Do social comparisons motivate workers? A field experiment on relative earnings, labor supply and the inhibitory effect of pay inequality

Abstract

In a field experiment where revelation of co-worker earnings and the shape of the earnings distribution are exogenously controlled, I test whether relative earnings information itself influences effective labor supply and labor supply elasticity. Piece-rate workers shown their peer earnings standing provide significantly more labor effort. However, the productivity boost from earnings disclosure disappears when inequalities in the underlying piece rate exist. By cross-randomizing net of tax piece rates, labor supply elasticity with respect to the net of tax wage is also estimated. Unlike labor level, I find this labor elasticity is unchanged by the relative standing information. Taken together, these findings have direct implications for how to best model relative status concerns in utility functions, supporting some and precluding other common ways. More speculatively, they also suggest social comparisons could be strategically used to grow firm output or the tax base, and, that underlying inequalities in compensation schemes inhibit the ability of social comparisons to incentivize work.

1. Introduction

Throughout the economy, we observe firms that publicly disclose information about the earnings of their employees. Earnings transparency exists for firms in a wide variety of industries encompassing many types of workers, from salespeople to software developers to upper management at Fortune 500 companies.¹ Many governments similarly disclose the earnings information of workers.² The rationales for such disclosure vary.³ This paper considers one novel rationale, namely, that peer earnings disclosure may be justified as a matter of firm or government policy on the grounds that it positively affects worker labor supply. Additionally, it investigates the interplay between earnings transparency and pay inequality, finding that co-worker earnings disclosure does motivate increased output among workers when there is parity in the pay received for equivalent performance. When there is pay inequality, however, the labor-generating features of such social comparisons are lost. By testing the effect of earnings disclosure not only on labor output but also on the elasticity of labor supply, and for different distributions of peer earnings, the present work also sheds new light on how to best model relative standing concerns, rejecting some common parameterizations of utility functions that include status concerns, and, supporting others.

Dating back to Duesenberry (1949); Veblen (1899), and, later Frank (1985), economists have been generally interested in how concern over relative standing may enter directly into individual preferences, and, thereby affect behavior, contrary to standard assumptions that only absolute levels of goods matter to decision-makers. Much of the early literature was theoretical, focusing, for instance, on how optimal income tax rates change when introducing preferences over relative position in earnings or consumption (Allgood, 2006; Beath and Fitzroy, 2007; Boskin & Sheshinski, 1978; Frank, 1985; Ireland, 1998, 2001 Oswald, 1983). In recent decades, there has been growth in work demonstrating that social comparisons do in fact matter empirically. For example, social comparisons have been shown to affect job satisfaction and job search intention (Card et al., 2012), electricity consumption (Allcott, 2011; Allcott & Rogers, 2014), choices over lotteries and costless charitable giving (Kuziemko et al., 2014), and self-reports of happiness (Luttmer, 2005; Perez-Truglia, 2020).

While such outcomes are important to firms and governments looking to maximize profit and tax revenue, respectively, the decision to adopt a policy disclosing peer earnings must, crucially, take into account its effect on worker output. For economists, given the priority our discipline places on revealed preference, there is particular interest in knowing whether the effects of peer earnings exposure on self reports of job satisfaction and happiness translate into changes in actual worker productivity, and, if so, how to best model such behavior. This paper investigates such matters using a field experiment where worker access to relative earnings information is exogenously controlled, allowing for a treatment group exposed to peer earnings information and a comparison group that is not.⁴

Specifically, workers in an online labor market perform bibliographic data entry work for which they are paid a piece rate (framed as a net of tax wage) for each article for which bibliographic information is correctly entered. As they have a fixed work period, labor supply in this context amounts to labor effort measured by effective output, i.e., the number of correctly inputted articles.⁵ After one period of work all workers are told of their earnings from this work period. A randomly selected group of workers is also told how their earnings in that period compare to those of a group of fellow workers. All workers then engage in a second period of work after which information is revealed about their own and (for some workers) peer earnings in that period of work (in the same fashion and to the same workers as before). Employment then terminates.

In this setting, there is no direct financial reward for improved relative standing. Perception of indirect financial reward (e.g., from increased odds of continued employment for higher performing workers) is also unlikely given the institutional setting and that workers are told the work relationship will finish at the end of the second period. The experiment, thus, serves as a test of intrinsic preferences over relative standing. An additional unique feature of the experimental design is that I am able to control the makeup of the presented peer distributions, randomly assigning some of the workers treated with relative earnings information a low-earning peer group and some a high-earning peer group. This exogenous assignment of relative position allows for an assessment of heterogenous effects of the peer earnings disclosure treatment that avoids confounding ability bias or mean reversion present in other designs.

I find that, on average, worker effective labor supply increases among workers who are presented information about their placement in the distribution of earnings among a group of fellow workers, a novel experimental finding in the field. This productivity boost in the second round of work amounts to roughly 10% of average output, a significant economic effect suggesting there may be substantial gains in some settings from disclosing peer earnings information. This result is evident when social comparisons are made using an earnings distribution from fellow workers who perform the same work at the same piece rate. An important corollary is that this significant productivity boost from peer earnings disclosure disappears in a follow-up session with different workers where the social comparison is made using co-workers who perform the same work under the same rules but who face different piece rates. This later result suggests the boundaries of applicability for a peer earnings disclosure policy designed to increase output, and, the inhibiting effect that underlying inequalities in compensation schemes may have on the ability of social comparisons to incentivize work.

Additionally, in a first for the literature, I am able to use varying piece rates between workers to test whether relative earnings information can be used not only to increase worker output and therefore total tax revenue, but, also, as an instrument to alter optimal marginal tax rates on labor income. In the standard optimal income tax problem, the counterweight to greater government spending is the disincentivizing effect a higher tax rate imposes by reducing the marginal reward for costly effort. When workers care only about their own earnings, this marginal reward is typically taken to be the consumption value of extra earnings. However, if workers care about relative earnings as well, deriving additional utility from having higher income relative to a peer group, the marginal reward for the “status” value of earnings may not be diminished by an increased tax if one’s peer group also experiences the same increase in tax rates.⁶ One possible implication is that stimulating worker concern for their relative earnings position via disclosure of peer earnings may be a way to minimize the efficiency loss of taxation. I test this hypothesis by measuring worker labor supply elasticity with respect to the net of tax wage, a sufficient statistic for optimal income tax rates (Saez, 2001). I find virtually no difference in the elasticity for workers in the control and treatment groups, suggesting that while governments may use the disclosure of earnings information to grow the tax base, as implied by the other finding here, there is not at present evidence that such a policy is an effective tool to alter the efficiency costs of taxation and optimal income tax rates. Furthermore, as discussed within, this null finding of peer earnings disclosure (in conjunction with the positive disclosure effect on labor supply level) sheds insight on the proper functional form assumptions to make (and not to make) in status utility models, as some parameterizations used in the existing literature imply the reduced elasticity in the treatment group just described, while others do not.

A final finding presented in this paper addresses possible heterogeneity in the response to different types of relative earnings information. With identification assisted, as detailed above, by the random assignment of low vs. high earning comparison groups to treated workers, I conclude the above-mentioned increase in treated worker output is primarily driven by increased effort from those who learned they ranked higher on average in the earnings distribution (who provide significantly more labor effort than those who receive no relative earnings comparisons whatsoever). The performance of those treated workers who learned that they ranked lower on average in the earnings distribution, while not worsening, is less uniform. This heterogenous treatment effect further suggests the design of a program revealing relative earnings information may matter for the optimal incentivization of workers, and, that, when feasible, firms and governments may want to selectively manipulate the exact distribution of earnings offered as the comparison group earnings.

This work fits into a long line of research on social comparisons (Allgood, 2006; Beath and Fitzroy, 2007; Boskin & Sheshinski, 1978; Frank, 1985; Ireland, 1998; Oswald, 1983) and, in particular, research on how relative standing affects work and performance in contexts in which there is no direct financial benefit from higher rank (Ashraf et al., 2014; Azmat & Iriberri, 2010; Barankay, 2011a; Blanes i Vidal and Nossol 2011; Charness et al., 2010; Clark et al., 2010; Eriksson et al., 2009; Freeman & Gelber, 2010; Kuhnen and Tymula, 2012; Tran and Zeckhauser, 2012). I describe in detail the state of this literature in my previous working paper version of this manuscript and I discuss existing work as relevant in context within the body of this paper. Here I highlight the chief contributions of this paper in light of the existing work.

First, the present finding of a positive effect on worker productivity from exposure to information about peer worker earnings is the first such finding using field experiment evidence. As the field experiment takes place in a context with no financial reward from such information, unlike many other field studies, this is causal evidence that social comparisons enter directly into worker utility and labor supply functions.

Second, none of the studies pre-dating my own test for a difference in labor supply elasticity (with respect to net of tax wages) among those treated with relative earnings information and those who are not, as the current design allows.⁷ Thus, in the current study I can consider both the usefulness of the public revelation of worker earnings as a tool to grow firm output and the tax base, and, additionally, as a tool in optimal income tax policy. By studying both labor supply and labor supply elasticity as outcomes, my work offers more than the previous literature regarding the exact form of the utility function over status that we should use to model worker behavior.

Third, this work further advances the existing literature on social comparisons by varying the compensation schemes of the peer groups whose earnings are disclosed, revealing different effects of earnings comparisons (vis a vis the control group with no relative earnings information) when peers’ effort is rewarded equally as one’s own effort rather than unequally. Having the control group plus both kinds of relative earnings comparisons in the design goes further than other studies that explore the effect of inequality in compensation on workers’ performance. Other related works effectively only include two of the three groups (Bracha et al., 2015; Breza et al., 2018), and including all three allows me to paint a fuller picture of how relative earnings information and inequality in compensation interact.

Finally, this study is the first to experimentally assign the distribution of peer earnings information that workers see, allowing for a clean test of heterogenous treatment effects for those who learn they rank high and those who learn they rank low compared to their peers.

This paper also contributes to two other separate strands of literature. First, I add to the peer effects literature (Falk & Ichino, 2006; Mas & Moretti, 2009; Sacerdote, 2001) by presenting the first experimental evidence of peer effects with absent and anonymous peers, where a positive effect on worker productivity is observed to result simply from the introduction of information about co-workers’ performance without the co-workers being known, physically present at the site of work, or, engaging in any interaction at all (a feature of the online workplace). Second, I add to the literature that estimates labor supply elasticities via randomized wages in the field (Dal Bó et al., 2013; Fehr & Goette, 2007; Goldberg, 2016)⁸ by contributing intensive labor supply elasticity estimates in a labor market with virtually no adjustment costs for workers, approaching the neoclassical ideal.⁹

In what follows, I describe the labor market and experimental design in Section 2. Section 3 presents the empirical results. Section 4 discusses what the results reveal about how to correctly model tastes for status. Section 5 discusses policy implications of the findings. Section 6 concludes.

2. Data and experimental design

2.1. Labor market under study

The field experiment takes place in the online labor market hosted by Amazon Mechanical Turk, with data collected in 2013-2014. MTurk and similar online subject pools are now commonplace as sites of experimental research in the social sciences.¹⁰ The MTurk platform has several distinct advantages for this study in particular when compared to both laboratory studies and many other alternative labor markets.

For one, in comparison to lab studies, MTurk increases internal validity by allowing workers to complete the experiment without interacting with the experimenter, or, in many cases, not even noticing they are in an experiment at all - thus, removing sources of experimenter bias, or demand characteristics (Orne, 1962). In my case, since I registered with MTurk as an employer hosting the kind of work (data entry) that is typical of other MTurk employers, nothing else distinguished my posted work from usual MTurk work, and, it is quite likely MTurk workers behaved as if they were facing just another employer.¹¹ Secondly, compared to other workplace settings in the field, the geographic dispersion and anonymity of MTurk workers makes it very unlikely that there is contamination of the control group – a particular concern with information treatments such as this one, or, spillover effects whereby untreated individuals are affected by the treatment indirectly (Duflo & Saez, 2003; Miguel & Kremer, 2004). Thirdly, MTurk also allows for the creation of faux enterprises (seeKube et al., 2012; Falk & Ichino, 2006) with relative ease, allowing the researcher to have complete control over worker pay, incentives, and exogenous variation in the comparison groups presented, without mediating partnered firms imposing constraints on the optimal research design. This permits clean identification of the causal effect of the relative earnings information. Lastly, the online nature of the work provides ample opportunity for on-the-job leisure and substituting away immediately from effort to another tab in the browser containing a favorite website when the compensation for work is sufficiently low. This is an attractive feature when studying elasticity of labor supply with respect to the net of tax wage, and approximates the assumptions of the neoclassical labor supply models over continuous consumption and leisure space.

These advantages of the platform are not without potential tradeoffs. In recent years, concerns have been raised regarding MTurk-based studies. One chief concern, highlighted by Brodeur et al. (2022), is that the MTurk-based experimental literature may be liable to detect false positives at high rates because of low statistical power and small samples. In their review of thousands of published experiments on the platform, the median MTurk experiment sample size is 249. The current study, on the other hand, has a much larger sample size (see Section 2.3). Other common concerns raised about MTurk studies (see Hauser et al., 2019) are also unlikely to be an issue in this study. For instance, concerns about deception in responses are less of an issue when work output is the object of study, while concern that subjects will pay insufficient attention because of low stakes are diminished by the decision in this case to pay an expected hourly wage well in excess of the going rate at the time of the study (though, naturally, not all concerns with MTurk samples can be removed entirely).¹²

2.2. Experimental work task

To conduct a useful test for whether relative earnings information can be manipulated to minimize the efficiency loss of taxation, and, to test for differential labor supply elasticity when relative income considerations are made salient, there must first be a task that ordinarily responds positively to monetary incentives. However, finding real effort tasks that demonstrate the expected upward sloping labor supply function with increasing pay is not a trivial matter. Camerer & Hogarth (1999) and Bonner et al. (2000) survey the economics and psychology literatures testing the effects of financial incentives on performance in a host of lab experiment settings. They find performance in a wide variety of tasks is not positively affected by increased compensation, and that only a few classes of laboratory tasks exhibit a positive relationship between piece rate and the level of performance. One class common to both surveys is clerical tasks, which inspire little intrinsic motivation, require little skill, and where effort increases actually improve performance. As such, I choose a simple clerical task to use in this experiment.

The task is a bibliographic entry task, modified from Tonin & Vlassopoulos (2015). The work involved filling in the correct bibliographic information for academic articles (author name, journal, article title, etc. for a series of published articles) and workers were paid a piece rate for each correctly entered article. See Appendix Figure 1 for an example. This task is derivative of earlier typing tasks, such as that by Swenson (1988) and others (Charness & Kuhn, 2011).¹³ It is an ideal work task since the only special skills needed to perform the work are the ability to type and read - prerequisites that any internet user, and thus MTurk worker, will possess. Thus, incentives, whether pecuniary or non-pecuniary, will not be rendered irrelevant due to ability limits when in fact they could potentially motivate in other settings. The data entry work is also incredibly simple and requires little attention to understand, thus rendering one possible drawback of an online platform - that subjects cannot be sufficiently instructed by an experimenter or manager in the proper rules of their work - largely moot. Lastly, differences in ability and effort will generate a wide dispersion of performance.

2.3. Experimental design

After registering with MTurk as an employer I posted an advertisement (see Appendix Figure 2) on the MTurk employer advertising bulletin where potential workers can scroll through alternative job postings and read short descriptions of the work opportunities. In this advertisement, workers were informed of the opportunity for work at a bibliographic data entry task for which they would be paid a piece rate plus a flat one-dollar fee for answering a few worker survey questions. The nature of this work is very similar to other work posted on MTurk, and by all appearances comparable to work offered by many other MTurk employers. The advertisement indicated the work would take about 45 minutes to an hour and interested workers were told to access the work through an external website. Once on the website workers were presented with longer instructions (Appendix Figure 3a-c) about the work task and the actual piece rate per correctly inputted article for the first twenty minutes of work. Following the instructions, workers were asked about their earnings expectations (see Appendix Figure 4) and then a 20-minute work period began (with the work screen looking like Appendix Figure 1 with the addition of a clock counting down the 20 minutes). Following this, a series of demographic questions were asked and workers were informed of their earnings in the previous period of work. Then a second 20-minute round of work began, with workers’ earnings expectations for this round of work again elicited immediately beforehand. In the second round of work some workers randomly received higher or lower piece rates than in the previous work period and some workers’ piece rates remained constant. Workers were told in the instructions that their wage in the second round of work may or may not be the same as that in the first and that it would be determined independently of their “performance or pay or any other factor in the previous round of work” and instead by “managerial needs,” as would be the case in any number of jobs utilizing real-time pricing or differential pricing for work from clients of different value. The piece rates were framed as net-of-tax wages with workers told “any withholdings required by Amazon consistent with state law will have already been applied, so the entire X cent bonus per correct article is yours, like an after-tax wage.” Following the second round of work, workers were informed of their earnings in this round of work and then the work relationship was terminated.

Piece rates were randomly assigned to workers as they successively entered the external website, as was the relative earnings information treatment status, with assignment to treatment and control status stratified by piece rate profile. Following each round of work, those in the treatment group were exposed to information about co-workers’ earnings in the previous period of work in addition to information about their own earnings in the previous period (information they were told they would receive in the instructions). Those in the control group learned only about their own earnings in the previous work period.¹⁴ For an example of what these screens looked like see Appendix Figures 5 and 6. The sole difference between the control and treatment groups was this additional exposure to earnings information about the distribution of earnings for a comparison group of four co-workers (whose earnings information had been collected previously) and the solicitation of two additional earnings expectations questions prior to each round of work.¹⁵ Those receiving the peer earnings information treatment were randomly assigned into two different types of peer earnings information treatments (without any knowledge of the distinction): one in which the peer group was drawn from low-earning peers and one in which the peer group was drawn from high-earning peers, leading to a greater chance that workers assigned to the former group learn they rank highly relative to their co-workers (and the reverse for those assigned to the latter group). I call these two different types of treatments inflated rank and deflated rank treatments, respectively. Pay was independent of relative position for all workers, and the workers were clearly told as much at the outset. Piece rates ranged from 2 cents to 16 cents per article, though workers only knew of their own piece rate in a given period of work and not about this range.

Initial workers assigned to the treatment condition were presented with peer earnings information from a group of peers who had participated, as these treated workers had been told, “in the same timed work under the same pay per article” as themselves (such parity in piece rates could also be plainly inferred from review of the screen in Figure 6). For an additional later group of workers in the treatment condition, the peer earnings presented to them were no longer drawn exclusively from workers who received the same piece rate as themselves (and the “same pay per article” part of the instructions was omitted in this case¹⁶), so that differences in own and revealed co-worker earnings may have been due to inequalities in the piece rate distribution among workers in addition to performance differences. Such inequalities in the peer piece rates were also obvious from Figure 6. In the presentation of the results that follows, I initially summarize the findings for the first of these treatment groups as compared to the control group in their sessions, referred to as PP (parity in peer piece rate) sessions. I then go on to make a comparison with the second treatment group, coming from what I term the IP (inequality in peer piece rate) session.

In total, the MTurk advertisement in Figure 2 yielded 1502 visitors to the data entry website, 883 of whom came following 4 initial recruitment sessions (representing 428 PP treatment assignments and 455 control assignments, balanced across sessions), and, 619 of whom came following a subsequent IP recruitment session (involving 314 IP treatment assignments and 305 control assignments). 22% of these visitors never moved beyond the initial instructions into round 1 work. Table 1 presents summary statistics of the remaining workers who provided demographic information, comparing those assigned to receive the relative earnings information treatment and those who were not (Columns 2 and 1, respectively). A balancing test (Wilcoxon-Mann-Whitney rank sum test) is performed to test if randomization of treatment status leads to balance of observables, as would be expected with successful randomization. The findings, presented in Column 3 of Table 1, suggest that based on observable characteristics like gender, age, race, and income, randomization was successful.

Table 1 Test for balanced treatment and control groups

Notes: The table reports the mean values of demographic variables for treatment (those exposed to relative earnings information) and control groups in Columns 2 and 1, respectively. In Column 3, the z statistics and p-values are reported for a Wilcoxon-Mann-Whitney test comparing the underlying distributions of each variable for the treatment and control groups. Results exclude 2 observations that report an age of 0. The value in parenthesis are the results excluding 2 outlier observations with income over $150,000.

3. Empirical results

In the main analysis in Section 3.1 I present results from the PP sessions where the initial relative earnings information treatment involves workers facing parity in their peers’ piece rates (PP session treated workers). Section 3.2 goes on to compare these results to the results of the relative earnings information treatment when there is inequality in the peers’ piece rates (IP session treated workers).

3.1. Main analysis

In the first 20-minute round of work (when treated workers expect relative earnings information but have yet to receive any) there is some evidence of higher performance by PP treated workers, indicating a positive ex ante effect of relative earnings information, consistent with one of the findings of DellaVigna and Pope (2018).¹⁷ This ex ante effect is only weakly significant and is less robust than the ex post effect,¹⁸ and in all that follows I concentrate on the round 2 performance of workers (the period post relative earnings information exposure for the treated workers). It is worth noting, though, that there is no evidence that the robust positive second period effect documented in PP treated workers below is offset by a dip in the productivity of the treated workers ex ante (an important consideration for policy implementation), and that, if anything, workers may also be directly motivated by competitive preferences in anticipation of their relative standing revelation at the announcement of the onset of such a policy.¹⁹

In analyzing PP session workers, I necessarily restrict the analysis to those workers who took up the treatment/control assignment in these sessions and did not leave the website, accounting for 78% of all initial visitors to the introductory page of the work website and 95% of those visitors who actually began work. There is no evidence of differential attrition between those assigned to the treatment group and those assigned to the control group, as can be seen in Column 1 of Table 2.²⁰ While Amazon makes efforts to assign only one unique MTurk worker ID to each person, in the analysis that follows I drop observations whose work comes from the same IP address, as is standard with more careful MTurk studies, to prevent the possibility that these may be repeat workers using different MTurk worker IDs. I also focus throughout on workers who supplied positive levels of output in each period of work to allow for intensive elasticity estimates and a meaningful comparison of actual earnings in the treatment (though the results are not significantly affected by this). Column 2 in Table 2, thusly, tests for differential attrition among the subset of workers closest to this base sample, and, also indicates there is no significant difference for treated and control workers.²¹

Table 2 Test of differential attrition

Notes: Columns 1-4 report results from parity-in-peer-piece-rate (PP) sessions while Columns 5-6 cover the inequality-in-peer-piece-rate (IP) session. Column 1 shows there is no statistically significant difference in the likelihood of dropping out (leaving the work website permanently) following exposure to information about only one’s own earnings in the previous round of work (those in the control group) rather than information about one’s own earnings and that of a peer group (those in the treatment group). Specifically, in Column 1 an indicator for attriting at the beginning of the second work period is regressed on an indicator for relative earnings information treatment status. Column 2 runs the same regression on the subset of observations whose work came from a unique IP address and who supplied positive levels of output in round 1 of work. In Column 3 this same outcome is regressed on an indicator for the type of relative earnings information treatment received (which takes a value of 1 for those assigned to a high-earning comparison group and, thus, a lower, or, deflated average rank) to test for differential attrition among the deflated versus inflated rank treatments (using only treated workers in the specification). Column 4 replicates the regression of Column 3 with the same subsample used in Column 2. Columns 5-8 replicate Columns 1-4 for the IP Session. Huber robust standard errors are reported in parentheses. *p < 0.05, **p < 0.01, ***p < 0.001

The positive effect that relative earnings information has on worker output can be seen in the results in Table 3. In Column 1, revelation of last period’s relative earnings information is found to increase the number of articles correctly entered in the second period by 2.4 articles (controlling for second period wage level). Results are significant at the 1% level and remain so upon the addition of demographic control variables (Column 2) and dummies for the experimental session (Column 3). In Column 2, with additional age, gender, race, and income controls, relative earnings information exposure increases worker output by 2.85 correct article entries or approximately 10% of average worker output. In Column 4, the sample is restricted to those workers who provided MTurk IDs that could be matched by Amazon. This leads to the exclusion of only seven observations from workers who did work but provided missing or erroneous MTurk IDs that could not be matched to those in Amazon Mechanical Turk’s database of workers who accepted this work. The results do not change in this sample. Finally, in Column 5 the regression is run with the log of worker output in period 2 and the log of period 2 wages in order to look at percentage changes and calculate a labor supply elasticity with respect to wage rate.²² With full compliance, given that all treated workers must go through the relative earnings revelation screen, and with an improbable chance of contamination, given that workers are geographically dispersed, anonymous and not working together, the estimates on the relative earnings information treatment constitute a local average treatment effect (Duflo et al., 2006).

Table 3 Relative earnings information and worker output

Notes: The table reports results from the parity-in-peer-piece-rate (PP) sessions. The dependent variable in Columns 1 through 4 is the total number of correct articles entered in round 2 of work, the round of work following the revelation of one’s own and (for treated workers) co-worker earnings information. The dependent variable in Column 5 is the log of this output. Relative Earnings Information Treatment is an indicator variable that takes the value of 1 if workers were randomly assigned to receive information about peer earnings in addition to the information about their own earnings that all workers receive. The Wage variable ranges from $0.02 to $0.16 per correct article entry, and the Log wage variable is the log of 100*Wage. Column 4 excludes those workers who failed to provide a valid MTurk ID. Huber robust standard errors are reported in parentheses.

* p < 0.10, **p < 0.05, ***p < 0.01

While the above results are perhaps the most policy-relevant results, demonstrating that earnings transparency of this form leads to significant productivity boosts overall, there remains the question of whether the treatment effect is driven primarily by those who learn they were low ranked or those who learn they were high ranked. To test this, the experiment was designed, as previously mentioned, so that treated workers were randomly assigned either a low-earning or high-earning comparison group (unbeknown to them), thereby, on average generating artificially inflated or deflated ranks, respectively, among workers who should be similar otherwise due to randomization. Table 4 shows that such an assignment did indeed generate better revealed relative standing for the inflated rank treatment vis a vis the deflated rank treatment, with about 65 % of workers in the former group learning they were in first place compared to their peer group in the previous period of work, and about 60 % of workers in the latter group learning they were in last place. Column 3 in Table 2 shows there is no differential attrition among these two different treatments, and, Column 4 shows the same when restricting the sample as in Column 2.

Table 4 Deflated and inflated rank treatments exogenously affect rank

Notes: The table reports the effect on own rank of assignment to the inflated rank treatment (being presented with the round 1 earnings of a comparison group where the co-worker earnings are drawn from low-earning peers) and the effect of assignment to the deflated rank treatment (i.e. being presented with the round 1 earnings of a comparison group where the co-worker earnings are drawn from high-earning peers). “First Place” indicates the worker learned prior to round 2 of work that s/he had just finished at the top of the earnings distribution relative to a comparison group of co-workers, and similarly for “Second Place” and so on. Data comes from the parity-in-peer-piece-rate (PP) sessions.

Table 5 reports the heterogenous effect of relative earnings information on labor supply, showing how the productivity boost among treated workers observed in Table 3 appears to come primarily from those treated with a low-earning comparison group who, thus, on average learned they were ranked highly. In Columns 1 and 2 of Table 5, I document how those workers given inflated ranks increase output by approximately 3.5 articles relative to the control group, with results that are highly significant both with and without controls. In the case where I control for demographic variables (Column 2), the increased output for the inflated rank workers amounts to an increase of 14% of the average worker performance. There is a smaller but still positive coefficient on the indicator for assignment to the treatment with exogenously deflated ranks. The performance for this deflated rank treatment is not quite significantly different at the 10% level than that of the control group unexposed to relative earnings information in the specification without demographic controls (Column 1 of Table 5) while it is significantly different at around the 6-7% level in Columns 2 and 3 where demographic controls are added to the base sample and the sample excludes workers without valid MTurk IDs. The p-value for the hypothesis that the inflated and deflated rank coefficients are equal is about 0.20 in these specifications and the inflated rank workers correctly input about 1.5 more articles than the deflated workers (about 5% of the average output).²³ Taken in total, the evidence suggests the deflated workers supply more labor than the control group and less than the inflated rank workers, though, it is not possible to reject at the standard 5% level the null that they supply labor at the same level as the control workers nor the null that they supply the same level of labor as the inflated rank workers (though, of course, both nulls cannot be true given that the inflated rank workers do supply significantly more labor than the control workers).

Table 5 High rank revelation and worker output

Notes: The dependent variable in Columns 1 through 3 is the total number of correct articles entered in round 2 of work, the round of work following the revelation of one’s own and (for treated workers) co-worker earnings information. “Inflated Rank” indicates a dummy variable for treated workers who were randomly assigned to low-earning peer groups, resulting in an inflated rank for themselves, while “Deflated Rank” indicates those treated workers randomly assigned to high-earning peer grousp, resulting in a deflated rank for themselves. Data comes from the parity-in-peer-piece-rate (PP) sessions. Column 3 excludes those workers who failed to provide a valid MTurk ID. Huber robust standard errors are reported in parentheses.

* p < 0.10, **p < 0.05, ***p < 0.01

Causal inference from these results hinges on the successful randomization of the low-earning and high-earning comparison groups to workers who on average would be equally productive otherwise. I perform a placebo test to see if first round work was somehow significantly different between these two groups of treated workers.²⁴ However, I find no significant difference in round 1 output for treated workers later assigned to low-earning comparison groups and those later assigned to high-earning comparison groups (the coefficient on the difference in round 1 performance between the inflated and deflated rank workers is about 0.5 and the t-stat is close to zero, results unreported). Taken together, the results in Tables 3 and 5 provide robust evidence that exposure to relative earnings information can increase worker productivity (in a statistically and economically significant way), and, that the average effect is likely driven by workers who experienced a favorable ranking following the previous period of work. This heterogeneity of the treatment effect along the dimension of favorable or unfavorable ranking information is, also, apparently gendered. Appendix Table A1 demonstrates that it is men who display this heterogeneity: men in the inflated rank treatment demonstrate a significant positive treatment effect while men in the deflated rank treatment do not. For women, both treatments yield positive and significant increases in output. These gender differences are discussed further in the Appendix.

In Table 6, I show that the elasticity of labor supply with respect to net of tax wage changes is almost identical for the treatment and control groups. This is confirmed by a Chow test, with the null that the elasticities are the same, yielding a p-value of over 0.9. While relative earnings information affects the level of output, as shown in Table 3, it does not seem to lead to differential sensitivity to wage changes. Table 6 also provides estimates of the labor supply elasticity in the field using exogenously assigned wages. The result (an elasticity of 0.16) conforms with moderately sized elasticities found in existing observational studies (e.g., Blundell et al., 1998).

Table 6 No differential elasticity among treated and control

Notes: The table replicates the log-log specification in Column 5 of Table 3, but, with the variable for relative earnings information treatment removed, and, instead, the regression run separately for treatment and control workers (see Table 3 for further description). A Chow test, with the null that the elasticities are the same in the two groups, yields a p-value of 0.93. Huber robust standard errors in parentheses.

* p < 0.10, **p < 0.05, ***p < 0.01

3.2. Inequality in compensation inhibits treatment effect

As noted, the previous significant results come from sessions where those workers who are treated make social comparisons with co-workers who were paid the same piece rate as them (parity-in-piece-rate, or PP, sessions). However, for a different group of treated workers who face inequality in the piece rates that co-workers are paid (those drawn from the IP session), presentation of peer earnings information no longer produces a significant productivity gain among these treated workers relative to control workers. This can be seen in Table 7 which presents the results of the PP and IP sessions jointly, and which is summarized below.²⁵

Table 7 Inequality in compensation undermines productivity gains from earnings comparisons

Notes: The dependent variable in Columns 1 through 4 is the total number of correct articles entered in round 2 of work, the round of work following the revelation of one’s own and (for treated workers) co-worker earnings information. The dependent variable in Column 5 is the log of this output. The two Relative Earnings Information Treatments are indicator variables that take the value of 1 if workers were randomly assigned to receive information about peer earnings in PP and IP sessions, respectively, in addition to the information about their own earnings that all workers receive. The Wage variable ranges from $0.02 to $0.16 per correct article entry, and the Log wage variable is the log of 100*Wage. Column 4 excludes those workers who failed to provide a valid MTurk ID. Huber robust standard errors are reported in parentheses.

* $p \lt 0.10$, ** $p \lt 0.05$, *** $p \lt 0.01$

In Column 1, the large and significant increase in performance for treated workers in the PP sessions (more than a 2.5 article, or about 10%, increase relative to control workers from the PP and IP sessions) is shown to almost entirely disappear for those IP session workers who are treated with information about their co-workers’ earnings. The point estimate representing the difference between these treated IP workers’ output ex-post relative earnings revelation and that of control workers is close to zero and not significantly different than the control group, while the estimate is significantly different than the PP worker treatment effect estimate at the 1% level. This general result is unchanged by the addition of demographic controls (Column 2) and session fixed effects (Column 3) and persists when the sample is restricted to those workers who provided MTurk IDs that could be matched by Amazon (with modestly different reported point estimates and p-values). Column 5 presents the specification with log of worker output in period 2 and log of period 2 wages.

It is worth noting that whether the inequality in peers’ piece rates takes the form of peer piece rates that are relatively higher or relatively lower than one’s own rate of compensation does not seem to matter for the general result; both inflated and deflated rank treatments in the IP sessions are not significantly different in output from the control group or from one another (results unreported).²⁶ In other words, the mere presence of an unequal compensation scheme seems to be enough to undo the productivity gains from the relative earnings information, whether the wage inequality favors the worker or not. Furthermore, the degree of inequality (as measured by the Gini coefficient on own and presented co-worker piece rates) has no predictive power in explaining IP worker output.

Viewed from one angle, this finding appears contrary to one of the findings in Breza et al. (2018), whose study postdates this experiment, as they show that when there are known unequal compensation rates among peers, those with relatively lower wages work less. However, this lower output is relative to a counterfactual of an identically compensated worker who works in a context where this worker knows that their peer workers are compensated equivalently as themselves. That is, it is a comparison between output in something like my IP treatment and something like my PP treatment (with nothing like a control group sans relative earnings information existing in this other paper). Thus, a reduction in output for some workers when their peers are compensated unequally relative to when the peers are compensated equally is entirely consistent with the inhibitory effect of inequality that I document in comparison between IP and PP treatments.²⁷ The properly understood takeaway of the two works, as it relates to inequality, is then as follows: inequality retards productivity, but, it does so relative to a baseline with available information about relative standing (where preferences over relative standing can motivate effort) not relative to a baseline of no relative standing information.

Turning to another comparison with related work, my finding of an insignificant difference between IP treatment worker output and control worker output is consistent with one of the findings in Bracha et al. (2015).²⁸ As in their “strong justification” treatment, where piece rate inequalities were justified on the basis of evaluating essays written by workers using an unspecified criterion of evaluation, here in this paper inequalities in worker piece rates were explained by the similarly opaque “managerial needs” of the employer. In both cases, this vague justification seems to be enough to offset potential worker performance reductions (relative to no peer compensation information) that could result from piece rate inequalities (whereas in the presence of patently arbitrary, unjustified piece rate inequalities, Bracha et al. did find a labor supply reduction relative to a no relative standing information baseline).²⁹ However, again, as I show above, even such “justified” piece rate inequalities do produce an inhibitory effect on worker output relative to the productivity gains in settings with social comparisons and no piece rate inequalities (where earnings differences exist only because of productivity differences).

4. Modelling implications of the findings

The previous section revealed four findings that must be explained by any model of worker preferences and labor supply in this context.

Finding 1: Those exposed to relative earnings information supply more labor effort on average than those without access to this information in a setting where co-workers are commensurately compensated for like effort.

Finding 2: When there is inequality in how co-workers are compensated for like effort, presentation of relative earnings information no longer has any effect on labor supply.

Finding 3: Finding 1 is driven by those shown lower earning comparison groups (resulting in inflated rank for themselves) in the previous period of work.

Finding 4: There is no significant difference in labor supply elasticity with respect to wage changes for those treated and untreated with relative earnings information, and both are positive.

In this section, I provide a simple stylized, descriptive model of worker utility that can explain the results observed in this field experiment. It is meant to be illustrative and is by no means the only specification of preferences that may be consistent with the results, but, it does parsimoniously explain the observed findings better than certain other plausible candidate models, which I discuss briefly below as well.

To begin, I derive worker labor supply by modifying a standard model of effort provision that imposes a separability assumption between consumption, or, post-tax earnings, and cost of effort. Specifically, worker utility is taken to be quasilinear in post-tax earnings (c) with a constant wage elasticity of labor supply and an additive term indicating relative earnings considerations, $s(c,\bar c)$

(1)\begin{align} U(c, e, \bar c; \theta, \lambda)= c - \theta e^{1+1/\epsilon} + \lambda s(c,\bar c) \end{align}

where $\bar c$ is the average of peer post-tax earnings and $s(c, \bar c)$ is weakly increasing in c, meaning one’s status utility is never negatively affected by one’s own increased earnings. The parameter λ represents the weight worker preferences place on relative earnings concerns (among the experimental population of co-workers), with a larger λ indicating greater concern with the status-value of earnings relative to the consumption-value of earnings.

For a worker in the control group who is not exposed to relative earnings information, λ is presumed to be zero since no co-worker peer group was ever mentioned to these workers, and, a decision about the allocation of consumption and labor seems unlikely to include concerns about an out of sight and out of mind comparison group of workers. Similarly, when there is wage inequality and no sense that there is a level playing field among oneself and co-workers, the utility derived from competing for status is thought to be nonexistent (in the same way that there is little motivation to compete in a race where the opponents started hours before or afterward). The information about co-worker earnings in the PP sessions then serves to “turn on” concerns for relative earnings $s(c,\bar c$),³⁰ with more weight placed on status concerns (larger λ) the more that attaining upper-tier, rather than lower-tier, status is believed to be feasible, as detailed further in the discussion below. More generally, these relative earnings concerns embodied by positive λ values would be expected to materialize in other settings where relative earnings information is made salient and where the jockeying for relative position in the earnings distribution realistically allows for possible movement in relative position – and especially movement toward the top of the distribution – based on a worker’s behavior.³¹

In the case of λ = 0, the preferences are standard neoclassical preferences, and, optimal labor supply³² is derived from maximizing (1) subject to the budget constraint $c=(1-\tau)w^{g}e$, yielding

(2)\begin{align} e(w)= \left(\frac{w}{\theta(1+1/\epsilon)}\right)^{\epsilon} \ \end{align}

where $w=(1-\tau)w^{g}$ with w ^g being the gross wage and $1-\tau$ the net of tax rate. The corresponding labor supply elasticity with respect to w is ϵ.

Workers in the PP treatment group, who are exposed to relative earnings information from commensurately compensated peers, maximize the expected value of (1) subject to the budget constraint, now with a positive value of λ and uncertainty introduced from incomplete knowledge of $\bar c$. The sub-utiliy function $s(c,\bar c)$ now matters, as does the distribution of worker beliefs about peer earnings, which I summarize by beliefs about the average peer earnings $\bar c$. I simplify by assuming there are two states of the world that a treated worker believes exist, one where $\bar c=\bar c_{L}$ (that is, the belief that they face a low-earning peer group) that occurs with probability P_L, and, one where $\bar c=\bar c_{H}$ (the belief that they face a high-earning peer group) that occurs with probability $P_{H}=1-P_{L}$. Status concerns have been modeled before in the literature using the simple functional form $s(c,\bar c)=c - \bar c$ (Allgood, 2006; Charness et al., 2010; Clark and Oswald, 1998) and I modify this functional form so that total utility $U(c, e, \bar c; \theta, \lambda)= c - \theta e^{1+1/\epsilon} + {\bf1}[\bar c = \bar c_{L}] \lambda^{0} (c - \bar c_{L}) + {\bf1}[\bar c=\bar c_{H}]\lambda^{1} (c- \bar c_{H})$. This allows for the possibility that the marginal status utility of one’s own additional earnings is non-linear (i.e. $\lambda^{0} \neq \lambda^{1}$). Optimal labor supply for the PP treated workers then becomes

(3)\begin{align} e^{*}(w)= \left(\frac{w(1+P_{L}\lambda^{0} + P_{H}\lambda^{1})}{\theta(1+1/\epsilon)}\right)^{\epsilon} \ \end{align}

Thus, comparing (2) and (3), Finding 1 and Finding 2 imply that at least λ ⁰ or λ ¹ is greater than zero given that $P_{L}\lambda^{0} + P_{H}\lambda^{1}$ must be greater than zero for the finding to hold (and given $P_{L}, P_{H} \gt 0$). Workers exposed to relative earnings information in PP sessions provide more effort (all other things being equal) since when compared to some group of commensurately compensated peers their concern with relative standing provides additional incentive to marginal effort in the form of not only increased consumption returns on earnings, but, now, also, increased relative standing and status returns. Finding 4 can be shown to follow from this specification as well, with worker labor supply elasticity with respect to net of tax wage equal to ϵ for both workers with labor supply defined by (2) and workers with labor supply defined by (3).

As for Finding 3, it is intuitive that those workers who were exposed to low-earning peers following round 1 performance (the inflated rank workers) have a larger P_L, and thus smaller P_H, than the deflated rank workers exposed to high-performing peers. Indeed, the data confirms that the different information they received changed their expectations in this way. A rank sum test testing the null that inflated and deflated rank workers in PP sessions have the same reported expectation of peer earnings in the second round of work (following the relative earnings revelation for these two types of treated workers) has a p-value of 0.01, indicating that the larger reported expected average peer earnings for the deflated rank workers is significantly larger. This fact together with Finding 3 imposes conditions on the relationship between λ ⁰ and λ ¹. Recall, the pattern of observed worker productivity in the PP sessions is inflated worker labor supply > deflated worker labor supply > control worker labor supply. This suggests that $\lambda^{0} \gt \lambda^{1} \gt 0$. This implies workers’ marginal utility from improving their relative standing when facing low earners (who make it more likely they will go to the top of the earnings distribution with extra effort) exceeds that from improving relative standing when facing high earners (who make achieving high relative position unlikely). In other words, the marginal status gain from extra effort is less psychically remunerative when moving up the lower rungs of the social status ladder than the higher rungs, and, there is a non-linearity in $s(c,\bar c)$.

Notably, the successful prediction of all four findings in the above model is sensitive to the choice of functional form for $s(c,\bar c)$. An alternative definition of $s(c,\bar c)= \frac{c}{\bar c} $ has been presented elsewhere in the literature (e.g., Boskin & Sheshinski, 1978) and can explain Findings 1–3 easily. Finding 4, however, would only be consistent with this specification under additional, nonstandard assumptions, namely, if assuming utility-maximizing behavior that is less than perfectly rational (so that the worker ignores the effect a workplace wage increase has on the earnings of other similarly compensated peer workers). To see this, let utility under this alternative functional form assumption be

(4)\begin{align} U(c, e, \bar c; \theta, \lambda)= c - \theta e^{1+1/\epsilon} + \lambda s(c,\bar c) = c - \theta e^{1+1/\epsilon} + \lambda \frac{c}{\bar c} \end{align}

Utility maximization yields a labor supply function for a PP treated worker of

(5)\begin{align} e^{*}(w)= \left(\frac{w(1 + \frac{P_{L}\lambda^{0}}{\bar c_{L}} + \frac{P_{H}\lambda^{1}}{\bar c_{H}})}{\theta(1+1/\epsilon)}\right)^{\epsilon} \end{align}

Under rational expectations, the comparative statics lead to a labor supply elasticity with respect to net of tax wage $\frac{\partial e^{*}(w)}{\partial{w}} \frac{w}{e^{*}(w)}=$

(6)\begin{align} \epsilon \times e^{*}(w) \times e^{*}(w)^{-1/\epsilon} \times [ \frac{1 + \frac{P_{L}\lambda^{0}}{\bar c_{L}} + \frac{P_{H}\lambda^{1}}{\bar c_{H}}}{\theta(1+1/\epsilon)}-\underbrace{w(\frac{P_{H}\lambda^{1} (\frac{\partial \bar c_{H} }{\partial w}){\bar c_{H}}^{-2}}{\theta (1 + 1/\epsilon)} + \frac{P_{L}\lambda^{0} (\frac{\partial \bar c_{L} }{\partial w}){\bar c_{L}}^{-2}}{\theta (1 + 1/\epsilon)})}_\text{g} ] \times \frac{w}{e^{*}(w)} \end{align}

which simplifies to

(7)\begin{align} \epsilon \times e^{*}(w)^{-1/\epsilon} \times [ e^{*}(w)^{1/\epsilon} -w g ] = \epsilon \times [ 1 -\frac{w g}{e^{*}(w)^{1/\epsilon}} ] \end{align}

Since g is positive under the above assumptions, $\frac{w g}{e^{*}(w)^{1/\epsilon}}$ is positive and

(8)\begin{align} \epsilon \times [ 1 -\frac{w g}{e^{*}(w)^{1/\epsilon}} ] \lt \epsilon \end{align}

Thus, the PP treated worker elasticity (under this alternative specification of utility) should be smaller than the elasticity of the control group ϵ - something that is contrary to the current findings.³³

Other candidate models of worker utility that do not consistently explain all the findings include a reference-dependent model that takes last period’s average peer earnings as the reference point, predicting a labor supply function for PP session deflated workers that is weakly greater than the labor supplied by PP session inflated workers for all wages, and, an alternative reference-dependent model that treats rank rather than earnings as the gain-loss commodity and takes last period’s rank as the reference point, yielding predictions that are consistent with each of the findings relevant to PP workers at some wage level but never simultaneously consistent with all three of them using the same draws from the wage distribution. Furthermore, using the preferred specification for status concerns offered here, but modeling the treatment as solely updating beliefs over relative standing without making status concerns more salient cannot convincingly explain all the findings (see footnote 29). And, at the most basic level, any model that neglects the direct role of social comparisons for worker utility fails to capture the mechanisms at play here. Finally, as already mentioned, since workers here knew in advance that they were participating in a one-off employment contract with no possibility of future work, explanations involving career concerns are unlikely to explain the findings.

5. Policy implications

The main result, showing that in certain settings individuals work more when exposed to information about relative standing even when such information yields no financial reward, is the first such evidence in a field experimental setting. The finding is consistent with previous work, including the lab experimental findings of Charness et al. (2010); Freeman & Gelber (2010), and, with the quasi-experimental findings of Blanes i Vidal & Nossol (2011), but it is at odds with the field experimental results of Barankay (2011a); Barankay (2011b), which document a negative effect from exposure to information about relative position. Before discussing the implications of the current study’s findings, a word about the reason for this difference is in order. One possibility is that a negative finding might be observed in settings where there is a baseline ability ceiling reached in the performance of the work task absent the relative earnings information. If this is the case and there are heterogenous treatment effects along some dimension not considered here, then those who might be positively incentivized by the relative earnings information have no room to improve their performance, while those (even if only a few) who might be negatively incentivized by the relative earnings information will lower their effort, bringing down average output. This seems at least plausible in the multi-tasking setting studied by Barankay (2011a) where workers are furniture salespeople since the job is one in which the mapping from effort to actual effective output (furniture sold) is not obvious, and, salespeople may be exerting maximum effort but find themselves at a loss for ways to effectively improve their sales given the considerable role that chance plays in their sales efficacy.³⁴

In any case, caution should be exercised in applying this work’s findings to settings far afield from the one studied here as there are many dimensions of variation between the present labor market and others, and, it is not clear how important some of these are for the extension of the results. This caution is worth reiterating and such uncertainty invites further work, however, in some ways at least, the current field experimental setting makes for a weak test of the importance of relative earnings considerations. For instance, existing literature suggests that competitive preferences can be more pronounced when workers share identifiable characteristics with their co-workers (e.g., when women compete against same-gendered peers, Gneezy et al., 2003), while in the present scenario, the peer groups are made up of anonymous co-workers with no known identifiers in common with the worker. Similarly, it seems reasonable to expect that concern with relative earnings may be more pronounced when workers personally know the members of their comparison group or work in close physical proximity to them – neither of which is the case in the present setting with anonymous, geographically dispersed peer groups.³⁵ Thus, there is some reason to believe that in other workplace settings the reported effects may represent a lower bound.

While the PP treatment effects in this paper may be more positive or more negative in other contexts, in what follows in this section I discuss the possible implications of the current findings if indeed future work confirms their generality. I focus on the implications for firms and include a similar but more speculative discussion of implications for government policy in the Appendix.

The clear takeaway of this work for firm personnel management is that in certain circumstances worker productivity could be increased significantly through implementation of a policy disclosing co-worker earnings. Such an incentive scheme is obviously attractive to firms in comparison to the costs of further monetary incentivization (in the present study, the relative earnings information treatment increased output by approximately as much as a doubling of the average wage). This productivity boost would be expected, based on this paper’s findings, in settings where workers are commensurately compensated for their performance. In many such settings, firms have the ability to manipulate who the comparison group of workers is with few constraints. This means a firm could choose to compare most workers to low-earning peers (perhaps from another site of operation) simulating the inflated rank treatment and generating an even higher increase in productivity than the 10% jump observed here across all treated PP session workers. Such a selection of peer groups would have the additional advantage of avoiding welfare costs to some workers from the relative earnings disclosure.³⁶ If selective manipulation of information is not practically sustainable over time, a recent Senn et al. (2023) working paper indicates that self-selection of peers has the power to motivate workers as much as targeted exogenous selection of a reference group done with that goal in mind.³⁷

On the other hand, where inequality in compensation exists, the findings suggest no productivity gains from an earnings transparency policy. As such, the 10 % productivity boost observed here in PP sessions would not be expected to apply across the board in the economy since in many jobs effort does not map into earnings in an equal fashion for co-workers. One interpretation of the different findings in the PP and IP sessions is as suggestive evidence of an inhibitory effect of wage inequality on the broader economy since the introduction of inequalities in piece rates is found to retard the output-increasing consequences of the peer earnings disclosure policy considered here. Under this interpretation, firm policies that shrink wage inequalities may thus have implications for growth in output in conjunction with a policy of earnings transparency. This prediction had been offered decades ago by Postlewaite (1998) but the current work offers the first known empirical support for such a view.³⁸ Another possible interpretation of the IP null result is that the co-workers in that treatment, by virtue of being paid a significantly different wage, may no longer be seen as part of one’s feasible social group (in the same way as those with more distant identities, as discussed earlier in this section) and thus are less likely to activate social comparison concerns.

Whatever the limits, the present work does provide clear evidence of a significant domain for the productivity-enhancing effects of peer earnings disclosure. The question then arises, why do more firms not implement such transparency? While worker productivity is a first-order consideration for firms, there are no doubt other margins of impact from a peer earnings disclosure regime that also matter. For instance, Card et al. (2012) find that workers who compare unfavorably to their co-workers in the earnings distribution report an increase in their reported intention to look for another job, and, Dube et al. (2019) demonstrate that job separations do in fact respond to peer wages (driven by comparisons with higher paid peers). If disclosure of peer earnings leads some workers to quit then additional costs to firms from searching for and retraining replacement workers could offset productivity gains.³⁹ This downside could potentially be moderated, as above, by careful selection of peer comparison groups to simulate the inflated rank treatment groups, given that Card et al. (2012) demonstrate no increase in intention to look for another job for those who compare favorably to their peer group. Additionally, firms may also be concerned that worker earnings disclosure will affect worker wage bargaining by increasing peer compensation demands at significant cost to the firm (see Strauss (1955), for one such example as well as Gartenberg & Wulf (2017), and Mas (2017), for related discussion of the effects of peer earnings disclosure on wages).⁴⁰ Or, firms may worry about negative consequences on worker morale that discourage cooperative behavior among co-workers (though, in contrast, the recent work by Heursen (2023), finds no such negative effect on morale or willingness to help the productivity of others).⁴¹ All of these additional considerations indicate the importance of future work that studies the effects of relative earnings disclosure jointly over a comprehensive set of outcomes and over the long term to ascertain the net result of such a policy.

6. Conclusion

To the author’s knowledge, this is the first work using an experimental identification strategy to show that worker effort in the field is positively affected by exposure to peer workers’ relative earnings information. Such exposure is found to lift worker effective effort by 10% of average output in a sample where treated workers can see how their total earnings compare to those of co-workers comparably compensated for on-the-job performance. This result can be causally interpreted as demonstrating intrinsic competitive preferences or concern for relative standing, as there was no direct financial reward from doing better than one’s peers, and indirect future employment considerations were unlikely given the one-off nature of employment. The findings can also be interpreted as the first evidence of peer effects with absent and anonymous peers, suggesting that having peers present in the workplace may be beneficial not because their physical presence or identity is important in and of itself but because it allows a worker to observe a rough measure of peer performance or earnings and this inspires a competition for status in the worker.⁴² This is also the first work to use the random assignment of high and low-earning peer groups to exogenously change worker rank. Doing so avoids common endogeneity problems that beset analysis of the differential effects that relative earnings information has on those who compare favorably and unfavorably to their co-workers. The results suggest that, on average, the higher productivity observed among workers exposed to relative earnings information is driven most clearly by those workers who experienced an exogenously assigned high relative earnings rank and low average comparison group earnings. Additionally, this work is able to test if relative earnings information exposure affects comparative statics results. In particular, the peer earnings disclosure is found to have no effect on labor supply elasticity with respect to the net of tax wage, shedding light on the limits of peer earnings disclosure policies as an instrument for optimal tax policy and the possibility of using such policies to minimize the efficiency cost of taxation. Finally, the observed productivity boost from peer earnings disclosure is found to disappear when the co-worker comparison group is not commensurately compensated for equivalent performance and there are underlying inequalities in compensation schemes.

Taken together, these findings novelly inform the proper modeling choices for utility over status: certain functional forms on the status sub-utility function - such as the difference in own earnings and average peer earnings - are consistent with the findings while others - such as the ratio of own earnings to average peer earnings, or, certain reference-dependent models that use either prior average peer earnings or prior ordinal income rank as reference points - are not. More broadly, the findings suggest that governments can potentially use social comparisons to grow the tax base - but not to affect optimal labor income tax rates - and that firms can generate significant productivity boosts in some settings simply by providing workers with information about the earnings of their peers. However, underlying inequalities in compensation schemes may inhibit the ability of social comparisons to incentivize work.