Locked In? The Enforceability of Covenants Not to Compete and the Careers of High-Tech Workers

ABSTRACT

We study the relationship between the enforceability of covenants not to compete (CNCs) and employee mobility and wages. We exploit a 2015 CNC ban for technology workers in Hawaii and find that this ban increased mobility by 11 percent and new-hire wages by 4 percent. We supplement the Hawaii evaluation with a cross-state analysis using matched employer–employee data. We find that eight years after starting a job in an averageenforceability state, technology workers have about 8 percent fewer jobs and 4.6 percent lower cumulative earnings relative to equivalent workers starting in a nonenforcing state. These results are consistent with CNC enforceability increasing monopsony power.

New practices have emerged to facilitate employer collusion, such as noncompete clauses and no-raid pacts, but the basic insights are the same: employers often implicitly, and sometimes explicitly, act to prevent the forces of competition from enabling workers to earn what a competitive market would dictate, and from working where they would prefer to work.

—Alan Krueger, "The Rigged Labor Market" (April 2017)

I. Introduction

In an op-ed, Furman and Krueger (2016) proposed that monopsony power is holding back wage growth, economic dynamism, and innovation. ¹ This provocative thesis builds on recent scholarship examining frictions that reduce labor market competition (Manning 2011; Ashenfelter, Farber, and Ransom 2010; Boal and Ransom 1997 ). One such friction that has received significant public policy and media attention in recent years is the use of covenants not to compete (CNCs), which are employment provisions that prohibit a worker from leaving to join or start a competing firm. ² Indeed, dozens of new reforms have sought to ban CNCs, and such proposals were on the list of labor reforms of almost all 2020 presidential candidates. ³

The link between CNCs and monopsony power follows from the similarity of CNCs to moving costs. In particular, it has long been argued (for example, Manning 2003) that, in general, moving costs give firms monopsony power by restricting worker mobility. Similarly, because they increase the costs of moving to the firms most likely to value worker human capital (competitors), CNCs could facilitate monopsony power. Yet, the fact that CNCs are voluntarily agreed upon complicates this analogy—wouldn't workers only agree to significant mobility restrictions if they received some benefits in exchange? And wouldn't firms use them only because they need to protect their investments or valuable information? That is, couldn't CNCs actually encourage training and human capital investment, which could enhance higher worker productivity, and hence result in higher wages, such that banning them would make workers worse off?

Existing studies do not provide a clear answer to the question of whether workers are indeed hurt by CNC enforceability. An early literature considered how CNC enforceability might reduce job-to-job mobility ( Fallick, Fleischman, and Rebitzer 2006; Marx, Strumsky, and Fleming 2009; Marx, Singh, and Fleming 2015), but given the voluntary nature of these provisions, the key question is not how CNC enforceability affects worker mobility per se, but whether workers will be better off as a result. A budding literature does examine wage differentials associated with CNC enforceability, but there are three shortcomings. First, the results are mixed in terms of their main effects. ⁴ Second, while the policy proposals consider a complete ban of CNCs, none of the studies examine the wage effects of a full CNC ban. Third, no research examines the cumulative career effects of CNCs, which is important because CNCs necessarily entail dynamic, intertemporal trade-offs. CNCs imply post-employment mobility restrictions that could suppress wage growth over time, so that average population effects may hide interesting heterogeneity over a worker's career or job spell. ⁵

In this study, we address the aforementioned gaps using two complementary approaches. First, we exploit an unusual natural experiment in which Hawaii banned CNCs in 2015 for technology workers only . Using Quarterly Workforce Indicators (QWI, Appendix Table 1) data (which aggregates all quarterly unemployment–insurance records to the industry–state–quarter level), we find that new-hire monthly earnings for technology workers rose following the July 2015 CNC ban relative to other industries in Hawaii, relative to technology workers in other states, and in a triple difference specification that controls for industry–quarter, state–industry, and state–quarter effects. In our preferred specifications, we find that Hawaii's 2015 CNC ban increased new-hire monthly earnings by 4.2 percent, while overall (that is, all worker average) monthly earnings rose 0.7 percent. The difference between new-hire and overall earnings is important because the 2015 Hawaii CNC ban only applied to new contracts. We also study worker mobility using data from QWI and find Hawaii's CNC ban increased mobility (measured in terms of separation rates) for technology workers by 12.5 percent (relative to tech workers in other states).

While the Hawaii CNC ban for technology workers provides a unique opportunity to study the effects of an outright ban, two concerns prompt us to complement this analysis. First, it is based on only one state, raising potential concerns about generalizability. Second, the recency of the Hawaii ban and data constraints preclude examination of outcomes over workers' careers. Accordingly, we supplement this analysis using quarterly employer–employee matched data for the universe of employees in 30 U.S. states between 1991 and 2008, a time period in which CNC policies were relatively stable. Our empirical approach is similar to Starr (2019) in that we examine how within-state differences between workers more and less likely to be bound by CNCs vary with cross-state measures of CNC enforceability. We focus on technology workers as the treatment group for three reasons. In addition to aligning with the focus on high-tech workers in the Hawaii case-study, high-tech workers are the most likely to sign CNCs among all occupations (Starr, Prescott, and Bishara 2021), and they are also likely to have access to intellectual property that would theoretically precipitate the potential benefits of CNCs. ⁶

Under the key identifying assumption that the group of workers we identify as "technology" workers are more strongly affected by CNC enforceability, and assuming that all other state-specific mobility and wage drivers that may be correlated with enforceability impacts workers in the technology sector in a similar way as other (control) industries, the coefficient on the interaction of technology sector with our CNC enforceability index measure provides an estimate of the differential effect of CNC enforceability on technology workers. ⁷ We first document that, despite more stringent identifying assumptions, this pseudo difference-in-differences empirical approach corroborates the findings from the Hawaii experiment: compared to nontech workers, technology workers have, on average, 6 percent longer job durations but 2–2.8 percent lower quarterly earnings in an average enforceability state relative to states that do not enforce CNCs (compared to the same differential for nontech workers). We subsequently expand our analysis to account for the cumulative mobility and earnings effects across eight years of a worker's career. We find that eight years after starting a job in an average enforceability state, high-tech workers have 4.6 percent lower cumulative earnings and 8 percent fewer jobs relative to observably equivalent high-tech workers in a nonenforcing state. We also study cross-state and cross-industry transitions. We find that workers whose first jobs are in technology in higher enforceability states are more likely to move across states without switching industries, potentially as a way to circumvent the CNC while retaining industry-specific capital.

Both sets of empirical analyses are robust to a variety of alternative specifications and subsample analyses, which are described in the robustness checks section and appendixes. ⁸

Taken together, our results strongly suggest that CNC enforceability is associated with "job-lock" (similar to the findings of Gruber and Madrian 1994) and reduced bargaining power for the average technical worker (as discussed in Arnow-Richman 2001, 2006). In particular, our results suggest that CNC enforceability serves as a barrier to workers switching jobs and contributes to lower labor dynamism and wage stagnation. Together, these results contribute to the budding literature on CNCs and earnings by exploiting an unusual natural experiment and by studying cumulative career effects of CNC policies. The fact that the average tech worker does not appear to be compensated more for the CNC-related reductions in job-to-job mobility (for example, in any of the first eight years after starting a job) is also directly relevant for the state and federal policymakers who are actively debating changes to CNC policy (Office of Economic Policy, U.S. Department of the Treasury 2016; Burke 2016).

More broadly, our work contributes to the literature on monopsony in labor markets. Our finding of wage differences being correlated with CNC enforceability suggests a deviation from the "law of one wage" and contributes to work documenting wage dispersion (for example, Katz and Krueger 1992; see also the review by Bhasker, Manning, and To 2002). As in Naidu (2010), our results suggest that CNC enforceability slows down and redirects worker movement, reducing the returns to tenure and experience more broadly. Our findings are also consistent with Cahuc, Postel-Vinay, and Robin (2006), who find that between-firm competition is quantitatively more important than wage bargaining in raising wages above workers' reservation wages.

II. Examining Hawaii's 2015 CNC Ban for Tech Workers

A. Legal Background and Empirical Design

Given the policy and theoretical interest in identifying the causal effects of banning CNCs on wages, we begin with a rare but recent natural experiment: Hawaii, which previously enforced "reasonable" CNCs (Malsberger et al. 2010), banned CNCs for technology workers only, effective July 1, 2015. Specifically, the text of the Hawaii bill reads:

...it shall be prohibited to include a noncompete clause or a nonsolicit clause in any employment contract relating to an employee of a technology business. The clause shall be void and of no force and effect.

(HB 1090 H.D 2 S.D.2 C.D.1)

The stated reason for this ban was to promote growth of technology businesses, protect jobs, and encourage the establishment of new technology businesses by tech employees. ⁹

We use data from the Quarterly Workforce Indicators (QWI) to examine mobility and wage patterns before and after July 2015 in Hawaii. The QWI is a public use database provided by the U.S. Census Bureau and derived from the universe of unemployment insurance records in the state. ¹⁰ The data include a set of quarterly "economic indicators," including employment, job creation, earnings, and other measures of employment flows at the state–industry–quarter level. Relevant for our purposes, the QWI includes variables that track both the monthly earnings and mobility of workers.

Given that the ban on CNCs is specific to Hawaii and specific to the technology industry, we leverage both the state-specific dimension and the industry-specific dimension to perform three types of difference-in-differences (DID) analyses. In each design, firms and workers in the "technology business" per the Hawaii statute are the "treated" entities, but what varies across these designs are the control groups. In the first analysis, "Within-Hawaii, Cross-Industry" (hereafter "Within-Hawaii"), the control group is other industries in Hawaii. In the second analysis, "Cross-State, Within-Tech" (hereafter "Cross-State"), the tech sectors in the other 50 states form the control group. In the triple-difference analysis, we exploit the fact that our shock is both state- and industry specific, allowing us to identify the Hawaii × Tech × Post 2015 interaction while controlling for industry–quarter, state–industry and state–quarter fixed effects. We undertake Fisher Permutation test (randomization inference) checks for all of the approaches (Hess 2017; Rosenbaum 2002 ), and also a synthetic control check of the "Cross-State, Within-Tech" DID results (Abadie, Diamond, and Hainmueller 2010).

Section 2 (d) of the Hawaii HB1090 bill defines a "technology business" to mean "a trade or business that derives the majority of its gross income from the sale or license of products or services resulting from its software development or information technology development, or both." Further, it states that "'Software development' means the creation of coded computer instructions", and that "'Information technology development' means the design, integration, deployment, or support services for software." Thus, we define "Tech" as NAICS four-digit subsectors related to software development, design, and related services. ¹¹

To examine how tech wages change following the CNC ban, we examine two QWI wage variables—average monthly earnings of workers in full quarter employment ("EarnS"), and average monthly earnings of all hires into full-quarter employment ("EarnHirAS"). While the ban on CNCs can be expected to improve the bargaining power of workers, because wage adjustment/renegotiation for existing workers is infrequent (and typically at year-end), larger effects should be expected for the latter, as wages for hires should reflect the changed bargaining position immediately after the ban. To obtain comparable length of pre- and post-ban trends, we examine data from 2013Q2–2017Q1 (the latest available data). To examine mobility responses, we construct a separation rate measure defined as the ratio of all separations of workers from employers in the quarter (variable named "Sep" in QWI) to total employment count (variable named "EmpTotal" in QWI). As an alternative, we use a defined separation rate variable available in the QWI—Beginning-of-Quarter Separation rate ("SepBegR") which is Beginning-of-Quarter Separations divided by average employment. ¹²

Our basic specifications are:

DID Cross-Industry, Within-Hawaii Analysis:

DID Cross-State, Within-Tech Analysis:

Triple Difference (DDD) Analysis:

where the subscripts j, k, and t are for industry, state, and quarter, respectively; Σ_t are year-by-quarter fixed effects; and ω _j are a set of industry fixed effects (NAICS four-digit codes). For the Cross-State analysis, we also allow for industry-by-year–quarter and state-by-industry fixed effects. In the triple difference analysis, ω_jk are a set of state–industry fixed effects, Σ_jt are industry × year-by-month (industry × year-by-quarter in QWI) fixed effects, and Σ_kt are state × year-by-quarter fixed effects. ¹³ Standard errors are clustered at the industry level in the Within-Hawaii analysis, and at the state level in the other two.

Within each of the alternative DID approaches and for the triple difference analysis, we check robustness to using alternative comparison groups. In particular, for the Within-Hawaii analysis, we use a smaller comparison group of the four-digit industries, which belong to the same two-digit level definition of the tech sector ("Tech 2d sector"), as well as a comparison group of all nontech four-digit sectors. Similarly, for the Cross-State and DDD analyses, we use a comparison group that excludes outlier CNC enforceability states by limiting the sample to the 40 states with CNC enforceability index scores (discussed in more detail in Section III.B below) closest (in absolute terms) to Hawaii in the pre-ban period, as well as a comparison to group of all other states.

B. Hawaii CNC Ban Results

We first discuss the wage effects. Figure 1 presents the time trends of the wage variables from QWI. In the top panel, the pre-ban trends in the wage variables are similar across

Figure 1.

Hawaii CNC Ban and Wage Variables from QWI

Notes: This figure presents period-specific means (controlling for industry fixed effects in the "Within-Hawaii, Cross-Industry" graphs and for state fixed effects in the "Cross-State, Within-Tech" graphs). Data are limited to the state of Hawaii in the "Within-Hawaii, Cross-Industry" graphs (top panel) and to "Tech" industries in the "Cross-State, Within-Tech" graphs (bottom panel). "Tech" is defined as QWI four-digit industry classifications that cover software design, development, and services, to concord with the definition of "technology business" in the Hawaii statute. Log Overall Average Monthly Earnings is the log of group average of overall Average Monthly Earnings (Full Quarter Employment) (that is, log EarnS). Log Hires Average Monthly Earnings is the log of Average Monthly Earnings of All Hires into Full Quarter Employment (that is, log EarnHirAS). The group average means are weighted means, with industry–period Beginning of Quarter Employment (Emp) as (analytical) weights. Data are from the QWI, 2013Q2–2017Q1.

tech and other sectors within Hawaii. After the ban, the tech sector overall log wages show a short-run upward spike (left figure), as do log hiring wages (right figure). In the longer run, the other industry wages appear to climb upwards, so the trend changes catch up with those for tech. In the bottom panel, the short-run increase in log overall wage appears partly to be a reflection of a similar jump for tech wages in other states (left figure). However, in the bottom-right figure, the increase in hiring wages for the tech sector in Hawaii appears to be systematically greater than for tech hiring wages in other states.

These patterns are largely confirmed by the regression results in Table 1. ¹⁴ Panel A presents Cross-Industry, Within-Hawaii specifications, and Panel B presents Cross-State, Within-Tech results. Columns 3, 4, 7, and 8 present full-sample results, while Columns 1, 2, 5, and 6 present comparisons to narrower groups (other industries within two-digit technology sector in Panel A, and the 40 states closest to Hawaii in terms of CNC enforceability in Panel B). While the overall post-ban change is small and not statistically significant for overall wages in the Within-Hawaii (Panel A) analysis, there appears to be a notable increase in hiring wages (significant relative to all other industries in Column 7), with the effect driven by a large short-run increase. The Cross-State comparison in Panel B shows a systematic increase in the wages for tech workers in Hawaii relative to tech workers in other states, and these effects (with additional industry-by-quarter and state-by-industry fixed effects) appear to be more precise than suggested by the trends in Figure 1. The magnitude of the cross-state effects is largest for the hiring wage, which increases by 0.078 log points in Column 5 (or 0.071 in Column 7). This is more than 50 percent of the standard deviation in the pre-ban log wage rate for tech workers in Hawaii (0.14 log points). As discussed earlier, because overall average wages reflect the contracted wage for all workers, including those that do not have or are not seeking outside opportunities, and including workers who may have pre-existing contracts with CNC clauses (which were not affected by the ban), the lower magnitude of effects on overall average wage is not surprising. Overall, the results suggest modest effects on overall wages, but stronger increases in hiring wages.

These DID analyses are confirmed by the DDD results in Panel A of Table 2. Our preferred specifications show an increase in overall (that is, all worker average) monthly earnings of 0.7 percent (Panel A, Column 3) and a 4.2 percent increase in new-hire wages after the ban (Panel A, Column 7). These results are reassuring, showing that the increases in wages are robust to Hawaii-specific and tech-specific shocks that may have coincided with the ban. In particular, the results for wages are consistently larger and more significant than in the Cross-Industry, Within-Hawaii analysis.

The mobility results are shown in Figure 2, which displays the time trends of the mobility variables from QWI. The top panel shows the Within-Hawaii trends and compares the Hawaii tech sector to other industries in Hawaii, controlling for industry fixed effects. The tech sector in Hawaii shows a distinct increase in the short run following the ban, though there appears to be a reversal and greater volatility in the postban trends. In contrast, the trends for other industries in Hawaii don't show a significant jump just after the ban, but exhibit a slow increase in mobility, so that towards the end of

Table 1.

QWI Wage Variables Analysis from the Hawaii Natural Experiment—Difference-in-Differences Results

Table 2.

QWI Wage and Mobility Analysis from the Hawaii Natural Experiment—Triple Difference Results

Figure 2.

Hawaii CNC Ban and Mobility Variables from QWI

Noes: This figure presents period-specific means (controlling for industry fixed effects in the "Within-Hawaii, Cross-Industry" graphs and for state fixed effects in the "Cross- State, Within-Tech" graphs). Data are limited to the state of Hawaii in the "Within-Hawaii, Cross-Industry" graphs (top panel) and to "Tech" industries in the "Cross-State, Within-Tech" graphs (bottom panel). "Tech" is defined as QWI four-digit industry classifications that cover software design, development, and services, to concord with the definition of "technology business" in the Hawaii statute. The Overall Separation Rate is defined as All Separations (Sep) divided by Employment in the Reference Quarter (EmpTotal). The "Beginning-of-Quarter Separation rate" is beginning of quarter separation rate (SepBegr). The aggregated means are weighted means, with industry–period Beginning of Quarter Employment (Emp) as (analytical) weights. Data are from the QWI, 2013Q2–2017Q1.

our window, the mobility levels are similar for other industries in Hawaii. The bottom panel of Figure 2 shows the cross-state trends and compares the tech sector in Hawaii to tech sectors in other states, controlling for state fixed effects. The tech sectors in other states do not show any surge in mobility after July 2015, and the increased mobility levels in the tech sector in Hawaii are generally higher than for the other states. Overall, the surge in mobility in Hawaii after the ban is consistent with a release of mobility restrictions, and suggests facilitation of reallocation by the CNC ban.

These graphical results for QWI mobility variables are confirmed by regression results in Table 3. We find that there is an increase in the separation rate in the Within- Hawaii analysis (Panel A), particularly relative to other industries in the Tech 2d sector (Columns 1 and 5), and this is most pronounced in the short run (first four quarters) after the passage of the ban (Columns 2 and 6). The overall increase of 1.25 percent relative to other tech sectors in Column 1 translates to a 13.7 percent increase in mobility when compared to the mean separation rate of 9.1 percent for the tech sector in the pre-ban period. The point estimate is smaller in Column 3 (0.272 percent, or 3 percent of pre-ban mean separation rate), though this overall effect is a combination of a surge in the short run (0.753 percent or 8.3 percent of pre-ban mean separation rate) and a reversal in the long run. In Panel B, relative to other states, the tech sector in Hawaii shows systematically higher mobility in both the short and long run, and across both QWI mobility variables. The magnitude in Column 1 and Column 5 are very similar and is about 12.5 percent of the pre-ban mean separation rate. Results for the alternative mobility variable in Columns 5–8 are similar to the overall separation rate variable in Columns 1–4, for both panels.We note that the mobility patterns may have been affected by anticipation of the passage of the statute, and in this context it is reassuring that the magnitude of the effect we find from the ban (about 12.5 percent, comparing tech sector across states) is similar to the 15.4 percent effect found for inventor mobility from the increase in enforceability for Michigan stemming from a state supreme court decision (which may have been less anticipated) in Marx, Strumsky, and Fleming (2009). Panel B of Table 2 examines a triple-difference specification for mobility variables, and we get consistently significant effects, with magnitudes in linewith that in the cross-state within-tech results. In particular, we find a 10.75 percent increase in overall separation rate (0.00979/0.091, in Column 3) and a 11.3 percent (0.0096/0.085, in Column 7) increase in beginning-of-quarter separation rate. ¹⁵

One challenge associated with studying the case study of a change for one state is that the traditional DID inference approach may have shortcomings. In particular, as discussed in Buchmueller, DiNardo, and Valletta (2011), who study the effects of Hawaii's Prepaid Healthcare Act which mandated employer health insurance, standard inference may be insufficiently conservative and clustering approaches may have shortcomings because only one state experiences the policy change.We check and confirm statistical significance of our estimates using two prominent alternative approaches used in the literature in contexts similar to ours: (i) inference using a synthetic control group and (ii)

Table 3.

QWI Mobility Analysis from the Hawaii Natural Experiment—Difference-in-Differences Results

inference using permutation tests, also used by Buchmueller, DiNardo, and Valletta (2011). In Online Appendix C, we check robustness of the Cross-State, Within-Tech analysis, using a synthetic control group approach proposed by Abadie, Diamond, and Hainmueller (2010). In this approach, a synthetic matched control is constructed based on a weighted average of states, with optimal weights constructed so that the predicted (from a factor model) dependent variable of interest for the synthetic control closely fits the pre-treatment trend in the treated state. Inference of statistical significance uses a variation of the Fisher permutation test, and goodness of fit (using a mean square prediction error measure) relative to the synthetic control in the post-treatment vs. pretreatment for the "treated" synthetic state relative to placebo runs involving other states (as in Figure 8 in Abadie, Diamond, and Hainmueller 2010). We undertook a synthetic matched control analysis comparing the tech sector in Hawaii to the synthetic control composite of the tech sector in others states. ¹⁶ We obtain a good fit for pre-trends relative to the synthetic control for all variables and find significance relative to synthetic control at 7 percent for average hiring wage and and at 2 percent for mobility variables (but lower at 19 percent for average wages). ¹⁷

In Online Appendix D, we verify the robustness of our results to a randomization inference (or permutation test) approach (Hess 2017 ). The randomization inference approach, analogous to Fisher permutation tests, collects estimates of Equation 2 across 500 replications that randomly allocate the tech indicator across four-digit sectors (in the Within-Hawaii analysis) and across states (in the Cross-State analysis), allowing us to examine how our point estimates compare with the distribution of potential point estimates using similarly sized alternative subsets of industries and states. We find results that are qualitatively consistent with those in the baseline analysis (Tables 1 and 2). In particular, for wage variables, we find stronger significance for increase in average hiring wage after the ban, and generally stronger significance when comparing tech sector in Hawaii to the tech sector in other states. We also find stronger cross-state, within-tech effects for mobility variables, with larger effects in the short-run period after the ban.

One caveat to keep in mind when interpreting our results is that the Hawaii statute included a prohibition of "nonsolicit" clauses (intended to prevent ex-employees from soliciting clients). Because these clauses are also broadly intended to discourage competition from ex-employees, this could be viewed as another form of restriction on competition; nevertheless, when considering implications of our results for policy interventions, it should be noted that the effects we find arise from a prohibition of both noncompete and nonsolicit agreements. ¹⁸

III. Examining Cross-State Variation in CNC Policies with Matched Employer–Employee Data

While the Hawaii analysis is a rare, policy-relevant opportunity to identify how banning CNCs influences worker wages and job-to-job transitions, the analysis has a few important limitations. First, Hawaii's labor market is geographically isolated, which raises concerns about the potential generalizability of the findings. Second, because the changes are recent, we lack individual-level data examining how the CNC ban may change long-term dynamics related to the evolution of wages within and across jobs. Third, the ban on CNCs simultaneously banned nonsolicitation agreements, suggesting that the effects we identified could be driven by the combination of the two provisions being banned, rather than just CNCs. Motivated by these limitations, in this section we bolster and extend the findings from the Hawaii experiment using employer–employee matched data covering all workers from 30 states for 1991–2008. ¹⁹

The data come from the Longitudinal Employer-Household Dynamics (LEHD) database at the U.S. Census Bureau and are derived from the universe of unemployment insurance records of employees (the same source as the QWI data used above). There are two advantages of the LEHD. First, the LEHD provides employment history data for individual workers over a long horizon for a full spectrum of industries across a large number of states that vary in CNC enforceability levels. Second, the quarterly administrative data on all firms provides a clear measure of job transfer, mobility, and wage at a high frequency, largely free from selection issues that may arise in studies that use patent or listed-firm executive employment data ( Marx, Strumsky, and Fleming 2009; Garmaise 2011).

Despite these benefits, the main downside of the LEHD is that it does not cover a time period with many major exogenous changes in the enforceability of CNCs to use within-state variation to identify the causal effects. Garmaise (2011), for example, identifies several such changes, but only one of those changes occurs during our timeframe, and Census disclosure rules require at least three states to have the same policy shock to disclose the estimated coefficient. ²⁰ Given these limitations, the only feasible identification strategy is to exploit cross-state heterogeneity in the enforceability of CNCs, which requires stronger identifying assumptions. Fortunately, cross-state variation in the enforceability of CNCs is large, and several recent studies have created indexes that seek to measure these differences (Bishara 2011 ; Starr 2019; Lavetti, Simon, and White 2020).

A central challenge to using only cross-state variation in enforceability is the concern that other omitted state-level variables may be correlated with our outcomes of interest, as well as with CNC enforceability. We describe our identification strategy and assumptions in detail in Section III.C below. The key idea is that we identify one group of workers—specifically workers employed in the "technology" sector (as defined below in Section III.C.1)—as those for whom CNC is likely to have a greater impact, and make the assumption that only CNC enforceability (and not other omitted state level variables) has a differential impact for this group of workers.

A. LEHD Data and Sample Construction

We construct two samples with the LEHD: a job-level (that is, worker–firm combination) data set and a worker-level data set that tracks workers within and across jobs (that is, their employment history). ²¹ In both data sets, we drop all left-censored jobs (that is, individual worker jobs spells that started before the beginning of our panel period). We do so because we do not know the lengths of the latent spells for these jobs (as we do not know the start date of these spells) or the characteristics of these jobs at the beginning of the spell, which we use to construct our job-level fixed effects (as described below). Further, dropping these jobs avoids bias from stock sampling. We also drop workers whose first-year annual income in the LEHD is less than $35,000 in 2008 dollars (close to the 10th percentile of 2008 earnings in the tech sector per the 2008 Occupational Employment Statistics), to focus on high-earning workers who are the most likely to sign CNCs (Starr, Prescott, and Bishara 2021). Secondary jobs (defined by the share of that job's earnings to the worker's total earnings) whose spell is continuing in parallel to another job for the same worker are also dropped. ²²

In terms of our key earnings outcomes, in the job-level analysis we measure log quarterly earnings at the 1st, 4th, 8th. 32nd quarters of the job spell, CPI-adjusted to 2008 dollars. ²³ We also examine log cumulative earnings within the job, and within job wage growth relative to the starting wage at the 4th, 8th. 32nd quarters of the job spell. In our analysis across the worker's employment history, which tracks wages regardless of whether the worker switches jobs, ²⁴ we use as a dependent variable, the cumulative earnings of the worker at the 4th, 8th, ., 32nd quarters since the worker started their employment history.

As before, we supplement the wage results with analyses of worker mobility. In the joblevel analysis, we measure the length of the job spell defined as the log number of quarters the worker was employed at the firm. To mitigate concerns about right-censoring, we restrict our sample to jobs whose spell started in 2000 or earlier for this analysis, so that we have a minimum of eight years of observations for each worker. ²⁵ The second approach avoids the right-censoring issue entirely by using a set of dummy variables for the job spell surviving a given length of time as the dependent variables: a dummy variable with a value of one if the job spell survives until the 4th, 8th, …, 32nd quarter of its spell (or eight years). These job-level analyses miss, however, the cumulative effect on job switches across multiple jobs. Accordingly, we also examine the cumulative number of jobs taken (in logs) and the number of state or industry switches (in logs) over the course of the worker's eight year employment history (estimated at the 4th, 8th. 32nd quarter). ²⁶

B. Index Measuring Cross-State Differences in CNC Enforceability

A central component of our empirical approach with the LEHD data is to measure the extent of CNC enforceability across states. We adopt the index derived in Starr (2019), but before describing the specifics of the index, we begin with a brief overview of the law and the ideal measure of CNC enforceability. States regulate CNCs, and states have historically come to very different positions related to whether and the conditions under which CNCs should be enforced (Bishara 2011). A handful of states (for example, California, North Dakota) will not enforce CNCs related to job-to-job mobility (exceptions are made in the context of CNCs ancillary to the sale of a business). Prior work on the California policy, which was adopted in 1872, has linked it to the growth of Silicon Valley (Gilson 1999; Fallick, Fleischman, Rebitzer 2006).

All other states enforce CNCs that pass a "reasonableness" test, though the contours of that test differs across states—what one state deems reasonable, another may not. Various editions of a treatise on CNC enforcement across states edited by Malsberger and coauthors (for example, Malsberger et al. 2010) provide detailed descriptions of the conditions under which each state will enforce a CNC. All prior measures of CNC enforceability review this treatise and score states on various dimensions of CNC enforceability (Stuart and Sorenson 2003; Bishara 2011; Garmaise 2011). These dimensions include, for example, whether the state will enforce CNCs even if a worker is fired, whether continued employment is sufficient consideration for the enforcement of a CNC, and whether the state courts can rewrite or "blue-pencil" overbroad provisions. A full list of the components in the index in Bishara (2011), which forms the basis for the Starr (2019) index used in this paper, is provided in Appendix Table 2.

Existing indexes score several of these dimensions, with higher scores reflecting that it is easier to enforce CNCs, and then aggregate these dimensions to obtain a statespecific score. Garmaise (2011) reviews 12 dimensions of enforceability and gives each dimension a score of one or zero. Bishara (2011) similarly scores seven dimensions from zero to ten (again with higher meaning easier to enforce). Furthermore, Bishara—a former practicing attorney who litigated CNCs—attempts to weight each dimension of CNC enforceability on the basis of his subjective assessment of its importance, while the Garmaise (2011) measure gives each dimension equal weight. This weighting is theoretically important. If we would like to measure the enforceability of CNCs in a given state (defined as the probability of enforcement for a random violator of a CNC), we would have to know not only the situations under which a state would enforce a CNC (as captured in the Malsberger treatises), but also the probability with which those conditions occur. For example, if a state enforces CNCs when a worker is fired, but such an event is either rare or nonexistent, then such a policy will not have any real effect on the probability of CNC enforcement.

We use the measure of CNC enforceability derived in Starr (2019) , which uses factor analysis of the seven underlying dimensions across all states of CNC enforceability initially scored in Bishara (2011) for both 1991 and 2009, to back out an estimate of a (latent) enforceability index for these years. The resulting index is normalized to have a mean of zero and a standard deviation of one in a sample where states are given equal weight; the index ranges from –4.23 for North Dakota to 1.60 for Florida. The scores for 1991 and 2009 have a correlation of 0.94, reflecting that during this time there is very little change in how states enforced CNCs. We use the 2009 measure for our analysis. Figure 3 presents the enforceability index scores by state. California and North Dakota have the lowest scores, while the highest enforcing states are Florida and Connecticut.

A potential concern about the CNC enforceability index arises from the fact that the measures for California and North Dakota are markedly lower than for other states. Administrative constraints related to use of LEHD data preclude a straightforward robustness check in the form of excluding these two states. As an alternative, we undertake and confirm robustness of all of our key results to using the rank of the indexes, which significantly mutes the differences in levels (see discussion in Section III.G).

A summary of states classified into three groups of high, medium, and low enforceability, as well as a brief description of enforceability provisions in a typical state in each group, is provided in Appendix Table 3. The index we use is not very different from, and hence highly correlated with, the Bishara (2011) index used in the literature (for example, Lavetti, Simon, and White 2020), as, rather surprisingly, the factor weights generated from the factor analysis by Starr (2019) closely match the subjective weights used by Bishara (2011). ²⁷ The means for the dummy variable measure used in Stuart and Sorenson (2003) by different enforceability groups are provided in Column 5 of Appendix Table 3 and show that our measure is broadly consistent with their measure as well.

Enforceability of CNCs is not geographically clustered in a systematic way, as there is significant variation within regions of the United States (Figure OA8 in the Online Appendix provides a geographic heat map of the index). To get a sense of what types

Figure 3.

Factor Analysis CNC Enforceability Index Scores for 2009 from Starr (2019)

of characteristics may be associated with this measure of state CNC enforceability, we examine how this measure was correlated with a range of state-level variables that could plausibly affect worker wages or mobility, around the midpoint of our data period (year 2000). Our analysis shows that our enforceability index has very little correlation with state per capita income, state corporate tax rates, union density, right to work law adoption, and different exceptions to the employment-at-will doctrine (taken from Autor, Donohue, and Schwab 2006), which could impact worker firing and hence mobility), with the R-squared from a regression including all seven state-level variables equal to 0.122. ²⁸

C. Empirical Approach with LEHD Data

1. Identification assumptions and definition of "tech" workers

The key identifying assumptions for the cross-state LEHD analysis are the following: (A1) the group of workers identified by us as "high technology" (high-tech or tech) workers are more strongly impacted by CNC enforceability than other workers, and (A2) other omitted state-level variables that may be incidentally correlated with CNC enforceability have a similar impact on high-tech and non-high-tech workers.

Specifically, we assume that variable Y_ks that measures the outcome in a job spell (for example, wage at end of Quarter 4 in a job spell) in state s and in sector k has the following form:

where R_s represents a vector of (omitted) state-level regulatory or other characteristics that can affect the outcome variable, CNC_s represents our enforceability measure, and I{Tech} _k is a dummy indicator variable for if the sector k belongs in high-tech (the definition of high-technology sector is explained in detail below). In general, the omitted R_s variables could be correlated with CNC_s, which makes it impractical to recover an unbiased estimate of parameter γ from cross-state regressions of the type we use. However, because by our assumptions CNC (but not other omitted state-level variables) has an additional impact on outcomes for job spells in the technology sector, we can recover an unbiased estimate of δ by including state fixed effects that condition out the effect of R_s. We want to note that under our assumptions, the estimated parameter δ yields only the differential effect of CNC enforceability on the group of workers we define as "high-tech" workers anδ hence must be interpreted carefully. ²⁹

The plausibility of our identifying assumptions rests importantly on our definition of high-technology workers. We define a worker, or more accurately a worker–firm pair job spell, as belonging to "high-tech" if the industry of the firm (as defined in the LEHD at the start of the job spell) belongs to a "Technology Employer" industry NAICS code (aggregated to three-digit level) per the classification in Paytas and Berglund (2004) . This definition uses a categorization of "science and engineering intensive occupations" based on U.S. Bureau of Labor Statistics Occupational Employment Statistics (OES) codes, developed by Chapple (2004), and an occupation–NAICS employment concordance provided by the Bureau of Labor Statistics to obtain the share of employment in science and engineering intensive occupations for each NAICS code. Paytas and Berglund then define "Technology Employers" as those NAICS industries where the share of employment in science and engineering intensive occupations exceeds three times the national average (that is, a cutoff of 9.98 percent, as the national average was 3.33 percent in 2002). We aggregate this definition to the NAICS three-digit level. ³⁰ Job spells in these "Technology Employers" industries form our treatment group, hereafter referred to as "hightech" or "tech" jobs, whereas jobs in "Other Industries" are referred to as "nontech jobs."

Given our definition of "high-tech" jobs, we believe Assumption A1 is plausible for two reasons. First, using nationally representative survey data, Starr, Prescott, and Bishara (2021) conclude that "the use of noncompetes is highest for technical occupations (computer, mathematical, engineering, architecture) in the manufacturing and information industries." Because our definition of high-tech workers relies on share of science and technology occupations within the sector, it is likely these workers are more subject to noncompetes and hence more likely to be impacted by CNC enforceability. To provide a sense of the differential in the use of CNCs across sectors, we note that Starr, Prescott, and Bishara (2021) find that 26.3 percent of workers in Information, Mining and Extraction, Manufacturing, or Professional, Scientific, and Technical Services sign CNCs, compared to 15.6 percent in other industries. Second, the sectors we define as high-tech are more intellectual property–intensive, as reflected in the commonly used (albeit imperfect) measure of patent counts. Specifically, our estimation using USPTO and QWI national data for the period 2000–2004 (where QWI national coverage is more complete than prior years) shows that these sectors accounted for 62.1 percent of all patents granted in this period, while accounting for only 14.5 percent of total employment. ³¹

Assumption A2 is an important one that we believe is plausible for several potential sources of omitted variable bias. For example, other labor regulations (such as exceptions to employment-at-will examined in Autor, Donohue, and Schwab 2006 ) ³² could be expected to impact firing (and hence mobility and wages) for a broad set of industries, not just the high-technology industries. However, any characteristics correlated with wages and CNC enforceability that have a differential relationship with tech or non-high-tech workers would lead to a violation of A2 and bias our estimates. In a key robustness check, we relax ASSUMPTION A2 by making a weaker assumption that the subgroup of more highly paid workers within the high-tech sector are more strongly impacted by CNC enforceability and that other omitted factors do not impact this specific subgroup differently. This approach is discussed briefly in Section III.G and in more detail in the Online Appendix A.

One particular weakness of Assumption A2 is that other state-level characteristics could influence selection of certain types of (for example, larger) firms or (for example, younger or more male) workers into a state, and these firms or workers may be associated with different levels of mobility or wages specifically for the high-tech sector. For example, if young male workers in high-tech are highly mobile, and young workers are attracted to low CNC locations (for example, California) because of other factors potentially correlated with enforceability, then we might find higher mobility associated with low CNC enforceability induced by this selection. Fortunately the richness of the LEHD data allows us to include a very rich set of interacted {sector by firm size by worker age by gender by initial wage by job-spell starting year} fixed effects that flexibly condition out biases from this type of sector–worker–firm–cohort selection effects.

2. Empirical specification

Equation 4 displays our estimating equation for the job-level analysis, which captures the differential relationship between CNC enforceability and outcomes for tech versus nontech workers, with additional subscripts to capture additional details in our actual estimation:

Similar to the discussion above, Y_ijkts denotes a job-spell-level outcome variable of interest (for example, wage at end of Quarter 1 of the job spell). The subscripts i, j, k, l, and s denote individual, job spell, industry, firm, and state, respectively. Our coefficient of interest is δ, which estimates the differential association between CNC enforceability and the dependent variable for high-tech jobs relative to nontech jobs. CNC_s is the 2009 CNC enforceability index measure (defined as discussed in Section III.B above) of the state where the job spell is observed. I{Tech}_k is one if the firm of the worker–firm pair is in one of the "Technology Industries" (defined as discussed in Section III.C.1 above). S_s denotes state fixed effects, which subsumes the main effect of CNC enforceability and controls for the direct effect of omitted state-level variables that affect wages and mobility. In addition to these basic controls, we include the aforementioned fixed effects in FE(i,j,k,l). Each joint fixed effect defines a group of jobs that are common (that is, fully interacted) in terms of their three-digit NAICS codes, job-spell starting year, firmsize group, job-spell starting-wage group, job-spell starting-age group of the worker, and gender of the worker. ³³ FB_i is a dummy that denotes whether the worker is foreignborn, which we include because foreign-born employees are subject to visa-related employment eligibility constraints that may affect their mobility (and wages).

For the worker-level analysis of career outcomes (in Section III.E), such as cumulative number of jobs taken, cumulative wages, and cumulative number of states (or industries), the CNC enforceability measure is that of the state in which the worker's first job is located. The job-level variables and the job-level fixed effects are based on the initial characteristics of the first observed job.

D. Job-Level Results

We first corroborate our baseline findings in the Hawaii analysis by examining the joblevel results. Table 4 presents the mirror of our Hawaii results in the context of our LEHD Analysis, tracking the relative effect of a one standard deviation increase in CNC enforceability on tech versus nontech workers. We observe a persistent negative relation between enforceability and wages. The coefficient δ ranges from 0.5 percent to 0.7 percent for high-tech jobs compared with nontech jobs in a given quarter, and lower earnings of 2.5 percent in the quarter hired. To put these estimates in context, assuming a uniform causal effect over the distribution of enforceability scores, applying the average enforceability score to a nonenforcing state (a difference of four standard deviations) suggests that moving from a ban to average enforceability would be associated with 2–2.8 percent lower wages for the average technical worker in a given quarter. The coefficient estimates and the 95 percent confidence intervals, translated to reflect the effect of applying the average enforceability score to a nonenforcing state (a difference of four standard deviations), are plotted in Figure 4. The wage profile is relatively flat, so the wage penalty of CNCs is similar in log difference terms over the job tenure. Column 1 of Table 4 presents results on the initial start of job spell wage (this specification naturally excludes initial wage fixed effects)—consistent with the results for new-hire wages for Hawaii, we find that initial wages are lower in states with higher CNC enforceability. Thus, there is no evidence that lower wages later in the job spell are offset by higher initial wages. Overall, the results are consistent with a reduction in bargaining power starting early in the job tenure of tech workers.

Table 4.

CNCs and High-Tech Workers' Wage across Job Tenure (LEHD)

Figure 4.

CNCs and High-Tech Workers' Wage across Job Tenure (LEHD)

Notes: This figure plots the coefficient estimates of the differential relation of CNC enforceability with wage, for high-tech jobs relative to nontech jobs, translated to reflect the effect of applying the average enforceability score to a nonenforcing state (a difference of four standard deviations) and the associated 95 percent confidence intervals. Wage is the log of quarterly wage at 4th, …, 32nd quarter of the job spell. Data are from the LEHD (1991–2008).

Next, in Table 5, we examine the relation between CNC enforceability and workers' cumulative wage and wage growth across job tenure. We measure wage growth as the difference between the log of monthly earnings at 4th, 8th, …, 32nd quarters of the job spell and the log of initial wage of the job. The results show that cumulative wages decline with CNC enforceability for tech workers, and the magnitudes of these declines increase over job tenure. For wage growth, the negative coefficient on CNC enforceability displays a U-shaped pattern. To provide context for the coefficient estimates, the results in Panel A suggest that applying the average enforceability score to a nonenforcing state would be associated with 4 percent lower cumulative earnings eight years into a job for the average tech worker relative to a nontech worker.

We next examine the duration of jobs. Table 6 presents the differential effect of CNC enforceability on mobility from estimating Equation 4. The column titles denote the dependent variables for each of the specifications. We find that an increase of one standard deviation in the enforceability score is associated with a 1.5 percent increase in the mean job-spell duration (Column 9). This is driven by rightward shifts in the job-spell distribution in higher enforceability states beginning in Year 2 (Column 2). An increase of one standard deviation in enforceability is associated with a 0.5 percentage points increase in the probability that a job spell lasts at least eight years (Column 8). Given that only 12.4 percent of all job spells last eight years, a onestandard-deviation increase in enforceability increases the likelihood that the job lasts

Table 5.

CNCs and High-Tech Workers' Cumulative Wage and Wage Growth across Job Tenure (LEHD)

Table 6.

CNCs and High-Tech Workers' Job Duration (LEHD)

Figure 5.

CNCs and High-Tech Workers' Job Duration across Job Tenure (LEHD)

Notes: This figure plots the coefficient estimates and the 95 percent confidence intervals of the differential relation of CNC enforceability with job duration, for high-tech jobs relative to nontech jobs (from Table 6 ), translated to reflect the effect of applying the average enforceability score to a nonenforcing state (a difference of four standard deviations), normalized by the mean probability of surviving to the end of that quarter. For example, the point estimate of 0.0.0052 for the 32nd quarter (column 8 of Table 6) translated for the effect of a four standard deviation change yields 4 × 0.0052 = 0.0208; this is normalized by the mean probability of surviving to Quarter 32 of 0.124 (from Online Appendix Table OA2) to yield the plotted point of 0.0208/0.124 = 0.1677. Job duration is measured as the dummy variable for the spell surviving at 4th,., 32nd quarter of the job spell. Data are from the QWI, 2013Q2–2017Q1.

at least eight years by 4 percent (0.5/12.4). ³⁴ Applying the average enforceability score to a nonenforcing state would imply a 6 percent increase in the mean job-spell length (similar to the 8 percent observed in Marx, Strumsky, and Fleming 2009) and a 16 percent increase in the likelihood that jobs last at least eight years. Figure 5 presents a graphic illustration of the coefficient estimates and the 95 percent confidence intervals in Table 6, translated to reflect the effect of applying the average enforceability score to a nonenforcing state (a difference of four standard deviations) relative to the mean probability of surviving to that quarter. The increase in the effect of CNC enforceability on the relative mobility of tech workers over the tenure profile is consistent with employees gaining more intellectual capital and, hence, beingmore strongly targeted by firms for CNC enforcement.

Together, the results in this section corroborate the baseline patterns observed in the Hawaii analysis: CNC enforceability is associated with longer job spells and with lower wages both initially and throughout the job spells.

E. Career Outcomes across Employment History

In this section, we exploit the richness of the LEHD data to extend the frame of analysis beyond single job spells (as in Section III.D above) to examine if and how the CNC enforceability level in a state where a worker started their initial job impacts cumulative earnings and job transitions across the span of the worker's career.

In Table 7, for cumulative earnings (Panel A) and mobility (Panel B), we observe persistent differentials associated with CNC enforceability. In Panel A, we find a gradually increasing and then decreasing wage suppression with CNC enforceability across employment history, such that eight years after starting a job in an average enforceability state a worker has on average 4.6 percent lower cumulative earnings relative to an equivalent worker who started a job at the same time in a nonenforcing state. For mobility, we find that themagnitude of the decline is gradually increasing across employment history, such that a one-standard-deviation increase in enforceability is associated with a 2.1 percent decrease in the number of jobs after eight years, which translates to an 8.2 percent differential (or about 0.22 additional jobs as mean log cumulative jobs after eight years is 0.939), when comparing an average enforceability state to a nonenforceability state.

One notable distinction between the cumulative earnings regressions at the career level (Table 7) versus at the job level (Table 5) is that the latter are conditional on the employee staying in the same job at the tenure examined (for example, the end of Quarter 24 analysis in Table 5 is conditional on workers staying in the job until Quarter 24). The mobility results (Table 6) suggest that high-tech workers in higher enforceability states have longer job spells than nontech workers. Thus, the estimated coefficients for the joblevel wage regressions could be affected by a composition effect, with the direction of the effect depending on whether the workers that quit in low-enforceability states would have had higher or lower earnings had they stayed on than the average for those who did not quit. To the extent that the more productive workers are more likely to find job opportunities, the coefficients in the job-level analyses would be biased toward zero. The larger magnitudes of the coefficients in Panel A of Table 7 compared with those in Table 5 suggest this is indeed the case.

F. State- and Industry-Switching Behavior across Employment History

If variation in CNC enforceability were indeed material as our previous results suggest, one way to circumvent CNC enforceability would be to transfer to jobs outside the geographic scope of the CNCs (for example, the state) or to jobs in other industries. In this subsection, we examine the total number of state switches, industry switches, state but not industry switches, and industry but not state switches across the workers' employment histories. The analysis is conducted at the worker level, similar to the analysis in Section III.E, and we use the same specifications, except we replace the dependent variables with log (1+ cumulative number of state switches), log (1 + cumulative number of industry switches), and log (1+ cumulative number of state-but-not-industry-switches), and log (1+ cumulative number of industry-but-not-state-switches). We define state and industry switches as changes in state and the three-digit NAICS code of theworker's employer, respectively.

In Table 8, we observe a greater frequency of state switches for high-tech workers with initial employment in a high-enforceability jurisdiction, compared with nontech workers (Panel A). In contrast, greater enforceability is associated with a negative differential effect on the number of industry switches for workers in high-tech industries across their

Table 7.

CNCs and High-Tech Workers' Career Outcomes across Employment History (LEHD)

employment history (Panel B). Panel C and Panel D show that what is driving these contrasting results is that greater enforceability is associated with workers switching states but not industries. ³⁵

These results suggest that while tech workers in high-enforceability states are more likely to switch states to avoid enforcement, they appear to have greater industry-specific human capital, so they are more likely to stay within the industry when they change jobs. This is consistent with greater investment in industry-specific human capital (or endogenous location of activities requiring industry-specific human capital) by firms in high-CNC locations ( Marx 2011; Starr, Ganco, and Campbell 2018). Taken together with the baseline results of the significantly lower frequency of job changes by tech workers in high-enforceability jurisdictions, these results suggest that CNC enforceability places noticeable constraints on the frequency and direction of worker mobility across jobs.

G. Robustness Checks

We perform several checks to assess the robustness of the aforementioned results.

1. Triple difference between high and low-wage jobs within tech

As discussed in Section III.C.1, a key assumption (A2) in our baseline pseudo DID approach is that omitted state-level variables, unlike CNC enforceability, do not differentially impact tech-sector workers. We relax this assumption by making a narrower assumption that the mobility and wages of only the highest paid tech workers are differentially impacted by CNC enforceability. This affords a triple difference DDD approach that allows for state-by-industry fixed effects, where we compare differences in impacts for the highest paid (top 2 percent) tech workers relative to other tech workers net of the analogous difference between the highest paid and other workers in nontech industries. Online Appendix A provides a detailed discussion of this analysis, and the results presented there confirm that there is indeed a differential lowering of mobility and wages for the highest paid subsegment of tech workers in locations with higher CNC enforceability, as expected.

2. Local labor market thickness

One potentially important concern is that unobserved local labor market thickness may be (incidentally) negatively correlated with enforceability and also correlated with greater wages and mobility (as thicker markets could imply greater competition among labor-demanding firms, as in Cahuc, Postel-Vinay, and Robin 2006). We repeat our main analysis of job-spell duration and wages, controlling for local labor market

Table 8.

CNCs and High-Tech Workers' Switching States or Industries (LEHD)

thickness proxied using total employment in state/three-digit NAICS code/year (in logs). The results (available in the Online Appendix Table OA3) are remarkably similar to the baseline results.

3. Using CNC ranks instead of raw score

Another potential concern is that California's large economy and near-complete CNC nonenforceability (an outlier among the CNC scores used in the baseline analysis) could be inordinately influencing the results. We therefore repeat our analyses in Section III.D, using ranks of the 2009 CNC enforceability index scores, which is free from extreme values by construction. The 2009 CNC enforceability index score ranks are assigned integer values of 1 to 50 across the 50 state values and are standardized (to have mean zero and standard deviation one). Larger values correspond to stronger CNC enforceability, and smaller values correspond to weaker CNC enforceability. In results presented in the Online Appendix (Table OA6 and Table OA7), we find that estimates using CNC ranks are very similar to those using CNC scores in terms of statistical significance and signs, and the magnitudes are similar as well (for a hypothetical change moving from California to Florida).

4. Balance of enforceability measures across missing and available states

Because the LEHD data we had access to does not cover all 50 U.S. states, there could be a bias as a result of workers' relocations to missing states. For example, when a worker is transferred to an establishment of the same firm that is located in a non-LEHD state, we lose track of the worker, potentially yielding a right-censoring in the spell measure. If firms relocate workers from low-enforceability states to high-enforceability states to protect their knowledge, and if the missing states have higher levels of CNC enforceability, there would be a positive bias in the estimated effect. However, a t-test for difference in the enforceability index scores between the states included in the LEHD and the states not included in the LEHD yields a p-value of 0.83, suggesting there is no significant difference in mean CNC enforceability scores across states in and out of the LEHD sample, which alleviates such a concern.

5. Robustness of job-spell analysis to using alternative samples

Finally, due to right-censoring, we restricted the sample to jobs that started in the year 2000 or earlier for our analysis of job-spell lengths. In an unreported analysis, we find that the results for the log of job-spells analysis are robust to the sample of non-rightcensored jobs that started in the year 2000 or earlier. We also repeat the job survival analysis and the wage analysis on the sample of jobs that started in year 2000 or earlier and find that the results are robust. The estimation results are available upon request.

IV. Discussion

This study uses a recent natural experiment in Hawaii and detailed matched employer–employee data from the U.S. Census Bureau to examine how CNC enforceability affects wages and employee mobility for workers in the technology sector. The longitudinal analysis of the recent ban on CNCs for tech workers in Hawaii suggests that the ban increased wages at hiring for tech workers, as well as mobility. In the cross-sectional analysis, higher CNC enforceability is associated with longer job spells, a greater likelihood of leaving the state, and a reduced propensity for crossindustry movement for tech workers. Most importantly, we also find that compared with their peers in low-enforceability states, tech workers in states with high enforceability receive reduced wages throughout a given job as well as over their career.

Our analysis of the Hawaii policy change is the first study of the impact of a complete ban on CNCs. Our cross-sectional analysis using the LEHD is the first to use comprehensive employer–employee matched data to examine the relative effect of CNC enforceability on tech workers, and it fills two important gaps related to: (i) variations in the effect of CNC enforceability over a worker's career and (ii) joint state–industry switching behavior to circumvent CNCs. Regarding the latter, we find nuanced results for job switching: there is increased propensity to move across states but decreased propensity to switch across industries, explained primarily by tech workers who leave the state but stay in the same industry. These results are consistent with greater investment in industry-specific human capital (or endogenous location of activities requiring industry-specific human capital) by firms in high-enforceability locations (Marx 2011; Starr, Ganco, and Campbell 2018).

Our finding of lower mobility of tech workers from CNC enforceability (both from the analysis of the Hawaii noncompete ban and from the cross-sectional analysis using LEHD data) is consistent with prior studies of CNC enforceability and mobility, such as Marx, Strumsky, and Fleming (2009); Marx, Singh, and Fleming (2015); and Garmaise (2011). The two former studies find that inventor mobility was reduced and redirected out of state following Michigan's reversal of its policy not to enforce CNCs. Based on within-state changes in enforceability, Garmaise (2011) finds reduced intra-industry mobility among top executives. Relative to these studies, our examination of job spells covers a significantly larger and less-selected sample that tracks mobility for all tech workers with greater accuracy. In particular, our data avoid four limitations of mobility measurement using inventor patent filings (discussed in detail in Agarwal, Frake, and Ganco 2018). ³⁶

Over the employee job spell for tech workers, we find that the potential impact of CNC enforceability on the duration of the job spell is lowest at short tenures, but rises at longer tenures. These results are consistent with CNCs being enforced only after workers gain or learn significant appropriable intellectual capital, indicating that CNC enforceability has a smaller effect early in the job tenure. ³⁷ The higher impact at midtenure is consistent with Lazear and Gibbs (2014, p. 82–85), suggesting that the value of a worker to a firm is highest for mid-career workers, making it more likely that firms enforce CNCs on such workers.

Lower mobility alone does not necessarily imply a negative effect on workers. Workers may trade off mobility in return for higher wages resulting from increased firm investments in their human capital. For instance, Lavetti, Simon, and White (2020) find that physicians who sign CNCs have higher earnings and earnings growth. In contrast, we find that stricter CNC enforceability is associated with lower wages, both initially and throughout the tech worker's tenure. ³⁸ In this respect, our results are similar to those in Garmaise (2011) and Starr (2019). The wage analysis in Hawaii finds similarly sized short-run increase in wages for hires following the ban on CNCs for tech workers.

Our last finding examining outcomes over the career of a tech worker suggests that starting a job in an average enforceability state—regardless of whether the individual eventually leaves their initial job or state—is associated with reduced earnings of 4.6 percent eight years after starting the job compared to a tech worker in a nonenforcing state. This finding is important because, contrary to models in which early training or information sharing investments will increase productivity and thus worker pay in later periods (that is, Rubin and Shedd 1981), it suggests that the dominant effect of CNC enforceability for the average technical worker is to depress wages (relative to nontech workers).

Together, our results strongly suggest that CNC enforceability lowers worker welfare, consistent with CNC enforceability reducing workers' bargaining power relative to the firm and "locking" them into their jobs, as argued by Arnow-Richman (2001, 2006), and consistent with the lack of negotiation over CNCs observed in Starr, Prescott, and Bishara (2021). Our results are thus consistent with CNC enforceability creating monopsony power, leading to deviations from the law of one wage, reducing the elasticity of labor supply (Bhasker, Manning, and To 2002; Manning 2011; Ashenfelter, Farber, and Ransom 2010), and dampening labor market dynamism (Furman and Krueger 2016).

In line with Krueger's (2017) concerns about CNCs facilitating collusion quoted at the beginning of the paper, our findings also highlight a potential similarity between labor market collusion and the enforceability of CNCs. The "gentleman's agreements" signed by Apple, Google, and many other tech companies in California to not recruit each other's employees served to reduce both wage competition and mobility between competitors (Helft 2009). ³⁹ Mukherjee and Vasconcelos (2012) model these agreements as alternate mechanisms for extracting surplus from productive workers, and our findings suggest that the outcomes for tech workers from high CNC enforceability may be similar to those due to labor market collusion under oligopsony (Krueger and Posner 2018).

Supplementary Material

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