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Emergence of Experimental Economics

The survey begins, in Part 1, with a presentation of the historical emergence of the subject and provides the methodological justification for economics experiments. In presenting the history of the field, Part I also discusses the forces that impelled or impeded its evolution.


1 Emergence of Experimental Economics

The survey begins, in Part 1, with a presentation of the historical emergence of the subject and provides the methodological justification for economics experiments. In presenting the history of the field, Part I also discusses the forces that impelled or impeded its evolution.

Economic & Political Weekly

August 27, 2011 vol xlvi no 35

1.1 Economics as an Experimental Science

hy was the experimental tradition so late to emerge in economics? Friedman and Sunder (1994) argued that a discipline became experimental when innovators developed techniques for conducting relevant experiments. Does the introduction of experiments to economics depend on anything more than this technological explanation? Do they have to do with the development of the discipline itself? To answer these questions, we have to sketch the history of its development as well as appreciate the forces that impelled or impeded the evolution of scientific thought.

Paul Samuelson, Milton Friedman and Friedrich Hayek declared long ago that economics as a discipline was not amenable to the experimental method, just as Aristotle thought physics to be nonexperimental. Only with 20-20 hindsight do such judgments seem surprising. To understand their basis is to understand the very nature of scientific experiments and their contributions to science. The essence of scientific experiments is control over the environment in which phenomena of interest take place. Of course, by control we mean true manipulative control, not the mere “quasi-control” sought in analyses of data gathered about naturally occurring phenomena. Whether a discipline is judged to be amenable to useful experimentation depends on whether the variables that are believed to be critical to the relevant phenomena are amenable to experimental control. The identity of these variables depends on the state of the extant theory. The state of extant theory, in turn, depends on the available evidence, experimental as well as non-experimental. If the variables that are crucial to the extant theory of a discipline are currently judged to be beyond experimental control, it seems reasonable to conclude, for the time being at least, that such a discipline is not experimental.

The state of extant theory defines what the discipline is at any given point of time. Received theories change over time. Paradigms shift when a complicated set of explanations based on many variables are replaced by a simple explanation based on fewer variables. Some variables that were believed to be “crucial” in the old paradigm may be absent from the new. If the lack of controllability of such variables held up the discipline from being “experimental” in the old paradigm, the discipline may become “experimental” in the new paradigm. The double helix model of DNA and the plate tectonic theory in geology are recent examples of previously non-experimental disciplines becoming amenable to certain types of experiments because of shifts in paradigms and the accompanying simplification of theory.

The amenability of a discipline to experiments is not inherent in it; it depends on the current state of its theory. When Aristotle wrote about physics not being subject to experiments, he may have


meant that this was so with reference to the theories of physical phenomena prevalent in his time, or their subset that was acceptable to him. Perhaps a similar interpretation would be appropriate for the judgments passed down by so many leading economists about economics not being an experimental science. However, if change in theory is a precondition for the conversion of a discipline from non-experimental to experimental, how could this occur in economics, where no obvious paradigm shift is known to have occurred in recent decades? How does one reconcile the judgments of eminent economists such as Samuelson, Hayek and Friedman with the increasing acceptance and use of experiments in economics in recent years? Why did so many economists believe their discipline to be non-experimental in the first place?

The scale of macroeconomic phenomena precludes most kinds of controlled experimenta tion. By the same criterion, astronomy might also be regarded as a non-experimental science. Due to their inability to manipulate planets, stars or galaxies, astronomers had to devise ingenious, sometimes spectacular, quasiexperiments on naturally occurring phenomena to adduce convincing evidence to reject contending theories (for instance, an experiment during the 1914 solar eclipse verified Albert Einstein’s prediction about the curvature of space in the neighbourhood of heavy celestial objects). It would be politically and ethically difficult, if not impossible, to conduct macroeco nomic experiments that manipulate monetary and fiscal policies to gather observations to verify or reject various macroeconomic theories. To this extent, the non-experimental tag assigned to economics seems justified. But these arguments do not apply to price theory or microeconomics, just as the arguments about astronomy are inapplicable to the physics and chemistry of most terrestrial phenomena.

In his introduction to Price Theory, Friedman wrote, Economic theory, like all theory, may be thought of in two ways. It may be thought of as a language or filing system, or it may be thought of as a set of substantive empirical propositions. With respect to theory in the first meaning, the relevant question to be asked is usefulness and not rightness or wrongness. The proposition that price is determined by the interaction of demand and supply forces is merely an attempt to set up a useful filing system within which there can easily be placed under the headings “demand” or “supply” any one of the forces affecting price. The usefulness of this filing system will in turn depend on the substantive fact whether a listing of the forces operating on demand contains few elements in common with the listing of the forces operating on supply. Economic theory as a list of substantive empirical propositions contains proposi tions which are, in principle, capable of being tested because they attempt to be predictive. The definition of a demand curve is theory as language. However, the statement that the demand curve slopes downward to the right is theory as a substantive empirical proposition. It has empirically observable consequences, whereas the definition of a demand curve does not. Theory as language coincides with Marshall’s engine of analysis. His objective, as well as that of any other investigator, is to construct a language that will yield as many substantive propositions as possible (1962: 8).

The experimental method has proved to be a powerful engine for generating substantive empirical propositions, and for distinguishing between competing propositions for prediction of the same phenomena – precisely the function Friedman attributed to a large part of economic theory.

We conjecture that the reasons for the residual distrust of experimental methods among economists are some of the same reasons that have given economics, among all social sciences, an extraordinary degree of coherence and power – its willingness to abstract from reality and its ability to use the mathematical technique of optimisation as a fundamental organising principle. Abstraction from reality is necessary for assumptions such as atomistic competition among fully informed agents, who are assumed to optimise for the market to arrive at an equilibrium. However, such abstraction and optimisation are devices of convenience to be used to build and solve simple models that can be tested for their predictive ability; they are not to be taken seriously in themselves. Absent experiments, and given the limitations of quasi-experiments that depend on naturally observable phenomena alone, abstract assumptions and optimisation came to be taken far too seriously by economists themselves. Since we know that no laboratory market could possibly meet all abstract assumptions and real human beings do not have the ability to optimise complex problems by intuition alone, it is easy to reject the potential of experiments to contribute to economic theory. This is why the results of Smith’s experiments, conducted in the late 1950s with a mere handful of students, came as a surprise not only to economists at large, but also to Smith himself who was trained as an economist and continued to regard his experiments as an avocation until well into the mid-1970s (Smith 1991).

New Macroeconomic Theory

About the same time experimental techniques made inroads into price theory, game theory and industrial organisation theory, microeconom ic theory began to be used to build a new macroeconomic theory. Experimental techniques have followed microeconomics into the new macroeconomics to identify substantive empirical propositions about expectation formation, monetary policy and inflation. Years ago, physics, with its sound experimental foundations, had made inroads into astronomy in the form of astrophysics. Reinhard Selten suggested a different explanation for the mid-20th century spurt of interest in experimental economics. The appearance of von Neumann’s and Morgenstern’s The Theory of Games and Economic Behaviour (1944), oligopoly theory, and cooperative game theory offered a multitude of solution concepts that could not be resolved by application of a priori reasoning alone. So those who had contacts with experimental psychology turned to experimental methods for selecting solution concepts. This explanation pointed to what is, perhaps, a unique role economics experiments can play – a role in selecting from multiple equilibria. It is consistent with the recent interest of theorists in experiments with overlapping generations of economies with multiple equilibria.

Herbert A Simon presented a slightly different perspective,

I believe that the 1952 Santa Monica conference came out of the general stir about the whole range of things that was then put under the label of cybernetics. RAND was at the centre of that stir, and just about everyone involved had close connections with the RAND group and/or the Cowles Commission. This was a response not only to von Neumann and Morgenstern (which itself was a response to these developments), but to the whole post-war interest in the application of mathematics to human affairs – which encompassed computers, servomechanism theory, information theory, mathematical economics, mathematical learning

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theory, game theory, brain architecture, robots and operations research (I am sure I have omitted some items). To the extent that some of the people interested in these matters had backgrounds in various areas of empirical science, they brought empirical techniques, including experimentation, into the picture (Qtd in Smith 1991: 21-22).

1.2 Pre-1952: Games and Decisions

In 1952, a proposal from the University of Michigan, and the support of Ford Foundation, Office of Naval Research and RAND Corporation, resulted in a conference in Santa Monica in which mathematicians, psychologists, game theorists and economists participated.1 The proceedings of this conference had a major influence, both on the participants’ work as well as that of many others through the papers published in a volume edited by Thrall, Coombs and Davis (1954). While the integrating theme of the conference was the use of mathematics in social science, five of its 19 papers and a good part of the discussion at the conference had to do with the reporting and interpretation of the results of experiments. Individuals who participated in this conference included those who subsequently had a major influence on the development of experimental economics and game theory – Jacob Marschak, Roy Radner, Herbert Simon and Sidney Siegel. Simon (1955, 1956) used these results to develop the contrast between his concepts of substantive and procedural rationality – what is rational to the experimenter, given all that he or she knows, may be quite different from what is rational to the subject in an experiment, given his or her typically incomplete knowledge of the environment in which he or she is expected to act.

One of the controversies at this conference was the interpretation of psychologist William K Estes’ results of his Bernoulli choice experiments. While the observed results of these experiments were consistent with the asymptotic learning equilibrium (the relative frequency with which each state is predicted converges to the true probability of the respective states), game theorists found such behaviour quite irrational because the expected reward could be maximised by always predicting the state that had the higher probability. Subjects’ pay-offs in Estes’ experiments were not salient; they were asked to “do your best to make a correct prediction”.

1.3 Siegel and Shubik

Siegel, a Stanford psychologist, took Estes’ results, and Simon’s distinction between substantive and procedural rationality and designed careful experiments to show that when subjects did not maximise the pay-off, it was only because such maximisation was not in their best interests. He postulated that since the boredom of repeated, almost mindless, responses caused subjects in Bernoulli learning experiments to deviate, the amount of this deviation could be controlled by manipulating the monetary rewards and punishments associated with the prediction task, and by introducing cognitive and kinesthetic variability in the task. Siegel (1959) presented compelling evidence to support this hypothesis. Experiments by Siegel and Fouraker (1960) and Fouraker and Siegel (1963) documented the dramatic effects of changing the salient pay-offs on bargaining behaviour. The experimental economics tradition today incorporates three of Siegel’s legacies – an insistence

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on careful instructions, an inclusion of instructions in research reports, and the payment of salient monetary rewards to subjects.2

Although he was not a participant in the 1952 conference, Martin Shubik worked in the company of Princeton and RAND mathematicians, and has promoted “gaming” and experimentation since the 1950s to this day (in his work with Juergen Huber and Shyam Sunder). His planned collaboration on an ambitious research programme with Fouraker and Siegel was interrupted by the latter’s untimely death in 1961. Shubik was also interested in free-form “gaming”, including role-playing business-simulation games developed jointly with Richard Bellman (later famous for his theoretical work in dynamic programming) and others. Shubik envisioned a large-scale computerised laboratory for conducting experiments and for gaming, an idea that Austin Hoggatt first brought to reality at the University of California in Berkeley in the 1960s. (Sunder recalls Hoggatt proudly showing him, a faculty recruit, around the lab during his visit to Berkeley in early 1973. Daniel Friedman also met Hoggatt, about 10 years later.) Shubik served as James Friedman’s thesis advisor and kindled his interest in game theory and laboratory oligopoly experiments. Friedman (1967) and Friedman and Hoggatt (1980) are examples of 1960s experimental economics at its best. They patiently pursued the implications of the game theory available at that time. But the experiments of the 1970s followed a different path. The importance of these early game theory experiments became apparent only with the resurgence of game theory in the 1980s.

Shubik’s interest in gaming led him early to design playable games to illustrate interesting results in game theory, even to peddle them to commercial enterprises. The dollar auction,3 a popular classroom exercise to illustrate the phenomenon of escalation of addiction, was conceived by him in the 1950s. Fouraker, Shubik and Siegel (1961) joined hands to conduct experiments on duopoly and tripoly, and had planned a substantial research agenda together when Siegel died. Through his wide-ranging interests in both game theory and economics, Shubik worked with, and influenced, many scholars, including Bellman, John Kennedy, David Stern, George Feeney, Hoggatt, James Friedman, Ted Tarson, Tappen Roy, Richard Levitan, Gerritt Wolf and H Eisenberg.

1.4 Classroom Markets of Chamberlin and Smith

Chamberlin (1948) was the first to design and conduct open outcry markets in his classes. He examined observed prices and volume in relation to market demand and supply as well as with respect to instantaneous supply and demand defined in several different ways. He pointed out that his market procedures did not permit recontracting and concluded that they did not exhibit a tendency towards the theoretical predictions of equilibrium suggested by Alfred Marshall. Chamberlin used these results to motivate the introduction of monopolistic competition to the theory as a replacement for the theory of perfect competition.

In these auctions, each individual was assigned the role of a buyer or a seller, given a reservation value, and was free to circulate in the room to find a party to negotiate with. Completed transactions were recorded on the board in the sequence they were completed and reported to the desk. In the absence of a centralised order flow that characterises a double auction, an open outcry


auction exhibited considerably greater noise in transaction prices during the first trial (Dalton and Sunder 1992). However, after a few trials, prices and efficiency in this auction converged close to the neighbourhood of equilibrium predictions. Chamberlin’s experiments never revealed this convergence because there was no repetition of trials. In any case, his aim had been only to establish that the observed data did not correspond exactly to the predictions of competitive theory as a verifiable empirical proposition. Unfortunately, experiments were so radically different from any other method in which economists were trained at the time that most graduate students who participated as subjects in Chamberlin’s experiments tended to reject them without serious consideration. This rejection may have been facilitated by their demonstrative nature, and Chamberlin’s use of the results to promote his own theory of monopolistic competition.

Among Chamberlin’s subjects at Harvard was Smith, a graduate student, who also gave little deliberate thought to these experiments at the time. A few years later, however, he concluded that subjecting propositions derived from economic theory to experimental tests was a sound idea. But in conducting his own experiments he modified Chamberlin’s procedures in two important ways to give the competitive model its best shot. This modified procedure, in its basic form, has come to be known as a “double auction”. First, all bids and offers were made known to all traders immediately because a full knowledge of all bids and offers captured the idea of perfect competition better than the localised knowledge of bids and offers in spontaneous ly generated multiple bargaining sessions in Chamberlin’s markets. This centralisation of bids and offers was also closer to the forms in which many stock exchanges were organised.4 Second, instead of expecting a competitive equilibrium to be attained instantaneously at all times, Smith relied on the Marshallian hypothesis that markets tend to approach equilibrium over time when supply and demand remain stationary. He therefore specified the individual (and market) supply and demand functions in units per trading session, and replenished the endowments of traders at the beginning of each of the many consecutive periods. In later years, Smith added two more features to his experiments – a bid/ask improvement rule, which meant that every new bid (ask) must be higher (lower) than the highest (lowest) standing bid (ask); and subjects were to be paid a non-trivial amount of compensation, usually in cash, which increased the profit earned by each in the experiment. With these changes, Smith found that the markets converged close to the neighbourhood of equilibrium in a variety of environments.

1.5 Selten, Sauermann and Tietz

The German movement in experimental economics started with Selten, who is known in game theory for his path-breaking refinements to the Nash equilibrium. He was influenced not only by gestalt psychologist Edwin Rausch at Frankfurt but also by two US publications. Thrall et al’s 1954 work on the Santa Monica conference papers (especially the Kalish, Milnor, Nash and Nering paper on characteristic function experiments) inspired the idea of economic experiments, while the American Management Association’s book on computerised business games designed by Bellman

44 and others suggested the topic of oligopoly. Selten convinced Sauermann, his economics teacher, of the appropriateness of experiments and wrote his first paper with him, “Ein Oligopolexperiment” (Sauermann and Selten 1960). In addition to Selten, the German group included Sauermann’s students such as Otwin Becker, Claus C Berg, Volker Haselbarth, Reinhard Tietz, and others. Sauermann collected, edited and published three volumes of this work in a book series, Beitrage zur experi mentellen Wirtschaftsforschung (1972).

While Selten’s experimental work started with oligopoly theory, he soon became interested in Simon’s theory of bounded rationality. His work has become more and more focused on developing a theory of bounded rationality. In the summer of 1991, he organised a two-week workshop at the University of Bonn, bringing together US and European experimental economists to discuss their work. While most work in the US has retained the outcome orientation of economic theory, the work of Selten and a large number of his students is oriented towards understanding the process, which is consistent with the goal of building a theory of bounded rationality.

1.6 Smith 1960-76: Theoretical Foundations

Smith’s first experimental economics article, published in Journal of Political Economy in 1962, presented the results of 11 double auction experiments conducted over six years. Subjects in these experiments were not paid any tangible rewards, they were only asked to try to make as many points as they could. Yet, the prices converged to the close neighbourhood of equilibrium predictions when collusion was prohibited and bids, offers and transaction prices were publicised. When supply and demand conditions were changed, changes in price and volume corresponded well to the predictions of competitive price theory, except for large errors during the transient phase. He also made three observations that pointed away from and beyond the extant theory – the static competitive equilibrium may be influenced by the shapes of the supply and demand functions as well as their point of intersection; the rules of the trading institution (such as single versus double auction) may affect market outcomes; and the process of equilibration in markets may be better described by excess “virtual” rent than by the Walrasian hypothesis.

For the next few years, Smith taught a seminar at Purdue that included individual and group decision-making, and utility and matrix game experiments in addition to what little was available on experimental markets. During this period, he also worked out the theory of induced valuation, which was not published until 1976 after some encouragement from Charles R Plott. This was also a period in which Smith had to develop answers to questions about the very relevance of the experimental method to economics. Discussions between Smith and Plott led to an appreciation and new appraisal of the results that had already been gathered, and to working out the philosophical underpinnings of a new discipline that began to blossom after 1974 when they both began to conduct experiments regularly.

1.7 Plott and Social Institutions

As Smith’s colleague at Purdue, Plott witnessed the experimental work of the mid-1960s. He recognised that the changing prices

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observed in Smith’s experiments may not entirely be because of changing “instantaneous” demand and supply following the Walrasian tatonnement (French for “groping”, a form of hill climbing) process. He conjectured that the equilibration process may be the result of a very different process. He worked with Harvey Reed, a graduate student, to build an alternative model rooted in game theory. Given the rudimentary nature of the available analytical tools at the time and the procedural errors they made, they arrived at conclusions that did not hold up later. In any case, economics at the time had no interest in such endeavours. Still, Plott was struck by the powerful nature of the evidence that the experimental method was capable of delivering.

The Smith-Plott interaction in the early 1970s led to the expansion of experimental ideas along three dimensions – from private good experiments to public goods experiments; from a rules of trading focus to a general institutional characteristics focus; and from a shared information and public incentives focus of the prevalent game theory (and economics) to a private information and incentives structure. All these three dimensions are evident in two key papers, Fiorina and Plott (1978) and Plott and Smith (1978). The Fiorina and Plott (1978) paper not only was a breath of empirical fresh air in a room stuffed with a large number of theories, but also presented the new branch of experimental economics to political science and public choice. In addition, it presented the “special case” argument, an important plank of the methodological platform on which experimental economics has come to rest – general theories should work in special cases of simple experiments, including the special case of simple laboratory economics, to justify their generality. These papers helped bring in three important principles to the emerging methodology of experimental economics – a focus on competition among theories to explain data; the “special case” argument; and the extension of laboratory methods to field phenomena and policy issues. Plott and Smith (1978) also turned out to be quite influential in its focus on the impact of economic institutions, and in measuring efficiency as the fraction of potential consumer and product surplus actually extracted.

1.8 Joining the Economics Mainstream

Plott moved to the California Institute of Technology and Smith to the University of Arizona in 1975. With Arlington Williams, Plott developed the first computerised double auction market, and with James Cox began to investigate sealed-bid auctions using non-cooperative game theory. With his new colleagues, Smith launched sustained research programmes in experimental economics and began to analyse the data from experiments he had conducted in the early 1960s. He finally wrote up his core methodological ideas in Smith (1976), and in the more comprehensive manifesto Smith (1982). Likewise, Plott maintained and expanded the ongoing research at Caltech and wrote his influential 1982 survey.

For reasons we discussed earlier, mainstream economics became potentially receptive to experimental methods by the early 1980s, and these articles and ongoing research programmes became the foundation of the success experimental work has enjoyed in mainstream economics. Many economists, including two of us, first heard about experimental economics around 1980 and began

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to think of new laboratory projects. The number of new investigators, new projects and new studies published in mainstream economics journals grew explosively in the early 1980s. In 2010, there were about 150 universities around the world with faculty and laboratories conducting experimental economics research. A recent compilation of the list of these laboratories is available at the website of a laboratory in France, the Laboratoire Montpelliérain d´Economie Théorique et Appliquée at Université Montpellier ( page=liste_ labos& lang =eng).

1.9 Divergence from Experimental Psychology

What is the relationship between experimental economics and the experimental side of the behavioural decision-making literature that is generally regarded as a part of cognitive psychology? The two have much in common. They share an intellectual tradition that includes the works of people like Estes, Merrill Flood and Siegel. To most psychologists, behavioural decision-making research appears to be closer to economics than to psychology; to most economists, the endeavours of experimental economists more resemble psychology than their own work. Research in both disciplines involves recruiting human subjects who are presented with the task of making some decision(s). Since they both deal with human subjects, both include procedures for handling subjects that share many common features. The same is true of analysis of data and presentation of results. Articles from both disciplines include procedural appendices as an important part of the publication. We do not believe that this list of similarities is close to being exhausted.

The experimental tradition in economics has evolved away from that of psychology since 1952. It is instructive to consider the reasons for the divergence, and to consider the prospects for a synthesis. The divergence in experimental traditions springs mainly from differences in disciplinary focus and style. First, economics focuses on human interactions mediated by markets and other specific institutions. Psychology focuses on individual human behaviour, possibly affected by the institutional environment. It is useful to visualise economic experiments to lie along a broad spectrum defined by the institutions that influence the behaviour of individuals. At one end of this spectrum are experiments in which the behaviour of individual subjects is constrained and modulated by powerful economic institutions in non-trivial ways. While the outcome of such experiments may be influenced by the individuality and ability of the subjects, the institutional structure itself is an important determinant of the outcome (Gode and Sunder 1993). At the other end of this spectrum lie behavioural decision-making experiments in which economic institutions that foster interaction among individuals and define the terms of that interaction are absent. The outcomes of these experiments are attributable purely to the characteristics of the individual, acting in isolation from others. Of course, most economic experiments lie somewhere between these two extremes, depending on the strength of the market or interactive forces present in their environment.

Second, and perhaps more important, is a stylistic difference. Over the past five decades, economics has been strongly theory-based.


Acceptable economic theories must be fully developed from pre-established first principles and relate specifically to a core micro theory. It is quite the contrary in psychology – new theories with new conceptual underpinnings (for example, recent connectionist/neural net theories) gain a serious hearing if they appear to offer a better explanation of some body of data, irrespective of their relation to pre-established theory. A third point of divergence is related to the first two. For experimental economists, salience is an essential and self-evident precept. To tie an experiment to a relevant theory, we take great pains to establish a clear incentive structure within an institutional framework. Psychologists are much more casual about defining their subjects’ incentives in experimental tasks. In particular, they feel no necessity to offer salient rewards; a “do your best” admonition to subjects is acceptable.

An example may help clarify this point. Recall Estes’ probability matching experiments. Psychologists even now are typically not sensitive to the difference between trying to maximise the fraction of correct responses and trying to predict the incorrect per cent of trials. They think of themselves as observing innate behavioural processes, so a simple “do your best” admonition seems to them to contain no important ambiguity. An economist would see that these two goals imply different optimal behaviour, and would use a specific reward structure to implement a specific goal (or would compare alternative reward structures implementing both goals). The differing attitudes towards deliberate deception spring from the same sources. Economists’ personal ethical standards are probably about the same as psychologists, but their tolerance of deceptive instructions is considerably less. Economists recognise that deception undermines salience, both directly and indirectly. Psychologists presume that innate processes will be unaffected by deception and so (as scientists) take a much more casual view of the matter. The limits psychologists may place on deception spring mainly from personal ethics or societal pressure, not from scientific principles. Psychologists generally have been more sophisticated than economists in their experimental designs. These issues are discussed in some detail in Section 3 and do not need repetition here.

When two social sciences share so much in common, it is natural to ask questions about their synthesis, or delineation of territory. If the two disciplines were to be synthesised into a single harmonious tradition, psychologists would have to take salience more seriously, and readopt the Siegel tradition. On the other hand, economists would have to become more sophisticated in the design of their experiments. Eventually, the methodological gulf will be spanned. But a methodological synthesis is unlikely to bridge the theoretical gaps and create a seamless tradition of experimentation in social science. While economics has developed a powerful imperialist lobby in recent decades, we find it useful to confine the domain of experimental economics to settings where interactive forces are still present. Psychologists have developed a deep, varied and large literature on individual decision-making that is important to many questions of interest to economists. However, experimental economics should not pretend or try to swallow that large territory. Starting from bilateral bargaining all the way back to general equilibrium experiments with interactive markets lies a vast area in which economic theory awaits experimentalists’ attention.

There is good reason to limit the extent of what we choose to label experimental economics in this manner. When economic interaction in the behaviour of individuals is absent, interesting research questions that can be asked and answered pertain to their sensory, cognitive or intellectual abilities. While we make important assumptions in economic theory about these matters, these issues are not at the centre of the discipline. If we ask 1,000 subjects to add two plus two and compute the mean answer to be 3.99, we would hardly be inclined to abandon the axioms of our number system. Instead, our schooling may deserve attention.

Among the interesting economic questions that can be addressed by the experimental method is verification if the predictions of economic theories still hold true in environments where their technical assumptions are abandoned. The focus of individual decision-making experiments is these very technical assumptions such as risk attitudes and utility functions.


China after 1978: Craters on the Moon

The breathtakingly rapid economic growth in China since 1978 has attracted world-wide attention. But the condition of more than 350 million workers is abysmal, especially that of the migrants among them. Why do the migrants put up with so much hardship in the urban factories? Has post-reform China forsaken the earlier goal of “socialist equality”? What has been the contribution of rural industries to regional development, alleviation of poverty and spatial inequality, and in relieving the grim employment situation? How has the meltdown in the global economy in the second half of 2008 affected the domestic economy? What of the current leadership’s call for a “harmonious society”? Does it signal an important “course correction”?

A collection of essays from the Economic & Political Weekly seeks to find tentative answers to these questions, and more.

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August 27, 2011 vol xlvi no 35

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