I have argued that the insistence that economic phenomena be treated by a single unified theory – equilibrium theory in particular – has no general justification. Whether equilibrium theory is the best way to proceed is an empirical question, and there is little reason to reject other approaches because they cannot be integrated into a unified theory of an economic realm. But in reaching this, my principal critical conclusion, I have not yet addressed two powerful arguments that may appear to establish the permanent hegemony of equilibrium theory. Even if these arguments can be answered, this book has said little about the upshot of this philosophizing for the practice of economics. Finally, even if equilibrium theory has no methodologically privileged position, one might reasonably question whether an outsider can challenge the methodological practice of an established discipline such as economics. Is not such a challenge futile and arrogant? What possible authority do I have to preach to economists?

15.1 The Hegemony of Equilibrium Theory

Suppose a theorist were to offer a maverick explanation of some economic phenomenon $P$, which employed ad hoc behavioral generalizations that violate the strictures of Section 7.5. In assessing this explanation compared to an explanation that applies equilibrium theory, there are three possible cases: (1) there is a competing explanation of the phenomenon $P$ in terms of equilibrium theory and permissible additions; (2) equilibrium theory does not appear to have any relevance to $P$ at all; and (3) $P$ is anomalous from the perspective of equilibrium theory, which apparently implies that the phenomenon ought not to occur.

If (1) the phenomenon were also explicable in terms of equilibrium theory and permissible additions, then one might argue that the standard microeconomic explanation is necessarily preferable to the deviant explanation unless the deviant explanation is much better supported by the data or is grounded in a competing research program that promises to match mainstream economics in scope and heuristic power. For the standard explanation employs a systematic theory and links $P$ to an extensive range of other phenomena. Since unification is one goal of scientific explanation (Michael Friedman Reference Friedman1974; Kitcher Reference Kitcher1981), the microeconomic explanation is, ceteris paribus, the better explanation. Furthermore, as Max Weber (Reference Weber, Shils and Finch1949), Fritz Machlup (Reference Machlup1969), and many of the Austrian economists emphasize, one constraint, or, at the very least, desideratum, on the explanations of social phenomena is that they show such phenomena to be the consequences of intelligible or understandable human action (§A.9). Microeconomic explanations do this in a particularly powerful way, since they are extensions of the standard folk-psychological account of human action in terms of beliefs and desires (see §A.9). It is hard to see how a genuine alternative to equilibrium theory could possess these explanatory virtues to nearly the same degree that equilibrium theory does. The alternative might be better confirmed – in better accordance with the facts – and so economists might be driven from their allegiance to equilibrium theory. But, given the difficulties involved in testing and confirmation in economics, this is an unlikely prospect.

In case 2, where equilibrium theory is not relevant at all, one might question whether the phenomenon $P$ truly belongs to the domain of economics. Since economics is defined by its causal factors, it could not be irrelevant to any genuinely “economic” phenomenon, and it is hard to see how equilibrium theory could fail to be relevant to any phenomenon in its standard domain. Again, this thought is strengthened by the tradition of Weber and the Austrians, who emphasize that the social phenomena of interest to us are those upon which human action and deliberation bear.

The most interesting case is the last. Suppose one has an explanation of some economic phenomenon, $P$, which employs a theory such as Tversky, Slovic, and Kahneman’s “compatibility hypothesis” (§14.5), where $P$ would apparently be ruled out by equilibrium theory and standardly accepted auxiliary assumptions. Such phenomena constitute an argument for revising equilibrium theory or limiting its scope. One can always defend equilibrium theory by ad hoc attributions of particular tastes, information failures, and the like, but significant success by some alternative theory in explaining behavior that is largely inexplicable in terms of equilibrium theory presents a major challenge (like that posed – in the opinion of some economists – by Keynes’ theory). Yet most economists neither seek alternative theories nor believe that they can be found.

Russell and Thaler list three reasons why economists have been critical of anomalous experimental findings and are consequently unwilling to consider alternative theories that explain those findings:Footnote ¹ (1) “[i]n the real world, people will learn,” (2) “[e]conomists are interested in aggregate behavior and these individual errors will wash out when we aggregate,” and (3) “[m]arkets will eliminate the errors” (1985, p. 1074; see also Gul and Pesandorfer 2008). The second response is a nonstarter, when, as in the case of preference reversal, the errors are systematic, and I have no more to say about it. The first and third responses, on the other hand, call for careful discussion.

15.2 How to Do Economics

Suppose that the conclusions of the previous chapters concerning confirmation and theory appraisal in economics are correct: economists employ an uncontroversial method of theory assessment. Unfortunately, owing to poor data (relative to the state of economic knowledge), little can be learned about which theories are better confirmed. Given the initial credibility of the basic behavioral postulates of economics, it is rational to remain committed to them in the face of apparent disconfirmations. The consequence of such a defense is to leave economists unable to learn very much from typical economic data.

If this account is correct, economists desperately need better data in order to advance their theoretical knowledge, and in the first edition, I called for a serious redirection of effort among economists, which is in fact taking place (although not because I said it should). Such data gathering must not be divorced from specific objectives and problems, both practical and, especially, theoretical. Economists must be prepared to consider alternative kinds of theorizing, or else there is little point to such data gathering. Ways of getting better data include:

1. 1. A major commitment of resources to take advantage of experimental opportunities. Experimental economics has blossomed over the last half-century. This is a positive development and should be encouraged.Footnote ¹¹

2. 2. A general willingness to make use of observational data of all kinds. Much can be done to refine the techniques of field reports and social experimentation.Footnote ¹² Many economists have overcome the animus economists have traditionally felt toward the laborious process of gathering data and the precarious process of interpreting them.

3. 3. More active engagement by economists in data gathering in order to appreciate better the limitations of particular data sets. Although econometricians have recognized and emphasized this point, the structure of rewards within the economics profession for too long made involvement with data gathering costly to individual researchers. That is now changing, with Nobel prizes going to experimenters, behavioral economists, and development economists whose main activities consist of field experiments.

4. 4. Further work on improved statistical techniques for the analysis of data. Lacking expertise in econometrics, I have no clear conception of the limitations of current methods and am uncertain about how much can be hoped of further developments.

Of course, even improved data will not help theoretical knowledge in economics grow if economists are unwilling to entertain alternatives because of methodological commitments to a single style of theorizing. If unfamiliar explanations can command empirical support, they should be pursued.

I defend three changes in theoretical economics, which are already well under way:

1. 1. More work should be devoted to exploring alternatives to elements of mainstream economics that have already been proposed, such as Machina’s proposal to surrender transitivity and the independence principle, Loomis’ and Sugden’s regret theory, McClennen’s notion of resolute choice, Simon’s theory of procedural, bounded rationality, and, most obviously, the many proposals of behavioral economists such as Kahneman and Tversky’s prospect theory.

2. 2. More serious attention should be paid to the work of other social scientists. Whether economists have anything to learn from the results of any particular psychological or sociological research is an empirical question. The only legitimate reason to dismiss all work of other social scientists as of little interest would be if the separate science of economics were a smashing success. In the case of preference reversals, we can see that economists are paying serious attention to both the findings and theories of psychologists.

3. 3. Quite different styles of theorizing, such as that exemplified by the institutionalists should be encouraged, and empirical work studying problems faced by particular firms or groups of employees should be taken seriously by economic theorists.

What do these generalities mean in detail? (It is here that I am most painfully aware of the limitations of my knowledge.) The best I can do is to consider specific examples, some of which exemplify these methodological recommendations and some of which do not, and to call attention to their methodological virtues and vices.

But, before doing so, two central qualifications are required:

• Economics is a diverse enterprise, and there is no reason why it should become less diverse. Economists face many different tasks and questions. My focus is only on theoretical economics.

• There is absolutely no reason why all economists should employ the same styles and strategies of theorizing. If my methodological recommendations were to find general favor among economists, work devoted to the further elaboration of a separate science of economics – that is, to the articulation and application of equilibrium theory – should still be done. There is no alternative that is so obviously superior that it would justify everyone abandoning mainstream economics. What is wrong with economic theorizing is not what economists are doing, but what they are not doing and what they refuse to do.

15.3 Cautionary and Encouraging Examples

15.4 What Is to Be Done?

If this book’s general story is correct, what can be done to improve economics? One thing is to get economists to recognize how much the discipline has changed from the portrait textbooks provide. Given the structure of academic disciplines, including economics, fundamental change is slow and rarely the result of philosophical argument. Indeed, sensible economists will place little credence in the arguments of outsiders such as philosophers. Moreover those, if any, who are persuaded drastically to change their research profiles may find themselves exiled.Footnote ²³

One should not suppose that the incentives within the discipline will automatically favor the optimal mix of methodological commitments. The “meta-level” arbitrage argument that economists who employ a better methodology will convert or bankrupt those who employ a worse methodology is even weaker than the arbitrage argument concerning the behavior of economic agents. The competitive structure of scientific disciplines (see Hull Reference Hull1988) is quite different from the structure of markets, and in economics, there is the additional complication that financial interests may bias the work of economists. Although these distortions may be weak among academic economists, economists who are employed by firms, unions, think tanks, and political parties often need to adjust their conclusions to the interests of their employers. The obstacles in the path of empirical success in economics are so profound and the costs of empirical research are so high that measurable standards of excellence in economics, such as mathematical prowess, can persist regardless of whether they contribute to or hinder progress in the discipline.Footnote ²⁴

I am not competent to map out further reforms that economists ought to undertake. The most important step is to comprehend where the discipline has been and how it is changing. Many detailed changes still need to be made in the education of economists,Footnote ²⁵ in the incentives in the profession, and in the tenuous relationships between economists and other social theorists. The discipline has been in need of the major overhaul that it is currently undergoing.

15.5 Epistemology, Methodology, and the Practice of Economics

Having climbed briefly and precariously on to my soap box, I am pleased to step down and address the philosophical question of whether I should have been up there. One might question the possibility or point of “external” criticisms: can any outsider grasp the constraints governing the different tasks economists undertake well enough to be able to offer sensible advice? Regardless of how well supported such advice was, could it possibly have any effect?Footnote ²⁶ Even religious moralists with the authority of divine writ have had a hard time changing people’s behavior. How then could a philosopher, armed with little more than modus pones, change practices that are devised by smart, dedicated, and well-educated economists? One’s reaction at this point might shift from cynicism to annoyance. What impertinence! How dare Hausman pretend to legislate for economists?

These rhetorical questions, which can be asked about all normative enterprises, suggest healthy skepticism but nothing more. Consider the analogy between philosophers of science studying science and economists studying business. Can economists know enough about business to offer advice? Can their advice possibly have any effect? Is it not arrogant to suppose that economists could know more about how to run a business than individuals who have devoted their lives to some firm and whose livelihood depends on its success? Such questions counsel caution, but they do not justify repudiating economic assessment and advice.Footnote ²⁷ The analogous doubts about normative methodology do not automatically discredit the recommendations offered by a philosopher.

With regard to the complaint that methodology is futile, remember that the influence of this book depends on you as well as me. There is no doubt that normative theorizing, like all theorizing, generally has little immediate influence on human practice. But this realization provides no better reason to dismiss methodological advice than to dismiss moral precept. No doubt, economists are and should be reluctant to change their practices, and the force of argument is limited. But arguments can persuade, and good arguments can persuade rationally. If a case is clear, cogent, and accessible, let us suppose that it can have some effect too.

More interesting than these general complaints against all methodological criticisms are arguments directed particularly against accepting the advice of philosophers (hiss!). Consider the following grounds for hesitation:

1. 1. The philosophical theories that supported previous methodological advice have, one after another, collapsed with their own internal problems.

2. 2. Philosophical claims to special authority in methodological matters have been progressively undermined by the development of philosophical thought itself.

3. 3. The most influential philosophical recommendations of the twentieth century – that supplied by the logical positivists (at least in popularized versions such as Ayer’s Language Truth and Logic (1936; see §A.1) and that offered by Popper and Lakatos – are, in my view, in large part bad advice. Why should this book be any better?

These objections to philosophy of economics call for some comments on the nature of my enterprise. In doing so I also react to provocative work by Deirdre McCloskey, who has pressed such objections with particular force. In her book, The Rhetoric of Economics (1985a), McCloskey repudiates the whole enterprise of methodology.Footnote ²⁸

McCloskey and I agree that the distinguishing feature of economic methodology is its concern with the relationship between the practices and products of economics and general cognitive ends such as truth and predictive reliability. Methodology is concerned with whether the claims of economics are predictively reliable or true and how one can judge whether they are reliable or true; and it is concerned with whether the practices of economists lead to conclusions that one ought to rely on or to believe. This is not to say that methodology is exclusively concerned with questions of theory assessment, which has obviously not been the only issue in this book. But much of methodology is normative, and the standards employed are in part “external” general standards, such as those stating when one is justified in relying on claims for practical purposes and when one is justified in regarding claims as true or close to the truth.

When McCloskey argues for an end to methodology, she is arguing against any connection between specific evaluative standards and the concerns of epistemology. Why? Obviously, there are evaluative standards; norms are unavoidable features of every human enterprise. But one might question whether any norms are better than any others in leading scientists to acquire predictively valuable or true conclusions. Paul Feyerabend comes close to rejecting all norms (1975), but this extreme view is not McCloskey’s.

A slightly more moderate view is that no norms can be shown to be better than others in achieving predictively valuable or true conclusions. One might argue for this claim by maintaining that “good” arguments in economics are simply those that accord with whatever standards happen (for whatever reason) to be prevalent among economists. Many have read McCloskey as defending this radically skeptical conclusion. I do not think this interpretation is correct, because rhetoric – her replacement for methodology – is supposed to be concerned with good arguments, that is, arguments that not only happen to persuade but which ought to persuade (1985a, p. 29). Furthermore, McCloskey criticizes the conflation between economic and merely statistical significance, which is common in leading economics journals and thus presumably persuasive to many economists (1985a, chapter 9).

If McCloskey agrees that there are grounds to believe that some norms are better than others, why does she deny that there are specifically epistemological grounds for distinguishing which are better and which are worse? Although some of McCloskey’s reasons apply to all methodological inquiry, many are directed only against a particular kind of methodology, which one might call “a priori” or “conceptualist.” Positivists or, more generally (in McCloskey’s terminology), “modernists” are often taken to believe that methodological standards are determined by the analysis of concepts.

Regardless of whether McCloskey correctly interprets traditional conceptualist methodology or justly criticizes it, her critique of specifically “modernist” methodology is not an argument against all methodology. In my view, philosophical theses about how knowledge ought to be acquired and structured, such as those defended in this book, are justified just as other theses are. One asks, “how well do they enable my body of knowledge, including my perceptual beliefs, to hold together?” Epistemology has been, in W. V. O. Quine’s terminology, “naturalized” (1969). Like physics or anthropology, it aims to improve our beliefs. Only the narrowness of its questions, which is dictated by its normative role, distinguishes epistemology from other empirical studies of the acquisition and revision of human beliefs.

The methodological inquiry in this book embodies this vision of philosophy. People acquire knowledge. To find out how, one must study what they do, without presuming that there is only one good way to learn. To find out how people have learned, and to find out which methods have been successful in which circumstances, one must study what has been done and how well it has worked. Insofar as McCloskey is only insisting that those interested in economic methodology must study how economists argue, I fully agree.

But McCloskey wants to draw more radical conclusions.Footnote ²⁹ She wants to repudiate all methodology, not merely a priori methodology. Apart from her critique of a priori methodology, she seems to have three main reasons for denying that economists can be held to “external” cognitive standards justified by epistemological considerations.

First, McCloskey asserts, “[n]othing is gained from clinging to the Scientific Method, or to any methodology except honesty, clarity, and tolerance” (1983, p. 482). Her point seems to be that external standards are vacuous. Truly informative and substantive standards are context dependent. They will be determined by features internal to economics, not by general epistemological considerations. The failed efforts of philosophers to provide contentful context-free accounts of notions such as confirmation or scientific explanation suggest that substantive norms will be context-specific (Miller Reference Miller1987). But the conclusion that no significant transdisciplinary claims can be made and that there can be no role for epistemology depends on the false assumption that epistemological claims can make no reference to context. Just how methodological rules should depend on features of the context of inquiry is itself an important epistemological question.

Second, McCloskey argues that “[i]t would be arrogant to suppose that one knew better than thousands of intelligent and honest economic scholars what the proper form of argument was” (1985a, p. 139). But epistemology seems arrogant only if one falsely assumes on the one hand that these “intelligent and honest economic scholars” agree on an internally consistent methodology that coheres reasonably with the rest of their beliefs and on the other hand that the methodologist drops from a philosophical cloud. As we have seen, there is plenty of methodological controversy among economists, and philosophers can learn some economics before issuing edicts. Since there need be no arrogance when economic scholars themselves invoke epistemological concerns, it is not automatically arrogant of outsiders to do so.

Finally, McCloskey argues that the methodological standards defended by the epistemologist depend on a chimerical notion of Truth (with a capital “T”) (1985a, pp. 46–7; 1985b, pp. 136–7; 1988a, pp. 255–6). This claim is confused. Truth is an objective, not an evidential criterion. McCloskey argues that the standard of good argument is whatever persuades the majority of competent economists. There is no other success to be obtained and no other objective to aim for.

This argument rests on a failure to distinguish among different issues. First, it is not true that all invocations of epistemology are bound up with the notion of truth, for not all epistemologies are realist (§A.2).Footnote ³⁰ The instrumentalist wants only predictively useful hypotheses. Second, although both instrumentalist and realist economists aim to persuade other economists, they seek to persuade not as an ultimate goal, but because they take success in persuasion to be a fallible result and indication of having made a good argument. Working among a set of corrupt and depraved colleagues, one might be disconcerted by persuasive success.

Third, the fact that truth and future reliability are not grounds for accepting conclusions is entirely consistent with the aspiration of making true or reliable claims. The truth of $P$ is not an argument in favor of believing $P$. One might persuade someone that tariffs are harmful by shouting with an air of great certainty: “It’s true! It’s true!” But shouts are not arguments. One might as well simply recite: “Tariffs decrease economic welfare. Tariffs decrease economic welfare. Tariffs decrease economic welfare.” Truth is what one seeks, not one’s evidence. Similarly, the greater future predictive success of $P$ as compared to $Q$ is no evidence or argument now in favor of $P$. Future predictive success, like truth, is a goal, not evidence. This platitude gives one no reason to be suspicious of the notions of truth or predictive reliability.Footnote ³¹

In addition, although this is not one of McCloskey’s arguments, one might argue that the proposal to find out how to do science by studying scientifically how people do science is multiply paradoxical. If one does not already know what science is, one will not know which practices to study, and if one does not already know how to do science, one will not know how to study those practices. Either one cannot start at all, or one must begin by assuming that one already knows the answers one is looking for. But, if one must beg all the significant questions, what point can the exercise have? (See Hausman 1980 or 1981a, postscript.)

The trick is to beg the questions in the right way. There is nothing wrong with beginning with the presumption that one knows how to find out what norms govern institutions such as theoretical economics, provided that one’s initial presuppositions are subject to correction in the course of inquiry (Friedman Reference Friedman1979). I began this methodological study of economics with many unavoidable presuppositions, which I have tried to scrutinize, piecemeal. Philosophy of economics, as I have attempted to practice it, thus resembles history, sociology, literary criticism, and economics itself as much as it resembles conceptual analysis.

I see no grounds to conclude that this sort of empirical methodological inquiry is misconceived. There is no good general philosophical case against the possibility of investigating empirically how people learn, what sorts of methods work best for which sorts of problems, or how one can best insure against the sorts of mistakes people are prone to make. Such questions are not purely psychological, although psychological evidence may bear on them. Investigations into the history and current state of science are also relevant to their answers. In any event, they are real questions. They appear to be answerable, and their answers may be of normative importance.

Moreover, appraisals of economics that draw on epistemological theses are inevitable. For the very terms in which one describes the practices of economists – theorizing, testing, deducing, modeling, sampling, and so forth – carry philosophical baggage. McCloskey unavoidably begins with such notions, and her object – the discourse of economists – is already penetrated through and through with philosophical influences. Could these philosophical influences on the methodological inquirer or on the object of inquiry ever be transcended? I doubt it, and, even if they could, they will be with us for a long while yet.Footnote ³²

Furthermore, at least one kind of normative epistemological theory, the Bayesian view of confirmation, is itself an application of central claims of economic theory. For economists to refuse to pay attention to the norms proposed by Bayesian epistemologists would be to refuse to heed the implications of more or less their own models. Epistemology is unavoidable.

Finally, as Alexander Rosenberg has argued (1988a), if economics ever succeeded in repudiating all epistemology and answered only to its own standards, it would lose its influence on noneconomists and its rational hold on economists themselves. If the standards of acceptance among economists had no connection to epistemologically significant goals, such as reliability or truth, then the fact that a particular conclusion was accepted by most economists would be of no more interest to policy-makers than is the fact that a particular conclusion is accepted by most astrologers.

These comments do not constitute a defense of the conclusions and recommendations of this book. They stand or fall on their merits. I have only argued that there is nothing misconceived about the project of appraising mainstream economics as an intended contribution to human knowledge.

This book has focused on the epistemological peculiarities of a special human cognitive enterprise: mainstream economics. It has not broached the central problems of epistemology or of philosophy of science in their full generality. Its conclusions concern economics, and although some are of general significance, many are not relevant to other disciplines, even other social disciplines. For example, although Richard Miller in his Fact and Method eloquently insists upon the importance of the particular problems and standards that characterize different disciplines, he endorses the philosophical platitude that scientific theories postulate the existence of unobservable things to explain generalizations at the level of observations (1987, p. 135). To make sense of economic theory, one should reject this view. Similarly, the extent to which the view of models and theories defended in Section 7.3 helps to illuminate economics provides an argument for the cogency of that general view. The discussion of Milton Friedman’s methodology helps one to disentangle different positions that might be called instrumentalist (§A.2) and shows that instrumentalists need to be concerned about truth, even if their ultimate goals are purely practical. The discussion in Chapters 13 and 14 of how evidence bears on utility theory illuminates the tenuous general relations between theory and data.

It would be tedious to compile a list of examples such as these, and, in any event, my main concern is economics, not general philosophy of science. Instead, in closing, I shall attempt to bring together the main theses of this book and to show how they clarify and explain the most prominent methodological peculiarities of economics. The fact that economics is a social science – a science of human beings (§A.9) – is crucial to its distinctive methodological problems.

16.1 The Structure and Strategy of Mainstream Theoretical Economics

Part I offered a general account of the structure and strategy of theoretical economics, which is summarized in Figure 3.6. I argued that equilibrium theory – that is, the generalizations of consumer choice theory and the theory of the firm – lies at the heart of mainstream theoretical economics. Mainstream economics is the articulation, elaboration, and application of equilibrium theory.

It is unhelpful to maintain that equilibrium theory is the hard core of a Lakatosian scientific research program, because mainstream economists are free in particular inquiries to drop some of the constituents of equilibrium theory and even to replace them with contraries. A commitment to equilibrium theory is only a commitment to some subset of its components and to a modeling style. Some of the generalizations that constitute equilibrium theory are more central than others, but if one attempts to say what theoretical economics is by identifying some common core of propositions that are shared by every model or theory, one will not be able to give an informative characterization. What Lakatosians might be inclined to call the “negative heuristic” does not forbid tampering with equilibrium theory. It effectively forbids removing rational acquisitiveness and the possibility of equilibrium from their central places, but the characterization of this “pseudo-hardcore” is left open: nonsatiation can be replaced with satiation, but claims about cognitive dissonance are suspect. Incompleteness or intransitivities can be explored, but psychological generalizations about procedure variance are unwelcome. At the same time, although not specific to economics, Lakatos’ emphasis on the unity of research programs and the importance of their “positive heuristic” provides a helpful framework for characterizing equilibrium theory.

Equilibrium theory consists of the theory of consumer choice, the theory of the firm, and the thesis that equilibrium obtains. This last constituent fits awkwardly, for it appears as a theorem rather than as an axiom, but it is a central constituent nevertheless. All the parts of equilibrium theory are problematic. In the theory of the firm, only the law of diminishing returns is relatively solid. Constant returns to scale shows up to ensure mathematical coherence rather than for its empirical success. Maximization of net returns not only appears to be false, but it is in conflict with utility maximization by members of firms in most institutional settings.

The theory of consumer choice consists of utility theory, acquisitiveness, and diminishing marginal rates of substitution. It is less problematic than the theory of the firm, for acquisitiveness and diminishing marginal rates of substitution seem to be reasonable first approximations, at least with respect to market behavior, and (ordinal) utility theory is perhaps a plausible approximation. In the context of choices among a finite number of options, continuity is harmless, and, although transitivity may break down, there is obviously a good deal to be said for its correctness with respect to the limited set of options among which individuals are choosing. Completeness is the most problematic of the axioms of ordinal utility theory, though perhaps not in the context of complete certainty (but that context is itself problematic).

As I understand scientific theories, they consist of sets of lawlike statements that are systematically interconnected; and I thus identify equilibrium theory with the laws of the theory of the firm and of consumer choice, plus the assertion that equilibrium obtains. But these laws do no work by themselves. In both theoretical and empirical inquiries, laws are always combined with simplifications and specifications of relevant circumstances. Some of these simplifications, such as infinite commodity divisibility, perfect information, or perfect competition are pervasive and help determine the character of theoretical economics. But these simplifications are not assertions or discoveries of economics.

Theories in mainstream economics can be classified as partial or general equilibrium accounts. Partial equilibrium analyses treat a small number of markets in relative isolation, while general equilibrium theories attempt to deal with general interdependencies among markets, although this is less true of highly aggregative general equilibrium models with few commodities. Mathematical investigations of abstract general equilibrium models have been methodologically puzzling, since the models are not even approximately true of existing economies. I argued that they are best interpreted as conceptual investigations, investigations of possibilities, or attempts to develop heuristically useful tools.

Equilibrium theory, not general equilibrium theory, is the fundamental theory of mainstream economics. In addressing general interdependencies, as opposed to single markets or small groups of markets, general equilibrium theories augment equilibrium theory with simplifications or specifications concerning the circumstances to be studied. In addition to practical applications, as in forecasting models or input–output models, general equilibrium theories serve as a proving ground for new tools and are used to explore whether equilibrium theory will be able to serve as the core of a separate economic science.

To make sense of this theoretical enterprise requires distinguishing between models and theories. Models are predicates or definitions of predicates. The assumptions of models are clauses in definitions and not true or false assertions about the world. However, the investigation of models typically involves scrutinizing a fictitious world, conjured up so as to allow economists to pretend that there is something of which the predicate the model constitutes or defines is true. Provided that this heuristically attractive way of proceeding is understood to involve fictions, it is harmless and may be fruitful. As I argued in Chapter 6, one crucial component of science is the articulation of new concepts in terms of which to theorize. But once philosophers and economists take literally the claim that models create worlds and make possible experiments, which have the same or even superior epistemic credentials as laboratory experiments have, I jump ship, for this vessel is headed for a metaphysical shipwreck.

When one offers a general theoretical hypothesis asserting that a model is true of some realm of reality, then one is offering a theory; and in offering the theoretical hypothesis, one is committed to treating what were the assumptions of the model as assertions about the world. Despite what they sometimes say, economists do not treat equilibrium theory as merely a fundamental model, to which no empirical commitments pertain. For economists believe that they can predict and explain economic phenomena by means of equilibrium theory.

Central to mainstream economics has been the thought that economists are concerned with a set of causal factors or “laws,” which predominate in a particular domain of social life. These laws are generally well known and make up accepted economic theory, which provides a unified and complete, but inexact, account of the entire economic realm. This vision expresses a methodological commitment to what Mill called “a separate science” of economics. Other generalizations about preferences, beliefs, and constraints may be added to economic models and theories, provided that they do not conflict with the central place within the economic realm of rational acquisitiveness or make equilibrium impossible. To employ any other generalizations is ad hoc. No changes in fundamental theory itself are welcome that do not preserve its universal scope. The further features of human behavior that psychologists and sociologists discover are, from this perspective, typically ad hoc and only have a narrow scope. They are usually not suitable for inclusion in particular economic models and are typically disqualified from inclusion within fundamental theory. The methodological commitment to a separate science, which is fortunately waning, leads to the view that equilibrium theory is (at a suitable level of abstraction and approximation) the whole theoretical truth about economics.

This methodological commitment to the structure and strategy of a separate economic science explains why economists theorize as they do. I argued that it is unjustifiably dogmatic. The methodological commitment to a separate science of economics preserves the scientific appearance of economics and spares economists the maddeningly difficult and disorderly task of floundering among disparate data, attempting to identify significant causal factors. It preserves the aesthetic attractions of economics and keeps it a tractable subject for mathematical exploration. The commitment to a separate science maintains the close connection between the empirical theory of how people choose and the theory of how they rationally ought to choose, which in turn provides a strong pragmatic argument for treating apparent disconfirmation as error. And this commitment is essential to the normative argument for perfectly competitive equilibrium, which underlies both conservative defenses of laissez-faire and liberal analyses of market failures.

This vision of economics is appealing, and it is easy to understand why economists have been so deeply committed to it, but I have argued that it stands in the way of empirical progress.

16.2 Appraising Microeconomics and General Equilibrium Theory

Part II was concerning with theory appraisal, and it was as much critical as constructive. Many hundreds of pages have been written concerning how to assess economic theories, much of it unhelpful in large part because questions of theory appraisal in economics have rarely been joined to a detailed treatment of its structure and strategy. When economists fail to take apparent disconfirmations as refutations, methodological critics accuse them of adhering to an unreasonably dogmatic theory of confirmation or as failing to live up to their scientific standards. But, as I have argued, their actions may instead be consistent with an uncontroversial view of theory assessment, given the limitations in economists’ knowledge and the constraints on experimentation, which together drastically limit the evidential relevance of predictive successes or failures. If economists are sometimes unreasonably dogmatic, it is usually because of their commitment to regarding economics as a separate science, not because of their views of theory appraisal.

Further complicating the story are Milton Friedman’s influential views, which direct economists to be guided entirely by the success of the relevant predictions of their theories. This advice is impractical, quite apart from the internal problems with Friedman’s methodology. Friedman’s advice has rarely been followed, and to implement it would require that economics be radically transformed. Yet, since Friedman presents his views in defense of theoretical “business-as-usual” against critics of standard economics, one finds economists espousing Friedman’s methodology who would never dream of seriously acting on it.

Add in the influences of Popper and Lakatos and the confusions deepen. Popper was a natural authority to look to, for he was a leading philosopher of science. Moreover, his political views and his views concerning the methodology of the social sciences appeal to many economists. His message may appear at first glance consonant with Friedman’s (Blaug 1976). But, if Popper were right about how to do science, then economists would show a massive failure of methodological nerve. If one takes seriously what Popper says about falsifiability and the critical attitude, then the methodological practice of economics is not only mistaken, it is intellectually scandalous. Although this book has been critical of features of the methodology of economics, it has shown how researchers of intelligence and scholarly integrity could be committed to it.

One can better defend the honor of economists by adapting Lakatos’ methodology of scientific research programs, since it is flexible enough that few practices can be unequivocally condemned. Yet some developments in economics that are widely regarded as central theoretical advances (such as the switch from cardinal to ordinal utility theory) must be seen from Lakatos’ perspective as evidence that the “neoclassical research program” is degenerating. Furthermore, Lakatos’ categories do not fit the practices and products of economics easily and his rejection of “justificationism” is an invitation to epistemological disaster.

Friedman, Popper, and Lakatos, each in his own way, would prevent us from relying on supporting evidence. But, in interpreting experimental failures and in gambling on theories in new circumstances, economists need to make careful use of the evidence bearing on the propositions involved. It is only because of the importance of such evidence that there is a special difficulty about testing in economics. There is no special logical problem deriving predictions from economic theory and other statements. The difficulty is that the other statements referred to here are so far from the truth that the test results tell us nothing about economic theory. It is difficult even to envision an activity that paid no attention to supporting evidence. It would be nothing like the sciences we know.

To appraise economic theory sensibly, one must also come to terms with its inexactness. While inexactness is not a virtue, it is not a mortal sin either. Inexactness must be distinguished from other sorts of empirical shortcomings, and one must explain how inexact sciences can be understood, criticized, and defended. The inexactness of equilibrium theory should be understood mainly in terms of tendencies or vague ceteris paribus qualifications. Until one understands how counterfactual or qualified claims can be true or false, valuable or valueless, and confirmed or disconfirmed, one is in no position to recognize the extent to which equilibrium theory is true, valuable, or confirmed.

The theory of confirmation is a difficult and puzzling area in philosophy of science, and I do not know exactly how theories should be appraised. Neither do scientists, including economists. If progress in science depended on having scientific method exactly right, there would be no progress in science. There is a good deal of truth to the simple story that says that one derives predictions from a hypothesis and other premises and draws conclusions concerning how likely it is that the hypothesis is correct “on the basis of”Footnote ¹ the success or failure of those predictions. Economists do exactly this, but they are blessed with the knowledge that there is a great deal of truth to equilibrium theory, and they are cursed with such difficulties in testing that they are rarely in any position to change their initial assessment. The weakness of the empirical control exerted by economic data provides for a legitimately large role for pragmatic factors. Choices about whether to deal with disconfirmations by means of fundamental theory modification or by the introduction of disturbances or interferences (which in many contexts do not need to be mentioned) will turn not only or mainly on the data, but on the sort of exactness one thinks obtainable, on the jobs the theory is supposed to do, and on the aesthetic, systematic, heuristic, and normative virtues the alternatives may have.

This looks like Mill’s inexact method a priori, his deductive method, but it is not a special theory of confirmation at all, and its apparent dogmatism arises from the precarious relevance of the data coupled with the good reasons economists have to find some truth in equilibrium theory.

16.3 Reasons and Causes: Rationality and Economic Behavior

If one says that Elizabeth’s preferences are complete, transitive, and continuous, one is offering empirical generalizations about her. These generalizations assert matters of fact. They are testable. And, unless Elizabeth is unlike the rest of the species, they are not all true, although there is a good deal of truth to them. Similarly, to connect Elizabeth’s actions to her preferences by asserting that Elizabeth never prefers an option she believes to be feasible to the one she chooses, is, on the ordinary understanding of the notion of preference, an empirical claim (although the theory of revealed preference mistakenly takes choice as defining preference). As many have pointed out, this generalization is not easy to test (Boland Reference Boland1981; Caldwell Reference Caldwell1983). To employ these generalizations – that is, utility theory – to explain why Elizabeth chose some option is to say only that she chose it because she most preferred it. Hamlet killed Claudius because he preferred to. Such explanations are vacuous and shallow. Utility theory can be used to explain Elizabeth’s choices only if it has something to say about what determines her preferences among the immediate objects of choice.

When economists employ consumer choice theory to explain why individuals chose some bundle of commodities, they give the agent’s reasons more clearly, and they also seem to provide a more definite causal explanation. Acquisitiveness and diminishing marginal rates of substitution are substantive “laws” of preferences. They have no obvious connection to rationality per se, and they are easier to test. The preference for more commodities and services over fewer is the motive force (“greed”), and diminishing marginal rates of substitution is a psychological constraint governing economic preferences. Utility theory guarantees the consistency of the chooser and derives a choice from acquisitiveness, diminishing marginal rates of substitution, and further facts. Both the causal story and the reason for the choice are clearer than in an explanation employing only ordinal utility theory.

Since an explanation employing consumer choice theory can be construed as a causal explanation, one might be tempted to regard the reason-giving aspect and the fact that utility theory is a theory of rationality as merely extra detail, some “local color” that is irrelevant to the explanatory logic of theoretical economics. But it seems to me that many of the distinctive methodological characteristics of economics can be understood better if the reason-giving feature of explanations in economics is taken seriously. In particular, the fact that utility theory is a theory of rationality helps to explain the following:

1. 1. Why the notions of Pareto optimality and Pareto superiority are so pervasive and appealing in welfare economics and why ethical concerns are so often intermingled in positive economic theorizing (§4.4 and Chapter 8).

2. 2. Why economists have such a strong empirical commitment to utility theory as the best account of how agents in fact choose (Chapters 13 and 15).

3. 3. Why economists follow their distinctive theoretical strategy (Chapter 7).

Much of the methodological distinctiveness of economics stems from the remarkable fact that a normative theory of rationality lies at its theoretical core.

1. 1. Pareto optimality. In Section 4.4 I sketched an argument for the moral approval (ceteris paribus) of perfectly competitive equilibrium on the basis of equilibrium theory and “minimal benevolence” (that, ceteris paribus, it is a morally good thing to make people better off). Equilibrium theory identifies people’s well-being with the satisfaction of their preferences, and it provides the premises for the welfare theorems which show that perfectly competitive equilibria are Pareto efficient and that all Pareto optima can be achieved as competitive equilibria. Rationality, in the form of utility theory, is specifically presupposed by the notion of Pareto efficiency and is central to welfare theorems and to the identification of well-being with the satisfaction of preferences. It is because preferences are reasons that the satisfaction of preferences has a claim to be a matter of prudence and thus a claim on the beneficence of others.

   Consequently, any challenges to the empirical adequacy of equilibrium theory, or to the argument for the Pareto optimality of the consequences of individually rational behavior in competitive markets, bear immediately and forcefully on the argument for perfect competition that relies on minimal benevolence. Hence a positive conceptual investigation such as Samuelson’s has immediate moral reverberations that are evident in Meckling’s and Lerner’s responses. Challenges or qualifications to individual rationality or to its consequences undermine the moral claims of competitive markets.

2. 2. The commitment to utility theory. As I argued in Chapter 15, the fact that utility theory is a theory of rationality can give one additional reason to favor it as an empirical theory of human preference and choice. The instability of irrational behavior and the educative effects of theories of rationality provide reason to believe that a theory that portrays individuals as behaving rationally is more likely to be true than a theory that depicts them as behaving irrationally. Furthermore, a theory which depicts actual behavior as rational permits explanations to be reason-giving as well as causal. These explanations can be accepted by economic agents as well as by economic theorists, and they permit actions to be appraised.Footnote ² Such a theory may also have better effects on how people will behave than a theory that describes people as irrational. Although these last pragmatic factors must take second place to empirical adequacy, they can have a large influence on theory choice in a discipline such as economics in which empirical adequacy is so hard to judge.

3. 3. Why economists follow their strategy. There are many reasons why it is hard to get knowledge in economics. In particular, I have stressed the inadequacies of the data with which economists have to work. Some of the limitations in these data have been economists’ own fault, since they have in the past avoided gathering or using certain kinds of evidence; but both the multiplicity of causal factors and the practical and moral problems of experimentation are serious difficulties, which can be mitigated but not eliminated.

One impediment to progress in economics, about which economists are in the course of addressing, is the hegemony of the vision of economics as a separate science. This hegemony is due in large part to the fact that equilibrium theory contains a theory of rationality. Utility theory links equilibrium theory to the plausible explanatory strategy embedded in everyday “folk” psychology. Generalizations concerning social phenomena that are not in terms of the beliefs and preferences of agents or the constraints on their actions are ad hoc and in need of explanation in these terms. Generalizations that cannot be explained in these terms are inherently unstable, because “people will learn,” or at least enough of them will that the competitive pressure of the market will bring them into line.

Theoretical constraints are necessary to focus research and to motivate the investigation of esoteric questions. But the justification for a particular paradigm or research program, like the justification for the commitment to economics as a separate science, is success and progress, including especially empirical success and empirical progress. How successful and empirically progressive theoretical economics has been is controversial. There are many nitty-gritty examinations of specific questions, but these often employ scarcely more theory than the assumption that people respond rationally to incentives. When theorists and experimenters in other disciplines have generated potentially relevant generalizations and data, economists should be eager to reach out and incorporate this material into their theorizing.

When one recognizes the centrality of rationality, one can understand better why so many economists are deeply committed to equilibrium theory and to the image of economics as a separate science. Linked to the notion of a separate science is not only the heuristic power of microeconomics but also the rational prescriptive force of utility theory and the moral argument for perfectly competitive equilibrium. Any step away from equilibrium theory weakens these links between purported facts, rational oughts, and moral oughts and surrenders the vision of a unified theory of economic phenomena. It is hard to give up so much.

If, as I believe, there are systematic failings of human rationality, and economic behavior is significantly influenced by many motive forces, apart from acquisitiveness and diminishing marginal rates of substitution, then equilibrium theory is an enfeebled theory, regardless of whether there is anything better. If factors from which the separate science of economics abstract are important influences on economic outcomes, mathematical expertise and elegance in modeling will not save the day.

The edifice of contemporary mainstream economics is gorgeous, and it can often help solve specific predictive problems. But its empirical difficulties are serious and, if the speculative thoughts of these pages are correct, it will never fully conquer them. Furthermore, concerns about rationality are unavoidable, and normative policy implications will always be close at hand to generate bias. The problems are serious, but there are ways forward. Although some theorists should keep pushing the current strategy as hard as they can, I applaud the extent to which economists have become more eclectic, more opportunistic, more willing to gather data, more willing to work with generalizations with narrow scope, and more willing to collaborate with other social scientists.