Amid a decades-long trend of wage stagnation and reduction in job mobility, the last few years have witnessed renewed policy and research interest in the use of noncompete agreements (NCAs). NCAs are employment provisions that prohibit departing workers from joining or starting competing businesses, often within time and geographic limits.1 Since the 2014 discovery of NCAs in low-wage jobs, more than 69 new state or federal NCA policies have been proposed, including bans on NCAs for all or a subset of the workforce.2 These proposals join a centuries-long debate over the value of NCAs, which juxtaposes the potential for NCAs to constrain the upward mobility of workers against the potential for NCAs to incentivize firm investment in the development and sharing of valuable information.3
A growing stream of academic research has aided this debate by seeking to understand how NCAs, and the policies that regulate them, influence economic activity. Most of this research examines NCA policies alone, that is, without any information on the actual use of NCAs.4 This omission is critical, given that the limited data we do have on NCAs suggest that they are frequently found in states where they are legally unenforceable. The data also suggest that workers perceive their NCAs to be enforceable when they are not and that NCAs can limit employee mobility regardless of the law.5 More broadly, existing data on NCAs have four limitations: (1) they are not publicly available, (2) they come from either selected occupations or nonrandom sampling schemes, (3) they are cross-sectional, and (4) they are not repeated cross-sections of the same population or sampling frame. As a result, researchers have not been able to study the evolution of NCA use and how NCAs affect a variety of economic dynamics, like wage stagnation and the historical decline in business dynamism.
To address these concerns, in 2017 the Bureau of Labor Statistics (BLS) added a question on NCAs to the National Longitudinal Survey of Youth 1997 (NLSY97)—a panel dataset consisting of individuals born between 1980 and 1984. The first NLSY97 wave with NCA data was published in December 2019, and data collection efforts are ongoing. These data address the gaps highlighted above by providing a publicly available, longitudinal dataset that will allow researchers to develop new evidence on this important labor market friction.
In this article, we introduce the first wave of these data.6 We begin with a brief discussion of the theoretical tensions related to NCAs, focusing on bargaining and holdup. Then we describe the NLSY97 and the new NCA question. In our empirical work, we examine the use of NCAs and their correlates, drawing parallels to prior work where possible. We then focus on how NCAs relate to wages, in light of competing predictions made by existing theories. Our estimates here should not be interpreted causally—indeed, one of our key findings is that the sensitivity of the NCA–wage relationship to controls suggests substantial selection into NCA use. In our analysis, we also seek to understand how NCAs relate to wage bargaining and the role of such bargaining in explaining (1) differences in the overall NCA–wage relationship and (2) for differences in effects across gender, education, ability, and NCA enforceability. We conclude with a discussion of research directions as future waves of data become available.
Since the first legal case dating back to 1414, NCAs have been a topic of significant theoretical debate.7 The essence of the debate is to understand whether, and under what circumstances, it is worth preventing workers from deploying their full set of human capital in a competing firm (typically within some time and geographic boundaries). Courts have generally been concerned that NCAs, like other restraints of trade, can impose significant hardship on workers, since workers who wish to leave the firm without violating their NCA will either have to change industries, leave the geographic area, or sit out of the labor market.8 Moreover, since NCAs increase the costs of moving to a competitor, they shield the firm from labor market competition, potentially curtailing wage growth for workers.9
However, theories rooted in efficient contracting posit that NCAs will only be observed when they are mutually beneficial to firms and workers. The theories tend to have two components. First, workers have the “freedom to contract,” such that they would only agree to an NCA if it made them better off.10 Second, firms would never pay a worker a compensating differential (a higher wage) for an NCA unless they too were benefiting from it. And the reason firms might benefit from NCAs is that they resolve an investment holdup problem.11 If a firm were to share valuable information with a worker, then without an NCA the worker could holdup the firm by threatening to use that information at a competitor. As a result, the firm may be unwilling to develop such information in the first place or unwilling to share it with the worker, both of which may reduce productivity. Accordingly, under this view NCAs can only be productive for both workers and firms, because they give firms stronger incentives to invest in worker training and to develop valuable information.12
Despite a burgeoning literature on NCAs, which of these theories is most accurate is still an open question. These competing theories make different predictions both about where NCAs should be used and (among other things) how NCAs relate to wages. Regarding the use of NCAs, the holdup theory suggests that NCAs will be used mostly in jobs that have access to valuable information (such as trade secrets and client lists) and only in places where they can be enforced (since court enforcement underlies firm confidence that NCAs will resolve the holdup problem).13 In contrast, theories that firms are using NCAs as value extraction tools posit that they will be used much more broadly—potentially even with low-wage workers who have no access to valuable information and in places where NCAs cannot be enforced.14
With regards to wages, three possibilities arise: (1) workers may receive higher pay (whether they had to negotiate for it or if it was included in the offer) for signing an NCA, but then suffer lower wage growth as the NCA prohibits workers from taking jobs with higher paying competitors; (2) wage growth may rise if NCAs indeed spur productivity-enhancing investments and wages are tied to productivity; (3) workers may not receive higher pay (because, for example, they just sign the NCA when asked) and experience lower wage growth.15
Prior research finds some evidence in favor of each of these arguments. NCAs are adopted widely, and they tend to be more common in states that enforce them and for workers in technical jobs.16 Regarding wage outcomes, prior research on NCA enforceability finds negative effects on wage levels and wage growth, while studies of NCA use find positive wage effects and positive wage growth.17 The discrepancy in wage results could arise from the specific occupations studied, differences between the actual effects of NCA enforceability and NCAs themselves, the period studied, selection into NCA use, the cross-sectional nature of the studies of NCA use, or lack of data on key variables (wage bargaining, job tasks, ability, etc.).18
In this regard, new data collected via the National Longitudinal Survey of Youth 1997 offer an important opportunity to push this literature forward, especially as more waves of data are collected over time.
In this section we discuss the details of the NLSY97 and how the NCA question fits into the survey.
The National Longitudinal Survey of Youth 1997 (NLSY97) is a nationally representative sample of 8,984 people born in the years 1980 to 1984. Sample members were first interviewed in 1997 when they were ages 12 to 17; the latest data available when we began this article are from the 2017–18 interview, when the sample members were ages 32 to 38. A particular strength of the NLSY97 is the collection of respondents’ employment histories from their teenage years until the present. The employment module of the NLSY97 contains a core set of questions that are asked in each survey round about each job held since the date of the last interview, but certain additional modules of interest to research and public policy rotate in and out.
Recent added questions include those on NCAs, job tasks, and wage bargaining. The NCA questions first appeared in the 2017–18 survey and are also in the 2019–20 survey (data released in November 2021). In the 2017–18 survey, the NCA questions were asked of all jobs that were not military or self-employed. In the 2019–20 survey, the NCA questions were restricted to newly reported jobs since the date of the last interview.
In the 2017–18 survey, for each job held since the date of the last interview, the respondent is asked about a series of job characteristics. The NCA question is as follows:
“Some employers try to restrict what their employees can do after they leave their job. In this job, did you agree that if you [leave/left] your employer, you [will/would] not start or join a competing business? This is often called a non-compete agreement.”
Because prior research has documented uncertainty in who signs NCAs, a followup question asks, “How confident are you in your answer?” The wording of the two NLSY97 questions on NCA agreements were based on those asked in prior surveys on the same topic.19
To construct our sample, we take the full NLSY97 sample (sample size of 8,984) and keep those who responded to the 2017–18 (round 18) interview (sample size of 6,734). We then restrict the sample to those who reported a job in the interview (sample size of 5,970). We drop the self-employed, government, and military workers, and those who are working for their family without pay (sample size of 4,481). We also drop those whose geographic region is missing (do not reside in the United States at the 2017–18 interview date) (sample size of 4,443). We then restrict our sample to those working at their main job at least 30 hours per week (sample size of 3,589). We use the Consumer Price Index for all Urban Consumers (CPI-U) to inflation-adjust hourly wages to 2017 dollars, and we drop those who earn less than $2 an hour and those who make above $250 an hour or those missing wage information (sample size of 3,490). Finally, we drop those whose NCA variable is missing (sample size of 3,426), those with missing wage bargaining questions (whether they bargained over pay when they were first offered their job) (sample size of 3,092), and a few observations with an unclassifiable occupation (Standard Occupational Classification code of 9990). Our final sample consists of 3,090 people. We use the NLSY97 weights for the 2017–18 interview, which account for the oversamples of Black and Hispanic individuals in the NLSY97 data and the complex survey design.
We begin by examining the incidence of NCAs. Table 1 provides summary statistics on NCA incidence from the NLSY97 in columns 1 and 2, and, for comparison purposes, data from the 2014 Noncompete Survey Project in column 3 and data from the 2019 Cornell National Social Survey (CNSS), collected by Stewart Schwab and Evan Starr, in column 4.20 Overall, 18.1 percent of the NLSY97 sample is bound by an NCA, identical to the overall multiple imputation estimates reported by Starr, Prescott, and Bishara in 2021, but slightly larger than the lower-bound estimates for this age group.21 The estimates are also nearly identical to the CNSS estimates. With regards to uncertainty regarding whether they have an NCA, 90.4 percent are very confident in their answer, whereas 9.0 percent are somewhat confident and 0.7 percent are not confident.22
|Characteristic||NLSY97||2014 NSP, lower bound NCA incidence (in percent)||2019 CNSS, NCA incidence (in percent)|
|NCA incidence (in percent)||Observations|
Less than a bachelor’s degree
Bachelor’s degree or higher
State enforces NCAs
State does not enforce NCAs
Hourly wage less then $20
Hourly wage greater or equal to $20
Tenure less than 3 years
Tenure greater or equal to 3 years
Less than 20 employees
20 to 99 employees
100 or more employees
Notes: NCA = noncompete agreement. n = sample size. 2014 NSP = 2014 Noncompete Survey Project (data are limited to workers ages 32–38 in 2014. n = 1649); incidence estimates from the NSP are lower bound estimates. 2019 CNSS = 2019 Cornell National Social Survey, collected by Stewart Schwab and Evan Starr in 2019 via random digit dial survey (data are limited to ages 25–50 in 2019: n = 338). NLSY97 = National Longitudinal Survey of Youth 1997.
 Not applicable.
Source: U.S. Bureau of Labor Statistics, NLSY97 (2017–18 interview); 2014 NSP; 2019 CNSS. Authors' calculation.
We briefly describe some of the NLSY97 NCA incidence results from table 1. In the NLSY97, men are about 5 percentage points more likely than women to report signing an NCA at their job (20 percent versus 15 percent), while non-Black, non-Hispanic workers are 4 percentage points more likely to be bound by an NCA than either Black or Hispanic workers. Chart 1 shows that NCA incidence rises with education, with 15 percent of those without a bachelor’s degree signing one, compared with 24 percent with at least a bachelor’s degree.
In terms of worker and firm characteristics, table 1 shows that NCAs rise with tenure and that NCAs are 12 percentage points more common for those working in the for-profit sector than the nonprofit sector (19.6 percent versus 7.4 percent). Unionized workers are only somewhat less likely to sign NCAs (16.6 percent versus 18.6 percent). With regards to wages, chart 2 shows that the incidence of NCAs is 9 to 11 percent for those in the bottom two wage deciles and rises with wages such that those with wages in the top decile (at least $45 per hour) have a 32 percent chance of having an NCA. Overall, NCAs are still found at the low end of the wage distribution, with 14.4 percent of workers earning less than median hourly wages signing one.
Charts 3 and 4 show the distribution of NCAs by two-digit occupational and industrial codes (conditional on having at least 20 observations in the occupation or industry).
Consistent with holdup theories, occupations in which NCAs are found most frequently are in more technical areas such as engineering (38 percent), computer science (36 percent), sales (28 percent), and management (24 percent). Occupations such as food preparation (7 percent) and social services (4 percent) have very low reported NCA incidences.23 Similarly, chart 4 shows that workers in industries such as professional services and information have high rates of NCAs (33 percent and 30 percent, respectively) in contrast to workers in social services, food services (10 percent), or agriculture (6 percent).
We also consider whether NCAs are deployed even in states that would not enforce them. Only three states—California, North Dakota, and Oklahoma—will void all NCAs agreed to in the employment context, and these policies have been in place since the 1800s.24 Table 1 shows that 15.0 percent of workers who live in these states are bound by NCAs, compared with 18.5 percent elsewhere.
Overall, while there are some discrepancies between the magnitude or direction of the NLSY97 results relative to both the 2014 NSP and the 2019 CNSS, the general patterns and magnitudes are roughly in line.
In table 2 we examine variables unique to the NLSY97. First, although investing in worker training is an oft-referenced rationale for using NCAs, workers whose employers have provided at least some training in the past are only marginally more likely to have NCAs (19.8 percent to 17.7 percent).25 Second, the NLSY97 includes a unique measure of ability—the Armed Forces Qualification Test (AFQT) (math and verbal aptitude percentile score).26 Chart 5 breaks down AFQT scores by decile, showing that the incidence of NCAs is 11 percent for those with the lowest AFQT scores but rises consistently such that those with the highest AFQT score have a 25-percent likelihood of agreeing to an NCA.
|Characteristic||NCA incidence (in percent)||Observations|
Some employer-provided training
No employer-provided training
AFQT score below 50th percentile
AFQT score equal or above 50th percentile
Repetitive tasks for more than half the workday
Repetitive tasks for less than half the workday
Physical tasks for more than half the workday
Physical tasks less than half the workday
Supervise or manage more than half the workday
Supervise or manage less than half the workday
Problem solve every day
Problem solve less than every day
Read long documents
Does not read long documents
A lot of face-to-face contact with noncoworkers
Not a lot of face-to-face contact with noncoworkers
Notes: AFQT = Armed Forces Qualification Test. NCA = noncompete agreement. NLSY97 = National Longitudinal Survey of Youth 1997.
Source: U.S. Bureau of Labor Statistics, NLSY97 (2017–18 interview). Authors' calculation.
Lastly, job tasks show considerable variation with NCA use:27 Individuals in jobs that require more physical and repetitive tasks are about 7 percentage points less likely to report signing an NCA, whereas individuals in jobs with more problem solving, reading long documents, and supervising are much more likely to sign one.
Since many of the characteristics described above are likely to be correlated with each other, in table 3 we incorporate these variables into a linear probability model to assess which characteristics are correlated with NCA use, conditional on the other variables. We cluster the standard errors by state. Several patterns emerge: Across all models, having a bachelor’s degree is associated with a greater chance of signing an NCA, even though AFQT scores are uncorrelated with NCA use.28 Nonprofit jobs are also far less likely to have NCAs relative to for-profit jobs (9.1 percentage points in the model with the most controls). Although the use of NCAs appears to be lower in states that cannot legally enforce NCAs, this difference becomes statistically insignificant with more controls. We also see that, even conditional on occupation and industry, several job tasks are still correlated with NCA use, including face-to-face contact with others (+4.4 percentage points), reading longer documents (+4.5 percentage points), solving problems daily (+6.3 percentage points), or frequent physical tasks (-3.3 percentage points).
|Variable||Model specification 1||Model specification 2||Model specification 3||Model specification 4|
At least a bachelor's degree
AFQT percentile score
25 percent to 50 percent
50 percent to 75 percent
75 percent or higher
State does not enforce NCAs
21 to 100 employees
Greater than 100 employees
Employer ever trained worker
Tenure, 3 years or more
Frequency with which contact with others is "a lot"
Longest document read at work is at least 11 pages
Use math to solve problems at least once a day
Solve problems at least once a day
Supervise or manage others more than half the time
More than half of tasks are physical
Short and repetitive tasks more than half the time
Occupation and industry fixed effects
Notes: Observations = 3,090. AFQT = Armed Forces Qualification Test. NCA = noncompete agreement. NLSY97 = National Longitudinal Survey of Youth 1997. Standard errors, clustered by state of residence, are in parentheses. Regressions are weighted with round 18 survey weights. If the variable of interest is missing for some values, an indicator is included (but not reported) which equals 1 if the variable is missing. Results are available from the authors.
 p < 0.01.
 p < 0.05.
 p < 0.10.
 Variable is not used in this model specification.
Source: U.S. Bureau of Labor Statistics, NLSY97 (2017–18 interview). Authors' calculation.
In this section we use NLSY97 wage and wage bargaining data to examine how NCAs relate to wage bargaining and wage outcomes.
We begin with a discussion of the ideal empirical designs to estimate the effect of NCAs, what our approach is, and why, ultimately, our results should be thought of as correlational and not causal. The ideal empirical design to estimate the causal effect of NCAs on bargaining and wages is to randomly ask some sample of workers to sign NCAs. Then one could consider who turns down the offer outright, who negotiates over the NCA or the terms of the offer, and wage outcomes. If NCAs were randomly assigned, then no other firm or worker characteristics (observed or unobserved) would differ between who received an NCA and who did not—at least before the NCA was deployed—allowing us to isolate the effect of NCAs. To our knowledge, such an experiment has yet to be run in the real world.
An alternative approach to estimating the causal effect of NCAs is to find an instrument—something that would randomly cause some firms to use NCAs but would not be correlated with wages or bargaining through any other pathway. The most natural instrument, it might seem, would be the enforceability of NCAs, which might exogenously increase the firm’s willingness to use them. However, the fact that firms still use NCAs relatively frequently in states that do not enforce NCAs poses some challenges for this approach. The exclusion restriction is also likely to be violated if the instrument is just cross-sectional state NCA enforceability, since other state characteristics might be correlated with the policy and outcomes of interest. Variation over time in state NCA enforceability, combined with variation over time in NCA use, is likely to be a more plausible identification strategy. Another approach that future data collection makes possible could use Bartik-style instruments that interact industry shares with national growth rates.29
To date, no research has been able to use these research designs, mostly because of the cross-sectional nature of data on NCAs. Instead, prior work documents conditional correlations. With just one cross-section of data, we face the same challenges (even though the NLSY97 contains some rich measures of job attributes) and so we also estimate conditional correlations.
We estimate models of the form using ordinary least squares, where is a dependent variable, is a vector of covariates, and is an error term. In order for to estimate the true causal effect of an NCA, we need a conditional independence assumption to hold—that , conditional on .30 This assumption is highly unlikely to hold. Based on where we see NCAs being deployed, our estimates of the NCA–wage differential will likely be seriously biased upward. For example, since NCAs are more common in technical jobs or for workers with more education, a worker bound by an NCA is highly likely to earn more than a worker not bound by an NCA—but this difference is perhaps mostly or entirely due to differences in their human capital, the type of job they are in, and the tasks they are asked to perform. We can control for some of these variables at a broad level, which should mitigate these concerns. However, because we cannot hold constant all the variables that determine both NCA use and wages, the positive bias will likely persist.
Nevertheless, inclusion of different covariates can be informative of the extent of selection into NCAs and thus the extent to which the NCA–wage differential is biased upward. Accordingly, we estimate two sets of models, one with “basic” controls, which are exogenous demographic characteristics. These are education, gender, race, AFQT score at or above 50th percentile, and whether the state enforces NCAs. We also estimate models that seek to compare workers who are in the same type of job and doing the same set of tasks. To do this, we add “advanced” controls in addition to the basic controls. These are the for-profit status of the firm, job tasks (as shown in table 2), and two-digit occupation and industry fixed effects. We note that some of the advanced controls may be bad controls in that they may be endogenous to agreeing to an NCA (that is, the tasks a worker does may depend on whether that worker agrees to an NCA).31 Due caution is required when interpreting the NCA coefficient with these controls.
We focus first on bargaining as an outcome of NCA use and later as a mediator and moderator of the NCA–wage relationship. Bargaining is relevant because NCAs give firms power only after an NCA is signed. As a result, NCAs put some pressure on the initial negotiations for workers to receive compensation for their postemployment concessions. Before we turn to the results, it is worth considering why bargaining may or may not arise in response to NCAs.
Different models of the labor market differ in how they consider bargaining. For example, wage-posting models assume employers simply post a take-it-or-leave-it offer, precluding the possibility of bargaining.32 In these models, as long as the NCA is sufficiently observable and perceived as costly to the worker, a compensating differential may be built into the posted wages, rendering bargaining unnecessary. Other wage bargaining models assume that workers bargain for some proportion of the surplus from the job, but these models are agnostic to the precise mechanics of how the bargaining occurs.33 Such a process may look as follows in the case of NCAs: the firm may initially offer an NCA paired with a wage offer that is at or slightly above the wages offered by firms that do not use NCAs. In this situation, the worker may either accept the contract as presented, turn it down, or ask for higher pay. In the third case, we might observe a positive relationship between bargaining and NCAs.
To set a baseline, prior research suggests that only approximately one-third of workers bargain over their wages at all and the only evidence on negotiation over NCAs suggests that only 10 percent of NCA signers report negotiating over the terms of their NCA or for other benefits in exchange for signing.34 In the NLSY97, 36 percent of workers report that their wage was bargained over, while the rest indicate that it was a take it or leave it offer. Chart 6 shows that the likelihood of wage bargaining rises effectively monotonically across the wage distribution, with 15 percent of the lowest earners bargaining over their wages, compared with 61 percent of the highest.
In light of this discussion, we begin by assessing whether NCAs are associated with a greater chance of wage bargaining. Table 4 panel A shows that while NCAs are associated with a 9.5-percentage-point increase in the likelihood of wage bargaining, controlling for basic controls and advanced controls reduces the differential to 2.1 percentage points and becomes statistically insignificant. Thus, the positive relationship between NCAs and wage bargaining seems largely driven by certain individual- or job-specific characteristics.
|Variable||Incidence of bargaining over wages||Logarithm of hourly wages|
|Model specification 1||Model specification 2||Model specification 3||Model specification 1||Model specification 2||Model specification 3|
Panel A: Baseline bargaining and wages
Percent increase in wages associated with NCA
Panel B: Wages as a function of bargaining
|Logarithm of hourly wages|
|Model specification 1||Model specification 2||Model specification 3||Model specification 4||Model specification 5||Model specification 6|
Bargaining over wages
NCA interaction with bargaining over wages
Percent increase in wages associated with NCA
Percent increase in wages associated with bargaining
Percentage of NCA-wage differential explained by bargaining
Notes: Observations = 3,090. NCA = noncompete agreement. NLSY97 = National Longitudinal Survey of Youth 1997. Basic controls include three education categories (less than a college degree, a college degree, and more than a college degree), indicators for race and ethnicity, Armed Forces Qualification Test (AFQT) score at 50th percentile or more, gender, and an indicator for whether the state of residence does not enforce NCAs. Advanced controls add an indicator for for-profit or nonprofit status, occupation and industry fixed effects (two digit Standard Occupational Classification and North American Industry Classification System codes), and indicators for job tasks including indicators for repetitive work, frequency of contact with others, the length of the longest document read on the job, solving problems, using math to solve problems, supervising others, and the extent of physical tasks. If the variable of interest is missing for some values, an indicator is included (but not reported) that equals 1 if the variable is missing. Results are available from the authors. Standard errors, in parentheses, are clustered by state of residence. Regressions are weighted with round 18 survey weights. The “Percentage of NCA-wage differential explained by bargaining” row takes the NCA coefficients from model specifications 1 to 6 from from panel B and divides them by the corresponding NCA coefficient in the top panel's "Logarithm of hourly wages," model specifications 1 to 3.
 p < 0.01.
 p < 0.05.
 p < 0.10.
 Variable is not used in this model specification.
 Not applicable.
Source: U.S. Bureau of Labor Statistics, NLSY97 (2017–18 interview). Authors' calculation.
Columns 4 to 6 of table 4 panel A examine the baseline wage results. Unconditionally, those bound by NCAs earn about 25 percent more.35 However, as in the case of bargaining, the inclusion of basic controls reduces this coefficient to 12.7 percent, and the inclusion of advanced controls reduces it to just 5.0 percent. Given the precipitous drop in the coefficient on NCAs as controls are added, the correlation between NCAs and wages is highly susceptible to unobserved variables. That is, there are many other variables that we cannot observe (for instance, access to valuable trade secrets and clients) that might drive both NCA use and wage outcomes. Such omitted variables will positively bias the NCA–wage correlation, even with the granular controls we observe in the NLSY97.
There are two unanswered questions that follow with regards to NCAs, wages, and bargaining. First, how much of the NCA–wage differential can be explained by baseline differences in bargaining behavior? Second, do workers with NCAs who bargain actually end up with higher wages, perhaps because they asked for a greater compensating differential?
Columns 1 to 3 of panel B of table 4 address the first question. Column 1 shows that, without basic or advance controls, controlling for bargaining causes the NCA coefficient to fall by 13.1 percent (from 0.221 to 0.192). However, when we include controls, the NCA–wage differential explained by bargaining falls to 7.5 percent and 4.1 percent (columns 2 and 3), and the extent to which bargaining itself positively relates to wages falls. Thus, bargaining only modestly drives the NCA–wage relationship.
Columns 4 to 6 of panel B considers question two and allow for bargaining to have a different relationship to wages depending on if a worker signed an NCA or not. Column 4 shows that, without controls, the NCA–wage differential for workers who do not bargain over wages is 16.8 percent—a 29.9-percent decrease from the baseline—while the NCA–wage differential is 9.5 percent higher among those who do bargain. Moreover, while the controls reduce the NCA–wage differential for those who do not bargain—reducing it by 63.3 percent in the most saturated model relative to the main effect in panel A (0.018 vs. 0.049)—the NCA–wage differential for those who bargain remains 7 percent higher.
Taken together, this suite of results suggests that NCAs are positively associated with wages but that there is strong selection into NCA use. Our analysis does not show that NCAs cause higher wages; in fact, it may be that NCAs reduce wages but that we cannot account for all the variables that confound the NCA–wage relationship. Our results also show that wage bargaining can explain a substantial amount of the NCA–wage relationship; not because workers with NCAs are necessarily more likely to bargain over wages, but because those with NCAs who do bargain drive much of the positive baseline relationship.
In this section we examine several potential heterogeneous effects discussed in the prior literature as well as novel heterogeneous effects made possible by the rich data in the NLSY97. The prior literature has emphasized the potential for historically disadvantaged populations to be especially harmed by NCAs. For example, Lipsitz and Starr found in 2021 that women particularly benefit when NCAs are banned, while Johnson, Lavetti, and Lipsitz found in 2020 that both women and Black workers are better off when NCA enforceability is weakened.36 Lastly, Starr found in 2019 evidence that those with less education are more likely to be harmed when NCAs are more likely to be enforced.37 Several rationales for these findings have been proposed, including that disadvantaged populations may be more likely to voluntarily abide by an NCA, that firms may selectively target such groups for enforcement, and that such workers are less likely to bargain over the NCA.
However, all of these studies examine state NCA policies, and none of the studies of NCA use have examined similar predictions. Accordingly, in table 5 we present analyses examining how, in the cross-section, the relationship of NCAs to wages is different for various groups. As before, we estimate models that include the same basic and advanced controls, clustering the standard errors by state.
|Variable||Logarithm of hourly wages|
|Model specification 1||Model specification 2||Model specification 3||Model specification 4|
Panel A: Education
Education higher than a bachelor's degree
Interaction of NCA and bachelor's degree
Interaction of NCA and education higher than bachelor's degree
Panel B: Race and ethnicity
Black or Hispanic
Interaction of NCA and Black or Hispanic
Interaction of bargaining indicator and group indicators
Panel C: Gender
Interaction of NCA and Female
Panel D: AFQT
AFQT score 50 percent or higher
Interaction of NCA and AFQT Score 50 percent or higher
Panel E: State NCA enforceability
State does not enforce NCAs
Interaction of NCA and whether a state does not enforce NCAs
Interaction of bargaining indicator and group indicators
Notes: Observations = 3,090. AFQT = Armed Forces Qualification Test. NCA = noncompete agreement. NLSY97 = National Longitudinal Survey of Youth 1997. The dependent variable is log hourly wage. Basic controls include three education categories (less than a college degree, a college degree, and more than a college degree), indicators for race and ethnicity, AFQT score at 50th percentile or more, gender, and an indicator for whether the state of residence does not enforce NCAs. Advanced controls add an indicator for for-profit or nonprofit status, occupation and industry fixed effects (two digit Standard Occupational Classification and North American Industry Classification System codes), and indicators for job tasks including indicators for repetitive work, frequency of contact with others, the length of the longest document read on the job, solving problems, using math to solve problems, supervising others, and the extent of physical tasks. If the variable of interest is missing for some values, an indicator is included (but not reported) that equals 1 if the variable is missing. Results are available from the authors. Standard errors, clustered by state of residence, are in parentheses. Regressions are weighted with round 18 survey weights.
 p < 0.01.
 p < 0.05.
 p < 0.10.
Source: U.S. Bureau of Labor Statistics, NLSY97 (2017–18 interview). Authors' calculation.
The results largely accord with what we saw in the case of wage bargaining: The main effects are highly sensitive to the inclusion of controls, while in most cases, the heterogeneous effects of NCAs are more stable (and often line up with the prior literature). For example, panel A shows that relative to the NCA–wage differential for those with less than a bachelor’s degree, the NCA–wage differential for those with a bachelor’s degree is practically no different, while for those with more than a bachelor’s degree it is 19 percent to 25 percent higher.
The heterogeneous effects of NCAs are more sensitive when it comes to race and gender. Panel B shows that the NCA–wage differential for minority (Black or Hispanic) workers is lower than the NCA–wage differential for non-Black non-Hispanic workers, but the estimates are noisy and fall close to zero in the most saturated model. Similarly, panel C shows that, at baseline, men bound by NCAs earn between 7 percent and 16 percent more than men without NCAs. The same differential for women, however, ranges from 5 to 10 percent lower than that of men, with the difference being statistically significant only in the model with basic controls.
Given the literature’s focus on disadvantaged workers, in panel D we consider whether higher ability workers, as measured by having an AFQT score at or above the 50th percentile, have higher NCA–wage differentials than lower ability workers. Indeed, the wage difference between those who signed NCAs and those who did not was larger for workers who had a high AFQT score than for those who had a low score.
Finally, we consider heterogeneous NCA–wage effects based on the extent of enforceability of the NCA. Under the efficient contracting theories, it is the actual law (i.e., whether a contract will be held up in court) that determines whether the firm can ultimately be protected from a holdup problem. Accordingly, under this theory, workers should be better off where NCAs are more enforceable—either because of being more likely to bargain or because access to valuable information makes them more productive. In contrast, if NCAs are value extraction tools for firms, then NCAs might more effectively extract value when firms can legitimately threaten a worker with a lawsuit for violating an NCA. Panel E shows that relative to states that enforce NCAs, the wage differential associated with NCAs when they are not enforceable is 4 to 7 percent higher.
Taken together, because the base rates are so sensitive to controls, our results suggest that it is not obvious whether the baseline positive NCA–wage relationship is driven by selection or treatment. However, the more consistent heterogeneous effects suggest that, whatever the baseline effect is, the wage differential associated with NCAs is lower for women, for those with less education, for those with low AFQT scores, and in states more able to enforce NCAs.
In columns 3 and 4 of table 5, we consider the plausible theory that the observed NCA–wage differentials are driven by group differences in bargaining. If, for example, women are less likely to bargain over wages or when they do bargain ask for smaller compensating differentials, then these baseline bargaining differences may explain why NCAs are more harmful to women than men. Accordingly, we rerun our heterogeneous effects models controlling for whether the individual bargained for their wages, and we allow for different groups (as defined for each panel) to have differential effects from bargaining. In each case, we observe that subgroup bargaining patterns do not explain the differences in pay, since the estimated NCA–wage differentials move little when including these controls.
This study is motivated by the recent and historical debates over the value of NCAs and by the relative lack of data on NCAs themselves, amidst a growing literature studying state NCA policies. Using new data collected on NCAs as part of the NLSY97, we examine who signs NCAs, how NCAs are related to wages and wage differentials between groups, and the role of bargaining in explaining these differentials. Our results both support the prior literature on NCAs and extend it in new, important ways.
Overall, we find that 18.1 percent of workers ages 32–38 in 2017 were bound by NCAs, very similar to prior estimates.38 We also document similar patterns to the prior literature—that the use of NCAs is more common for workers with more education and that NCAs are more common in technical occupations and industries. However, as the prior literature also suggests, NCAs are still used for a wide swath of workers at the low end of the wage distribution or even workers in states that would never enforce such an agreement.39 We extend these findings by showing that NCAs are also more common for workers with high ability and that even within a job-type, variation in job tasks (such as problem solving) are strongly associated with NCA use. Interestingly, our results suggest little selection into NCA use by ability after conditioning on broad demographics.
Examining wage outcomes, we find that NCAs are positively associated with wages but that this association is highly sensitive to demographic and job characteristics, as in prior work.40 As a result, we recommend interpreting the main correlations with due caution. Heterogeneous effects in the NCA–wage differential are more stable, however. For example, the wage increase associated with NCAs is lower for those with less education (relative to more education), lower for those with lower ability (relative to higher ability), and lower for women (relative to men) in some models. Although we also find that the NCA–wage differential is lower for those who do not bargain over wages (relative to the NCA–wage differential for those who do bargain), bargaining differentials across groups do not explain the NCA–wage differentials across groups. Finally, our results suggest that the enforceability of NCAs reduces NCA–wage differentials, as found by Starr, Prescott, and Bishara in 2021.41
Taken together, our results are consistent with elements of the efficient contracting perspective, for example that NCAs are more common in high-skilled jobs and that NCAs are associated with higher wages on average. But our results also challenge that narrative because (1) the use of NCAs is widespread, (2) the NCA–wage effect is highly sensitive to demographic and job controls, and (3) the fact that the positive wage associations with NCAs dissipate where NCAs are more enforceable suggest that the baseline positive wage estimates may be highly selected. Our results also suggest that since bargaining power differentials are unlikely to underlie the NCA–wage differentials for the groups we study, alternative theories may be considered, such as differential to access to legal services or acquiescence to legal threats.
While these analyses advance our understanding of NCA adoption, wage setting, and wage bargaining, they have several important shortcomings. Notably, the data are from a single cross-section, making it difficult to extract anything but correlational relationships and precluding a study of longitudinal earnings or job mobility dynamics. However, as more data are collected, there are several clear opportunities to exploit the richness of the NLSY97. In this section, we lay out a broader research agenda that these data will allow researchers to fill.
First, one of the major challenges in this literature is finding exogenous variation in the use of NCAs, given the existence of only cross-sectional data. However, as more states change their policies on NCAs, and as more data on NCAs are collected in the NLSY97, it seems natural that such policy variation could be used to instrument for NCA use. For example, between 2017 and 2021 several states banned NCAs for low-wage workers. These policy changes will likely exogenously reduce the use of NCAs among the low-wage population, especially those policies that impose penalties for using NCAs deemed illegal. As long as these policies leave unaffected the enforcement for those above the wage threshold (which some seem to do), then the exclusion restriction may plausibly hold (i.e., that these policies affect various outcomes only through their effect on NCA use). With this and perhaps Bartik-style approaches, we can hopefully begin to tease out the selection and treatment effects of NCAs.
Second, as longitudinal data are collected, the scope of variables one can analyze grows substantially, enabling analyses of within-individual wage profiles, job mobility choices, entrepreneurial behavior, and variation in nonwage benefits. NLSY97 data on moves and their timing also allow one to explore the relationship between NCAs and migration. Data on spouse and partner labor supply could be used to study the role job restrictions like NCAs play in dual labor market decisions. The NLSY97 also has unique data on several other dimensions that could be used to examine unique heterogeneous effects (such as job tasks, bargaining, AFQT, and more), which would not be possible with other data. Moreover, those interested in understanding the causal drivers of NCA use will be better positioned to use time-variant identification strategies. For example, one can examine how changes in minimum wages over time affect NCA use or how changes in subsidies or tax incentives for investment might drive firms into using NCAs.
Third, as longitudinal data on the use of NCAs becomes available, one can calculate estimates of the growth of NCAs and relate them to various outcomes relevant to multiple disciplines. For example, one important question is what are the downstream effects of NCAs? How does the rise of NCAs affect prices, product quality, research and development expenditures and innovation, and consumer welfare more broadly?42 Another set of questions relates to the patterns of wage stagnation and economic dynamism and what role NCAs played in those dynamics. Note that care should be given to these estimates because estimates of the growth of NCAs will track the use of NCAs among a given age cohort and so may just reflect how NCA adoption changes as a cohort ages. Thus, it may be helpful to benchmark the results to other nationally representative cross-sections to separate out the trends from cohort-specific effects.43
As the NLSY97 data continue to accumulate, so too will the opportunities to learn more about how these contractual restrictions on employee mobility affect many important economic dynamics.
DISCLAIMER: The views expressed are those of the authors and do not reflect the policies of the BLS or the views of other BLS staff members.
Donna Rothstein and Evan Starr, "Noncompete agreements, bargaining, and wages: evidence from the National Longitudinal Survey of Youth 1997," Monthly Labor Review, U.S. Bureau of Labor Statistics, June 2022, https://doi.org/10.21916/mlr.2022.18
1 See “Non-compete contracts: economic effects and policy implications,” U.S. Department of Treasury Office of Economic Policy, March 2016; and Non-Compete Agreements: Analysis of the Usage, Potential Issues, and State Responses, (Washington: DC: The White House, May 5, 2016).
2 See Steven Greenhouse, “Noncompete clauses increasingly pop up in array of jobs,” New York Times, June 8, 2014, https://www.nytimes.com/2014/06/09/business/noncompete-clauses-increasingly-pop-up-in-array-of-jobs.html; Dave Jamieson, “Jimmy John’s makes low-wage workers sign ‘oppressive’ noncompete agreements,” Huffington Post, October 13, 2014, https://www.huffpost.com/entry/jimmy-johns-non-compete_n_5978180; Evan Starr, J.J. Prescott, and Norman Bishara, “Noncompete agreements in the US labor force,” The Journal of Law and Economics, vol. 64, no. 1, 2021, pp.53–84; and Matthew S. Johnson and Michael Lipsitz. “Why are low-wage workers signing noncompete agreements?” Journal of Human Resources, vol. 57, May 12, 2020, pp. 0619-10274R2. For an example of potential state and federal actions, in 2021 the Uniform Law Commission promulgated the Uniform Restrictive Employment Agreement Act for adoption by state legislatures. The proposed act bans noncompete agreements (NCAs) and related restrictive agreements for low-wage workers and mandates notice and other requirements for other workers (see "Restrictive employment agreement act," Uniform Law Commission (2022), https://www.uniformlaws.org/committees/community-home?communitykey=f870a839-27cd-4150-ad5f-51d8214f1cd2&tab=groupdetails). For other state and federal policies, see generally Russell Beck, “The Changing landscape of trade secrets laws and noncompete laws around the country,” Fair Competition Law, May 2021, https://faircompetitionlaw.com/changing-landscape-of-trade-secrets-laws-and-noncompete-laws/. In addition, state Attorneys General have investigated more than a dozen NCA cases (see Lisa Madigan, and Jane Flanagan, “Protecting competition on behalf of the people: the role of state Attorneys General in challenging noncompetes and other restraints on employee mobility,” In Sharon Block and Benjamin H. Harris, editors, Inequality and the Labor Market: The Case for Greater Competition (Washington, DC: Brookings Institution Press, 2021), pp. 107–26, http://www.jstor.org/stable/10.7864/j.ctv13vdhvm.12.). The Federal Trade Commission has considered making a rule related to regulating NCAs, and several federal agencies have written reports on the topic (see “Non-compete contracts: economic effects and policy implications,” U.S. Department of Treasury Office of Economic Policy, March 2016; and Non-Compete Agreements, the White House.
4 See Norman Bishara and Evan Starr, “The incomplete noncompete picture,” Lewis and Clark Law Review, vol. 20, 2016, pp. 497–546. For a review of NCA use literature, see Evan Starr, “Consider this: training, wages, and the enforceability of covenants not to compete,” ILR Review, vol. 72, no. 4, August 2019, pp. 783–817, https://doi.org/10.1177/0019793919826060. Indeed, only a handful of studies possess data on the use of NCAs (see Alan B. Krueger and Eric A. Posner, “A proposal for protecting low-income workers from monopsony and collusion,” The Hamilton Project, February 2018). Of these studies, most examine a specific occupational context, such as executives (see Stewart J. Schwab and Randall S. Thomas, “An empirical analysis of CEO employment contracts: What do top executives bargain for?” Washington and Lee Law Review, vol. 63, no. 1, Winter 2006, p. 231, https://scholarlycommons.law.wlu.edu/wlulr/vol63/iss1/6; and Norman D. Bishara, Kenneth J. Martin and Randall S. Thomas, “An empirical analysis of noncompetition clauses and other restrictive postemployment covenants,” Vanderbilt Law Review, vol. 68, no. 1, January 2015, pp.1–51), engineers (see Matt Marx, “The firm strikes back: non-compete agreements and the mobility of technical professionals.” American Sociological Review, vol. 76, no. 5, August 24, 2011, pp. 695–712), physicians (see Kurt Lavetti, Carol Simon, and William D. White, “The impacts of restricting mobility of skilled service workers evidence from physicians,” Journal of Human Resources, vol. 55, no. 3, Summer 2020, pp. 1025–67), and hair stylists (see Johnson and Lipsitz, “Why are low-wage workers signing noncompete agreements?”).
5 For NCAs found in states where they are unenforceable, see Sarath Sanga, “Incomplete contracts: An empirical approach,” Journal of Law, Economics, and Organization, vol. 34, no. 4, November 2018, pp. 650–79, https://doi.org/10.1093/jleo/ewy012; Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force,”; and Alexander J.S. Colvin and Heidi Shierholz, “Noncompete agreements: ubiquitous, harmful to wages and to competition, and part of a growing trend of employers requiring workers to sign away their rights,” Economic Policy Institute, December 10, 2019. For workers' perception of NCA enforceability, see J.J. Prescott and Evan Starr, “Subjective beliefs about contract enforceability,” University of Michigan Law and Economics Research Paper, 2022. For how NCAs limit mobility regardless actual law, see Evan Starr, J.J. Prescott, and Norman Bishara, “The behavioral effects of (unenforceable) contracts,” Journal of Law, Economics, and Organization, vol. 36, no. 3, November 2020, pp. 633–87.
6 For a concurrent work that also examine the incidence of NCAs using the National Longitudinal Survey of Youth 1997 (NLSY97) data, see Tyler Boesch, Katherine Lim, and Ryan Nunn, “Non-compete contracts sideline low-wage workers.” Federal Reserve Bank of Minneapolis, 2021, https://www.minneapolisfed.org/article/2021/non-compete-contracts-sideline-low-wage-workers.
7 Harlan M. Blake, “Employee agreements not to compete,” Harvard Law Review, 1960, pp. 625–91.
8 See Marx, “The firm strikes back: non-compete agreements and the mobility of technical professionals.”; Matt Marx, Jasjit Singh, and Lee Fleming, “Regional disadvantage? Employee non-compete agreements and brain drain,” Research Policy, vol. 44, no. 2, November 11, 2014, pp. 394–404; and Natarajan Balasubramanian, Jin Woo Chang, Mariko Sakakibara, Jagadeesh Sivadasan, and Evan Starr, “Locked in? The enforceability of covenants not to compete and the careers of high-tech workers,” Journal of Human Resources, May 2020, pp. 1218–9931R1.
9 See Starr, “Consider this: training, wages, and the enforceability of covenants not to compete,”; Michael Lipsitz and Evan Penniman Starr, “Low-wage workers and the enforceability of non-compete agreements,” Management Science, vol. 68, no.1, January 2022, https://doi.org/10.1287/mnsc.2020.3918; and Matthew S. Johnson, Kurt Lavetti, and Michael Lipsitz. “The labor market effects of legal restrictions on worker mobility,” SSRN Electronic Journal, June 6, 2020, https://dx.doi.org/10.2139/ssrn.3455381.
10 See David Friedman, “Non-competition agreements: some alternative explanations,” unpublished preliminary draft, April 2, 1991, http://daviddfriedman.com/Academic/non-comp/Non-Competition.html; and Maureen B. Callahan, “Post-employment restraint agreements: A reassessment,” The University of Chicago Law Review, vol. 52, no.3, Summer 1985, pp. 703–28.
11 Rubin and Shedd, “Human capital and covenants not to compete.”
12 Jonathan M. Barnett, and Ted Sichelman. “The case for noncompetes,” University of Chicago Law Review, 87, 2020, pp. 953–1049.
13 In practice, unenforceable NCAs may resolve holdup problems to some degree if, (1) workers are unaware of the law (as in Prescott and Starr, “Subjective beliefs about contract enforceability”), or (2) workers cannot access legal counsel or otherwise face costs of breaking an unenforceable contract (as in Starr, Prescott, and Bishara, “The behavioural effects of (unenforceable) contracts,”). Classic efficient contracting theories do not consider these possibilities.
14 David J. Balan, “Labor non-compete agreements: tool for economic efficiency, or means to extract value from workers?” The Antitrust Bulletin, vol. 66, no. 4, December 2021, pp. 593–608, https://doi.org/10.1177/0003603X211045443.
15 Arnow-Richman, Rachel S, “Cubewrap contracts and worker mobility: the dilution of employee bargaining power via standard form noncompetes,” Michigan State Law Review, vol. 2006, No. 963, December 2006.
16 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force;” and Natarajan Balasubramanian, Evan Starr, and Shotaro Yamaguchi, “Bundling employment restrictions and value capture from employees.” SSRN Electronic Journal, April 2021.
17 For a summary, see Evan Starr, “Are noncompetes holding down wages?” In Sharon Block and Benjamin H. Harris, editors, Inequality and the Labor Market: The Case for Greater Competition (Washington, DC: Brookings Institution Press, 2021), http://www.jstor.org/stable/10.7864/j.ctv13vdhvm.13. For studies on the negative effects of NCAs, see Natarajan Balasubramanian, Jin Woo Chang, Mariko Sakakibara, Jagadeesh Sivadasan, and Evan Starr, “Locked in? The enforceability of covenants not to compete and the careers of high-tech workers,” Journal of Human Resources, May 2020, pp. 1218–9931R1; Lipsitz and Starr, “Low-wage workers and the enforceability of non-compete agreements,”; Johnson and Lipsitz, “Why are low-wage workers signing noncompete agreements?”; and Starr, “Consider this: training, wages, and the enforceability of covenants not to compete.” For studies finding positive effects, see Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force”; Lavetti, Simon, and White, “The impacts of restricting mobility of skilled service workers evidence from physicians”; Omesh Kini, Ryan Williams, and David Yin, “CEO noncompete agreements, job risk, and compensation,” Review of Financial Studies, vol. 34, no. 10, October 2021, pp. 4701–44, https://doi.org/10.1093/rfs/hhaa103; Liyan Shi, “The macro impact of noncompete contracts,” EIEF Working Papers Series, 2103, revised 2021.
18 Balasubramanian, Starr, and Yamaguchi in 2021 used data on NCAs and three other restrictions and show that selection effects likely underlie the positive average NCA–wage differential, while the true effect is negative. See Balasubramanian, Starr, and Yamaguchi, “Bundling employment restrictions and value appropriation from employees.”
19 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force” and Balasubramanian, Starr, and Yamaguchi, “Bundling Employment Restrictions and Value Appropriation from Employees.”
20 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.” Data from the 2014 Noncompete Survey Project is described in greater detail in J.J. Prescott, Norman Bishara, and Evan Starr, “Understanding noncompetition agreements: The 2014 Noncompete Survey Project,” Michigan State Law Review, vol. 2016, no.2, 2016, pp. 369–464. The project covers in total 11,505 respondents. It derives from an online survey that the authors created and deployed via Qualtrics in 2014. Note that data from the 2014 Noncompete Survey Project include both imputed and lower bound estimates, which differ in how they treat individuals who are unaware whether they have signed a noncompete; here we emphasize the lower-bound estimates. See also Stewart Schwab and Evan Starr, "Cornell National Social Survey," unpublished data, 2019. Data from the Cornell National Social Survey (CNSS) derives from a random digit dial survey of 1,000 respondents. The noncompete question from the CNSS data is very similar to the one in the NLSY97. Note that, relative to the NLSY97, which is cohort-specific, these surveys cover all age categories. Accordingly, in the Noncompete Survey Project Data we limit to the same age range as the NLSY97, and in the CNSS, we limit to 25–50, in order to keep a large enough sample to say anything meaningful.
21 Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.”
22 Values do not sum to 100 because of rounding. We also examined confidence levels by gender, education, wages, and NCA status. Across all these stratifications, at least 81.0 percent of workers are very confident in their NCA answer and at most 1.6 percent are not confident.
23 Legal jobs have the lowest use of NCAs (4 percent), which likely arises because they are the only occupation in which NCAs are unenforceable in all 50 states. See Russell C. Buffkin, “Non-competition clauses in law firm partnership agreements: how far can partnership agreements control future conduct of lawyers,” Journal of the Legal Profession, vol. 23, 1999, p. 325; and Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.”
24 See Rachel Arnow-Richman, “The new enforcement regime: revisiting the law of employee mobility (and the scholarship of Charles Sullivan) with 2020 vision,” Seton Hall Law Review, vol. 50, 2020, pp. 1223–59. Other states have NCA bans for some sets of workers, though most of these bans started in 2017 or later, see Russell Beck, “The changing landscape of trade secrets laws and noncompete laws around the country,” Fair Competition Law, May 2021, https://faircompetitionlaw.com/changing-landscape-of-trade-secrets-laws-and-noncompete-laws/.
25 Rubin and Shedd, “Human capital and covenants not to compete.”
26 The Armed Forces Qualification Test (AFQT) covers four sections of the Armed Services Vocational Aptitude Battery (ASVAB) and measures math and verbal aptitude. This test was given to NLSY97 respondents in 1997–98.
27 For information on job tasks, see David H. Autor and Michael J. Handel, “Putting tasks to the test: human capital, job tasks, and wages,” Journal of Labor Economics, vol. 31, no. 2, June 2009, pp. S59-S96.
28 Theoretically, one may worry that workers sort into NCAs on the basis of unobserved ability; and since unobserved ability also drives wages, such sorting will cause upward bias in the NCA–wage effect. The results in table 3 suggest that workers are not sorting in NCAs by ability, conditional on demographic characteristics.
29 Paul Goldsmith-Pinkham, Isaac Sorkin, and Henry Swift. "Bartik instruments: what, when, why, and how," American Economic Review, vol. 110, no. 8, August 2020, pp. 2586–624.
30 Practically, this condition means that anything else that affects wages must not also be related to NCAs. This condition will be violated if there are omitted variables that affect NCAs and wages, if there is reverse causality, etc.
32 Kenneth Burdett and Dale T. Mortensen. "Wage differentials, employer size, and unemployment," International Economic Review, vol. 39, no.2, May 1998, pp. 257–73.
33 Dale T. Mortensen and Christopher A. Pissarides, "Job creation and job destruction in the theory of unemployment," The Review of Economic Studies vol. 61, no. 3, July 1, 1994, pp. 397–415, https://doi.org/10.2307/2297896.
34 See Robert E. Hall, and Alan B. Krueger, "Evidence on the incidence of wage posting, wage bargaining, and on-the-job search," American Economic Journal: Macroeconomics, vol. 4, no. 4, October 2012, pp. 56–67; and Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.”
35 Percent changes are calculated by raising the constant e to the power of the coefficient in the table and then subtracting 1. In this case, , a 25-percent increase.
36 See Lipsitz and Starr, “Low-wage workers and the enforceability of non-compete agreements”; and Matthew S. Johnson, Kurt Lavetti, and Michael Lipsitz. “The labor market effects of legal restrictions on worker mobility,” SSRN Electronic Journal, June 6, 2020, https://dx.doi.org/10.2139/ssrn.3455381.
37 See Starr, “Consider this: training, wages, and the enforceability of covenants not to compete.”
38 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force”; and Schwab and Starr, "Cornell National Social Survey."
39 See Johnson and Lipsitz. “Why are low-wage workers signing noncompete agreements?”
40 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force;” and Balasubramanian, Starr, and Yamaguchi, “Bundling Employment Restrictions and Value Appropriation from Employees.”
41 See Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.”
42 See Michael Lipsitz and Mark Tremblay, “Noncompete agreements and the welfare of consumers,” SSRN Electronic Journal, January 25, 2022, https://dx.doi.org/10.2139/ssrn.3975864; and Naomi Hausman, and Kurt Lavetti. "Physician practice organization and negotiated prices: evidence from state law changes." American Economic Journal: Applied Economics, vol. 13, no. 2, April 2021, pp. 258–96.
43 See Natarajan Balasubramanian, Evan Starr, and Shotaro Yamaguchi, “Bundling employment restrictions and value capture from employees,” SSRN Electronic Journal, April 2021; and Starr, Prescott, and Bishara, “Noncompete agreements in the US labor force.”