5 More Lab Labor: Bargaining, Search, Markets, and Discrimination

In this section we summarize the contributions of laboratory experiments to aspects of labor economics other than the principal-agent problem or labor supply issues. These are, in turn, bargaining, strikes and arbitration; search; models of labor market equilibrium; and the study of gender, race and discrimination in labor markets.

5.1 Bargaining, strikes and arbitration

The bilateral bargaining problem—how a surplus is divided between two players—has a long and rich history in economic theory, dating back at least to Nash’s (1950, 1953) contributions to co-operative and non-cooperative bargaining, and important subsequent developments such as Rubinstein (1982).79 Experimental studies of bargaining also have a long history, both in psychology (see for example Deutsch and Krauss, 1960) and economics (Siegel and Fouraker, 1960). Roth (1995) reviews the experimental economics literature on bargaining up to that point, much of which aims to test predictions of the Nash, Rubinstein and related models. As already noted, a well known and robust result of these tests is that bargaining outcomes in the lab are not well described by perfect equilibria of games between rational, selfish agents; behavior is often highly suggestive of social preferences among the bargainers.

Given these early laboratory findings, it is perhaps not surprising that much of the more recent experimental bargaining literature has attempted to understand the nature of apparent social preferences in bargaining situations; this is typically done using extremely simple bargaining games (such as the ultimatum and dictator games) where there are fewer confounding factors, including strategic considerations, that might also affect outcomes. Recent examples of this approach include Charness and Rabin (2002), Andreoni et al. (2003), and Frechette et al., 2005; Charness et al., 2007).

While the above bargaining models and experiments were motivated and framed in a variety of ways (including relatively abstract frames, or as buyer-seller interactions), labor economists have found them of primary interest for the light they might shed on union-firm negotiations.80 In particular, labor economists have used formal bargaining models and laboratory experiments to shed light (a) on the determination of disputes (strikes, lockouts, holdouts) and (b) on mechanisms—in particular, arbitration—that are designed to reduce the costs of such disputes.81 We consider these two applications of bargaining theory and experiments in turn below.

While economists have been discussing the determinants of strikes since Hicks (1932) stated his famous “paradox” (if parties can forecast the bargaining outcome after a strike they can always do better to settle on that outcome immediately without a strike), theoretical and experimental analysis of strikes by economists did not begin in earnest until the advent of asymmetric information models of bargaining, which produced disputes such as strikes as equilibrium outcomes. Early theoretical contributions of this nature include Hayes (1984); Kennan (1987) provided an early review of the “economics of strikes”. Since then, Sopher’s (1990) laboratory experiment tested the simple “joint cost” theory that strikes will be less common when their social cost to the bargainers is higher in a shrinking pie bargaining game. Berninghaus et al., 2001, 2003; Tournadre and Villeval, 2004).82

The aspect of bargaining on which labor economists and others have conducted the largest number of laboratory experiments is not strikes per se, but the effectiveness of dispute resolution (i.e. arbitration) mechanisms in encouraging bargaining and reducing disputes. In at least one way this is not surprising, as arbitration is a classic example of mechanism design, and a laboratory experiment is a natural way to “pre-test” a mechanism under ideal conditions to see if it has a reasonable chance of functioning as predicted in the field.83 In addition, there is of course considerable policy interest in the design of arbitration mechanisms that encourage (efficient) settlements and minimize the use of the mechanism itself (especially in view of Crawford’s 1979 dictum that the best arbitration system is one that is never used). Thus, the evaluation of arbitration mechanisms is one area where laboratory research by labor economists has already been successful in influencing economic policy.

While laboratory experiments testing different arbitration (and other forms of third-party intermediation) systems have a long history in psychology (see for example Johnson and Tullar, 1972), the earliest experiment on arbitration by economists of which we are aware (Farber and Bazerman, 1986) is noteworthy for its methodology in view of current debates in economics about the lab “versus” the field: Farber and Bazerman essentially conduct what is now called an (unpaid) “artefactual” field experiment by confronting professional labor arbitrators with hypothetical cases and asking them to choose a settlement under different arbitration schemes. Since then, economists have performed a multitude of experiments evaluating different arbitration schemes, most of them “traditional” laboratory experiments, such as Ashenfelter et al. (1992).

A key question addressed in early experimental studies was the differential effects of conventional arbitration (where the arbitrator can impose any settlement he feels is “fair”) versus final-offer arbitration (where the arbitrator is constrained to choose either the firm’s or the union’s final offer). In line with its proponents’ expectations, early laboratory experiments (e.g. Dickinson (2004, 2005) and Deck and Farmer (2003). Deck and Farmer (2007) and Deck et al. (2007) further show that this result is robust to uncertainty over the final value of the quantity bargained over. Also to the credit of conventional arbitration, Kritikos (2006) finds that final-offer arbitration pushes parties to an equal split of the pie 80% of the time, which he interprets as an unnatural distortion of bargaining.

In addition to conventional versus final-offer arbitration, laboratory experiments have been used to study the effects of the following dispute-resolution mechanisms: tri-offer arbitration (an amendment to final-offer arbitration where the arbitrator can also choose a third option provided by an outside “fact finder”); combined arbitration (which imposes final offer arbitration when the arbitrator’s “fair” settlement lies between the parties’ final offers, and conventional arbitration otherwise); and other schemes known as double-offer arbitration, amended-final-offer arbitration, and automated negotiation. Providing a full description of these results is beyond the scope of the current paper. A recent review, however, is available in Kuhn (2009). By pointing the reader towards this large literature, we hope instead simply to provide an example of a “success story” for laboratory experiments in labor economics: The use of the lab as a testing ground for dispute-resolution mechanisms in labor markets has yielded results of interest not only to readers of Econometrica, but also to policymakers who are faced with the real problem of designing dispute-resolution mechanisms, especially in public-sector labor markets where strikes are prohibited by law. This is clearly a case where “lab labor” has already passed the market test.

5.2 Search

Labor economists have been using sequential search models to interpret field data on unemployment durations since at least Lippman and McCall’s classic survey (Meyer (1995, 1996).84

This said, both the field experiments and econometric studies of job search and unemployment durations discussed above are probably better suited to evaluating the effects of specific policy changes in specific markets than to testing the most basic predictions of sequential job-search models; indeed many of the estimated effects of policy changes are just as consistent with simple labor-supply models (e.g. Moffitt and Nicholson, 1982) as they are with the search paradigm. The history of laboratory experiments on search, however, focuses much more on the decision processes of individual searchers, and on assessing whether these are consistent with the rules derived from search-theoretic optimization. Given the significant role still played by search models in interpreting microeconomic studies of unemployment and other durations, and in general equilibrium and macroeconomic models of the labor market, laboratory search experiments make an important, but distinct contribution to the economics of labor market search.

To our knowledge the first economists to conduct laboratory search experiments were Schotter and Braunstein (1981, 1982).85 Subjects engaged in search for a wage drawn at random from a known distribution (either rectangular or triangular), where each draw from the distribution cost the subject image. In the baseline treatment, subjects could take as many draws as they wished, and could accept any of the offers they had received (i.e. there was unlimited recall of past offers). Optimal search theory has strong and well-known predictions in this situation—including the fact that the optimal strategy is a constant reservation wage—and the authors were interested in comparing subjects’ actual behavior to these predictions.

In many ways, the subjects’ behavior conformed to theory quite closely. The authors elicited reservation wages by asking workers to bid for the right to search; these reservation wages were, on average, very close to the theoretical optimum for a risk-neutral searcher. Actual search behavior conformed to these elicited reservation wages. Subjects responded to increased search costs and to a mean-preserving spread of the wage distribution as predicted. This said, two interesting anomalies were identified. First, in violation of the theoretical predictions, reservation wages were not constant over time—they fell. (Since reservation wages were optimal at the start of a search spell, this meant that, on average, subjects did not search long enough.) Second, when the subjects were asked to describe their search strategy, most subjects reported that their strategy had two components: (a) a reservation wage, and (b) a maximum number of searches they would conduct. It is tempting to conclude that the latter aspect of the subjects’ self-reported strategies explains the falling reservation wage in Schotter and Braunstein’s results.

Hey (1982) conducted search experiments similar to Schotter and Braunstein’s, (infinite horizon, full recall, constant cost per offer) though in Hey’s case the context was consumer search, and subjects did not know what distribution the offers were drawn from (it was normal in practice). Despite this, over 40% of subjects stopped searching with the first price below the theoretically optimal reservation price. Hey’s study is however most interesting for the methodological innovation (in economics) of protocol analysis in which the subjects are asked to report their thinking during the session out loud, and their words are recorded. It is interesting to compare these self-reported strategies to the predictions of theory. Interestingly, while only a small minority reported a pure reservation-wage strategy, many of the rule-of-thumb strategies described by the subjects performed well, both as (sometimes imperfectly) implemented by the agents themselves and as mechanically played by a computer against the price distribution in the experiment. Hey’s paper thus illustrates another potential advantage of laboratory experiments—the ability to acquire information about strategies more directly than inferring them from choice behavior alone, which can often present serious econometric challenges in both the field and the lab.

During the next decade, a number of laboratory experiments explored the predictions of search theory under various scenarios, including a finite horizon (Cox and Oaxaca, 1989, 1992), variable search intensity (Harrison and Morgan, 1990), and search from unknown wage distributions (Cox and Oaxaca, 2000). Like most of these studies, Sonnemans (1998) finds that, while overall search efficiency is high (subjects stopped optimally in more than 60% of cases), subjects stop searching too early on average; risk aversion cannot fully account for this. Sonnemans elicits information about subjects’ strategies in two ways (apart from their search behavior): one is subjects’ use of an electronic information board, which gave subjects information about various aspects of their own past experience, including the number of draws, the highest bid to date, total costs and earnings to date, etc. It seems reasonable to infer that if a subject consulted this information, it was an input into her strategy. Second, after conducting a sequential search, subjects were asked to conduct another search using the strategy method: they gave explicit instructions to the computer, which conducted the search on their behalf.86 Interestingly, only 22% of such strategies were of the pure reservation wage form, and only a minority of these picked an optimal wage close to the optimal level. A significant share of such strategies had a satisficing property of stopping when total earnings exceeded a threshold.

More recent laboratory experiments on search include Carbone and Hey (2004), who study the excess sensitivity of consumption to income often noted in macroeconomic data; they find that subjects also over-react when facing similar problems in the lab and argue that agents’ limited ability to plan ahead may help explain this phenomenon. Gabaix et al. (2006) explore the ability of a specific model of limited rationality—directed cognition—to account for laboratory evidence on search problems, finding that the directed cognition model better matches the lab evidence whenever its predictions diverge from full rationality. Schunk (2009) considers instead the ability of reference point updating (in a model where subjects are assumed to care about their total net earnings—including those that are sunk—from the search) and loss-aversion to explain behavior in a laboratory search problem. As in many previous studies, on average Schunk’s subjects end their search too soon; he argues that a model in which a subset of agents use suboptimal strategies that depend in part on sunk costs accounts well for this phenomenon. Additional results in Schunk and Winter (2009) support the claim that “early stopping” is related to loss aversion, rather than, for example, simple risk aversion.

The most recent paper to address the “early stopping”/declining reservation wage phenomenon in the lab is Brown, Flinn and Schotter (forthcoming). Like other authors, they find sharply declining reservation wages over time.87 By comparing subjects’ behavior in a treatment where offers arrive at a fixed rate but with stochastic cost to one where the time between offers is random but there are no search costs, the authors are able to distinguish hypotheses (such as Schunk and Winter’s loss-aversion model) in which searchers respond to accumulating search costs from a competing scenario in which the subjective costs of searching rise sharply over time. They find that rising subjective search costs play a more important role, and argue that the behavioral factors they identify in the lab may help explain the phenomenon of declining reservation wages and/or increasing re-employment hazards in field data. Alternatively, laboratory subjects’ rapidly rising time costs may simply reflect some students’ short-term scheduling commitments outside the economics laboratory that are not relevant to real-world job searches.

In sum, laboratory experiments on search have, to date, focused almost exclusively on the “partial equilibrium” question of choices by individuals facing an exogenously given wage distribution.88 In doing so, laboratory experiments have exploited the strengths of that methodology, which include the ability to compare behavior to the exact numerical predictions of a theoretical model, and the ability to study the searchers’ strategies in a dynamic choice situation more directly than attempting to infer strategies from choice histories alone. The main findings of the literature are that, while (especially early in the search process) many subjects behave as if they pursued a theoretically optimal strategy, subjects tend to search too little overall, with falling reservation wages and rising acceptance hazards over time. In addition, a majority of subjects report that their strategies depended on factors other than the highest offer received (including total earnings in the search), and indeed selected such strategies when required to play the game using the strategy method. Playing such strategies did not cost subjects much in the search situations examined in the lab, but this does not imply that such strategies have low costs in other environments, including some that are encountered in the real world. Ongoing research continues to attempt to understand these “anomalies” in the light of different behavioral models. What remains unclear is to what extent these anomalies help shed light on job search in real labor markets. Still, the notion that, even under ideal laboratory conditions, subjects systematically choose search strategies that are suboptimal in a particular way, raises interesting hypotheses for research using field data, and for structural models of job search.

5.3 Labor markets

It is probably fair to say that the vast majority of existing labor market experiments focus on interactions between a single “firm” and “worker”, whose payoffs if they choose not to interact are exogenously set by the experimenter. That said, as mentioned in Section 2, experimenters have sometimes implemented various forms of markets in which workers compete for jobs (and/or firms compete for workers) in the lab. These papers fall into two main categories, the first of which—the “market design” papers—studies the effects of different institutional mechanisms on labor market performance. The focus here is typically on thin markets where match quality matters a lot, as in the markets for professional workers. Worker effort decisions are typically not considered. The second group of papers is primarily interested in the effects of contractual incompleteness regarding worker effort on the functioning of labor markets.

5.3.1 Market design

One highly successful set of laboratory experiments on labor markets forms part of a larger literature that is sometimes referred to as “market design” (for a recent survey and assessment, see Roth (2008)). This literature draws on a combination of economic theory, market case studies, computation, field experiments and lab experiments to compare the performance of different forms of decentralized market mechanisms and centralized clearinghouses (the latter often designed by the researcher) for specific goods. Markets that have been studied in this literature include airport landing rights (Grether et al., 1981; Rassenti et al., 1982); college admissions (Roth and Sotomayor, 1989); sorority rushes (Mongell and Roth, 1991); macroeconomic risks (Shiller, 1993); newly privatized firms in transition economies (Svejnar and Singer, 1994); postseason college football bowls (Roth and Xin, 1994); radio spectrum licenses (McMillan, 1994); space shuttle payload priorities (Ledyard et al., 2000); student housing (Chen and Sonmez, 2002); electric power (Wilson, 2002); internet auctions (Ariely et al., 2005); human kidneys (Roth et al., 2007); and admissions to New York City high schools (Abdulkadiroglu et al., 2009). Laboratory experiments play an important role in this literature, both in testing hypotheses about particular market mechanisms and in comparing the mechanisms’ performance; one lab experiment in this area that may be of particular interest to labor economists is Chen and Sonmez’s (2006) study of school choice mechanisms.

Labor markets that have been studied in the “market design” literature include those for American physicians (Haruvy et al., 2006; Avery et al., 2007). Of these labor market studies, Nalbantian and Schotter (1995), Kagel and Roth (2000), McKinney et al. (2005) and Haruvy et al. (2006) all use laboratory experiments as at least part of their research design.89 Key issues studied in these investigations include the causes of “unraveling” that is observed in some markets (e.g. for law clerks) where offers are made so early that little information is available about candidates, and the design of mechanisms that effectively ensure enough market thickness to allow for efficient matching.

Lab experiments play a number of roles in the above studies of labor markets, one of which is to isolate the effects of different institutional changes that cannot be identified in field data, because they co-vary in the field (for example, Niederle and Roth (2009) use the lab to disentangle the effects of exploding offers and binding acceptances). While this could in principle be done in a field experiment, the time, expense, and ethical barriers involved place strict limits on the amount of experimental manipulation that can be done. In contrast, after cross-validating the lab and field in a baseline case, one can quickly and cheaply compare many design permutations in the lab. Market designers are also interested in the robustness of market mechanisms to large potential swings in demand and supply (McKinney et al., 2005); in most cases these cannot be practically (or ethically) manipulated in a field experiment. A final role of lab experiments is simply to provide a level of detail on how individual actions change, for example during transition between market regimes, that is unavailable in field data (Kagel and Roth, 2000).

In sum, the literature on market design, like the arbitration literature, is another economics “success story”, where economic theory combined with a carefully chosen set of research methods including lab experiments has created institutions that improve the process of economic exchange in the real world.90 This includes some labor markets, especially for professionals—where markets are thin and match quality is arguably highly heterogeneous—and some allocation problems in education (such as school admissions) that are of considerable interest to labor economists.

5.3.2 Contractual incompleteness and labor markets

While the vast majority of laboratory experiments on principal-agent interactions incorporate labor markets in only the most minimal of senses (as noted, the experimenter typically fixes the two parties’ outside options) it is noteworthy that one of the earliest papers to demonstrate the importance of social preferences in principal-agent interactions (Fehr et al., (FKR) 1993) included an explicit labor market, and was explicitly interested in the effect of social preferences on the nature of labor market equilibrium. As already noted, this experiment modeled the labor market as a one-sided auction in which firms posted contract offers to all workers in the session. A main result was that these markets failed to clear when effort was not contractible: firms posted above-market-clearing wages because these wages elicited more effort than market-clearing wages. Firms that tried to underbid such wages did poorly due to workers’ endogenous effort responses; involuntary unemployment resulted. This result is evocative of Shapiro and Stiglitz’s (1984) well known model of involuntary unemployment, though the mechanism (reciprocity by workers) is different from the disciplinary dismissals that are central to Shapiro and Stiglitz’s model.

Since FKR 1993, the most influential paper on the effects of contractual incompleteness on the nature of market interactions is probably Brown et al. (BFF) (2004). This experimental paper is framed as a set of repeated interactions between firms and workers and generates, in our view, a set of results that may significantly influence how labor economists conceptualize labor markets. In BFF’s experiments, ten workers interacted with seven firms over fifteen trading periods. Each trading period had two stages: a market for contracts, followed by the exchange of effort for pay in contracts that had been concluded. In all cases, the market for contracts was, again, a one-sided auction: firms posted offers (consisting of a wage, a desired effort level, and the firm’s ID number), which could be accepted or rejected by workers. Once a firm’s offer was accepted by a worker, both the firm and worker were removed from the market for that trading period. Importantly, firms could make both private and public offers: private offers were only conveyed to the worker with whom the firm wanted to trade.

Under the above conditions, BFF compared two main experimental conditions: under complete contracts (C), the firm’s required effort level was automatically implemented (by the computer) if a worker accepted a contract. Under incomplete contracts (ICF), this third party enforcement of desired effort levels was absent.91 In both treatments, firms only observe the (current and past) effort levels of their “own” workers. Perhaps unsurprisingly, BFF find that under complete contracts, markets resemble the textbook case: contract offers are public, long-term relations between firms and workers are absent, trading parties seem to be indifferent to their partners’ identities, and rent sharing is driven toward the competitive equilibrium (where firms retain all the surplus). Under incomplete contracts, successful exchange is usually initiated by a generous contract offer that a worker reciprocates with a high effort level. After that, firms repeatedly seek out the same worker with a private offer. Rents are shared in these long-term bilateral relationships, which are disciplined by the threat of non-renewal. The result, rather than a classically competitive market, is a market where bilateral monopoly emerges endogenously once the employment relationship has been established, a change described eloquently by Williamson (1985) as the “fundamental transformation”.

In many ways, the labor markets that emerge under BFF’s ICF condition are much more familiar to today’s workers than a “classical” labor market: Workers invest in their reputations early in their careers by working hard; this reputation is (rationally) rewarded by their employer by continuing employment at a “good” wage; both parties’ actions are disciplined by the (rational) fear that their contract will not be renewed if they do not continue to cooperate by providing ‘fair’ levels of wages and effort. For the latter reason, BFF’s results are thus more directly supportive (than FKR 1993) of Shapiro and Stiglitz’s (1984) model where disciplinary dismissals generate unemployment. In sum, BFF (2004) show very elegantly that if contractual incompleteness plays an important role in firm-worker interactions, the correct theoretical model of labor market equilibrium may not be the competitive one we are used to, nor one of the several interesting equilibrium search models that have been developed in the past two decades (e.g., Mortensen and Pissaridies, 1994), but one in which reciprocity and bilateral monopoly play important roles.

A number of interesting variations on BFF’s (2004) design have yielded additional insights. Perhaps the most obvious such variation is replacing the excess supply of workers by an excess supply of firms (Brown et al., 2008). Interestingly, long-term employment relationships still emerge, in which firms pay workers above the going market rate and workers reciprocate with higher effort. Market performance remains high, suggesting that unemployment is not required to enforce high effort levels, though long-term relationships are less frequent than in the excess-worker case. Falk et al. (2008) consider the effects of two institutions—dismissal barriers and bonus pay—in the BFF (2004) model. Perhaps unsurprisingly, given the important disciplining role of contract renewal risk, legislated dismissal barriers lead to large reductions in equilibrium effort and market efficiency. Giving firms the option to reward high effort with bonus pay, however, offsets much of these inefficiencies; interestingly, the resulting equilibrium exhibits many fewer long-term relationships.92

So far, all the papers in this subsection have considered the effects of hidden actions (effort choices) on the functioning of labor markets. We therefore conclude by noting a number of papers that have considered the effects of hidden information (adverse selection) on market equilibrium in the laboratory as well. Interestingly, experimental studies of signaling and screening models have quite a long history, dating back at least to Miller and Plott (1985). These papers may not be familiar to labor economists since they are typically cast in the context of markets for insurance (especially in the screening case), or product quality (signaling). For a recent experimental study of both signaling and screening that is cast in a labor market context, and that reviews the earlier experimental literature, see Kübler et al. (2008). Other recent experiments that have considered the effects of hidden information (about worker ability) in labor markets are Cabrales et al. (2006) and Charness et al. (2008).

5.4 Gender, race and discrimination: Insights from the lab

The existence of discrimination and its effect on employment and wages is a major topic in labor economics. Discrimination is typically considered with respect to gender or ethnic considerations, but may also be relevant in relation to attractiveness.93 A fundamental issue is how to ameliorate concerns such as the male-female wage gap and racial disadvantage. Can policies such as affirmative action be effective or are these likely to be counter-productive? Once again, it is possible to focus specifically on these issues using laboratory techniques. We review the relevant economics literature in turn.94

5.4.1 Gender

One of the puzzles in labor economics is the gender-wage gap. Even though the provision of equal opportunities for men and women has been a priority for decades, large gender differences prevail in competitive high-ranking positions. Why do women receive less pay than men? Some of this may stem from a difference in tastes for negotiation. For example, Babcock and Laschever (2003) suggest that women are more likely to shrink from negotiation, potentially costing themselves thousands of dollars in not asking for promotions or in choosing career paths that don’t involve negotiation. Another factor may be a difference in risk aversion: Charness and Gneezy (2009) find a very consistent result across a number of experimental studies in that women are more financially risk averse than men. Related to this point, Niederle and Yestrumskas (2008) offer participants a choice of a hard or an easy task, finding gender differences in seeking challenges: Men choose the hard task about 50% more frequently than women, independent of performance level.

Stereotypical attitudes towards female workers may well be at the heart of discriminatory gender-based compensation. Schwieren (2003) considers the issue of why women receive lower pay for comparable work in a gift-exchange experiment in which each firm knows whether workers are male or female. She adapts the double-auction format from Fehr and Falk (1999), with 4 firms and 6 workers in each session. Each group of workers in a session was all-female or all-male, as was each group of firms in a session; she varied whether male workers were paired with male or female workers and vice versa. The results are striking, in that female workers receive significantly lower wages than male workers, even when women are in the role of the firm. But this doesn’t pay for firms, as a high discrepancy between the wage requested and the wage offered leads to low effort. The results suggest that stereotypes are the driving force, rather than statistical discrimination. Women also learn that they cannot successfully ask for high wages and reduce their bids over the course of a session.

The main thrust of experimental research on gender differences in performance is based on the notion that women are less inclined to compete. The first experiment to demonstrate this point is Gneezy et al. (2003), who find that women appear to be less effective than men in competitive environments, despite the fact that their performance is similar to that of males when the environment is not competitive. The experimental task was solving mazes, with six people in each session. In one treatment, people were paid two units for each maze solved; in a second treatment, where there were three men and three women in a session, the person who solved the most mazes received 12 units for each solved maze; the final treatment was identical to the second, except that there were either six men or six women in each session.95 There is a definite performance gap across gender in tournaments, even though there is no significant difference in performance across gender in the non-competitive treatment. This is driven by an increase in men’s performance in the tournament, as women’s performance does not differ across the tournament and piece-rate cases. Furthermore, the effect is more pronounced when women compete against men than when women compete against women, as men’s tournament performance does not differ according to gender composition, while women’s tournament performance in the same-sex treatment is significantly higher than in the piece-rate condition.

This result is confirmed in Gneezy and Rustichini (2004), a field experiment with school children (aged 9-10) in Israel. The performance measure was the time needed to run 40 meters. Each child first ran alone; the teacher then matched the students in pairs, with the two fastest children paired, then the next two fastest children paired, etc. The children in each pair then ran along side each other. The times in the first task were very similar for boys and girls; however, there were significant gender differences in the change in times from the first run to the second. When girls ran with other girls, the time actually increased slightly; however, the opposite effect was observed when boys ran with other girls. In mixed pairs, the reduction in time for boys was much larger than the reduction in time for girls.

Niederle and Vesterlund (2007) provide evidence that women “shy away” from competition in a task involving adding up sets of five two-digit numbers. In stage 1, participants performed this task under a non-competitive piece-rate scheme, and then performed the task in a four-person tournament in stage 2. In stage 3, people then chose whether they wished to choose the piece-rate scheme or the tournament (in the latter case, they competed against the performance of the other group members in stage 2). There are no significant differences in performance across gender, yet men select the tournament in stage 3 more than twice as frequently (73% versus 35%) as do women. This difference in rates remains significant even when differences in risk attitudes are taken into account. The authors conclude: “…the tournament entry gap is driven by men being more overconfident and by gender differences in preferences for performing in a competition. The result is that women shy away from competition and men embrace it.” (p. 1067).

Gneezy et al. (2009) perform field experiments (involving tossing a tennis ball into a bucket) in Tanzania and India. People chose whether they wished to be paid by a piece-rate scheme or to participate in a two-person tournament. The Maasai society in Tanzania is a patriarchal society while the Khasi society in India is matrilineal. The results in the patriarchal society correspond closely to the results in Western cultures, as the Maasai men choose to compete about twice as frequently as do the Maasai women. However, it is quite interesting that the comparison across gender goes in the opposite direction in the matrilineal society. Their results strongly suggest that it may be differences in culture, rather than inherent genetic traits, that drive the results observed in previous experiments.

Two other experiments consider the context of the environment in relation to gender differences in risk-taking and in choosing to compete. Booth and Nolen (2009a) conduct an experiment in which participants choose between a risky gamble and a certain one, with the expected value of the risky gamble being higher than that of the certain outcome. They compare girls who attended coed or single-sex schools. The main finding is that girls from single-sex schools are substantially more likely to choose the gamble than girls from coed schools; in fact, girls from single-sex schools choose the gamble roughly as frequently as do boys. This indicates that social learning and nurture may well be the source of the gender differences found in previous studies. Booth and Nolen (2009b) consider whether girls from single-sex schools differ from girls from coed schools in terms of willingness to compete. They find substantial differences, with girls from single-sex schools more likely to choose competition and behaving more like boys with respect to competitiveness.

5.4.2 Minorities

Discrimination occurs not only with respect to gender, but also with respect to ethnic background. As it is considerably more difficult to arrange experiments in which ethnic background is systematically varied, there are fewer studies in this area.

Fershtman and Gneezy (2001) consider discrimination in Israeli society between Ashkenazic Jews and Eastern Jews; the former tend to be wealthier and better educated. Three different experimental games were used in their study. First, in the investment (“trust”) game, three times as much (17.16 versus 5.62) was sent to Ashkenazic male responders as to Eastern male responders; this pattern was observed for both male Ashkenazic and Eastern first-movers (in fact, this discrimination was only observed for males). However, there was no significant difference in the amounts returned by Ashkenazic and Eastern responders. Since first-mover behavior could reflect preferences per se rather than trust, a dictator-game control was also conducted, with the amount transferred to the recipient tripled, as in the investment game. Here there is no difference (5.6 versus 5.1) in the amounts sent to male Ashkenazic and Eastern recipients by male dictators, indicating that there is no per se taste for discrimination, but rather that the investment game results were driven by (mistaken) beliefs about the expected returns from each ethnic group. Finally, an ultimatum game was conducted to test for the stereotype that Eastern Jews are driven more by a sense of “honor” and so would be more likely to reject small proposals. In fact, Eastern male responders received significantly higher proposals (8.4 versus 5.9) than did Ashkenazic male responders, even though rejection rates for lopsided proposals were nearly the same for both groups. Overall, the observed discrimination in this paper appears to reflect stereotypes rather than rational statistical discrimination.

Fershtman et al. (2005) attempt to distinguish between discrimination against people and “nepotism” in favor of one’s own group. At issue is the notion of anonymity rules, which forbid disclosure of group affiliation or background. Using the investment game, they compare behavior when group identity is fully observable and when it is not. The paper considers two different societies: Belgian (Walloons versus Flemish) and Israeli (ultra-orthodox religious versus secular). Belgian society shows evidence of discrimination, as both Walloons and Flemish sent much more to the responder when he or she was of the same background as the first mover than when the responder was of the other background (1200 versus 745 and 1009 versus 536, respectively). On the other hand, transfers made to anonymous responders were about the same as transfers to own-group responders for both Walloon and Flemish first-movers. However, a very different pattern was observed in Israeli society. In this case, ultra-orthodox religious Jews favor members of their own group, but send similar amounts to both secular Jews and anonymous responders.

5.4.3 Beauty

Does one’s level of attractiveness matter in terms of hiring practices and behavior in the workplace? Many people feel that good-looking people are highly advantaged and that looks are essential for being hired in some occupations (e.g. pharmaceutical representatives selling to physicians). Job applicants are routinely counseled to look their best for job interviews. Some recent experimental studies have tested this issue in the laboratory.

Mobius and Rosenblat (2006) investigate the “beauty premium” in an experimental labor market in which firms choose wages for workers in a real-effort task involving solving mazes. Physical attractiveness is found to be uncorrelated with skill in this task. The experimental design varies the degree of oral and visual interaction between firms and workers (and also elicits worker confidence). In the baseline, the firm only observes the “resume” of the worker, which includes the labor-market characteristics of the worker; in the visual treatment, the firm also sees a photograph of the worker; in the oral treatment, the firm sees the resume and also has a telephone conversation with the worker; in the face-to-face treatment, this conversation is face-to-face. They find a substantial beauty premium, which they decompose into three transmission channels: Physically attractive workers are more confident and higher confidence increases wages, these workers are also (incorrectly) considered to be more capable by firms, and these workers also have better oral skills that raise their wages.

Wilson and Eckel (2006) also investigate the beauty premium, using the investment game and photographs. They find a modest beauty premium, in that the average amount sent to an “unattractive” (“attractive”) counterpart was $4.64 ($4.98); attractive trustees appear to reciprocate this trust. On the other hand, there is also a “beauty penalty” for attractive first movers, as responders return 35% (30%) of the amounts sent by “unattractive” (“attractive”) first movers. It appears that this is driven by disappointed expectations, as responders withhold repayment in this case. Furthermore, responders expect more from attractive first movers, so their expectations are unmet more frequently and so this withholding is exacerbated when the first mover who disappointed the responder is attractive.

Andreoni and Petrie (2008) study the beauty premium in a public-goods game. When people are not told the contributions of others, there is indeed a beauty premium: attractive people earn 7% more than people of intermediate attractiveness and 12% more than unattractive people. In another treatment, participants are told the individual contributions of each other player. In this case, the beauty premium becomes a beauty penalty, as it appears (as in Wilson and Eckel) that people expect (hope for?) more from attractive people. As these expectations are more likely to be unmet, attractive people seem relatively more selfish, leading to decreased contributions from other participants. There are also some gender effects, as men make larger contributions and this appears to “lead” other people to contribute more in subsequent periods.

5.4.4 Affirmative action

A thorny policy issue is that of affirmative action, whereby some group that is considered to be generally disadvantaged is given an immediate advantage. Emotions run high on this topic, and “reverse discrimination” lawsuits are not uncommon. What are the effects of affirmative action? Clearly this helps disadvantaged people (at least in the short run), but it may well be detrimental with respect to overall performance. Some recent laboratory experiments have investigated this issue in controlled settings.

Schotter and Weigelt (1992) find, in a two-person tournament setting, that the effects of affirmative action depend on the severity of the cost disadvantage for the non-minority group. When the tournament was “unfair”, one of these people had to win by a certain amount and/or was assigned a cost function greater than that for the other person. Affirmative action is found to discourage disadvantaged agents from “dropping out”, as was observed without affirmative action. Nevertheless, overall the effect of affirmative action on output appears to depend on the degree of disadvantage. When this is large, then affirmative-action programs did improve profits for the “tournament administrators”; however, this did not occur when the cost disadvantage was less severe.

Corns and Schotter (1999) provide an “existence proof” that there exist parameters under which price-preference auctions (often used to promote minority representation in government contracting) can increase minority representation while being cost effective; however, there is a decrease in cost effectiveness if the degree of price preference is too large. The experimental design involves high-cost firms (simulating minority firms) that receive either a 0%, 5%, 10%, or 15% price preference. There were six participants in each session, with costs drawn from a uniform distribution of [100, 200] for the four low-cost firms and [110, 220] for the two high-cost firms. The frequency of a high-cost firm winning the auction increased from 12% in the 0% treatment to 43% in the 15% treatment, largely in line with the theoretical predictions. The average observed price was 121.24 in the 0% condition, 119.29 in the 5% condition, 122.84 in the 10% condition, and 124.41 in the 15% condition. There is no significant difference in the distribution of drawn costs across any two price-preference treatments. Nevertheless, the results indicate that it is possible to use price preferences to increase representation of “minority” firms without increasing the overall cost or the average observed price.

Niederle et al. (2008) follow up the Niederle and Vesterlund (2007) study by examining how affirmative action affects competitive entry and performance. If women shy away from competition, it may be advantageous to institute an affirmative-action policy under which women are favored in competitions. Participants are formed into groups of six, including three men and three women, and add up a series of five two-digit numbers; in one task, they are paid $0.50 for each correct answer, while in another task the two best performers are paid $1.50 for each correct answer. In the third task, people choose either the piece-rate or the tournament payment scheme. Next there is an affirmative-action task, in which the two winners in a tournament are the highest-performing woman and the highest performer of the other people in the group. The results indicate that when women guaranteed equal representation among winners, more women and fewer men enter competitions. Results also suggest that affirmative action need not be costly, but may be sensitive to parameters, as in Corns and Schotter (1999). Measured beliefs about one’s rank and attitudes concerning competition are affected by the affirmative-action policy. While affirmative action may result in reverse discrimination towards men, the authors claim: “…this need not be the outcome when competitive entry is not payoff maximizing. The response in entry implies that it may not be necessary to lower the performance requirement for women to achieve a more diverse set of winners”. Thus, affirmative-action policies may potentially be beneficial.

Balafoutas and Sutter (2009) investigate three alternative policy interventions that should promote women in competitive environments: Preferential Treatment, Repetition of the Tournament, and Affirmative Action. These environments are compared with respect to the willingness of men and women to enter a tournament (addition exercises) and the impact on both tournament efficiency (selecting the most qualified people to be the winners) and post-tournament efficiency when groups then participate in a minimum-effort coordination game (the minimum effort translates into the efficiency level). Affirmative-action policy interventions lead to significantly higher entrance rates of women, except for in the Repetition treatment. Tournament efficiency does not appear to deteriorate when these policies are introduced; in fact, a “small push” (giving women credit for one additional solved exercise) leads to the highest efficiency. Furthermore, efficiency in a post-tournament teamwork-task is slightly higher in the treatments with successful policy interventions; thus, to the extent that this experimental game serves as a proxy for dynamic considerations, cooperation is not harmed by the introduction of affirmative action.

Calsamiglia et al. (2009) consider affirmative action in two-player tournaments involving solving mini-Sudoku puzzles. Elementary school children at two otherwise-identical private schools in Spain were paired, with the person solving more (net) puzzles winning the tournament. In one of these schools, the students had experience with these Sudoku puzzles. These policies included adding some number of points to the disadvantaged students total and multiplying the number of solved puzzles by disadvantaged students by some factor greater than one. Their results indicate that performance was not reduced for either advantaged or disadvantaged subjects and that it was in fact enhanced. Additionally, while affirmative action balanced the proportion of disadvantaged individuals winning their respective tournament, the average performance of the pool of winners only decreased slightly.

6 Conclusions

Laboratory experiments have been used to study almost every aspect of labor economics, ranging from the effects of final-offer arbitration in public sector labor disputes to the causes of gender wage differentials. This vast literature includes a number of noteworthy “success stories”, including the use of laboratory experiments as testing grounds for proposed institutional innovations—in particular, matching mechanisms for professional workers, and arbitration systems in public sector union bargaining—that are subsequently used to organize the actual pricing and exchange of labor.

We see laboratory experiments as a useful tool among several at the labor economist’s disposal; their key strengths include the ability to control conditions and confounding factors affecting a possible causal relationship more tightly than any other method, the ability to replicate results quickly and easily with newly collected data, the unique ease with which they can test the exact quantitative predictions of simple game-theoretic models, the ability to cleanly study behavior in situations where precise theoretical predictions are absent (as in the case of multiple equilibria), their low cost, the ability to more readily study phenomena that are hidden in the field because they are illegal or disapproved of (such as sabotage, discrimination, and spite), and the ability to elicit data relatively easily on such central game-theoretic concepts as beliefs and strategies that are often difficult to infer from observed behavior alone.

Key objections that have been raised to lab experiments in economics include the artificiality of the experimental context in general and the labor “task” specifically, low stakes, short duration, and the effects of experimenter scrutiny. All of these are important issues, which experimenters should (and typically do) consider seriously. As we have argued in detail in this review, however, none of these concerns—with the possible exception of duration—are insurmountable in the lab, and in general these disadvantages need to be weighed against the lab’s potential benefits, enumerated above. In many cases a combination of methods, or a hybrid method—such as the artefactual field experiments and framed field experiments described by List (2009)—may be the best approach.

Perhaps the most widespread concern with lab experiments is the representativeness of the laboratory population relative to the field population of interest; this concern seems particularly acute when discussing lab results that are hard to explain without some recourse to “non-standard” preferences. As we have noted, this issue can be addressed in a number of ways, including conducting lab experiments directly on the field population of interest and studying the selection process itself (for example, selection into competitive versus co-operative work environments, or into situations where altruism might be expected or not) in the lab.

Greater clarity on “representativeness” can, in our opinion, be also achieved if future investigators are more precise about which field environment their experiment is intended to represent. Clearly, if the intended field population is highly specific (for example, new registrants for unemployment insurance in Illinois), and the researcher’s main interest is in the magnitude of the behavioral response to a contemplated policy change affecting this population, the ideal research design is almost certainly what List (2009) calls a ‘natural field experiment’ on that population. However, when searching for underlying principles of behavior, derived from a specific theoretical model of strategic interaction and/or social preferences that one hopes might apply to a broader field population (for example, all college-educated employees, or even all humans), a lab experiment on a random sample from a broader group may be more useful. In all cases, the research question should guide the choice of method, and the investigator should specify the population on which the experiment is intended to shed light.

Probably the most frequent application of lab experiments in labor economics has been to principal-agent interactions between workers and firms. While many predictions of what one might call “traditional” principal-agent theory have been confirmed in the lab—for example, in most cases effort increases when marginal work incentives are raised, contributions to team production fall with the number of team members, and ratchet effects disappear when ex post labor market competition is intensified—lab experiments have also identified a significant number of robust departures from rational, selfish behavior in principal-agent interactions. As already noted, a catch-all phrase for the modifications to traditional preference structures that have been proposed to explain these “anomalies” is “social preferences”; the discovery and mapping of social preferences is probably the most important contribution of lab experiments to principal-agent analysis, and to labor economics more generally.96

That said, much remains unknown about social preferences. On the theoretical side, one area in which progress is needed is in the development of social-preference models that successfully apply to large, multi-worker workplaces. Most current social-preference models have been developed to explain behavior in the lab. While social preferences might explain behavior in these situations, it is remains unclear how these models are best generalized to larger firms with many workers and several hierarchical levels. On the empirical side, social preferences seem capable of changing their shape and form considerably between different contexts, as well as between the lab and the field. Empirical work that sheds light on which social preferences (including, among others, inequity aversion, reciprocity, guilt, spite, jealousy and simple altruism) come into play when will be of great value.

While much remains to be learned about the effects of compensation systems on worker behavior within firms, it is perhaps worth gauging our progress by considering the state of knowledge on this topic some 15 years ago in the words of some of the main contributors (emphasis added):

“There is a large and growing interest in the economic theory of the internal workings of firms. However, this literature is based on very little data and limited stylized facts.”

(Baker et al., 1994a)

“For a time there was considerable excitement about implicit contract theory …That literature soon fell out of favor, but in its place came more refined information economic analyses that viewed wage contracts as optimal responses to asymmetries in information between employees and firms. With this, the logical possibilities for explaining wage behavior grew dramatically. Today’s large variety of models and modeling options has put theory well ahead of observation”.

(Baker et al., 1994b).

And finally, from an article titled “Internal Labor Markets: Too Many Theories, Too Few Facts”:

“With the advent of information economics and contract theory, models of internal labor markets—or at least selected features of these markets—have begun to emerge. The objective of these theories is to show that internal-labor-market outcomes can be construed as second-best solutions to contracting problems under incomplete information. …At this point, there is hardly any feature of internal labor markets that cannot be given some logical explanation using the right combination of uncertainty, asymmetric information and opportunism.

(Baker and Holmstrom, 1995)

Thus, just 15 years ago, research on incentives in organizations consisted to a disappointingly large extent of (a) identifying a “paradoxical” feature of some internal labor market (for example, academic tenure, or pay raises based purely on seniority), then (b) crafting a theoretical model showing how that feature was in fact an efficient response to some contracting problem. Most analyses stopped there.

Today, thanks both to a laboratory literature that began in the mid-1990s and a more recent surge in field experiments, we now face a cornucopia (some might say, an unmanageable deluge) of facts about agents’ and principals’ behavior in the above models. Indeed, after reviewing this literature, it is tempting to conclude that we now have “Too Many Facts, Too Few Theories”. Certainly, an important part of the road ahead is the development of models (that can account for the robust departures from the predictions of ‘traditional’ principal-agent models) both in the lab and in the field. In our view, a variety of empirical tools including both lab and field experiments, natural experiments, econometric studies, and calibration of structural models will provide the necessary empirical discipline in this next phase of research on one of the most basic issues in labor markets: the exchange of effort for pay within firms.

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1 Furthermore, Falk and Fehr (2003) point out that other factors such as communication, peer pressure, and whether the interaction is one-shot or repeated may well affect behavior and are unlikely to be known to a researcher using field data.

2 See Charness (2010) for more discussion regarding replicability.

3 Note that in addition to being low-cost, undergraduate participants also tend to be fairly intelligent (in fact, evidence suggests that the undergraduates who participate in experiments are more capable than the average); this is a nice combination for the experimenter.

4 In the latter study, a mobile laboratory was taken to the workplaces of two French firms, where older (over the age of 50) and younger workers (under the age of 30) were tested in three experimental environments.

5 A similar comment applies to “natural experiment” studies of the effects of changes in compensation policy, which have focused on stadium vendors (Oettinger, 1999), Continental Airlines employees (Knez and Simester, 2001), textile workers (Hamilton et al., 2003), steel minimill workers (Boning et al., 2007), and taxi drivers (Crawford and Meng, 2008), among others.

6 It is also worth mentioning that Bewley (1999) finds evidence of fairness considerations in his interviews of business people, Krueger and Mas (2004) find evidence of negative reciprocity amongst Firestone workers and Mas (2008) shows that police performance suffers after unfavorable arbitration decisions.

7 They also observe that “reanalysis of the original Hawthorne data [see Jones, 1992] shows that no Hawthorne effect was present in the Hawthorne study” (p. 537).

8 A comprehensive study by Camerer and Hogarth (1999) indicates that in many cases whether or not a laboratory participant is given financial incentives has little effect on behavior.

9 We are indebted to Keith Murnighan for this information. For more detail, see the discussion in Murninghan (2008a).

10 They state: “This control allows for the testing of precise predictions derived from game-theoretic models” (p. 636).

11 Indeed, Levitt et al. (2009) discuss some of the limitations of field experiments, such as the difficulties with some forms of replication, and the fact that “they sometimes cannot be used to distinguish between alternative theories because the experimenter exerts less control than in the lab” (p. 1414).

12 Holt (2007) points out that field experiments are particularly valuable when social context is critically important. However, he cautions: Although field experiments can induce a more realistic social context and environment, the cost is often a partial loss of control over incentives, over measurement of behavior, or over the ability to replicate under identical conditions” (p. 14). Regarding the independence of observations, he writes: “To the extent that social context and target demographics are important in a field experiment, each field experiment is in some sense like a data point that is specific to that combination of subjects and context unless appropriate random selection of subjects is employed” (p. 14).

13 Charness et al. (2007) provide one example, as they find that the presence of an audience of peers with a common interest can lead to more aggressive behavior in experimental games.

14 Echoing the discussion on Section 1.2, the standard policy in the experimental laboratory at the University of Amsterdam is to separate the payment of experimental participants from any observation of behavior, by having non-experimenters place payments in envelopes that are then passed out by the experimenter. Given that this is standard procedure, experienced participants know to expect this and are not particularly suspicious about it being utilized in any specific experiment. List et al. (2004) use another approach, in which a “randomized response” means that the experimenter cannot ascertain whether a participant made a pro-social choice.

15 Both authors of this chapter have also used both methods in their research.

16 An example from the games in Charness and Rabin (2002) may provide a useful illustration. In one treatment, a participant unilaterally made a choice between (Other, Own) payoffs of (750, 375) or (400, 400); in a second treatment, 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). In the first treatment, roughly half of the population chose to sacrifice 25 units, selecting (750, 375); however, only 10% did so in the second treatment. The comparison of the two treatments qualitatively shows a strong effect, which indicates that a form of negative reciprocity is present. Nevertheless one would be naive to conclude that these quantitative levels would also be observed in the outside world.

17 Regarding the latter case, one example comes from industry. Hewlett–Packard was interested in the consequences of changing their minimum-advertised-price policy (see Charness and Chen, 2002). Rather than use a costly test market, laboratory experiments were conducted; it this situation, it was critical to match their retailer environment as closely as possible. As another example, if firms in the experiment are losing money, it is difficult to argue that the observed behavior will persist over time in the field.

18 However, it is quite possible that people bring their own (uncontrolled) personal experience or habits with them to the experiment, so that a neutral context may not achieved the desired effect.

19 However, note that Palacios-Huertas and Volij (2008) find that professional soccer players (at least in the aggregate) play a mixed strategy that corresponds remarkably closely to the equilibrium predictions in the O’Neill game, where there are four choices for each of two players, but there is no pure-strategy equilibrium.

20 Specific approaches include rolling of a die after each period with some continuation rule or having a pre-set ending that is not divulged to the participants.

21 A detail that is sometimes overlooked in designs with re-matching is that, in practice, many re-matching schemes incorporate a positive probability that an agent will be re-matched with the same person at a later point in the session. This can be important in calculating expected equilibrium behavior. Sometimes investigators choose to eliminate this possibility (thus reducing the number of rounds of data that can be collected), or to minimize it by informing subjects that they will never be matched with the same partner in the next period.

22 One can systematically vary the sequence to test for sequencing effects.

23 A related issue is the distinction between hours of work and effort. While “traditional” labor supply theory is framed as a worker’s choice of hours at a fixed hourly wage, principal-agent theory and virtually all labor experiments are framed as a choice of effort. While in many ways the choices are isomorphic, there are some important distinctions; caution is required when generalizing “effort” results to choices of hours worked. See for example Dickinson (1999).

24 Another design option is to use automated agents when there is really only one sensible response for some types of agent. In some cases this can substantially increase the amount of data that can be collected. See for example Charness et al. (forthcoming).

25 For an alternative and complementary review of some of these issues, see Camerer and Weber (forthcoming).

26 Battalio et al.’s work, in turn, has roots in an extensive literature in experimental psychology on the effects of reward structures and amounts on animal behavior. See for example Ferster and Skinner (1957), Barofsky and Hurwitz (1968) and Kelsey and Allison (1976). These studies commonly find backward-bending labor supply curves as the reinforcement rate is increased, but do not relate their results to a theory of utility-maximization, or consider the effects of income-compensated changes in “wages”.

27 Other labor economics questions addressed by these researchers in the lab include the “welfare trap” (do high levels of unearned income in past treatments reduce current labor supply?), and the “cycle of poverty”: does deprivation raise animal subjects’ discount rates (i.e. their preference for a small immediate reward over a larger delayed one), thereby leading to more deprivation in the future? Interestingly, little evidence of either effect was found (Kagel et al., 1995).

28 As discussed in Section 2.2, laboratory principal-agent experiments with human subjects can be divided into those where subjects are paid to perform an actual task (“real-effort”) and those where effort decisions are represented by the choice of a decision number that imposes increasing marginal financial costs on the agent (“chosen effort”). Bruggen and Strobel (2007) find little difference between the two methods in a simple gift-exchange labor market game.

29 It may be worth noting that backward-bending labor supply in the context of a laboratory experiment is actually somewhat of a puzzle for humans, since, at least in the classic intertemporal labor supply model, implausibly severe liquidity constraints would be required to generate such effects for payments of the size and duration that are typical for lab experiments.

30 In Sillamaa’s experiments, workers decoded numerical codes into letters; in Dickinson’s workers repeatedly typed paragraphs, with a penalty for mistakes. Sprinkle (2000) considers the effect of strengthening incentives for a considerably more complex task, spanning multiple periods and requiring belief revision and judgment calls. Here, incentives again increase effort, but only after the subjects had been exposed to considerable feedback and experience.

31 Psychologists provided compelling evidence that monetary incentives can crowd out intrinsic motivation long before Gneezy and Rustichini’s paper (see Deci et al., 1999 for a meta-analysis). See also Frey and Oberholzer-Gee (1997) for an earlier economic analysis, though not in the domain of labor economics.

32 Dohmen and Falk (2006) examine laboratory subjects’ voluntary self selection into several types of contracts (fixed pay, piece rate, tournament or revenue-sharing scheme) according to subjects’ risk attitudes, overconfidence, social preferences, gender and personality. They find that most of the extra output generated by all three variable pay schemes is due to the selection of abler workers into them. Burks et al. (2009) provide additional evidence on the importance of selection into pay-for-performance by conducting a context-rich prisoner’s dilemma lab experiment on bicycle messengers who are employed in three types of firms: firms using pay for performance, those using hourly wages, or workers’ cooperatives. Workers in the first type of firms were the least cooperative in prisoners’ dilemma games. Using data from cities where bicycle messengers were not able to choose among these firm types, the authors argue, however, that these differences are not due to selection, but due to workers’ (rapidly) adopting the norms governing cooperation in their workplace.

33 Our section on the role of reciprocity and social preferences in principal-agent interactions also considers the closely-related role of communication, especially its ability to foster trust, cooperation and guilt. See for example Charness and Dufwenberg (2006, forthcoming).

34 See also Bartling and Fischbacher (2008) and Coffman (2009).

35 Another possible reference point in a bilateral relationship is the terms of an ex-ante competitively negotiated contract between the parties. Experimental evidence of these effects is provided in Fehr et al. (2008), though not in a labor or principal-agent context.

36 Note that the agent’s actual effort, image, is observed by the principal ex post in all contracts, whether the agent is “audited” or not; auditing simply means that a punishment can be enforced if effort is short of the requirement.

37 Note that the class of bonus contracts includes the “trust” contract as a special case, with bonus of zero.

38 Agents try to attain a maximum value of a non-decreasing function by costly sequential search.

39 Ellingsen and Johannesson (2008) provide a theoretical model of crowding out in which some audiences are more worth impressing than others. In their model, the principal’s choice of monetary incentives signals that he/she is not worth impressing. See Bénabou and Tirole (2003, 2006) for closely related models.

40 Of course, the voluntary bonuses studied by Fehr et al. (2007a) are nonlinear ex post, but here we focus on enforceable reward schedules, announced ex ante, that contain discrete jumps. Incidentally, Fehr et al. (2007b) adds an enforceable fine to Fehr et al. (2007a), but finds it is rarely selected by principals and has little effect on agents’ effort.

41 Mas and Moretti (2009) also detect small effects on productivity of being observed by a more productive worker, in a setting where workers were not paid for performance.

42 Maximiano et al. (2006) also examine gift exchange in multi-worker firms, but in their treatment all workers are equally productive and receive the same wage by design. Güth et al. (2001) consider a situation in which the principal can offer a menu of contracts to two independent agents with different productivities. As in Charness and Kuhn, public observability of the co-worker’s contract induces the employer to compress compensation schemes.

43 This variance result appears quite robust. See, for example, Van Dijk et al. (2001) for a replication.

44 Falk et al. (2008) also focus on the behavior of principals in a setting where agents can invest in sabotage. They find that both sabotage and loss-aversion among agents compromise the ability of large prize differentials to increase effort levels; principals respond to this by choosing wage compression.

45 Of course, while zero effort by all agents is probably a good sign of collusion, the question of how one would identify collusive behavior in a tournament is an interesting one. Clearly, individual effort can be below the privately-optimal level for reasons other than collusion.

46 In an interesting field experiment, Bandiera et al. (2005) found that, when engaged in a tournament with their friends, fruit pickers moderated their output (relative to a piece rate) in apparent response to the negative externality their effort imposed on those co-workers. Since this behavior occurs only when workers can monitor others and be monitored, it seems more likely to be motivated by collusion than altruism.

47 Eriksson et al.’s finding that feedback tends to reduce the quality of the low-performers’ work is however evocative of the greater risks taken by agents who find themselves running behind, discussed earlier in this section.

48 In Gill and Prowse’s context (where the agents select their outputs sequentially, and the interim feedback consists of informing the second agent about the first agent’s performance), being “behind” simply corresponds to a high level of performance by the first agent.

49 An additional question concerning interim feedback involves the principal’s ex post incentives to reveal this information honestly; for example, it may be in the principal’s interest to report that the race is closer than it really is. Both Gürtler and Harbring (2007) and Ederer and Fehr (2007) consider this question; they do find evidence that the gap is underreported, though the level of underreporting is lower than predicted by a model without aversion to lying.

50 The team production problem is, however, closely related to the problem of voluntary contributions to a public good, which has a longer experimental history.

51 Nalbantian and Schotter also implement a scheme where the principal can observe an individual’s effort at a cost. Not surprisingly, they find that “monitoring works, but is costly”. Van Dijk et al. (2001) implement individual, team, and tournament based compensation in a real-effort experiment. While some free riding occurred in teams, overall effort levels were the same under individual and team payment, since free-riding was counteracted by many subjects providing more effort than in case of individual pay.

52 Eckel and Grossman (2005) consider a classic VCM problem, framed as a team production problem, with no modifications to the incentive structure at all. Instead, they manipulate the amount of anonymity, contact and “identity” of team members, for example by having the members perform a cooperative task before the experiment. They find some positive effects of increased contact among team members, though the two interventions that yielded the greatest gains also offered extra financial incentives relative to the base case (wages for teamwork, and a monetary bonus to the team with the highest total output).

53 Bornstein et al. (2002) find that this co-ordination is somewhat mitigated when intergroup competition is introduced—specifically, two groups compete for a prize received by the group with higher minimum. The members of the losing group were paid nothing. Sutter and Strassmair (2009) introduce communication into experimental tournaments between teams. In their experiment, communication within teams increases efforts (by facilitating coordination) while communication between teams reduces effort (by facilitating collusion).

54 In the opposite case of substitutability in production, the only reward scheme that induces efficiency as a unique Nash equilibrium is the symmetric one that treats all workers alike. Thus, Winter’s model provides interesting predictions for the relationship between the group’s production technology and the efficient compensation policy.

55 Note that tournaments do not face this problem, since the principal’s total compensation bill does not depend on which worker wins; indeed this has been suggested as a possible advantage of tournament-based compensation (Carmichael, 1983a,b).

56 There is, of course, a sense in which tournaments in which agents can allocate their effort between productive activities and sabotage are a multi-task situation. We discuss these in the section on tournaments.

57 See for example Baker et al. (1994) for a more explicit argument in favor of subjective performance evaluation.

58 Field and econometric studies are also rare. Slade (1996) studies multitasking in contracts between oil companies and gasoline stations; more recently Griffith and Neely (2009) consider multitask incentives in a UK distribution firm.

59 Carmichael and MacLeod (2000) interpret some historical evidence in light of the ratchet effect.

60 Akerlof (1976) presents a signaling model in which agents signal a low cost of effort by working harder; separating equilibria in which (almost) all workers provide socially excessive effort exist. For a more recent career concerns model with similar properties, see Acemoglu et al. (2008). It may also be worth noting that labor economists have developed a variety of models in which workers’ abilities are gradually revealed to markets over time (see for example Bernhardt and Scoones, 1993, and Altonji and Pierret, 2001). Since our focus in this section is on principal-agent interactions, we consider only the subset of those models which, like the career-concerns model, involve an effort decision by workers.

61 For a review of the hold-up literature in the context of labor markets, see Malcomson (1997).

62 Sloof et al. (2007) consider the effects of keeping the level of one’s specific investment secret on the hold up problem: the simple theoretical intuition is that if the other party does not know how much one has invested, they will be at an informational disadvantage in bargaining over the ex post surplus. The framing (and likely relevance) seems more appropriate to non-labor market interactions, however.

63 In their experiment, if a proposal is rejected there is another round in which the pie is substantially reduced; the person who rejected the initial offer can then make a proposal to split the smaller pie. A disadvantageous counter-offer is a proposal that, if accepted, would lead to a smaller material payoff for the second-round proposer than he or she had rejected in the initial proposal.

64 However, there are two models in the appendix of Rabin (1993) that do consider the distribution of material payoffs.

65 In the image-player case, another difference is that Bolton and Ockenfels compare the ratio of one’s material payoff to the total material payoffs, while Fehr and Schmidt consider the sum of pairwise comparisons.

66 Note that the real model is in the appendix of the paper.

67 One might wonder whether a complex model such as Charness and Rabin (2002) is needed, as the substantially more parsimonious and tractable Fehr and Schmidt (1999) model does a reasonably good job of organizing much of the observed experimental behavior. While this topic is still being debated, it seems fair to say that there are many papers that provide data that cannot be explained by distributional models without considering reciprocity. These include Kahneman et al. (1986), Blount (1995), Charness (2004), Offerman (2002), Brandts and Charness (2003), Andreoni et al. (2002), Falk et al. (2003a,b), Charness and Rabin (2002), and Charness and Levine (2007).

68 For another survey of social preferences, see Cooper and Kagel (in press).

69 The language used in this paper involves buyers and sellers, prices and quality; however, the paper emphasizes the labor interpretation, so we adopt the terminology used in almost all subsequent papers.

70 They state on p. 1026: “Frankly, we did not believe that the gift exchange model would survive the more realistic multiple workers per employer design. We were wrong”.

71 We hasten to add that, despite the large number of papers that find a strong positive relationship between wage and effort, gift exchange is not robust to all experimental conditions. Hannan et al. (2002) find little gift exchange with undergraduates; on the other hand, MBA students provide effort responses similar to those in most gift-exchange studies. Charness et al. (2004) find that when a complete payoff table is provided in the experimental instructions, workers choose substantially less effort compared to a treatment in which participants had only the information needed to compute their payoffs.

72 In a related paper, Meidinger et al. (2003) examine team heterogeneity and productivity. There is considerable free riding as each agent is greatly influenced by his or her teammate’s behavior. On the other hand, workers are better able to cooperate when the team is homogeneous.

73 A further example from Charness and Rabin (2002) provides evidence of negative reciprocity. In ultimatum-game experiments, a high proportion of responders reject offers that would give them only 20% of the pie. However, when we offered 36 participants a choice between (Other, Own) payoffs of (800, 200) or (0, 0), exactly zero chose (0, 0). Thus, distributional considerations are insufficient to explain rejections in the ultimatum game, so that negative reciprocity would appear to be the driving force.

74 Once again, we order papers by the date they were written (in this case, 1996), rather than the publication date.

75 In the standard version of this game, both a first mover and a responder are endowed with 10 units. The first mover can pass up to 10 units, with the amount passed tripled by the experimenter and then received by the responder. The responder can then pass back any number of units (not tripled).

76 In a related study, Kube et al. (2006a) conduct a controlled field experiment that tests the extent to which cash and non-monetary gifts affect workers’ productivity. The main result is that a non-monetary gift leads to a significant and substantial increase in workers’ productivity, while a cash gift of the same value is ineffective.

77 Charness and Villeval (2009) also find that students are less cooperative than young workers, older workers, and retirees.

78 In fact, there is a 5/6 chance that these payoffs are (12, 10) and a 1/6 chance that they are (0, 10). In this way, the principal cannot be certain of the agent’s choice when a zero payoff is received.

79 Summaries of these theoretical developments are available in Binmore and Dasgupta (1987), and in Osborne and Rubinstein (1990), as well as many other sources.

80 Another important and promising application of bargaining experiments of interest to labor economists is to gender differences in labor market outcomes (e.g. Eckel and Grossman, 1997; Babcock and Laschever, 2003).

81 There is also a literature that models the wage and employment outcomes of union-firm bargaining, and attempts to test for the appropriate model of the bargaining process. For reviews, see Farber (1987) and Kuhn (1998); we are not aware of any laboratory experiments in this area.

82 Non-experimental studies of strikes motivated by asymmetric information bargaining models include Card (1990), Cramton and Tracy (1992), Gu and Kuhn (1998) and Kuhn and Gu (1999).

83 Labor economists have also been active in the use of field data to study the effects of arbitration; see for example Currie and McConnell (1991), who studied dispute rates for public employees across Canadian provinces with different arbitration laws.

84 For a more recent example of field experiments on job search and UI, see Dolton and O’Neill (2002).

85 As in the case of bargaining, psychologists conducted laboratory experiments on search long before economists did. See for example Rapoport and Tversky (1966, 1970) and Kahan et al. (1967).

86 See also Sonnemans (2000) for a more direct comparison of search decisions under the strategy method versus decisions made “by hand”.

87 Brown et al. elicit subjects’ reservation wages directly in advance of every offer by asking the subjects to name such a wage; a computer then automatically accepts all offers above this and declines the rest.

88 For an exception in the context of consumer search, see Abrams et al. (2000).

89 Recent examples of laboratory experiments with applications to two-sided matching markets include Niederle and Roth (2009) and Niederle et al. (2009).

90 See Roth (2002) for a review of methodological issues in the market design literature.

91 This condition is labeled ICF because workers’ ID numbers were fixed throughout the entire session (as they were in the C condition). This allowed firms to target their offers to specific workers (presumably to a worker who had provided high effort in the past), and distinguishes it from an “ICR” treatment where contracts were incomplete but workers’ identities could not be tracked during a session.

92 Two other papers that insert new variations into repeated experimental labor markets similar to BFF(2004) are Healy (2007) and Schram et al. (2007). Healy considers the ability of group reputations to substitute for individual reputations; Schram, Brandts and Gerxhani ask what happens when firms can see workers’ past effort levels at other firms when bilateral contracts are negotiated.

93 Discrimination may be based on bias or due to accurate perceptions about differences in ability or other characteristics across groups. While we do not discuss this at length in this section, there is experimental evidence in this regard. For example, Fryer et al. (2005) have “green” and purple” workers with different “investment costs”. Investment improves the chance the worker does well on a pre-employment test; this is observed by the firm, who can hire either green (lower cost) or purple. Green workers were hired substantially more often.

94 There is a substantial and active laboratory literature on racial, gender and other forms of discrimination in the fields of psychology and management science; adequately summarizing this literature would go far beyond the bounds of the current review. A common research design in these papers has laboratory subjects (who in many cases are employed as recruiters in “real life”) evaluating job candidates whose race or sex is exogenously manipulated by the experimenter (see Cohen and Bunker, 1975 for a highly-cited example regarding sex, and Dovidio and Gaertner, 2000 for a more recent example regarding race). Other interesting approaches include scenario-based experiments such as Levi and Fried’s (2008) on affirmative action, and internet experiments where subjects play on-line games, interacting with avatars of different races (race is manipulated via the other player’s first name and the skin tone of the avatar) (Goodwin et al., 2010).

95 An additional treatment in which one person was chosen at random to receive 12 units per solved maze led to results quite similar to these in the first treatment.

96 Non-selfish preferences are of course not the only possible explanation of departures from predicted equilibria in effort-supply models. Others include simple limits to human cognition (especially in complex, multi-period games), and practical difficulties of coordinating on Nash equilibrium even when a unique one exists.

☆The authors thank Michael Kuhn and Loni Spilberg for excellent research assistance. While have done our utmost to identify as many lab experimental papers in labor economics as possible, omissions are inevitable given the volume of excellent recent research in this area. The authors regret all such omissions but nevertheless hope that our review provides a helpful guide to the “lab labor” literature to date.

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