1.1 Advantages of laboratory experiments

Most practitioners of lab experiments would probably agree that a key advantage is the ability to control conditions more tightly than in any other context. For example, testing theory is a basic component of both the physical and social sciences, and the scientific method relies upon explicit tests of theory. While empirical data are indeed rich and abundant, they reflect a variety of environmental factors; disentangling these factors is difficult if not impossible.

Falk and Fehr (2003) provide the concrete example of testing tournament theory (e.g., Lazear and Rosen, 1981), where contestants should in equilibrium choose effort levels to equate marginal effort with marginal gain. Since a direct empirical test of this theory must take into account “the number of workers who compete for the prize, the effort cost functions of the workers, the exact level of the prize, and the production level including the nature of the error term” (p. 400), such a test seems impossible with traditional empirical data.¹ However, all of these factors can be controlled (and systematically varied) in a laboratory experiment. In this manner, it is also feasible to study the impact of specific institutional arrangements on behavior by systematically varying them.

Of course, the same argument can be made regarding the effects of workers’ outside options, minimum wages, sick pay, discrimination, etc. As another example, the gift-exchange game (an experimental model of Akerlof (1982)) tests for a positive relationship between wages and effort; as this is a critical assumption of efficiency-wage theories (as discussed for example in Akerlof (1984) and Akerlof and Yellen (1986)), it is useful to test it; however, it is quite difficult to do so with standard field data. In general, the laboratory offers superior control, which make it possible to identify causal relationships. In field data, variables are often determined endogenously and usually it is only possible to identify correlation. Finally, if one has doubts concerning data reported in a laboratory experiment, one can readily replicate the experiment (particularly when a standard subject pool is used).²

One of the greatest strengths of lab experiments is the ability to take a specific theoretical model (say of behavior under a specific group incentive scheme, with no communication between players and one-shot interaction), where theory says exactly what, say, the Perfect Bayesian equilibrium should be, and have real agents play exactly that game with real monetary consequences. One can then compare the predictions of the model to what happens; if the theory is rejected it is then relatively easy to test competing explanations (e.g. inequity aversion, “reciprocity”, loss aversion, framing) for the rejection. One way to think about a lab experiment is as a first link in a longer chain running from theory to actual interactions in real firms. A distinct role of lab experiments applies to situations where ‘standard’ game theory doesn’t give us crisp predictions, as in games with multiple equilibria. Important examples include production in teams with complementarities among the agents’ efforts (Brandts and Cooper, 2007), where the multiple equilibria are due to coordination problems, and repeated principal-agent interactions (e.g. Brown et al., 2004) where the folk theorem can generate an infinity of equilibria. In these cases, experiments provide information on how people behave in situations where existing theory provides little or no guide to what should happen.

The theory of mechanism design often provides suggestions for a number of mechanisms that are predicted to yield socially-efficient outcomes, or sometimes for a number of alternative mechanisms that are all predicted to be equivalent (for example, it is well known that a properly-designed tournament should be able to exactly mimic an efficient individual piece rate). Lab experiments however can be used to show that mechanisms/institutions that work in theory don’t always do so in practice, even under conditions designed to be ideal for the institution. Also, institutions that are predicted to yield identical results may not do so. In fact, the use of lab experiments to ‘pre-test’ proposed allocation mechanisms before implementing them in the real world already has an established history (see Plott (1987) for some examples). The same is true of lab experiments in at least two labor contexts: the design of matching mechanisms in professional labor markets (e.g. McKinney et al., 2005) and the design of arbitration mechanisms for public-sector union bargaining (e.g. Deck et al., 2007).

A sometimes-overlooked advantage of lab experiments is their low cost, especially compared to field experiments and survey data collection: competing explanations can often be tested or distinguished quickly and inexpensively with a modest number of sessions. In this sense, dropping laboratory experiments from our toolkit would be a little like dropping animal studies from cancer research: while results from animal studies do not always apply to humans, the ability to test many hypotheses cheaply under carefully controlled conditions provides an indispensable tool for the development of models that work in the real world.

Another comparative advantage of lab experiments is in the study of phenomena that are hard to measure in the field because they are illegal or face disapproval, such as acts of sabotage, discrimination, and spite. It is also relatively easy to measure agents’ beliefs in the lab, using monetary incentives. This is important in view of the role played by beliefs in many game-theoretic models. Belief data from experiments has been central in the development of new behavioral theory such as guilt aversion (see Charness and Dufwenberg (2006) and Battigalli and Dufwenberg (2007, 2009)).

Finally, lab experiments offer unique opportunities to researchers who are interested in the form of strategies used by agents in solving dynamic problems (or playing dynamic games). An illustrative example here is the classic problem of search from a fixed wage distribution, which is often used by labor economists to model individual workers’ unemployment spells. Theory has strong predictions here—that the optimal strategy has a reservation wage property—but it is difficult to test this prediction from field data (whether experimental or not) because strategies need to be inferred from choice histories. In contrast, the lab makes it easier to elicit subjects’ strategies more directly in a number of ways, including asking subjects to describe their strategy (Hey, 1982), observing subjects’ use of information boards (Sonnemans, 1998), and forcing subjects to play the game using the strategy method (Sonnemans, 1998; Brown et al., forthcoming). This approach has identified some interesting deviations between actual and predicted strategies (for example, subjects seem to condition their acceptance behavior on factors like their total earnings to date, which is not optimal) that researchers are now attempting to understand using a variety of behavioral approaches.

1.2 Objections to laboratory experiments and some responses

The most common objection to the data obtained through laboratory experiments is that they have nothing to do with the field environment (no external validity). In principle, this is a serious objection, of course. It comprises a number of facets, such as the fact the participants are usually undergraduate students, who typically have little experience in labor markets (particularly as firms), the issue that the stakes are low, and the fact that the “labor task” is often simply the choice of how much money to assign to another party. One might also be concerned that participants are affected by the mere fact that they are being observed (Hawthorne effects).

There are at least two main responses to these objections. First, as pointed out by Falk and Heckman (2009), “for the purpose of testing theories, [representative evidence] is not a problem because most economic models derive predictions that are independent of assumptions concerning participant pools (p. 537). Of course, it seems better to have a richer variation than is provided by undergraduate students, the most convenient source of participants for experiments conducted by academic researchers.³ The second response involves the use of more “real-world” participants, allowing for agent self-selection in the lab, less artificial tasks, and higher stakes.

Laboratory experiments have been conducted on soldiers (Fehr et al., 1998), Costa Rican coffee-plantation CEOs (Fehr and List, 2004), Chinese central planners (Cooper et al., 1999), professional arbitrators (Farber and Bazerman, 1986), Ghanaian manufacturing workers (Barr and Serneels, 2009), Japanese shrimp fishermen (Carpenter and Seki, forthcoming), and employees at large French firms (Charness and Villeval, 2009), among others.⁴ In fact, the performance by student participants is often fairly closely matched in such experiments. In addition, many if not most field experiments on incentive effects focus on highly specific industries or occupations, such as windshield repairers (Lazear, 2000), tree planters (Shearer, 2004), fruit pickers (Bandiera et al., 2005), and bicycle messengers (Fehr and Goette, 2007).⁵ Virtually all of these seem likely to be a more highly-selected population than college students as a group, who can reasonably be considered to be representative of the college-educated labor force. Therefore, if the goal is to identify general principles that apply broadly to a large population of workers, college students might be a more attractive choice than workers in a single, narrowly-defined occupation or industry.

A second approach to the “representativeness” issue is to mimic, in the lab, the same sorts of self-selection that generate different subpopulations in the real world. Clearly, such selection can be important, for example, if altruistic workers tend to self-select into cooperative work environments (such as teams), or risk-loving (or overconfident) workers self-select into highly competitive work environments. Persons in jobs that frequently require them to make “tough” decisions such as cutting workers’ pay or firing them (i.e. managers) might have highly selected social preferences indeed, so that laboratory experiments that randomly assign college students to represent “principals” may provide a particularly poor guide to the decisions of real managers. To some extent, however, laboratory experiments can allow for such self selection and even shed important light on how it works. Interesting examples of this approach in a non-labor-market context include Lazear et al. (2006), and DellaVigna et al. (2009), who allow experimental subjects to self-select out of a situation where they are “expected” to be altruistic. In a labor market context, Eriksson et al. (2008) show that allowing risk-averse subjects to self-select out of tournaments improves tournament performance. A series of interesting experiments beginning with Gneezy et al. (2003) show that women tend to self-select out of tournaments. A key advantage of the lab in addressing these self-selection questions is the opportunity to directly measure, and control for, confounding factors such as the agent’s ability at the task, her perception of her own and others’ abilities, loss aversion, and risk aversion.

Concerning the objection that the labor task is abstract and artificial, there has been an increasing trend in “real-effort” experiments, in which tasks have included proofreading (Frohlich and Oppenheimer, 1992), solving puzzles (Rütstrom and Williams, 2000), mazes (e.g., Gneezy et al., 2003), anagrams (Charness and Villeval, 2009), complex optimization problems (Van Dijk et al., 2001), simple clerical tasks (Falk and Ichino, 2006; Carpenter et al., 2010) and cracking walnuts (Fahr and Irlenbusch, 2000).

Regarding the issue of small stakes, laboratory experiments have been conducted in locations where the stakes translated into more than a month’s earnings (e.g., Fehr et al., 2002; Slonim and Roth, 1998), with evidence that fairness considerations still seem to apply.⁶ Furthermore, it is not obvious whether stakes involving larger sums of money or the small stakes that apply to decisions people make on a daily basis are more relevant for economic purposes. It is also the case that large stakes do not necessarily lead to fewer mistakes, as in shown by Ariely et al. (2008). Finally, it is possible that participants behave differently due to scrutiny (Levitt and List, 2007). As discussed by Falk and Heckman (2009), in many laboratory experiments involving more complex decisions, this is likely to be only a minor problem.⁷ And of course scrutiny can be present in the field as well, as workers are often monitored. In any event, scrutiny can be eliminated (or systematically varied); some experimenters use double-blind techniques, where payments are placed in envelopes by monitors who have not observed the experiment, so that participants understand that the experimenter cannot know their choices.

Thus, many of the objections raised against laboratory experiments are either red herrings or can be met by taking the laboratory to the field, using “real” people (of course, students are real people as well, and they respond to the financial incentives provided), real-effort tasks, and varying the stakes.⁸ So, while there are certainly issues in taking the results of laboratory experiments to the field environment, these can be ameliorated. The real value of laboratory experiments is in the enhanced opportunities for, and lower cost of carefully-controlled variation, as is required for causal knowledge rather than simple correlation. This control extends to environmental features such as institutions, payoff parameters, participant pools, the nature of the interaction among the participants (e.g., anonymity versus face-to-face; one-shot versus repeated), and even the level of scrutiny. To quote Falk and Heckman (2009): “Laboratory experiments are very powerful whenever tight control …is essential. …Tight control …also allows replicability of results, which is generally more difficult with field data” (p. 537). If one wishes to perform careful tests of theory, laboratory experiments are particularly useful. Of course, none of the comments above should be taken to imply that laboratory techniques are intrinsically superior to standard empirical data or field experiments. We discuss this issue in some detail in the next subsection.

1.3 Laboratory experiments and field experiments

Is a hammer a better tool than a screwdriver (or vice versa)? Sometimes one needs a hammer and sometimes one needs a screwdriver. They are different tools, suited for different purposes. Claiming superiority for one tool over the other seems misplaced. This principle also applies to research methods, as each method has its own strengths and weaknesses. The idea is not a new one; Runkel and McGrath (1972) identify eight research strategies (including field studies, field experiments, and laboratory experiments), which they categorize along the two dimensions of obtrusive-unobtrusive research operations and universal-particular behavior. They state: “We cannot emphasize too strongly our belief that none of these strategies has any natural or scientific claim to greater respect from researchers than any other” (p. 89).⁹

This brings us to the current debate about the value of field experiments compared to the value of laboratory experiments. List (2008) and Levitt and List (2009) extol the value of field experiments, often mentioning the notion that these are a useful bridge between naturally-occurring environments and laboratory experiments. Levitt and List (2007) provide a criticism of laboratory experiments, pointing out factors that are beneficial in field experiments, while pointing out a number of factors that make the interpretation of data in laboratory experiments problematic. Their main issue is the degree to which “the insights gained in the lab can be extrapolated to the world beyond” (p. 153); this is also known as external validity. They mention five factors (p. 154) that can influence behavior in the lab; in our view, the three most relevant of these involve the nature and extent of scrutiny (on which the greatest emphasis is placed in the paper), the context in which the decision is embedded, and the stakes of the game.

Falk and Heckman (2009) provide a response to these comments, and strongly emphasize the value of laboratory experiments. The thrust of their argument is that the controlled variation possible in laboratory experiments facilitates tests of theory, causal effects, and treatment effects.¹⁰ To a certain extent, field experiments also can provide fairly good control of the environment, although rarely to the level attainable with laboratory experiments.¹¹ Falk and Heckman address the notion that the conditions in field experiments are more “realistic”; for example, they point out how it is unclear whether undergraduate students are less representative of the overall population than sports-card traders in their natural setting.¹²

A number of arguments regarding scrutiny are mentioned above. Indeed, there is no doubt that the mere act of scrutiny can affect behavior.¹³ However, since there is also scrutiny in field environments and since the sense of scrutiny and the associated possibility of “demand effects” (where the participant acts in a manner that he or she believes reflects the experimenter’s desired outcome) can be nearly eliminated,¹⁴ this concern seems somewhat overstated. The notion that social preferences can be crowded out by large financial incentives is hardly new, as it is a feature of the Rabin (1993) model. Nevertheless, as Falk and Heckman point out, many real-life decisions involve small stakes, so that it is not clear that one requires larger stakes in order to provide incentives that are meaningful enough to match the relevant field environment.

Despite the divergent views expressed in these articles and others, it is worth noting that there is indeed common ground. For example, in both Levitt and List (2007) and Falk and Heckman (2009), the authors discuss how one needs a model or theory to transport findings to new populations or environments, whether these data originate in laboratory experiments or field experiments. These articles also appear to agree that the controlled variation in the laboratory is better for careful tests of theory. Both state that there are shortcomings in both laboratory and field experiments, but that each can provide useful insights. In fact, both camps apparently agree that both forms of experimentation (as well as hybrids) can be combined to yield a better understanding of the phenomena involved. One interesting point is that two of the key players in the debate (Falk and List) have used and continue to use both laboratory and field experiments in their research.¹⁵ In a certain sense, one wonders what the shouting is about.

Our own view is that laboratory experiments are best at testing theory and identifying treatment effects, and they can also provide useful qualitative insights. However, any assumption that the quantitative levels of behavior observed in the laboratory apply to naturally-occurring settings must be carefully considered, as the laboratory is only a model of the field environment and cannot include many details that may influence behavior.¹⁶ Field experiments, for their part, offer promise in areas that are not readily susceptible to laboratory experimentation and generally involve a greater range of personal and demographic characteristics. Field experiments are especially valuable to the extent that they can capture more realistic behavior (particularly in settings where the participants are unaware that there is an ongoing experiment). That said, a similar level of care needs to be taken in applying quantitative estimates from some highly selected field populations (fruit pickers, bicycle messengers, tree planters, school children) to other field populations. These research methodologies are complements, not substitutes. One should use the most appropriate tool or tools for the job at hand.

2.1 General design questions

The first and most basic question is how closely to try to match the field environment. This will depend to a substantial degree on whether one is testing theory, one is trying to isolate a treatment effect, or one is trying for realism in an effort to draw conclusions about the effect of policy changes in a specific environment.¹⁷ While one should be fairly insistent that the details of the design deal correctly with the issues involved with a test of theory, one cannot expect the experimental design to precisely match the field environment. There are typically trade-offs between parsimony and richness. A general rule is to err on the side of simplicity, but to include the central elements of the question at issue. It is fundamental that the participants understand the task at hand, and this varies inversely with the degree of complexity.

Regarding the issue of comprehension, a choice variable is the degree of examples (or even actual coaching) that will be provided. Experimental practice has to some extent evolved over the years. In earlier times, it was customary to provide neither examples nor test questions, out of concern that giving examples could introduce bias or demand effects. However, this policy runs the serious risk that participants will fail to understand some important aspects of the task. It has become nearly standard practice to at least ask participants questions about what outcome would prevail in the event of various combinations of choices; it is also customary to provide examples in the instructions. Of course there is always the possibility that some bias may be introduced due to this process. Nevertheless, one can minimize this possibility by going over every contingency; if this is not feasible due to the presence of a large number of contingencies, one can select “representative” contingencies. Whether examples are needed will depend on the complexity present in the experiment.

A closely-related issue is whether to use an abstract context in the instructions or to provide a richer context that points to the field environment in question. In some experiments (e.g., Charness and Rabin, 2002), the researchers are careful to choose completely neutral terms. The main advantage of this policy is that it may well limit bias.¹⁸ On the other hand, many laboratory experiments explicitly label the subjects’ roles as “firms” or “workers” (or even more specifically as “high-ability workers”, etc.) and to label the choices as “wages” or “effort”, etc., even though (strictly speaking) the experiment is simply a game with no actual work performed. As with providing examples, the main advantage of a richer context is that it makes it easier for subjects to understand the game, while the primary disadvantage is that it might bring in established behavior patterns/expectations from those environments.

The question of context, framing and reference points is not innocuous. Sometimes the details of instructions given to the subjects can unwittingly cause their behavior to focus on certain outcomes. One nice example of framing comes from Liberman et al. (2004). There are two treatments, both of which feature the identical prisoner’s-dilemma game. However, in one treatment, the game is labeled “The Wall St. Game”, while the game is labeled “The Community Game” in the second treatment. The rate of cooperation was less than 30% in The Wall St. Game, but was over 70% in The Community Game. A second example is provided by Cooper et al. (1999), who find that providing context for Chinese central planners in a lab experiment improved their understanding of the game; however this had no effect on the students in other sessions of the experiment. More recently, Levitt et al. (2009) present evidence suggesting that even professionals (such as world-class poker players who are skilled randomizers in the field) have difficulty transferring those skills to the unfamiliar context of the laboratory.¹⁹

Another important design question concerns whether an experiment features multiple periods or not. In our view, the first question the investigator needs to ask here is whether the real-world situation they are interested in understanding most closely resembles (a) repeated interactions between the same decision-makers over a long and indefinite horizon, (b) repeated interactions with a clear end date, or (c) one-shot interactions. Case (a) can be mimicked in the lab by having the same subjects interact repeatedly with the last period of the experiment unknown to the subjects;²⁰ case (b) is straightforward to implement; case (c) can be implemented either by having a single period, or by randomly re-matching subjects between multiple periods (i.e. a “strangers” design). If the experimenter is interested in one-shot interactions, having only one period is in a sense the cleanest design, but it is also the most expensive approach to gathering experimental data. It can also be problematic if agents need some experience to actually understand the game they are playing. This leads most investigators interested in one-shot interactions (where the predictions of theory are usually the sharpest) to implement multiple periods with re-matching. Interestingly, even though “standard” game theory predicts no repeated-game effects under these conditions,²¹ behavior sometimes resembles the predictions of one-shot models more closely in the last few rounds.

“Partners” designs where agents are matched for the duration of the session are, of course, expected to yield repeated-game effects; the predicted effects of repeated interaction typically differ dramatically between finitely- and infinitely-repeated games (with the “folk theorem” applying to the latter case). In the latter case, experiments are less useful in testing theory than in providing some idea of what tends to happen when “standard” theory has little predictive power. A related design question is whether people are always in the same role or whether this can change from period to period. There is disagreement concerning which approach facilitates learning, but role change permits the experimenter to compare an individual’s behavior across the various roles.

This leads us to the question of whether to use a “within-subjects” design or a “between-subjects” design. Labor economists’ experience with field data where there is typically substantial nonrandom heterogeneity disposes them towards research designs with subject fixed effects; in the laboratory, this requires administering both the treatment(s) and the control situation to the same subjects. Experimenters are accustomed to having (both observable and unobserved) heterogeneity handled by randomization, but are highly sensitive to framing and sequencing effects. Thus one’s behavior under one condition may be influenced by his exposure to other conditions (something that is usually ruled out by assumption in fixed-effects econometric models). Thus, many experimenters tend to prefer “between-subjects” designs, where each subject is exposed to one and only one treatment.

Labor economists need to be aware of this motivation for the between-subject approach. In some ways, a between-subjects design is cleaner and avoids sequencing effects (although sometimes these are a main topic of interest),²² but it is typically less powerful and costlier to implement; on the other hand, a within-subjects approach tends to be more powerful in statistical tests, but can lead to spurious correlations. An advantage of a within-subjects design is that one can control for individual differences by letting each person serve as their own control. Some experiments combine both. One way to incorporate both approaches is (a) to vary the order of treatments in a within-subject design, then (b) use only the cross-sectional data from the first treatment as a between-subjects experiment to test the robustness of the within-subject approach.

A truly crucial issue in experimental design is the calibration of the parameters, as results can be very sensitive to parameter values and functional forms. Calibration typically involves establishing a baseline for comparisons. There is little “science” to guide one to choosing parameter values; instead, this is an art that is informed by the experimenter’s intuition and experience. However, one tip is to find a calibration for which the baseline treatment’s results leave room to move in either direction (a calibration that leads to a very low or very high rate in the baseline permits movement in only one direction). The researcher must also consider how to justify the choice of parameter values and functional forms.

The choice of payoff method is intimately connected to the issue of calibration. Incentives should be large enough to induce thoughtful and motivated behavior by the participants. An additional consideration is whether to pay for each period or to pay the participant for only one (or several) periods randomly-chosen at the end of the session. It is more traditional to pay for each period, but there is a definite trend towards paying for only some random subset of all periods. The latter approach avoids wealth effects (the amount already earned in a session: participants often have some form of income targets), mitigates boredom in later rounds, and avoids issues of people taking chances because they know that they have negative earnings (bankruptcy) at some point in the session and that negative earnings are uncollectible.

Finally, while it is traditional to tell a responder the choice of the paired first mover before the response, a more economical approach involves contingent payments. In this “strategy method” (Selten, 1967), the responder states an action at each and every information set. This permits the researcher to obtain an observation at every node of the game, which is particularly valuable when a node is reached rather infrequently. However, while the quantity of data is maximized, there remains the issue of the quality of the data. The strategy method is quite popular, but remains controversial. The most exhaustive study to date (Brandts and Charness, forthcoming) examines many comparisons of results with the two methods, finding that there is generally no qualitative difference; we are unaware of any experiment in which a treatment effect is found using the strategy method that vanishes when the game is played through (“direct response”). In any case, this is an arrow in the experimentalist’s quiver and is something to consider.

We close this section with a list of “fatal errors” mentioned in Holt (2007, p. 14):

Needless to say, one should endeavor to avoid these pitfalls.

2.2 Design questions in principal-agent/effort experiments

Principal-agent experiments, discussed in detail in Sections 3 and 4, are a broad class of experiments in which a principal (who in some cases is the experimenter herself) first specifies a “contract” that describes how the agent (who moves second) will be rewarded as a function of his performance in a task. In the second stage, the agent performs the task, choosing—among other things—how much effort to expend. Principal-agent experiments are perhaps the largest class of lab experiments of interest to labor economists; this section discusses some design issues specific to these types of experiments.

A first question in these experiments is whether there will be a market for contracts. Most experiments simply start with firm-worker pairs that can realize some rents if they make an exchange and have a fixed outside option if they do not exchange. For many questions this is perfectly fine. But this leaves no room for labor markets, which can affect and be affected by the nature of principal-agent interactions. Early principal-agent experiments (e.g. Fehr et al. (FKR) 1993) incorporated an ex ante market for labor contracts, and showed that fairness considerations in the principal-agent interactions caused that market to fail to clear. More recently, Charness et al. (forthcoming) have shown how causation can run the other way: introducing ex post labor markets can eliminate the well-known ratchet effect in the repeated principal-agent problem.

If one chooses to implement a market in the laboratory, how can this be achieved? One approach involves an auction, as in FKR, who set up a two-stage game in their experiment. The first stage was a one-sided oral auction in which firms made wage proposals, but could not choose any individual worker, as every worker could accept every offer. If a worker accepted an offered wage, a binding contract ensued; people who were not paired at the end of three minutes received zero profits for this period. In the second stage, workers chose effort anonymously (only the paired firm learned the chosen effort). Other, simpler approaches to modeling agents’ outside options include simply manipulating the agent’s compensation if he/she chooses not to work for the principal to whom he/she has been assigned, or allowing an agent to receive simultaneous offers from more than one principal (see for example Charness et al., forthcoming).

As mentioned earlier, some labor experiments use some form of real effort, while others use a stated effort level that is simply a transfer (at some rate of exchange) from the agent to the principal. An advantage of stated effort is that we know the disutility-of-effort function and can therefore calculate exactly what the equilibrium effort levels should be, according to different theories. This approach also allows the investigator to induce, and manipulate, differences in ability/cost of effort, separately from other personal characteristics (e.g. risk aversion, competitiveness, reciprocity) that might be correlated with it in a sample of persons. Of course, the advantage of using real effort is that the task is more in line with what most people consider labor, and so might be considered to be a better match to the field environment.²³

Another design issue concerns who plays the role of the principal. One approach is to place all participants in the role of agents, with the agent’s compensation scheme manipulated by the experimenter. If the researcher’s only interest is in the response of agents to different compensation schemes, one might argue that this is the simplest and most economical design: all subjects are agents, essentially working “for” the experimenter by performing either a real task or selecting a level of “chosen effort”.²⁴ An alternative design assigns some subjects to the role of principals, who choose compensation policies to which agent-subjects respond. Some arguments in favor of the former approach are that (a) subjects might be more disposed to treat the experimenter (as opposed to a fellow student in the lab) like a “real” employer, and (b) the behavior of college students acting as firms provides little insight into the behavior of “real employers”. Also, when participants choose the pay scheme, it is not randomly assigned. On the other hand, the latter approach (with subjects as principals) may have advantages if one is interested in social preferences towards persons other than the experimenter, or in the behavior of principals per se (for example if the subjects are experienced managers).

Additional considerations in the design of principal-agent experiments include whether workers can self-select among reward schemes, such as a tournament or a piece-rate scheme (Niederle and Vesterlund, 2007); whether the experimenter induces reference points (Abeler et al., 2009); allows communication (Charness and Dufwenberg, 2006; Brandts and Cooper, 2007); allows for a monitoring/fines technology (Fehr et al., 2007); or for some coercion of agents (Falk and Kosfeld, 2006). In the case of multiple agents per principal, the experimenter needs to decide whether agents can observe each other’s actions (Falk and Ichino, 2006) or wages (Charness and Kuhn, 2007), whether pay is based on relative performance, or whether subjects interact in teams. All of these, and related questions, constitute the fabric of an extensive research agenda on principal-agent interactions in the lab, which we review in detail in Sections 3 and 4 below.

2.3 Reading papers involving laboratory experiments

Labor economists may be at a loss in reading papers that report the results of laboratory experiments. The format may well be unfamiliar, the design mysterious, and the statistical methods foreign. In addition, many experimental papers seem written for experimental audiences, rather than the general population of economists. Nevertheless, there are some pointers that can be provided for labor economists interested in gleaning the substance and details of experimental papers.

Perhaps the most important factor in reading an experimental paper is to understand the experimental design. This is not always as clear as it should be in the text; often, experimental referees first read the experimental instructions. These should be consulted if there is any doubt concerning the exact procedures. It is critical for the reader to understand the flow of information; this means knowing what the participants knew and when they knew it, in terms of the stages of the experimental game or task. When the design is complex, there is also a concern that participants may not have understood the game or task involved.

Once the instructions are understood, the reader should consider how well the experimental design constitutes an appropriate test of theory or matches the “ideal” field environment of interest. While one should be fairly insistent that the details of the design deal correctly with the issues involved with a test of theory, one cannot expect the experimental design to precisely match the field environment. Still, it is important that the reader is persuaded of the relevance of the experiment to the field or to the theoretical environment. The reader should also be alert to the issue of framing, given the substantial possibility that this affects behavior. To a certain degree, framing effects may wash out when one compares across treatments, but this can be a delicate issue.

An important issue when reading an experimental paper is the presentation and analysis of the data. If one is concerned with “where the bodies are buried” some degree of caution may be sensible. Authors have been known to put the best face on the data (for example, empirical researchers may tend to report the more useful regressions), so readers should keep this in mind. For example, sometimes articles emphasize (or only report) data from a subset of the periods; at times this can be justified and at times it is convenient. Sometimes authors will pool data from treatments; this increases the number of observations and makes statistical tests more powerful, but this pooling must be justified. In general, it has happened that experimental papers (and others) have interpreted their results in a favorable light. One should consider whether these interpretations are justified and whether there are alternative interpretations.

Regarding the issue of statistical and econometric tests, since most labor experiments in the laboratory feature multiple periods and interaction amongst the participants, one must have some approach towards determining how to treat multiple observations for the same individual. Labor economists are very familiar and comfortable with panel-data techniques, but experimenters are less so. Some feel that each session can only be considered to present one independent observation. A less strict approach is to collapse each individual’s choices to an average, eliminating the issue of multiple observations (but not eliminating the issue of interactions during the session). In either of these cases, it is common for experimenters to report non-parametric tests, and sometimes no regressions are reported; labor economists may be unfamiliar with these tests. One workhorse is the Wilcoxon rank-sum test, which ranks the behavior of individual participants of individual sessions in each treatment and then compares the sums. When within-subject data are available, the binomial test is often used; here one can compare changes for each individual across tasks. If these changes go predominantly in one direction or the other, one can conclude statistically that the behavior is significant. The reader should understand how these tests (and the ones reported in the article) work.

3.1 The basic principal-agent problem: One principal, one agent, one task, and one interaction

3.2 Tournaments

3.3 Teams

3.4 Multi-task principal-agent problems

Suppose the agent performs multiple tasks the principal cares about, but the principal is only able to base the agent’s compensation on her performance in a subset of those tasks. At least since Farrell and Shapiro (1989) outlined their “Principle of Negative Protection”, and Holmstrom and Milgrom (1991) introduced the “multi-task principal agent problem”, economists have recognized that, depending on circumstances, incentive systems based on a subset of the tasks performed by the agent may be less efficient than a compensation system with no incentives at all.

The first experimental implementation of a multi-task principal-agent model we are aware of is Fehr and Schmidt (2004).⁵⁶ In their experiment, an agent exerts two types of effort, both of which are observed by the principal and agent, but only one of these is contractible. The two types of effort are complements in the production of total output (specifically, output equals the product of and ). Disutility of effort, on the other hand, is given by , where is increasing and convex. Principals can choose between two types of contracts: A “piece rate contract” pays the agent a fixed base wage plus a linear piece rate per unit of task one performed. A “bonus contract” consists of a fixed base wage plus an unenforceable announcement that the agent might receive a bonus from the principal if his overall performance is “satisfactory”. Principals and agents interact anonymously, and only once.

Absent concerns for reciprocity (in the sense of perceived intentions for offering a bonus rather than a fine), it is clear that both the above contracts should perform relatively poorly: the bonus contract should yield zero effort, and the piece rate should produce effort only on the first task, which leads to very low output due to the assumed complementarity in production. Allowing for reciprocity, it is not immediately clear which contract should perform better, since both contracts allow for principals to make generous fixed wage payments that agents could conceivably reciprocate. Empirically, however, echoing results in Fehr et al. (2007b), bonus contracts perform much better than piece rates in this environment: many agents reward high effort levels on both tasks with generous bonuses, and agents seem to anticipate this. (Some apparent reciprocation of high fixed pay was evident in both treatments, but was not very effective, relative to the possibility of earning a bonus.)

In some sense, Fehr and Schmidt’s results support Holmstrom and Milgrom’s prediction that powerful incentives may be a mistake when they are based on a strict subset of the agents’ actions that affect the principal’s welfare. Indeed in such situations, Fehr and Schmidt’s results suggest that vague and unenforceable subjective performance evaluations by the principal can outperform piece rates in this case.⁵⁷ Of course, the advantages of such “bonus” contracts depend heavily on what Fehr and Schmidt interpret as workers’ concerns for fairness vis-à-vis the firm; if workers’ perceptions of fairness are manipulable or highly context-dependent, the widespread use of vague expectations as a solution to multitask principal-agent problems may not be practical.

The only other multitask principal-agent experiment we know of is by Oosterbeek et al. (2006). In contrast to Fehr and Schmidt, rather than choosing between two complementary, productive activities, Oosterbeek, Sloof and Sonnemans’ agent chooses between a productive and a “rent-seeking” activity. The latter activity is pure social waste, but increases the agent’s bargaining power by improving his outside options. In the “classic” model with no social preferences, effort devoted to rent seeking should increase when the experimenters raise the marginal efficacy of effort in that activity. In some behavioral models, however, the opposite could happen, because abstaining from rent-seeking activities becomes a more powerful signal of the agent’s good intentions the more effective those activities are. The authors’ experimental results are largely in line with the classic model.

In sum, economists are just beginning to study the multitask principal-agent problem in the lab.⁵⁸ Some key patterns that have been observed to date are:

3.5 Multi-period principal-agent interactions

4.1 Models of social preferences

We begin the discussion of the relevant literature by summarizing some of the more prominent models of social preferences. We proceed historically, rather than by publication date. For detail of the models and their full functional forms, we refer the reader to the individual papers.

Bolton (1991) develops a model in which people care about both their own money and their relative position; this model is based on the Ochs and Roth (1989) finding that people frequently make disadvantageous counter-offers in a two-round ultimatum game.⁶³ One receives negative utility from receiving less than the other person, but is not bothered by receiving more. There is a trade-off between one’s material payoff and one’s relative standing, in that a person might prefer (Own, Other) material payoffs of (3, 2) to material payoffs of (4, 6). This model is entirely consequential, as intentions or previous history does not affect preferences.

Rabin (1993) was the first to provide a formal game-theoretic model incorporating reciprocity preferences. The central notion is that of kindness, defined in terms of the payoff options made available to the other player by one’s own choice, with one’s kindness increasing as the best available payoff for the other person increases. If you are unkind, the other person may sacrifice money to hurt you, while if you are kind, the other person may sacrifice money to help you. In the latter case, mutual cooperation in the prisoner’s dilemma can be supported as an equilibrium. Dufwenberg and Kirchsteiger (2004) formally extend this model (still including kindness as the main concept) to sequential games, which facilitates application to the more standard experimental games with first movers and responders. These models concentrate on reciprocity and only employ simplistic notions of fairness and distributional preferences.⁶⁴

The Bolton and Ockenfels (2000) and Fehr and Schmidt (1999) consequential models of relative position (or inequity or difference aversion) were developed approximately simultaneously. The heart of these models is that people may (depending on parameter values) trade off money to make material payoffs closer together. The Bolton and Ockenfels model is more general and does not provide a specific functional form, while the Fehr and Schmidt model provides a simple and quite tractable functional form. The main difference between these models (in the two-player case) is that people are more bothered by being behind than by being ahead in the Fehr and Schmidt model, but that one’s disutility from unequal payoffs is unaffected by whether one is ahead or behind in the Bolton-Ockenfels model.⁶⁵

Falk and Fischbacher (2006) combine the Fehr and Schmidt notion of inequity aversion with reciprocity considerations in a complex hybrid model where a person is less bothered by another’s refusal to come out on the short end of a split than by a refusal to share equally. Importantly, they assume that one does not resent harmful behavior by the other player if it seems to come only from the other player’s unwillingness to come out behind rather than his or her selfishness when ahead. In other words, the prevailing social norm is one where it is bad form to be selfish when one has more than others, but is understandable when one has the short stick.

Charness and Rabin (2002) also combine distributional preferences with reciprocity.⁶⁶ The key innovation of this model is that people care about social efficiency, or the total payoffs for the reference group. Absent “misbehavior” (determined endogenously), one’s utility is determined by a weighted average of one’s material payoff and a social component, which is itself comprised of a weighted average of the total payoffs for the reference group and the lowest payoff for anyone in the reference group. With misbehavior, there is negative reciprocity: one withdraws one’s willingness to sacrifice to help the miscreant, by diminishing or eliminating the weight put on their payoff; one may even be willing to sacrifice to hurt the other person. However, in line with considerable experimental evidence (see the discussion below), there is no positive reciprocity in this model.⁶⁷

Cox et al. (2007) present a non-equilibrium approach that combines a form of distributional preferences with reciprocity considerations. In this approach, both status (relative position) and reciprocity affect one’s emotional state, which in turn affects the choices that are made by a utility-maximizing agent. They introduce a parametric model of other-regarding preferences in which one’s emotional state determines the marginal rate of substitution between own and others’ payoffs, and thus my subsequent choices. In turn, one’s emotional state responds to relative status and to the kindness or unkindness of others’ choices. Structural estimates of this model with six existing data sets demonstrate that other-regarding preferences depend on status, reciprocity, and perceived property rights.

A final model involves a trade-off between one’s material payoff and one’s degree of guilt from violating the expectations of another person. This is called “disappointment aversion” in Dufwenberg and Gneezy (2000), but is probably better known as “guilt aversion” (Charness and Dufwenberg, 2006). The idea is that the more one believes that a party with whom one is paired is expecting a favorable move, the more likely it is that one chooses the actual move. Charness and Dufwenberg (2006) find support for this notion, as there is a strong positive correlation between a responder’s beliefs about the first-mover’s beliefs and the responder’s choice of the favorable action. Formal presentations of this concept (“simple guilt”) and a more complex version (“guilt-from-blame”) in which one feels guilt only to the extent that one believes that the other party blames one for an unfavorable outcome can be found in Battigalli and Dufwenberg (2007, 2009).⁶⁸

In sum, a number of models of social preferences have been proposed, mainly classifiable into distributional models and reciprocity models and hybrids of these two approaches. Other motivations such as guilt aversion (and lying aversion, which has not generally been formalized; however, see Charness and Dufwenberg (forthcoming) for one approach) are also being considered in recent models.

4.2 The gift-exchange game

Probably no experimental game in the area of labor economics has had as much impact as the gift-exchange game, which tests the notion (Akerlof, 1982; Akerlof and Yellen, 1988, 1990) that there is a positive relationship between wages and effort. This game was designed to mimic an employment relationship, in that labor contracts are typically incomplete and effort is not (fully) enforceable; thus a wage offer is binding, but effort is discretionary. In its basic form, the experimental participants are divided into “firms” and “workers”, who interact anonymously either in some form of labor market or in one-to-one pairings; typically, the game is played for a number of periods. In this subsection we report results from the earliest gift-exchange experiments.

The first paper reporting results from the gift-exchange game is Fehr et al. (1993). They create a competitive labor market using a two-stage game. Workers and firms⁶⁹ (with more workers than firms) were separated into two rooms, and communication between the two rooms took place via telephone. The first stage was a one-sided oral auction with employers as bidders. Firms made wage proposals, which were posted in the room containing the workers. Once a worker accepted an offered wage, the first stage was concluded for both the firm and the worker. A firm could revise its (non-accepted) wage offer upward, so that it was higher than any existing posted wage offer. People who did not contract received zero earnings for the period. In the second stage, workers chose effort and this choice was only revealed to the paired firm. Firms chose wages (restricted to be multiples of five) from the interval [26, 126], earning (126-wage) × effort. Workers earned the wage less 26 less the cost of effort, shown below:

If workers are purely self-interested, the prediction is of course that they will choose regardless of the wage. Knowing this, firms will choose a wage of 30, the lowest wage ensuring participation. However, the main result is that both wages and effort levels far exceed the predictions with self-interested workers, as the average wage was 72 and the average effort chosen was 0.4. In addition, there is a very strong positive relationship between effort and wage.

The second paper in this series is Fehr et al. (1998), who conduct both a one-sided oral auction treatment and a bilateral-gift-exchange treatment using Austrian soldiers to test the robustness of the Fehr et al. (1993) results and to determine the relative effect of competition on wages. An additional treatment involves complete contracts, in the sense that the experimenter enforced an effort level of 1.0 and no effort costs were subtracted from worker’s earnings. The main finding is that gift exchange persists even in the absence of competition, when firms and workers are matched on a one-to-one basis; after a few periods wages in this treatment (and the ratio of effort to wage) coincide with wages in the one-sided oral auction without effort enforcement. Thus, the qualitative findings of Fehr et al. (1993) are replicated with non-student participants and even without competition. Wages were considerably lower when effort is enforced, although still substantially above the minimum needed to ensure participation (workers could reject offers).

Fehr et al. (1997) study the impact of reciprocity on contract terms and their enforcement with three experimental treatments involving competitive markets and more workers than firms. In each treatment, the firm specifies a wage, a desired effort level, and a fine imposed if the firm detects that the worker has shirked (provided less than the contracted level of effort). In the weak-reciprocity treatment, workers who have accepted posted contracts choose effort levels, and a random device determines whether shirking is verifiable (and fined at the specified level); the firm then learns the chosen effort level. The no-reciprocity treatment is identical, except that the experimenter exogenously fixes the effort level. Finally, in the strong-reciprocity treatment, there is an additional stage in which firms can reward or punish workers at a cost. The results show that firms demand and enforce much higher effort levels in the strong-reciprocity treatment than in the weak-reciprocity treatment; there is much less shirking in the strong-reciprocity treatment. In fact, both firms and workers earn more in the strong-reciprocity treatment, in large part because the higher effort levels lead to a larger pie. Nevertheless, firms’ contract offers are much higher in the weak-reciprocity treatment than in the no-reciprocity treatment, and the offers increase with the desired effort level.

In sum, the gift-exchange game has been a very successful approach to modeling labor issues in the laboratory. The main finding is that higher wages lead to higher effort. This section reports only the earliest gift-exchange experiments.

4.3 Multi-worker gift-exchange experiments

It seems substantially more realistic to consider an environment in which a firm has more than one employee. When there are multiple workers who receive wages and who can provide effort that benefits the firm, there is the possibility of dispersed responsibility for the firm’s earnings (leading to possible free riding) and there are considerations of horizontal fairness (one’s pay compared to the pay of other workers).

Maximiano et al. (2007) compare a bilateral gift-exchange game with one in which each firm has four workers; in the latter case the employer is likely to earn much more than any of her workers, thus reducing the need for any individual worker to sacrifice to help the relatively high-income firm. The authors did not expect gift exchange to survive in this environment.⁷⁰ In fact, effort levels in the latter treatment are only marginally lower than in the bilateral game, so that “the gift exchange relationship is quite robust to increases in the size of the workforce” (p. 1026).⁷¹ Their results suggest that intentions-based reciprocity is a driving factor, although efficiency preferences (Charness and Rabin, 2002) may also play a role in inducing this behavior.

Charness and Kuhn (2007) match two workers (with different productivity levels, although the precise levels are unknown to the workers) with one firm to investigate whether workers have concerns with pay inequality and whether pay secrecy and pay compression is therefore beneficial for a firm; in a within-subjects design, we varied whether a worker was aware of the other worker’s wage. Under fairly general conditions, we demonstrated theoretically that workers’ responsiveness to co-workers’ wages should lead profit-maximizing firms to compress wages or maintain pay secrecy. And, as in other gift exchange experiments, we observed a strong positive empirical relationship between “own” wages and effort. Surprisingly, however, the effort level provided by a worker was unaffected by the wage paid to his or her co-worker. Furthermore, although firms compress wages when the co-workers will know both wages, this did not raise profits. It seems that the relationship between a worker and the firm is much more salient than the relationship between the pay of the co-workers. Overall, our experimental evidence “casts doubt on the notion that workers’ concerns with equity might explain pay policies such as wage compression or wage secrecy” (p. 693).

Gächter et al. (2008) perform an experimental analysis of pay-comparison information and effort-comparison information in an environment in which firms are matched with two workers. While effort is highly sensitive to the worker’s wage, co-worker wages per se have no effect. Further, when the firm pays different wages to the workers, the co-worker’s effort decision is ignored. However, worker behavior is affected when both pieces of social information are provided: a generous wage generates higher effort when one’s co-worker exerts high effort, but is ineffective when the co-worker contributes little or no effort. They suggest that group composition is a relevant factor for obtaining beneficial effects from social information.

Abeler et al. (forthcoming) focus on a two-worker-one-firm environment in which a worker knows both the ability and effort level of the co-worker. However, they reverse the order of play, as workers first choose effort levels and the paired firm then chooses wages. In one treatment firms are constrained to pay equal wages, while in a second treatment there is no such constraint. Perhaps surprisingly, they find that there is lower effort when the firm is forced to pay equal wages, as a worker who chooses higher effort than the co-worker does not feel it is fair to receive the same wage as the co-worker, and subsequently reduces effort. Thus, it is important to pay attention to equity considerations rather than equality per se.⁷²

In sum, there have been a modest number of gift-exchange experiments with multiple workers, a more realistic case than the standard game.

4.4 Positive and negative reciprocity

While the classic gift-exchange experiments provide strong evidence of reciprocal behavior, it is less clear that this represents reciprocity in a strict sense. The reason for this is that people may have distributional preferences that could lead to the same behavior that is observed in an environment where reciprocity is possible. Thus, positive or negative reciprocity reflects behavior that differs from what a responder would have done in the absence of a first-mover action that is perceived to be positive or negative. Some experimental games from Charness and Rabin (2002) illustrate this point. In the baseline case, a participant unilaterally chooses between (Other, Own) material payoffs of (400, 400) or (750, 375). Around fifty percent of the population chooses to sacrifice 25 units to give the other person an additional 350 units, even though this leads to a large difference in material payoffs.

In a second case, the other paired participant first faced a choice between payoffs of (750, 0) or passing the choice to the second participant, who would once again face a choice between (Other, Own) payoffs of (750, 375) or (400, 400). Positive reciprocity would imply that the rate of (750, 375) choices should increase, as the first mover would clearly seem to be kind by allowing the responder to receive a positive payoff. However, in fact the rate goes down slightly (to 39%)! So positive reciprocity doesn’t seem to be present here. In a third case, the other paired participant first faced a choice between payoffs of (550, 550) or passing the choice to the second participant, who would once again face a choice between (Other, Own) payoffs of (750, 375) or (400, 400). Negative reciprocity would imply that the rate of (750, 375) choices should decrease, as the first mover would clearly seem to be unkind by forcing the responder to receive a smaller material payoff than was available with the outside option. In fact, the rate of (750, 375) choices does decrease sharply to 11%; thus, negative reciprocity is a factor.⁷³

Perhaps the first experimental paper to carefully test for positive and negative reciprocity was Charness (2004).⁷⁴ This paper considers gift-exchange in a bilateral setting, varying whether the wage was determined by a self-interested firm or generated by an exogenous process (such as a draw from a bingo cage); in all cases, the firm benefits from the worker’s chosen effort. There is a strong positive relationship between wage and effort in all treatments. However, the effort level with low wages is lower when the wage was chosen by a self-interested firm than when it was generated exogenously, suggesting the presence of negative reciprocity. On the other hand, there was virtually no difference across treatments in the effort level with high wages. Thus, this paper was the first to provide experimental evidence that positive reciprocity seems to be much weaker than negative reciprocity, while at the same time clearly identifying the effect of the distribution of payoffs per se on behavior.

A subsequent and related paper (in a non-labor setting) is Offerman (2002), who studies the effects of random choice mechanisms while allowing for both positive and negative reciprocity. He considers players’ responses to a helpful or hurtful choice, as a function of whether the “choice” was made by an interested party or generated at random (responders could sacrifice one unit to either increase or decrease the first-mover’s payoff by four). Following the helpful choice, responders never paid to lower the first-mover’s payoff, but paid to help first movers more often when the first mover made the choice than when the choice was randomly-determined. This suggests some positive reciprocity may be present, although the effect is not significant. On the other hand, the effect on the response to the first-mover’s perceived intentions was dramatic and significant following a hurtful choice, again suggesting that hurting hurts more than helping helps (the title of the paper).

Brandts and Charness (2003) test for punishment and reward in a cheap-talk game and show that intention is a critical issue, finding substantial negative reciprocity and limited positive reciprocity. One player sends a message about her intended play to another player; after play takes place, the other player is then given an opportunity to punish or reward the first player. The authors found that the responder was twice as likely to punish unfavorable play by the first player if that first player had lied about his play than if he had told the truth. A relatively small number of responders chose to reward a favorable play by the first mover.

On the other hand, Cox (2004) reports significant positive reciprocity in the investment game (Berg et al., 1995).⁷⁵ The triadic design compares behavior in the standard game with behavior when the first mover is a dictator and to behavior when the experimenter determines the amount received by the responder rather than this being determined by a self-interested first mover; this procedure should allow one to distinguish distributional preferences per se from reciprocal preferences. Cox et al. (2008) finds significant positive reciprocity, but does not find significant negative reciprocity in the “moonlighting game”, where the first mover can take from the responder as well as pass to the responder. Finally, Cox and Deck (2005, 2006) report mixed findings on positive reciprocity; the results depend on whether or not the experimenter can observe the actions of the players (double blind or single blind), as well as on the sex of the subject.

In sum, the experimental evidence regarding intention-based positive and negative reciprocity is mixed, although the general result is that negative reciprocity is stronger than positive reciprocity. In a sense, this can be seen as reflecting expectations and violations thereof, as seen in a self-serving way. If one expects kind or favorable treatment and receives it, there is no strong emotional jolt; on the other hand, if one has this expectation and receives unkind or hurtful treatment, the emotional response is much stronger.

4.5 Pay regulation

Governments often consider whether to regulate pay by means such as mandating a minimum wage or a sick-pay rate. What are the effects of such policies? In the field, it is difficult to ascertain this, as there are many factors present and changing at the same time. Thus, experimental techniques are likely to be useful, as the effects of such policies can be successfully isolated.

Brandts and Charness (2004) were the first to study the effect of a minimum wage in a gift-exchange format. They created a more symmetric payoff design. Each person was endowed with 10 units, the first mover could pass up to 10 units, and the responder received five times whatever was passed; the responder could then send back up to 10 units, with the original first mover receiving five times whatever was passed back. Brandts and Charness imposed a minimum wage of five in a condition with an excess supply of workers. The mandated minimum wage was counterproductive in the sense that the average effort was 30% lower than without it, even though the average wage was 5% higher. In addition, they found that the highest wage was chosen only half as frequently in the minimum-wage condition, with effort also reduced by 30% at this top wage.

Falk et al. (2006) test the effect of imposing a minimum wage in an environment in which each firm is matched with three workers and must choose the same wage for each of the workers. The workers decide on the minimum wage that they would conditionally accept (the strategy method) and the actual assigned wage is then accepted or rejected accordingly; however, workers do not choose effort levels, and a firm’s profits only depend on the number of workers who accept the wage offer. In some sessions, fifteen periods of a mandated minimum wage were followed by 15 periods with no minimum wage; the order was reversed in the other sessions. They find that there are lasting consequences of the mandated minimum wage even after it has been removed, in that firms must pay higher wages after the removal than before it was imposed. Thus, the authors conclude that policy can affect people’s sense of what is a fair wage.

Owens and Kagel (2010) use a variant of the payoff design in Brandts and Charness (2004). They find that an imposed minimum wage reduces effort in the neighborhood of the minimum wage, but that there are no significant effects on effort levels for higher wages. The minimum wages leads to improved incomes for both firms and workers (particularly the latter). Since there is little effect at higher wages, it appears that the minimum wage requirement is less salient at these higher wages and/or that employees recognized that wages set a good deal higher than the minimum represent just as large a monetary gift as without the presence of the minimum.

Dürsch et al. (2008) report the results of a form of gift-exchange game that investigates the issue of sick pay in an experimental labor market. The main variation is whether there is one-to-one matching of firms and workers or whether there is a market setting in which firms post wage offers and workers select the ranking of their preferences regarding the possible offers; in the latter case, a firm may end up hiring more or less than one worker. In all cases, there is a one-third chance (chosen at random) that a worker will be “sick” and so be unable to complete his or her intended effort. Firms chose one of five possible contracts, each of which specified a wage to be paid in case of zero effort (not showing up for work, either because the computer made this choice or because the worker chose zero effort voluntarily; the firm cannot tell if the worker is actually sick or simply chose to stay home) and a wage to be paid in case of positive effort. The main findings are that higher wage offers significantly increase effort choices (both with respect to sick pay and non-sick pay), firms can attract more reciprocal workers by offering sick pay, but firms benefit from offering sick pay only in the market setting where there is competition for workers.

Bauernschuster et al. (2009) use a similar design to consider the effect of sick pay with heterogeneous workers with different likelihoods of being “sick”. They use a 2×2 experimental design, in which they vary whether there is a minimum sick-pay rate (40% of the wage) and whether workers all have the same 20% rate of being sick or whether half of the workers have a 10% chance of being sick and the other workers have a 30% chance of being sick. Issues of interest include the degree of moral hazard (pretending to be sick), whether the adverse-selection problem is severe enough to lead to a collapse in the market for sick pay, and whether higher levels of sick pay lead workers to choose higher effort levels. The main results are that higher-risk workers do indeed select into contracts with higher sick pay rates, and they pay for this by getting lower wages and an overall worse deal than the low risk workers, higher sick pay leads to increased effort, but only in the case where the sick pay rate is freely-chosen, and the sick-pay market does not break down due to the adverse-selection problem.

In sum, there are mixed results regarding the effect of imposing a minimum wage. Regarding sick pay, it appears it is possible (but perhaps not easy) to design systems where this is a useful policy intervention.

4.6 Do gift-exchange and social preferences map into the field?

A major question that labor economists might have concerning laboratory gift-exchange results is the degree to which these mean anything in the field environment (external validity). Two recent papers call into question the degree to which the social preferences exhibited in these experiments are robust. On the other hand, a number of other studies provide evidence that the social preferences identified in the laboratory map well into the real world.

Gneezy and List (2006) investigate whether gift-exchange behavior persists over time in two real-effort tasks, one involving work in a library and the other involving door-to-door solicitation. The mechanism for testing for reciprocity consists of the experimenters telling people that they will be receiving a certain piece rate for their work, but then announcing at the time of the six-hour task that in fact they will be paid a substantially higher piece rate. The results are persuasive, particularly for the fundraising task: people do in fact work harder for the surprise pay, but this effect vanishes over the course of time. Thus, these results constitute a cautionary note against applying the results of these laboratory experiments to the field environment. However, one caveat is that these experiments only pertain to positive reciprocity, as even the lower advertised pay rate is above the alternative wage that the student workers would normally earn. Given the relative dearth of positive reciprocity in laboratory experiments, it may not be so surprising that positive reciprocity in these field experiments is fleeting.

Fershtman et al. (2009) present compelling evidence that social preferences are subject to framing effects and are not general to all environments. They show that introducing a competitive frame to the environment crowds out social preferences in mini-dictator and trust games. For example, 72.5% of dictators choose an (Own, Other) allocation of (8, 8) instead of (11, 2). This is followed by a real-effort competition between the dictator and the recipient, where the (8, 8) outcome is implemented if the recipient wins but the (11, 2) outcome is implemented otherwise. If the dictator really wanted the (8, 8) split, the simple strategy would be to solve no problems; however, dictators contribute considerably more effort when solving more problems leads to higher own payoffs than when solving more problems doesn’t affect these payoffs (in the baseline condition). Furthermore, in another treatment the (11, 2) split is implemented if the dictator loses to the recipient, while otherwise the (8, 8) split is implemented. In this case, 85% of the dictators do nothing. This result demonstrates that social preferences may not have much effect when competition is salient.

Two other experiments present a different view than Gneezy and List (2006). Bellemare and Shearer (2009) conduct a field experiment that investigates worker responses to a monetary gift from their tree-planting firm using incentive contracts. Workers were told that they would receive a pay raise for one day. Productivity on the day of the gift is compared with productivity on adjacent days, under similar planting conditions. They find direct evidence of a significant and positive effect on daily planter productivity on the day of the gift, controlling for a variety of other possible factors. Kube et al. (2006b) conduct a field experiment involving a six-hour task in which the participants were told that they would presumably receive 15 Euro per hour; in three treatments, they were then paid either 10, 15, or 20 Euro per hour. The main result is that there is little difference in performance in the treatments where people are paid either 15 or 20 Euro per hour, but that there is a strong, deleterious, and lasting effect on performance when people are paid less than the presumptive rate. These results suggest that there is an asymmetry between positive and negative reciprocity in the field, very much in line with the evidence found in laboratory experiments. However, one caveat to these results is that the sample size is quite small.⁷⁶

There are two main threads of evidence suggesting that social preferences are linked to the general population and the workforce. First, there are a number of non-laboratory experiments in European nations that show that the basic behavioral patterns observed in fairness-related experiments with students also prevail in representative samples of the general population, with older cohorts generally being more reciprocal than younger cohorts.⁷⁷ Holm and Nystedt (2005) analyze behavior in the investment game, with people selected from a public database in Sweden. While the average amount returned was similar for both cohorts, the proportions dispersed for the older responders, suggesting a greater degree of responsiveness to the environment. Other studies conducted with representative surveys in Germany (Fehr et al., 2002) and the Netherlands (Bellemare and Kröger, 2007) conclude that older cohorts are more generous as responders. Falk and Zehnder (2006) find substantial evidence of social preferences in a sequential trust game conducted with 1000 residents of Zurich, also finding evidence of discrimination and in-group favoritism. Sutter and Kocher (2007) find that the elderly are more reciprocal, in a study with participants ranging from 8-year-old children to people in their late sixties. In their study, trust increases from early childhood to early adulthood, but stays constant thereafter. Finally, Karlan (2005) finds that the amounts returned in a laboratory investment game conducted in Peru predict micro-finance loan payments a year after the experiment.

The second thread involves studies that show a relationship between worker productivity and social preferences. Barr and Serneels (2009) conducted a study with Ghanaian manufacturing workers. They find that a measure of trustworthiness (the ratio of the amount returned to the amount sent) has a positive relationship with the wages paid, with these wages being used as a proxy for productivity. This is particularly true with respect to the average trustworthiness in the workplace in question, although the direction of any causal relationship is unclear—are people more trustworthy because their wages are higher or vice versa? They conclude that behavioral characteristics and corporate culture are major determinants of the productivity of the firm and the operation of the labor market. Carpenter and Seki (forthcoming) conducted a series of experiments with local shrimp fisherman in Japan. They used a laboratory public-goods game to measure social preferences and also obtained measures of fishing productivity. The main finding is that there is a strong correlation between measured social preferences and productivity for the fisherman; a second finding is that social preferences grow with the degree to which team production is present in the fishing environment.

In sum, there is mixed evidence regarding the extent to which social preferences manifest in the field. It is clear that these are not present in all environments, but there are a number of papers providing evidence from laboratory and field experiments, as well as work environments and surveys, that suggest that social preferences can be a factor in the field.

4.7 Communication

In this final subsection, we consider how communication can affect behavior in principal-agent relationships. While it is true that other forms of social considerations such as distributional preferences and negative reciprocity are likely to lessen the applicability of the equilibrium contracts derived from standard theory, some studies demonstrate that communication can lead to better social outcomes than can be achieved with more standard social preferences.

Charness and Dufwenberg (2006) examine experimentally the impact of communication on trust and cooperation with hidden action (moral hazard). The principal has an outside option that (in the main treatment) gives (Principal, Agent) payoffs of (5, 5); alternatively, the principal can leave matters up the agent, who chooses between (Principal, Agent) payoffs of (0, 14) and expected payoffs of (10, 10).⁷⁸ With standard preferences, the agent would choose (0, 14), so that the principal will choose (5, 5). In fact, there are substantial rates of cooperation even in the absence of communication, but the likelihood of the (10, 10) expected outcome increases from 20% to 50%. Furthermore, this increase is almost entirely driven by free-form and endogenous promises (statements of intent) by the agent to behave cooperatively. The evidence is consistent with people striving to live up to others’ expectations so as to avoid guilt. When players exhibit such guilt aversion, communication may influence motivation and behavior by influencing beliefs about beliefs. Charness and Dufwenberg argue that guilt aversion may be relevant for understanding strategic interaction in a variety of settings, and that it may shed light on the role of language and social norms in these contexts.

Brandts and Cooper (2007) study manager-worker interactions in an environment where payoffs depend on employees coordinating at high effort levels; the lowest effort level chosen by any worker determines the overall production. One treatment investigates the effect of increased incentives (the marginal benefit of coordinating on a higher effort level increases substantially) on worker behavior, while a second treatment allows the manager to communicate via chat with the workers. It turns out that communication is a more effective tool than incentive changes for improving coordination on high effort levels. An analysis of the content of communication indicates that the most effective communication strategy is to request high effort, pointing out the mutual benefits of high effort. Thus, direct financial incentives have some benefit in terms of coordination, but messages are the better strategy if one cannot choose both.

Charness and Dufwenberg (forthcoming) investigate the impact of communication on trust and cooperation with hidden information (adverse selection). There are two possible agent ability levels, with a 1/3 chance that an agent will have high ability. The principal has an outside option or can leave matters up the agent. There are two main cases. In the first, there are possible Pareto-improvements over the outside option for both types of agents. In the second case, there is no feasible Pareto-improvement for the low-ability agent. While the standard game-theoretic prediction is for the principal to choose the outside option in both cases, the authors find a dramatically different effect of free-form communication from the agent to the principal in these two cases. When a Pareto-improvement is feasible with a low-ability agent, communication doubles the rate at which the low-ability agent sacrifices money to help the principal. However, communication has no effect in the alternative case. The difference is driven by the fact that many messages in the first treatment confess that the agent has low ability, but that he or she will choose the Pareto-improvement over the selfish option (and they all do so). Charness and Dufwenberg conclude that is good policy to offer lower-ability workers an opportunity to participate in a socially-beneficial outcome, as they are likely to behave cooperatively.

In sum, while experiments on cheap talk have been conducted for over 20 years, some recent work has applied such nonbinding pre-play communication in clear principal-agent environments. This is a very promising area for both future research and policy.