The Structure of Scientific Inference

By Mary Hesse

This title is part of UC Press's Voices Revived program, which commemorates University of California Press’s mission to seek out and cultivate the brightest minds and give them voice, reach, and impact. Drawing on a backlist dating to 1893, Voices Revived makes high-quality, peer-reviewed scholarship accessible once again using print-on-demand technology. This title was originally published in 1974.

• Language: English
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Mary Hesse

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THE STRUCTURE

OF

SCIENTIFIC INFERENCE

by the same author

Science and the Human Imagination

Forces and Fields

Models and Analogies in Science

THE STRUCTURE

OF

SCIENTIFIC

INFERENCE

MARY HESSE

Woolfson College

and University of Cambridge

UNIVERSITY OF CALIFORNIA PRESS

Berkeley and Los Angeles 1974

University of California Press

Berkeley and Los Angeles, California

ISBN: 0-520-02582-2

Library of Congress Catalog Card Number: 73-85373

© M. B. Hesse 1974

pages 210-222 (© University of Minnesota Press 1970

All rights reserved. No part of

this publication may be reproduced

or transmitted, in any form or by

any means, without permission

Printed in Great Britain

Contents 1

Contents 1

Acknowledgments

Introduction THE TASK OF A LOGIC OF SCIENCE

CHAPTER ONE Theory and Observation 1. Is there an independent observation language?

II. Entrenchment

III. The network model

IV. Theoretical predicates

V. Theories

VI. Conclusion

CHAPTER TWO A Network Model of Universals 1. The problem of universals

II. The correspondence postulate

III. Coherence conditions

IV. Some epistemological consequences

V. Meaning-change

VI. Goodman’s strictures on similarity

VII. Absolute universals again

CHAPTER THREE The Grue Paradox I. Principles of solution

II. Objective tests of ‘grue'

III. Meaning variance and entrenchment

CHAPTER FOUR The Logic of Induction as Explication I. Hume s legacy

II. A more modest programme

III. Probabilistic confirmation

CHAPTER FIVE Personalist Probability I. Axioms and interpretation

II. Bayesian methods

III. Convergence of opinion

IV. Non-Bayesian transformations

V. Uncertain evidence

CHAPTER SIX Bayesian Confirmation Theory I. The positive relevance criterion

II. The transitivity paradox

III. Suggested resolutions

CHAPTER SEVEN Universal Generalizations I. Exchangeability and clustering

II. The raven paradoxes

III. Clustering in Carnap’s confirmation theory

IV. Extension to analogical argument

V. Causal laws and eliminative induction

CHAPTER EIGHT Finiteness, Laws and Causality 1. The distribution of initial probabilities

II. The probability of laws

III. The necessity of laws

CHAPTER NINE Theory as Analogy I. Some false moves: ‘acceptance’ and ‘explanation’

II. Deduction from phenomena

III. Whewell’s consilience of inductions

IV. The analogical character of theories

V. The function of models

VI. Identification of theoretical predicates

CHAPTER TEN Simplicity I. Subjective and notational simplicity

II. Content

III. Economy and clustering

IV. The principle of relativity and classical electrodynamics

V. Einstein’s logic of theory structure

VI. Summary

CHAPTER ELEVEN Maxwell’s Logic of Analogy I. Hypothetical, mathematical and analogical methods

II. Experimental identifications

III. The electrodynamic theory

IV. Meaning variance and experimental identifications

CHAPTER TWELVE A Realist Interpretation of Science I. The aims of science

II. From naive realism to pluralism

III. Realism and relativity

IV. The cumulative character of science

Index of Names

Index of Subjects

Acknowledgments

Some previously published material has been incorporated in this book: chapter i is reprinted from The Nature and Function of Scientific Theories, ed. R. G. Colodny (1970), 35-77, with permission of the editor and Pittsburgh University Press; chapter 3 is adapted from ‘Ramifications of grue Brit. J. Phil. Sci., 20 (1969), 13-25, with permission of the Cambridge University Press; parts of chapters 5 and 6 will appear in volume 6 of Minnesota Studies in the Philosophy of Science, ed. G. Maxwell (University of Minnesota Press); part of chapter 8 is reprinted from ‘Confirmation of laws’, in Philosophy, Science, and Method, ed. S. Morgenbesser, P. Suppes and M. White (1969), 74-91, with permission of St Martin’s Press; part of chapter 9 is reprinted from ‘An inductive logic of theories’, Minnesota Studies in the Philosophy of Science, vol. 4, ed. M. Radner and S. Winokur (1970), 164-180, with permission of the University of Minnesota Press; and chapter 11 is reprinted from Foundations of Scientific Method, ed. R. Giere and R. S. Westfall (1973), 86-114, with permission of Indiana University Press. All these permissions to reprint are gratefully acknowledged.

Formal and informal discussions with many friends and colleagues have contributed decisively to anything that is of value in this book. Among many others I should like specially to acknowledge the help and continuing collaboration of Gerd Buchdahl, Hugh Mellor and Robert Young. David Bloor and Allan Birnbaum saved me from many pitfalls in chapters 1 and 5-7 respectively, and I am indebted to Elliot Sober for long discussions on the subject matter of chapter 10. I am deeply grateful to the University of Notre Dame Philosophy Department for enabling me to spend a peaceful and intellectually active semester on their beautiful campus in the spring of 1972, and especially to Ernán McMullin, Gary Gutting and Vaughan McKim, and to the members of the graduate seminar who were exposed to much of the book in embryo. My gratitude is also due to Mrs Verna Cole and Mrs B. Reeson for doing the typing. Responsibility for the finished product is, of course, all my own.

Cambridge April 1973

Introduction

THE TASK OF A LOGIC OF SCIENCE

The modern analytic style in philosophy of science is the product of an era in which confidence in natural science was at its height. In both nineteenth-century positivism and twentieth-century logical positivism the only recognized mode of knowledge was the scientific, together with those extensions of the scientific which could plausibly be claimed to be modelled on its methods. Classic problems of the theory of knowledge were brushed aside by appeal to the scientific consensus of ‘observation’; metaphysics was dismissed as unintelligible because untestable by experience; experience itself was reduced to the narrowest and most superficial domain of agreed sense-experience; and introspection, insight and creativity had their place only in subjective psychology, not in philosophy or logic.

Doubts about the adequacy of this positivist epistemology arose within the analysis of science itself, first with regard to its theoretical components, and then increasingly with regard to its observational basis. It was soon found to be impossible to devise logical criteria of ‘verifiability’ for scientific theories which do not admit either too little or too much. Either all concepts not derived directly from observation were excluded by such criteria—manifestly distorting the nature of theoretical science—or else the attempt to liberalize the notion of verification in order to include theoretical concepts was found to readmit as meaningful the metaphysics and the nonsense which verification had been designed to exclude.

Popper concluded from this development that the problem should be seen as one of demarcation of scientific from other forms of knowledge,1 thus significantly breaking with the positivist tradition that only science constitutes knowledge. His introduction in this context of the criterion of ‘falsifiability’ appeared to solve the immediate problem of demarcation, and led to the replacement of verificationism by the so-called hypothetico-deductwe model of science (or the deductive model for short). Here theories are held to be deductive in structure: their postulates and concepts are not necessarily

directly derived from observation, but they must be connected with observables by deductive (or, more generally, by deductive and statistical) chains of inference, in such a way that a theory can be falsified by modus tollens argument if any of its consequences turn out observationally to be false. 2 Problems remained, however, about the character and function of theoretical postulates and concepts. Are postulates derived merely by imaginative conjecture, as Popper maintained, or by some form of inductive reasoning? If theoretical concepts are not part of ordinary descriptive language, or immediately definable in terms of such language, how are they to be understood? What is it to be a theoretical explanation?

These problems were, however, quickly overtaken by a more fundamental issue. All positivist analyses had presupposed a common and easily intelligible ‘observation language’ which was at once the basis of, and the court of appeal for, all scientific theorizing. As early as 1906 Pierre Duhem 3 had implicitly questioned this basis by pointing out that experimental laws derived from observation form part of a network of mutually supporting laws, the whole of which may be used to correct and reinterpret even parts of its own observational basis. The same point was made by N. R. Campbell,⁴ who went on to propose a solution to the problem of the derivation and meaning of theoretical postulates and terms by regarding them as analogies or models drawn from the observationally familiar. Quine5 has pursued Duhem’s network analogy in increasingly far-reaching analyses of logical and scientific systems, culminating in influential studies of the problem of translation from the language of one total theory, including its observational component, to another, and from one total culture to another.

Other philosophers have drawn even more radical conclusions from the ‘holistic’ character of theory and interpretations of observation in the light of theory. In some of the most influential of these discussions, P. K.

Feyerabend6 has attacked what he calls the ‘pragmatic’ and the ‘phenomenological’ theories of meaning which are presupposed by those who wish to rest science respectively upon easily agreed observational reports, or upon ‘sense data’. Feyerabend goes on to reject the alleged stability and theoryindependence of the observation language, as had been universally presupposed in empiricist philosophy of science, and also to reject the claim of the deductive model that observation statements are strictly deducible from theories (even when these are non-statistical) and hence that if the observation statements are false they necessarily act as falsifiers of the theory from which they are deduced. On the contrary, Feyerabend argues, all interpretation of observation is ‘theory-laden’, and this includes even the common descriptive terms with which we form observation statements in natural language. For example, ‘light’ and ‘heavy’ mean something different for the Aristotelian and for the Newtonian, and ‘mass’ means something different in classical and in relativistic physics.

Feyerabend’s analysis is supported by historical examples intended to illustrate the ‘meaning variance’ of observational terms when infected by the concepts of radically different theories and cosmologies. The history of science has been used in a similar way by other writers to arrive at similar conclusions. For example, T. S. Kuhn 7 interprets the history of science as a succession of ‘paradigms’ imposed on nature and interspersed by ‘revolutions’ which are explainable not by a logic of scientific change but by the increasing complexity and anomaly of a previous paradigm and the impatience with it of a new generation, helped by cultural and social discontinuities. N. R. Hanson has given analyses of historical cases in science in terms of Wittgen- steinian ‘duck-rabbit’, or gestalt, switches, and S. E. Toulmin in terms of an evolutionary model of mutations and natural selection of scientific theories.⁸

Such studies are generally characterized not only by rejection of most of the presuppositions of positivist philosophy of science, but also by explicit rejection of the logical and analytic style in philosophy of science in favour of persuasive argument from historical examples, on the grounds that in the past logical formalism has grossly distorted the natural of ‘real science’. Some of these studies are also increasingly characterized by appeal to pragmatic, intuitive, subjective and ultimately polemical explanations and justifications of the development of science, and abandonment of the search for logical criteria of the empirical truth or falsity of science. Thus discussions of truth criteria are often replaced by descriptions of science wholly within its own context, without ‘external’ judgments of validity, or by judgments of science relative to the consensus of a scientific elite, or even by avowedly aesthetic or ‘hedonistic’ criteria.9

Romantic excesses in reaction to excessive logical pedantry and analytic subtlety are not unknown in the history of philosophy, and their lifetime is usually brief. The essays which follow in this book are not in a rigorously formal mode, but they are in a looser sense analytic in style and are intended to indicate a via media between the extremes of both formalism and historical relativism. In a series of papers over the last six or seven years I have attempted to develop a model of scientific theorizing which takes account of recent radical criticism but also retains the notions of empirical truth-value and of logical inference, particularly inductive inference. Some of the chapters which follow are reprinted from earlier papers, some are substantially new, and others provide linking and systematizing arguments.

The model of science developed here is essentially inductive, and it owes much to the network model first outlined by Duhem and adopted by Quine. Briefly, the model interprets scientific theory in terms of a network of concepts related by laws, in which only pragmatic and relative distinctions can be made between the ‘observable’ and the ‘theoretical’. Some lawlike statements of the system can be tested relatively directly by observation, but which these are may depend on the current state of the whole theory, and whether an observation statement is accepted as ‘true’ or ‘false’ in any given case may also depend on the coherence of the observation statement with the rest of the currently accepted theory. Both coherence and correspondence aspects of truth are involved here. The correspondence aspect requires that, at any given time in any given descriptive language, most but not necessarily all statements made on the basis of observation must be taken to be true, but at that time we shall not usually be able to identify which are the true statements. Which statements are taken to be true depends on coherence with a whole theoretical network. In this account theoretical concepts are introduced by analogy with the observational concepts constituting the natural descriptive language. Scientific language is therefore seen as a dynamic system which constantly grows by metaphorical extension of natural language, and which also changes with changing theory and with reinterpretation of some of the concepts of the natural language itself. In this way an empirical basis of science is maintained, without the inflexibility of earlier views, where the observation language was assumed to be given and to be stable.

The main problems that arise from the network model concern its analysis of the ‘meaning’ of observational and theoretical concepts, and of the ‘truth’ of statements containing them. In chapter i I attack some epistemological problems of the theses of theory-ladenness and meaning variance by explicitly directing attention to the problematic character of the observation language itself. On the basis of a reinterpretation of the notion of ‘observable’ in terms of the theoretical network, I try to reconstruct and provide solutions in general terms for some problems bequeathed by positivism and deductivism, namely the meaning and justification of theoretical terms, the relation between theory and observation, the role of models in theories, and the nature of explanation and reduction. In chapter 2 I relate the reinterpretation of observation terms to more traditional discussions of universals, sense and reference, intensions and extensions, and correspondence and coherence accounts of truth. The theory of universals assumed is essentially a resemblance theory, and depends on non-extensional recognition of similarities; therefore some defence is given of the notion of ‘similarity’ against recent critics, especially Goodman. Goodman’s ‘grue’ paradox stands in the way of any attempt to construe the observation language as an empirical basis of science, and so in chapter 3 I suggest a solution to this paradox which fits well with the network model, in that what counts as an ‘observation term’ is shown to be partially dependent on the whole context of theory. Anyone who wishes to claim that ‘gruified’ predicates form a basis for descriptive language or for inductive inference that is as valid as our usual predicates, is challenged to justify his choice in relation to a total physics which is non-trivially distinct from our physics.

The logical system that immediately suggests itself for the explication of inference in a network of theory and observation is the theory of probability. This is an obvious generalization of the deductive model of science, which, though inadequate as it stands, may certainly be seen as a first approximation to adequacy as a logic of science. In the deductive model, theory and observation are seen in terms of a hierarchy ordered by deductive inferences from theory to observation, but the deductive model as such gives no account of logical inference from observation to theory. In a probabilistic inductive model, on the other hand, the hierarchy is replaced by a system in which all statements are reciprocally related by conditional probability, of which deductive entailment is the limiting case. Probabilistic inference can therefore be seen as a generalization of deduction, permitting inductive and analogical as well as deductive forms of reasoning in the theoretical network.

Chapters 4, 5 and 6 lay the foundations of a probabilistic confirmation theory which can be used to analyse the network model in more detail. The intention here is to show that commonly accepted scientific methods, including parts of the traditional logic of induction, can be explicated in a probabilistic theory, where probability is interpreted in personalist and Bayesian terms as ‘degree of rational belief’. The explicatory relation between probability and induction is neither a justification of induction in terms of probability—for this would lead to a further demand for non-inductive justification of the probability postulates of induction themselves—nor does it require that all intuitively adopted inductive methods are necessarily acceptable in the light of systematic reconstruction in a probabilistic theory. Explication consists rather of analysing and systematizing intuitive methods and assumptions about the logic of science, and hence opens up possibilities of clarifying and modifying some of these in the light of others. In particular, and this is one of the more controversial outcomes of this study, the explication suggests that the interpretation of scientific theory as consisting essentially of strictly universal laws in potentially infinite domains is mistaken, and should be replaced by a view of science as strictly finite. That is to say, I shall argue that in so far as scientific theories and laws can be reasonably believed to be true, this reasonable belief is, and needs to be, non-zero only for statements whose domain of application is finite. Such a reinterpretation of the nature of scientific laws is argued in chapters 7 and 8. In chapters 9 and 10 finite probability methods are extended to account for theoretical inference which depends on analogical argument from models and on simplicity criteria. Chapter 11 is a detailed case history to illustrate the method of analogy, taken from the electrodynamics of J. C. Maxwell. In chapter 12 the consequences of the network model for a realistic interpretation of science are discussed.

Since I am here attempting, against all current odds and fashions, to develop a logic of science, a little more must be said about the nature of such an enterprise, and it must be distinguished from other types of study with which it may be confused.

Firstly, a logic of science differs from a descriptive study of methodology, whether historical or contemporary, since it should supplement mere description with normative considerations. This is because it presupposes that there are norms or criteria of ‘good science’ in terms of which groups of scientists judge scientific theories, and that these have some elements, perhaps tacit, of internal logical coherence and rationality. Obviously such criteria are not timeless, and they may not even be the same for different groups of scientists at the same time. In almost all periods, for example, there have been opposing tendencies towards a priori or speculative science on the one hand, and instrumentalist or positivist science on the other. But it does not follow that all sets of criteria are logically arbitrary. For each such set it is possible to explore the rational or normative connections and consequences of principles explicitly or implicitly adopted. Some of these may have been known to the group, and some may not have been known; this approach therefore makes possible a critical history of a group’s methodology. For example, it will be my contention that William Whewell missed an important element of his own analysis of ‘consilience of inductions’ when he used it to interpret the history of science, and that Maxwell misunderstood the significance of his own Newtonian claim that he had ‘deduced’ his electromagnetic theory from experiments, and hence underestimated the analogical element in his thinking. It follows from this normative character of the logic of science, and from the possibility of critical history, that there will be no simple process of testing of a proposed logic against historical examples—the relation of logic and cases will rather be one of mutual comparison and correction.

Secondly, a normative critique of method may disclose the implicit aims of a methodology and judge the appropriateness of its means to its ends. A science whose aim is application and prediction may have different normative requirements from one which desires truth, beauty or morality. Sometimes comprehensive theories of maximum empirical content are appropriate, sometimes instrumentalist predictions, sometimes inductive inferences. It is a naïve reading of the history of science to suppose that different methodologies are necessarily in conflict, given their different aims. The logic of science should provide a comparative study of such methodologies, rather than a partisan polemic on behalf of some against others.

Thirdly, it is often claimed that philosophical studies of science are irrelevant to the practice of science and unrecognizable as accounts of its methods. This objection, however, rests on a misunderstanding of the primary purpose of a logic of science. A study of the logical structure of science is not intended in the first place as an aid to scientific research, much less as a descriptive manual of experimental method. For example, although probabilistic methods have been suggested here as a handy means of explicating the inductive criteria of a scientific theory, it is unlikely that professional statisticians will find much that is relevant to their own technical problems, except perhaps incidentally. But the logic of science is in the first place a branch of philosophy, specifically of epistemology or the theory of knowledge, and also of ontology or the theory of what kinds of things there are. It is not surprising if the practice of science largely passes these questions by. They have, after all, been controversial for many centuries, and modern science in part developed intentionally as an enterprise that was neutral with respect to them and could afford to ignore them. Science has been remarkably successful in pursuing its own aims independently of philosophical disputes. But that is not to say that the philosophical critique of the foundations of science itself can ultimately be ignored, for that critique is concerned both with the understanding and justification of the aims of science itself, and with the existence and character of modes of knowledge other than the scientific.

In particular, the logic of science is very relevant to two matters of current interest and controversy. Firstly, there are rising doubts about the value of natural science itself as this has been traditionally understood. Far from being the paradigm of all knowledge, its aims to make true discoveries about the natural world and to exploit these discoveries are both being increasingly questioned.10 And secondly, the question of the character of other modes of knowledge, particularly in history, and the human and social sciences generally, has attained a new importance.11 These Geisteswissenschaften no longer look automatically to natural science for methodological guidance, and are badly in need of analysis and systematization of their own aims and methodologies. In relation to such questions a search for better understanding of the logic of the natural sciences themselves is clearly very relevant. A logic of science may also, of course, have some fallout in terms of direct usefulness to research in natural science, for self-understanding is often a desirable supplement to any enterprise, but the logic of science does not have to justify itself primarily on these grounds.

1 See especially K. R. Popper, The Logic of Scientific Discovery (London, 1959; first published 1934), chap. 1, and Conjectures and Refutations (London, 1963), chap. 1.

2 For the deductive model of scientific explanation (also called the covering-law model), see especially C. G. Hempel and P. Oppenheim, ‘Studies in the logic of explanation’, Phil. Sci., 15 (1948), 135, reprinted in Hempel, Aspects of Scientific Explanation (New York, 1965), 245; R. B. Braithwaite, Scientific Explanation (Cambridge, 1953), chaps. 1, 2; and E. Nagel, The Structure of Science (New York and London, 1961), chap. 2.

The special problems for this model of statistical theories which, if true, do not exclude any observation but only make some observations very improbable, and therefore cannot be conclusively falsified by observation, are considered by Popper, The Logic of Scientific Discovery, chap. 8; Braithwaite, Scientific Explanation, chaps. 5-7; and Hempel, ‘Inductive inconsistencies’, Aspects of Scientific Explanation, 53.

3 P. Duhem, The Aim and Structure of Physical Theory (Eng. trans, of 2nd edition, Princeton, 1954; first published as La Théorie physiquCy Paris, 1906), part II, chaps. 4-7.

4 ³ N. R. Campbell, Foundations of Science (New York, 1957; first published as Physics: the Elements, Cambridge, 1920), part I.

5 W. v. O. Quine, ‘Two dogmas of empiricism’, From a Logical Point of View (Cambridge, Mass., 1953), 20; Word and Object (New York, 1960), chaps. 1-3; Ontological Relativity and Other Essays (New York, 1969).

6 P. K. Feyerabend, ‘An attempt at a realistic interpretation of experience’, Proc. Aris. Soc.t 58 (1957-8), 143; ‘Explanation, reduction and empiricism’, Minnesota Studies in the Philosophy of Science, vol. Ill, ed. H. Feigl and G. Maxwell (Minneapolis, 1962), 28; ‘How to be a good empiricist’, Philosophy of Science: the Delaware Seminar, vol. 2, ed. B. Baumrin (New York, 1963), 3Î and many subsequent papers.

7 T. S. Kuhn, The Structure of Scientific Revolutions (Chicago, 1962; second edition 1970).

8 ⁷ N. R. Hanson, Patterns of Discovery (Cambridge, 1958); S. E. Toulmin, Foresight and Understanding (London, 1961), and Human Understanding (Oxford, 1972).

9 An interpretation of science in terms of ‘intuition’ and ‘tacit knowledge’ is given by M. Polanyi, Personal Knowledge (London, 1958). For the ‘consensus’ interpretation, see for example J. M. Ziman, Public Knowledge (Cambridge, 1968), and for ‘hedonism’ and all kinds of other polemic, see P. K. Feyerabend, ‘Consolations for the specialist’, Criticism and the Growth of Knowledge, ed. I. Lakatos and A. Musgrave (Cambridge, 1970), 197, and ‘Against method’, Minnesota Studies, vol. IV, ed. M. Radner and S. Winokur (Minneapolis, 1970), 17.

Almost any recent contribution of quality to the ‘history of scientific ideas’ illustrates the tendency to judge and interpret past science in the categories of its own time, without raising the question of ‘truth’. For some references, and some misgivings about this tendency, see my ‘Hermiticism and historiography’, Minnesota Studies, vol. V, ed. R. Stuewer (Minneapolis, 1970). 134-

10 See for example H. Marcuse, One Dimensional Man (London, 1964), chap. 6; and J. R. Ravetz, Scientific Knowledge and its Social Problems (Oxford, 1971).

11 For careful comparative analyses of method, see especially J. Habermas, Knowledge and Human Interests (Eng. trans., London, 1972; first published 1968); and C. Taylor, ‘Interpretation and the sciences of man’, Rev. Met.y 25 (1971), 3. I have discussed some of Habermas’s conclusions in Tn defence of objectivity’, Proc. Brit. Academy, 57 (1972).

CHAPTER ONE

Theory and Observation

1. Is there an independent observation language?

Rapidity of progress, or at least change, in the analysis of scientific theory structure is indicated by the fact that only a few years ago the natural question to ask would have been ‘Is there an independent theoretical language?’ The assumption would have been that theoretical language in science is parasitic upon observation language, and probably ought to be eliminated from scientific discourse by disinterpretation and formalization, or by explicit definition in or reduction to observation language. Now, however, several radical and fashionable views place the onus on believers in an observation language to show that such a concept has any sense in the absence of a theory. It is time to pause and ask what motivated the distinction between a so-called theoretical language and an observation language in the first place, and whether its retention is not now more confusing than enlightening.

In the light of the importance of the distinction in the literature, it is surprisingly difficult to find any clear statement of what the two languages are supposed to consist of. In the classic works of twentieth-century philosophy of science, most accounts of the observation language were dependent on circular definitions of observability and its cognates, and the theoretical language was generally defined negatively as consisting of those scientific terms which are not observational. We find quasi-definitions of the following kind: Observation-statement designates a statement ‘which records an actual or possible observation’; ‘Experience, observation, and cognate terms will be used in the widest sense to cover observed facts about material objects or events in them as well as directly known facts about the contents or objects of immediate experience’; ‘The observation language uses terms designating observable properties and relations for the description of observable things or events’; "observables, i.e., … things and events which are ascertainable by direct observation’.1 Even Nagel, who gives the most thorough account of the alleged distinction between theoretical and observation terms, seems to

presuppose that there is nothing problematic about the ‘direct experimental evidence’ for observation statements, or the ‘experimentally identifiable instances’ of observation terms.2

In contrast with the allegedly clear and distinct character of the observation terms, the meanings of theoretical terms, such as ‘electron’, ‘electromagnetic wave’ and ‘wave function’,3 were held to be obscure. Philosophers have dealt with theoretical terms by various methods, based on the assumption that they have to be explained by means of the observation terms as given. None of the suggested methods has, however, been shown to leave theoretical discourse uncrippled in some area of its use in science. What suggests itself, therefore, is that the presuppositions of all these methods themselves are false, namely

(a) that the meanings of the observation terms are unproblematic;

(b) that the theoretical terms have to be understood by means of the observation terms; and

(c) that there is, in any important sense, a distinction between two languages here, rather than different kinds of uses within the same language.

In other words, the fact that we somehow understand, learn and use observation terms does not in the least imply that the way in which we understand, learn and use them is either different from or irrelevant to the way we understand, learn and use theoretical terms. Let us then subject the observation language to the same scrutiny which the theoretical language has received.

Rather than attacking directly the dual language view and its underlying empiricist assumptions, my strategy will be first to attempt to construct a different account of meaning and confirmation in the observation language. This project is not the ambitious one of a general theory of meaning, nor of the learning of language, but rather the modest one of finding conditions for understanding and use of terms in science—some specification, that is to say, in a limited area of discourse, of the ‘rules of usage’ which distinguish meaningful discourse from mere vocal reflexes. In developing this alternative account I shall rely on ideas which have become familiar particularly in connection with Quine’s discussions of language and meaning and the replies of his critics, whose significance for the logic of science seems not yet to have been exploited nor even fully understood.

I shall consider in particular the predicate terms of the so-called observation language. But first something must be said to justify considering the problem as one of ‘words’ and not of ‘sentences’. It has often been argued that it is

sentences that we learn, produce, understand and respond to, rather than words; that is, that in theoretical discussion of language, sentences should be taken as units. There are, however, several reasons why this thesis, whether true or false, is irrelevant to the present problem, at least in its preliminary stages. The observation language of science is only a segment of the natural language in which it is expressed, and we may for the moment assume that rules of sentence formation and grammatical connectives are already given when we come to consider the use of observation predicates. Furthermore, since we are interested in alleged distinctions between the observation and theoretical languages, we are likely to find these distinctions in the characteristics of their respective predicates, not in the connectives which we may assume that they share. Finally, and most importantly, the present enterprise does not have the general positive aim of describing the entire structure of a language. It has rather the negative aim of showing that there are no terms in the observation language which are sufficiently accounted for by ‘direct observation’, ‘experimentally identifiable instances’ and the like. This can best be done by examining the hardest cases, that is, predicates which do appear to have direct empirical reference. No one would seriously put forward the direct-observation account of grammatical connectives; and if predicates are shown not to satisfy the account, it is likely that the same arguments will suffice to show that sentences do not satisfy it either.

So much for preliminaries. The thesis I am going to put forward can be briefly stated in two parts.

(i) All descriptive predicates, including observation and theoretical predicates, must be introduced, learned, understood and used, either by means of direct empirical associations in some physical situations, or by means of sentences containing other descriptive predicates which have already been so introduced, learned, understood and used, or by means of both together. (Introduction, learning, understanding and use of a word in a language will sometimes be summarized in what follows as the function of that word in the language.)

(ii) No predicates, not even those of the observation language, can function by means of direct empirical associations alone.

The process of functioning in the language can be spelled out in more detail.

A. Some predicates are initially learned in empirical situations in which an association is established between some aspects of the situation and a certain word. Given that any word with extralinguistic reference is ever learned, this is a necessary statement and does not presuppose any particular theory about what an association is or how it is established. This question is one for psychology or linguistics rather than philosophy. Two necessary remarks can, however, be made about such learning.

(1) Since every physical situation is indefinitely complex, the fact that the particular aspect to be associated with the word is identified out of a multiplicity of other aspects implies that degrees of physical similarity and difference can be recognized between different situations.

(2) Since every situation is in detail different from every other, the fact that the word can be correctly reused in a situation in which it was not learned has the same implication.

These remarks would seem to be necessarily implied in the premise that some words with reference are learned by empirical associations. They have not gone unchallenged, however, and it is possible to distinguish two sorts of objections to them. First, some writers, following Wittgenstein, have appeared to deny that physical similarity is necessary to the functioning of any word with extralinguistic reference. That similarity is not sufficient, I am about to argue, and I also agree that not all referring words need to be introduced in this way, but if none were, I am unable to conceive how an intersubjective descriptive language could ever get under way. The onus appears to rest upon those who reject similarity to show in what other way descriptive language is possible. For example, Donald Davidson claims that there is no need for a descriptive predicate to be learned in the presence of the object to which it is properly applied, since, for example, it might be learned in ‘a skilfully faked environment*.4 This possibility does not, however, constitute an objection to the thesis that it must be learned in some empirical situation, and that this situation must have some similarity with those situations in which the predicate is properly used. Chomsky, on the other hand, attacks what he regards as Quine’s ‘Humean theory’ of language acquisition by resemblance of stimuli and conditioned response.5 But the necessity of the similarity condition for language learning does not depend on the particular empirical mechanism of learning. Learning by patterning the environment in terms of a set of ‘innate ideas’ would depend equally upon subsequent application of the same pattern to similar features of the environment. Moreover, ‘similar’ cannot just be defined as ‘properly ascribed the same descriptive predicate in the same language community’, since for one thing similarity is a matter of degree and is a non-transitive relation, whereas ‘properly ascribed the same descriptive predicate’ is not, or not obviously. The two terms can therefore hardly be synonymous. I therefore take it as a necessary a priori condition of the applicability of a language containing universal terms that some of these terms presuppose primitive causal recognitions of physical similarities.

A different sort of objection to the appeal to similarity is made by Popper, who argues that the notion of repetition of instances which is implied by ï and 2 is essentially vacuous, because similarity is always similarity in certain respects, and ‘with a little ingenuity’ we could always find similarities in some same respects between all members of any finite set of situations. That is to say, ‘anything can be said to be a repetition of anything else, if only we adopt the appropriate point of view’.6 But if this were true, it would make the learning process in empirical situations impossible. It would mean that however finitely large the number of presentations of a given situation-aspect, that aspect could never be identified as the desired one out of the indefinite number of other respects in which the presented situations are all similar. It would, of course, be possible to eliminate some other similarities by presenting further situations similar in the desired respect but not in others, but it would then be possible to find other respects in which all the situations, new and old, are similar—and so on without end.

However, Popper’s admission that ‘a little ingenuity’ may be required allows a less extreme interpretation of his argument, namely that the physics and physiology of situations already give us some ‘point of view’ with respect to which some pairs of situations are similar in more obvious respects than others, and one situation is more similar in some respect to another than it is in the same respect to a third. This is all that is required by the assertions i and 2. Popper has needlessly obscured the importance of these implications of the learning process by speaking as though, before any repetition can be recognized, we have to take thought and explicitly adopt a point of view. If this were so, a regressive problem would arise about how we ever learn to apply the predicates in which we explicitly express that point of view. An immediate consequence of this is that there must be a stock of predicates in any descriptive language for which it is impossible to specify necessary and sufficient conditions of correct application. For if any such specification could be given for a particular predicate, it would introduce further predicates requiring to be learned in empirical situations for which there was no specification. Indeed, such unspecified predicates would be expected to be in the majority, for those for which necessary and sufficient conditions can be given are dispensable except as a shorthand and hence essentially uninteresting. We must therefore conclude that the primary process of recognition of similarities and differences is necessarily unv erb alizable. The emphasis here is of course on primary, because it may be perfectly possible to give empirical descriptions of the conditions, both psychological and physical, under which similarities are recognized, but such descriptions will themselves depend on further undescribable primary recognitions.

B. It may be thought that the primary process of classifying objects according to recognizable similarities and differences will provide us with exactly the independent observation predicates required by the traditional view. This, however, is to overlook a logical feature of relations of similarity and difference, namely that they are not transitive. Two objects a and b may be judged to be similar to some degree in respect to predicate P, and may be placed in the class of objects to which P is applicable. But object e which is judged similar to b to the same degree may not be similar to a to.the same degree or indeed to any degree. Think of judgments of similarity of three shades of colour. This leads to the conception of some objects as being more ‘central’ to the p.class than others, and also implies that the process of classifying objects by recognition of similarities and differences is necessarily accompanied by some loss of (unverbalizable) information. For if P is a predicate whose conditions of applicability are dependent on the process just described, it is impossible to specify the degree to which an object satisfies P without introducing more predicates about which the same story would have to be told. Somewhere this potential regress must be stopped by some predicates whose application involves loss of information which is present to recognition but not verbalizable. However, as we shall see shortly, the primary recognition process, though necessary, is not sufficient for classification of objects as P, and the loss of information involved in classifying leaves room for changes in classification to take place under some circumstances. Hence primary recognitions do not provide a stable and independent list of primitive observation predicates.

C. It is likely that the examples that sprang to mind during the reading of the last section were such predicates as ‘red’, ‘ball’ and ‘teddy bear’. But notice that nothing that has been said rules out the possibility of giving the same account of apparently much more complex words. ‘Chair’, ‘dinner’ and ‘mama’ are early learned by this method, and it is not inconceivable that it could also be employed in first introducing ‘situation’, ‘rule’, ‘game’, ‘stomach ache’ and even ‘heartache’. This is not to say, of course, that complete fluency in using these words could be obtained by this method alone; indeed, I am now going to argue that complete fluency cannot be obtained in the use of any descriptive predicate by this method alone. It should only be noticed here that it is possible for any word in natural language having some extralinguistic reference to be introduced in suitable circumstances in some such way as described in section A.

D. As learning of the language proceeds, it is found that some of these predicates enter into general statements which are accepted as true and which we will call laws’. ‘Balls are round’; ‘In summer leaves are green’; ‘Eating unripe apples leads to stomach ache’. It matters little whether some of these are what we would later come to call analytic statements; some, perhaps most, are synthetic. It is not necessary, either, that every such law should be in fact true, only that it is for the time being accepted as true by the language community. As we shall see later, any one of these laws may be false (although not all could be false at once). Making explicit these general laws is only a continuation and extension of the process already described as identifying and reidentifying proper occasions for the use of a predicate by means of physical similarity. For knowledge of the laws will now enable the language user to apply