How to Follow a Career Path Without Mistaking Sorting for Causation
The difficult part of studying non-compete agreements is not finding a wage difference; it is deciding what that difference means. This chapter focuses on how the Chicago Fed study follows workers through job-to-job transitions, changes in NCA status, and later wage outcomes. Understanding that design lets the reader distinguish a contract effect from the kinds of workers and jobs that tend to be sorted into NCA-covered employment, while also seeing why a careful comparison still depends on an assumption.
The basic problem is easy to state. Workers who sign NCAs may differ from workers who do not. They may have different abilities, occupations, industries, employers, education, or opportunities. Jobs with NCAs may also offer different training or pay. If we compare all NCA jobs with all non-NCA jobs, the result blends the possible effect of the restriction with the conditions that led a worker to take that job. The study’s solution is to look for a change in NCA status around a job transition and compare it with a transition where the status does not change.
What the work history can actually observe
The data come from the National Longitudinal Survey of Youth 1997, known as the NLSY97. It follows 8,984 U.S. men and women born between 1980 and 1984. Interviews were annual from 1997 through 2011 and biennial afterward. Respondents report jobs held since the previous interview, and those jobs can be linked across waves. Beginning in 2017, the survey also asked whether each job was subject to a non-compete agreement.
That combination gives the study something a one-time survey cannot: a sequence of jobs, wages, and transitions for the same people. It does not mean that NCA status is observed continuously for every job throughout the entire panel. The NCA measure arrives in the later survey waves used for the analysis, and the relevant sample is built from the observations that contain the needed information. That timing is an important boundary, not a flaw to hide. Longitudinal data improve the comparison, but they do not turn every year of a worker’s career into a fully observed experiment.
The study separates workers into two education groups: low education means less than a four-year college degree, while high education means a four-year degree or more. The split is useful because the investment and outside-option mechanisms may not have the same force in every labor market. It is not a complete description of a worker’s skill, occupation, employer, or bargaining power. The groups are a way to test whether one average NCA effect would conceal materially different wage paths.
The unit of analysis is a job-to-job transition. A transition occurs when one job ends and another begins within three months. A job is defined as a relationship with a specific employer, so a separation with recall is not used to identify a move. The researchers focus on regular jobs, exclude self-employment, non-traditional and military jobs, and omit government jobs and work without pay. They also impose wage, hours, region, and destination-job restrictions so that the transition and wage observations are usable in the analysis.
The study then assembles wages around the move. In survey years when the old job has ended, the data contain the last wage in that job and the current wage in the ongoing job. After the transition, the panel follows the worker’s main jobs, including the first post-transition job and later jobs when observed. This matters because the question is not simply, “What does an NCA job pay?” It is, “When NCA status changes at a move, how does the worker’s wage path compare with the path of a similar worker whose status does not change?”
That distinction changes the role of the descriptive wage gap. In the retained sample, NCA-covered jobs pay about 15% more for low-education workers and about 22% more for high-education workers than jobs without NCAs. But those are average levels across different worker-job combinations. The paper reports that the gaps shrink substantially and become insignificant when worker fixed effects and occupation or industry controls are imposed. The transition design follows the logic of that warning: start with a common person, observe a change, and compare the change with a carefully selected counterfactual.
The comparison, the horizons, and the assumption
The clean-controls design pairs each treated transition with workers who share the same NCA status in the prior job but do not experience a status change. A worker moving from a non-NCA job into an NCA job is compared with a worker moving from a non-NCA job into another non-NCA job. A worker leaving an NCA job is compared with a worker moving from an NCA job into another NCA job. The control is therefore not “everyone who never signed an NCA.” It is a worker whose starting restriction status is comparable and whose status remains unchanged for the relevant comparison.
The treatment variable records the direction of the status change. Moving into an NCA job is coded as a change of 1. Moving out of an NCA job is coded as −1. A worker whose status remains unchanged is coded as 0. The baseline NCA status is included separately, so the comparison does not quietly mix workers who began from different contractual conditions. The design asks what happens when the destination changes status, conditional on where the worker started.
There is a second condition that is easy to miss. For a given post-transition horizon, the analysis requires the NCA status to remain unchanged through that horizon. If the study is measuring the four-year wage response to entering an NCA job, the relevant observation must continue to satisfy the specified status condition through those four years. This makes the comparison cleaner by avoiding another treatment in the middle of the measured response, but it also means that the observations available at a longer horizon are not identical to those at the transition. A four-year estimate is about transitions that can be followed under the study’s rule, not about every worker who ever signed a clause.
The method is called a clean-controls local-projections difference-in-differences design. The name is technical, but its purpose is concrete. Ordinary two-way fixed-effects difference-in-differences can behave poorly when people receive treatment at different times and effects differ across treatment cohorts or across years since treatment. It can implicitly compare workers already affected by a treatment with workers who are only newly affected, then average effects that are not truly comparable. The clean-controls approach keeps the control group from being contaminated by prior or future status changes in the relevant horizon.
Local projections add a separate estimate for each horizon rather than forcing the whole response into one average number. The study estimates cumulative changes in log hourly wages relative to the wage before the transition. The coefficient at h = 0 represents the transition effect: the wage change realized around the move into or out of an NCA job. A positive value would fit the idea of an upfront compensating differential. Estimates at positive horizons, such as two or four years later, trace the subsequent wage trajectory. A positive gradient is consistent with a return to human-capital investment; a negative gradient is consistent with a weakening of outside options and earnings power.
Negative horizons are a placebo test. If workers whose NCA status will change already had a different wage trend before the transition, a later difference could be reflecting a pre-existing divergence rather than the status change. The paper reports that the low-education estimate at two years before the transition is close to zero and insignificant, which supports the absence of differential pre-trends in that comparison. This does not prove that every unobserved difference has been eliminated. It makes one important alternative explanation less visible in the measured pre-period.
Transition-year fixed effects absorb common timing influences, while the prior job’s NCA status accounts for different starting conditions. Together, these details make the design more disciplined than a simple before-and-after comparison. They do not answer every question. The identifying assumption is that, conditional on the prior job’s NCA status and the timing of the transition, whether the destination job has an NCA is quasi-random with respect to potential outcomes. In plain language, after the observed starting point and timing are taken into account, the destination’s NCA status must not still be systematically chosen for reasons that would have changed the worker’s wages anyway.
That assumption is demanding because destination jobs are not assigned by a researcher. A worker and employer may select one another for reasons that are only partly observed. The destination may differ in training, management, occupation, industry, location, or advancement prospects. The paper addresses some of these concerns by controlling for changes in occupation and industry and by estimating entry and exit separately, but those checks do not make the assignment random. They make the reported pattern more credible within the specified design while leaving room for time-varying selection and measurement limits.
The design also treats entry and exit symmetrically in its baseline model: the effect of entering an NCA job is assumed to be the inverse of leaving one. The authors relax that restriction by analyzing transitions into and out of NCAs separately. This is a useful check because a restriction’s effects need not be perfectly reversible. Losing an outside option and regaining one may not produce equal responses at equal speeds, especially if a worker’s skills, employer relationships, or confidence have changed in the meantime.
The same framework is used for job tenure, but the outcome is different. The study estimates the probability of switching to a subsequent job at a given horizon, conditional on remaining in the first post-transition job up to that horizon. That is a specific exit-hazard measure. It is not the same as observing every job search, every rejected application, or the full value of a worker’s mobility. A wage path can therefore be more clearly estimated than a tenure effect without contradiction: earnings and leaving behavior are related, but they are not interchangeable outcomes.
The authors report additional checks using compensation that includes signing bonuses and other non-base earnings, alternative sample restrictions, occupation and industry controls, and separate entry and exit specifications. The results remain broadly similar, although standard errors become somewhat larger in some cases. For both education groups, the estimated transition wage differential remains insignificant. These checks support the directional wage pattern within the design, but they do not validate the core quasi-random-destination assumption or eliminate possible error in measuring NCA status.
The sequence captures the design’s central discipline. It starts with a worker’s observed history, creates a comparison from the same contractual starting point, and then follows outcomes at defined distances from the transition. It does not show a random assignment because none exists. Nor does it show a court deciding the clause’s legal validity; the study is measuring what follows an observed change in NCA status.
A well-designed comparison narrows the question. It does not make the question disappear. The Chicago Fed study can speak most directly to wage trajectories and a defined tenure outcome among the retained NLSY97 transition sample. It can reduce the risk that fixed worker differences or contaminated controls drive the result. It cannot by itself observe every belief about enforceability, every investment made by the firm, or every opportunity a worker chose not to pursue. With those boundaries in place, the next question is what the design finds for low-education workers—and why their average NCA wage does not predict their later path.