On the Cyclicality of Real Wages and Employment: New Evidence and Stylized Facts from Performance Pay and Fixed Wage Jobs

Abstract

1. Introduction

There is now widespread empirical evidence that management practices are determinants of firm productivity (Ichniowski et al. 1997; Bloom and Van Reenen 2007; Bloom et al. 2012, 2019) and influence firms’ response to business cycle fluctuations (Lazear et al. 2016; Aghion et al. 2019). Evidence has focused on both the selection and causal effects on decision-making at the firm-level, highlighting the role of human capital (Bender et al. 2018) and agile decision-making (Bloom et al. 2013). Moreover, motivated by a large literature on the causal effect of incentives on productivity (Lazear 2000a; Hamilton et al. 2003; Shearer 2004; Bandiera et al. 2005, 2007; Griffith and Neely 2009), a related literature has also documented complementarities between management and human resource practices, like the use of incentives (Ichniowski et al. 1997; Choudhury et al. 2019).¹

This paper focuses on the role that performance pay (PP)—one dimension of human resource practices—plays in influencing the responsiveness of employment and compensation growth to cyclical fluctuations.² While the prevailing view among many macroeconomists, dating back to Keynes (1936) and Bewley (2002), was that nominal wages are downward rigid, there is increasing evidence from a combination of survey (Elsby et al. 2016), administrative (Kurmann and McEntarfer 2017), and payroll data (Jardim et al. 2019; Grigsby et al. 2021) that wages are more flexible. To estimate the role of PP contracts as a source of flexibility for business cycle fluctuations, we use underutilized micro-data from the National Compensation Survey (NCS) at the Bureau of Labor Statistics (BLS) to measure employment and compensation across jobs within establishments between 2004 and 2017. Because we observe the same job for up to 5 years, we can examine how employment and hourly compensation growth respond to changes in local conditions separately for PP and fixed wage (FW) jobs. Moreover, unlike prior work that has had to rely on proxies of PP from household survey data (Lemieux et al. 2009, 2012), we measure PP in a job × establishment using information provided by the employer. This improvement is important since household surveys contain significant measurement error and different individuals are surveyed at varying lengths (Bound et al. 2001).

Although our job-level data come at the cost of aggregating across individuals in the same position, our data also come with two important advantages that are unique to this literature. First, we measure total compensation, which is important since non-wage compensation has grown from 10.9% in 1966 to 18.7% in 2018.³ Second, our data capture information about the contracting arrangement, allowing us to distinguish between PP and FW jobs. This is important given the long-run increase in the share of PP workers (Lemieux et al. 2009; Makridis 2019), which represents roughly 35% of the labor force as of 2019.⁴ These features are integral to identifying the ways that organizations use different incentive contracts to cushion against cyclical fluctuations.

We begin by documenting four facts about PP and FW jobs. First, there is considerable dispersion in the pervasiveness of PP contracts in the labor market: whereas as low as 10% of workers in office and administrative industries may have PP, upward of 70% of workers in financial services may have it. Second, average hourly compensation growth has been greater in PP jobs, relative to their counterparts: the average annual growth in real hourly compensation was 1.97% for PP jobs between 2004 and 2017 when compared with 0.7% for FW jobs. Third, PP is more prevalent in larger organizations, ranging from 36% in those with under 50 employees to 52% in those with over 500 employees. Fourth, 84% of establishments with at least one PP job also have at least one other job with PP, suggesting that the provision of PP is decided at the firm-level.

Motivated by these stark differences across contracting arrangements, we subsequently estimate the asymmetric sensitivity of employment and compensation growth in PP and FW jobs to local business cycle shocks. Our baseline specification exploits plausibly exogenous variation in the exposure of similarly ranked jobs within an establishment to state employment growth, allowing for the response of employment and compensation growth to vary by PP status. We find that a 1 percentage point (pp) rise in state employment growth is associated with a 0.084pp rise in the employment growth rate of PP jobs, versus 0.313pp in FW jobs, and a 0.006pp rise in the compensation per worker growth rate of PP jobs, versus a 0.018pp decline in FW jobs. These results suggest that organizations can use employer–employee contracting as a strategic tool to buffer against idiosyncratic shocks over the business cycle.

While these results could be consistent with the incentive effects of PP—that is, establishments use PP contracts to encourage higher effort during booms—we cannot rule out the presence of composition effects since we do not have worker data that would allow us to track the same person over time. These composition effects could create the perception of cyclicality since job switchers tend to accept higher wages (Solon et al. 1994; Haefke et al. 2013; Daly and Hobijn 2016, 2017). We nonetheless conduct three diagnostic exercises that together cast doubt on the empirical importance of composition effects.

First, we demonstrate robustness using sample weights that hold fixed employment composition by industry × occupation cell. Second, we gauge the magnitude of composition effects by exploring the time series patterns for the share of jobs that exhibit no quarter-to-quarter change in employment, which is roughly 70% (Lettau 2012). We find no statistically significant differences between PP and FW jobs in this measure, which would not be the case if the composition of the labor force was systematically changing in these two sets of jobs. Third, using panel variation from the Current Population Survey (CPS), we find that the logged wage difference between job switchers and non-switchers is positively correlated with the unemployment rate, but not statistically significant. Moreover, alternative explanations related to time-varying omitted variables (e.g., change in management), reverse causality, and long-run contracting are inconsistent with the data.

Our paper contributes to three related literatures. The first literature relates to PP as a strategic decision. Starting with Lazear (1986) who illustrated the important selection effects of PP contracts—attracting a higher quality set of candidates for job postings—a consensus now exists documenting the causal effect of PP on employee productivity (Lazear 2000a; Paarsch and Shearer 2000; Shearer 2004). Although there is some evidence that firm-level human resource (Ichniowski et al. 1997) and management practices (Bloom and Van Reenen 2007; Bloom et al. 2013) are causally linked with improvements in productivity, much less is known about how specific forms of employer–employee contracting affect organizational outcomes. For example, Aghion et al. (2019) investigate decentralized management practices, finding that firms with greater decentralization were less adversely affected by the Great Recession. Our results suggest that flexible wage-setting might be one mechanism behind decentralized management practices.

The second literature relates to sources of wage rigidity and the composition of jobs over the business cycle, which dates back to early survey evidence from Bewley (1998) suggesting that managers do not cut wages during a recession for fear of reducing employee morale (Akerlof and Yellen 1985). More recent work from Le Bihan et al. (2012), Barattieri et al. (2014) and Fallick et al. (2015), and Sigurdsson and Sigurdardottir (2016) has also documented wage rigidity using micro-data from France, United States, and Iceland. While we find similar degrees of wage rigidity among FW jobs, our data points toward highly procyclical wages among PP jobs, consistent with early evidence from Devereux (2001) and Swanson (2007). We build upon these contributions by leveraging new data on establishments that directly measures the use of PP, allowing us to compare observationally equivalent workers within the same establishment who vary in their contracting mechanism. Moreover, unlike Gu et al. (2020), we allow for heterogeneity in the timing and intensity of business cycles across states and in the response of employment and compensation growth based on the use of PP.

Our paper complements Grigsby et al. (2021) and Jardim et al. (2019) in three ways. First, we directly measure total compensation, as well as incentive pay and bonuses, whereas Grigsby et al. (2021) proxy for bonus payments by taking the difference between monthly gross and base earnings. While such a proxy is sensible, it bundles different types of payments, including reimbursements and non-standard payments (e.g., vacation pay).⁵ In this sense, the results from Grigsby et al. (2021) that these residual earnings payments are acyclical could result from attenuation in the measurement of PP. Similarly, Jardim et al. (2019) only observe earnings and hours worked for the state of Washington, preventing them from investigating heterogeneity in employee–employer contracting and patterns in PP. Second, we observe information about not only the establishment, but also the underlying occupation and work level, allowing us to control for potential time-varying shocks and heterogeneity across organizational structures and tasks. Finally, our data spans from 2004 to 2017, capturing the run-up to the Great Recession and its aftermath.

The third literature relates to risk sharing over the business cycle. At least since Friedman (1957), there has been an active investigation into the margins of adjustment for dealing with cyclical shocks, most notably the adjustment of hours worked (Low 2005; Swanson 2012; Heathcote et al. 2014; Blundell et al. 2016). However, non-convexities and frictions can stifle the adjustment of labor supply (Rogerson and Wallenius 2013). These factors prompted Weitzman (1984) to forcefully advocate for a “share economy” model built on profit sharing between employers and employees when the economy experienced stagflation during the 1970s. By linking compensation with profits, Weitzman suggested that firms would not have to lay as many people off and real wages would adjust to cyclical factors. While we cannot quantify the welfare effects associated with nominal wage rigidity as in Ehrlich and Montes (2020), our results suggest that the flexibility of these contracts moderates fluctuations in employment and amplifies fluctuations in compensation over the business cycle. In particular, we contribute to an emerging literature on the role of flexible work arrangements, as in the case of ridesharing (Koustas 2018; Chen et al. 2019).

The structure of the paper is as follows. Section 2 provides the theoretical background about why companies use PP. Section 3 introduces the data and measurement strategy. Section 4 documents four stylized facts about PP and FW jobs. Section 5 estimates the cyclicality of employment and compensation growth in PP and FW jobs and provides several robustness exercises. Section 6 concludes.

2. Why Do Firms Use PP?

PP compensation comes in many shapes and sizes: piece-rates, bonuses, commissions, stock options and equity, and profit sharing are the main categories. Firms use PP for two reasons: (i) to influence the quality of candidates who select into their firm in the presence of a heterogeneous labor force and (ii) to align incentives to encourage higher productivity in the presence of unobserved effort (Lazear 1986). While stock options, equity, and profit sharing are typically used more for their selection effects (Oyer and Schaefer 2005), commission and bonus schemes are typically more associated with incentive effects. However, firms ultimately must balance the provision of incentives with the heightened risk-sharing that PP contracts provide over more stable FW schemes since individuals are risk averse (Holmstrom 1979).

The typical rationale for PP focuses on static selection and incentive effects. For example, Lazear (2000a) provides arguably the best known example of an organization that adopted PP and experienced a significant increase in productivity, exploiting within-person variation. These results have been replicated many times in a variety of industries and institutional settings (Paarsch and Shearer 1999, 2000; Shearer 2004; Bandiera et al. 2005; Griffith and Neely 2009). The adoption of PP is largely driven by two factors (Prendergast 2011): (i) the noisiness of individual output and (ii) the degree of multitasking. For example, if distinguishing the contribution across employees in an organization is costly, or rewarding one type of output comes at the expense of another type, then simply paying a FW provides greater incentives.

In this sense, shocks to monitoring technology or the ease of measuring output will affect the returns to using PP. We provide two illustrative examples. First, a rise in information technology, which has manifested itself in the expansion of both capital expenditures (Stiroh 2002) and employment (Gallipoli and Makridis 2018), could potentially explain the historical increase in the share of PP contracts (Lemieux et al. 2009). For example, while work away from the office was traditionally difficult to monitor, mobile phones allow employees to submit time worked from distant locations, enable interactions among team members and managers, submit expense reports and other paper work while traveling, and more. Second, a rise in competition could also explain the rise of PP. Since competition affects the variance of firm profits, incentives to achieve cost reductions (e.g., through explicit cuts or innovation) may rise (Raith 2003). While some evidence suggests that competition is increasing at a local level (Rinz 2018; Rossi-Hansberg et al. 2018), competition could also be weakening at a national level (Autor et al. 2020).

Turning toward a dynamic setting with frictions, there are at least two potential reasons for heterogeneity in PP. One reason is that information about the benefits of performance compensation might diffuse slowly and/or be difficult to obtain. For example, if a firm was operating in a highly unionized state, but the state adopts right to work laws and union membership declines, the benefits of transitioning toward more competitive compensation contracts might not be immediate (https://www.journals.uchicago.edu/doi/abs/10.1086/707081?journalCode=jle); organizational best practices might take time to adopt as companies experiment with human resource practices. Similarly, Bloom et al. (2013) implement a randomized experiment among Indian textile manufacturers, finding that the provision of management consulting services was linked with a direct and sustained increase in plant-level productivity. These productivity differences among treated and control plants remained even 10 years later (Bloom et al. 2020).

A second reason is that firms face heterogeneous adjustment costs to capital and labor based on their product or local talent pool. For example, the presence of search costs means that firms retain some of their market value by avoiding layoffs and the loss of skilled workers (Merz and Yashiv 2007). To the extent higher skilled workers take longer to find, organizations with a higher demand for skilled workers may use more flexible employment contracts that help cushion against uncertainty over the business cycle. Conversely, organizations with greater adjustment costs of capital may face incentives to lock in contracts in advance before the realization of cyclical shocks. For example, if an organization can lock in wages during a boom, then the threat of termination coupled with above market pay may create countercyclical effort (Lazear et al. 2016; Bils et al. 2020).

3. Data and Measurement

3.1 National Compensation Survey

We primarily draw from under-utilized quarterly establishment micro-data from the NCS to understand the heterogeneous dynamics of PP and FW jobs over the business cycle. The NCS is a quarterly, nationally representative establishment-based survey that is used by the BLS to produce measures of changes in compensation (the Employment Cost Index), compensation levels, and the incidence and provision of employer-provided benefits. We measure what employees ultimately care about—total compensation, not just wages.⁶ Other data are not suited to capture total compensation dynamics. Moreover, while employers in both the private sector and state and local government are included in the NCS, we restrict our sample to those establishments in the private sector. Between 2004 and 2017, there were anywhere from 7,000 to 14,000 establishments in a given quarter and 30,000–60,000 jobs. The total number of observations is approximately 2.4 million.

Establishments are tracked for 5 and 3 years in the first and second parts of the sample, respectively, due to a change in the NCS policy for its rotation groups. The structure of the data provides us with a panel to track quarterly job-level outcomes within an establishment over the Great Recession. We weight all our observations by the NCS job-level sample weights. For most of the period, data were collected from a three-stage probability sample: local areas (metropolitan), establishments within the sampled areas, and jobs within the sampled establishments. Some areas were selected with certainty according to their size, whereas others were selected based on a probability. Jobs within each establishment are also sampled probabilistically based on the number of employees working in each job.

Usually four to eight jobs are sampled within each establishment, each of which is labeled as having either an incentive pay component or not, providing within-establishment and job variation over time. Jobs are selected in the following fashion. When a BLS field economist contacts an establishment, the employer will provide a list of all employees, which is adjusted to match the NCS scope. Individuals are randomly selected with their corresponding jobs and the field economist classifies the job with the appropriate Standard Occupational Classification (SOC) code, together with a number of other characteristics about the job, ranging from job duties to compensation.

We also observe the work level for each observation ranking on a scale of 1–15 (corresponding to the general schedule for Federal government jobs), constructed from established criteria used by field economists when surveying employers. For example, a score of one often signals an entry-level worker, whereas a score of 15 may signal a high-level executive. Work level explains approximately 70% of the variation in individual compensation, which illustrates that these classifications capture important differences in skill across jobs. Average hourly compensation is measured by taking the ratio of total compensation for all workers within a particular type of job and the number of hours worked by all workers in that job within a given establishment. We produce measures of real compensation using the deflator for personal consumption expenditure (PCE) excluding food and energy (Q2:2017 base), although we have replicated our results in nominal terms so that they are also informative for the debate on nominal wage rigidity.

We follow prior literature in defining PP according to whether at least one of the following conditions hold: (i) the pay is tied, at least in part, to commissions, piece rates, production bonuses, or other incentives based on production or sales, and (ii) the job has a non-production bonus (Gittleman and Pierce 2013, 2015).⁷ Field economists identify workers in jobs as having time or incentive pay according to whether the worker’s pay is based directly on actual production of the worker versus solely the number of hours worked. Time-based workers are those whose wages are based solely on an hourly rate or salary, whereas incentive workers are those whose wages are based at least partially on piece rates, commissions, or production bonuses. Administered by the BLS each quarter, the NCS is unique in that it is the only source that contains detailed data not only on traditional labor outcomes, but also non-wage compensation (e.g., benefits) and the type of contractual arrangement across a subset of sampled jobs within each establishment.

One limitation of the data, however, is that it measures compensation for the job, rather than the individual. This means that we cannot distinguish between average hourly compensation for new hires versus incumbents, which has been an important distinction in recent work (Bils et al. 2020). Nonetheless, our data still confer several advantages over existing data sources on top of the direct measurement of PP status. First, compared with the Panel Study of Income Dynamics (PSID), which contains heavy measurement error in labor supply and income (Bound and Krueger 1991; Bound et al. 1994), as well as the National Longitudinal Survey of Youth (NLSY) to a lesser extent, the NCS data come directly from establishment records. Second, compared with the CPS, which contains measurement error in the classification of workers into industries and occupations (Mellow and Sider 1983; Kambourov and Manovskii 2013), the NCS coding is based on interviews with the establishment. Third, unlike in both the PSID and NLSY, which contain small samples of individuals who cannot be linked to their employer, the NCS surveys roughly four to eight jobs in the same establishment. The variation within the same establishment allows us to control for important time-invariant differences (e.g., management) that have challenged prior contributions (Lemieux et al. 2009, 2014).

3.2 Panel Micro-data Containing PP Classifications

We also augment our main analysis with additional longitudinal data from the NLSY from the BLS between 1979 and 2014 from the NLSY79 and NLSY97 cohorts. The NLSY79 covers some 12,686 youths between ages 14 and 22 years in 1979, interviewed annually each year until 1994 and, since then, interviewed biennially. The NLSY97 covers roughly 9,000 youths between ages 12 and 16 years in 1996, interviewed annually each year subsequently. We restrict the sample to full-time workers and deflate annual earnings. The final sample contains 219,763 person-year observations with 163,238 coming from NLSY79 and 56,525 coming from NLSY97; between 4,500 and 8,000 individuals are surveyed every year through one of the two cohorts. We follow Lemieux et al. (2009) in defining a PP worker as one who receives bonus, piece-rate, or commission at least once with the same employer.

4. Empirical Patterns for PP

One of the advantages of our data is that it contains a direct measure of PP status. This allows us to clearly separate between PP and FW jobs. While there is already evidence of a decline in the share of PP over the past decade (Gittleman and Pierce 2013), we now document four empirical patterns.

First, there is considerable variation in the relative compensation differences between PP and FW jobs throughout the job hierarchy. Moreover, there is significant cross-sectional variation in the incidence of PP across industries and occupations. Second, both hourly wage and total compensation growth rates are significantly larger in PP jobs, relative to FW jobs, over the entire business cycle. Third, the share of PP is increasing in employer size. Fourth, the incidence of PP within an establishment is consistent with its provision being determined by firms, related with managerial and compensation policy.

4.1 Hourly Compensation, Employment, and the Incidence of PP

We begin with a comparison between the types of PP and FW jobs. Since part of our identification strategy will exploit differences in employment and compensation outcomes within similar work levels—that is, jobs that have similar responsibilities and fall closely within the same hierarchy—we examine the differences in average compensation per hour and employment across these work levels. Table  1 documents these differences.

First, there are meaningful differences in average hourly compensation differences between the two types of jobs, which we define as the PP premium, ranging from 0.06 and 0.24 log points across the job ladder.⁸ For example, whereas the move from work level 2 to 3 involves a 0.27 log point jump for PP jobs, it is a 0.22 jump for FW jobs, culminating in a 0.24 log point difference within work level 3. Although the rise in average hourly compensation across work levels slows in the middle of the job distribution, the increases begin growing again at the top of the job ladder. For example, the move from work level 13 to 14 involves a 0.23 (0.22) log point jump for PP (FW) jobs. These differences may reflect that a larger share of promotions come from the upper deciles of lower ranked jobs (Baker et al. 1994) or from right-skewness in the ability distribution (Lazear and Rosen 1981).⁹

Second, while the PP premium is nearly always positive across the job ladder, it is not monotonically increasing. Whereas the premium is highest (at 24%) in work level 3, it is lowest (at 6%) in work level 7. Given that the share of employees covered by PP contracts is monotonically increasing throughout the job ladder, growing from 22% in work level 1 to 73% in work level 15, this pattern likely reflects a combination of incentive and selection effects. For example, as PP contracts become more prevalent at higher levels, the quality necessarily declines, thereby lowering the PP premium. Moreover, the heterogeneity and non-monotone patterns of the premium underscore that PP contracts are not simply a proxy for skill. For example, Wu (2017) develops a model where firms use incentive contracts to elicit unobservable effort, which matters more in managerial and business jobs that exhibit a greater span of control.

Having examined the differences in compensation and employment across work levels by contract, we turn toward the incidence of PP across industries and occupations in Figure  1. For example, whereas the financial sector has the highest fraction of PP workers at nearly 70%, leisure and hospitality have the lowest at 20%. (Some workers in leisure and hospitality receive tips, but, since tips are not an employer cost, they are not tracked by the NCS.) There is significant heterogeneity across the remaining major industries, ranging from professional services with nearly 50% to construction with under 40%. We also see that PP contracts are overwhelmingly most common among managers and business professionals with an incidence of nearly 60%, followed by several other occupations that include both non-routine jobs (e.g., professional workers) and blue-collar jobs (e.g., production and installation/repair workers).

Figure 1.

Incidence of PP, by Major Industry and Occupation. Note: The figures plot the fraction of PP employees by major industry and occupation. Source: NCS 2021.

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Figure  2 provides an additional graphical illustration of the relative proportion of PP workers when splitting by industry × occupation. There are a couple of very stark examples. Consider, for example, the service-by-mining and professional-by-hospitality cells, which contain under 10% and 20% of workers compensated via PP, respectively. In this sense, while professional services occupations have 60% of employment in PP, certain industries have a very low incidence (e.g., hospitality). We have also explored dispersion within narrowly defined occupation level, finding that six-digit occupation fixed effects explain only 34% of the variation in PP, which again points toward PP as a design feature for an organization.

Figure 2.

Share of PP Workers, by Industry × Occupation. Note: The figure plots the share of PP workers by major two-digit industry and occupation cell. Source: NCS 2004–2017.

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4.2 Magnitude of Hourly Compensation Changes

We now explore the magnitude of changes in real average hourly compensation in PP and FW jobs. Table  2 documents these over three periods of our sample: 2005–2007 (pre-recession), 2008–2009 (recession), and 2010–2014 (recovery).

First, PP jobs exhibit systematically higher growth in hourly compensation growth. For example, whereas real average hourly compensation and wages grew at a rate of 1.4–1.6% for PP jobs between 2005 and 2007, they only grew by 0.8–0.9% for FW jobs over those same years. Between Q2:2008 and Q2:2009, average hourly compensation and wage growth increased by 2.3–2.4% for PP jobs and by 0.6–0.7% for FW jobs, which reflects the sharp decline in employment and the laying off of lower productivity workers first during the financial crisis (Foster et al. 2016; Deming and Kahn 2018). However, average hourly compensation and wage growth remained high for PP jobs during the recovery from 2010 to 2014.

Second, hourly compensation growth has been greater than wage growth, reflecting that an increasing share of compensation comes from non-wage benefits. For example, between 2005 and 2007, hourly compensation growth is 1.6% (0.9%) for PP (FW) jobs, whereas it is only 1.4% (0.8%) for wage growth. Similarly, between 2010 and 2014, hourly compensation growth is 2.3% (compared with 2% for wage growth) for PP jobs, relative to −0.09% (and −0.3%) for FW jobs. The one deviation is during the height of the financial crisis for FW jobs, which likely stems from the fact that FW jobs were more likely to lay people off in response to the unanticipated shock and the first employees to be laid off were the less productive ones (Hershbein and Kahn 2018).¹⁰

4.3 PP and Employer Size

We explore the incidence of PP across the distribution of employer size. Table  3 shows that larger employers exhibit a higher incidence of PP jobs. For example, the share of PP is 36% among employers with under 50 employees, but it is 52% among employers with over 500 employees. We also find that the correlation between the share of PP jobs in an establishment and its number of employees is 0.09, which is partially attenuated since we only observe a sample of jobs within each establishment.

While the fact that the share of workers with PP is increasing in employer size may not be surprising—although we believe the empirical estimates are useful for disciplining structural models that embed principal–agent problems—we note that the share of incentive pay is decreasing in employer size. One explanation could stem from a corollary of Lucas (1978) where managers in larger firms are able to exercise a larger span of control. In this sense, the strength of incentives for these managers and executives could be greater, but the share of employees receiving these types of contracts is smaller since the number of employees outpaces the growth in incentives.

4.4 PP as a Firm Decision

We now examine whether the provision of PP is a decision that is made more by the firm, tied to, for example, its decisions about management practices and compensation. We begin with the result that 84% of establishments with at least one PP job also have at least one other job with PP. We subsequently find the following:

• 35% of establishments with one PP job have at least one FW job.

• 82% of establishments with one FW job have at least one other FW job.

• 29% of establishments with one FW job have at least one PP job.

If PP was not driven as much by firm decisions, then we would expect to see much more dispersion in these patterns. For example, if prospective employees bargained over it, then there would be much more idiosyncrasy across establishments in the incidence given the heterogeneity in employees that we see even within the same firm. Instead, we see that having some PP in the establishment means that there is a high likelihood that there is additional PP in the establishment; similarly for FW jobs.

5. Quantifying Asymmetry in Hourly Compensation and Employment Growth by Contract Type

5.1 Empirical Specification

While we do not observe individuals directly, individuals are grouped into a job using the occupational classification of the establishment, work level, union status, incentive pay, and full-time status, which controls for a significant amount of heterogeneity. We use state-level employment growth primarily because it is a comprehensive measure of local business activity and follows convention from the literature (Haltiwanger et al. 2018), but our results are robust to using metro/micropolitan areas (as we did in an earlier version). We cluster standard errors at the state-level to allow for arbitrary degrees of correlation across establishments within-location.

The inclusion of work level and establishment fixed effects is especially important for two reasons. First, they overcome the bias that arises from individuals non-randomly sorting into PP jobs based on unobserved ability (Lazear 1986). Failing to account for positive sorting between productive employees and establishments would cause us to overestimate the role of PP (Lazear 2000a). Second, they overcome the bias that arises from the fact that more productive establishments might not only use more PP, but also attract and promote better managers (Bloom et al. 2014).^11,12 Our identification strategy compares the response of employment and compensation growth to local shocks among similarly rated jobs within the same establishment, addressing both employee and employer selection effects.

We nonetheless outline three potential remaining threats to identification, for which we discuss and present robustness results in Online Appendix Section A.6. First, since we only observe jobs, rather than individuals, it is possible that fluctuations in employment and compensation growth simply reflect changes in the quality of the marginal worker. This concern is important for identifying the cyclicality of real wages (Solon et al. 1994; Haefke et al. 2013). While our inclusion of work level, establishment, and occupation fixed effects play an integral role in controlling for potential unobserved heterogeneity in the marginal worker, a concern about unobserved heterogeneity nonetheless remains.

Second, while our measurement of labor demand shocks using state employment growth follows a large literature in labor economics (Blanchard et al. 1992; Hershbein and Kahn 2018), it is possible that employment growth reflects both demand and supply shocks. For example, if information technology is becoming more widely available during these years, and information technology benefits PP jobs more than their counterparts because of a reduction in the cost of monitoring, then our estimates may be biased. To address this concern, we adopt the standard solution of a Bartik-like instrument that exploits the pre-sample (2003) exposure of different industries to national employment growth patterns to isolate variation in labor demand. The first-stage on the interaction is highly significant: a regression of quarterly state employment growth on the Bartik instrument, conditional on state and time fixed effects, produces an F-statistic of 94; see Figure A.6 in the Online Appendix for further details on the first-stage and diagnostics for the exclusion restriction.

Third, the use of PP could be correlated with business cycle fluctuations. In general, jobs that are classified as PP in one year are PP in the next year too; establishments infrequently alter the use of incentive contracts for a given job within a 3- or 5-year period. One reason for this could be managerial inertia (Bloom et al. 2014). Another could be the complementarity between incentives and management (Brynjolfsson and Milgrom 2013). Moreover, bias would only occur if firms alter their use of PP in expectation of future state employment growth.

5.2 Main Results

If PP contracts allow firms greater agility to adapt to uncertainty, we may expect that $π>0$ under both outcome variables, which would imply that PP jobs have higher hourly compensation and employment growth. The main coefficient of interest, however, is δ, which characterizes the potentially asymmetric response of PP jobs over the business cycle. If PP jobs adjust more easily on the intensive margin of compensation, then $δ>0$ when the outcome is hourly compensation and $δ<0$ when the outcome is employment. In particular, that means that PP jobs have relatively more cyclical compensation growth, but less cyclical employment growth. Our main results are consistent with theoretical predictions about the incentive effects of PP contracts. In particular, PP jobs are more flexible since variable compensation allows employers to ramp up or down employee compensation or hours over the business cycle, rather than having to hire and fire workers altogether.

The marginal effect of an employment shock in PP jobs, $γ+δ$⁠, governs the cyclicality of the employment and hourly compensation growth. Table  4 documents the results associated with Equation (1) under several specifications. Column 1 begins by presenting the raw regression coefficients between both job-level employment and compensation growth and local demand shocks, suggesting that a one pp rise in state employment growth is associated with a 0.338pp increase in employment growth in FW jobs, but only a 0.177pp $(=0.338−0.161)$ increase in PP jobs (Panel A, column 1). We also observe that a 1pp rise in state employment growth is associated with a 0.043pp decrease in hourly compensation growth in FW jobs, but a weaker 0.013pp decline in PP jobs (Panel B, column 1). To put these in perspective, these asymmetries are economically meaningful: 47–70% of the cross-sectional effects.¹³

However, there are several reasons to suspect that these coefficients are biased. For example, more productive workers might sort into more productive establishments, which could generate upward bias if these establishments have higher employment and hourly compensation growth. Once we add establishment and time fixed effects in column 2, our results now suggest that a 1pp increase in state employment growth is associated with a 0.29pp increase in employment growth rate of FW jobs, but a 0.106pp $(=0.29−0.184)$ increase in the growth rate of PP jobs (Panel A), whereas a comparable shock is now associated with a 0.024pp decline in the growth rate of hourly compensation in FW jobs and an approximately null (but potentially positive) 0.005pp $(=−0.024+0.029)$ rise in the growth rate of PP jobs (Panel B).

To the extent there is sorting of more productive workers into PP jobs even within the same establishment, since there is significant heterogeneity in the incidence of PP across work levels (see Table  1), we must introduce work level fixed effects, which exploit variation among similarly ranked jobs within the same establishment over time. Here, we find a 1pp rise in state employment growth is associated with a 0.084pp $(0.313−0.229)$ rise in the employment growth rate of PP jobs, versus 0.313pp in FW jobs, and a 0.006pp $(−0.018+0.024)$ rise in the hourly compensation growth rate of PP jobs, versus a 0.018pp decline in FW jobs. Our finding of an acyclical response of hourly compensation growth among FW jobs is consistent with prior empirical contributions on downward nominal wage rigidity (Le Bihan et al. 2012; Barattieri et al. 2014; Sigurdsson and Sigurdardottir 2016). This could emerge as a result of attenuation bias in samples of predominantly FW workers when the econometrician cannot distinguish employment in different contracting arrangements.

Are these different layers of fixed effects informative about the magnitude of incentive versus selection effects? Comparing columns 1 and 3 in Panel A, we see that the more “causal effect” in column 3 for PP workers is roughly 47% the magnitude of the raw effect in column 1, suggesting that selection effects account for slightly more than half of the overall volatility in employment growth for PP jobs. In contrast, selection effects are much greater among fixed wage jobs, which is consistent with the view that FW pay jobs tend to attract a more heterogeneous and skilled workforce (Lazear 1986). Turning toward Panel B, the “causal effect” accounts for roughly 31% of the overall effect for PP jobs, whereas it accounts for 42% among FW jobs.¹⁴ Admittedly, composition effects may still be present since we cannot trace out the response of the same worker over time, but these comparisons are nonetheless useful heuristics to gauge the importance of controlling for heterogeneity across establishments and work levels.

While our fixed effects may help overcome the potential for non-random sorting, it is still possible that we are overlooking important time-varying technology shocks, like increasing diffusion of information technology, that might heterogeneously impact PP and FW jobs. Column 4 now introduces two-digit industry × year fixed effects, which produces estimates that are statistically indistinguishable from our baseline in column 3. Moreover, since occupations are closely linked with skills and tasks (Autor and Handel 2013), column 5 introduces two-digit occupation × year fixed effects, which again produces statistically indistinguishable estimates. The fact that the inclusion of these occupational fixed effects does not alter our baseline results suggests that any time-varying trends arising from the boom-and-bust of the Great Recession, such as the decline in routine jobs (Cortes et al. 2017) and demand for cognitive skills (Beaudry et al. 2016), is not a source of bias.

5.3 Evaluating Composition Effects

Table A.1 in Section A.4 of the Online Appendix shows that these results are robust to an alternative measurement strategy where we define a job as PP if it has ever received performance related pay over its 3–5 year window in our longitudinal data. We also assess the potential for composition effects over the business cycle—that is, how the quality of the labor force within these two sets of contract types might be changing.¹⁵ Figure A.5 in Section A.4 of the Online Appendix shows that, although the share of jobs with zero employment growth oscillates between 64% and 72%, the patterns between PP and FW jobs have a 0.79 correlation. That means the magnitude of composition effects would have to be implausibly large in certain quarters to account for our results given that employment within a job does not change roughly two-thirds of the time. While there could still be composition changes that result in no change in employment (e.g., one worker leaves and another one joins), we suspect that these instances of zero employment growth would contribute to attenuation bias.

Second, Online Table A.2 presents results using weights that hold fixed changes in composition across 531 industry–occupation cells. The results are statistically indistinguishable. While this only controls for composition at an industry × occupation level, the invariance of the results suggests that selection on observed characteristics, such as industry and occupation, are minor and, therefore, cast doubt on the possibility that selection on unobserved characteristics is of great importance.

Third, since hourly wages are a useful proxy for latent productivity, we can compare the wages of incumbents versus entrants in PP and FW jobs to see if they display differential cyclicality. Using the monthly CPS, we aggregate hourly wages to the two-digit NAICS × three-digit SOC level and compute the logged wage difference between job switchers and incumbents. We subsequently regress it on the (monthly) national unemployment rate, an indicator for whether the industry × occupation has a share of PP workers above the median, and their interaction, conditional on demographic controls for each cell. Because the sample is sparsely populated in many of these cells, we weight by the number of observations per cell to reduce noise. We find a coefficient of 0.11 on the interaction between the unemployment rate and the indicator for PP status in the occupation–industry cell, but it is statistically insignificant (p-value = 0.8). If we do not use weights, the interaction is −0.003 (p-value = 0.9). In sum, this suggests that composition effects could not account for our overall effects.¹⁶

5.4 Alternative Explanations

We now investigate two additional concerns with our main results. First, the asymmetric response of employment and compensation growth could reflect unobserved supply-side shocks. For example, if PP workers benefit more from increases in information technology, then unobserved increases within a state could account for these effects.

To overcome the potential endogeneity of these local labor market shocks, we instrument for state employment growth with a Bartik-like measure that exploits the pre-sample (2003) exposure of an industry in a state to national shocks (see Section A.6 of the Online Appendix for details). Column 6 presents these estimates. While the direct effect is noisy, the key interaction effect holds: PP jobs exhibit less volatility in employment growth than their FW counterparts—an asymmetry that is even larger than the baseline—and more volatility in hourly compensation growth than their FW counterparts—slightly less than the baseline.

Second, another concern is that these differences in the volatility of employment and compensation are simply driven by higher ranked executives who receive more skewed compensation. While these employees exhibit systematically greater and more volatile earnings than their counterparts, they constitute a small employment share in organizations and our work level fixed effects should absorb these differences. Nonetheless, columns 7 and 8 now partition the sample into two sets: jobs between work levels 1 and 7 and between 8 and 15. Perhaps counterintuitively, we find that nearly all of the asymmetry resides within jobs between levels 1 and 7: a 1pp increase in state employment growth is associated with a 0.342pp increase in the employment growth rate for FW jobs, but a 0.112pp increase for PP jobs. We similarly find that a 1pp increase in state employment growth is associated with a statistically weak 0.017pp decline in the hourly compensation growth rate for FW jobs, but a 0.011pp increase in PP jobs.¹⁷

While our data do not allow us to measure the intensive margin of labor supply reliably because we only see the regularly scheduled hours of work associated with jobs, we can draw on the American Time Use Survey (ATUS) to investigate the correlation between the volatility of labor supply and the incidence of PP at a three-digit occupational level.¹⁸ We follow Aguiar and Hurst (2007) in assembling the data, but collapse at the three-digit occupational × year group level where we bundle 3 years to increase the sample size (2004–2006, 2010–2012, and 2015–2017). We subsequently weight by the number of observations in an occupation × year group. Figure  3 plots the relationship for 2010–2012, producing a correlation of 0.33 and implying that occupations with greater shares of PP also exhibit greater volatility in hours worked.¹⁹ This is consistent with an interpretation where PP is used to encourage greater effort over the business cycle, thereby creating more volatility in hourly compensation than employment.

Figure 3.

Dispersion in the Intensive Margin and PP. Notes: The figure plots the logarithm of the standard deviation of hours worked per day across all respondents within a given three-digit occupation × year group and the corresponding share of PP workers for the years 2010–2012. The dispersion in the intensive margin of labor supply is obtained by following Aguiar and Hurst (2007) in cleaning the ATUS and focusing on three-digit SOCs over 3-year groups to increase the sample representativeness. The observations are weighted by the number of respondents in a given occupation × year category. Source: NCS and ATUS 2004–2017.

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We provide two ways to reconcile our findings with those from these prior contributions. First, as far as we can see, microeconomic studies have not used measures of wage income that include performance-related pay. For example, Barattieri et al. (2014) use the Survey of Income and Program Participation (SIPP), but it was not until the 2014 SIPP wave that the public files began including bonus and commission income, which are important margins of adjustment for PP jobs. Second, there are differences in sample selection resulting from attrition and the short panel component of 24–48 months in the SIPP. The fact that we find such a strong asymmetry in the response of hourly compensation growth to state employment growth suggests that pooling the two types of jobs together could explain the traditional results that favor models of downward nominal wage rigidity.

5.5 The Barro Critique and Further Robustness

Ever since at least Barro (1977), researchers have been aware of the difficulty of identifying genuine wage rigidity from heterogeneity in long-term contracting. When employers set and negotiate contracts with their employees, firms can adjust the employee wage profile even if current wages do not respond to contemporaneous shocks. One concern, therefore, is that our result of asymmetric cyclicality is driven by a heterogeneous probability for employers to engage in long-run contracting, rather than representing an actual rigidity in the contracts that FW workers face.²⁰ For example, Rudanko (2009) develops an equilibrium model where firms post long-term contracts to attract risk-averse workers—wage smoothing is, therefore, an optimal outcome in the presence of incomplete commitment.

Our identification strategy addresses this concern in several respects. For example, our inclusion of establishment and work level fixed effects removes any time-invariant heterogeneity in underlying contracting between workers and the employer that might be different between these two sets of jobs. Similarly, since we are looking at employment and compensation growth, we are identifying elasticities from variation in changes in growth rates (not levels). We nonetheless implement an additional exercise that focuses on the central burden of proof introduced by Barro [1977]—that “… it is necessary to demonstrate a link between the potential for long-term contracts and the propensity of the private economy to experience cyclical phases of more or less missed opportunities for advantageous trade.”

Having examined the main empirical concern with our results, we now implement several other robustness exercises. One natural concern, for example, is the presence of reverse causality since increases in employment and compensation at the job-level might induce changes in employment at the local level. While these forces must clearly align in the aggregate, the likelihood that reverse causality exists at the micro-level is low since none of the establishments are market makers in their respective local areas. We nonetheless run a regression of the change in logged local employment on logged job-level establishment compensation and employment, conditional on location and time fixed effects, producing coefficients close to zero with p-values of 0.992 and 0.834, respectively.

We finally turn to a more careful examination of the distribution of hourly compensation growth, displayed in Figure  4, focusing on 2005–06 and 2008–09. Specifically, we find that the average real hourly compensation growth is 0.21 pp between 2005 and 2006 and 0.13pp between 2008 and 2009 for PP jobs, whereas it is 0.067pp and 0.13pp for FW jobs, respectively. First, hourly compensation growth is larger for FW jobs during the recession, whereas the opposite holds for PP jobs: that is consistent with our main message, especially since the rise in the hourly wage during recessions generally reflects the fact that lower productivity workers are laid off first, raising the wage due to composition effects. Second, we find a twice as large of dispersion in hourly compensation growth for PP jobs.

Figure 4.

Distribution of Hourly Compensation Growth, 2005–2006 and 2008–2009. Notes: The figure plots the distribution of growth rates in average hourly compensation growth in PP and FW jobs during a boom (2005–2006) and recession (2008–2009) obtained by averaging job-by-establishment values within the same three-digit industry and year cells separately for PP and FW jobs. We also trim the sample at below/above 5% growth increases and decreases. Source: NCS 2004–2017.

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6. Conclusion

Do firms adjust employee compensation over the business cycle? While there is a large literature that has traditionally pointed toward evidence of downward wage rigidity, recent evidence suggests that compensation is more flexible than previously thought. We investigate the cyclicality of compensation and employment, focusing on the role of employee–employer contracting mechanisms. Using the NCS between 2004 and 2017, we exploit variation in the use of PP across jobs and establishments to quantify how PP contracts potentially provide organizations with greater flexibility to buffer against cyclical shocks. These contracts allow firms to adjust employee compensation, rather than laying off employees and engaging in costly search, in response to fluctuations in demand.

We began by documenting four new stylized facts: (a) there is substantial dispersion in the use of PP not only across industries and occupations, but also within, (b) hourly compensation growth is greater in PP jobs than FW jobs, (c) the share of PP jobs is increasing in employer size, and (d) the provision of PP is largely determined at the firm-level. We subsequently estimate the responsiveness of average hourly compensation and employment growth to local demand shocks. We find that a 1pp rise in state employment growth is associated with a 0.313pp rise in employment growth among FW jobs and a 0.084pp increase among PP jobs, whereas a comparable local shock is associated with a 0.018pp decline in hourly compensation growth among FW jobs and a 0.006pp increase among PP jobs. Our results are identified off of responses in employment and hourly compensation growth between comparable PP and FW jobs in the same establishment, allowing us to overcome traditional empirical challenges, including self-selection into PP jobs and within-establishment heterogeneity in managerial quality.

While Section A.7 of the Online Appendix provides some speculative evidence that the asymmetric cyclicality is driven by the incentive effects of PP, we leave this subject to future research. That is, what are the underlying incentives and/or processes within organizations that produce the asymmetric behavior between these two sets of jobs over a business cycle? Moreover, future research could use panel data from the Longitudinal Employer Household Dynamics to track workers in sectors and worker categories that tend to have higher shares of PP, but the drawback is that the measure of PP would be a proxy at best since there is no longitudinal large-scale data that tracks workers and contains information on PP.

Supplementary Material

Supplementary material is available at Journal of Law, Economics, & Organization online.

Conflict of interest statement. None declared.

We thank Matilde Bombardini, Nicholas Bloom, Julien Champagne, Steve Davis, Wouter Dessein, Andres Donangelo, Mircea Epure, Fatih Guvenen, Bart Hobijn, Joe Kaboski, Dmitri Koustas, Ioannis Kospentaris, Marianna Kudlyak, Edward Lazear, Desmond Lo, Bentley MacLeod, Andreas Mueller, Emi Nakamura, Paul Oyer, Edward Prescott, Thijs van Rens, and Richard Rogerson, as well as participants at the 2016 AEA Meetings, and seminars at Columbia University, Stanford University, the San Francisco Federal Reserve, and the Bureau of Labor Statistics. We also thank John Bishow for research assistance and Erin McNulty for answering numerous questions about the NCS. C.A.M. acknowledges the National Science Foundation (NSF) Graduate Research Fellowship and Shultz Fellowship for Economic Policy for funding. The views expressed here are those of the authors and do not necessarily reflect the views or policies of the Bureau of Labor Statistics or any other agency of the U.S. Department of Labor. The paper was formerly titled: “Does ‘Performance Pay’ Pay? Wage Flexibility over the Great Recession.”

Footnotes

References