 
"No!" replied the partisans of Lorentz. "What 
we could measure in that way is not their 


absolute velocity, but their relative velocity with 
respect to the ether, so that the principle of rela 
tivity is safe." Whatever there may be in these 
objections, the edifice of electro-dynamics seemed, 
at any rate in its broad lines, definitively con 
structed. Everything was presented under the 
most satisfactory aspect. The theories of Ampere 
and Helmholtz, which were made for the open 
currents that no longer existed, seem to have no 
more than purely historic interest, and the in 
extricable complications to which these theories 
led have been almost forgotten. This quiescence 
has been recently disturbed by the experiments of 
M. Cremieu, which have contradicted, or at least 
have seemed to contradict, the results formerly 
obtained by Rowland. Numerous investigators 
have endeavoured to solve the question, and fresh 
experiments have been undertaken. What result 
will they give ? I shall take care not to risk a 
prophecy which might be falsified between the 
day this book is ready for the press and the day on 
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" . J U L U 

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Science and hypothesis