I'm going to repost a few items from the summer--when many regular readers were doing better things with their time--which might still be of interest now that we're back in our regular routines. This item was ORIGINALLY POSTED ON JULY 16, 2004. With the pseudo-Nobel Prize in Economics being awarded on Monday, it seems particularly timely to revisit this one.
As fate would have it, an economist has been posting on the topic du jour--the scientific status of economics: see Tyler Cowen here and here. Professor Cowen's perspective on this question (rather typical of economists, I fear) is well-expressed by a colleague of mine:
"I guess the reason that I think economics is a science is that empirical testing is a huge part of economics. I.e., if economics were only about the mathematical models, without falsifiable claims, I would agree it's not scientific. But economics makes falsifiable claims all the time and tests them frequently. And some are confirmed, repeatedly, and they become accepted wisdom. Others are falsified, and they fall by the wayside. Isn't that what science is all about?"
This isn't, however, what "science is all about" on any plausible account. Pest control, for example, would be a science on this account (exterminators operate with evidentiary hypotheses ["ah-ah, tell-tale rat droppings!"], which they test ["since it's rats, we'll lay this kind of poison"], and which are sometimes falsified ["well, I'll be damned, it turns out it's not rats, but field mice"]), which doesn't seem the right conclusion. And lots of paradigmatic scientific propositions ("there are black holes," "there are quantum singularities") wouldn't be "scientific", because they aren't falsifiable (I owe the examples to Larry Laudan). Some philosophers of science go further, and argue that no claims are falsifiable (on evidentiary or logical grounds) because of the underdetermination of theory by evidence (the "Duhem-Quine" thesis as it is known) (Laudan has interesting arguments against this point--a nice presentation is in the so-titled chapter on undeterdetermination in his Science and Relativism [Chicago, 1990], which is still the best introduction to the subject I've read.)
So empirical testing and falsfiability can't be all that's at stake here. So is economics a science?
As it happens, this is a topic I’ve written on a few years ago. What follows is excerpted, with some editing, from my contribution on “Holmes, Economics, and Classical Realism,” in S.J. Burton (ed.), The Path of the Law and Its Influence: The Legacy of Oliver Wendell Holmes, Jr. (Cambridge University Press, 2000). The main subject of this essay was Holmes’s place in an intellectual tradition I denominate “classical realism.” But given Holmes’s prescient (for a lawyer) interest in economics as a predictive science, a section of the essay discussed this topic. There is little original here, mostly a synthesis of the work of others. “PJ,” below, is a reference to Posner’s The Problems of Jurisprudence. Some references and footnotes have been omitted; others have been inserted in to the text. I will be interested to hear from economists where I’ve gone wrong here. Do see the Addendum at the very end too.
As Richard Posner observes:
“Economists pride themselves on being engaged in a scientific endeavor. From the basic premise that people are rational maximizers of their satisfactions the economist deduces a variety of hypotheses, of which the best known is the "law of demand"--a rise in the relative price of a product will, other things held constant, cause a reduction in the quantity of the product demanded. These hypotheses are confirmed or refuted by studies of actual economic behavior.” (PJ, 362-363)
It is important to remember that a lot of the credibility of economics depends precisely on its claim to be a science, in the precise sense of generating successful predictions. (Predictive power may be neither a necessary nor sufficient condition for science, but economists generally view it as what makes their discipline "scientific.") Indeed, many economists and lawyer/economists have emphasized the putatively "scientific" character of economic theory. Friedman's classic paper on "The Methodology of Positive Economics" is predicated on the idea that economics is "a positive science [whose] generalizations about economic phenomena. . .can be used to predict the consequences of changes in circumstances." This, of course, is also Posner's view. In his Nobel Lecture, laureate George Stigler puts it this way: "The central task of an empirical science such as economics is to provide general understanding of events in the real world, and ultimately all of its theories and techniques must be instrumental to that task" (emphasis added). Indeed, most economists would probably agree with Mark Blaug that "no time [should] be wasted defending the assertion that economics is a science."
All of these scientistic sentiments about economics co-exist, of course, with a very different picture of the discipline as essentially a pseudo-science. It is better, perhaps, than astrology, but not much more predictively successful than common-sense psychology. It parlays a set of implausible and utterly unrealistic assumptions into tidy, mathematically-expressible theories that have little or no connection to reality. A recent article in The New Yorker captures this sentiment well. "[A] good deal of modern economic theory," says the author, "even the kind that wins Nobel Prizes, simply doesn't matter much.” (“The Decline of Economics,” Dec. 2, 1996, p. 50). The article continues:
“If economics had made the same intellectual progress as physics or chemistry, it wouldn't matter that it often appears baffling and impenetrable to the layman. . .[But] it is gradually becoming clear that the attempt to convert economics into an exact science has failed.” (52)
The New Yorker uses the example of Nobel laureate Robert Lucas's anti-Keynesian theories attacking the ability of the Federal Reserve to affect the economy, theories that exerted a profound affect on public policy for some time. "[A] number of [subsequent] empirical studies" (55) disconfirmed them…. [other examples omitted].
This debunking view of economics is not merely the stuff of popular culture. A recent study by the American Economic Association found that top economics graduate students were better trained in "formal modeling techniques than" in solving "real world problems" and that nonacademic employers "registered disquiet about the ability of the profession's recruits to conduct empirical research" (William J. Barber, "Reconfigurations in American Academic Economics: A General Practitioner's Perspective," Daedalus 126 (1997), pp. 87-103, at pp. 96-98.) Legal academics who actually do empirical work confirm this worry. They have routinely found economic treatments of their subject-matters to be detached from the reality. (See, e.g., the work of the "Texas empiricists," including: Julius Getman & Thomas Kohler, "The Common Law, Labor Law, and Reality: A Response to Professor Epstein," Yale Law Journal 92 (1983), pp. 1415-1434; Julius Getman & F. Ray Marshall, "Industrial Relations in Transition: The Paper Industry Example," Yale Law Journal 102 (1993), pp. 1803-1895; Ronald J. Mann, "Explaining the Pattern of Secured Credit," Harvard Law Review 110 (1997), pp. 625-683; Thomas O. McGarity, "The Expanded Debate Over the Future of the Regulatory State," University of Chicago Law Review 63 (1996), pp. 1463-1532; Teresa Sullivan, Elizabeth Warren, & Jay Lawrence Westbrook, As We Forgive Our Debtors: Bankruptcy and Consumer Credit in America (Oxford: Oxford University Press, 1989); Elizabeth Warren & Jay Lawrence Westbrook, "Searching for Reorganization Realities," Washington University Law Quarterly 72 (1994), pp. 1257-1289.)
Often, modern economic analyses of law turn out to be remarkably indifferent to the empirical facts. Even predictions generated from the Coase Theorem--the cornerstone of modern law-and-economics--have been empirically falsified! (See Robert Ellickson, Order Without Law: How Neighbors Settle Disputes (Cambridge, Mass: Harvard University Press, 1991)). The Coase Theorem says that "if there are no transaction costs to impede bargaining, legal rights will be allocated efficiently through private exchanges, regardless of the underlying rule of law." Robert Cooter, "Against Legal Centrism," California Law Review 81 (1993), pp. 417-429, at 419 n. 6. As Cooter explains: “Liability rules can be structured in different ways. With cattle, for example, the law can make owners of cows responsible for fencing them in ("closed range") or non-owners responsible for fencing them out ("open range"). Coase reasoned that owners will fence cows in or non-owners will fence them out, whichever is cheaper, regardless of the law. . ..Ranchers need only bargain together. . ..The law simply tilts bargaining against the party who is legally liable. Thus the law affects who pays for the fence ("distribution prediction"), but not its extent or location ("efficency prediction"). Id. at 419. What Ellickson found is that neither prediction was borne out among real ranchers that Ellickson studied in Northern California. Cooter notes: "Not only does the Coase Theorem fare poorly in empirical tests, but theorists who have tried to prove it mathematically usually conclude that it is either false or a tautology." Id. at 422. None of this, remarkably, has undermined its importance for the "science" of economics!
Philosophers, too, have recently launched a devastating attack on the scientific and cognitive credentials of economics, starting from the observation that, "[E]conomic theory [is] one of the more dismal empirical failures in the history of science" (John Dupre). This is widely conceded about the laughably unsuccessful predictions of macroeconomics, but it is only somewhat less true of microeconomics, which "has made no advances in the management of economic processes since its current formalism was first elaborated in the nineteenth century" (Alexander Rosenberg, "If Economics Isn't Science, What Is It?" reprinted in D. Hausman (ed.), The Philosophy of Economics: An Anthology, 2nd ed. (Cambridge: Cambridge University Press, 1994), p. 377. Cited hereafter in the text by page number only as Rosenberg II. See also, Wassily Leontief, "Input-Output Economics," Scientific American 185 (1951), pp. 15-21.) This last point bears elaboration.
Like Newtonian mechanics and Darwinian evolution, microeconomics pursues what philosophers of science call an "extremal strategy" of explanation. Such an approach views the phenomena to be explained "as reflecting forces which always move towards stable equilibria that maximize or minimize some theoretically crucial variable. In the case of microeconomics this crucial variable is utility (or its latter day surrogates). . ." (Rosenberg II, p. 378). Such a strategy entails that the theory be preserved in the face of any putatively falsifying data by revising the auxiliary hypotheses that inform any empirical test of the theory. This, of course, permits economic theory to persist in the face of a dismal record of empirical failure. But if Newtonian mechanics or Darwinian evolution is none the worse for pursuing such a strategy, why should we worry about economics? Because, as Alexander Rosenberg notes, economics can not,
“boast even a small part of the startling successes that other extremal research programs have achieved. . .[T]wo hundred years of work in the same direction have produced nothing comparable to the physicists' discovery of new planets, or of new technologies by which to control the mechanical phenomena that Newton's laws systemized. Economists have attained no independently substantiated insight into their domain to rival the biologists' understanding of macroevolution and its underlying mechanism of adaptation and heredity. There has been no signal success of economic theory akin to these advances of extremal theory.” (Rosenberg II, 380)
(Even Posner concedes that while "economic theory can take credit for some new trading strategies in securities markets, some new methods of pricing, and some new public policies, such as the deregulation of transportation and banking--these interventions are less dramatic, and more ambiguous in their results and interpretation, than the interventions of natural science in such areas as weaponry and medicine" (PJ, 365).)
In other words, economics is a failed extremal research program, one whose own resistance to falsification belies the empiricist and Popperian rhetoric of which economists are so enamored.
Of course, economists have generated an extensive literature of apologetics to account for the fact that their discipline has met with so little empirical success. Two typical responses bear consideration here. First, and most simply, is the frequent assertion that economics has met with predictive success. Thus, Posner writes:
“Here is a random sample of economic predictions that have empirical support: a price ceiling will cause queues, black markets, and quality problems; deregulation results in lower prices and more product variety; communist economies are less productive than capitalist;. . .dirty or dangerous jobs pay more (ceteris paribus) than clean or safe ones;. . .an increase in the severity of punishment will (ceteris paribus) reduce the amount of crime. . .I could go on for hours.” (This is from a letter to Leiter, July 22, 1996)
Even a sharp critic of economics' pretension to scientific status like Alexander Rosenberg concedes that "for all its infirmities, economic theory does at least sometimes seem to be insightful. Occasionally, [its] qualitative predictions are borne out, and even more frequently, retrospective economic explanations of events that were unexpected. . .can be given" (Rosenberg II, 384).
Even if we were to concede these predictive/empirical successes to economics, the force of the preceding argument would not be vitiated. The crux of this argument has not been that economics generates no successful predictions, but only that (a) the quality of its predictions (their precision and reliability), and (b) the growth of its predictive power over time, are not of scientific quality. They do not live up to the standards that economists themselves claim for them. Generating true generic predictions is not the hallmark of science. All of us, drawing on common-sense psychological assumptions, do that all the time. Genuinely scientific theories must anticipate the future with a degree of precision and consistency greater than that realized by common-sense.
I predict, for example, that a movie which receives a rave review in Friday's New York Times will produce queues at the New York City movie theaters on Friday and Saturday nights--ceteris paribus, of course (e.g., as long as there is no strike that Friday by the newspaper delivery drivers). I predict that ignoring the curve and giving A's to all my students will increase enrollment in my courses. I predict that covering a class for an absent colleague will make it more likely that that colleague will give me detailed comments on a manuscript I've given him to read. All of this is the stuff of common-sense, but no one would think of characterizing the common-sense psychology that undergirds such predictions as the core of a scientific research program. The question is: does economics really do any better, in predictive precision and reliability?
The sort of mundane predictions Posner proffers hardly give one confidence in an affirmative answer. That price ceilings will generate queues, for example, seems a simple enough conclusion to draw from a set of plausible psychological assumptions. Unable to charge the real price that the market will bear, merchants and producers (selfishly seeking the highest price) will withhold goods from the marketplace, thus producing lines for the limited stock actually made available, in order to divert some of their product to the black market where it can command a higher price. But what is the precise relationship between price ceilings and queues? What (quantifiable) changes in ceilings will produce what (quantifiable) changes in lines? What antecedent conditions must obtain for price ceilings to produce lines? What additional penalties or incentives will block the queuing effect? Economics simply has no answers to these questions.
The banality of economic "predictions" is especially vivid in Posner's claim that "an increase in the severity of punishment will (ceteris paribus) reduce the amount of crime." But surely we don't need economics--or any putative social science--to draw that conclusion! (One might worry here, however, that the ceteris paribus clause will swallow the law. Crime, for example, often seems more strongly correlated with economic conditions (e.g. recessions), than with severity of punishment.) As to the precise correlation between severity of punishment and crime reduction, or the causally relevant parameters of the ceteris paribus condition, economics is largely silent. As one commentator on Gary Becker's recent work puts it, economics "abounds in pronouncements of such transparent banality that they would seem to spring more from common sense or ordinary introspection than from sophisticated science" (David Throsby in the TLS, Jan. 24, 1997, p. 31).
In fact, most theoretically self-conscious defenders of economics concede that economics does no better than "generic" predictions (e.g., Gibbard & Varian, “Economic Models,” Journal of Philosophy 75 (1978: 664-677)--that is, "predictions of the existence of a phenomenon, process, or entity, as opposed to specific predictions about its detailed character" (Rosenberg I, 69). In this sense, economics is largely indistinguishable from the predictions generated all the time by the (admittedly non-scientific) applications of common-sense psychology that are a feature of ordinary coping in daily life. But, the economist might point out, generic predictions are also a feature of parts of evolutionary theory and even thermodynamics. (Yet most scientists share the view that, as the Nobel laureate in physics Steven Weinberg puts it, "what a successful scientific explanation would have to accomplish. . .[is] the quantitative understanding of phenomena." Dreams of a Final Theory (New York: Vintage, 1992), p. 7. "[T]he capacity for quantitative prediction" is so important to science, that Weinberg says in teaching undergraduates, he views it as his "most important task. . .to give the students a taste of the power of being able to calculate in detail what happens under various circumstances in various physical systems." Id. at 7, 8.)
Once again, however, Rosenberg identifies an important difference:
“[I]n other disciplines, generic theories have been either supplemented or improved in order to make specific predictions. Thus, if we add theories about heredity, physiology, development, behavior, and environment to evolution's mechanism of variation and natural selection, we can hope to increase the specificity of generic predictions. In thermodynamics, if we provide a measure of entropy and a description of the mechanical and thermal properties of a system, we can make specific predictions about the amount of entropy increase it will manifest.” (Rosenberg I, 70)
The difficulty for putative economic "laws" and predictions is, as Rosenberg puts it, that,
“we cannot sharpen their applicability beyond the most qualitative or generic levels, or quantify the values of their parameters like elasticity, or improve our foresight or hindsight in the employment of these principles. Now the fact that we can usefully employ false or vacuous general statements, up to certain limits, is no mystery in the philosophy of science at all. The clearest instance of such restrictedly useful though false or vacuous general statements is Euclidean geometry. . ..[I]nterpreted as a theory of actual spatial relations, Euclidean geometry is false, and interpreted as a body of a priori truths implicitly defining the terms that figure in it, Euclidean geometry is vacuous. More important. . ., it was shown to be useless and inapplicable as a body of conventions, beyond certain values of distance and mass in space. ...” (Rosenberg II, 386)
So the fact that some generic economic predictions work is hardly reason to give us confidence in the cognitive content of economic theory, for unlike real sciences, economics does not seem to be able to move beyond the purely qualitative level in its predictions.
Rosenberg's comments do suggest, however, a second line of defense for economics. The demand for quantitative precision is really, the economist might say, a demand that all the ceteris paribus clauses be purged from economic laws. But perhaps economic laws simply contain irremediably vague ceteris paribus clauses. This would not preclude their being genuine laws, assuming certain other conditions are satisfied. So the "law of demand"--that "a rise in the relative price of a product will, other things held constant, cause a reduction in the quantity of the product demanded" (PJ, 363)--can be a genuine law, even though we can never specify all the causally relevant parameters picked out by the "other things held constant" clause. As a result the predictions generated by this law will be irremediably generic.
Now, in fairness to economics, it should be noted that all experimentally confirmed laws of physics and chemistry involve ceteris paribus clauses, often in the form of ad hoc "phenomenological" factors. It is only in the rarefied atmosphere of pure theoretical physics that one encounters universal, exceptionless laws. That economic laws include ceteris paribus clauses is not then, per se, worrisome.
What is worrisome, however, is that in economics "ceteris paribus" does not serve as a placeholder for, e.g., phenomenological factors that simply do not admit of quantification. Rather, it serves primarily as an excuse for predictive weakness. The details on what constitute "normal conditions" and the like (i.e. the cetera) never seem to be forthcoming. Scientific laws, to repeat, need not be "strict" in the Davidsonian sense of specifying with precision all the parameters of the boundary conditions that fall under the "ceteris paribus" clauses. But over time genuine scientific research programs are distinguished by their ability to at least approximate or approach strictness, even if they never realize it. The "progress" of economics over the last century gives little reason for thinking it is moving in this direction. Even with the "law" of demand, for example, a price increase can actually trigger an increase in demand since "consumers often take prices as an index of quality and often are warranted in doing so" (PJ, 364). But this, of course, means--as Posner recognizes--that "it is distressingly easy to explain away empirical findings that appear to conflict with the basic theoretical assumptions and propositions of economics" (PJ, 364). (Another quite astonishing example of this problem is the theory of rational choice, on which modern economics rests. According to this theory, the preferences of agents are consistent and (usually) transitive. Yet the phenomenon of "preference reversal" has been well-established by empirical psychologists, thus undermining the core of rational choice theory. See Hausman, The Inexact and Separate Science of Economics, pp. 227-241.) Add to this problem the purely generic character of the predictions generated in the first place and it becomes sorely tempting to look for a very different explanation than high cognitive content for why the "science" of economics has exerted such a profound influence on social policy in recent decades. Perhaps the ascendancy of economics as a force in public policy has much more to do with its ability to rationalize policies that tangibly benefit ruling groups in American society than with its empirical and cognitive credentials.
Defenders of economics are fond of saying, as Posner does, that while "economics is weak in comparison with the natural sciences. . .it is the strongest of the human sciences" (PJ, 366). Yet while economics is certainly the most pretentious and formalized of the human sciences, it clearly has none of the successes of, say, empirical cognitive psychology over the past quarter-century. (See, e.g., the three-volume series edited by Daniel Osherson: An Invitation to Cognitive Science, 2nd ed. (Cambridge, Mass.: MIT Press, 1995) (with volumes on "Language," "Visual Cognition," and "Thinking"). The second edition contains important empirical case studies.) And even calling economics the most predictively successful of the human sciences may be to damn economics with faint praise. Perhaps the real question to ask is why economics has performed so poorly. Daniel Hausman, in an otherwise sympathetic philosophical account of economic methodology, concludes with the following observation, which bears quoting at length:
“[T]he 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 progress. Since economics has not been very successful and has not made much empirical progress, economists should be exploring alternatives. . ..[U]nless equilibrium theory [the core of what makes economics a distinct science according to Hausman] has captured the major causes of economic phenomena, the separate science of economics can never be successful. If, as seems likely to me, there are systematic failings of human rationality, and economic behavior is significantly influenced by many motive forces, apart from consumerism and diminishing marginal rates of substitution, then equilibrium theory is not a very good theory, whether or not there is anything better. . ..”
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Addendum (July 16, 2004): It does seem to me in retrospect that too much is made to turn in this analysis on whether economics is a “science”; I was prompted originally to write on the topic after hearing lawyer/economist colleagues state, in all seriousness, that they viewed economics as on a par with physics, not quite as successful yet, of course, but still…. Making clear why this was utterly silly seemed worthwhile. But having done that, it would be a mistake to conclude that we should not try to bring scientific techniques, methods, and styles of explanation to bear on unruly human phenomena. Qualitative and generic predictions can be worth quite a lot, especially if it’s all we have! And holding our theorizing about human affairs to epistemically robust standards like those we see exemplified in the hard sciences seems good for intellectual hygiene, even if the results are never going to be as powerful. How well, of course, economics fares by even these more relaxed criteria is an open question; as Hausman and Rosenberg document, the record is mixed. (And, conversely, the record of much maligned explanatory paradigms, like Freud’s, are actually rather good—but more on that on another day.)