Chapters 11 and 12 canvassed the main twentieth-century alternatives to the method a priori. None shows how economists can rationally commit themselves to a highly inexact science such as economics. Each of the alternatives runs into internal philosophical difficulties, and (except Koopmans) each implies drastic changes in methodological practice.

Perhaps methodological practice in economics was due for a major overhaul. Many writers on methodology, including myself in the first edition, called for a greater engagement with the details of actual economic relations among individuals and firms. Let us look again at Mill’s deductive method and the criticisms it faced to see what is defensible and what is mistaken.

As I said before, Mill’s inexact deductive method has been subject to logical, methodological, and practical criticisms:

1. 1. The logical criticism, which one finds in Hutchison and to some extent in Samuelson, maintains that inexact (ceteris paribus) laws are scientifically illegitimate, because they are meaningless or unfalsifiable. But the arguments in Chapters 9 and 10 show that qualified claims are not meaningless or untestable and, as argued in Section 12.2, no interesting scientific claims are logically falsifiable.

2. 2. The methodological criticism of Mill’s inexact deductive method, which one finds in Popperians such as Mark Blaug, is that it is too dogmatic: it rules out the possibility of disconfirming the basic “laws.” Adhering to Mill’s inexact deductive method thus, it is alleged, impedes the progress of economics and leads to ad hoc responses to apparent disconfirmation characteristic of a degenerating research program. I accept this criticism of the method, but not generally of economists, who, despite appearances, rarely adhere to it.Footnote ¹

3. 3. Furthermore, methodological vice is alleged to lead to practical impotence by authors such as Hutchison and, from a different perspective, Friedman. Even if the inexact laws and the other statements needed to deduce a prediction are true, the unspecified ceteris paribus clauses mean that the prediction follows only if there are no interferences. Since these ceteris paribus qualifications are vague, it is hard to know when they are satisfied. If economists do not know when they are satisfied, then economic theory is of little use in practice. For practical purposes, economists need to know what will happen if a policy is instituted, not what would happen if there were no disturbing causes. Even if Milton Friedman’s views are mistaken, at least he is concerned about when theories actually work. Does not the reliance on the deductive method render economics useless?

Although the methodological rules of Mill’s inexact method a priori, as summarized at the end of Chapter 10, cannot be defended as stated, I shall nevertheless defend (for the most part) the existing practices of theory assessment among economists. These practices appear to follow Mill’s inexact deductive method, but they are, I contend, also consistent with standard methods of theory appraisal in the special circumstances with which economists have to cope. Although apparent Millians in practice, economists can be good Bayesians or hypothetico-deductivists in principle.Footnote ² After demonstrating this possibility in Sections 13.1 and 13.2, I sketch the method of theory appraisal economists typically employ, and I discuss the large and legitimate role of pragmatic factors in economic theory choice. Only then does this chapter discuss the practical objection. The chapter concludes by pointing to the real source of dogmatism in economics.

13.1 Apparent Dogmatism and the Weak-Link Principle

To maintain that economists should never attribute apparent disconfirmations to shortcomings in their theories is unjustifiable. To this extent, the critics of the deductive method are correct. To follow such a rule would preclude theoretical and empirical progress. Such a rule is objectionably dogmatic.

It looks as if economists are adhering to this rule, but, given the tasks and difficulties economists face, widely accepted theories of confirmation, such as the Bayesian and hypothetico-deductivist views, recommend confirmational practice that is largely indistinguishable from what Mill’s inexact method a priori recommends. The methods of theory appraisal economists employ may be defensible, even though the method a priori is indefensible, and economists appear to conform to it.

It is not unacceptably dogmatic to refuse to find disconfirmation of economic “laws” in typical failures of their market predictions. When the anomalies are those cast up by largely uncontrolled observation of complicated market phenomena, it may be more rational to pin the blame on some of the many disturbing causes, which are always present. Since the confidence of economists in the simplifications and ceteris paribus assumptions necessary to apply economic theory to actual market phenomena will generally be much lower than their confidence in the basic laws, the more likely explanation for the apparent disconfirmation will usually be a failure of the simplifications and ceteris paribus assumptions. In consequence, little can be learned about the purported laws from such observations, but the failure will lie in the difficulties of the task, not in methodological mistake. The possibility of discovering errors in the “laws” of equilibrium theory may be foreclosed by the inadequacies in the data and limitations in economic knowledge, not by unjustifiable methodological fiat.

In responding this way to apparent disconfirmation, economists are implicitly relying on what I call “the weak-link principle”:Footnote ³

This is but one of many principles that economists might use in modifying a model so that it conforms to some observation and serves as a reliable predictive tool. Scientists and nonscientists alike use the weak-link principle, and (pace Popper) it is rationally justifiable to do so. If either $G$ or $B$ is false and the subjective probability of $B$ is less than that of $G$, then (other things being equal) it is more likely that $B$ is false than that $G$ is. However, the weak-link principle is neither inviolable nor always appropriate. Details concerning the model’s failures might point to a different premise as the culprit.

Since the simplifications and ceteris paribus clauses needed to derive predictions concerning uncontrolled market phenomena from equilibrium theory are the weak links, mistaken predictions rarely disconfirm the theory. Hence, one can see why Mill’s views seemed so plausible and were so easily refuted, and yet why methodological practice apparently continues to conform to them.

Given their subject matter, economists are bound to look like followers of Mill’s inexact deductive method. Powerful tests require either experimentation, with its possibilities of intervention and control, a great deal of knowledge, or good fortune in finding natural experiments, and without such tests (or superior alternatives) it would be irrational to react to apparent disconfirmations by surrendering credible hypotheses with great pragmatic attractions. If economists could do experiments easily, then they could control for disturbances and avoid the complexity of the phenomena with which they are presented nonexperimentally. If they knew enough, they could exert much the same control even if experiments are not possible. If they were blessed with a comparatively simple set of phenomena such as those of celestial motion, then neither the inability to experiment nor the paucity of their knowledge would be crippling. But the combination of these handicaps makes knowledge of economic phenomena hard to garner.

Limitations in the ability to test can make the basic “laws” of economics de facto unfalsifiable, even if economists were explicitly employing a Bayesian account of confirmation (§§10.1 and A.7). Let $H$ be either a “law” of equilibrium theory or a conjunction of such laws and $A$ be the conjunction of all the other statements needed to derive a prediction, $e$ from $H$. The prior probability of $H$, $Pr(H)$ is much larger than the prior probability of $A$, $\text{Pr}(A)$. In the case of uncontrolled market predictions, $\text{Pr}(A)$ will be tiny. For each of the simplifications and ceteris paribus qualifications is improbable, and the probability of the conjunction will be much smaller than that of the separate conjuncts. If $e$ is deducible from $H\&A$, then $\text{Pr}(e/H\&A)=1$, but that does not imply that $\text{Pr}(e/H)$ is large. Given how weakly evidence bears on $H$, the credible “laws” with which economists begin will be de facto nonfalsifiable.

13.2 Are Economists Too Dogmatic?

The deficiencies of market data coupled with the weak-link principle will mimic Mill’s inexact method a priori only if economists judge the “laws” of equilibrium theory to be much more probable than the simplifications and ceteris paribus claims that are needed to test them. Given the empirical problems with those “laws,” can such a judgment be defended? And, if it cannot be defended, then are not economists as unjustifiably dogmatic as critics of the method a priori have alleged?

Few economists regard the “laws” of equilibrium theory as proven or obvious truths, although they may take them for granted when trying to predict the outcome of some proposed policy. Only some fancy philosophical footwork permits one to regard these “laws” as true (see Chapter 9), and it is questionable whether they can be regarded as well established (see Chapter 10). Why then do economists takes these behavioral postulates for granted? Why do they make use of them in the face of their apparent disconfirmation? Is it introspection, as Mill maintains, or everyday experience, as in Robbins’ view, or are these assumptions implicit in the very concept of action, as has been maintained by Austrian theorists such as von Mises (Reference Mises1978, p. 8)?

A full answer would take us back to the discussion of the theoretical strategy of economics in Chapter 7 or forward to the conclusion of this chapter. Everyday experience and introspection are sufficient to establish that some of these laws, such as diminishing marginal rates of substitution and diminishing returns, are reasonable approximations. Without qualifications and a margin of error, they are false, but with these they are unlikely to lead one astray; and economists have good reason to be committed to them.

Furthermore, each of the laws of equilibrium theory possesses pragmatic virtues, for each plays an important role in making the theory mathematically tractable, consistent, and determinate. Indeed, this is about the only virtue of the postulate of constant returns to scale, to which economists are not nearly as committed. Constant returns to scale figures in many economic theories for essentially mathematical reasons, and because it is hoped that its falsity does not do much harm.

Claims such as acquisitiveness and profit maximization are not such good approximations to the truth as are diminishing returns or diminishing marginal rates of substitution, but neither are they as poorly established as constant returns to scale. And what is the alternative? There is a great deal of truth to them, and their virtues in permitting determinate mathematical formulations are considerable. Firms pursue all sorts of objectives besides profits, and a usable theory that heeds these facts should be more accurate. But the accuracy would be purchased at the cost of complexity, and complications could destroy the normative force equilibrium theory has when it is coupled with minimal benevolence. In such circumstances, pragmatic factors may justifiably be more than empirical tie-breakers. If the empirical benefits of a theory change are small – that is, if (1) a slightly more accurate theory does not serve the often practical purposes of economists appreciably better and (2) economic theorists do not believe that an appreciably more exact or useful economic theory is feasible – then the pragmatic virtues of current theory may be decisive. It may be more sensible to treat other objectives of managers and other behavioral generalizations concerning individuals as disturbing causes that may usually be ignored, even if they are important in particular contexts.Footnote ⁴

Thus, one finds a combined empirical and pragmatic basis for refusing to regard the basic propositions of equilibrium theory as disconfirmed. Although not necessarily unjustifiably dogmatic, there is a serious risk that economists become so entranced by their models that they overlook anomalies and do not consider alternatives. As Mill so presciently remarked (though only when criticizing his father, not his own work):

In my view, the dogmatism of economists, such as it is, lies in an overly complacent commitment to equilibrium theory and to the theoretical strategy underlying it, not in a mistaken view of theory appraisal.

Because economists have reasonable grounds for judging their basic explanatory and predictive generalizations to be less open to revision than are the simplifications and ceteris paribus claims that are also needed to derive conclusions about market phenomena, they may behave in the way that Mill’s inexact deductive method recommends, without being committed to a dogmatic view of theory appraisal. The apparent dogmatism may be just the result of the good fortune of beginning with a set of plausible generalizations coupled with the bad luck of being unable to perform good tests. Consider these remarks of Robert Lucas (Reference Lucas1980, pp. 710–11):

How can one tell whether economists are committed to Mill’s inexact method a priori or whether they are good Bayesians or hypothetico-deductivists doing the best they can in the face of poor data coupled with informal sources of knowledge? If the only data economists could gather were the results of uncontrolled observations of markets, then we might not be able to find out what the methodological commitments of economists were. But experimentation in economics has never been impossible, and in some experiments going back to the middle of the twentieth century, the auxiliary assumptions – the additional premises needed to derive predictions from equilibrium theory – have been sufficiently strong links that the experimental results could actually disconfirm the theory. By examining how economists have responded in such cases, one can determine whether they are proponents of a dogmatic theory of confirmation or whether their apparent dogmatism in nonexperimental circumstances is a rational response to weak evidence.

13.3 Expected Utility Theory and Its Anomalies

Although I cannot offer a comprehensive survey of how economists have reacted to well-established anomalies, I offer some examples here and in Chapters 14 and 15. Expected utility theory (§1.3) has many of the same axioms as equilibrium theory (including completeness, an axiom I focus on). It is, like parts of equilibrium theory, a theory of rationality, and it is accepted on the same sort of grounds as equilibrium theory. But unlike equilibrium theory it is readily testable. Consequently, it is easier to consider how apparent disconfirmations bear on expected utility theory.

The case for expected utility theory, as for equilibrium theory, seems to rest upon an application of Mill’s inexact method a priori. Consider the following remarks of Daniel Ellsberg:

Ellsberg is pointing out that economists sometimes accept theories, such as expected utility theory, because the axioms appear “reasonable.” The credibility of the axioms is largely prior to any testing of predictions derived from the theory.

One cannot regard the axioms of expected utility theory as proven scientific truths, though one may say on their behalf (1) that they are, as Ellsberg notes, “reasonable”; (2) that there is some experimental evidence that confirms them; and (3) that, if people do not conform to the axioms of expected utility theory, then, contrary to observation, they may make fools of themselves.Footnote ⁵ These grounds provide the axioms with some credibility, and (via the weak-link principle) they provide the theory with an ability to withstand casual falsifications.

Unlike equilibrium theory, expected utility theory is readily testable, and the assumptions necessary to derive predictions from the theory need not always be weak links. Psychologists and decision theorists have shown that human behavior sometimes does not conform to the “laws” of expected utility theory. Some of these anomalies can be explained as the consequence of nonrational disturbing causes – such as the result of minor peculiarities in how people process information or of people’s failure to take small differences in probabilities seriously.Footnote ⁶ Others are more troubling. Let us see how economists and decision theorists do and should deal with some of these.

13.4 Behavioral Economics and Methodological Changes

One way to determine whether economists are committed to the dogmatic method a priori or whether they are instead handicapped by the complexity of the phenomena coupled with the inability to experiment is to see what happens when economists discover new possibilities for exerting or finding experimental controls. Do they continue to defend their theories from the possibility of disconfirmation, or do they modify them when their implications are not borne out by the data? Do they expand the range of the variables and relations discussed in their theories as they acquire the ability to make testable and significant claims about them?

Over the last half-century, slowly at first but with an increasing pace, economists have discovered new possibilities for both laboratory and field experiments, and they have uncovered ways to interpret changes in policies and other historical events as if they were experimental interventions. Although some economists have argued that much of this experimentation is irrelevant to economics (notably Gul and Pesandorfer 2008), experimentation and historical investigation that identify natural experiments have become standard tools of economics. Fifty years ago, the leading journals published only a tiny fraction of the empirical investigations to be found in the same journals today. Chapter 14 is devoted to an extended case study concerning the reception by economists of psychological investigations purporting to reveal the existence of preference reversals. In that history, one can trace the evolution of the responses of economists to this phenomenon, from attempting to explain it away, to attempting to relegate the problems it suggests to peripheral aspects of economic models, to uncomfortable acceptance of the phenomenon, and then finally to inquiry concerning its causes and the ramifications.

One serious issue raised by critics of behavioral and neuroeconomics,Footnote ¹⁶ such as Gul and Pesandorfer, concerns the relevance of behavioral and neurological findings to the questions that economists are concerned with, which focus on the aggregate consequences of individual choices rather than on the idiosyncratic factors that are responsible for preference rankings. The discovery that people are no less cooperative when hungry (Reynolds Reference Reynolds2019) may be very useful to an employee approaching her boss for a raise before lunch, but it doesn’t bear significantly on our understanding of economic fluctuations or the properties of markets.

Although a fair criticism of some work in behavioral and neuroeconomics, these qualms do not apply to all of it. Consider, for example, anchoring, loss aversion, framing, and the endowment effect. Many experiments show that individuals “anchor” their evaluation of alternatives to a reference state of affairs, typically the status quo, and they assess gains and losses from that reference point differently. People weigh losses more heavily than gains with both marginal losses and marginal gains of diminishing importance. People’s choices reflect a value function shaped like the one shown in Figure 13.1.

Figure 13.1 Anchoring and loss aversion.

Like a standard preference ranking, this value function is supposed to determine choices, but unlike a preference ranking, it depends on the reference point, and for that reason it is obviously context dependent. Contextual factors that affect people’s reference point, which are irrelevant to a preference ranking that satisfies the standard axioms, can dramatically shift the rankings of alternatives. Tversky and Kahneman (Reference Tversky and Kahneman1981) present the following striking example, which is by now very well known. They asked groups of subjects to assess alternative policies to treat a disease that threatens the lives of 600 people. When given the choice between programs A and B in Table 13.2, about three-quarters of experimental subjects prefer program A.

Other experimental subjects were asked to compare Programs C and D in Table 13.3. Faced with a choice between C and D, about three-quarters of experimental subjects prefer program D. Yet A and C are descriptions of the same state of affairs, as are B and D. Anchoring and loss aversion explain this framing effect. The same outcomes look different depending on whether the reference point is the death of 600 people (and one’s action is seen as saving 200 for sure or 600 with a probability of one-third) or whether the reference point has all 600 living with policies permitting the deaths of different numbers.

Because people weigh gains and losses differently, their choices depend on the reference point. Rather than unsystematic failures of the axioms, these data identify an additional systematic influence on choice, which is relevant to the behavior of consumers and firms. As Kahneman et al. put it:

The crucial points are, first, that these anomalies show that the influence of the diverse factors that motivate people cannot be summarized in a single ranking that is complete, transitive, context independent, and choice determining; and second, that some of the divergences are systematic and predictable. The preferences of consumers and the ranking of investments by firms are likely to depend significantly and regularly on the reference point from which individuals evaluate alternatives.

Loss aversion is also manifest in the so-called endowment effect (Kahneman et al. Reference Kahneman, Knetsch and Thaler1991) whereby individuals demand more to part with some commodity than they would have been willing to pay to acquire it. Although the effect was demonstrated with students and coffee mugs, the phenomenon is far from trivial. As Benjamin Friedman (Reference Friedman2005) argues, loss aversion and the endowment effect are among the factors that make redistributive policies so much more difficult to implement when there is little economic growth. When the economy is growing, redistribution will look to those who lose out to be a lesser improvement rather than a loss.

The newly discovered factors that affect choice behavior derive from a blossoming of empirical economics. This takes the forms of laboratory experimentation, field experimentation, and the exploitation of natural experiments, particularly with the assistance of instrumental variable techniques. Empirical investigation of economic phenomena has always faced serious problems. Economists can hardly cast some individuals into poverty to observe the effects of an unexpected loss of wealth on a random sample. It would be unethical and scarcely feasible. Giving some random sample of the population $1,000,000 to observe the effects on consumption might be ethical, but it would be prohibitively expensive. Controlled experiments on participants in realistic markets are difficult to carry out, given how many factors there are to control for. When controlled experiments are possible, economists face the huge (“external validity”) problem of determining whether the findings in the controlled environment of the experiment will hold true outside of the laboratory.

These problems are ineliminable, but economists have found ways of lessening them. Modeling interactions between firms or consumers as simple games has made it possible to simulate economic problems facing market participants by interactions among students and other experimental subjects communicating via computer terminals. Shifting from explicit controls to the control exercised by randomization has made it easier to investigate specific putative causal factors and has lessened (although certainly not eliminated) the problems of external validity.

Randomized control trials are especially useful in field experiments, where explicit controls are infeasible, but field experiments raise special problems of external validity, because they are necessarily carried out within a specific and typically not-well-understood social context. For example, the Tamil Nadu Integrated Nutrition Project (TINP) provided nutritional education to pregnant women in rural districts of the state of Tamil Nadu and apparently greatly lessened malnutrition among infants. Encouraged by these results, policy-makers instituted a similar program in Bangladesh, where it failed. The explanation lies in a difference in an additional causal factor: in Bangladesh, mothers-in-law distribute the family’s food, while in Tamil Nadu, mothers do (Cartwright and Hardie Reference Cartwright and Hardie2012).

Although the TINP was not a randomized control trial, it illustrates the difficulties of extrapolating a finding from one context to another. Moreover, since not all of the districts in Tamil Nadu received this assistance, one might conjecture that the receipt of the assistance was close enough to an experimental intervention that the results could be attributed to the intervention rather than to unknown confounding factors. Such conjectures can be more or less reasonable, and sometimes the implementation of policies can be sequenced so as to create an experiment. For example, Mexico’s PROGRESA (Programa de Educación, Salud y Alimentación), which is a comprehensive antipoverty program combining health care, education, and nutrition, was implemented gradually, with the first locations chosen randomly and the outcomes compared to locations in which PROGRESA had not yet been implemented. Although there is always some possibility that the districts in which PROGRESA was first introduced differed in some other relevant regard from districts in which PROGRESA had not yet been implemented, such a study should count as a randomized control trial. The fact that the experiment is part of the implementation of a policy may create a risk of bias, but it is otherwise irrelevant.

Natural experiments are not easy to find, because of the importance of confounders, but sometimes there are ways around the problems. For example, consider Angrist’s (Reference Angrist1990) study of the effects of serving in the Vietnam War on lifetime earnings. The possibility that young men from less affluent families were more likely to enlist rules out any simple attribution of the lesser earnings of veterans to having served in the military. But an individual’s number in the draft lottery, which determined whether the individual was “draft eligible,” counts as an intervention. Because draft eligibility is determined by a random process, one can attribute the earnings differences between those who were and those who were not draft eligible to the difference in draft eligibility. (Of course, it is possible by chance that those whose numbers in the draft lottery made them eligible to be drafted all happened to be less valuable employees, but this is enormously improbable.) Knowing the effect of draft eligibility on lifetime earnings, Angrist could then use information concerning the proportions of draft-eligible and draft-ineligible men who wound up serving in the military to reach a conclusion concerning the effect of military service on lifetime earnings.Footnote ¹⁷ Draft eligibility serves as an instrument that permits inferences concerning the effects on earnings of military service.

In explicitly causal language, one can explain the definition and use of instrumental variables as follows. If economists want to determine whether $X$ causes $Y$, in circumstances in which there are likely to be unmeasured confounders, they cannot draw any causal conclusions from observing a correlation between $X$ and $Y$. But if there is some other variable $Z$ that is (1) a cause of $X$, that is (2) independent of any confounders of the relationship (if any) between $X$ and $Y,$ and (3) has no causal connection to $Y$ unless there is a causal path from $Z$ to $Y$ via $X$, then $Z$ counts as an instrumental variable, and the discovery of a correlation between $Z$ and $Y$ is strong evidence that $X$ causes $Y$.

Figure 13.2 An instrumental variable.

In Figure 13.2, economists cannot determine whether $X$ causes $Y$ from information concerning whether $X$ and $Y$ are correlated, owing to the possibility of unknown confounders, $W$. But if there is a cause of $X$, such as $Z$, that has no causal relationship to $Y$ apart from a causal relationship that it might have in virtue of causing $X$, then the discovery of a correlation between $Z$ and $Y$ is evidence that $X$ causes $Y$. The causal inferences economists can draw on the basis of measuring the correlation between $Z$ and $Y$ presuppose causal knowledge concerning the relationship between $Z$ and the other variables. For example, Angrist’s conclusions rest on the premises that draft eligibility does not affect lifetime earnings, except via its effects on military service, that draft eligibility increases the probability of military service, and that draft eligibility is not caused by another of the other variables including possible confounders.

Although the ethical and feasibility constraints on economic experimentation remain, economists are now able and willing to confront economic hypotheses with evidence. For example, instead of concluding (plausibly) that an increase in the minimum wage increases unemployment among unskilled workers, because firms can substitute machinery or more highly skilled workers for the now more expensive unskilled labor, economists have taken advantage of natural experiments to discover that relatively small increases in the minimum wage have little effect on the employment of unskilled workers (Card and Kreuger Reference Card and Kreuger1994).

13.5 The Economists’ Deductive Method

We are now in a position to formulate a schema sketching a “deductive” method of theory appraisal that is both justifiable and consistent with existing theoretical practice in economics, insofar as that practice aims to appraise theories empirically. For, as I stressed earlier (§§6.4, 7.3, and 7.4), a good deal of theoretical work in economics is still concerned with conceptual exploration, not with empirical theorizing.

To facilitate the comparison of what I am calling the economists’ deductive method with Mill’s inexact method a priori, I have juxtaposed sketches of the two methods in Table 13.4.

The economist’s deductive method, unlike the inexact method a priori, is consistent with standard views of confirmation. What justifies continuing to call it a deductive method, despite its concessions that the inexact laws with which one begins are not proven and that they can be refuted by economic evidence? First (in sharp contrast to the methodological views discussed in Chapters 11 and 12), independent direct confirmation of the basic inexact laws plays a crucial role.Footnote ¹⁸ Second, refutation is largely proscribed, albeit by the circumstances, not by methodological rule. Since economists are typically dealing with complex phenomena in which many simplifications are required and in which interferences are to be expected, the evidential weight of predictive failure will be small. It will rarely be rational to surrender a well-supported hypothesis because of a predictive failure in circumstances such as these. The Allais problem exaggerates the weight of evidence because of its quasi-experimental basis.

The simplified account of the economist’s deductive method sketched earlier follows the hypothetico-deductive method (§10.1) precisely in steps 2 and 3 and is consistent with it in steps 1 and 4, where it is merely more specific. The hypothetico-deductive method is mute on where hypotheses to be tested come from and permits one to begin with a theory with known empirical and pragmatic virtues.

The fourth step of the economist’s deductive method abbreviates Section 13.3.2. It is consistent with the hypothetico-deductive method, which merely requires that the correctness or incorrectness of the predictions contribute to the appraisal of the hypothesis tested. The empirical grounds for discriminating between theories in the economist’s deductive method remind one of Lakatos’ formulations, and they direct one to consider what theory modifications or qualifications best explain the data and best increase the confirmed empirical content of the theory. It will be extremely difficult to judge theory modifications on empirical grounds, because of the acute practical Duhem–Quine problem in economics (§A.7), which is a consequence of how dubious are the various auxiliary hypotheses that are necessary in order to perform most tests. Pragmatic grounds may consequently play a large role. If one cannot tell which theory modification is empirically better, it is sensible to choose the one that has greater pragmatic virtues – that is, the one that it is easier to use, gives sharper advice, lends itself to cleaner mathematical expression, and so forth.Footnote ¹⁹

Yet, when experiments are possible and when alternatives are available that inherit the initial credibility of the accepted theory and offer similar pragmatic advantages, then the economist’s deductive method favors theory change. If one studies how economists respond to experimental anomalies, one can see that they are not committed to a dogmatic view of confirmation, such as the inexact method a priori. The case study in Chapter 14 provides evidence for this claim. The dogmatism one used to find in economists’ responses to anomalies, which resulted more from a commitment to an image of economics as a separate science than from any theory of confirmation, has not disappeared, but it has faded. Many modifications are proposed, discussed, and tested.

13.6 The Deductive Method and the Demands of Policy

The one remaining criticism of the deductive method is practical: in following a deductive method, economists allegedly condemn their work to practical futility. This criticism is mistaken. The economist’s deductive method does not rule out theory changes when doing so will increase the empirical content of the theory – on the contrary, it mandates them. Nor does it – or any other variety of the deductive method – condemn empirical generalization. Mill is explicit in endorsing common sense on this point: if something works, use it (though with due caution). Moreover, the development of empirical generalizations, for which no deductive derivation is currently possible, is of great theoretical importance too, for such generalizations constitute the most important data for which theories need to account. There are, as we saw in Section 7.5, methodological rules against employing ad hoc generalizations – that is, generalizations that do not permit rational choice explanations, that do not give pride of place to consumerism, that have narrow scope, or that rule out the possibility of equilibrium. But these result from the vision of economics as a separate science, not from distinctive views of theory appraisal.

The economist’s deductive method does not recommend repudiating useful empirical generalizations or abandoning accurate predictive devices. Instead, it condemns naive reliance on unreliable empirical generalizations, and it offers an additional means of getting a predictive grasp on the phenomena. Whether the best way to aim an artillery piece is by firing it in various circumstances and fitting a curve to the data points or by calculating from fundamental laws is an empirical question. Rather than forbidding the first procedure, the deductive method offers a way of improving, correcting, and extending the results one gets by it.

If the standard theory of the firm had all the empirical virtues claimed for it by Milton Friedman and others, then one should make use of it for relevant practical purposes. The economist’s deductive method does not recommend theoretical purism that spurns useful tools that are not in perfect condition or perfectly understood. By considering the realism of a theory’s assumptions – the constituent causal processes and their laws – one may be able to get some guidance concerning when the predictions of the theory are likely to break down and concerning how to modify the theory in the face of apparent disconfirmation.

13.7 Conclusion: Economics as a Decreasingly Separate Science

What may stand in the way of developing generalizations that are of practical utility is not the deductive method per se but Mill’s vision of economics as a separate science: as a discipline that is concerned with a domain in which a small number of causal factors predominate. I argued in Chapter 7 that this vision of economics as a separate science, although not often expressed in this terminology, remains central to contemporary microeconomics. Mainstream microeconomics, macroeconomics, and general equilibrium theory presuppose that a single set of causal factors underlies economic phenomena and determines their broad features. Other relevant causal factors are countenanced typically only as disturbing causes, whose influence must be acknowledged, but which do not form a part of the central theory. Their effects are allegedly significant with respect to a narrow range of cases; while, without its many specific qualifications, the basic theory is still purportedly a good general guide. As already noted, Mill makes such a pragmatic case:

To surrender the understanding of economics as a separate science would be to part with the grand vision that a single theory could provide one with a basic grasp of the subject matter. A considerable number of economists are now willing to pay the price, and they have paired up with psychologists, political scientists, neurologists, and much less frequently with sociologists and anthropologists. However, the temper and character of modern economics still embodies the Millian vision of the discipline as a separate science.

Can one better understand economies by applying equilibrium theory, or would economists do better to develop a variety of different theories with narrower domains and a larger repertory of causes? The latter alternative would lower the barriers between economics and other social sciences, since the causal factors with which sociologists and psychologists have been concerned may be important in particular economic subdomains. Although the question is an empirical one, the answer also depends on the objectives and uses of economic theories. For a separate science of economics has aesthetic appeal, heuristic power, and normative force, none of which economists will willingly sacrifice unless the more fragmented and less purely “economic” alternatives have similar virtues and fit the data much better. So long as the data consist of noisy economic statistics, I doubt that the sacrifice will often appear worthwhile.

But, with the development of experimental economics and with increasingly sophisticated field research, this situation is changing; and if twenty-five years from now I undertake a third edition of this book, its title may no longer be appropriate. The central economic theories may have more structural similarities to the sorts of theories favored by institutionalist economistsFootnote ²⁰ than to contemporary microeconomics, macroeconomics, behavioral economics, and general equilibrium theory. But I have no crystal ball, and it may be impossible to generate additional significant theories that provide any appreciably better grip on the data than do contemporary mainstream theories. In that case, economics will go on as it has; and critics may continue to complain that economists are not behaving as responsible scientists should. But before criticizing prematurely, they should recognize that the apparent dogmatism can arise from the circumstances in which economists find themselves – blessed with behavioral postulates that are plausible, powerful, and convenient, and cursed with the inability to learn much from experience.

Economists are committed to equilibrium theory because they regard its basic laws as credible and as possessing heuristic and pragmatic virtues. Their response to anomalous market data, which mimics the inexact method a priori, is not illegitimately dogmatic. It is, on the contrary, consistent with standard views of theory assessment, once one takes account of how bad these data are. The problem is not a moral failing among economists – their inability to live up to their Popperian convictions – but a reflection of how hard it is to learn about complex phenomena if one does not know a great deal already and can do few controlled experiments.