Science is a human cognitive enterprise, and philosophy of science is a part of epistemology (the theory of knowledge), although philosophers of science also address logical, metaphysical, ethical, and aesthetic questions. Questions concerning the nature of science go back to the beginnings of Western philosophy, but philosophy of science only became a separate subspecialty in the last one or two centuries. Important figures in the early development of modern philosophy of science are David Hume (Reference Hume1738, Reference Hume1748), Immanuel Kant (Reference Kant1787), John Stuart Mill (Reference Mill1843), William Whewell (Reference Whewell1840), and major scientists themselves such as Galileo, Descartes, Newton, and Herschel. Only at the end of the nineteenth century was the field of philosophy of science launched with striking monographs by scientists or historians of science such as Ernst Mach (Reference Mach1942), Piere Duhem (Reference Duhem1906), and Henri Poincaré (Reference Poincaré1905).

In the first half of the twentieth century, the so-called logical positivists dominated thinking about the philosophy of science, although Karl Popper’s views exerted a growing influence. In the 1960s, philosophy of science took a historical and empirical turn that became dominant in the last decades of the twentieth century. Developments in statistical inference, causal modeling, cognitive science, and the sociology of science have made twenty-first-century philosophy of science much more diverse. Contemporary philosophy of science is a lively field in which there is a great deal of disagreement about both substantive theses and approaches.

Most of what I need to say about philosophy of science in general has already been said in the chapters of this book. But since the discussion of many of the topics is scattered over multiple chapters, I think it is helpful if, in this appendix, I provide a compact exposition of aspects of philosophy of science that bear significantly on economics. Although I make clear what is the current consensus on the issues, when there is one, I do not hesitate to defend my own views. This is not the place to write a comprehensive account of philosophy of science, and I pass over many subtleties.

The issues I discuss in this appendix can be divided into eight groups:

1. 1. What are the ultimate goals of science? Does science aim exclusively to provide correct predictions, which may be of practical use, or should science seek explanations and truth?

2. 2. What is causation and what is scientific explanation?

3. 3. What are scientific models, laws, and theories?

4. 4. Paradigms and research programs: How are particular theories related to one another? What sort of “global” theory structure is characteristic of science?

5. 5. Discovery: How are scientific theories, laws, and causal relations discovered or constructed?

6. 6. Induction, confirmation, and theory appraisal: How should scientists test and appraise scientific theories and how should scientists compare competing theories? How can theories be supported by observation?

7. 7. Demarcation between science and other inquiries and scientific method.

8. 8. The unity of science: Can human actions and institutions be studied in the same way that one studies nature?

   1. a. Is a science of society possible?

   2. b. Do explanations in the social sciences have the same logic and structure as explanations in the natural sciences?

   3. c. Are the social sciences reducible to the natural sciences?

   4. d. How are the links between social theories and values to be understood?

Question number 6 – the general problem of appraising and comparing scientific theories – has been of most interest to writers on economic methodology, and it is central to this book as well. But it is important to remember that there are many other important philosophical questions. I make no claims for this way of grouping the questions, apart from expository convenience.

A.1 Historical and Philosophical Background

Because current philosophy of science is still to some extent a reaction against the views of its predecessors, something needs to be said about the logical positivist, logical empiricist, and Popperian ancestors of contemporary views on the issues I have listed. Chapter 12 examined Popper’s views in some detail, and the logical empiricist views of theories, models, laws, and appraisal were discussed in Chapters 6, 9, 10, and 11. Only a little more needs to be said. For brevity, I am lumping together the logical positivists and their successors, the logical empiricists.

Logical positivism was a philosophical movement beginning in the 1920s in Berlin and Vienna and continuing (thanks to Hitler) mainly in the United States into the 1950s (see Ayer Reference Ayer1959; Hanfling Reference Hanfling1981a; 1981b). It was an exceptionally influential intellectual movement. Although most of its distinctive theses are untenable, the logical positivists generated the refutations of their views themselves and faced them with unrivaled honesty (see Nagel Reference Nagel1961).

Among the many influences on the logical positivists, who had diverse intellectual backgrounds, there were four main inspirations: (1) twentieth-century physics, especially Einstein; (2) late nineteenth- and early twentieth-century formal logic; (3) empiricism, especially as espoused by Hume and Mach; and (4) Kant’s “critical” philosophy.

Although Kant had held that scientific knowledge requires sensory data, he regarded the products of sensation as cognitively empty apart from conceptual “synthesizing” imposed by the “understanding.” Mathematics and mathematical physics were the best exemplars of how systematic relations imposed on sensory data constitute objective knowledge. Like Kant, the logical positivists regarded objective knowledge as possible only insofar as sensory experiences are systematically related to one another. Like Kant, the logical positivists regarded mathematics and mathematical physics as paradigmatic of objective knowledge. But they rejected Kant’s notion that space and time were “pure intuitions” and his claims for the necessary applicability to experience of mathematical systems such as Euclidean geometry (see Friedman Reference Friedman1998).

Although the Kantian background of logical positivism was inconsistent with an extreme empiricism that takes knowledge to be piling up sensory experiences, empiricism remained central to logical positivism, and it provided a way to show how scientific knowledge could be objective. Empiricism consists of two related theses: (1) all evidence bearing on “synthetic” statements (statements concerning matters of fact) derives from sense perception; and (2) terms are “cognitively significant” only if it is possible to distinguish (however indirectly) by means of sense perception what they refer to or whether something belongs to their extension.Footnote ¹ The positivists sought to purge science of sentences that contain terms that are not cognitively significant. Scientific theories should be formulated so that the bearing of empirical evidence is precise and transparent.

The positivists believed that formal logic could be marshaled in the empiricist cause. Logicians such as Frege and Russell appeared to offer the possibility of a new language for science that avoids the vagueness and ambiguity of ordinary language (Russell’s Reference Russell and Russell1905 showed what might be possible). The distinction logicians draw between syntactic notions such as well-formedness, proof, or consistency and semantic notions such as truth, reference, and meaning (discussed in Chapter 6) became especially important to the positivists. They saw formal logic as liberating empiricism from the psychological and metaphysical garb in which it was presented by Hume and Mach and as permitting one to distinguish analytic or inconsistent statements, which are true or false by virtue of logic and meanings, from the statements which must pass the test of observation (Ayer Reference Ayer1936, chapter 4).

Finally, the positivists believed that formal logic coupled with empiricism could help explain the breakthroughs of contemporary physics and could contribute to further scientific progress. They saw Einstein’s contribution as in part the conceptual discovery that the Newtonian notion of simultaneity of spatially separated events was not cognitively significant: there is no way to tell whether pairs of spatially separated events belong to the extension of the Newtonian predicate “is simultaneous.”Footnote ² This revolution in physics showed the importance of formulating theories precisely enough that the cognitive significance of their terms could be assessed by intellects less lofty than Einstein’s.

Despite the deep empiricist commitments of the positivists, their work was always constrained by a respect for the achievements of the natural sciences, especially physics. If a philosophical model condemned the major achievements of contemporary physics, then it, not the physics, was regarded as suspect. The application (or misapplication) of positivist and logical empiricist views is discussed in Chapter 11. As I discuss major features of science in the succeeding sections in this appendix, I repeatedly take the positivists’ construals as points of departure.

A.2 The Goals of Science: Realism versus Instrumentalism

One of the longest-standing disagreements among scientists concerns the ultimate goals of theorizing.Footnote ³ There have been two main schools of thought. Scientific realists hold that in addition to enabling us to make accurate predictions, science should aim to discover new truths about the world and to explain phenomena. When a theory is sufficiently well supported, the realist holds that one may justifiably regard its claims, even those which talk about unobservable things, as true, although evidence always falls short of proof, and even the best supported of our current theories may turn out to be false. Copernicus (Reference Copernicus1543), for example, was a realist.Footnote ⁴ He sought an alternative to Ptolemy’s earth-centered astronomy mainly because its account of the heavens made no physical sense and could not be true (Dreyer Reference Dreyer1953, p. 320; Toulmin and Goodfield Reference Toulmin and Goodfield1961, pp. 178–9)

Members of the other school, instrumentalists, maintain that the ultimate goal of science is purely predictive. Milton Friedman asserts an instrumentalist view explicitly. Explanations may be important to diagnose anomalies and to determine where theory has gone wrong, but the ultimate goal of science is to guide action by providing accurate conditional predictions – that is, predictions about what will happen if certain actions are undertaken. Because of their view about goals, many instrumentalists are ontological, semantic, or epistemological anti-realists – that is, they question the existence of entities postulated by scientific theories that cannot be observed, or they question whether claims about unobservables are meaningful, or they question whether claims about unobservables can be well supported by empirical evidence. Instrumentalism is distinct from anti-realism. There are instrumentalists who are not anti-realist, such as Friedman himself or John Dewey (Reference Dewey1939a, pp. 534–45, 574–5), and there are anti-realists, such as Bas van Fraassen (Reference van Fraassen1980), who do not maintain that the ultimate goals of science are exclusively predictive.

Realists and instrumentalists agree that scientists should develop theories which introduce unobservables, and they should thus be distinguished from anti-theoretic views like those defended by B. F. Skinner in psychology and Paul Samuelson in economics (§11.2). Unlike realists and instrumentalists, Skinner and Samuelson want to eschew all theory that goes beyond identifying regularities among observable phenomena (Skinner Reference Skinner1953; 1974).

Problems about unobservables seldom arise in discussions of economic methodology, because economic theories rarely postulate unobservable things beyond those which are part and parcel of everyday life, such as beliefs and preferences. (See the discussion of Machlup’s views in §11.3.) Economists have, however, been attracted to instrumentalism concerning the goals of science. Friedman’s “narrow” instrumentalism (§11.4) is distinctive because he maintains that the ultimate goal of a science lies in correct predictions concerning only those phenomena with which a particular science is concerned. False predictions concerning other phenomena are in Friedman’s view not relevant to theory appraisal.

A.3 Causation and Scientific Explanation

A traditional view of science is that it is an inquiry into the causes of phenomena, that laws describe the operations of causes, and that explanations identify causes (Aristotle Reference Aristotle1958, book II, chapter 3). But the notion of causality has been hard to understand, and explicitly causal language fell out of philosophical favor, particularly when the influence of logical positivism was strongest. Bertrand Russell went so far as to claim that “the reason why physics has ceased to look for causes is that, in fact, there are no such things. The law of causality, I believe, like much that passes muster among philosophers, is a relic of a bygone age, surviving, like the monarchy, only because it is erroneously supposed to do no harm” (1912, p. 132). This repudiation of causal notions was motivated by empiricism, which was as central to Russell’s later views as it was to those of the logical positivists or to David Hume’s arguments two centuries before. Hume wanted to know how observations can provide evidence for or against causal claims, and he argued that all one ever observes are that the cause and effect are “constantly conjoined” and that the cause precedes the effect.Footnote ⁵ The necessary connection that people imagine obtaining between cause and effect is empirically ineffable, and Hume offers a psychological explanation for how the illusion of some further connection arises from repetition (1748, §7). Apart from this illusion, causality consists in empirical regularity with temporal priority of the cause to the effect – nothing more.

Although Hume generally speaks of “the cause” of an effect, and much effort in everyday discussion (Collingwood Reference Collingwood1940, pp. 304–5; Gorovitz Reference Gorovitz1969) and in the law (Hart and Honoré Reference Hart and Honoré1985) is devoted to singling out the (salient) cause from among the various causal influences and conditions, Hume’s analysis can easily be adapted to the notion of “a cause or causal condition.” It is this notion, not the notion of the cause, which is of interest to science. A useful way of adapting it in the deterministic case is J. L. Mackie’s. Although one would regard the striking of a match as a cause (indeed “the” cause) of its lighting, strikings of matches are not always followed by matches lighting, and matches that are not struck may be lighted in other ways. Mackie argues that the regularity that is implicit in the claim that striking a match caused it to light is that matches light if and only if either they are struck and a variety of other conditions obtain (they are dry, oxygen is present, etc.), or some other set of factors sufficient for a match lighting obtains. Such claims are vague but testable, and they highlight the facts that events can have different causes and that the joint presence of multiple separate causal factors is typically necessary in order to bring about a given effect. Causes are insufficient but necessary components in sets of factors that are unnecessary but sufficient for the effect to occur, or INUS conditions for short (Mackie Reference Mackie1974, chapter 3). They are components in minimal sufficient conditions for their effects. To guarantee the asymmetry of cause and effect, some other condition, such as the temporal priority of the cause, must be added. This account of causation offers a simple way to think about the problems of extrapolation: establishing in an experiment that C is a cause of E, we do not know whether in the wild C will bring about E if we do not know what other factors are contained in the minimal sufficient condition for E that contains C (Cartwright and Hardie Reference Cartwright and Hardie2012).

Hume’s account of causality is compatible with a once dominant but now discredited view of explanation, Carl Hempel’s deductive-nomological model. Explanations answer “why?” questions. They remove puzzlement, they provide understanding, and they have an important pragmatic aspect (emphasized by Bromberger Reference Bromberger and Colodny1966; van Fraassen Reference van Fraassen1980; and Achinstein Reference Achinstein1983a). One naive view is that explanations make unfamiliar phenomena familiar. But explanations often talk of things that are less intuitively comprehensible than what is being explained. What could be more familiar than that water is a liquid at room temperature? Certainly not the explanation physicists give for its liquidity.

The dominant view among the logical positivists and logical empiricists was that scientific explanations show that the phenomenon to be explained was to have been expected: a scientific explanation shows some happening or some regularity to be an instance of a broader or “deeper” regularity. A scientific explanation shows that the thing being explained did not just happen. It was the sort of thing that could have been expected to happen in the circumstances, given knowledge of laws of nature. Notice that, in explaining something as an instance of a more fundamental law, one need not have any explanation for that law itself. Explanations come to an end at the current frontiers of science.

This expectability or subsumption view of explanation goes back to the Greeks, but it receives systematic development in essays by Hempel (Reference Hempel1965). Hempel develops two main models of scientific explanation: the deductive-nomological and the inductive-statistical models. The inductive-statistical model, as its name suggests, is concerned with statistical explanations and raises additional difficulties, which I do not discuss.

In a deductive-nomological explanation, a statement of what is to be explained (the “explanandum”) is deduced from the explanans, which consists of a set of true statements which includes at least one law, without which the deduction would not go through. Scientists show that the phenomenon to be explained is an instance of broader regularities, by deducing a statement of what is to be explained from laws and other true statements. Explanation, like causation (as understood by Hume), requires universal generalizations, and if the initial conditions specified in the explanans come before the explanadum in time, then deductive-nomological explanation would appear to be causal explanation.

It is essential that some law or laws play a role in the deduction of the explanandum. To deduce that this apple is red from the true generalization that all apples in the bowl are red and the true statement that this apple is in the bowl does not explain why the apple is red. “Accidental generalizations,” unlike laws, are not explanatory, and accidental associations are not causal. Some philosophers, such as van Fraassen, relax the requirement that the statements in the explanans be true and demand only empirical adequacy – truth of their observable implications. Empirical adequacy, like truth, is a semantic property and an ontological aspiration, not a standard of belief or justification. Hempel’s concept of deductive-nomological explanation is not epistemic. Whether some set of statements explains another is not a matter of our beliefs but a matter of fact.

Whether explanations require laws and truth is important in thinking about economics. For economists are often hesitant to regard their basic generalizations as laws, yet economists nevertheless claim to be able to explain economic phenomena. These questions are discussed in Chapters 9 and 10.

The deductive-nomological model is only an account of deterministic, or nonstatistical explanations. If one has only a statistical regularity, then one will not be able to deduce what is to be explained, but one may be able to show that it is highly probable, which is what Hempel’s inductive-statistical model requires.

The deductive-nomological model is problematic. Not only is it limited to nonstatistical explanations, but an argument may satisfy all its conditions without being an explanation. Consider the following well-known example:

If George is a man, nobody would regard this argument as explaining why George does not get pregnant. If one assumes for the sake of this discussion that the first premise is a law and that George does faithfully take his birth control pills, then the conditions of the deductive-nomological model are met, but one has not explained why George does not get pregnant. Why not? The intuitive answer is that it does not matter whether George took birth control pills. His taking the pills was not causally relevant. If he had not taken the pills, he would still not have gotten pregnant. The factors explanations cite must be causally relevant.

Explanation apparently requires not only causal relevance, but that the explanans should cite causes rather than effects of the explanandum. For example, one can deduce that the air in a spherical balloon has grown colder by measuring a decrease in the circumference of a well-sealed balloon, but the diminished circumference of the balloon does not explain why the air has gotten colder. On the contrary, the fact that the air has cooled explains why the balloon has shrunk. From the fact that Fido is pregnant, one can deduce that she is female, but her pregnancy does not explain her sex. Effects do not explain their causes, and effects of a common cause do not explain one another.

Given the pervasiveness of facts such as these, it has grown increasingly obvious to philosophers that the deductive-nomological model of explanation is untenable, and that causal explanations need to cite causes explicitly. Although there is no new orthodoxy, the most persuasive of the many new accounts of causal explanationFootnote ⁶ is James Woodward’s in Making Things Happen (2003), mentioned in Chapter 9. Woodward maintains that causal explanations in science rely on functional relations between variables whose values are to be explained and the variables upon which they depend. Neither the values of the variables nor the functional relations need be quantitative. A causal explanation of, for example, an increased demand for flat-screen televisions would consist of an equation such as q^d_tv = f(p_tv, p_c, p_b, t), where q^d_tv is the quantity of flat-screen televisions demanded, p_tv is the price of flat-screen televisions, p_c is an index of the prices of substitutes such as computers, p_b records the price of complements such as cable or satellite television connections, and t is tastes. A change in p_tv explains a change in q^d_tv if and only if some interventions that change p_tv from the initial price, pⁱ_tv, to p*_tv with all other variables on the right-hand side unchanged are followed by a change in q^d_tv from f(pⁱ_tv, pⁱ_c, pⁱ_b, tⁱ) to f(p*_tv, pⁱ_c, pⁱ_b, tⁱ). The functional relationship, f, is in this sense “invariant to interventions on p_tv.” An intervention on p_tv is a variable z that causes a change in the value of p_tv and has no other causal relation to any of the other variables apart from those that follow from z causing a change in p_tv.

If one does not want to scrap the deductive-nomological model altogether, one can cling to it as providing necessary conditions for nonstatistical explanations. Even this weaker thesis requires qualifications, for explanations in science rarely fit the deductive-nomological model explicitly. Defenders of the deductive-nomological model respond by arguing that actual scientific explanations are often elliptical or mere explanation sketches. Even if one accepts these excuses, the deductive-nomological model seems to abstract from much of what is most significant about scientific explanations. Most of the interesting features of explanations in economics are at a much lower level of generality.

A.4 Laws, Theories, and Models

When one thinks naively about science, one thinks of its many laws and theories: Newton’s theory of universal gravitation, Coulomb’s law of electrostatic repulsion, Mendel’s laws of inheritance, and so forth.Footnote ⁷ The deductive-nomological account of explanation maintains that scientific explanations presuppose scientific laws. Economics has some well-known laws too: the law of demand, the law of diminishing returns, the law of a single price, Gresham’s law, Engel’s law, and so forth. What is odd about economic laws is that they are false (at least if understood as universal generalizations). This embarrassment, coupled with the difficulties in distinguishing laws from accidental generalizations,Footnote ⁸ suggests that the notion of a scientific law is unhelpful, at least for the purposes of understanding the content of economic models and theories.

But what should theoretical economists search for if not laws? As this book documents, and Chapter 6 discusses in some detail, economists in fact typically think in terms of models whose relationship to economic interactions is analogous to the relationship between model airplanes whose aerodynamic properties, which are tested in wind tunnels, inform designers concerning the properties of full-scale airplanes. The models economists use differ, however, in that they are entirely made up. Although economists regard them as “analogue economies” (Lucas Reference Lucas1980), they are not economies. They are sentences and equations, which are make-believe true of make-believe worlds. A model such as Samuelson’s overlapping-generations economy discussed in Chapter 8 is entirely made up: it has no location or date or interactions with actual causal factors, which means that one cannot learn anything about it or about actual economic interactions beyond what is implicit in its definition.

Although I recognize the heuristic virtues of treating models as make-believe worlds, I argue in Chapter 6 that models in economics should be understood as predicates or as definitions of predicates that, when asserted of actual states of affairs, make empirical claims. This roundabout procedure of, for example, first defining a model of rational agency and then saying that people are rational agents highlights the fact that there are two distinct kinds of achievement involved in constructing a scientific theory. Of course, a theory must identify features of nature or society, and that is what ultimately counts in an empirical science. But science does not proceed solely by spotting correlations among well-known observable properties of things. The construction of new concepts, of new ways of classifying and describing phenomena, is an equally crucial part of science. Such conceptual work – the construction of models – has been prominent in economics.

This account of models clarifies the form of economic investigations, but it does not tell us whether those investigations are searching for laws, tendencies, mechanisms, causal relations, descriptions, or theories. If one believes, as is plausible, that universality is a central desideratum on theoretical achievements, then one regards laws or something very much like laws as a central objective of theoretical endeavor, and one needs to explain how the inexact generalizations of economics can nevertheless constitute laws or constitute an acceptable surrogate for laws. Theories on this view are sets of lawlike statements that are related to one another to explain and predict some domain of phenomena. As discussed in Chapter 6, this view of theories denies both the syntactic and the semantic views of theories.

However, philosophers such as James Woodward and Nancy Cartwright question the importance of universality and regard the attachment of many philosophers of science to universality as collateral damage from Hume’s futile attempt to find an empiricist account of causation in terms of constant conjunction with causes preceding their effects. Once one gives up on this account of causation, models can be regarded as specifications of possible causal relations (in Woodward’s view) or as assemblages of tendencies and capacities (in Cartwright’s view), and regularities, most of which will have relatively narrow scopes, will figure only as consequences that arise when capacities line up in just the right way.

Although the application to economics of standard views in philosophy of science faces special challenges owing to the inexactness of economic generalizations, economics is in one regard less problematic from an empiricist perspective than is a science such as physics. Unlike theories in many of the natural sciences, economic theories do not postulate new unobservable entities and properties that influence what can be observed. This is not to say that economics makes no references to unobservable entities. The beliefs and preferences of others can be inferred from their joint contributions to choices, but they are not observable themselves. Human capital is not observable. Nor is the rate of inflation. But our awareness of these unobservables does not depend on economic theory. Without economic theory, we might not have the term “human capital,” the Laspeyres price index, or utilities as indices of preferences, but we would know that some people are more productive, that prices in general may be rising or falling, and that people seek to bring about more highly ranked alternatives. There is nothing comparable to the menagerie of strange unobservable entities contemporary physics claims to have discovered. So economists can dodge the problem of evaluating what sort of epistemic warrant there may be for such postulates. Accordingly, in Section 11.3, I criticize Fritz Machlup’s effort to apply the views of the logical empiricists concerning unobservables to economics. Economics has enough methodological problems without annexing those of physics as well.

A.5 Paradigms and Research Programs

One shortcoming of reflections on science in the first half of the twentieth century is that philosophers paid little attention to the relations among different theories within a research community and to the structure of those communities. Beginning mainly with Thomas Kuhn’s Structure of Scientific Revolutions,Footnote ⁹ that changed, and in arguing for my account of the global structure of mainstream economics in Chapter 7, I discussed two of these accounts: Kuhn’s disciplinary matrices and Lakatos’ research programs. Although neither of these views can be applied “off-the-shelf,” as it were, to mainstream economics, they provide useful categorizations and questions. The common theme – that challenge, revision, and transformation within the sciences are structured rather than haphazard – is a crucial insight.

A.6 Scientific Discovery

Through most of the twentieth century, most philosophers held that there was little of philosophical interest to be said about invention in science. Although Karl Popper titled his major work Die Logik der Forschung or, in its misleading English translation, The Logic of Scientific Discovery, he held that discovery is not subject to rational rules and that the normative interests of philosophers should be confined to the assessment of scientific theories (1968, p. 31). In Hans Reichenbach’s well-known terminology, one can distinguish the context of discovery from the context of justification, and philosophy of science is concerned exclusively with the context of justification (Reichenbach Reference Reichenbach1938, pp. 6–7; Hoyningen-Huene Reference Hoyningen-Huene1987). Earlier epistemologists and philosophers of science, such as J. S. Mill, were criticized for failing to distinguish these contexts clearly enough.

Writers on economic methodology have reiterated this repudiation of any logic of discovery. Witness Milton Friedman:

But this bit of methodological orthodoxy fits economics badly. The grounds for accepting economic theories are rarely distinct from the grounds upon which they were generated in the first place, and much of traditional economic methodology has been concerned as much with the context of discovery as with the context of justification. J. S. Mill’s deductive or a priori method, which dominated methodological thinking concerning the appraisal of economic theories for a century (a revised version of which I attempt to resuscitate in Chapters 9, 10, and 13), is primarily an account of how to generate plausible and credible economic theories.

Mill’s view is not the worse for being an account of theory generation, for here, as elsewhere, philosophical dogma has come into question (Nickles Reference Nickles1980 and Nickles, ed. 1980). Once one recognizes that discovery depends on abstract relations between evidential features and the theories that may be generated to account for them as well as on the causal processes involved in theory generation, there is little reason to deny that there can be a logic of discovery. There are, of course, psychological questions about what led to the formation of a belief, but there are also normative questions about whether mental processes issue in beliefs. Indeed some of the formal procedures for theory assessment proposed by the logical positivists are themselves procedures for theory generation (Kelly Reference Kelly1987). The existence of computer programs that generate theories from evidence vividly demonstrates that there can be rational procedures for scientific discovery (Langley et al. Reference Langley, Simon, Bradshaw and Zytkow1987; Glymour et al. Reference Glymour, Kelly, Scheines and Spirtes1987).

A.7 Induction, Testing, and Assessing Scientific Theories

Most philosophers, economists, and ordinary folk are empiricists about theory assessment. They believe that the evidence that ultimately leads one to accept or to reject claims about the world is observational evidence. Economists believe that individuals generally prefer more commodities to fewer because this claim is largely borne out by experience.

However, empiricist views of theory assessment face deep problems, some of which become evident when one tries to be more precise about confirmation. There is also a serious philosophical puzzle about the very possibility of confirmation. As David Hume argued in the eighteenth century, observation or experimentation only leads one directly to accept singular statements about the existence and properties of things at particular times and places. What, then, is the basis for our confidence in generalizations or in singular statements about instances not yet observed? As Hume put it:

Hume is issuing a challenge: “Show me a good argument whose conclusion is some generalization or some claim about something not observed and whose premises include only reports of sensory experiences.” Such an argument cannot be a deductive argument, because the conclusions of arguments Hume seeks may be mistaken, even when all the premises are true: Europeans had ample inductive evidence for the false generalization that all swans are white. Nor will an inductive argument do, since one has only inductive and thus question-begging grounds to believe that inductive arguments are good ones. The validity of inductive arguments is precisely what is being questioned.

This is Hume’s problem of induction. It is primarily a problem concerning how generalizations or singular claims about unobserved things can be supported or justified. It is not mainly a problem about the discovery of generalizations. Nor is it a problem about the actual arguments scientists make in defense of particular hypotheses, whose premises are never limited to observation reports. In Hume’s view, belief in some claim about the world is justified only if it is the conclusion of a valid argument from premises consisting only of reports of sensory experiences. If one rejects foundationalism and permits the premises in justificatory arguments to include parts of one’s purported knowledge beyond observation reports, then one faces a more tractable (although still very difficult) problem of understanding how evidence bears on theories. Observations and experiments have a crucial role in the expansion and correction of empirical knowledge, but one cannot and need not trace knowledge claims back to any experiential foundation (Quine Reference Quine1969; Levi Reference Levi1980). To use a superb metaphor that Quine cites repeatedly: in learning about the world it is as if one is rebuilding a ship while staying afloat in it. In learning more, people rely on what they think they know.Footnote ¹⁰

The ship metaphor is Otto Neurath’s. Although Neurath was a member of the Vienna Circle, the logical positivists generally resisted such a view of scientific knowledge. Instead Carnap (Reference Carnap1950) and others attempted to develop an inductive logic, a canon of thought whereby conclusions could be established with a certain subjective probability from premises, which included only logic, mathematics, analytical meaning postulates, and reports of observations and experiments. These efforts were not successful, but Carnap’s work helped lead to less foundational approaches to confirmation.

Not all claims require empirical evidence. Consider assertions such as “all tables are tables,” “triangles have three angles,” or “this square is circular.” These do not require testing, and confidence in their truth or falsity does not depend on test results. The logical positivists dealt with such cases by distinguishing synthetic claims – claims about the world – from analytic or contradictory claims whose truth or falsity depend solely on logic and on the meanings of the terms. But, largely owing to the critiques of W. V. O. Quine (Reference Quine1953, pp. 20–46) and Morton White (Reference White1956), many doubt that there is a useful distinction between analytic and synthetic claims.Footnote ¹¹ Consider, for example, the following claim: “If x and y are substitutes, then ceteris paribus, people will buy more of x when the price of y increases.” Is this an empirical claim or does it follow from the definition of a substitute? Is “the equation of exchange”: MV ≡ PT a definition of V, the velocity of money, or a testable claim about the effect of the quantity of money, M, on economic activity? On Quine’s view, these are not good questions (see also Putnam 1962), and acceptance or denial of such propositions rests on their role in larger sets of propositions that have testable implications.

Although subject to difficulties, empiricism remains dominant. But it is not unchallenged. Kant argued in his Critique of Pure Reason that there are synthetic truths about the world that can be known a priori – that is, without empirical confirmation. Some propositions, such as the axioms of Euclidean geometry, are, Kant asserted, implied by the possibility of having conscious experience of the world. No perceptual evidence could lead one to reject such propositions.

Modern physics has refuted Kant’s view that the axioms of Euclidean geometry are a priori truths. Yet Kant’s general position still has supporters among writers on economic methodology. Modern “Austrian” economists, especially Ludwig von Mises and his followers, believe that the fundamental postulates of economics are synthetic a priori truths (von Mises Reference Mises1949; 1978; 1981; see also Rothbard Reference Rothbard1957; 1976, pp. 24–5). With few exceptions, such as Frank Knight, whose views are mentioned in Chapter 11, defenders of mainstream economics have been empiricists. Nevertheless, like Lionel Robbins, who is quoted in Chapter 10, economists have often treated equilibrium theory as de facto irrefutable.

If one supposes that the grounds for assessing claims about the world are the results of observations and experiments, one then faces the question of how such results provide evidence for or against scientific theories. Two different questions should be distinguished:

1. 1. The problem of evidence: How does observational evidence provide any confirmation or disconfirmation (no matter how weak) of scientific hypotheses?

2. 2. The problem of acceptance or choice: When are hypotheses strongly confirmed or disconfirmed on the basis of the results of observation and experiment?

My comments here, as in Chapters 10, 11, and 13, focus on the first question. In those chapters I presented several highly simplified schema for appraising economic hypotheses: the hypothetico-deductive method, Bayesian updating, likelihood comparisons, and the inexact deductive method. Their common features are that they begin with some hypothesis or theory, H (or possibly two or more competing hypotheses, H and H’), which are to be tested. Attention then turns to some testable claim E whose truth or falsity bears on the truth or predictive adequacy of H (or H and H’). E is then tested and, depending on the results, the hypotheses are confirmed or disconfirmed to some extent.

The devil (or, more accurately, the devils) are in the details. Each step is problematic. Where do the hypotheses come from? How much weight should one place in H’s prior probability? Unless one can deduce E from H all by itself, which is unlikely ever to be the case, how can one judge whether and to what extent the truth or falsity of E bears on the truth or falsity or predictive accuracy of H? How is E to be tested? Finally, in light of the test results, how strongly is H confirmed or disconfirmed either absolutely or in comparison to H’?

When H is, as in economics, an inexact law or the statement of a tendency, these problems are compounded. Suppose one wants to test an economic hypothesis such as the law of demand. From (1) the law of demand, (2) a statement describing a price change, (3) a ceteris paribus assumption, and (4) various assumptions about the reliability of the data one is relying on, one can deduce a prediction about how demand will change. And one can then observe whether the prediction is true. But the point is to determine whether the evidence supports the hypothesis and to what extent. For example, suppose one finds that price and demand both decrease. Such apparently disconfirming data are readily available. Ought one to regard the law of demand as disconfirmed? Hardly. For demand also depends on other factors. That is why the law of demand states only that a change in price will, ceteris paribus, cause a change in quantity demanded. Given the many “disturbing causes” in economics and the difficulty of performing controlled experiments to weed these out, it seems that little can be learned from experience. And, if this is so, one must question whether economics can be a science. How these difficulties should be dealt with is a central concern of this monograph (see particularly Chapter 13).

The philosophical difficulty of pinning either the blame for predictive failures or the praise for predictive successes on particular elements in the amalgams from which testable consequences are derived is known as the “Duhem–Quine problem.”Footnote ¹² Pierre Duhem, particularly in The Aim and Structure of Physical Theory (1906), pointed out that scientists never test significant scientific propositions on their own. Testing a hypothesis involves deriving a prediction from a conjunction of many propositions, of which the hypothesis is only one. Even if one could capture formally the requirement that the hypothesis be essential to the deduction, there would still be the problem that a predictive failure could be due to the falsity of one of these other propositions. Consequently, economists can always “save” any given hypothesis by casting the blame on some other claim needed to deduce the implications they directly test. Moreover, if one takes the further step, which Quine endorses, of rejecting the distinction between analytic and synthetic statements and the notion of necessary truth, then the predictive failure could be due to a “mistaken definition” or perhaps even to the use of the “wrong” logic.

If the Duhem–Quine problem is posed as a purely logical difficulty, then it may not be in practice very serious. But, as argued in Chapter 13, if one is unable to place much confidence in the other premises needed to derive a prediction P from a hypothesis H, then there is a serious practical problem: it becomes almost impossible to learn from experience. This is the situation in economics.

Perhaps one should settle for a more modest account of confirmation. Richard Miller defends the view that confirmation is fair causal comparison (1987, chapter 4). One examines competing causal accounts of the evidence and prefers the account that offers the better explanation of that evidence. In Miller’s view, there is little more to be said in such abstract terms. All the substance lies in discipline-specific knowledge and standards that govern such causal comparisons.

A.8 Demarcation and Scientific Method

Although some philosophers have questioned whether the natural sciences have increased human knowledge, their best efforts impress one only with their cleverness; they do not lead to serious doubts about whether sciences have been epistemic successes. Furthermore, the achievements of science have not come entirely from individual genius and good luck, but they have had something to do with the institutional structure of sciences and the norms which guide scientific practice. It seems worth asking what rules guide science, which is what this book does, and what distinguishes sciences from nonsciences or pseudo-sciences. As discussed in Chapter 12, what distinguishes science from other inquiries was a major preoccupation of Karl Popper, who calls this “the problem of demarcation.” Unfortunately, as argued in Chapter 12, Popper fails to distinguish between two different problems of demarcation, and his solutions to both are failures. The problem of demarcation arises for anyone who wants to know what is distinctive about science. In my view, the problem of demarcation cannot be completely separated from the problems of theory assessment and the problems in characterizing the global structure of scientific theories.

The problem of demarcation has an increasingly important political significance, owing to both the authority of science in modern societies and threats to that authority. On the one hand, determining that some discipline is a science gives it a certain status. But on the other hand, increasing portions of the population, who do not understand the difference between anecdotal and significant evidence or who have economic or political reasons to deny scientific findings, are turning their backs on scientific conclusions and repudiating scientific argument. This is no trivial matter. Unfounded vaccine skepticism has, as I write, killed thousands of people, and promises to kill thousands more.

The philosophical point of the problem of demarcation must not be forgotten amid this political dispute. There are reasons why science has authority and prestige. Although its status is a sociological fact, there is something distinctive and important about science that does not depend on the social attitudes toward science. The problem of demarcation could still be important if the status of scientists were no greater than that of welders.

What is special about science is not that its claims are uniquely true. It would be absurd to maintain that science is the only source of truth or that whatever scientists (let alone economists) regard as well established is true. If science has any special claim on our regard, it is as an engine of discovery and as providing particularly good reason to believe its assertions. Popper and Lakatos would not approve of this formulation, for they deny that there are ever good reasons to believe the claims of science and because Popper denied that there was any method to discovery. But the basic sentiment, that science has an especially effective way of contributing to the growth of knowledge, was one that they fully shared, and it motivated their work on the problem of demarcation.

Despite these reasons to tackle the question of what distinguishes science from nonscience and pseudo-science, I agree with Laudan (Reference Laudan1983) that it is not the right question to ask. For, in addressing the differences between sciences and nonsciences as a single problem, one is forced to draw a single distinction where many distinctions should be drawn, and one is driven toward the view, which should be independently considered, that all sciences share the same methods of discovery and confirmation. One may, of course, offer a summary comparison and contrast between a science such as physics and activities such as philology, history, “scientific” creationism, or, for that matter, golf – just as one may offer a summary comparison and contrast between a science such as physics and quite different sciences such as archeology, computer science, or economics. But both the philosophical and political demands that give rise to the problem of demarcation are better addressed by focusing on more specific questions.

Setting aside the problem of demarcation as the wrong problem to pursue (except in the political arena), one would still like to know more about the special features of sciences: What rules, attitudes, and traditions govern scientific disciplines? How can one study markets or economies scientifically? The abstract discussions of the previous sections are motivated by such questions. For to understand theories and models, laws and explanations, confirmation and discovery, and the goals and observational basis of science, is largely to understand what sort of human activities sciences are.

In thinking seriously about methodology in a narrow senseFootnote ¹³ – about how to do the work of some discipline – it is important to be aware of the distinctively methodological perspective. Unlike the philosopher, who sees philosophy of science as a branch of epistemology and as casting up particular metaphysical, logical, conceptual, ethical, or aesthetic problems, the methodologist is primarily interested in understanding how a particular discipline works and how to make it work better. This distinction resembles the division of labor between theoretical and applied economics. Just as the methodologist wants to understand what makes some scientific practice tick and how to improve it, so the applied economist wants to understand how particular markets work and how to make them work better (Railton Reference Railton1980, pp. 686–7).

Put this way, it is an open question whether a methodologist is well advised to employ the tools of a philosopher of science. Perhaps the tools of a sociologist or of a literary critic might serve methodologists better (see §15.3). Some affinity between methodology and philosophy of economics is unavoidable, for in the attempt to improve economics the methodologist necessarily shares some of the normative concerns of the philosopher of science. Methodology cannot avoid its normative calling.

In my view, philosophy of economics can be in large part an empirical discipline, a sort of social science that studies the institutions and practices of economics in much the same way that economics studies the institutions and practices of economies. Questions about knowledge acquisition in economics can only be answered well if philosophers have learned what makes for good economic science. And, in my view, to learn about science, one needs to study science. This book is both methodology and philosophy of economics. In its concern with the particular problems that confront economists, it is intended as a contribution to economic methodology (particularly in Chapter 15), but it also focuses on epistemological questions cast up by economics.

If one goes to contemporary philosophy of science in search of hard and fast rules for scientific practice, one will be disappointed. Philosophers of science know a great deal about science, but that knowledge falls short of providing usable algorithms. Economists and many other scientists consequently often express disgust with so much “useless philosophizing” – and then proceed to do more of it, only less carefully and less knowledgeably. Some are tempted by a skeptical relativism that denies that there are any rules of scientific practice. As this monograph shows (especially in Chapters 15 and 16), such negative, relativist, and skeptical conclusions are unjustified, which is fortunate, for skepticism and relativism are cold comfort when one needs to decide what to do about unemployment (see §§15.2 and 15.3).

Although perhaps disappointed at finding no simple rules for doing science, economists should not overlook what philosophers have learned. Even the failures of oversimplified accounts of science have taught important lessons. There are some simple generalizations that apply to all empirical sciences – the results of experiments and observations are still what ultimately determine which theories are accepted or rejected – but such generalizations are not very useful. Sciences are not only very complicated institutions, but their norms depend on the content of current scientific knowledge. Valid and helpful accounts of the nature of sciences cannot be simple.

Nobody is going to learn how to do science from this appendix, for useful rules and hints lie at a lower level of generality and require more detail. One reason for writing a monograph such as this one is precisely the need to focus on the methodological details of a single discipline.

A.9 Social Theory and the Unity of Science

One theme which has surfaced frequently is that sciences are not all alike, and that philosophers and methodologists must be sensitive to the details of the disciplines they study. Even within the physical sciences there are large differences. Consider, for example, the allied fields of chemistry and physics. In the submolecular realm the two largely overlap, and parts of chemistry have been reduced to physics. But even here the differences must not be overlooked. Much of chemistry is, unlike physics, concerned with the properties of particular substances and with the molecular structure that explains these properties. Even if the laws the chemist relies on to study benzene, for example, are physical laws, the attention of the chemist is on the properties and molecular structure of substances, not on the laws. Economists have drawn analogies between economics and physics without asking whether these are the right analogies to stress. Are the resemblances to physics more instructive than the resemblances to chemistry, biology, or paleontology? I am inclined to agree with Sidney Morgenbesser, who suggested to me that economics is more like chemistry than physics.Footnote ¹⁴

It makes sense to look for both similarities and differences among the sciences. Philosophers of science have concentrated their efforts on a few disciplines, especially physics and biology, while paying little attention to other disciplines, such as electrical or chemical engineering or anthropology. One reason may be that the differences between engineering and theoretical physics are so large that philosophers had trouble seeing engineering as science at all. Yet electrical and chemical engineering are systematic empirical studies. They have theories and engage in extensive experimentation. Their results are used by “pure” scientists, and no sharp boundary can be drawn between them and physics “proper.” The neglect of engineering may be one reason why philosophers and methodologists have found economics so puzzling. For, as suggested to me by Hal Varian and as discussed in a well-known essay by Gregory Mankiw (Reference Mankiw2006), parts of economics are more like engineering than like physics. Consider the repeated efforts of economists to show that economic conclusions follow even if one denies the basic behavioral generalizations of economics (discussed in §§2.2 and 7.3). These efforts are deeply puzzling if one conceives of economics as a sort of social physics. Except to undermine support for particular physical laws, physicists are not trying hard to show that the phenomena would still obtain even if the laws of physics were different. But the practice makes perfectly good sense if economics is conceived of as a sort of engineering. For in engineering one wants “robust” conclusions that can be established in various ways.

In thinking about economics, one needs to recognize that there are important differences between physics, chemistry, electrical engineering, and population biology, but one must also pay attention to the fact that economics is a social science. As such, one might question whether it should be modeled after any of the natural sciences. Human beings and their social interactions are different objects of study than are planets, proteins, integrated circuits, or populations of rabbits or grasses. Should one’s goals or methods in investigating economies be the same as those of natural scientists? Many writers on the social sciences have insisted that there are fundamental differences between the natural and the social sciences (see Morgenbesser Reference Morgenbesser, Emmett and MacIntyre1970).

Those who have been concerned with this question of “social-scientific naturalism” – those who have asked whether the social sciences can be “real sciences” – have been concerned with several distinct questions. They have wondered about the possibility of social laws. Is there something about human behavior that makes the formulation of laws impossible? Second, they been concerned about explanation in the social sciences and about the goals of social theory. Third, many have questioned whether social-scientific theories develop and are tested in the same ways as those in the natural sciences. Finally, the policy implications of disciplines such as economics raise questions about the limits of objectivity in social theory and about the relations between fact and value in the social sciences. I argue that the fact that economics is a social science explains some of its most important methodological peculiarities.

A.10 Concluding Philosophical Remarks

This overview of basic issues in the philosophy of science should not encourage pessimistic conclusions. There is, to be sure, a good deal of disagreement among philosophers and much yet to be learned about science. But much has been accomplished. Although logical positivism finds few supporters today, this is not because of some change in intellectual fashion. With their intellectual honesty and their devotion to clarity, the positivists uncovered their own mistakes. The empirically oriented philosophy of science that has succeeded them has many inadequacies, as do the more recent cognitive science and sociological perspectives. But these begin with much of the knowledge that the positivists gained in the course of their efforts to capture the scientific enterprise within a formal empiricist framework.

These words are no comfort to citizens, policy-makers, economists, or other social scientists who want to know whether economics is a science, whether they should rely on particular economic theories, or how they can best contribute to economics or to some other social science. It won’t do just to say that the problems are difficult and that philosophers have discovered the mistakes of other philosophers. But, with respect to grand theories of science, philosophers cannot do better now. Unfortunately, they have only criticism and specific insights to offer. Given how complex and diverse sciences are, it is perhaps inevitable that there is no well-founded general philosophical system to resolve the methodological difficulties of economics.

This background in the philosophy of science helps explain the peculiarities of my attempt to clarify the methodology of mainstream economics. It is a rich background with many fruitful suggestions, insightful arguments, well-wrought concepts, and cautionary tales of philosophical work gone wrong, and I could not have written the book without studying it. But philosophy of science provides no simple algorithms. In addressing the problems of economics, one cannot use philosophy of science as a fundamentalist preacher might use the Bible in addressing the heathen. Its role is more like that which a graduate education in anthropology plays for the ethnologist. One must address the problems of economic methodology by studying economists and economics in the flickering light of epistemology.