it will be true for a = 
 + 1.1 Now, it is true for a = 1,
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:
1For (
 + 1) + 1 = (1 + 
) + 1 = 1 + (
 + 1).—[Tr.]
science and hypothesis 10
The theorem has just been shown to hold good for b = 1,
and it may be verified analytically that if it is true for
b = , it will be true for b =  + 1. The proposition is
thus established by recurrence.
definition of multiplication.
We shall define multiplication by the equalities
(1) a  1 = a;
(2) a  b = a  (b 􀀀 1)+ a:
Both of these include an infinite number of definitions;
having defined a1, it enables us to define in succession
a  2, a  3, and so on.
properties of multiplication.
Distributive.—I say that
(a + b)  c = (a  c) + (b  c):
We can verify analytically that the theorem is true for
c = 1; then if it is true for c = 
, it will be true for
c = 
 +1. The proposition is then proved by recurrence.
nature of mathematical reasoning. 11
Commutative.—(1) I say that
a  1 = 1  a:
The theorem is obvious for a = 1. We can verify analytically
that if it is true for a = , it will be true for
a =  + 1.
(2) I say that
a  b = b  a:
The theorem has just been proved for b = 1. We can
verify analytically that if it be true for b =  it will be
true for b =  + 1.
IV.
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 n = 1; we then show that if it is true
for n􀀀1 it is true for n, and we conclude that it is true for
all integers. We have now 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.
science and hypothesis 12
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 analytical instrument,
and is incapable of teaching us anything new. If
mathematics had no other instrument, 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, we 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 modified form. It is
therefore mathematical reasoning par excellence, and we
must examine it closer.
V.
The essential characteristic of reasoning by recurrence
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 1. Now,
if it is true of 1, it is true of 2; therefore it is true of 2.
nature of mathematical reasoning. 13
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 􀀀 1, 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 particular 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 syllogisms, and we
science and hypothesis 14
should have to cross an abyss which the patience of the
analyst, restricted to the resources of formal logic, will
never succeed in crossing.
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 chessplayer
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 faculties to Arithmetic, he cannot conceive its
general truths by direct intuition alone; to prove even
the smallest theorem he must use reasoning by recurrence,
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 indispensable, 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
nature of mathematical reasoning. 15
there would be no science at all, because there would be
nothing general.
VI.
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 ourselves the illusion of having proved that reasoning
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 therefore escape the conclusion that
the rule of reasoning by recurrence is irreducible to the
principle of contradiction. Nor can the rule come to us
from experiment. Experiment may teach us that the 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
science and hypothesis 16
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
aid. This rule, inaccessible to analytical proof and to
experiment, is the exact type of the à 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 1, 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
nature of mathematical reasoning. 17
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
belief 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.
VII.
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 + 1 = 1 + 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
science and hypothesis 18
otherwise have appeared incomprehensible to us at the
beginning of this study, but which 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
(1) a + 2 = 2 + a;
we need only apply the rule
a + 1 = 1 + a
twice, and write
(2) a + 2 = a + 1 + 1 = 1 + a + 1 = 1 + 1 + a = 2 + a:
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
nature of mathematical reasoning. 19
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 (1), and analysis only
serves to separate the elements which enter into these
combinations and to study their relations.
Mathematicians therefore proceed “by construction,”
they “construct” more complicated combinations. 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
themselves. 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 condition 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
science and hypothesis 20
elements themselves. What can this advantage be? Why
reason on a polygon, for instance, which is always decomposable
into triangles, and not on elementary triangles?
It is because there are properties of polygons 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 juxtaposition
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 induction,
construction would be powerless to create science.
Let me observe, in conclusion, that this induction is
only possible if the same operation can be repeated indefinitely.
That is why the theory of chess can never become
nature of mathematical reasoning. 21
a science, for the different moves of the same piece are
limited and do not resemble each other.
CHAPTER II.
MATHEMATICAL MAGNITUDE AND EXPERIMENT.
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 instruments to him; he uses space in his
geometry just as he uses chalk; and further, too much
importance must not be attached to accidents which are
often nothing more than the whiteness of the chalk.
The pure analyst has not to dread this pitfall. He has
disengaged mathematics from all extraneous elements,
and he is in a position to answer our question:—“Tell
me exactly what this continuum is, about which mathematicians
reason.” Many analysts who reflect on their
art have already done so—M. Tannery, for instance, in
his Introduction à la théorie des Fonctions d’une variable.
Let us start with the integers. Between any two consecutive
sets, intercalate one or more intermediary 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; bemathematical
magnitude. 23
tween 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 preliminary
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,” according 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
when 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 metaphysicians.
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
science and hypothesis 24
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 definition.
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
complete, and we come back to it after this rather long
digression.
Definition of Incommensurables.—The mathematicians
of the Berlin school, and Kronecker in particular,
have devoted themselves to constructing 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
mathematical magnitude. 25
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 now 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
science and hypothesis 26
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 division.
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 commensurable whose square
is still nearer to 2. From Kronecker’s point of view, the
incommensurable number p2 is nothing but the symbol
of this particular method of division of commensurable
numbers; and to each mode of repartition corresponds in
this way a number, commensurable or not, which serves
mathematical magnitude. 27
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 11 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
science and hypothesis 28
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 disagreement with
the law of contradiction, and the necessity of banishing
this disagreement has compelled 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 senses.
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 intermathematical
magnitude. 29
calated 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
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
continuum 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
science and hypothesis 30
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 intermathematical
magnitude. 31
calate new sets according to the laws of incommensurable
numbers, we obtain what may be called a continuum of
the second order.
Second Stage.—We have only taken our first step. We
have explained the origin of continuums 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 some 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
science and hypothesis 32
point, and this truth seems intuitive.
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 commensurable
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 incommensurable
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
mathematical magnitude. 33
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 continuum properly so called.
Summary.—To sum up, the mind has the faculty of
creating symbols, and it is thus that it has constructed
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 continuum, 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
science and hypothesis 34
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 continuum become measurable, and the operations
of arithmetic be applicable. This can only be done
by the aid of a new and special convention; 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 n intermediary
sets; by convention we now assume these new sets
to be equidistant. This is one of the ways of defining 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
mathematical magnitude. 35
important questions.
(1) 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 Reymond.
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
1 + , however small  may be. Here, then, are new
terms intercalated 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 continuum 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.
science and hypothesis 36
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 experiment 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 following 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 secmathematical
magnitude. 37
ond 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 contradictory formulæ
A = B; 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 11 grammes.
This is all that is required to construct the continuum of
several dimensions.
science and hypothesis 38
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
nebulæ, 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 belonging 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 elements, A and B,
mathematical magnitude. 39
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 indistinguishable 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 distinguishable the one from the other (and therefore
forming neither one continuum nor several continuums),
we shall call C a continuum of one dimension. If, on the
contrary, C can only be subdivided 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 dimensions is defined, thanks to the
very simple fact, that two aggregates of sensations may
science and hypothesis 40
be distinguishable 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 AB is equal to or twice
the arc BC. 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 qualitative.
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.
mathematical magnitude. 41
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.
PART II.
SPACE.
CHAPTER III.
NON-EUCLIDEAN GEOMETRIES.
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 à 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:—(1) 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
non-euclidean geometries. 43
line. Although we generally dispense 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 enunciation,
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 Hungarian,
Lobatschewsky and Bolyai, showed irrefutably that
this proof is impossible. They have nearly rid us of inventors
of geometries without a postulate, and ever since
the Académic 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 Geometrie 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 Beltrami 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
science and hypothesis 44
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. The theorems
are very different, however, from those to which we
are accustomed, and at first will be found 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 construct
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 propositions have
no relation to those of Euclid, but they are none the less
non-euclidean geometries. 45
logically interconnected.
Riemann’s Geometry.—Let us imagine to ourselves
a world only peopled with beings of no thickness, 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 reasoning 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,
while 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,
science and hypothesis 46
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 construct 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 Lobatschewsky, and greater than two right angles in
that of Riemann. The number of parallel lines that can
non-euclidean geometries. 47
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 Lobatschewsky. 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 contradiction 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 contradiction? This difficulty
does not exist for Riemann’s geometry, provided
it is limited to two dimensions. As we have seen, the
two-dimensional geometry of Riemann, in fact, does not
differ from spherical geometry, which is only a branch
of ordinary geometry, and is therefore outside 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
consider any figure whatever on a surface. Imagine this
science and hypothesis 48
figure to be traced on a flexible and inextensible 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 thickness 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 curvature 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
Lobatschewsky are connected with Euclidean geometry.
Interpretation of Non-Euclidean Geometries.—Thus
non-euclidean geometries. 49
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.
Plane . . . . . . . . . . . . . . Sphere cutting orthogonally
the fundamental plane.
Line . . . . . . . . . . . . . . . Circle cutting orthogonally the
fundamental plane.
Sphere . . . . . . . . . . . . . Sphere.
Circle . . . . . . . . . . . . . . Circle.
Angle . . . . . . . . . . . . . . Angle.
science and hypothesis 50
Distance between two
points . . . . . . . . . .
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 orthogonally.
Etc. . . . . . . . . . . . . . . . . Etc.
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
two theorems made by the aid of our dictionary would be
contradictory also. But these translations are theorems
non-euclidean geometries. 51
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 interesting to
science and hypothesis 52
try and extract them from the classical proofs.
John Stuart Mill asserted1 that every definition contains
an axiom, because by defining we implicitly 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 re-
1Logic, c. viii., cf. Definitions, §5–6.—[Tr.]
non-euclidean geometries. 53
flections, such as, for example, that of the equality of two
figures. Two 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 evident. 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
à priori intuition would be. Moreover, 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
science and hypothesis 54
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 perpendicular from a point
to a straight line, assume propositions 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 AB, we consider
a straight line AC movable about the point A, and initially
identical with the fixed straight line AB. We then
can make it turn about the point A until it lies in AB
produced. Thus we assume two propositions—first, that
such a rotation is possible, and then that it may continue
non-euclidean geometries. 55
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 remarkable of them. A
real straight line may be perpendicular 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: (1) 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 threescience
and hypothesis 56
dimensional geometries.
Riemann’s Geometries.—However, this result seems
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 incompatible 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 Lobatschewsky,
the difference is proportional to the area of
non-euclidean geometries. 57
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 à 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 convince ourselves of this, let us take a true
synthetic à priori intuition—the following, for instance,
which played an important part in the first chapter:—If
a theorem is true for the number 1, and if it has been
proved that it is true of n + 1, 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 rejecting 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 intuitions
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
science and hypothesis 58
all their experience. 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;
we 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 properties
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 would 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 geometrical axioms are therefore neither synthetic
à priori intuitions nor experimental facts. They
are conventions. Our choice among all possible conventions
is guided by experimental facts; but it remains free,
non-euclidean geometries. 59
and is only limited by the necessity of avoiding every
contradiction, and thus it is that postulates 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. One geometry cannot be more
true than another; it can only be more convenient. Now,
Euclidean geometry is, and will remain, the most convenient:
1st, 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 properties of
natural solids, those bodies which we can compare and
measure by means of our senses.
CHAPTER IV.
SPACE AND GEOMETRY.
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 suitablychosen
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 men who think in this
space and geometry. 61
way, the preceding statement might well appear extraordinary;
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 essential:—
1st, 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
space.
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 rôle.
The yellow spot can in no way be regarded as identical
science and hypothesis 62
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 continuity 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 distance, and
therefore to perceive a third dimension. But every one
knows that this perception of the 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 rôle 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
space and geometry. 63
know three of them; or, in mathematical language, they
will be functions 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 convergence of the eyes.
No doubt these two indications 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
A0 and B0 which accompany them respectively
will also be indistinguishable. But that is, so to
speak, an experimental fact. Nothing prevents us à 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
science and hypothesis 64
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 constitutes 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 dimensions
as we have muscles. I know that it is said that if
space and geometry. 65
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
geometrical 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 that 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 correspond,
according to the position of the limbs, to very different
movements of direction. Moreover, 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
science and hypothesis 66
according to other laws.
Characteristics of Representative Space.—Thus representative
space in its triple form—visual, tactile, and
motor—differs essentially from geometrical 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 external objects in
geometrical space? Our representations are only the reproduction
of our sensations; they cannot therefore be
arranged in the same framework—that is to say, in representative
space. It is also just as impossible for us
to represent 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 geometrical space, an
image deformed by a kind of perspective, and we can only
represent to ourselves objects by making them obey the
laws of this perspective. Thus we do not represent to ourselves
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 “lospace
and geometry. 67
calise” such an object in such a point of space, what does
it mean? It simply means that we represent to ourselves
the movements 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 ourselves 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 space.
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 our impressions are subject to change; but
among the changes that we ascertain, we are very soon
science and hypothesis 68
led to make a distinction. Sometimes we say that the
objects, 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 aggregate of
impressions by making movements which would confront
us with the movable object in the same relative situation.
We thus correct the modification which was produced,
and we re-establish the initial state by an inverse
modification. 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
space and geometry. 69
from the aggregate of impressions A to the aggregate B
in two different ways. First, involuntarily and without
experiencing 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 whatever.
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
science and hypothesis 70
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 different 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 displaced,
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 à priori if compensation is possible. But experiment
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 position.
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
space and geometry. 71
objects, whose form is variable, 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 experiments,
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 “deformations” 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 position.
If, then, there were no solid bodies in nature there
would be no geometry.
science and hypothesis 72
Another remark deserves a moment’s attention. Suppose
a solid body to occupy successively the positions
 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
, where it gives us the aggregate of impressions A0
to the position , where it gives the aggregate of impressions
B0. In general, the aggregate A will have nothing in
common with the aggregate A0, nor will the aggregate B
have anything in common with the aggregate B0. The
transition from the aggregate A to the aggregate B, and
that of the aggregate A0 to the aggregate B0, are therefore
two changes which in themselves have in general nothing
in common. Yet we 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, constitutes
the sole connection between two phenomena which
otherwise we should never have dreamed of connecting.
On the other hand, our body, thanks to the number
of its articulations and muscles, may have a multitude
space and geometry. 73
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 body.
To sum up:—
1. In the first place, we distinguish two categories of
phenomena:—The first involuntary, unaccompanied 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 displacements. The laws
of these phenomena are the object of geometry.
science and hypothesis 74
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 , so that we are brought
back to the aggregate A. Suppose now that another external
change 0 brings us again from the aggregate A
to the aggregate B. Experiment then shows us that this
change 0, like the change , may be corrected by a voluntary
correlative movement 0, and that this movement 0
corresponds to the same muscular sensations as the movement
 which corrected .
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 we
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
apprehended. To be complete, to the law of homogeneity
must be added a multitude of other laws, into the details
space and geometry. 75
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 representations
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 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
science and hypothesis 76
sphere, and r the distance of the point considered from
the centre, the absolute temperature will be proportional
to R2 􀀀 r2. 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
circumference of the sphere. Let us observe, in the first
place, that although from the point of view of our ordinary
geometry this world is finite, to its inhabitants
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 these imaginary beings it will be the study of
the laws of motion of solids deformed by the differences
of temperature alluded to.
No doubt, in our world, natural solids also experience
space and geometry. 77
variations of form and volume due to differences of temperature.
But in laying the foundations of geometry we
neglect these variations; 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 R2 􀀀 r2. 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 conformity with the law of temperature
assumed above. To use an abbreviation, we shall
science and hypothesis 78
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 impressions will also
be unchanged. These imaginary beings will therefore
be led to classify the phenomena they observe, and to
space and geometry. 79
distinguish among them the “changes of position,” which
may be corrected by a voluntary correlative movement,
just as we do.
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 displacements,” and this will be non-Euclidean
geometry. So that beings like ourselves, educated in such
a world, will not have the same geometry as ours.
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 movements 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 perspective
to another is often accompanied by muscular
sensations. If the transition from the perspective A to
science and hypothesis 80
the perspective B, and that of the perspective A0 to the
perspective B0 are accompanied 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 combined, 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-dimensional 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 dimensions. 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 understood
space and geometry. 81
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 imagining 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 who has a retina of two
dimensions, and who may be displaced 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
rôle 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 approximative 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
science and hypothesis 82
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 preexists
in our minds, at least potentially. It is imposed on
us not as a form of our sensitiveness, 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 change.
CHAPTER V.
EXPERIMENT AND GEOMETRY.
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 Lobatschewsky’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 three geometries.
But what we call a straight line in astronomy is simply
science and hypothesis 84
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 experiments.
4. Can we maintain that certain phenomena which
are possible in Euclidean space would be impossible in
non-Euclidean space, so that experiment 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 following, 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 contradict 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
experiment and geometry. 85
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 possesses 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 we
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 property 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 property 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 ascertain by experiment if
it belongs to any particular concrete object? Distances
must be measured, and how shall we know that any conscience
and hypothesis 86
crete magnitude 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, that is not true, and
if we are not convinced by these considerations, I challenge
any one to give me a concrete experiment which
can be interpreted in the Euclidean system, and which
cannot be interpreted 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 violation of the principle of suffiexperiment
and geometry. 87
cient 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 position 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 position
and orientation of the system. In other words, the
state of the bodies and their mutual distances at any moment
will solely depend on the state of the same bodies
and on their mutual distances at the initial moment, but
will 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, rescience
and hypothesis 88
quires 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
experiment and geometry. 89
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 depend 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 position and orientation are
changing. For the mind to be fully satisfied, the law of
relativity would have to be enunciated as follows:—The
state of bodies and their mutual distances at any given
science and hypothesis 90
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 position 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 constantly
covered with a thick curtain of clouds, so that he
could never see the other stars. On that planet he would
live as if it were isolated in space. But he would 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
experiment and geometry. 91
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. However
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
meaning.
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
science and hypothesis 92
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, will 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 properties of bodies? I
assume that it is a question of the relations of the bodies
to space. These properties therefore are not reached by
experiments 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 relaexperiment
and geometry. 93
tions 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   
.
I now suppose that we find that we can bring into contact

 with ago; by that I mean  with a, and at the
same time  with g, and 
 with o. Then we can successively
bring into contact 
 with bgo, cgo, dgo, ego,
fgo, then with aho, bho, cho, dho, eho, fho; and then

 successively with ab, bc, 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 experiment 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
science and hypothesis 94
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 
 were an invariable solid
of our ordinary geometry in the shape of a right-angled
triangle, and if the points abcdefgh were the vertices of
a polyhedron formed of two regular hexagonal pyramids
of our ordinary geometry having abcdef 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 
 successively
to ago, bgo, cgo, dgo, ego, fgo, aho, bho, cho, dho, eho,
fho, and then that we can apply  (and no longer 
)
successively to ab, bc, cd, de, ef, and fa. These are observations
that could be made if non-Euclidean geometry
were true. If the bodies 
, 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 show, if we carried them out,
that the bodies in question do not move according to the
experiment and geometry. 95
Euclidean group. And so, without 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 cannot 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
science and hypothesis 96
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 negligible, 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 o0a0b0c0d0e0f0g0h0, and two triangles

 and 00
0. The first double pyramid would
be rectilinear, and the second curvilinear. The triangle

 would consist of undilatable matter, and the
other of very dilatable matter. We might therefore make
our first observations with the double pyramid o0a0h0 and
the triangle 00
0.
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.
supplement.
8. To round the matter off, I ought to speak of a very
delicate question, which will require considerable development;
but I shall confine myself to summing up what I
have written in the Revue de Métaphysique et de Morale
and in the Monist. When we say that space has three
experiment and geometry. 97
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,
however, that we shall often look upon two series S and S0
as defining the same attitude B (since the initial and final
attitudes A and B remaining the same, the intermediary
attitudes of the corresponding 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 continuum of six dimenscience
and hypothesis 98
sions; 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 à priori. 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.
experiment and geometry. 99
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 contact 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
corresponding 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, anscience
and hypothesis 100
other finger, would the results be the same? That is by
no means à priori evident. But, as we have seen, experiment
has shown us that all our criteria are in agreement,
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 displacements
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 neighbouring 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 concerned. Which shall we choose to form a kind of
standard by which to compare natural phenomena? 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 rôle ends.
PART III.
FORCE.
CHAPTER VI.
THE CLASSICAL MECHANICS.
The English teach mechanics as an experimental science;
on the Continent it is taught always more or less as a deductive
and à 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 approximate 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 experiment,
what is mathematical reasoning, what is convention,
and what is hypothesis. This is not all.
1. There is no absolute space, and we only conceive of
relative motion; and yet in most cases mechanical facts
science and hypothesis 102
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 convention.
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 explained this in an article entitled “Mesure
du Temps.”1
4. Finally, is not our Euclidean geometry in itself only
a kind of convention of language? Mechanical facts might
be enunciated with reference 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
1Revue de Métaphysique et de Morale, t. vi., pp. 1–13, January,
1898.
the classical mechanics. 103
mechanics in a language independent of all these 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
Leçons de Mécanique 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 enunciation.
As far as we are concerned, I shall ignore all
these difficulties; not because I disregard them, far from
it; but because they have received 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 à 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
science and hypothesis 104
change, or that the curvature of its path cannot change,
without the agency of an external cause? Is, then, the
principle of inertia, which is not an à priori truth, an
experimental fact? Have there ever been experiments 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 consequences. 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
the classical mechanics. 105
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 à 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
science and hypothesis 106
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
mentioned.
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 perturbing 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 mechanics.
the classical mechanics. 107
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 hypothesis.
Has this generalised law of inertia been verified 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 replaced 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 which 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 0:1 and the other 0:2. The probascience
and hypothesis 108
bility 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 experiment will falsify the
law in some domain of physics? An experimental law is
always subject to revision; we may always expect to see
it replaced 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.
the classical mechanics. 109
Yet this is not all. In Astronomy we see 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 conditions, 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 we 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 3n co-ordinates satisfy
a system of 3n differential equations of the fourth
order (and not of the second, as required by the law of
inertia). We know that by introducing 3n variable auxiliaries,
a system of 3n equations of the fourth order may
be reduced to a system of 6n equations of the second order.
If, then, we suppose that the 3n auxiliary variables
represent the co-ordinates of n invisible molecules, the
science and hypothesis 110
result is again conformable 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 experiment.
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 mentioned 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
the classical mechanics. 111
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 what 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 two 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 impossible to tell how two forces which are not acting
in exactly opposite directions would behave 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 dynamometer or with a balance. Two
forces, F and F0, which I suppose, for simplicity, to be
acting vertically upwards, are respectively applied to two
bodies, C and C0. I attach a body weighing P first to C
and then to C0; if there is equilibrium in both cases I
science and hypothesis 112
conclude that the two forces F and F0 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 magnitude
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.
the classical mechanics. 113
Thus we are compelled to bring into our definition 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 but 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—are
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 product 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,
science and hypothesis 114
A and B, act on each other; the acceleration 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 dependent on their distance
apart; if, in a word, we admit the hypothesis of central
the classical mechanics. 115
forces.
We know that to determine the masses of the heavenly
bodies we adopt quite a different principle. 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 m0 their masses, k a constant, then their attraction
will be kmm0=r2. 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 inversely proportional to the
square of the distance, without being proportional to the
product of the masses, that it is equal to f=r2 but without
having f = kmm0. 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 composcience
and hypothesis 116
nent 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 principle 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 classical mechanics. 117
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 mechanics would be in
contradiction neither with experiment nor with the general
principles of dynamics (the principle of inertia, proportionality
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
science and hypothesis 118
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 definitions. 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; what 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 with 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
the classical mechanics. 119
more accurate experiment. What, in fact, would a more
accurate experiment teach us? It would 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,
science and hypothesis 120
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 lb. 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
reduced 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 rôle
in 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 character.
The Thread School.—M. Andrade, in his Leçons de
the classical mechanics. 121
Mécanique physique, has modernised anthropomorphic
mechanics. To the school of mechanics with which Kirchoff
is identified, he opposes a school which is quaintly
called the “Thread School.”
This school tries to reduce everything to the consideration
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 magnitude 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 ,
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 , and the acceleration
of B is noted. The experiment is then renewed
with both A and B until the increment of length is .
The four accelerations observed should be proportional.
science and hypothesis 122
Here we have an experimental verification of the law of
acceleration 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
consequence, our definition will be in default; no sense
the classical mechanics. 123
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 acceleration.
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 verifications 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
science and hypothesis 124
a naïve anthropomorphism to the present conception of
science.
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 convention.
Are the laws of acceleration and of the composition
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.
CHAPTER VII.
RELATIVE AND ABSOLUTE MOTION.
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 experiment 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 conclude 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 B. ès Sc. It is clear
that the attempt has failed. The obstacle which prescience
and hypothesis 126
vented 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 with 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 movable axes
to which the relative motion is referred move uniformly
in a straight line; or, if it is preferred, 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
principle 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 acceleration 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
relative and absolute motion. 127
be deduced from experiment or from à 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 coordinates,
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 important
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 à 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
science and hypothesis 128
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 paradoxical 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, conclude 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 no absolute space, can a thing turn without
turning 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 excused.
relative and absolute motion. 129
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 contradiction.
In the theory of relative motion we observe,
besides real forces, two 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
science and hypothesis 130
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. Centrifugal force increases indefinitely with distance.
Already this difficulty would seem to them sufficiently 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 exercise 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 accumurelative
and absolute motion. 131
lating complications until the long-expected 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 affirmation: “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
contradiction; or, in other words, these two propositions,
“the earth turns round,” and, “it is more 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 surprising that among all the hypotheses,
or rather all the conventions, that can be made on this
science and hypothesis 132
subject there is one which is more convenient than the
rest? But if we have admitted it without difficulty 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 determined
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 equations 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 derivatives
with respect to time—that would not be sufficient to derelative
and absolute motion. 133
termine 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 areaconstant.
But here we 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 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 exscience
and hypothesis 134
ponent 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 law.
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 distinction; 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 accustomed 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 constant.
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 prerelative
and absolute motion. 135
vent 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, distances
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
would 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 consequences 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
science and hypothesis 136
system. But our conclusions 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 convenient solution for the geometer. But it
is not the most satisfactory for the philosopher, because
relative and absolute motion. 137
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 containing
my reflections on the principle of inertia. But as a matter
of fact the difficulty is artificial. Provided that the
future indications of our instruments 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.
CHAPTER VIII.
ENERGY AND THERMO-DYNAMICS.
Energetics.—The difficulties raised by the classical 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. Helmholtz gave it its definite form.
We begin by defining 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 t0, and at B at the time t1, 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 t0 and t1 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
energy and thermo-dynamics. 139
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 impossible
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 distances 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 independent of their velocities; the
second is proportional to the squares of these velocities.
This decomposition can only take place in one way. The
science and hypothesis 140
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 (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 property. 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 reapenergy
and thermo-dynamics. 141
pear in the more complicated cases if the forces, instead
of depending solely on the distances, depend also on the
velocities. For example, Weber supposes the mutual action
of two electric molecules to depend not only on their
distance but on their velocity and on their acceleration.
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 distinguish
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 conservation 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
science and hypothesis 142
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 electrostatic
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 selection of the
terms which should form part of T, and U, and Q, and
of separating the three parts of the energy. If T+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
energy and thermo-dynamics. 143
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 experiment 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 reversible 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
science and hypothesis 144
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 principle
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 causes.
Thermo-dynamics.—The rôle of the two fundamental
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 foundations 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,
energy and thermo-dynamics. 145
àpropos 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 experiments 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 circumstances is changed.
science and hypothesis 146
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 altogether 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
energy and thermo-dynamics. 147
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
deduced 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 unexpected order, and form a
harmonious whole. We cannot believe that this unexpected
harmony 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 proportion 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
science and hypothesis 148
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 universe is determined
by an extremely large number n of parameters, which I
shall call x1, x2, x3; : : : ; ; xn. 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 calculate 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􀀀1 integrals, and therefore
there are n􀀀1 functions of x1, x2, x3; : : : ; xn, 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
energy and thermo-dynamics. 149
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 n􀀀p 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 we 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 determinist 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 x which define the state of
science and hypothesis 150
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 we 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
energy and thermo-dynamics. 151
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 lost.
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.
science and hypothesis 152
General Conclusions on Part III.—The principles 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 convention
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. We admit it because certain experiments
have shown us that it will be convenient, 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 comenergy
and thermo-dynamics. 153
plete, the rôle of experiment seems the same. We shall
therefore 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 experiments 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
science and hypothesis 154
are the natural and direct generalisations of experimental
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 conventional
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 geometry.
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.
energy and thermo-dynamics. 155
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 paradoxical 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 experimental 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.
PART IV.
NATURE.
CHAPTER IX.
HYPOTHESES IN PHYSICS.
The Rôle 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 everything, 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 recollection 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 naïvely. Descartes used to commiserate the Ionihypotheses
in physics. 157
ans. 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 something 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.
1V. Past and Present, end of Chapter I., Book II.—[Tr.]
science and hypothesis 158
The latter accumulate in vain. Whether there are a hundred
or a thousand, one single piece of work by a real
master—by a Pasteur, for example—will be sufficient to
sweep them into oblivion. Bacon would have thoroughly
understood that, for he invented the phrase experimentum
crucis; but Carlyle would not have understood 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 an isolated
fact. It is that which enables us to predict, and to
generalise. Without generalisation, 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 continhypotheses
in physics. 159
uous 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 extraordinary 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
science and hypothesis 160
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 predictions
having the highest possible degree of probability.
The problem is, so to speak, to increase the output of
hypotheses in physics. 161
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 rôle 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 of 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 react one upon the other; they
would mutually ignore each other, and we in particular
science and hypothesis 162
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 interpolation. 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 behypotheses
in physics. 163
cause 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 interpretation? Not because it is absurd, but because
it is uselessly complicated. We 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 produced two
science and hypothesis 164
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 combination 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 proportionality. 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 inhypotheses
in physics. 165
finitely 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 foundation 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 contains 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
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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 therefore
hypotheses in physics. 167
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 inadmissible rôle to chance. However, there
is a difference. If the simplicity were real and profound
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.
Rôle of Hypothesis.—Every generalisation is a hypothesis.
Hypothesis therefore plays a necessary rôle,
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 jusscience
and hypothesis 168
tified. 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 extraordinary
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
hypotheses in physics. 169
which is its characteristic, 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 hypotheses, 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?
We must also take care to distinguish between the
different kinds of hypotheses. First of all, there are those
which 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,
science and hypothesis 170
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 dangerous provided
their characters are not misunderstood. They may
be useful, either as artifices for calculation, or to assist
hypotheses in physics. 171
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 experiment.
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 numerous.
Origin of Mathematical Physics.—Let us go further
and study more closely the conditions which have assisted
the development of mathematical 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 elementary
phenomena, and that in three different ways.
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
science and hypothesis 172
Newton.
Next, we try to decompose the phenomena in space.
What experiment gives us is a confused aggregate of facts
spread over a scene of considerable extent. We must try
to deduce the elementary phenomenon, which will still
be localised in a very small region of space.
A few examples perhaps will make my meaning
clearer. If we wished to study in all its complexity the
distribution of temperature in a cooling solid, we could
never do so. This is simply because, if we only reflect
that a point in the solid can directly impart some of
its heat to a neighbouring 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 phenomenon 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 impossible. 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
hypotheses in physics. 173
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 valuable, 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
monochromatic components. When we have discovered
in which direction to seek for the elementary phenomscience
and hypothesis 174
ena, 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 towards its neighbour—we need not inquire
according 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 neighbouring 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 play.
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 disguised a very complex
mechanism. Evidently the best means of reaching
hypotheses in physics. 175
the elementary phenomenon would be experiment. It
would be necessary by experimental artifices to dissociate
the complex system which nature offers for our
investigations 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 sufficient, and sometimes the mind must
run ahead of experiment. I shall only give one example
which has always struck me rather forcibly. If I decompose
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 monochromatic give us a very fine ray,
but one 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
monochromatic 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
science and hypothesis 176
of polarisation, and that we try to obtain interference. If
the light were rigorously monochromatic, there would be
interference; 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 elementary fact enables us to state the
problem in the form of an equation. It only remains to
deduce from it by combination the observable and verifiable
complex fact. That is what we call integration, and it
is the province of the mathematician. 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
hypotheses in physics. 177
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, mathematics 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 contrary
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 generalisation.
CHAPTER X.
THE THEORIES OF MODERN PHYSICS.
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 movements 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 equathe
theories of modern physics. 179
tions 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
science and hypothesis 180
phenomena an intimate relationship which corresponds
to a profound reality; that this relationship, this similarity,
or rather this parallelism, is continued in the details;
that it is a consequence of more general principles such
as that of the conservation 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
true; not merely because they express a true relation—
that between absorption 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 obthe
theories of modern physics. 181
jections, 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
contradictions 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.
science and hypothesis 182
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 hypotheses.
These considerations explain to us why certain theories,
that were thought to be abandoned and definitively
condemned by experiment, are suddenly revived from
the theories of modern physics. 183
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
supported 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 unexpected 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,
science and hypothesis 184
other inexact relations, the débris 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 branches.
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 rôle 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 conthe
theories of modern physics. 185
stant. 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 relationship;
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 would be satisfied
if they could account for all phenomena by the
motion of molecules attracting one another according
science and hypothesis 186
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., àpropos
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 Königs,
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 demonstrated 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
the theories of modern physics. 187
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 rôle 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 geometrical 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
science and hypothesis 188
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 perceived. 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 photographic plate experiences the
consequences of a phenomenon of which the incandescent
mass of a star was the scene several years before. Now, in
ordinary mechanics, the state of the system under consideration
depends only on its state at the moment immethe
theories of modern physics. 189
diately 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 preceding,
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 reaction
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
science and hypothesis 190
counterbalanced by the reaction 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 phenomena 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
the theories of modern physics. 191
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 world.
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 displacements 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 rôle? 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
science and hypothesis 192
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 absolute.
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 continually
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
the theories of modern physics. 193
this à 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 compelled 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 completed.
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 slightscience
and hypothesis 194
est idea. As to the possibility of the inclusion, 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 annexation 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 construction. That it still possesses a
serious fault I have shown above. It is in contradiction
the theories of modern physics. 195
with Newton’s law that action and reaction 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 reaction 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 dispersion 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, Macscience
and hypothesis 196
Cullagh’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 reaction are equal and
opposite. According to Larmor we know the movements
of the ether, and we can prove that the compensation
does not take place.
If Larmor has failed, as in my opinion he has, does
it necessarily follow that a mechanical explanation 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
the theories of modern physics. 197
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 thermodynamics
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 explored, and it
has even attacked chemistry itself. The same laws hold
science and hypothesis 198
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
the theories of modern physics. 199
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 Xrays,
uranium and radium rays; in fact, a whole world
1Clerk-Maxwell imagined some supernatural agency at work,
sorting molecules in a gas of uniform temperature into (a) those
possessing kinetic energy above the average, (b) those possessing
kinetic energy below the average.—[Tr.]
science and hypothesis 200
of which none had suspected the existence. How many
unexpected 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
the theories of modern physics. 201
can say of it is but approximate, and our formulæ are
constantly requiring new terms.
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. Subsequently, 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
science and hypothesis 202
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 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,
the theories of modern physics. 203
osmosis, and the movements of ions.
From this cursory exposition what can we conclude?
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.
CHAPTER XI.
THE CALCULUS OF PROBABILITIES.
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 examining 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 prediction 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
the calculus of probabilities. 205
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 therefrom no
small advantage. How can we explain this apparent contradiction?
Has probability been defined? Can it even be
defined? And if it cannot, 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  6 = 36. The number of favourable cases
is 11; the probability is 11
36
. That is the correct solution.
But why cannot we just as well proceed as follows?—The
science and hypothesis 206
points which turn up on the two dice form 6  7
2
= 21
different combinations. Among these combinations, six
are favourable; the probability is 6
21
. 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
the calculus of probabilities. 207
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 1
2 , and
with the other 1
3 . 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 commonsense,
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
science and hypothesis 208
very improbable. From this point of view all the sciences
would only be unconscious applications of the calculus
of probabilities. 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 probabilities 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 observation,
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 which 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 interpolation 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
the calculus of probabilities. 209
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 disappear.
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 probability. 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
science and hypothesis 210
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 scepticism 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 probability 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
the calculus of probabilities. 211
ask the probability that a function will satisfy a given
condition. 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, when 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 mathematics we may set
ourselves problems in probability. 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 1
10 . 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 and
this initial state, we have a simple mathematical probscience
and hypothesis 212
lem 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 distribution 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 distribution. In the kinetic theory of gases we assume
that the gaseous molecules follow rectilinear 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 calculus of probabilities. 213
the most interesting of all from their scientific applications.
I play at écarté with a gentleman whom I know
to be perfectly honest. What is the chance that he turns
up the king? It is 1
8 . 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 experimental 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 practically 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 probability.
II. Probability in Mathematics.—The impossibility
of squaring the circle was shown in 1885, but before
that date all geometers considered this impossibility as
so “probable” that the Académie des Sciences rejected
science and hypothesis 214
without examination the, alas! too numerous memoirs on
this subject that a few unhappy madmen sent in every
year. Was the Académie 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 Académie 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 probability that an
unknown scientist should have found out what has been
vainly sought for so long, with the probability that there
is one madman 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
equation, 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
the calculus of probabilities. 215
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 without any hesitation
that the probability is 1
2 , 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 +1 if the third decimal of the corresponding
logarithm is even, and 􀀀1 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
science and hypothesis 216
an article that I published in the Revue générale des Sciences,
April 15th, 1899. The only point to which I wish
to draw attention is the following. In this calculation 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
whatever, 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 inequalities, just as a skilled calculator
before finishing his multiplication takes into account
what it ought to come to approximately. And besides,
since what I call my intuition was only an incomplete
summary of a piece of true reasoning, it is clear that
observation has confirmed my predictions, and that the
objective and subjective probabilities 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 nu? This problem
the calculus of probabilities. 217
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 (a) da; that it is
therefore proportional to the infinitely small interval da,
and is equal to this multiplied by a function (a), 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, I
may without loss of generality assume that u lies between
0 and 2, and I shall thus be led to suppose that (a) is
a periodic function whose period is 2. 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
2MK
nK ;
MK being the maximum value of the Kth derivative
of (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 1
nK+1 .
The mean value of sin nu when n is very large is therefore
zero. To define this value I required a convention,
but the result remains the same whatever that convention
may be. I have imposed upon myself but slight restricscience
and hypothesis 218
tions when I assumed that the function (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 rôle of what philosophers call the principle of sufficient
reason, and on the other hand of the importance of
the fact that certain properties 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
the calculus of probabilities. 219
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 t will be at + b. To say that the
present distribution 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 representative points to be found on a certain
portion of the plane is proportional to the quantity
science and hypothesis 220
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 representative 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 proportional 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 impossible, 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 suppose that this function
is continuous. That is sufficient, as we shall see, to
the calculus of probabilities. 221
enable us to reach our conclusion.
What is at the instant t the probable distribution 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 imaginary
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
science and hypothesis 222
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 continuous; 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 0,
but that it could not lie between 0 and 1?
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 supposititious 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
1
nXsin(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
the calculus of probabilities. 223
representative 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 =

2 􀀀 at, the longitude of
all the planets at the time t would be 
2
, and the mean
value in question would be evidently unity. For this to
be the case at the time 0, 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 improbable (and even if
it were realised, the distribution would not be uniform at
the present time—for example, on the 1st 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 anything on the subject of
the probability of this or that present distribution. Once
science and hypothesis 224
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 et Noir.—The questions raised by games of
chance, such as roulette, are, fundamentally, quite analogous
to those we have just treated. For example, a wheel
is divided into a large number of 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 1
2 . The needle describes
an angle , including several complete revolutions.
I do not know what is the probability that the ball is
spun with such a force that this angle should lie between
 and +d, but I can make a convention. I can suppose
that this probability is () d. As for the function (),
I can choose it in an entirely arbitrary manner. I have
the calculus of probabilities. 225
nothing to guide me in my choice, but I am naturally induced
to suppose the function to be continuous. Let  be
a length (measured on the circumference of the circle of
radius unity) of each red and black compartment. We
have to calculate the integral of () d, 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 comprising two consecutive red
and black compartments. Let M and m be the maximum
and minimum values of the function () in this
interval. The integral extended to the red compartments
will be smaller than PM; extended to the black it will
be greater than Pm. The difference will therefore be
smaller than P(M 􀀀 m). But if the function  is supposed
continuous, and if on the other hand the interval 
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 1
2 . We see that
without knowing anything of the function  we must act
as if the probability were 1
2 . 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
science and hypothesis 226
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 1
2 . 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
the calculus of probabilities. 227
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 à priori to reject discontinuous functions, for example,
or certain absurd conventions. We shall again find something
analogous to this when we deal with the probability
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 à 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 à 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
écarté mentioned before. My adversary deals for the first
time and turns up a king. What is the probability that
he is a sharper? The formulæ ordinarily taught give 8
9 ,
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
science and hypothesis 228
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 à priori probability was unjustified, and that is why
the conclusion of the à posteriori probability led me into
an inadmissible result. The importance of this preliminary
convention is obvious. I shall even add that if none
were made, the problem of the à 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 represent 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
the calculus of probabilities. 229
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 two 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 corresponding point from
that curve. But the problem has no meaning if before
the observations I had an à 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 sacrificed
to regularity.
Why, then, do I draw a curve without sinuosities?
Because I consider à priori a law represented by a continuous
function (or function the derivatives of which to
science and hypothesis 230
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 impossible.
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 à posteriori
value of each error, and therefore the probable value
the calculus of probabilities. 231
of the quantity to be measured. But, as I have just explained,
we cannot undertake this calculation unless we
admit à 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 probability
science and hypothesis 232
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 undulations. 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 worth
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? 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
the calculus of probabilities. 233
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, however, 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 rescience
and hypothesis 234
gret 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 convention
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 independent of the hypothesis
made at the outset, provided only that this hypothesis
satisfies the condition of continuity.
CHAPTER XII.1
OPTICS AND ELECTRICITY.
Fresnel’s 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 explanation of phenomena. After all, have we any
other reason for believing in the existence of material ob-
1This chapter is mainly taken from the prefaces of two of my
books—Théorie Mathématique de la lumière (Paris: Naud, 1889),
and Électricité et Optique (Paris: Naud, 1901).
science and hypothesis 236
jects? 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 rôle. 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
explains why most of the conclusions of Fresnel remain
unchanged when we adopt the electro-magnetic theory of
light.
optics and electricity. 237
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 electricity.
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
precision 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
science and hypothesis 238
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 mechanics.
A mind accustomed to admire such models is not easily
satisfied with a theory. Not only will it not tolerate
the least appearance of contradiction, 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
mathematical 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 matter.
Then only will he be thoroughly satisfied, and he will
optics and electricity. 239
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 Frenchman 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
preparing 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 phenomena.
In particular it is not easy if we take as our startingpoint
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.
science and hypothesis 240
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 electro-static attractions are explained
by the pressures and tensions of the dielectric medium.
This chapter might be suppressed 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 what 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 phenomena?
optics and electricity. 241
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 explanation of things, may, in fact, be very
useful instruments 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 importance 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
science and hypothesis 242
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 m, 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 action.
The first of these two principles teaches us that the
total energy is constant, and may be divided into two
parts:—
(1) 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.
optics and electricity. 243
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 t0 to the final position occupied at
the instant t1, the system must describe such a path that
in the interval of time between the instant t0 and t1, 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 one 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;
science and hypothesis 244
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 final 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.
To form these equations we need not know the relations
which connect the parameters q with the co-
1We 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.
optics and electricity. 245
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
explanation 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
science and hypothesis 246
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
Électricité et Optique 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 hypothetical molecules, some
will be our parameters q, 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.
optics and electricity. 247
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 field 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
intensity of the currents as derivatives of other parameters
q—under these conditions, Maxwell has recognised
that electric phenomena satisfy 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
science and hypothesis 248
mechanical explanation, it allows of an unlimited number
of others, which will equally take into account all the
particulars revealed by experiment. 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 experimentum
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 explained,
thanks to the properties of the Lagrange equations.
It is easy now to understand Maxwell’s fundamental
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
experimental laws.
How shall we choose from all the possible explanations
one in which the help of experiment will be wantoptics
and electricity. 249
ing? 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
metaphysicians. That day has not yet come; man does
not so easily resign himself to remaining for ever ignorant
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
science and hypothesis 250
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.
CHAPTER XIII.
ELECTRO-DYNAMICS.
The history of electro-dynamics is very instructive from
our point of view. The title of Ampère’s immortal work
is, Théorie des phénomènes electro-dynamiques, uniquement
fondée sur expérience. 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 Ampère’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 see.
I. Ampère’s Theory.—In Ampère’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. According
science and hypothesis 252
to the ideas of Ampère’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 Ampère 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
resistance 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
electro-dynamics. 253
is considered to be perfectly analogous to the conduction
current, the circuit BNAMB is closed; if on the contrary
the convection 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 Ampère’s disposal
we may almost say it was impossible.
To sum up, Ampère could conceive of the existence
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 displacements
of the moving part may be studied under the action of
another closed current. On the other hand, Ampère had
no means of studying the action of an open current either
science and hypothesis 254
on a closed or on another open current.
1. The Case of Closed Currents.—In the case of the
mutual action of two closed currents, experiment revealed
to Ampère 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 electrodynamical
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
C0 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.
electro-dynamics. 255
(b) 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 C0 is displaced, the amount of the
work done by the electro-dynamic action of C on C0 will
be equal to the increment of “flow of magnetic force”
which passes through the circuit.
2. Action of a Closed Current on a Portion of Current.—
Ampère 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
movable and the other fixed. The movable part was, for
instance, a movable wire , the ends  and  of which
could slide along a fixed wire. In one of the positions of
the movable wire the end  rested on the point A, and
the end  on the point B of the fixed wire. The current
ran from  to —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  and  were respectively at A0 and B0
science and hypothesis 256
on the fixed wire. The current ran from  to —i.e.,
from A0 to B0 on the movable wire, and returned from B0
to B, and then from B to A, and then from A to A0—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 displaced just as if it were acted
on by a force. Ampère admits that the force, apparently
acting on the movable part AB, representing the action
of C on the portion  of the current, remains the same
whether an open current runs through , stopping at
 and , or whether a closed current runs first to  and
then returns to  through the fixed portion of the circuit.
This hypothesis seemed natural enough, and Ampère 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 Ampère,
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 proportional to that component
of the magnetic force which is normal to the element.
electro-dynamics. 257
(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
contact 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 C0 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 C0 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
science and hypothesis 258
passage from the fixed to the movable part, or vice versâ,
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 contact 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.
Ampère admits that the action of the circuit on the
movable part of C0 is the same as if the fixed part of C0
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 versâ, 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 enunciated, and to
which, as I said above, Helmholtz declined to subscribe.
electro-dynamics. 259
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. Ampère falls back on hypothesis.
He assumes: (1) 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 Ampère
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 defined
this force in three different ways: (1) 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.
science and hypothesis 260
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 disappeared.
Let us see in what this unity consists. Two systems
which exercise the same action on a magnetic 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 Ampère it would not be true if the systems
electro-dynamics. 261
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 electrodynamical
induction followed not long after the immortal
work of Ampère. 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 Ampère. 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
Ampère’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 practiscience
and hypothesis 262
cal 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 circuit 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 Ampère, 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 Ampère’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 Ampère—namely, that the mutual
electro-dynamics. 263
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 celebrated polemic
between Bertrand and Helmholtz. Helmholtz replaces
Ampère’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 Ampère, 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 Ampère
supposed, the force which 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 C0, 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  is not isolated,
but is part of a closed circuit. When it passes from AB
to A0B0, the total electro-dynamic potential varies for two
science and hypothesis 264
reasons. First, it has a slight increment because the potential
of A0B0 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
AA0 and B0B 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,  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 wire with the magnet
were suppressed, and an open current were to run along
the wire, the wire would still have a movement of continuous
rotation. 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
electro-dynamics. 265
is zero according to experiment and according to the two
theories. Its action on an open current would be zero according
to Ampère, 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 meaning,
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.—Helmholtz’s
theory is an advance on that of Ampère; it is necessary,
science and hypothesis 266
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 conelectro-
dynamics. 267
ductors bearing positive and negative charges are placed
in connection 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 displacement which close this current
of conduction. We know that Maxwell’s theory leads
to the explanation of optical phenomena which would
be due to extremely rapid electrical oscillations. At that
period such a conception was only a daring hypothesis
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 fundamental
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
science and hypothesis 268
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 conduction in one part of the circuit and by convection
in the other part. The question might be regarded as
solved for open currents of the first kind; they were closed
by currents of displacement. 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 experimental 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
electro-dynamics. 269
seem to triumph, over these difficulties. A disc received
a strong electro-static 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 Baltimore.
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 cathode rays; Crookes
attributed these rays to very subtle matter charged with
science and hypothesis 270
negative electricity and moving with very high velocity.
He looked upon them, in other words, as currents of convection.
Now, these cathode rays are deviated by the
magnet. In virtue of the principle of action and reaction,
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 law.
VI. Lorentz’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
electro-dynamics. 271
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 explanation 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 phenomena 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. Crémieu, M. Lippman has
presented 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
science and hypothesis 272
velocity with respect to the ether, so that the principle of
relativity is safe.” Whatever there may be in these objections,
the edifice of electro-dynamics seemed, at any rate
in its broad lines, definitively constructed. Everything
was presented under the most satisfactory aspect. The
theories of Ampère and Helmholtz, which were made for
the open currents that no longer existed, seem to have
no more than purely historic interest, and the inextricable
complications to which these theories led have been
almost forgotten. This quiescence has been recently disturbed
by the experiments of M. Crémieu, 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 which it is placed before the public.
THE END.
THE WALTER SCOTT PUBLISHING CO., LIMITED, FELLING-ON-TYNE.


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