How the Study Knows the Hiring Shift Was Not Just a Story
The subject of this chapter is the NBER study’s test of whether harassment-related NDA reforms changed hiring at venture-backed startups. The focus is not the technical label “difference-in-differences” for its own sake, but the counterfactual behind the headline: compared with similar startups that had not yet faced the legal change, did female hiring move differently where the reform took effect? Understanding that comparison—and its limits—lets us read the reported decline as evidence to weigh rather than as a statistic detached from its denominator.
From legal exposure to a startup-year comparison
The researchers combine two kinds of records. PitchBook identifies U.S. startups that received venture financing. Revelio Labs supplies worker employment histories drawn primarily from online profiles such as LinkedIn. Linking them lets the study observe more than a company’s total headcount. It can count hires, identify job titles and seniority, and follow promotions and departures. It can also classify workers by education and other characteristics, although some of those fields are missing and gender is inferred probabilistically from names rather than reported as a direct administrative attribute.
The final state-level panel contains 52,607 unique VC-backed startups and 207,469 startup-year observations. The study follows a young firm from its founding year through age five, then removes it when it ages out or when the database reports an acquisition, bankruptcy, or initial public offering. It measures hiring in the startup’s headquarters state. That geographic choice is important: the state law is expected to apply to the workforce subject to that state’s rules, not simply to wherever the company was incorporated. It also keeps the legal exposure aligned with the location that generates the study’s comparison.
The sample is substantial, but it is not the whole startup economy. Online employment data are especially strong for professional, managerial, and technical workers. The manuscript reports broad coverage of white-collar profiles and meaningful, though lower, coverage of the overall labor force. A startup that hires workers who do not maintain visible online profiles may be represented incompletely. A worker whose gender, age, education, or job title cannot be inferred may not appear in a subgroup analysis. These are not footnote inconveniences; they determine what population the estimate describes.
The treatment is a change in legal exposure over time. A startup is treated when its headquarters state has enacted an NDA-weakening law by that year. The researchers then compare outcomes before and after treatment with outcomes for startups in states that have not enacted such a law, while accounting for persistent differences between startups and common changes across calendar years. In plain language, the question is whether the treated group’s change is larger or smaller than the change that would have occurred anyway.
This is the counterfactual the design needs. Suppose female hiring falls in 2019 in a state that adopted a reform. That fall by itself proves little: a local recession, a change in the startup mix, or a national shift in recruiting could have caused it. The relevant comparison is what happened to comparable startups that were not yet exposed to the reform during the same period. If both groups moved together before the law, then diverged at the reform date, a reform-linked explanation becomes more plausible.
The design also uses the headquarters state as more than a convenient label. The paper argues that a startup cannot necessarily evade the relevant rule simply by incorporating elsewhere, because state employment law can govern workers who primarily work in the state. This keeps treatment connected to the legal environment experienced by employees. It does not mean every worker in a company faces identical exposure, or that a company with offices in multiple states is governed by one simple rule. The study’s main comparison is a firm-level measure of headquarters-state exposure, not a worker-by-worker legal opinion.
The unit being compared is a startup in a particular year. That sounds obvious, but it prevents several common misreadings. The outcome is not the number of women already employed, nor the number of complaints, nor a survey score for workplace culture. It is the flow of new female workers into the headquarters-state workforce. A startup may have a stable female staff and still hire fewer women in a given year. Conversely, a single hire can matter a great deal in a firm that is only beginning to build a team. The paper therefore studies an entry decision, not a complete measure of gender equality inside the organization.
The choice of a count outcome also reflects the reality of startup hiring. Many young firms hire no one in a given year, while a few add several employees. A model designed for counts with many zeroes can use that uneven distribution without pretending that every startup has a smooth, continuous hiring rate. The reported percentage is consequently a change in an estimated hiring flow. It should not be read as a claim that every treated firm cut a fixed share from a planned slate of female candidates.
The comparison absorbs two kinds of persistent background difference. A startup fixed effect means that a firm’s stable characteristics—such as its founding team, sector, or baseline propensity to hire—do not have to be mistaken for the legal reform. Calendar-year effects absorb shocks common to startups across states, including nationwide changes in financing or recruiting. The design still depends on the assumption that, absent the reform, treated and comparison startups would have followed sufficiently similar paths. Fixed effects make that assumption more plausible by removing some differences; they cannot observe a counterfactual firm that experienced everything except the change in law.
The age restriction is another interpretive boundary. The study follows firms through their first five years because early-stage hiring is where workforce composition is being established and because the sample can be constructed consistently around founding. It does not show what happens when a startup becomes a mature employer with a larger HR function, a different ownership structure, or a workforce spread across many jurisdictions. A result that is strong in the early stage may weaken, persist, or change direction as the organization develops. The same limitation applies to the question of recovery: the observed panel can show persistence over its window, not whether later adaptation reverses the initial change.
Finally, the legal treatment is assigned at the state-and-year level, while hiring decisions are made by people inside firms. That gap is exactly why the study is informative and why it cannot reveal motive directly. A state rule can alter the expectations of founders, managers, employees, lawyers, and investors at once. One firm may respond by improving its systems; another may respond by narrowing recruitment; a third may do both. The estimate averages across those responses. The pattern across firm size, prior female representation, and worker seniority—examined later—helps distinguish them, but the baseline comparison alone does not tell us which internal decision produced each observed hire count.
The flow from records to conclusion has a deliberate stopping point. The data can show that the number or share of women hired changed after a legal reform. They cannot show that a particular hiring manager rejected a particular candidate because of expected harassment liability. They do not record whether a startup had an actual harassment incident, whether its reporting channel was independent, or whether its employees felt safer. The design can test a relationship between legal exposure and aggregate employment behavior; it cannot turn that relationship into a transcript of individual decisions.
What the estimates mean—and why the checks matter
The baseline result is a relative change, not a national count. In the study’s main count specification, the coefficient on legal exposure is approximately -0.081. Converted into a percentage, that implies startups in treated states hired about 7.8% fewer women per year than the comparison group after the reform. The NBER landing page summarizes the result as about an 8% reduction. The estimate is economically meaningful for young firms because they hire only a few people in a typical year. A percentage change in a small flow can determine whether a firm adds one person, waits, or never crosses the threshold of having a woman in its early workforce.
The study checks whether the result is simply an overall employment contraction. It is not what the reported patterns suggest. The female share of annual hires falls by 1.2 percentage points from an average of about 34%, a relative decline of roughly 3.5%. Direct estimates of male hiring are statistically insignificant and economically small. When the researchers place male and female counts in the same comparison, the interaction implies that treated startups hire about 5–6% fewer women relative to men. The important judgment is therefore gender-specific: the reform-linked change is not just “startups hired fewer people.”
There are two ways to count the female-hiring response. The first is the intensive margin: among startups that hire women, how many women do they hire? Conditional on making at least one female hire, that number falls by about 3%. The second is the extensive margin: does a startup begin hiring any woman at all? Among startups that had not previously hired a woman, the probability of making a first female hire within one year of treatment falls by 2.8 percentage points. Within four years, the decline reaches 4.9 points. Relative to the relevant sample means, those correspond to approximately 10% and 12% reductions.
The two measures answer different questions and should not be added together. A firm can remain willing to hire women but hire fewer of them, or it can avoid beginning female hiring altogether. The extensive-margin result matters because early composition can accumulate. The first female employee may become a colleague, recruiter, manager, or source of referrals for the next group. The study does not prove that a delayed first hire permanently determines a startup’s culture, but it shows why a small annual response can have consequences beyond the year in which it is measured.
A credible before-and-after design needs more than a plausible story. The first check is the pre-trend. In the four years before a state reform, the study finds no evidence that female hiring in treated startups was already diverging from the control group. The coefficients are economically small and statistically indistinguishable from zero. The negative change appears sharply in the first year after enactment and persists over the following years in the observed state-level window. That timing is consistent with a reform-linked break rather than a gradual trend that happened to be labeled as treatment.
The second check addresses a problem specific to reforms adopted at different times. In a simple two-way fixed-effects comparison, an early-treated state can unintentionally help form the comparison group for a later-treated state. If effects differ across cohorts or change over time, that can distort the estimate. The authors therefore use a stacked regression that compares each treatment cohort with startups in states that never received the reform, rather than allowing already-treated units to serve as implicit controls. The resulting coefficient is approximately -0.090, close to the baseline -0.081. That similarity does not prove the design is perfect, but it makes it less likely that the headline result is an artifact of the staggered timing alone.
The geographic placebo is especially intuitive. State laws should affect hiring in the legal jurisdiction where the startup’s workforce is exposed, not hiring in other states that have not adopted the reform. The study replaces headquarters-state hiring with female hiring in the startup’s non-headquarters states that did not adopt an NDA-weakening law. That coefficient is statistically insignificant and close to zero. If a company-wide product shock, founder departure, or general change in strategy were driving the result, the decline should appear outside the treated headquarters state too. Its absence supports the claim that the legal exposure is doing meaningful work.
The authors also report that the baseline result survives excluding the post-2019 period, which reduces the opportunity for the COVID-19 pandemic to explain the finding, and excluding California and New York, two large early-adopting startup hubs. These tests matter because the reform period overlaps with unusual macroeconomic conditions and because a few large states could otherwise dominate a sample of venture-backed firms. A later federal reform supplies an additional comparison among previously untreated states, but its interpretation as a demand-side test becomes more useful once we examine why the effects concentrate where they do.
None of these checks removes every alternative explanation. Reforming states may differ from other states in ways the controls do not capture. The adoption sequence may correlate with other policies. Online profiles may overrepresent particular occupations, and the gender measure is inferred rather than directly observed. The study’s state-level analysis also ends in 2022, so persistence after that date is not established by the main sample. These limitations do not make the estimate meaningless; they define the claim it can support.
The careful version of the conclusion is this: across a large panel of young U.S. VC-backed startups, female hiring falls after headquarters states adopt laws that weaken harassment-related NDA enforceability, relative to the comparison pattern for unexposed startups. The fall appears in both the number of women hired and the chance of beginning female hiring, while male hiring does not show a comparable response. Pre-trends, alternative estimation, geographic placebo, and robustness exclusions all make a reform-linked interpretation more credible. But the evidence is still aggregate and quasi-experimental. It does not identify an individual decision, prove a single motive, measure actual harassment, or settle the law’s long-run effect on workplace safety.
That last distinction is what makes the next question possible. The estimate is not evenly distributed across all women or all startups. It is sharper among junior women and in small or male-dominated firms, while skill-level differences are less decisive. Those patterns can tell us whether the hiring response looks more like a firm managing expected legal exposure or workers changing where they want to work.