I got my Ph.D. in 1928, and in 1929 I qualified as a teacher of mathematics and physical science in (lower) secondary schools. For this qualifying examination I wrote a thesis on problems of axiomatics in geometry, which also contained a chapter on non-Euclidean geometry.
It was only after my Ph.D. examination that I put two and two together, and my earlier ideas fell into place. I understood why the mistaken theory of science which had ruled since Bacon—that the natural sciences were the inductive sciences, and that induction was a process of establishing or justifying theories by repeated observations or experiments—was so deeply entrenched. The reason was that scientists had to demarcate their activities from pseudoscience as well as from theology and metaphysics, and they had taken over from Bacon the inductive method as their criterion of demarcation. (On the other hand, they were anxious to justify their theories by an appeal to sources of knowledge comparable in reliability to the sources of religion.) But I had held in my hands for many years a better criterion of demarcation: testability or falsifiability.
Thus I could discard induction without getting into trouble over demarcation. And I could apply my results concerning the method of trial and error in such a way as to replace the whole inductive methodology by a deductive one. The falsification or refutation of theories through the falsification or refutation of their deductive consequences was, clearly, a deductive inference (modus tollens). This view implied that scientific theories, if they are not falsified, for ever remain hypotheses or conjectures.
Thus the whole problem of scientific method cleared itself up, and with it the problem of scientific progress. Progress consisted in moving towards theories which tell us more and more—theories of ever greater content. But the more a theory says the more it excludes or forbids, and the greater are the opportunities for falsifying it. So a theory with greater content is one which can be more severely tested. This consideration led to a theory in which scientific progress turned out not to consist in the accumulation of observations but in the overthrow of less good theories and their replacement by better ones, in particular by theories of greater content. Thus there was competition between theories—a kind of Darwinian struggle for survival.
Of course theories which we claim to be no more than conjectures or hypotheses need no justification (and least of all a justification by a nonexistent “method of induction”, of which nobody has ever given a sensible description). We can, however, sometimes give reasons for preferring one of the competing conjectures to the others, in the light of their critical discussion.98
All this was straightforward and, if I may say so, highly coherent. But it was very different from what the Machian positivists and the Wittgensteinians of the Vienna Circle were saying. I had heard about the Circle in 1926 or 1927, first from a newspaper article by Otto Neurath and then in a talk he gave to a social democratic youth group. (This was the only party meeting I ever attended; I did so because I had known Neurath a little since 1919 or 1920.) I had read the programmatic literature of the Circle, and of the Verein Ernst Mach; in particular a pamphlet by my teacher, the mathematician Hans Hahn. In addition I had read Wittgenstein’s Tractatus, some years before writing my Ph.D. thesis, and Carnap’s books as they were published.
It was clear to me that all these people were looking for a criterion of demarcation not so much between science and pseudoscience as between science and metaphysics. And it was also clear to me that my old criterion of demarcation was better than theirs. For, first of all, they were trying to find a criterion which made metaphysics meaningless nonsense, sheer gibberish, and any such criterion was bound to lead to trouble, since metaphysical ideas are often the forerunners of scientific ones. Secondly, demarcation by meaningfulness versus meaninglessness merely shifted the problem. As the Circle recognized, it created the need for another criterion, one to distinguish between meaning and lack of meaning. For this, they had adopted verifiability, which was taken as being the same as provability by observation statements. But this was only another way of stating the time-honoured criterion of the inductivists; there was no real difference between the ideas of induction and of verification. Yet according to my theory, science was not inductive; induction was a myth which had been exploded by Hume. (A further and less interesting point, later acknowledged by Ayer, was the sheer absurdity of the use of verifiability as a meaning criterion: how could one ever say that a theory was gibberish because it could not be verified? Was it not necessary to understand a theory in order to judge whether or not it could be verified? And could an understandable theory be sheer gibberish?) All this made me feel that, to every one of their main problems, I had better answers—more coherent answers—than they had.
Perhaps the main point was that they were positivists, and therefore epistemological idealists in the Berkeley-Mach tradition. Of course they did not admit that they were idealists. They described themselves as “neutral monists”. But in my opinion this was merely another name for idealism—and in Carnap’s books99 idealism (or, as he called it, methodological solipsism) was pretty openly accepted as a kind of working hypothesis.
I wrote (without publishing) a great amount on these issues, working through Carnap’s and Wittgenstein’s books in considerable detail. From the point of view I had reached this turned out to be fairly straightforward. I knew only one man to whom I could explain these ideas, and that was Heinrich Gomperz. In connection with one of my main points—that scientific theories always remain hypotheses or conjectures—he referred me to Alexis Meinong, On Assumptions (Über Annahmen, 1902), which I found not only to be psychologistic but also to assume implicitly—as did Husserl in his Logical Investigations (Logische Untersuchungen, 1900, 1901)—that scientific theories are true. For years I found that people had great difficulty in admitting that theories are, logically considered, the same as hypotheses. The prevailing view was that hypotheses are as yet unproved theories, and that theories are proved, or established, hypotheses. And even those who admitted the hypothetical character of all theories still believed that they needed some justification; that, if they could not be shown to be true, their truth had to be highly probable.
The decisive point in all this, the hypothetical character of all scientific theories, was to my mind a fairly commonplace consequence of the Einsteinian revolution, which had shown that not even the most successfully tested theory, such as Newton’s, should be regarded as more than a hypothesis, an approximation to the truth.
In connection with my espousal of deductivism—the view that theories are hypothetico-deductive systems, and that the method of science is not inductive—Gomperz referred me to Professor Victor Kraft, a member of the Vienna Circle and author of a book on The Basic Forms of Scientific Method.100 This book was a most valuable description of a number of the methods actually used in science, and it showed that at least some of these methods are not inductive but deductive—hypothetico-deductive. Gomperz gave me an introduction to Victor Kraft (no relation to Julius Kraft) and I met him several times in the Volksgarten, a park near the University. Victor Kraft was the first member of the Vienna Circle I met (unless I include Zilsel, who, according to Feigl101 was not a member). He was ready to pay serious attention to my criticisms of the Circle—more so than most of the members I met later. But I remember how shocked he was when I predicted that the philosophy of the Circle would develop into a new form of scholasticism and verbalism. This prediction has, I think, come true. I am alluding to the programmatic view that the task of philosophy is “the explication of concepts”.
In 1929 or 1930 (in the latter year I was, at last, appointed to a teaching position in a secondary school) I met another member of the Vienna Circle, Herbert Feigl.102 The meeting, arranged by my uncle Walter Schiff, Professor of Statistics and Economics at the University of Vienna, who knew of my philosophical interests, became decisive for my whole life. I had found some encouragement before in the interest shown by Julius Kraft, Gomperz, and Victor Kraft. But although they knew that I had written many (unpublished) papers,103 none of them had encouraged me to publish my ideas. Gomperz had indeed impressed upon me the fact that publishing any philosophical ideas was hopelessly difficult. (Times have changed.) This was supported by the fact that Victor Kraft’s great book on the methods of science had been published only with the support of a special fund.
But Herbert Feigl, during our nightlong session, told me not only that he found my ideas important, almost revolutionary, but also that I should publish them in book form.104
It had never occurred to me to write a book. I had developed my ideas out of sheer interest in the problems, and then written some of them down for myself because I found that this was not only conducive to clarity but necessary for self-criticism. At that time I looked upon myself as an unorthodox Kantian, and as a realist.105 I conceded to idealism that our theories are actively produced by our minds rather than impressed upon us by reality, and that they transcend our “experience”; yet I stressed that a falsification may be a head-on clash with reality. I also interpreted Kant’s doctrine of the impossibility of knowing things in themselves as corresponding to the for ever hypothetical character of our theories. I also regarded myself as a Kantian in ethics. And I used to think in those days that my criticism of the Vienna Circle was simply the result of having read Kant, and of having understood some of his main points.
I think that without encouragement from Herbert Feigl it is unlikely that I should ever have written a book. Writing a book did not fit my way of life nor my attitude towards myself. I just did not have the confidence that what interested me was of sufficient interest to others. Moreover, nobody encouraged me after Feigl left for America. Gomperz, to whom I told the story of my exciting meeting with Feigl, definitely discouraged me, and so did my father, who was afraid that it all would end in my becoming a journalist. My wife opposed the idea because she wanted me to use any spare time to go skiing and mountain climbing with her—the things we both enjoyed most. But once I started on the book she taught herself to type, and she has typed many times everything I have written since. (I have always been unable to get anywhere when typing—I am in the habit of making far too many corrections.)
The book I wrote was devoted to two problems—the problems of induction and of demarcation—and their interrelation. So I called it The Two Fundamental Problems of the Theory of Knowledge (Die beiden Grundprobleme der Erkenntnistheorie), an allusion to a title of Schopenhauer’s (Die beiden Grundprobleme der Ethik).
As soon as I had a number of chapters typed I tried them out on my friend and onetime colleague at the Pedagogic Institute, Robert Lammer. He was the most conscientious and critical reader I have ever come across: he challenged every point which he did not find crystal clear, every gap in the argument, every loose end I had left. I had written my first draft pretty quickly, but thanks to what I learned from Lammer’s insistent criticism I never again wrote anything quickly. I also learned never to defend anything I had written against the accusation that it is not clear enough. If a conscientious reader finds a passage unclear, it has to be rewritten. So I acquired the habit of writing and rewriting, again and again, clarifying and simplifying all the time. I think I owe this habit almost entirely to Robert Lammer. I write, as it were, with somebody constantly looking over my shoulder and constantly pointing out to me passages which are not clear. I know of course very well that one can never anticipate all possible misunderstandings; but I think one can avoid some misunderstandings, assuming readers who want to understand.
Through Lammer I had earlier met Franz Urbach, an experimental physicist working at the University of Vienna’s Institute for Radium Research. We had many common interests (music among them), and he gave me much encouragement. He also introduced me to Fritz Waismann, who had been the first to formulate the famous criterion of meaning with which the Vienna Circle was identified for so many years—the verifiability criterion of meaning. Waismann was very interested in my criticism. I believe it was through his initiative that I received my first invitation to read some papers criticizing the views of the Circle in some of the “epicyclic” groups which formed its halo, so to speak.
The Circle itself was, so I understood, Schlick’s private seminar, meeting on Thursday evenings. Members were simply those whom Schlick invited to join. I was never invited, and I never fished for an invitation.106 But there were other groups, meeting in Victor Kraft’s or Edgar Zilsel’s apartments, and in other places; and there was also Karl Menger’s famous “mathematisches Colloquium”. Several of these groups, of whose existence I had not even heard, invited me to present my criticisms of the central doctrines of the Vienna Circle. It was in Edgar Zilsel’s apartment, in a crowded room, that I read my first paper. I still remember the stage fright.
In some of those early talks I also discussed problems connected with the theory of probability. Of all existing interpretations I found the so-called “frequency interpretation” the most convincing, and Richard von Mises’s form of it the one which seemed most satisfactory. But there were still a number of difficult problems left open, especially if one looked at it from the point of view that statements about probability are hypotheses. The central question then was: are they testable? I tried to discuss this and some subsidiary questions, and I have worked on various improvements of my treatment of them ever since.107 (Some are still unpublished.)
Several members of the Circle, some of whom had been at these meetings, invited me to discuss these points with them personally. Among them were Hans Hahn, who had so impressed me through his lectures, and Philipp Frank and Richard von Mises (on their frequent visits to Vienna). Hans Thirring, the theoretical physicist, invited me to address his seminar; and Karl Menger invited me to become a member of his colloquium. It was Karl Menger (whom I had asked for advice on the point) who suggested to me that I should try to apply his theory of dimension to the comparison of degrees of testability.
Very early in 1932 I completed what I then regarded as the first volume of The Two Fundamental Problems of the Theory of Knowledge. It was conceived, from the beginning, largely as a critical discussion and as a correction of the doctrines of the Vienna Circle; long sections were also devoted to criticisms of Kant and of Fries. The book, which is still unpublished, was read first by Feigl and then by Carnap, Schlick, Frank, Hahn, Neurath, and other members of the Circle; and also by Gomperz.
Schlick and Frank accepted the book in 1933 for publication in the series Schriften zur wissenschaftlichen Weltauffassung of which they were the editors. (This was a series of books most of which were written by members of the Vienna Circle.) But the publishers, Springer, insisted that it must be radically shortened. By the time the book was accepted I had written most of the second volume. This meant that little more than an outline of my work could be given within the number of pages the publishers were prepared to publish. With the agreement of Schlick and Frank I put forward a new manuscript which consisted of extracts from both volumes. But even this was returned by the publishers as too long. They were insisting on a maximum of fifteen sheets (two hundred and forty pages). The final extract—which was ultimately published as Logik der Forschung—was made by my uncle, Walter Schiff, who ruthlessly cut about half the text.108 I do not think that, after having tried so hard to be clear and explicit, I could have done this myself.
I can hardly give here an outline of that outline which became my first published book. But there are one or two points I will mention. The book was meant to provide a theory of knowledge and, at the same time, to be a treatise on method—the method of science. The combination was possible because I looked on human knowledge as consisting of our theories, our hypotheses, our conjectures; as the product of our intellectual activities. There is of course another way of looking at “knowledge”: we can regard “knowledge” as a subjective “state of mind”, as a subjective state of an organism. But I chose to treat it as a system of statements—theories submitted to discussion. “Knowledge” in this sense is objective; and it is hypothetical or conjectural.
This way of looking at knowledge made it possible for me to reformulate Hume’s problem of induction. In this objective reformulation the problem of induction is no longer a problem of our beliefs—or of the rationality of our beliefs—but a problem of the logical relationship between singular statements (descriptions of “observable” singular facts) and universal theories.
In this form, the problem of induction becomes soluble:109 there is no induction, because universal theories are not deducible from singular statements. But they may be refuted by singular statements, since they may clash with descriptions of observable facts.
Moreover, we may speak of “better” and of “worse” theories in an objective sense even before our theories are put to the test: the better theories are those with the greater content and the greater explanatory power (both relative to the problems we are trying to solve). And these, I showed, are also the better testable theories; and—if they stand up to tests—the better tested theories.
This solution of the problem of induction gives rise to a new theory of the method of science, to an analysis of the critical method, the method of trial and error: the method of proposing bold hypotheses, and exposing them to the severest criticism, in order to detect where we have erred.
From the point of view of this methodology, we start our investigation with problems. We always find ourselves in a certain problem situation; and we choose a problem which we hope we may be able to solve. The solution, always tentative, consists in a theory, a hypothesis, a conjecture. The various competing theories are compared and critically discussed, in order to detect their shortcomings; and the always changing, always inconclusive results of the critical discussion constitute what may be called “the science of the day”.
Thus there is no induction: we never argue from facts to theories, unless by way of refutation or “falsification”. This view of science may be described as selective, as Darwinian. By contrast, theories of method which assert that we proceed by induction or which stress verification (rather than falsification) are typically Lamarckian: they stress instruction by the environment rather than selection by the environment.
It may be mentioned (although this was not a thesis of Logik der Forschung) that the proposed solution of the problem of induction also shows the way to a solution of the older problem—the problem of the rationality of our beliefs. For we may first replace the idea of belief by that of action; and we may say that actions (or inactions) are “rational” if they are carried out in accordance with the state, prevailing at the time, of the critical scientific discussion. There is no better synonym for “rational” than “critical”. (Belief, of course, is never rational: it is rational to suspend belief; cp. note 226 below.)
My solution of the problem of induction has been widely misunderstood. I intend to say more about it in my Replies to my Critics.109a