Firm Performance and the Volatility of Worker Earnings

A. Firm Data

The results presented here are based on data from three US Census Bureau annual business surveys that collect information on revenues for a particular industry or industry group.

For each of the survey panels, a new sample is drawn every 5 years, once new information from the quinquennial Economic Census is incorporated into the sampling frame. Over the span of years in our data, new samples for ARTS and SAS started in 2001, 2006, and 2011, while new ASM panels began in 1999, 2004, and 2009. While new firms appear in the panel primarily in those years, large firms may be selected again in subsequent panels and so remain in our data set for more than 5 years.⁷ The ARTS and SAS sample firms or, in some cases, the part of a firm that operates in an in-sample industry. The ASM differs from the other surveys in that it samples establishments (individual locations) rather than firms.

We use data from these annual business surveys primarily to measure changes in firm revenues. While some firms in the ARTS and SAS report sales separately for different parts of their organization or broken down by detailed industry, we use total sales reported for the firm within a three-digit NAICS industry as our measure of firm outcomes. In manufacturing, where we have information on revenues by location, we sum revenues up to the firm/state level, which is the most detailed level at which we can combine data on firms and their employees.

B. Employee Data

Our data on employees come from the US Census Bureau’s Longitudinal Employer-Household Dynamics (LEHD) database, which draws much of its data from complete sets of unemployment insurance (UI) earnings records for US states. Workers’ quarterly UI earnings records have been matched to characteristics of their employers drawn from quarterly administrative UI reports and to demographic and employer information from other US Census Bureau data sources. Earnings covered by UI reporting include wage and salary income, commissions, tips, bonuses, and other cash payments. The various forms of earnings are not separately identified. UI earnings do not include employer payments for benefits such as health insurance or retirement savings plans.

While all states provided data for the LEHD program, the availability of data from earlier years varies by state. Our primary analysis sample of workers is selected on the basis of their employment by the firms in our business samples, as detailed in the next section. To provide some context for the variation captured in our primary analysis, we also draw a 1% sample of all UI-covered workers in 39 states for years 2000–2011 and use that sample to estimate overall levels of earnings volatility.

C. Linked Data

To construct our linked data set, we first take all of the firms (or, in some cases, industry segments of firms) in the business samples that have nonmissing and nonzero sales measures. Firms with multiple locations (“multiunit”) firms may file information using more than one federal employer identification number (EIN), so we pull all EINs used by the firm from the US Census Bureau’s Business Register.⁸ The UI employer records also include EINs, so we then use the set of EINs from the business surveys to select UI employer records for sampled firms. Firms do not always use the same tax identifiers in filing federal payroll taxes (the primary source of EINs for the Business Register) and state UI taxes (the source of EINs for the LEHD files). As a consequence, it is likely that our sample of employees is incomplete for some of the firms included in our analysis. We find EIN match rates of 84%–90% for the industries we use.

In comparing our linked sample to economic census statistics for 2012, we find that the average firm in the industries sampled for the ARTS survey (NAICS 44–45 and 72) had $4.3 million in revenues, while the employment-weighted average was $22.155 billion. This compares to linked-worker weighted average in our ARTS sample of $119 million. For professional services, those statistics are $1.9 million (firm mean), $1.189 billion (worker-weighted mean), and $1.687 billion (worker-weighted mean, our sample). For manufacturing, they are $22 million (firm mean), $5.187 billion (worker-weighted mean), and $788 million (worker-weighted mean, our sample). For finance, they are $9 million (firm mean), $6.154 billion (worker-weighted mean), and $6.165 billion (worker-weighted mean, our sample). These statistics suggest that our sample is primarily made up of larger firms, making our results more representative from the perspective of a typical worker than from the perspective of a typical firm. At the same time, we have lower match rates for workers in large firms with complex structures, particularly in retail and in manufacturing, so that on a worker-weighted basis our sample is smaller than the population of firms in these industries.⁹

D. Stayer Samples

Once we have a list of UI employer identifiers, we select all employees aged 25–59 who are employed by a sample firm in at least one year during the period the firm is in sample and have at least one “full quarter” of employment in that year. In the tables below, we refer to this set of workers as our cross-sectional sample. As is standard in using the LEHD earnings data, we treat quarter t as a full quarter if that worker has earnings reported in quarters $t-1$, t, and $t+1$ at that employer. This definition is based on the notion that the individual was likely employed for the full 13 weeks of the quarter if he or she had earnings with the same employer both right before and right after the quarter. We use only full-quarter observations in measuring earnings. This restriction serves to eliminate variation in earnings due to the number of weeks worked, but note that we cannot eliminate variation due to changes in the hours individuals work, as we do not have data on worker hours. We do have establishment-level measures of hours in manufacturing, which we use in a robustness check discussed later in the paper.¹⁰

Our regression analysis requires that we further restrict our sample of workers to those with two consecutive full years of earnings with a sample employer (“stayers”) so that we can measure the relationship between changes in worker annual earnings and the annual firm outcomes from the business data. In the least restrictive sample we use for our primary analysis, we define stayers in year t as those having positive earnings with the same employer for each quarter in two adjacent calendar years (t and $t+1$) plus 2 quarters on either end of that spell (the fourth quarter of year $t-1$ and the first quarter of year $t+2$). When we examine longer changes, we must further restrict our sample—for example, using those who are in the data for six adjacent calendar years when looking at 5-year differences. Results presented here are primarily based on samples of jobs lasting long enough to use for either 3- or 5-year changes, which we will refer to as our 3- and 5-year samples (although they require 4 and 6 years of data, respectively).¹¹

The length of the panel data sets we analyze depends on the availability of both LEHD and firm data. Our linked retail and manufacturing samples span the years 1998–2011.¹² For finance, our sample includes the years 2002–2011, and for professional services it includes the years 1992–2011. Because more states are included in the LEHD data in more recent years, our samples are larger for more recent years, and so our estimates weight recent years more heavily. We should also note that because samples are refreshed every 5 years, the 5-year samples are particularly large for intervals starting with the first year of data for a new panel.

E. Summary Statistics

Table 1 shows summary statistics for our analysis sample for the long-run stayers who are included in our regression analyses, alongside two other comparison samples. One comparison sample—the cross-sectional sample described above—includes all workers aged 25–59 linked to our sample of firms in that industry group with at least one full quarter of earnings. We include these statistics to serve as a point of comparison for the more restrictive samples we use for our primary analysis. The age restriction and the requirement of one full quarter of earnings eliminates many transient and low-earnings jobs. Annual average earnings for these cross-sectional samples range from $51,300 in retail to over $200,000 in finance.¹³ The ranking of pay by industries probably conforms with most readers’ expectations, but the pay levels may seem surprisingly high. Part of the high average is explainable by the sample restrictions—for example, staying with the same retailer for many years is probably much more common among store managers than cashiers. But in addition these means are based on the full distribution of UI-covered earnings and are not top coded, and so they will be influenced by workers with very high earnings, such as executives. Because the statistics are worker weighted, averages for firm-side variables, such as revenues, reflect the characteristics of larger firms.¹⁴

The rows labeled “One-year difference” further restrict the samples to observations on stayers at firms in sample for adjacent match years.¹⁵ Restricting to stayers raises the average age by approximately 2 years and raises average annual earnings substantially. Further restricting our samples to allow estimation based on longer-run changes of course reduces observation counts and further raises average earnings in all sectors except finance. The 5-year samples are also more affected by the cycle of sample refreshment, which for our retail and finance samples means that a large portion of the 5-year sample observations fall in the interval 2005–2010 and so reflect variation during the Great Recession.¹⁶

A. Firm Shocks

Revenues are presumed to act as firm-side drivers affecting worker earnings. Letting j index firms and t index time, log revenues R_jt follow

B. Permanent versus Temporary Shocks

It is useful to specify permanent and temporary components to the innovations Δϵ_jt and to distinguish true from measured values. True error shocks ${ϵ}_{\mathit{jt}}^{*}$ incorporate a random walk to capture a permanent component and a moving average process to capture transitory effects:

C. Worker Earnings

Log earnings for worker i are presumed to depend on time-varying observable factors, permanent and temporary firm-side shocks, worker fixed effects h_i, and a shock ψ_ijt:

D. Estimation

Estimating equation (9) directly is difficult since firm-side revenue growth includes measurement error and both temporary and permanent innovations. Earnings growth does not depend on the measurement error part of firm revenue growth, but even with no measurement error we would have difficulty distinguishing the α and β responses, as we do not directly observe the separate components of $\mathrm{\Delta }{ϵ}_{\mathit{jt}}^{*}$. We adopt two complementary approaches that we think offer sensible information, particularly about α. In this section we relate our proposed OLS and IV model estimates to the parameters in the stochastic setup above.

One approach involves estimating OLS regressions of wage growth on firm sales growth for various lengths of change (we estimate models for 1-, 3-, and 5-year changes). The idea is that correlations among longer differences should more heavily reflect the impact of permanent shocks rather than transitory shocks or measurement error. Consider an OLS regression on 5-year changes from ($t-3$) to ($t+2$), an interval that spans the 1-period changes above. The stochastic setup implies

If there were no measurement error, the OLS coefficients would reflect a weighted average of α and β, with α more heavily weighted for longer changes. If there were no measurement error and α equaled β, the ratio of equation (12) to equation (13) would give the common parameter $\alpha =\beta$. Measurement error biases coefficients toward zero, but less so as the difference length increases. Generally speaking, there is a difficulty in distinguishing between the effects of measurement error and different responses to permanent and transitory firm shocks (${\sigma }_m^2=0$ and $\alpha >\beta$ could look the same in the data as ${\sigma }_m^2>0$ and $\alpha =\beta$). This seems intuitive, since measurement error is transitory in the setup.

In our second approach, we follow Card, Cardoso, and Kline (2016) and use revenue growth at different dates as instruments, in particular choosing instrument dating that overlaps the independent variable but without common end points. For instance, the IV coefficient in a 1-period change model using the 5-period change $\left({ϵ}_{j,t+2}-{ϵ}_{j,t-3}\right)$ as an instrument is

Instrumenting with a just barely overlapping change would return α if $\theta =0$ but not otherwise. For example, a 3-period earnings growth model instrumented using a 5-period change in firm revenues returns

To summarize, we expect OLS coefficients to rise with difference length and to give a better measure of the earnings response to permanent shocks for longer changes. However, we cannot determine how much of any observed pattern in OLS coefficients to attribute to measurement error versus different responses to transitory and permanent shocks. We expect the IV strategies identifying α to return larger coefficients because they avoid the variation associated with measurement error and the transitory shocks (assuming $\alpha \ge \beta$). Higher IV coefficients are consistent with both measurement error in firm revenues and with a greater response to permanent than transitory shocks. Finally, we would take similar OLS and IV coefficients as some evidence in favor of small measurement error along with $\alpha \approx \beta$, meaning that earnings responses to transitory and permanent shocks are similar.

A. Baseline Results

Table 3 presents OLS regression results for four industries—manufacturing, retail, professional services, and finance (as defined in Sec. III). The table shows estimates for 1-, 3-, and 5-year changes. To compare shorter and longer-run changes on the same sample of workers and firms, we restrict our sample to firms and workers who remain in sample long enough to be included in 5-year changes. The OLS estimates indicate that very little of the firm-level shocks in revenue are passed to worker earnings. In manufacturing, shown in the top left panel, the estimate is a highly significant 0.007 for 1-year changes. The estimates for 3- and 5-year changes are larger (0.012 and 0.013, respectively) but are still quite small. Estimates for professional services and retail are generally a bit larger than those for manufacturing but still small. While we expected to find larger effects for finance because that is where we thought variable pay should be most important, there is little evidence that firm-level performance is transmitted to worker earnings in the finance sector.

Table 4 reports results for IV models where the change in firm revenues is instrumented with nonoverlapping shorter or longer changes. The columns refer to changes in worker log earnings (the dependent variables), while the rows refer to changes in firm log revenues (the instruments). For example, the coefficient 0.023 reported for manufacturing is the estimate obtained from regressing 1-year changes in log worker earnings on 1-year changes in firm log revenues, with the 3-year change in log revenues used as an instrument. The IV estimates for manufacturing are generally larger than the OLS estimates shown in Table 3 and are now generally roughly 0.02. The IV estimates are also larger for professional services, where some of the estimates are now close to 0.05. The results for retail vary rather substantially from .024 to .067 and appear to be sensitive to specification.²¹ Again, we find little evidence of transmission of firm-level shocks to worker earnings in finance.

It is useful to compare our results for the United States to others in the literature. Our estimates are in the neighborhood of those found by Arai (2003) for Sweden, of those found by Margolis and Salvanes (2001) for Norwegian manufacturing, and of those found by Martins (2009) for Portuguese manufacturing; these form the lower end of the range of estimates identified by Card, Cardoso, Heining, and Kline (2016). There are many reasons related to both data and measurement that could account for the lower rates we estimate in the United States compared with those from European countries. But issues of measurement aside, lower pass-through of firm-level shocks to workers is somewhat unexpected given the existence of greater labor market flexibility in the United States. For example, the United States has the lowest rates of unionization and collective bargaining agreements among Organization for Economic Cooperation and Development (OECD) countries (Freeman 2007).

One explanation is that while unionization and collective bargaining may reduce wage flexibility at a more aggregate level, the presence of such institutions may not necessarily preclude wage adjustments at the firm level (Teulings 1997; Cardoso and Portugal 2005). Another possibility is crowd out of private insurance by public insurance (Ellul, Pagano, and Schivardi 2017). The United States offers less generous unemployment and disability insurance benefits compared with most OECD countries (OECD 2010, 2016). This type of crowd out is unlikely, however, since these benefits are tied to nonemployment rather than to wage cuts. Another possible explanation is that US firms provide less employment insurance and are more likely to lay off workers in the event of a negative productivity shock.

In our paper as well as in Guiso et al. (2005), the focus has been on earnings changes among workers who are continuing with the firm. We show that stayers are a select sample compared with a broader sample of employees working at least one full quarter. Thus, a focus on earnings risk, conditional on employment, leaves open the important question of whether firms readily transfer employment risk by laying off workers even as they reduce wage risk for the workers who are retained.²² Lamadon (2014) finds that a significant fraction of earnings risk is due to unemployment and job mobility. We view exploring employment risk in conjunction with wage insurance parameters as an important topic for future research.

In the results reported above, we have restricted our sample to the 5-year-change sample in order to compare shorter- and longer-run changes holding sample composition constant. In doing so, however, we lose a large share of our original sample, particularly in the retail sector, where the average tenure of workers is shorter. One concern is that our 5-year-change sample is not very representative of typical workers or firms in the industry. We have examined how much this restriction affects our results by repeating our analysis of 1- and 3-year changes on a sample that requires staying in our data for four consecutive years (our 3-year-change sample) rather than six consecutive years. These results are reported in tables A2 and A3. The results using this more robust sample are qualitatively similar to those reported in tables 3 and 4.

B. Heterogeneity by Size and Direction of Shocks

While we find small effects overall, it is possible that our estimates of mean effects obscure different patterns at other parts of the distribution of firm-level shocks. In particular, it seems relevant to ask whether firms insure workers against particularly large shocks or are more likely to insure workers against negative shocks but allow earnings to vary with positive shocks. We explore this possibility in figure 4 by graphing mean changes in log worker earnings against changes in log firm revenues.²³ We utilize the more robust 3-year-change sample for this exercise. We order the firm revenue changes and divide them into 50 bins with approximately equal numbers of firm/year observations and then average the changes in log revenues and changes in worker earnings within each bin. We have omitted the lowest and highest bins from the figure.

The figure shows suggestive evidence that firms insure workers against very large shocks in manufacturing and professional services. This seems to be true both for large positive shocks and for large negative shocks. The slope relating firm revenue shocks to changes in worker earnings is flatter at the extremes than in the middle. The pattern is less clear for retail and for finance; those figures do not point to obvious asymmetric effects of positive and negative shocks. We verify this by running regressions for the 3-year changes allowing the coefficients to differ for positive and negative shocks, the results of which we report in Table 5. The coefficients are slightly larger for negative shocks, although in the case of manufacturing the difference is minimal (and in finance none of the coefficients are significant). While we do not interpret our estimates as rent-sharing parameters, this type of asymmetry would be hard to reconcile with a rent-sharing story alone. The expectation is that firms do not cut wages in the case of negative shocks because workers may leave while they are likely to share the rents generated by positive shocks. One caveat is that we cannot separately identify hours variation in our data.²⁴ It is possible at least in the retail sector, where part-time employment is common, that firms cut hours for stayers in the case of negative demand shocks.

C. Heterogeneity by Worker Characteristics

Wage insurance and incentive pay are likely to be more relevant motives for structuring pay for some jobs than others. Given what can be measured in our data, grouping workers by relative position in their firm’s earnings distribution seems the most useful way to try to distinguish groups that might be more or less affected. To do this, we pool information on all workers (stayers or not) who work at least one full quarter for a firm in sample. We then regress log quarterly earnings on dummies for single years of age and a full set of year × quarter dummies to adjust for differences in the age and time periods in which earnings are observed. We take residuals from this regression and average them across all quarters that an individual is in sample. We use these average residuals to rank workers within each firm. While our analysis sample is again based on the 5-year-change sample, we assign workers in sample to quantiles based on order statistics calculated including any nonstayers who worked one or more full quarters. Therefore, our quantiles do not split the sample of stayers into equal fractions, but they do preserve a reasonable ordering of our in-sample observations.

Table 6 shows the results for quintile 1, for quintile 3, and for the top 5% of the distribution. The table reports OLS estimates based on 5-year changes and IV estimates that instrument 5-year changes in log revenues with 3-year changes in log revenues. In the retail sector, the effects are similar across the wage categories. In manufacturing and professional services, there is more evidence that coefficients are larger for higher-wage workers. In manufacturing, the IV coefficient increases from being close to zero and insignificant for quintile 1 workers to 0.029 for the top 5% workers. The pattern is much more pronounced in professional services, where the IV coefficient goes from being insignificant and close to zero for quintile 1 workers to 0.091 for the top 5%. The near 10% elasticity is the largest coefficient estimate we find in any of our specifications. This suggests that shifting composition of employment from manufacturing to professional services and from less skilled jobs to higher-skilled jobs may have contributed to increased volatility of worker earnings, although we note that we do not find much evidence of performance-related pay (connected to firm-level outcomes) for the vast majority of workers in our data. This is somewhat in contrast to the findings of Lemieux et al. (2009), who attribute a substantial role to the rising incidence of performance pay to the increasing level of earnings inequality.

While we generally find small estimates and interpret this as evidence of partial wage insurance, a competing explanation is that labor markets are effectively competitive and firms have little leeway in setting wages. This is more likely to be true for workers who have just been hired and have no accumulated firm-specific human capital. We examine whether workers with greater tenure in the firm (and presumably more firm-specific human capital) experience larger transmission of firm-level shocks compared with the just hired.

We explore these differences in Table 7. We use our 3-year-change sample here because requiring the longer 5-year interval is likely to have particularly large effects on the number of new hires who remain in sample. We distinguish between just-hired employees and longer-term employees, where the latter category is defined as workers who have 4 quarters of tenure or more in the first year of the 3-year change. Table 7 shows that in retail and professional services, workers with more tenure experience somewhat larger changes in their earnings in response to firm shocks than do the just hired, but even in these cases the transmission of firm-level shocks to worker earnings continues to be fairly small. Estimated differences for both manufacturing and finance are insignificant. It thus appears that even for workers with greater tenure, there is little transmission of firm-level shocks to worker earnings, suggesting that wage insurance is still a compelling explanation for the small size of the elasticities.

D. Additional Robustness Checks Using Manufacturing Data

We have focused on revenues as our measure of firm performance, presuming that revenue changes are driven by demand shocks or productivity changes so that the prospect of profits to be shared with workers grows. However, mergers or acquisitions could also lead to revenue increases without necessarily reflecting improved firm performance. To examine whether this is an important concern, we include controls for changes in firm employment for manufacturing so that our estimates should be less sensitive to such reorganizations.²⁵ We also include specifications that add a control for hours: log differences of the ratio of total production worker hours to production worker employment. We do this to see whether adding hours reduces our estimates, which would suggest that part of the adjustment is due to changes in hours rather than wages. We focus on 5-year-change models, and the sample is similar to that in Table 4.²⁶ Column 1 of Table 8 reports OLS results, while column 2 reports IV results. Compared with our baseline results reported in Table 4, we find somewhat larger coefficients when we add employment controls. For example, the IV estimates for manufacturing reported in Table 4 ranged between 0.016 and 0.024. Our estimate with employment controls is 0.038. On the other hand, we find that adding hours has very little effect on our estimates. This suggests that the interpretation of our estimates as referring to wage insurance is still valid and that, at least in manufacturing, the elasticity parameters do not simply reflect an hours adjustment. Finally, we replace sales with value added for the final row of Table 8. Card, Cardoso, Heining, and Kline (2016) find that coefficients estimated using value added are somewhat larger than those estimated using sales. We do not find that to be the case in Table 8—in fact, our estimates using value added are somewhat lower than those using sales. On net, the results in Table 8 suggest that various specification changes may lead to slightly smaller or larger estimates, but the overall similarity of these results to our baseline results are reassuring.