I now turn to the problem of demarcation, and to explaining how this problem is related to the problems of empirical content and of testability.
The great scientists, such as Galileo, Kepler, Newton, Einstein, and Bohr (to confine myself to a few of the dead) represent to me a simple but impressive idea of science. Obviously, no such list, however much extended, would define scientist or science in extenso. But it suggests for me an oversimplification, one from which we can, I think, learn a lot. It is the working of great scientists which I have in my mind as my paradigm for science. Not that I lack respect for the lesser ones; there are hundreds of great men and great scientists who come into the almost heroic category.
But with all respect for the lesser scientists, I wish to convey here a heroic and romantic idea of science and its workers: men who humbly devoted themselves to the search for truth, to the growth of our knowledge; men whose life consisted in an adventure of bold ideas. I am prepared to consider with them many of their less brilliant helpers who were equally devoted to the search for truth - for great truth. But I do not count among them those for whom science is no more than a profession, a technique: those who are not deeply moved by great problems and by the oversimplifications of bold solutions.
It is science in this heroic sense that I wish to study. As a side result I find that we can throw a lot of light even on the more modest workers in applied science.
This, then, for me is science. I do not try to define it, for very
good reasons. I only wish to draw a simple picture of the kind of men I have in mind, and of their activities. And the picture will be an oversimplification: these are men of bold ideas, but highly critical of their own ideas; they try to find whether their ideas are right by trying first to find whether they are not perhaps wrong. They work with bold conjectures and severe attempts at refuting their own conjectures.
My criterion of demarcation between science and non-science is a simple logical analysis of this picture. How good or bad it is will be shown by its fertility.
Bold ideas are new, daring, hypotheses or conjectures. And severe attempts at refutations are severe critical discussions and severe empirical tests.
When is a conjecture daring and when is it not daring, in the sense here proposed? Answer: it is daring if and only if it takes a great risk of being false - if matters could be otherwise, and seem at the time to be otherwise.
Let us consider a simple example. Copernicus’s or Aristarchus’s conjecture that the sun rather than the earth rests at the centre of the universe was an incredibly daring one. It was, incidentally, false; nobody accepts today the conjecture that the sun is (in the sense of Aristarchus and Copernicus) at rest in the centre of the universe. But this does not affect the boldness of the conjecture, nor its fertility. And one of its main consequences - that the earth does not rest at the centre of the universe but that it has (at least) a daily and an annual motion - is still fully accepted, in spite of some misunderstandings of relativity.1
But it is not the present acceptance of the theory which I wish to discuss, but its boldness. It was bold because it clashed with all then accepted views, and with the prima facie evidence of the senses. It was bold because it postulated a hitherto unknown hidden reality behind the appearances.
It was not bold in another very important sense: neither Aristarchus nor Copernicus suggested a feasible crucial experiment. In fact, they did not suggest that anything was wrong with the traditional appearances: they let the accepted appearances severely alone; they only reinterpreted them. They were not anxious to stick out their necks by predicting new observable appearances. (This is an oversimplification as far as Copernicus is concerned, but it is almost certainly true of Aristarchus.)
To the degree that this is so, Aristarchus’s and Copernicus’s theories may be described in my terminology as unscientific or metaphysical. To the degree that Copernicus did make a number of minor predictions, his theory is, in my terminology, scientific. But even as a metaphysical theory it was far from meaningless; and in proposing a new bold view of the universe it made a tremendous contribution to the advent of the new science.
Kepler went much further. He too had a bold metaphysical view, partly based upon the Copernican theory, of the reality of the world. But his view led him to many new detailed predictions of the appearances. At first these predictions did not tally with the observations. He tried to reinterpret the observations in the light of his theories; but his addiction to the search for truth was even greater than his enthusiasm for the metaphysical harmony of the world. Thus he felt forced to give up a number of his favoured theories, one by one, and to replace them by others which fitted the facts. It was a great and a heartrending struggle. The final outcome, his famous and immensely important three laws, he did not really like - except the third. But they stood up to his severest tests - they agreed with the detailed appearances, the observations which he had inherited from Tycho.
Kepler’s laws are excellent approximations to what we think today are the true movements of the planets of our solar system. They are even excellent approximations to the movements of the distant binary star systems which have since been discovered. Yet they are merely approximations to what seems to be the truth; they are not true.
They have been tested in the light of new theories-of Newton’s theory and of Einstein’s - which predicted small deviations from Kepler’s laws. (According to Newton, Kepler’s laws are correct only for two-body systems [see also selection 12 below].) Thus the crucial experiments went against Kepler, very slightly, but sufficiently clearly.
Of these three theories - Kepler’s, Newton’s, and Einstein’s -the latest and still the most successful is Einstein’s; and it was this theory which led me into the philosophy of science. What
impressed me so greatly about Einstein’s theory of gravitation were the following points.
(1) It was a very bold theory. It greatly deviated in its fundamental outlook from Newton’s theory which at that time was utterly successful. (The small deviation of the perihelion of Mercury did not seriously trouble anybody in the light of its other almost incredible successes. Whether it should have done is another matter.)
(2) From the point of view of Einstein’s theory, Newton’s theory was ^n excellent approximation, though false (just as from the point of view of Newton’s theory, Kepler’s and Galileo’s theories were excellent approximations, though false). Thus it is not its truth which decides the scientific character of a theory.
(3) Einstein derived from his theory three important predictions of vastly different observable effects, two of which had not been thought of by anybody before him, and all of which contradicted Newton’s theory, so far as they could be said to fall within the field of application of this theory at all.
But what impressed me perhaps most were the following two points.
(4) Einstein declared that these predictions were crucial: if they did not agree with his precise theoretical calculations, he would regard his theory as refuted.
(5) But even if they were observed as predicted, Einstein declared that his theory was false: he said that it would be a better approximation to the truth than Newton’s, but he gave reasons why he would not, even if all predictions came out right, regard it as a true theory. He sketched a number of demands which a true theory (a unified field theory) would have to satisfy, and declared that his theory was at best an approximation to this so far unattained unified field theory.
It may be remarked in passing that Einstein, like Kepler, failed to achieve his scientific dream - or his metaphysical dream: it does not matter in this context what label we use. What we call today Kepler’s laws or Einstein’s theory of gravitation are results which in no way satisfied their creators, who each continued to work on his dream to the end of his life. And even of Newton a similar point can be made: he never believed that a theory of action at a distance could be a finally acceptable explanation of gravity.2
Einstein’s theory was first tested by Eddington’s famous eclipse experiment of 1919. In spite of his unbelief in the truth of his theory, his belief that it was merely a new important approximation towards the truth, Einstein never doubted the outcome of this experiment; the inner coherence, the inner logic of his theory convinced him that it was a step forward even though he thought that it could not be true. It has since passed a series of further tests, all very successfully. But some people still think the agreement between Einstein’s theory and the observations may be the result of (incredibly improbable) accidents. It is impossible to rule this out; yet the agreement may rather be the result of Einstein’s theory’s being a fantastically good approximation to the truth.3
The picture of science at which I have so far only hinted may be sketched as follows.
There is a reality behind the world as it appears to us, possibly a many-layered reality, of which the appearances are the outermost layers. What the great scientist does is boldly to guess, daringly to conjecture, what these inner realities are like. This is akin to myth making. (Historically we can trace back the ideas of Newton via Anaximander to Hesiod, and the ideas of Einstein via Faraday, Boscovic, Leibniz, and Descartes to Aristotle and Parmenides.4) The boldness can be gauged by the distance between the world of appearance and the conjectured reality, the explanatory hypotheses.
But there is another, a special kind of boldness - the boldness of predicting aspects of the world of appearance which so far have been overlooked but which it must possess if the conjectured reality is (more or less) right, if the explanatory hypotheses are (approximately) true. It is this more special kind of boldness which I have usually in mind when I speak of bold scientific conjectures. It is the boldness of a conjecture which takes a real risk - the risk of being tested, and refuted; the risk of clashing with reality.
Thus my proposal was, and is, that it is this second boldness, together with the readiness to look out for tests and refutations, which distinguishes ‘empirical’ science from non-science, and especially from pre-scientific myths and metaphysics.
I will call this proposal (D): (D) for ‘demarcation’.
The italicized proposal (D) is what I still regard as the centre of my philosophy. But I have always been highly critical of any idea of my own; and so I tried at once to find fault with this particular idea, years before I published it. And I published it together with the main results of this criticism. My criticism led me to a sequence of refinements or improvements of the proposal (D): they were not later concessions, but they were published together with the proposal as parts of the proposal itself.5
n Difficulties with the Demarcation Proposal
(1) From the beginning I called my criterion of demarcation a proposal. This was partly because of my uneasiness about definitions and my dislike of them. Definitions are either abbreviations and therefore unnecessary, though perhaps convenient, or they are Aristotelian attempts to ‘state the essence’ of a word, and therefore unconscious conventional dogmas [see selection 6 above]. If I define ‘science’ by my criterion of demarcation (I admit that this is more or less what I am doing) than anybody could propose another definition, such as ‘science is the sum total of true statements’. A discussion of the merits of such definitions can be pretty pointless. This is why I gave here first a description of great or heroic science and then a proposal for a criterion which allows us to demarcate - roughly - this kind of science. Any demarcation in my sense must be rough. (This is one of the great differences from any formal meaning criterion of any artificial ‘language of science’.) For the transition between metaphysics and science is not a sharp one: what was a metaphysical idea yesterday can become a testable scientific theory tomorrow; and this happens frequently (I gave various examples in The Logic of Scientific Discovery and elsewhere: atomism is perhaps the best).
Thus one of the difficulties is that our criterion must not be too sharp; and in the chapter ‘Degrees of Testability’ of The Logic of Scientific Discovery I suggested (as a kind of second improvement of the criterion (D) of the foregoing section) that a theory is scientific to the degree to which it is testable.
This, incidentally, led later to one of the most fruitful discoveries of that book: that there are degrees of testability (or of
scientific character), which can be identified with degrees of empirical content (or informative content).
(2) The formula (D) of the foregoing section is expressed in somewhat psychological language. It can be considerably improved if one speaks of theoretical systems or systems of statements, as I did throughout The Logic of Scientific Discovery. This leads at once to the recognition of one of the problems connected with the falsifiability criterion of demarcation: even if we can apply it to systems of statements, it may be difficult if not impossible to say which particular statement, or which subsystem of a system of statements, has been exposed to a particular experimental test. Thus we may describe a system as scientific or empirically testable, while being most uncertain about its constituent parts.
An example is Newton’s theory of gravitation. It has often been asked whether Newton’s laws of motion, or which of them, are masked definitions rather than empirical assertions.
My answer is as follows: Newton’s theory is a system. If we falsify it, we falsify the whole system. We may perhaps put the blame on one of its laws or on another. But this means only that we conjecture that a certain change in the system will free it from falsification; or in other words, that we conjecture that a certain alternative system will be an improvement, a better approximation to the truth.
But this means: attributing the blame for a falsification to a certain subsystem is a typical hypothesis, a conjecture like any other, though perhaps hardly more than a vague suspicion if no definite alternative suggestion is being made. And the same applies the other way round: the decision that a certain subsystem is not to be blamed for the falsification is likewise a typical conjecture. The attribution or non-attribution of responsibility for failure is conjectural, like everything in science; and what matters is the proposal of a new alternative and competing conjectural system that is able to pass the falsifying test.
(3) Points (1) and (2) illustrate that however correct my criterion of bold conjectures and severe refutations may be, there are difficulties which must not be overlooked. A primitive difficulty of this kind may be described as follows. A biologist offers the conjecture that all swans are white. When black swans are discovered in Australia, he says that it is not refuted. He insists that
these black swans are a new kind of bird since it is part of the defining property of a swan that it is white. In other words, he can escape the refutation, though I think that he is likely to learn more if he admits that he was wrong.
In any case - and this is very important - the theory ‘All swans are white’ is refutable at least in the following clear logical sense: it must be declared refuted by anybody who accepts that there is at least one non-white swan.
(4) The principle involved in this example is a very primitive one, but it has a host of applications. For a long time chemists have been inclined to regard atomic weights, melting points, and similar properties as defining properties of materials: there can be no water whose freezing point differs from 0°C; it just would not be water, however similar in other respects it might be to water. But if this is so, then according to my criterion of demarcation ‘Water freezes at 0°C’ would not be a scientific or an empirical statement; it would be a tautology - part of a definition.
Clearly, there is a problem here: either my criterion of demarcation is refuted, or we have to admit the possibility of discovering water whose freezing point is other than 0°C.
(5) I plead of course for the second possibility, and I hold that from this simple example we can learn a lot about the advantages of my proposal (D). For let us assume we have discovered water with a different freezing point. Is this still to be called ‘water’? / assert that the question is totally irrelevant. The scientific hypothesis was that a liquid (no matter what you call it) with a considerable list of chemical and physical properties freezes at 0°C. If any of these properties which have been conjectured to be constantly conjoined should not materialize then we were wrong; and thus new and interesting problems open up. The least of them is whether or not we should continue to call the liquid in question ‘water’: this is purely arbitrary or conventional. Thus my criterion of demarcation is not only not refuted by this example: it helps us to discover what is significant for science and what is arbitrary and irrelevant .
(6) As explained in the very first chapter of The Logic of Scientific Discovery, we can always adopt evasive tactics in the face of refutations. For historical reasons I originally called these tactics ‘conventionalist stratagems [or twists]’, but now call them
‘immunizing tactics or stratagems' :6 we can always immunize a theory against refutation. There are many such evasive immunizing tactics; and if nothing better occurs to us, we can always deny the objectivity - or even the existence - of the refuting observation. (Remember the people who refused to look through Galileo’s telescope.) Those intellectuals who are more interested in being right than in learning something interesting but unexpected are by no means rare exceptions.
(7) None of the difficulties so far discussed is terribly serious: it may seem that a little intellectual honesty would go a long way to overcome them. By and large this is true. But how can we describe this intellectual honesty in logical terms? I described it in The Logic of Scientific Discovery, as a rule of method, or a methodological rule: ‘Do not try to evade falsification, but stick your neck out!’
(8) But I was yet a little more self-critical: I first noticed that such a rule of method is, necessarily, somewhat vague - as is the problem of demarcation altogether. Clearly, one can say that if you avoid falsification at any price, you give up empirical science in my sense. But I found that, in addition, supersensitivity with respect to refuting criticism was just as dangerous: there is a legitimate place for dogmatism, though a very limited place. He who gives up his theory too easily in the face of apparent refutations will never discover the possibilities inherent in his theory. There is room in science for debate: for attack and therefore also for defence. Only if we try to defend them can we learn all the different possibilities inherent in our theories. As always, science is conjecture. You have to conjecture when to stop defending a favourite theory, and when to try a new one.
(9) Thus I did not propose the simple rule: ‘Look out for refutations, and never dogmatically defend your theory.’ Still, it was much better advice than dogmatic defence at any price. The truth is that we must be constantly critical; self-critical with respect to our own theories, and self-critical with respect to our own criticism; and, of course, we must never evade an issue.
This, then, is roughly the methodological form of (D), of the criterion of demarcation. Propose theories which can be criticized. Think about possible decisive falsifying experiments - crucial
experiments. But do not give up your theories too easily - not, at any rate, before you have critically examined your criticism.
The difficulties connected with my criterion of demarcation (D) are important, but must not be exaggerated. It is vague, since it is a methodological rule, and since the demarcation between science and non-science is vague. But it is more than sharp enough to make a distinction between many physical theories on the one hand, and metaphysical theories, such as psychoanalysis, or Marxism (in its present form), on the other. This is, of course, one of my main theses; and nobody who has not understood it can be said to have understood my theory.
The situation with Marxism is, incidentally, very different from that with psychoanalysis. Marxism was once a scientific theory: it predicted that capitalism would lead to increasing misery and, through a more or less mild revolution, to socialism; it predicted that this would happen first in the technically highest developed countries; and it predicted that the technical evolution of the ‘means of production’ would lead to social, political, and ideological developments, rather than the other way round.
But the (so-called) socialist revolution came first in one of the technically backward countries. And instead of the means of production producing a new ideology, it was Lenin’s and Stalin’s ideology that Russia must push forward with its industrialization (‘Socialism is dictatorship of the proletariat plus electrification’) which promoted the new development of the means of production.
Thus one might say that Marxism was once a science, but one which was refuted by some of the facts which happened to clash with its predictions (I have here mentioned just a few of these facts).7
However, Marxism is no longer a science; for it broke the methodological rule that we must accept falsification, and it immunized itself against the most blatant refutations of its predictions. Ever since then, it can be described only as non-science - as a metaphysical dream, if you like, married to a cruel reality.
Psychoanalysis is a very different case. It is an interesting psychological metaphysics (and no doubt there is some truth in it, as there is so often in metaphysical ideas), but it never was a science. There may be lots of people who are Freudian or Adlerian cases: Freud himself was clearly a Freudian case, and Adler an Adlerian case. But what prevents their theories from being scientific in the sense here described is, very simply, that they do not exclude any physically possible human behaviour. Whatever anybody may do is, in principle, explicable in Freudian or Adlerian terms. (Adler’s break with Freud was more Adlerian than Freudian, but Freud never looked on it as a refutation of his theory.)
The point is very clear. Neither Freud nor Adler excludes any particular person’s acting in any particular way, whatever the outward circumstances. Whether a man sacrificed his life to rescue a drowning child (a case of sublimation) or whether he murdered the child by drowning him (a case of repression) could not possibly be predicted or excluded by Freud’s theory; the theory was
compatible with everything that could happen - even without any special immunization treatment.
Thus while Marxism became nonscientific by its adoption of an immunizing strategy, psychoanalysis was immune to start with, and remained so.8 In contrast, most physical theories are pretty free of immunizing tactics and highly falsifiable to start with. As a rule, they exclude an infinity of conceivable possibilities.
The main value of my criterion of demarcation was, of course, to point out these differences. And it led me to the theory that the empirical content of a theory could be measured by the number of possibilities which it excluded (provided a reasonably nonimmunizing methodology was adopted).
iv Ad Hoc Hypotheses and Auxiliary Hypotheses
There is one important method of avoiding or evading refutations: it is the method of auxiliary hypotheses or ad hoc hypotheses.
If any of our conjectures goes wrong - if, for example, the planet Uranus does not move exactly as Newton’s theory demands - then we have to change the theory. But there are in the main two kinds of changes; conservative and revolutionary. And among the more
conservative changes there are again two: ad hoc hypotheses and
auxiliary hypotheses.
In the case of the disturbances in the motion of Uranus the adopted hypothesis was partly revolutionary: what was conjectured was the existence of a new planet, something which did not affect Newton’s laws of motion, but which did affect the much older ‘system of the world’. The new conjecture was auxiliary rather than ad hoc for although there was only this one ad hoc reason for introducing it, it was independently testable: the position of the new planet (Neptune) was calculated, the planet was discovered optically, and it was found that it fully explained the anomalies of Uranus. Thus the auxiliary hypothesis stayed within the Newtonian theoretical framework, and the threatened refutation was transformed into a resounding success.
I call a conjecture ‘ad hoc’ if it is introduced (like this one) to explain a particular difficulty, but if (in contrast to this one) it
cannot be tested independently.
It is clear that, like everything in methodology, the distinction between an ad hoc hypothesis and a conservative auxiliary hypothesis is a little vague. Pauli introduced the hypothesis of the neutrino quite consciously as an ad hoc hypothesis. He had originally no hope that one day independent evidence would be found; at the time this seemed practically impossible. So we have an example here of an ad hoc hypothesis which, with the growth of knowledge, did shed its ad hoc character. And we have a warning here not to pronounce too severe an edict against ad hoc hypotheses: they may become testable after all, as may also happen to a metaphysical hypothesis. But in general, our criterion of testability warns us against ad hoc hypotheses; and Pauli was at first far from happy about the neutrino, which would in all likelihood have been abandoned in the end, had not new methods provided independent tests for its existence.
Ad hoc hypotheses - that is, at the time untestable auxiliary hypotheses - can save almost any theory from any particular refutation. But this does not mean that we can go on with an ad hoc hypothesis as long as we like. It may become testable; and a negative test may force us either to give it up or to introduce a new secondary ad hoc hypothesis, and so on, ad infinitum. This, in fact, is a thing we almost always avoid. (I say ‘almost’ because methodological rules are not hard and fast.)
Moreover, the possibility of making things up with ad hoc hypotheses must not be exaggerated: there are many refutations which cannot be evaded in this way, even though some kind of immunizing tactic such as ignoring the refutation is always possible.
PartII PhilosophyofScience
ft
The theory to be developed in the following pages stands directly opposed to all attempts to operate with the ideas of inductive logic. It might be described as the theory of the deductive method of testing, or as the view that a hypothesis can only be empirically tested - and only after it has been advanced.
Before I can elaborate this view (which might be called ‘deductivism’, in contrast to ‘inductivism’1) I must first make clear the distinction between the psychology of knowledge which deals with empirical facts, and the logic of knowledge which is concerned only with logical relations. For the belief in inductive logic is largely due to a confusion of psychological problems with epistemological ones. It may be worth noticing, by the way, that this confusion spells trouble not only for the logic of knowledge but for its psychology as well.
it must already have been presented to us. Someone must have formulated it, and submitted it to logical examination.
Accordingly I shall distinguish sharply between the process of conceiving a new idea, and the methods and results of examining it logically. As to the task of the logic of knowledge - in contradistinction to the psychology of knowledge -1 shall proceed on the assumption that it consists solely in investigating the methods employed in those systematic tests to which every new idea must be subjected if it is to be seriously entertained.
Some might object that it would be more to the purpose to regard it as the business of epistemology to produce what has been called a ‘rational reconstruction’ of the steps that have led the scientist to a discovery - to the finding of some new truth. But the question is: what, precisely, do we want to reconstruct? If it is the processes involved in the stimulation and release of an inspiration which are to be reconstructed, then I should refuse to take it as the task of the logic of knowledge. Such processes are the concern of empirical psychology but hardly of logic. It is another matter if we want to reconstruct rationally the subsequent tests whereby the inspiration may be discovered to be a discovery, or become known to be knowledge. In so far as the scientist critically judges, alters, or rejects his own inspiration we may, if we like, regard the methodological analysis undertaken here as a kind of ‘rational reconstruction’ of the corresponding thought processes. But this reconstruction would not describe these processes as they actually happen: it can give only a logical skeleton of the procedure of testing. Still, this is perhaps all that is meant by those who speak of a ‘rational reconstruction’ of the ways in which we gain knowledge.
It so happens that my arguments here are quite independent of this problem. However, my view of the matter, for what it is worth, is that there is no such thing as a logical method of having new ideas, or a logical reconstruction of this process. My view may be expressed by saying that every discovery contains ‘an irrational element’, or ‘a creative intuition’, in Bergson’s sense. In a similar way Einstein speaks of the ‘search for those highly universal laws ... from which a picture of the world can be obtained by pure deduction. There is no logical path’, he says, ‘leading to these ... laws. They can only be reached by intuition, based upon
something like an intellectual love (‘Einfuhlung’) of the objects of experience.’2
n Deductive Testing of Theories
According to the view that will be put forward here, the method of critically testing theories, and selecting them according to the results of tests, always proceeds on the following lines. From a new idea, put up tentatively, and not yet justified in any way - an anticipation, a hypothesis, a theoretical system, or what you will - conclusions are drawn by means of logical deduction. These conclusions are then compared with one another and with other relevant statements, so as to find what logical relations (such as equivalence, derivability, compatibility, or incompatibility) exist between them.
We may if we like distinguish four different lines along which the testing of a theory could be carried out. First there is the logical comparison of the conclusions among themselves, by which the internal consistency of the system is tested. Secondly, there is the investigation of the logical form of the theory; with the object of determining whether it has the character of an empirical or scientific theory, or whether it is, for example, tautological. Thirdly, there is the comparison with other theories, chiefly with the aim of determining whether the theory would constitute a scientific advance should it survive our various tests. And finally, there is the testing of the theory by way of empirical applications of the conclusions which can be derived from it.
The purpose of this last kind of test is to find out how far the new consequences of the theory - whatever may be new in what it asserts - stand up to the demands of practice, whether raised by purely scientific experiments, or by practical technological applications. Here too the procedure of testing turns out to be deductive. With the help of other statements, previously accepted, certain singular statements - which we may call ‘predictions’ - are deduced from the theory; especially predictions that are easily testable or applicable. From among these statements, those are selected which are not derivable from the current theory, and more especially those which the current theory contradicts. Next we seek a decision as regards these (and other) derived statements by
comparing them with the results of practical applications and experiments. If this decision is positive, that is, if the singular conclusions turn out to be acceptable, or verified, then the theory has, for the time being, passed its test: we have found no reason to discard it. But if the decision is negative, or in other words, if the conclusions have been falsified; then their falsification also falsifies the theory from which they were logically deduced.
It should be noticed that a positive decision can only temporarily
support the theory, for subsequent negative decisions may always
/
overthrow it. So long as a theory withstands detailed and severe tests and is not superseded by another theory in the course of scientific progress, we may say that it has ‘proved its mettle’ or that it is ‘corroborated’3 by past experience.
Nothing resembling inductive logic appears in the procedure here outlined. I never assume that we can argue from the truth of singular statements to the truth of theories. I never assume that by force of ‘verified’ conclusions, theories can be established as ‘true’, or even as merely ‘probable’. And a more detailed analysis of the methods of deductive testing shows that all the problems can be dealt with that are usually called ‘epistemological’. Those problems, more especially, to which inductive logic gives rise, can be eliminated without creating new ones in their place.
In accordance with my proposal made above, epistemology, or the logic of scientific discovery, should be identified with the theory of scientific method. The theory of method, in so far as it goes beyond the purely logical analysis of the relations between scientific statements, is concerned with the choice of methods- with decisions about the way in which scientific statements are to be dealt with. These decisions will of course depend in their turn upon the aim which we choose from among a number of possible aims. The decision here proposed for laying down suitable rules for what I call the ‘empirical method’ is closely connected with my criterion of demarcation [see selection 8, section i above]: I propose to adopt such rules as will ensure the testability of scientific statements; which is to say, their falsifiability.
What are rules of scientific method, and why do we need them? Can there be a theory of such rules, a methodology?
The way in which one answers these questions will largely depend upon one’s attitude to science. Those who, like the positivists, see empirical science as a system of statements which satisfy certain logical criteria, such as meaningfulness or verifiability, will give one answer. A very different answer will be given by those who tend to see (as I do) the distinguishing characteristic of empirical statements in their susceptibility to revision - in the fact that they can be criticized, and superseded by better ones; and who regard it as their task to analyse the characteristic ability of science to advance, and the characteristic manner in which a choice is made, in crucial cases, between conflicting systems of theories.
I am quite ready to admit that there is a need for a purely logical analysis of theories, for an analysis which takes no account of how they change and develop. But this kind of analysis does not elucidate those aspects of the empirical sciences which I, for one, so highly prize. A system such as classical mechanics may be ‘scientific’ to any degree you like; but those who uphold it dogmatically - believing, perhaps, that it is their business to defend such a successful system against criticism as long as it is not conclusively disproved - are adopting the very reverse of that critical attitude which in my view is the proper one for the scientist. In point of fact, no conclusive disproof of a theory can ever be produced; for it is always possible to say that the experimental results are not reliable, or that the discrepancies which are asserted to exist between the experimental results and the theory are only apparent and that they will disappear with the advance of our understanding. (In the struggle against Einstein, both these arguments were often used in support of Newtonian mechanics, and similar arguments abound in the field of the social sciences.) If you insist on strict proof (or strict disproof) in the empirical sciences, you will never benefit from experience, and never learn from it how wrong you are.
If therefore we characterize empirical science merely by the formal or logical structure of its statements, we shall not be able to exclude from it that prevalent form of metaphysics which results from elevating an obsolete scientific theory into an incontrovertible truth.
Such are my reasons for proposing that empirical science should be characterized by its methods: by our manner of dealing with scientific systems: by what we do with them and what we do to them. Thus I shall try to establish the rules, or if you will the norms, by which the scientist is guided when he is engaged in research or in discovery, in the sense here understood.
iv The Naturalistic Approach to the Theory of Method
The hint I gave in the previous section as to the deepseated difference between my position and that of the positivists is in need of some amplification.
The positivist dislikes the idea that there should be meaningful problems outside the field of ‘positive’ empirical science -problems to be dealt with by a genuine philosophical theory. He dislikes the idea that there should be a genuine theory of knowledge, an epistemology or a methodology.4 He wishes to see in the alleged philosophical problems mere ‘pseudoproblems’ or ‘puzzles’. Now this wish of his - which, by the way, he does not express as a wish or a proposal but rather as a statement of fact -can always be gratified. For nothing is easier than to unmask a problem as ‘meaningless’ or ‘pseudo’. All you have to do is to fix upon a conveniently narrow meaning for ‘meaning’, and you will soon be bound to say of any inconvenient question that you are unable to detect any meaning in it. Moreover, if you admit as meaningful none except problems in natural science, any debate about the concept of‘meaning’ will also turn out to be meaningless. The dogma of meaning, once enthroned, is elevated forever above the battle. It can no longer be attacked. It has become (in Wittgenstein’s own words) ‘unassailable and definitive’.5
The controversial question whether philosophy exists, or has any right to exist, is almost as old as philosophy itself. Time and again an entirely new philosophical movement arises which finally unmasks the old philosophical problems as pseudoproblems, and which confronts the wicked nonsense of philosophy with the good sense of meaningful, positive, empirical, science. And time and again do the despised defenders of ‘traditional philosophy’ try to explain to the leaders of the latest positivistic assault that the main problem of philosophy is the critical analysis of the appeal to the authority of ‘experience’6 - precisely that ‘experience’ which every latest discoverer of positivism is, as ever, artlessly taking for granted. To such objections, however, the positivist only replies with a shrug: they mean nothing to him, since they do not belong to empirical science, which alone is meaningful. ‘Experience’ for him is a programme, not a problem (unless it is studied by empirical psychology).
I do not think positivists are likely to respond any differently to my own attempts to analyse ‘experience’ which I interpret as the method of empirical science. For only two kinds of statement exist for them: logical tautologies and empirical statements. If methodology is not logic, then, they will conclude, it must be a branch of some empirical science - the science, say, of the behaviour of scientists at work.
This view, according to which methodology is an empirical science in its turn - a study of the actual behaviour of scientists, or of the actual procedure of ‘science’ - may be described as ‘naturalistic’. A naturalistic methodology (sometimes called an ‘inductive theory of science’7) has its value, no doubt. A student of the logic of science may well take an interest in it, and learn from it. But what I call ‘methodology’ should not be taken for an empirical science. I do not believe that it is possible to decide, by using the methods of an empirical science, such controversial questions as whether science actually uses a principle of induction or not. And my doubts increase when I remember that what is to be called a ‘science’ and who is to be called a ‘scientist’ must always remain a matter of convention or decision.
I believe that questions of this kind should be treated in a different way. For example, we may consider and compare two different systems of methodological rules; one with, and one without, a principle of induction. And we may then examine whether such a principle, once introduced, can be applied without giving rise to inconsistencies; whether it helps us; and whether we really need it. It is this type of inquiry which leads me to dispense with the principle of induction: not because such a principle is as a matter of fact never used in science, but because I think that it is not needed; that it does not help us; and that it even gives rise to inconsistencies.
Thus I reject the naturalistic view. It is uncritical. Its upholders
fail to notice that whenever they believe themselves to have discovered a fact, they have only proposed a convention.8 Hence the convention is liable to turn into a dogma. This criticism of the naturalistic view applies not only to its criterion of meaning, but also to its idea of science, and consequently to its idea of empirical method.
Methodological rules are here regarded as conventions. They might be described as the rules of the game of empirical science. They differ from the rules of pure logic rather as do the rules of chess, which few would regard as part of pure logic: seeing that the rules of pure logic govern transformations of linguistic formulae, the result of an inquiry into the rules of chess could perhaps be entitled ‘The Logic of Chess’, but hardly ‘Logic’ pure and simple. (Similarly, the result of an inquiry into the rules of the game of science - that is, of scientific discovery - may be entitled ‘The Logic of Scientific Discovery’.)
Two simple examples of methodological rules may be given. They will suffice to show that it would be hardly suitable to place an inquiry into method on the same level as a purely logical inquiry.
(1) The game of science is, in principle, without end. He who decides one day that scientific statements do not call for any further test, and that they can be regarded as finally verified, retires from the game.
(2) Once a hypothesis has been proposed and tested, and has proved its mettle, it may not be allowed to drop out without ‘good reason’. A ‘good reason’ may be, for instance: replacement of the hypothesis by another which is better testable; or the falsification of one of the consequences of the hypothesis.9
These two examples show what methodological rules look like. Clearly they are very different from the rules usually called ‘logical’. Although logic may perhaps set up criteria for deciding whether a statement is testable, it certainly is not concerned with the question whether anyone exerts himself to test it.
[In selection 8] I tried to define empirical science with the help of the criterion of falsifiability; but as I was obliged to admit the justice of certain objections, I provided a methodological supplement to my definition. Just as chess might be defined by the rules proper to it, so empirical science may be defined by means of its methodological rules. In establishing these rules we may proceed systematically. First a supreme rule is laid down which serves as a kind of norm for deciding upon the remaining rules, and which is thus a rule of a higher type. It is the rule which says that the other rules of scientific procedure must be designed in such a way that they do not protect any statement in science against falsification.
Methodological rules are thus closely connected both with other methodological rules and with our criterion of demarcation. But the connection is not a strictly deductive or logical one.10 It results, rather, from the fact that the rules are constructed with the aim of ensuring the applicability of our criterion of demarcation; thus their formulation and acceptance proceed according to a practical rule of a higher type. An example of this has been given above (rule 1): theories which we decide not to submit to any further test would no longer be falsifiable. It is this systematic connection between the rules which makes it appropriate to speak of a theory of method. Admittedly the pronouncements of this theory are, as our examples show, for the most part conventions of a fairly obvious kind. Profound truths are not to be expected of methodology.11 Nevertheless it may help us in many cases to clarify the logical situation, and even to solve some far-reaching problems which have hitherto proved intractable. One of these, for example, is the problem of deciding whether a probability statement should be accepted or rejected.12
It has often been doubted whether the various problems of the theory of knowledge stand in any systematic relation to one another, and also whether they can be treated systematically. I hope to show that these doubts are unjustified. The point is of some importance. My only reason for proposing my criterion of
b
demarcation is that it is fruitful: that a great many points can be clarified and explained with its help. ‘Definitions are dogmas; only the conclusions drawn from them can afford us any new insight’, says Menger.13 This is certainly true of the definition of the concept ‘science’. It is only from the consequences of my definition of empirical science, and from the methodological decisions which depend upon this definition, that the scientist will be able to see how far it conforms to his intuitive idea of the goal of his endeavours. [See also selection 12 below.]
The philosopher too will accept my definition as useful only if he can accept its consequences. We must satisfy him that these consequences enable us to detect inconsistencies and inadequacies in older theories of knowledge, and to trace these back to the fundamental assumptions and conventions from which they spring. But we must also satisfy him that our own proposals are not threatened by the same kind of difficulties. This method of detecting and resolving contradictions is applied also within science itself, but it is of particular importance in the theory of knowledge. It is by this method, if by any, that methodological conventions might be justified, and might prove their value.14
Whether philosophers will regard these methodological investigations as belonging to philosophy is, I fear, very doubtful, but this does not really matter much. Yet it may be worth mentioning in this connection that not a few doctrines which are metaphysical, and thus certainly philosophical, could be interpreted as typical hypostatizations of methodological rules. An example of this is what is called ‘the principle of causality’.15 Another example is the problem of objectivity. For the requirement of scientific objectivity can also be interpreted as a methodological rule: the rule that only such statements may be introduced into science as are intersubjectively testable [see selection 10, section n, selection 11, section n, and selection 30]. It might indeed be said that the majority of the problems of theoretical philosophy, and the most interesting ones, can be re-interpreted in this way as problems of method.
Elimination of Psychologism
I said above that the work of the scientist consists in putting forward and testing theories.
The initial stage, the act of conceiving or inventing a theory, seems to me neither to call for logical analysis nor to be susceptible of it. The question how it happens that a new idea occurs to a man - whether it is a musical theme, a dramatic conflict, or a scientific theory - may be of great interest to empirical psychology; but it is irrelevant to the logical analysis of scientific knowledge. This latter is concerned not with questions of fact (Kant’s quid facti?), but only with questions of justification or validity (Kant’s quid juris?). Its questions are of the following kind. Can a statement be justified? And if so, how? Is it testable? Is it logically dependent on certain other statements? Or does it perhaps contradict them? In order that a statement may be logically examined in this way,