Economics in general, and agricultural economics in particular, have come to rely heavily on an assortment of fancy analytical tools. Once rarely employed, quantitative methods are now clearly in the mainstream of economic thought and practice. But can this imply that we are up the creek with an ornate paddle?
Aware of the trend as early as 1963, George Stigler commented, "Less than a century ago a treatise on economics began with a sentence such as 'Economics is a study of mankind in the ordinary business of life.' Today it will often begin, 'This unavoidably lengthy treatise is devoted to an examination of an economy in which the second derivatives of the utility function possess a finite number of discontinuities. . . .Only elementary mathematical tools such as topology will be employed, incessantly."
To illuminate the trend, I surveyed articles published in U.S. agricultural economics journals during 1950, 1966, and 1983, tabulating the primary tools of analysis used by the authors (see table 1). Contrast the yearly totals for articles using only the English language (15, 8, and 2) with those using programming and simulation models (zero, 7, and 18), and the trend seems clear. Moreover, within each category of tools, the level of sophistication has increased; for example, dynamic and recursive programming occurred frequently in 1983, while linear programming dominated in 1966.
Currents and eddies can be found within table 1. There is some hint that the use of regression analysis has peaked, while enthusiasm for large-scale simulation modeling still may be on the rise, as exemplified by the Economic Research Service's recent development of a large-scale, food and agricultural policy simulator. Again, in 1950, Agricultural Economics Research allotted considerable space to survey research, but other publications showed little interest in the topic. Donald McCloskey argues that economists generally have a strong aversion to survey research, and that they tend to accept only the externally observable behavior of economic actors while rejecting the results of questionnaires and other self-descriptions. Consequently, an important source of information remains untapped.
Dollars and sense
Is it possible to evaluate this increased emphasis on the econometric and mathematical? From a market perspective, it might appear to be an eminently successful approach. Indeed, practitioners of the technical and econometric crafts probably achieve better than average returns in their professional careers. As McCloskey points out, Paul Samuelson's skill at mathematics is itself an important and persuasive argument for his being accepted as an authority, even if his use of mathematics often is pointless. But, as McCloskey concludes, such virtuosity is itself some evidence of virtue. More generally, the increasing use of mathematical techniques suggests that a growing demand for such tools has evoked a supply response on the part of those who are adept at reading the market. Nevertheless, widespread disenchantment with the market's results exists. Is this because of market shortfalls or failures, or unmet extramarket goals?
Critiques and rejoinders
Several overlapping complaints appear in the "literature of disenchantment." Critics point out that the tool-oriented work:
- Is hard to read and difficult to understand
- Is not oriented to industry and policy issues
- Is overspecialized
- Does not exhibit enough concern about data
- Involves questionable practice, particularly in regression analysis
- Is not problem-oriented, to the point of posing trivial or even nonexistent problems
On assuming the editorship of the American Journal of Agricultural Economics in 1978, V. James Rhodes—noting criticism under the first three categories of complaint—responded, "Members of the profession... must be prepared to make some investment in understanding what has become a very diverse subject matter... We will publish more papers on policy and on results of applied research if we receive quality pieces. The unfortunate fact is that we receive very few papers—of any quality—in those areas."
Table 1. Enumeration of Primary Tools Used in Articles Appearing in Agricultural Economics Journals, 1950, 1966, and 1983
An investment in understanding seems a diplomatic way of pointing out a technological lag on the part of some readers. Here, it seems worthwhile to recount Clark Edwards's observation that, in the early days of linear programming, the modelers of farm-management problems took comfort in finding that their computer printout was consistent with the solutions obtained by traditional farm-management specialists. That sort of consistency remains a virtue for latter-day modelers, as well.
Specialization has been defended by Stigler, who notes that it is desirable and inevitable, as befits one of the central insights of economics. He adds that Adam Smith taught jurisprudence, politics, rhetoric, and belles-lettres, illustrating that the division of labor is limited by the extent of the market. Nevertheless, specialization does bring increased frictions (costs) of communicating with outsiders, and Theodore W. Schultz—confronting the dilemma of specialization—cites Hayek's observation that "an economist who is only an economist is likely to become a nuisance if not a positive danger." Schultz argues that although the economist's job is to develop economic logic, quantitative tools, and empirical analysis, he or she also needs the insights of the humanities and history. A dictionary definition of a dilemma is a choice between two mutually unsatisfactory alternatives, a real-life situation perhaps not too well recognized in the economist's calculus of choice. Here Schultz may be hinting at a market choice (that is, specialization) versus a more socially useful choice (that is, the understanding of other intellectual realms). In practice, that choice involves the optimal levels of alternative investments of the economist's human capital, a tradeoff that each of us has to make in our own way.
Numerous observers—including Wassily Leontief and Andrew Kamarclv—contend that economists apply their tools without proper regard for the underlying data that the tools employ. James Bonnen stresses the importance of being careful about one's numbers, citing many instances of bad practice in the field; for example, some economists no longer look at secondary data, but get them on magnetic tape and let the computer do the looking. Considering our subdiscipline, Bonnen concludes, "Agricultural economists have a tradition of inquiry that prevents innocence of the empirical. Even we, however, are increasingly failing in individual and institutional research to do the hard, unglamorous slogging in data collection that often is most productive of new knowledge."
Regression analysis is one of our major tools, but the way it has been applied has drawn much critical fire. Edward Leamer sees the current situation as one in which "hardly anyone takes anyone else's data analyses seriously." This results from the common practice of fitting many models and then selecting the one that seems best. Luther Tweeten warns that this practice reverses the usual scientific method by using statistical techniques to determine the hypothesis. Disregarding the textbook admonition to specify one's model beforehand and then to accept the results—however they turn out—the regression analysis uses trial and error to choose from among many variables the "best" subset, based on such criteria as highest R2, "reasonable" coefficient signs, and "best" significance levels. The unpleasant consequence of this approach is that standard errors, t ratios, and other test statistics no longer are strictly applicable. Yet, even its critics see reason for "specification search." How we "know" what we know is the crux of the matter, for we must necessarily draw heavily upon outside information in carrying out our work and in reaching our conclusions. In response to the mistrust of published results, Leamer and Rod Ziemer recommend presenting additional information on the range of all the results in a particular application, to reveal how robust (or invariant) they are. And McCloskey suggests that such mistrust is unwarranted. Our colleagues can be expected to be bound by professional ethics; further, attempts to impose overly rigid standards of scientific purity lead to self-deception on how we know what we know.
Finally, consider the complaint that sophisticated tools often are used for trivial or nonexistent problems. Earl Swanson restates the complaint in less pejorative fashion by characterizing one of the main analytic paths in research as involving no immediate interest in delivering useful results to public or private decision makers. This path is chosen by those who find an emphasis on methodology to be attractive and comfortable. It is also often chosen by the novice in research; skills in problem selection, which are not so easily taught, can be expected to be part of the natural development of the student.
Swanson's discussion is helpful, but I think additional issues are bound up in the complaint. Of particular relevance in addressing those issues is Emery Castle's observation that work in agricultural economics involves both autonomous and popular functions—that is, scholarship and various forms of public service. The tension between these functions well may involve the relationship between our research agenda and its sponsorship, manifested by our choice of problems to study. That relationship deserves some in-depth scrutiny, to which I now turn.
Sponsors and problems
It seems more than an interesting coincidence that both Willard Cochrane and Theodore W. Schultz charge that we do not pay enough attention to important problems, although I see Cochrane as emphasizing the popular and Schultz the autonomous functions of our work. Cochrane contends that the university's emphasis on research methodology and discipline-oriented research occurs through the neglect of work on important problems. Schultz argues that academic economists tend to avoid important problems by concentrating instead on the needs of their sponsors. Of course, each sees different areas of neglect. Cochrane is interested in how government agencies—particularly the Economic Research Service—can attend to mission-oriented, pressing problems of current concern, and is afraid that academic economists will furnish only limited help on these problems. Schultz feels that the key function of academic economics is comprehensive analysis and criticism of institutions and policy, but that heavy reliance on government support has led to a distorted emphasis on short-range, politicized research.
Could they both be right? This would imply a deliberate turning away from short-term, "hot" policy issues (Cochrane) and long-term, fundamental policy issues (Schultz), and presumably would account for our focus on tool-building and application. To turn the Bard upside down, are there incentives for "less matter, more art?"
Advice and dissent
Two speculative answers to that question should be considered. First, in a time of reduced opportunities for academic tenure and promotion, scholars may become more timid in dealing with controversy. Yet I doubt that there currently is a greater dearth of courage than that which usually prevails. Even if one discounts the straight talk emanating from such illuminati as Bonnen (for example, his devastating 1983 critique of federal statistical policy), Cochrane, and Schultz, many recent examples of the conscientious and courageous dissemination of "dangerous" knowledge can be found. For example, Robert Boynton, Brian Blake, and Joe Uhl, who studied the effects of publicizing differences in retail food prices, published their results despite trade opposition; the U.S. Department of the Interior's Robert Nelson was remarkably candid in assessing coal-leasing policy; and some agricultural economists had the temerity to publish objective appraisal of major water-development projects even though their results were displeasing to their local establishment.
The second speculation is based on the perception that society does not show great interest in much of our policy advice. What we say on macroeconomic policy (on which we know little) receives much more attention than what we say on microeconomic policy (on which we know a considerable amount). Stigler argues that "society" (viewed as a collection of interest groups) is not stupid; it merely accepts those recommendations that serve the interest of a particular dominant group. Under these conditions, tool-building and application are likely to become more attractive to the practicing economist, assuming that society is willing to support that activity. According to Stigler, society is willing to pay that cost under the presumption that the activity will lead to more convincing advocacy in the long run. Put less harshly, much tool-building and application have occurred in response to legislative mandate, as in the implementation of environmental regulation.
The business of economics and economics as business
In any event, Stigler does distinguish between the economist's teaching and advocacy functions. In earlier work, he defined the good teacher's task as that of instilling the conscience of the scholar, who engages in "knightly conduct in the pursuit of knowledge." The value conflict here leads to the realizations that economists usually include some non-market goals in their objective functions, and that precise allocation among alternatives is not always easy. As an economic actor, the agricultural economist must necessarily value meeting the research needs of his or her sponsors, including the general agricultural sector, as well as government agencies supportive of that sector. But as an academic scholar the economist must value the search for the truth, wherever it leads and whatever trouble its pursuit causes. In principle, both values seem unassailable, but in practice, nasty choices do become necessary. For example, how far can one go in setting one's research agenda?
Choosing between the two basic values when they conflict is a perpetual—even eternal—problem. That problem of choice may be especially pressing in times of financial stringency, which bring much soul searching over what we have been doing wrong. The concern with which we trod is documented by the observation that at least nineteen books on economic methodology have been published since 1975. Among the finger pointers at what has gone wrong, McCloskey demolishes methodological purism; Nelson uses his study of coal-leasing policy to question the underlying ideologies that economists as policy makers have drawn upon in attempting to formulate and implement policy; and Cooter and Rappoport suggest that the ordinalists of the 1930s may have led economists astray in thinking about welfare economics. I recommend those authors' publications as mind-stretchers. Indeed, their doubts and insights give us a fresh look at the world, and at ourselves as well.
Author Irving Hoch is a senior fellow in RFF's Renewable Resources Division. This article—based on a paper presented at the 1984 Annual Meeting of the American Agricultural Economics Association in connection with others delivered by Earl R. Swanson and Paul W. Barkley—originally appeared in the December 1984 issue of the American Journal of Agricultural Economics vol. 66, pp. 793-797. It is reprinted here with permission of the American Agricultural Economics Association.
A version of this article appeared in print in the May 1985 issue of Resources magazine.
