Karl Popper held that the effort of reaching a preference of one theory against others is the key to escaping the trap of the logical error of induction. This position was not a late appendage but was clearly stated for the English-speaking world in “The Logic of Scientific Discovery” (1959), the translated version of “Logik der Forschung” (1934). To assist a critical analysis of the evolution of Popper’s thoughts on critical preference I have compiled in the appendix excerpts from a number of his works. The concluding, Paul Arthur Schilpp “Philosophy of Karl Popper” (1974), extract is possibly as good an explication as Popper has made on this topic. In it Popper gives credit to his associate David Miller. On Page 52 of his own book “Critical Rationalism a Restatement and Defence” (1994), Miller states: “There are no such things as good reasons; that is, sufficient or even partly sufficient favourable (or positive) reasons for accepting a hypothesis rather than rejecting it, or for rejecting it rather than accepting it, or for implementing a policy, or for not doing so”. Here it seems that Miller is talking about reasons that are not critical preferences.
The following map of Popper quotes is not meant to replace the reading of the original publications but rather to provide references to guide further exploration in his scattered works. It is not an exaggeration to say that each time one opens Popper, Thomas Stearn Eliot’s much quoted paragraph from the last quartet, “Little Gidding” (1942), of “Four Quartets” might come to mind:
“We shall not cease from exploration
And the end of all our exploring
Will be to arrive where we started
And know the place for the first time.”
Any reference to “knowing” is not a reference to anything like justified true belief but rather an attestation that we do not know but rather guess and critically appraise. One should not even glorify this conjectural effort by saying it is to the best of our abilities, for who knows whether our abilities have been best used nor even what such abilities are? The quest for certainty in much 20th and now 21st century philosophy is unfortunately too often given an epistemic significance that fills volume after volume but leads to no escape from Hume’s problem of induction nor Kant’s problem of demarcation. Relegating Popper to footnotes or comfortable low rungs in textbook chapter organization does not help in problem solving and even worse the strawman naive-falsificationist legend of Popper actually hinders it.
The introductory extract from “The Logic of Scientific Discovery” highlights Popper’s understanding of the problem of the empirical basis in that acceptance of evidence (basic statements) is the result of human decisions, agreements. Science is a human activity, indeed a communal activity. What decides the fate of a theory is decisions not on aesthetic considerations such as how simple (Occam’s Razor) the theory is worded but decisions on what basic statements are to be accepted for attempted rebuttal of theories. The value of simplicity is to improve testability. One must also differentiate between existential trends e.g. statistical samples of events and so-called probability of hypotheses. Popper rejects the latter.
In the 1963 essay “Models Instruments and Truth”, included in the anthology”The Myth of the Framework” (1994) Popper is critical of the ridiculous phrase “truth is relative”. This phrase confuses the choice we make relative to competing theories’ perceived closeness to truth with TRUTH, unsullied by our opinions and efforts. No matter how well we test our theories they may still not be fair reflections of reality.
APPENDIX: Samples from Popper’s works that address critical preference.
From “The Logic of Scientific Discovery” (1959 orig., ninth impression July 1977, Hutchinson & Co, London)
Page 108 – Section 30, Theory and Experiment
It may now be possible for us to answer the question: How and why do we accept one theory in preference to others?
The preference is certainly not due to anything like an experiential justification of the statements composing the theory; it is not due to a logical reduction of the theory to experience. We choose the theory which best holds its own in competition with other theories; the one which, by natural selection, proves itself the fittest to survive. This will be the one which not only has hitherto stood up to the severest tests, but the one which is also testable in the most rigorous way. A theory is a tool which we test by applying it, and which we judge as to its fitness by the results of its applications.
From a logical point of view, the testing of a theory depends upon basic statements whose acceptance or rejection, in its turn, depends upon our decisions. Thus it is decisions which settle the fate of theories. To this extent my answer to the question, ‘how do we select a theory?’ resembles that given by the conventionalist; and like him I say that this choice is in part determined by considerations of utility. But in spite of this, there is a vast difference between my views and his. For I hold that what characterizes the empirical method is just this: that the convention or decision does not immediately determine our acceptance of universal statements but that, on the contrary, it enters into our acceptance of the singular statements – that is, the basic statements.
For the conventionalist, the acceptance of universal statements is governed by his principle of simplicity: he selects that system which is the simplest. I, by contrast, propose that the first thing to be taken into account should be the severity of tests. (There is a close connection between what I call ‘simplicity’ and the severity of tests; yet my idea of simplicity differs widely from that of the conventionalist; see section 46.) And I hold that what ultimately decides the fate of a theory is the result of a test, i.e. an agreement about basic statements. With the conventionalist I hold that the choice of any particular theory is an act, a practical matter. But for me the choice is decisively influenced by the application of the theory and the acceptance of the basic statements in connection with this application; whereas for the conventionalist, aesthetic motives are decisive.
Thus I differ from the conventionalist in holding that the statements decided by agreement are not universal but singular. And I differ from the positivist in holding that basic statements are not justifiable by our immediate experiences, but are, from the logical point of view, accepted by an act, by a free decision. (From the psychological point of view this may perhaps be a purposeful and well-adapted reaction.)
This important distinction, between a justification and a decision – a decision reached in accordance with a procedure governed by rules – might be clarified, perhaps, with the help of an analogy: the old procedure of trial by jury.
The verdict of the jury (vere dictum = spoken truly), like that of the experimenter, is an answer to a question of fact (quid facti?) which must be put to the jury in the sharpest, the most definite form. But what question is asked, and how it is put, will depend very largely on the legal situation, i.e. on the prevailing system of criminal law (corresponding to a system of theories). By its decision, the jury accepts, by agreement, a statement about a factual occurrence – a basic statement, as it were. The significance of this decision lies in the fact that from it, together with the universal statements of the system (of criminal law) certain consequences can be deduced. In other words, the decision forms the basis for the application of the system; the verdict plays the part of a ‘true statement of fact’. But it is clear that the statement need not be true merely because the jury has accepted it. This fact is acknowledged in the rule allowing a verdict to be quashed or revised.
The verdict is reached in accordance with a procedure which is governed by rules. These rules are based on certain fundamental principles which are chiefly, if not solely, designed to result in the discovery of objective truth. They sometimes leave room not only for subjective convictions but even for subjective bias. Yet even if we disregard these special aspects of the older procedure and imagine a procedure based solely on the aim of promoting the discovery of objective truth, it would still be the case that the verdict of the jury never justifies, or gives grounds for, the truth of what it asserts.
Neither can the subjective convictions of the jurors be held to justify the decision reached; although there is, of course, a close causal connection between them and the decision reached – a connection which might be stated by psychological laws; thus these convictions may be called the ‘motives’ of the decision. The fact that the convictions are not justifications is connected with the fact that different rules may regulate the jury’s procedure (for example, simple or qualified majority). This shows that the relationship between the convictions of the jurors and their verdict may vary greatly. In contrast to the verdict of the jury, the judgment of the judge is ‘reasoned’; it needs, and contains, a justification. The judge tries to justify it by, or deduce it logically from, other statements: the statements of the legal system, combined with the verdict that plays the role of initial conditions. This is why the judgment may be challenged on logical grounds. The jury’s decision, on the other hand, can only be challenged by questioning whether it has been reached in accordance with the accepted rules of procedure; i.e. formally, but not as to its content. (A justification of the content of a decision is significantly called a ‘motivated report’, rather than a ‘logically justified report’.)
The analogy between this procedure and that by which we decide basic statements is clear. It throws light, for example, upon their relativity, and the way in which they depend upon questions raised by the theory. In the case of the trial by jury, it would be clearly impossible to apply the ‘theory’ unless there is first a verdict arrived at by decision; yet the verdict has to be found in a procedure that conforms to, and thus applies, part of the general legal code. The case is analogous to that of basic statements. Their acceptance is part of the application of a theoretical system; and it is only this application which makes any further applications of the theoretical system possible. The empirical basis of objective science has thus nothing ‘absolute’ about it. Science does not rest upon solid bedrock. The bold structure of its theories rises, as it were, above a swamp. It is like a building erected on piles. The piles are driven down from above into the swamp, but not down to any natural or ‘given’ base; and if we stop driving the piles deeper, it is not because we have reached firm ground. We simply stop when we are satisfied that the piles are firm enough to carry the structure, at least for the time being.
Addendum 1972 edition page 281.
(a) We can never rationally justify a theory, that is to say, our belief in the truth of a theory, or in its being probably true. This negative solution is compatible with the following positive solution, contained in the rule of preferring theories which are better corroborated than others: (b) We can sometimes rationally justify the preference for a theory in the light of its corroboration, that is, of the present state of the critical discussion of the competing theories, which are critically discussed and compared from the point of view of assessing their nearness to the truth (verisimilitude). The current state of this discussion may, in principle, be reported in the form of their degrees of corroboration. The degree of corroboration is not, however, a measure of verisimilitude (such a measure would have to be timeless) but only a report of what we have been able to ascertain up to a certain moment of time, about the comparative claims of the competing theories by judging the available reasons which have been proposed for and against their verisimilitude.
APPENDIX *i Two Notes on Induction and Demarcation, (1959) Page 315
Scientific theories can never be ‘justified’, or verified. But in spite of this, a hypothesis A can under certain circumstances achieve more than a hypothesis B-perhaps because B is contradicted by certain results of observations, and therefore ‘falsified’ by them, whereas A is not falsified; or perhaps because a greater number of predictions can be derived with the help of A than with the help of B. The best we can say of a hypothesis is that up to now it has been able to show its worth, and that it has been more successful than other hypotheses although, in principle, it can never be justified, verified, or even shown to be probable. This appraisal of the hypothesis relies solely upon deductive consequences (predictions) which may be drawn from the hypothesis. There is no need even to mention induction.
The mistake usually made in this field can be explained historically: science was considered to be a system of knowledge – of knowledge as certain as it could be made. ‘Induction’ was supposed to guarantee the truth of this knowledge. Later it became clear that absolutely certain truth was not attainable. Thus one tried to get in its stead at least some kind of watered-down certainty or truth; that is to say, ‘probability’.
But speaking of ‘probability’ instead of ‘truth’ does not help us to escape either from the infinite regress or from apriorism.
From this point of view, one sees that it is useless and misleading to employ the concept of probability in connection with scientific hypotheses. The concept of probability is used in physics and in the theory of games of chance in a definite way which may be satisfactorily defined with the help of the concept of relative frequency (following von Mises). Reichenbach’s attempts to extend this concept so as to include the so-called ‘inductive probability’ or the ‘probability of hypotheses’ are doomed to failure, in my opinion, although I have no objection whatever against the idea of a ‘truth-frequency’ within a sequence of statements which he tries to invoke.
From “After the Open Society” (2008),
page 10 “Optimist,Pessimist and Pragmatist Views of Scientific Knowledge” (1963)
The position between optimism and pessimism which I am trying to establish may be briefly described as follows.
I agree with the pessimists that there is no justification for the claim of any particular theory or assertion to be true. Thus there is no justification of any claim to know, including the claims of scientific knowledge. But this merely means that all knowledge, including scientific knowledge, is hypothetical or conjectural: it is uncertain, fallible. This certainly does not mean that every assertion is as good as any other, competing, assertion. For we can discuss our various competing assertions, our conjectures, critically; and the result of the critical discussion is that we find out why some among the competing conjectures are better than others.
Accordingly, I agree with the optimists that our knowledge can grow, and can progress; for we can sometimes justify the verdict of our critical discussions when it ranks certain conjectures higher than others.
A verdict of this kind always appraises our conjectures or theories from the point of view of their approach to truth: although we cannot justify any claim that a theory is true, we can sometimes give good reasons for asserting that one theory is better than another, or even than all its competitors. In this way our knowledge can grow, and science can progress.
From “The Myth of the Framework” (1994), Models, Instruments and Truth (orig 1963)
As to the rationality of science, this is simply the rationality of critical discussion. Indeed there is nothing, I think, which can better explain the somewhat abstract idea of rationality than the example of a well-conducted critical discussion. And a critical discussion is well-conducted if it is entirely devoted to one aim: to find a flaw in the claim that a certain theory presents a solution to a certain problem. The scientists participating in the critical discussion constantly try to refute the theory, or at least its claim that it can solve its problem.
It is most important to see that a critical discussion always deals with more than one theory at a time. For in trying to assess the merits or demerits even of one theory, it always must try to judge whether the theory in question is an advance: whether it explains things which we have been unable to explain so far – that is to say, with the help of older theories. But of course there is often (in fact, always) more than one new theory competing at a time, in which case the critical discussion tries to assess their comparative merits and demerits. Older theories, however, always play an important part in the critical discussion, especially those theories which form part of the ‘background knowledge’ of the discussion – theories which, for the time being, are not criticized, but are used as the framework within which the discussion takes place. Any single one of these background theories may however he challenged at any time (though not too many at the same time), and thus move into the foreground of the discussion. Though there is always a background, any particular part of the background may at any time lose its background character.
Thus critical discussion is essentially a comparison of the merits and demerits of two or more theories (usually more than two). The merits discussed are, mainly, the explanatory power of the theories (discussed at some length in my Logic of Scientific Discovery) – the way in which they are able to solve our problems of explaining things, the way in which the theories cohere with certain other highly valued theories, their power to shed new light on old problems and to suggest new problems. The chief demerit is inconsistency, including inconsistency with the results of experiments that a competing theory can explain,
It will be seen from this that critical discussion will often be undecided, and that there do not exist very definite criteria for tentative acceptability: that the frontier of science is very fluid.
Thus the result of a scientific discussion is very often inconclusive, not only in the sense that we cannot conclusively verify (or even falsify) any of the theories under discussion – this should by now be obvious – but also in the sense that we cannot say that one of our theories seems to have definite advantages over its competitors. if we are lucky, however, we may sometimes come to the conclusion that one of the theories has greater merits and lesser demerits than the others. (In this case some people say that the theory is ‘accepted’ – of course, only for the time being.)
From this analysis of the process of the critical discussion of theories it should be clear that the discussion never considers the question whether a theory is Justified’ in the sense that we are justified in accepting it as true. At best, the critical discussion justifies the claim that the theory in question is the best available, or, in other words, that it comes nearest to the truth.
Thus although we can judge theories only ‘relatively’ in the sense that we compare them with each other (and not with the truth, which we do not know), this does not mean that we are relativists (in the sense of the famous phrase that ‘truth is relative’). On the contrary, in comparing them, we try to find the one which we judge comes nearest to the (unknown) truth. So the idea of truth (of an `absolute’ truth) plays a most important part in our discussion. It is our main regulative idea. Though we can never justify the claim to have reached truth, we can often give some very good reasons, or justification, why one theory should be judged to be nearer to it than another.
From “Conjectures and Refutations” (1963)
Page 235 – Chapter 10 Truth, Rationality, and the Growth of Knowledge, XIII
It always remains possible, of course, that we shall make mistakes in our relative appraisal of two theories, and the appraisal will often be a controversial matter. This point can hardly be over-emphasized. Yet it is also important that in principle, and as long as there are no revolutionary changes in our background knowledge, the relative appraisal of our two theories, t1 and t2 , will remain stable. More particularly, our preferences need not change, as we have seen, if we eventually refute the better of the two theories. Newton’s dynamics, for example, even though we may regard it as refuted, has of course maintained its superiority over Kepler’s and Galileo’s theories. The reason is its greater content or explanatory power. Newton’s theory continues to explain more facts than did the others; to explain them with greater precision; and to unify the previously unconnected problems of celestial and terrestrial mechanics. The reason for the stability of relative appraisals such as these is quite simple: the logical relation between the theories is of such a character that, first of all, there exist with respect to them those crucial experiments, and these, when carried out, went against Newton’s predecessors. And secondly, it is of such a character that the later refutations of Newton’s theory could not support the older theories: they either did not affect them, or (as with the perihelion motion of Mercury) they could be claimed to refute the predecessors also.
Page 248 – XXII
While the verificationists or inductivists in vain try to show that scientific beliefs can be justified or, at least, established as probable (and so encourage, by their failure, the retreat into irrationalism), we of the other group have found that we do not even want a highly probable theory. Equating rationality with the critical attitude, we look for theories which, however fallible, progress beyond their predecessors; which means that they can be more severely tested, and stand up to some of the new tests. And while the verificationists laboured in vain to discover valid positive arguments in support of their beliefs, we for our part are satisfied that the rationality of a theory lies in the fact that we choose it because it is better than its predecessors; because it can be put to more severe tests; because it may even have passed them, if we are fortunate; and because it may, therefore, approach nearer to the truth.
Page 387 – Addenda Some Technical Notes 1. Empirical Content
Empiricists usually believed that the empirical basis consisted of absolutely ‘given’ perceptions or observations, of ‘data’, and that science could build on these data as if on rock. In opposition, I pointed out that the apparent ‘data’ of experience were always interpretations in the light of theories, and therefore affected by the hypothetical or conjectural character of all theories.
That those experiences which we call ‘perceptions’ are interpretations-interpretations, I suggest, of the total situation in which we find ourselves when ‘perceiving’ is an insight due to Kant. It has often been formulated, somewhat awkwardly, by saying that perceptions are interpretations of what is given to us by our senses; and from this formulation sprang the belief that there must be present some ultimate ‘data’, some ultimate material which must be uninterpreted (since interpretation must be of something, and since there cannot be an infinite regress). But this argument does not take into account that (as already suggested by Kant) the process of interpretation is at least partly physiological, so that there are never any uninterpreted data experienced by us: the existence of these uninterpreted ‘data’ is therefore a theory, not a fact of experience, and least of all an ultimate, or ‘basic’ fact.
Thus there is no uninterpreted empirical basis; and the test statements which form the empirical basis cannot be statements expressing uninterpreted ‘data’ (since no such data exist) but are, simply, statements which state observable simple facts about our physical environment. They are, of course, facts interpreted in the light of theories; they are soaked in theory, as it were.
As I pointed out in my Logic of Scientific Discovery (end of section 25), the statement ‘Here is a glass of water’, cannot be verified by any observational experience. The reason is that the universal terms which occur in this statement (‘glass’, ‘water’) are dispositional: they ‘denote physical bodies which exhibit a certain law-like behaviour.
From “Objective Knowledge” (1972)
Page 20 – Chapter 1. Conjectural Knowledge, Section 8 Corroboration: The Merits of Improbability
The fundamental difference between my approach and the approach for which I long ago introduced the label `inductivist’ is that I lay stress on negative arguments, such as negative instances or counter-examples, refutations, and attempted refutations – in short, criticism – while the inductivist lays stress on `positive instances’, from which he draws ‘non-demonstrative inferences’ , and which he hopes will guarantee the ‘reliability’ of the conclusions of these inferences. In my view, all that can possibly be ‘positive’ in our scientific knowledge is positive only in so far as certain theories are, at a certain moment of time, preferred to others in the light of our critical discussion which consists of attempted refutations, including empirical tests. Thus even what may be called ‘positive’ is so only with respect to negative methods.
From “Realism and the Aim of Science” (1983)
Page 65 – Chapter 1 Induction, Section 4 A Family of Four Problems III
Accordingly, I should not expect that a more highly corroborated theory will as a rule outlive a less well corroborated theory. The life expectancy of a theory does not, I think, grow with its degree of corroboration, or with its past power to survive tests.
But do I not (I will be asked) expect the sun to rise tomorrow, or do I not base my predictions on the laws of motion? Of course I do, because they are the best laws available, as discussed at length above. Even where I have theoretical doubts, I shall base my actions (if I have to act – that is, to choose) on the choice of the best theory available. Thus I should be prepared to bet on the sun’s rising tomorrow (betting is a practical action), but not on the laws of Newtonian (or Einsteinian) mechanics to survive future criticism, or to survive it longer than, say, the best available theory of synaptic transmission, even though the latter has (or so it seems) a lesser degree of corroboration. As to practical actions (such as betting on predictions made by these theories), I should be ready to base them in both cases on the best theory in its field, provided it has been well tested.
The matter can also be put like this. The question of survival of a theory is a matter pertaining to its historical fate, and thus to the history of science. On the other hand, its use for prediction is a matter connected with its application. These two questions are related, but not intimately. For we often apply theories without any hesitation even if they are dead – that is falsified – as long as they are sufficiently good approximations for the purpose in hand. Thus there is nothing paradoxical in my readiness to bet on applications of a theory combined with a refusal to bet on the survival of the same theory.
My refusal to bet on the survival of a well corroborated theory shows that I do not draw any inductive conclusion from past survival to future survival.
page 71 Chapter 1 Induction, Section 4 A Family of Four Problems VI
I have replaced the problem “How do you know? What is the reason or justification, for your assertion?” by the problem: “Why do you prefer this conjecture to competing conjectures? What is the reason for your preference?”
While my answer to the first question is “I do not know”, my answer to the second problem is that, as a rule our preference for a better corroborated theory will be defended rationally by those arguments which have been used in our critical discussion, including of course our discussion of the results of tests. These are the arguments of which the degree of corroboration is intended to provide a summary report.
In this way the logical problem of induction is solved.
From “Unended Quest” (1974), standalone printing. Unended Quest is the autobiography included in the two volume Schilpp “The Philosophy of Karl Popper”
Page 103 Chapter 20 Truth; Probability; Corroboration
I regarded (and I still regard) the degree of corroboration of a theory merely as a critical report on the quality of past performance: it could not be used to predict future performance. (The theory, of course, may help us to predict future events.) Thus it had a time index: one could only speak of the degree of corroboration of a theory at a certain stage of its critical discussion. In some cases it provided a very good guide if one wished to assess the relative merits of two or more competing theories in the light of past discussions. When faced with the need to act, on one theory or another, the rational choice was to act on that theory – if there was one – which so far had stood up to criticism better than its competitors had: there is no better idea of rationality than that of a readiness to accept criticism; that is, criticism which discusses the merits of competing theories from the point of view of the regulative idea of truth.
Accordingly, the degree of corroboration of a theory is a rational guide to practice. Although we cannot justify a theory – that is, justify our belief in its truth – we can sometimes justify our preference for one theory over another; for example if its degree of corroboration is greater.
I have been able to show, very simply, that Einstein’s theory is (at least at the moment of writing) preferable to Newton’s, by showing that its degree of corroboration is greater.
A decisive point about degree of corroboration was that, because it increased with the severity of tests, it could be high only for theories with a high degree of testability or content. But this meant that degree of corroboration was linked to improbability rather than to probability: it was thus impossible to identify it with probability (although it could be deﬁned in terms of probability – as can improbability).
All these problems were opened, or dealt with, in Logik der Forschung; but I felt that there was more to be done about them, and that an axiomatization of the probability calculus was the thing I should do next.
from P. A. Schilpp, “The Philosophy of Karl Popper” (1974)
Page 1024 + Replies to My Critics -Section 14 The Psychological and Pragmatic Problems of Induction
It is, I think, hardly open to serious doubt that we are fitted with an immensely rich genetic endowment which, among other things, makes us most eager to generalize and to look out for regularities; and also, to apply the method of trial and error. Now I assert that all learning of new things is by the selective elimination of error rather than by instruction. (I do not deny that there exists what Konrad Lorenz calls imprinting; but this is very different from inductive instruction through repetition.) I assert, moreover, that this is an application of what I have called the principle of transference from logic to psychology – the principle that what is true in logic must, by and large, be true in psychology.
My solution of the logical problem of induction was that we may have preferences for certain of the competing conjectures; that is, for those which are highly informative and which so far have stood up to eliminative criticism. These preferred conjectures are the result of selection, of the struggle for survival of the hypotheses under the strain of criticism, which is artificially intensified selection pressure.
The same holds for the psychological problem of induction. Here too we are faced with competing hypotheses, which may perhaps be called beliefs, and some of them are eliminated, while others survive, anyway for the time being. Animals are often eliminated along with their beliefs; or else they survive with them. Men frequently outlive their beliefs; but for as long as the beliefs survive (often a very short time), they form the (momentary or lasting) basis of action.
My central thesis is that this Darwinian procedure of the selection of beliefs and actions can in no sense be described as irrational. In no way does it clash with the rational solution of the logical problem of induction. Rather, it is just the transference of the logical solution to the psychological field. (This does not mean, of course, that we never suffer from what are called “irrational beliefs”.)
Thus with an application of the principle of transference to Hume’s psychological problem Hume’s irrationalist conclusions disappear.
In talking of preference I have so far discussed only the theoretician’s preference – if he has any; and why it will be for the “better”, that is, more testable, theory, and for the better tested one. Of course, the theoretician may not have any preference: he may be discouraged by Hume’s, and my, “sceptical” solution to Hume’s logical problem; he may say that, if he cannot make sure of finding the true theory among the competing theories, he is not interested in any method like the one described – not even if the method makes it reasonably certain that, if a true theory should be among the theories proposed, it will be among the surviving, the preferred, the corroborated ones. Yet a more sanguine or more dedicated or more curious “pure” theoretician may well be encouraged, by our analysis, to propose again and again new competing theories in the hope that one of them may be true – even if we shall never be able to make sure of any one that it is true.
Thus the pure theoretician has more than one way of action open to him; and he will choose a method such as the method of trial and the elimination or error only if his curiosity exceeds his disappointment at the unavoidable uncertainty and incompleteness of all our endeavours.
It is different with him qua man of practical action. For a man of practical action has always to choose between some more or less definite alternatives, since even inaction is a kind of action.
But every action presupposes a set of expectations, that is, of theories about the world. Which theory shall the man of action choose? Is there such a thing as a rational choice?
This leads us to the pragmatic problems of induction, which to start with, we might formulate thus:
(a) Upon which theory should we rely for practical action, from a rational point of view?
(b) Which theory should we prefer for practical action, from a rational point of view?
My answer to (a) is: from a rational point of view, we should not “rely” on any theory, for no theory has been shown to be true, or can be shown to be true (or “reliable”).
My answer to (b) is: we should prefer the best tested theory as a basis for action.
In other words, there is no “absolute reliance”; but since we have to choose, it will be “rational” to choose the best tested theory. This will be “rational” in the most obvious sense of the word known to me: the best tested theory is the one which, in the light of our critical discussion, appears to be the best so far; and I do not know of anything more “rational” than a well-conducted critical discussion.
Since this point appears not to have got home I shall try to restate it here in a slightly new way, suggested to me by David Miller. Let us forget momentarily about what theories we “use” or “choose” or “base our practical actions on”, and consider only the resulting proposal or decision (to do X, not to do X; to do nothing; or so on). Such a proposal can, we hope, be rationally criticized; and if we are rational agents we will want it to survive, if possible, the most testing criticism we can muster. But such criticism will freely make use of the best tested scientific theories in our possession. Consequently any proposal that ignores these theories (where they are relevant, I need hardly add) will collapse under criticism. Should any proposal remain, it will be rational to adopt it.
This seems to me all far from tautological.” Indeed, it might well be challenged by challenging the italicized sentence in the last paragraph. Why, it might be asked, does rational criticism make use of the best tested although highly unreliable theories? The answer, however, is exactly the same as before. Deciding to criticize a practical proposal from the standpoint of modern medicine (rather than, say, in phrenological terms) is itself a kind of “practical” decision (anyway it may have practical consequences). Thus the rational decision is always: adopt critical methods that have themselves withstood severe criticism.
There is, of course, an infinite regress here. But it is transparently harmless.
Now I do not particularly want to deny (or, for that matter, assert) that, in choosing the best tested theory as a basis for action, we “rely” on it, in some sense of the word. It may therefore even be described as the most “reliable” theory available, in some sense of this term. Yet this is not to say that it is “reliable”. It is “unreliable” at least in the sense that we shall always do well, even in practical action, to foresee the possibility that something may go wrong with it and with our expectations.
But it is not merely this trivial caution which we must derive from our negative reply to the pragmatic problem (a). Rather, it is of the utmost importance for the understanding of the whole problem, and especially of what I have called the traditional problem, that in spite of the “rationality” of choosing the best tested theory as a basis of action, this choice is not “rational” in the sense that it is based upon good reasons in favour of the expectation that it will in practice be a successful choice: there can be no good reasons in this sense, and this is precisely Hume’s result. On the contrary, even if our physical theories should be true, it is perfectly possible that the world as we know it, with all its pragmatically relevant regularities, may completely disintegrate in the next second. This should be obvious to anybody today; but I said so before Hiroshima: there are infinitely many possible causes of local, partial, or total disaster.
From a pragmatic point of view, however, most of these possibilities are obviously not worth bothering about because we cannot do anything about them: they are beyond the realm of action. (I do not, of course, include atomic war among those disasters which are beyond the realm of human action, although most of us think just in this way since we cannot do more about it than about an act of God.)
All this would hold even if we could be certain that our physical and biological theories were true. But we do not know it. On the contrary, we have very good reason to suspect even the best of them; and this adds, of course, further infinities to the infinite possibilities of catastrophe.
It is this kind of consideration which makes Hume’s and my own negative reply so important. For we can now see very clearly why we must beware lest our theory of knowledge proves too much. More precisely, no theory of knowledge should attempt to explain why we are successful in our attempts to explain things.
Even if we assume that we have been successful-that our physical theories are true – we can learn from our cosmology how infinitely improbable this success is: our theories tell us that the world is almost completely empty, and that empty space is filled with chaotic radiation. And almost all places which are not empty are occupied either by chaotic dust, or by gases, or by very hot stars – all in conditions which seem to make the application of any physical method of acquiring knowledge impossible.
There are many worlds, possible and actual worlds, in which a search for knowledge and for regularities would fail. And even in the world as we actually know it from the sciences, the occurrence of conditions under which life, and a search for knowledge, could arise-and succeed-seems to be almost infinitely improbable. Moreover, it seems that if ever such conditions should appear, they would be bound to disappear again, after a time which, cosmologically speaking, is very short.
It is in this sense that induction is inductively invalid, as I said above, in section 13, subsection I. That is to say, any strong positive reply to Hume’s logical problem (say, the thesis that induction is valid) would be paradoxical. For, on the one hand, if induction is the method of science, then modern cosmology is at least roughly correct (I do not dispute this); and on the other, modern cosmology teaches us that to generalize from observations taken, for the most part, in our incredibly idiosyncratic region of the universe would almost always be quite invalid. Thus if induction is “inductively valid” it will almost always lead to false conclusions; and therefore it is inductively invalid.