Mr. Turnbull had predicted evil consequences, . . . and was now doing the best in his power to bring about the verification of his own prophecies.
ANTHONY TROLLOPE
I.
When I received the list of participants in this course and realized that I
had been asked to speak to philosophical colleagues I thought, after some hesitation
and consultation, that you would probably prefer me to speak about those problems
which interest me most, and about those developments with which I am most intimately
acquainted. I therefore decided to do what I have never done before: to give
you a report on my own work in the philosophy of science, since the autumn of1919
when I first began to grapple with the problem, "When should a theory be
ranked as scientific?" or "Is there a criterion for the scientific
character or status of a theory?"
The problem which troubled me at the time was neither, "When is a theory
true?"nor, "When is a theory acceptable?" My problem was different.
I wished to distinguish between science and pseudo-science; knowing very well
that science often errs, and that pseudo-science may happen to stumble on the
truth.
I knew, of course, the most widely accepted answer to my problem: that science
is distinguished from pseudoscience or from "metaphysics"by its empirical
method, which is essentially inductive, proceeding from observation or experiment.
But this did not satisfy me. On the contrary, I often formulated my problem
as one of distinguishing between a genuinely empirical method and a non-empirical
or even a pseudo-empirica1 method-that is to say, a method which, although it
appeals to observation and experiment, nevertheless does not come up to scientific
standards. The latter method may be exemplified by astrology with its stupendous
mass of empirical evidence based on observation-on horoscopes and on biographies.
But as it was not the example of astrology which led me to my problem I should
perhaps briefly describe the atmosphere in which my problem arose and the examples
by which it was stimulated. After the collapse of the Austrian Empire there
had been a revolution in Austria: the air was full of revolutionary slogans
and ideas, and new and often wild theories. Among the theories which interested
me Einstein's theory of relativity was no doubt by far the most important. Three
others were Marx's theory of history, Freud's psycho-analysis, and Alfred Adler's
so-called "individual psychology."
There was a lot of popular nonsense talked about these theories, and especially
about relativity (as still happens even today), but I was fortunate in those
who introduced me to the study of this theory. We all-the small circle of students
to which I belonged-were thrilled with the result of Eddington's eclipse observations
which in 1919 brought the first important confirmation of Einstein's theory
of gravitation. It was a great experience for us, and one which had a lasting
influence on my intellectual development.
The three other theories I have mentioned were also widely discussed among
students at that time. I myself happened to come into personal contact with
Alfred Adler,
and even to co-operate with him in his social work among the children and young
people in the working-class districts of Vienna where he had established social
guidance clinics.
It was during the summer of 1919 that I began to feel more
and more dissatisfied with these three theories-the Marxist theory of history,
psychoanalysis, and
individual psychology; and I began to feel dubious about their claims to scientific
status. My problem perhaps first took the simple form, "What is wrong
with Marxism, psycho-analysis, and individual psychology? Why are they so
different
from physical theories, from Newton's theory, and especially from the theory
of relativity?"
To make this contrast clear I should explain that few of us at the time would
have said that we believed in the truth of Einstein's theory of gravitation.
This shows that it was not my doubting the truth of those other three theories
which bothered me, but something else. Yet neither was it that I merely felt
mathematical physics to be more exact than the sociological or psychological
type of theory. Thus what worried me was neither the problem of truth, at
that
stage at least, nor the problem of exactness or measurability.It was rather
that I felt that these other three theories, though posing as sciences, had
in fact more in common with primitive myths than with science; that they
resembled
astrology rather than astronomy.
I found that those of my friends who were admirers
of Marx, Freud, and Adler, were impressed by a number of points common to these
theories, and especially
by their apparent explanatory power. These theories appeared to be able to
explain
practically everything that happened within the fields to which they referred.
The study of any of them seemed to have the effect of an intellectual conversion
or revelation, opening your eyes to a new truth hidden from those not yet initiated.
Once your eyes were thus opened you saw confirming instances everywhere: the
world was full of verifications of the theory. Whatever happened always confirmed
it. Thus its truth appeared manifest; and unbelievers were clearly people who
did not want to see the manifest truth; who refused to see it, either because
it was against their class interest, or because of their repressions which
were
still "unanalyzed" and crying aloud for treatment.
The most characteristic element in this situation seemed to me the incessant
stream of confirmations, of observations which "verified" the theories
in question; and this point was constantly emphasized by their adherents. A
Marxist could not open a newspaper without finding on every page confirming
evidence for his interpretation of history; not only in the news, but also in
its presentation-which revealed the class bias of the paper-and especially of
course in what the paper did not say. The Freudian analysts emphasized that
their theories were constantly verified by their "clinical observations."
As for Adler, I was much impressed by a personal experience. Once, in 1919,
1 reported to him a case which to me did not seem particularly Adlerian, but
which he found no difficulty in analysing in terms of his theory of inferiority
feelings, although he had not even seen the child. Slightly shocked, I asked
him how he could be so sure. "Because of my thousand fold experience,"
he replied; whereupon I could not help saying: "And with this new case,
I suppose, your experience has become thousand-and-one-fold."
What I had in mind was that his previous observations may not have been much
sounder than this new one; that each in its turn had been interpreted in the
light of"previous experience," and at the same time counted as additional
confirmation. What, I asked myself, did it confirm? No more than that a case
could be interpreted in the light of the theory. But this meant very little,
I reflected, since every conceivable case could be interpreted in the light
of Adler's theory, or equally of Freud's. I may illustrate this by two very
different examples of human behaviour: that of a man who pushes a child into
the water with the intention of drowning it; and that of a man who sacrifices
his life in an attempt to save the child. Each of these two cases can be explained
with equal ease in Freudian and in Adlerian terms. According to Freud the first
man suffered from repression (say, of some component of his Oedipus complex),
while the second man had achieved sublimation. According to Adler the first
man suffered from feelings of inferiority (producing perhaps the need to prove
to himself that he dared to commit some crime), and so did the second man (whose
need was to prove to himself that he dared to rescue the child). I could not
think of any human behaviour which could not be interpreted in terms of either
theory. It was precisely this fact-that they always fitted, that they were always
confirmed-which in the eyes of their admirers constituted the strongest argument
in favour of these theories. It began to dawn on me that this apparent strength
was in fact their weakness.
With Einstein's theory the situation was strikingly different. Take one typical
instance-Einstein's prediction, just then confirmed by the findings of Eddington's
expedition. Einstein's gravitational theory had led to the result that light
must be attracted by heavy bodies (such as the sun), precisely as material
bodies
were attracted. As a consequence it could be calculated that light from a distant
fixed star whose apparent position was close to the sun would reach the earth
from such a direction that the star would seem to be slightly shifted away
from
the sun; or, in other words, that stars close to the sun would look as if they
had moved a little away from the sun, and from one another. This is a thing
which cannot normally be observed since such stars are rendered invisible in
daytime by the sun's overwhelming brightness; but during an eclipse it is possible
to take photographs of them. If the same constellation is photographed at night
one can measure the distances on the two photographs, and check the predicted
effect.
Now the impressive thing about this case is the risk involved in a prediction
of this kind. If observation shows that the predicted effect is definitely
absent,
then the theory is simply refuted. The theory is incompatible with certain
possible results of observation-in fact with results which everybody before
Einstein
would have expected. This is quite different from the situation I have previously
described, when it turned out that the theories in question were compatible
with the most divergent human behaviour,so that it was practically impossible
to describe any human behaviour that might not be claimed to be a verification
of these theories.
These considerations led me in the winter of 1919-20 to conclusions which I
may now reformulate as follows:
One can sum up all this by saying that the criterion of the scientific status of a theory is its falsifiability, or refutability, or testability.
II.
I may perhaps exemplify this with the help of the various theories so far mentioned.
Einstein's theory of gravitation clearly satisfied the criterion of falsifiability.
Even if our measuring instruments at the time did not allow us to pronounce
on the results of the tests with complete assurance, there was clearly a possibility
of refuting the theory.
Astrology did not pass the test. Astrologers were greatly impressed, and misled,by
what they believed to be confirming evidence so much so that they were quite
unimpressed by any unfavourable evidence. Moreover, by making their interpretations
and prophecies sufficiently vague they were able to explain away anything that
might have been a refutation of the theory had the theory and the prophecies
been more precise. In order to escape falsification they destroyed the testability
of their theory. It is a typical soothsayer's trick to predict things so vaguely
that the predictions can hardly fail: that they become irrefutable.
The Marxist theory of history, in spite of the serious efforts of some of its
founders and followers, ultimately adopted this soothsaying practice. In some
of its earlier formulations (for example in Marx's analysis of the character
of the "coming social evolution') their predictions were testable, and
in fact falsified.2 Yet instead of accepting the refutations the followers of
Marx reinterpreted both the theory and the evidence in order to make them agree.
In this way they rescued the theory from refutation; but they did so at the
price of adopting a device which made it irrefutable. They thus gave a "conventionalist
twist" to the theory; and by this stratagem they destroyed its much advertised
claim to scientific status.
The two psycho-analytic theories were in a different class. They were simply
non-testable, irrefutable. There was no conceivable human behaviour which could
contradict them. This does not mean that Freud and Adler were not seeing certain
things correctly: I personally do not doubt that much of what they say is of
considerable importance, and may well play its part one day in a psychological
science which is testable. But it does mean that those "clinical observations"
which analysts naively believe confirm their theory cannot do this any more
than the daily confirmations which astrologers find in their practice.3 And
as for Freud's epic of the Ego, the Super-ego, and the Id, no substantially
stronger claim to scientific status can be made for it than for Homer's collected
stories from Olympus. These theories describe some facts, but in the manner
of myths. They contain most interesting psychological suggestions, but not in
a testable form.
At the same time I realized that such myths may be developed, and become testable;
that historically speaking all-or very nearly all-scientific theories originate
from myths, and that a myth may contain important anticipations of scientific
theories. Examples are Empedocles' theory of evolution by trial and error, or
Parmenides' myth of the unchanging block universe in which nothing ever happens
and which, if we add another dimension, becomes Einstein's block universe (in
which, too, nothing ever happens, since everything is, four dimensionally speaking,
determined and laid down from the beginning). I thus felt that if a theory is
found to be non-scientific, or "metaphysical" (as we might say), it
is not thereby found to be unimportant, or insignificant, or "meaningless,"
or "nonsensical." it cannot claim to be backed by empirical evidence
in the scientific sense-although it may easily be, in some genetic sense, the
"result of observation."
(There were a great many other theories of this pre-scientific or pseudoscientific
character, some of them, unfortunately, as influential as the Marxist interpretation
of history; for example, the racialist interpretation of history-another of
those impressive and all-explanatory theories which act upon weak minds like
revelations.)
Thus the problem which I tried to solve by proposing the criterion of falsifiability
was neither a problem of meaningfulness or significance, nor a problem of truth
or acceptability. It was the problem of drawing a line (as well as this can
be done) between the statements, or systems of statements, of the empirical
sciences, and all other statements-whether they are of a religious or of a metaphysical
character, or simply pseudo-scientific. Years later-it must have been in 1928
or 1929-I called this first problem of mine the "problem of demarcation.
" The criterion of falsifiability is a solution to this problem of demarcation,
for it says that statements or systems of statements, in order to be ranked
as scientific, must be capable of conflicting with possible, or conceivable,
observations....
III.
Let us now turn from our logical criticism of the psychology of experience
to our real problem-the problem of the logic of science. Although some of the
things I have said may help us here, in so far as they may have eliminated certain
psychological prejudices in favour of induction, my treatment of the logical
problem of induction is completely independent of this criticism, and of all
psychological considerations. Provided you do not dogmatically believe in the
alleged psychological fact that we make inductions, you may now forget my whole
story with the exception of two logical points: my logical remarks on testability
or falsifiability as the criterion of demarcation; and Hume's logical criticism
of induction.From what I have said it is obvious that there was a close link
between the two problems which interested me at that time: demarcation, and
induction or scientific method. It was easy to see that the method of science
is criticism, i.e., attempted falsifications. Yet it took me a few years to
notice that the two problems-of demarcation and of induction-were in a sense
one....
I recently came across an interesting formulation of this belief in a remarkable
philosophical book by a great physicist-Max Born's Natural Philosophy of Cause
and Chance.5 He writes: "Induction allows us to generalize a number of
observations into a general rule: that night follows day and day follows night
. . .But while everyday life has no definite criterion for the validity of an
induction, . . .science has worked out a code, or rule of craft, for its application."
Born nowhere reveals the contents of this inductive code (which, as his wording
shows, contains a "definite criterion for the validity of an induction");
but he stresses that "there is no logical argument" for its acceptance:
"it is a question of faith"; and he is therefore "willing to
call induction a metaphysical principle." But why does he believe that
such a code of valid inductive rules must exist? This becomes clear when he
speaks of the "vast communities of people ignorant of, or rejecting, the
rule of science, among them the members of anti-vaccination societies and believers
in astrology. It is useless to argue with them; I cannot compel them to accept
the same criteria of valid induction in which I believe: the code of scientific
rules." This makes it quite clear that "valid induction" was
here meant to serve as a criterion of demarcation between science and pseudo-science.
But it is obvious that this rule or craft of "valid induction" is
not even metaphysical: it simply does not exist. No rule can ever guarantee
that a generalization inferred from true observations, however often repeated,
is true.(Born himself does not believe in the truth of Newtonian physics, in
spite of its success, although he believes that it is based on induction.) And
the success of science is not based upon rules of induction, but depends upon
luck, ingenuity,and the purely deductive rules of critical argument.
I may summarize some of my conclusions as follows:
If, as I have suggested, the problem of induction is only an instance or facet
of the problem of demarcation, then the solution to the problem of demarcation
must provide us with a solution to the problem of induction. This is indeed
the case, I believe, although it is perhaps not immediately obvious.
For a brief formulation of the problem of induction we can turn again to Born,
who writes: ". . . no observation or experiment, however extended can give
more than a finite number of repetitions"; therefore, "the statement
of a law-B depends on A-always transcends experience. Yet this kind of statement
is made everywhere and all the time, and sometimes from scanty material.'
In other words, the logical problem of induction arises from (a) Hume's discovery
(so well expressed by Born) that it is impossible to justify a law by observation
or experiment, since it "transcends experience"; (b) the fact that
science proposes and uses laws "everywhere and all the time." (Like
Hume, Born is struck by the "scanty material," i.e. the few observed
instances upon which the law may be based.) To this we have to add (c) the principle
of empiricism which asserts that in science,only observation and experiment
may decide upon the acceptance or rejection of scientific statements, including
laws and theories
.
These three principles, (a), (b), and (c), appear at first sight to clash; and
this apparent clash constitutes the logical problem of induction.
Faced with this clash, Born gives up (c), the principle of empiricism (as Kant
and may others, including Bertrand Russell, have done before him), in favour
of what he calls a "metaphysical principle"; a metaphysical principle
which he does not even attempt to formulate; which he vaguely describes as a
"code or rule of craft"; and of which I have never seen any formulation
which even looked promising and was not clearly untenable.
But in fact the principles (a) to (c) do not clash. We can see this the moment
we realize that the acceptance by science of a law or of a theory is tentative
only;which is to say that all laws and theories are conjectures, or tentative
hypotheses(a position which I have sometimes called "hypotheticism")
and that we may reject a law or theory on the basis of new evidence, without
necessarily discarding the old evidence which originally led us to accept it.7
The principles of empiricism (c) can be fully preserved, since the fate of a
theory, its acceptance or rejection, is decided by observation and experiment
by the result of tests. So long as a theory stands up to the severest tests
we can design, it is accepted; if it does not, it is rejected. But it is never
inferred, in any sense, from the empirical evidence. There is neither a psychological
nor a logical induction. Only the falsity of the theory can be inferred from
empirical evidence, and this inference is a purely deductive one.
Hume showed that it is not possible to infer a theory from observation statements;
but this does not affect the possibility of refuting a theory by observation
statements. The full appreciation of the possibility makes the relation between
theories and observations perfectly clear. This solves the problem of the alleged
clash between the principles (a), (b), and(c), and with it Hume's problem of
induction....
NOTES
1. This is a slight oversimplification, for about half of the Einstein effect
may be derived from the classical theory, provided we assume a ballistic theory
of light.
2. See for example, my Open Society and Its Enemies, ch. 15, section iii, and
notes 13-14.
3. "Clinical observations," like all other observations, are interpretations
in the light of theories;and for this reason alone they are apt to seem to support
those theories in the light of which they were interpreted. But real support
can be obtained only from observations undertaken as tests (by"attempted
refutations"); and for this purpose criteria of refutation have to be laid
down beforehand;it must be agreed which observable situations, if actually observed,
mean that the theory is refuted. But what kind of clinical responses would refute
to the satisfaction of the analyst not merely a particular analytic diagnosis
but psycho-analysis itself? And have such criteria ever been discussed or agreed
upon by analysts? Is there not, on the contrary, a whole family of analytic
concepts, such as"ambivalence" (l do not suggest that there is no
such thing as ambivalence), which would make it difficult, if not impossible,
to agree upon such criteria? Moreover, how much headway has been made in investigating
the question of the extent to which the (conscious or unconscious) expectations
and theories held by the analyst influence the "clinical responses"
of the patient? To say nothing about the conscious attempts to influence the
patient by proposing interpretations to him, etc.) Years ago I introduced the
term "Oedipus effect" to describe the influence of a theory or expectation
or prediction upon the event which it predicts or describes: it will be remembered
that the causal chain leading to Oedpus' parricide was started by the oracle's
prediction of this event. This is a characteristic and recurrent theme of such
myths, but one which seems to have failed to attract the interest of the analysts,
perhaps not accidentally. (The problem of confirmatory dreams suggested by the
analyst is discussed by Freud, for example in Gesammelte Schriften,i 111, 1925,
where he says on p. 314: "If anybody asserts that most of the dreams which
can be utilized in an analysis . . . owe their origin to [the analyst's] suggestion,
then no objection can be made from the point of view of analytic theory. Yet
there is nothing in this fact,"he surprisingly adds, "which would
detract from the reliability of our results.']
4. The case of astrology, nowadays a typical pseudo-science, may illustrate
this point. It was attacked, by Aristotelians and other rationalists, down to
Newton's day, for the wrong reason-for its now an accepted assertion that the
planets had an "influence" upon terrestrial ("sublunar")events.
In fact Newton's theory of gravity, and especially the lunar theory of the tides,
was historically speaking an offspring of astrological lore. Newton, it seems,
was most reluctant to adopt a theory which came from the same stable as for
example the theory that "influenza"epidemics are due to an astral
"influence." And Galileo, no doubt for the same reason, actually rejected
the lunar theory of the tides; and his misgivings about Kepler may easily be
explained by his misgivings about astrology.
5. Max Born, Natural Philosophy of Cause and Chance, Oxford, 1949, p. 7.
6. Natural Philosophy of Cause and Chance, p. 6.
7. I do not doubt that Born and many others would agree that theories are accepted
only tentatively. But the widespread belief in induction shows that the far-reaching
implications of this view are rarely seen.