How Researchers Know the Equity Response Is Not Just Selection
The Finnish evidence is designed to answer a specific question about employee equity in startups: when equity holders appear more likely to stay and advance, is that because ownership changes their behavior or because firms give equity to people who were already different? The distinction matters for anyone trying to understand what an equity grant does. A large gap between holders and non-holders can be informative, but it cannot by itself tell us what would happen if a different employee received the same grant. To interpret the causal result, we need to know who is in the data, what changed independently of a startup's compensation decision, and which assumptions connect that change to later outcomes.
What the Finnish data can see—and what they cannot
The study combines linked administrative records on employment, wages, ownership, financial statements, and union coverage. Its unit of observation is an individual working for a startup in a given year, while some ownership measures are constructed at the firm level. The sample contains 16,347 Finnish startups, 97,016 startup-year observations, and 2,060,012 individual–startup–year observations. It covers firms founded between 2006 and 2022 that are newly incorporated limited liability companies, reach at least ten employees at some point, and report complete shareholder information. Because the outcomes look from year t to year t+1, the main estimates use years through 2021.
Those boundaries are part of what makes the data interpretable. The ten-employee threshold excludes the smallest owner-managed businesses, where the relationship between founder and worker may be less like an internal labor market. Requiring complete shareholder information excludes some incomplete cases. The resulting data are population-wide within the defined administrative setting, not a sample of every startup in every country. The study can observe a very large number of employment and ownership relationships, but it cannot turn that scale into universal applicability.
The ownership records also show why employee equity is economically relevant even though it is not common. Among startups that survive to at least age ten, founders' average ownership falls from 71.6% at founding to 50.4% at age ten. Over the same conditional life cycle, managers' ownership rises from 0.3% to 6.1%, rank-and-file employees' from 1.0% to 2.4%, and venture-capital ownership from 1.8% to 7.1%. These are descriptive averages, not a prediction for an individual grant. They show a firm becoming more diffuse as it matures while founders remain the dominant owners. Employee equity occupies a small share of the total structure, but a small share can still affect the decisions of the person who holds it.
The raw mobility patterns make the selection problem impossible to ignore. The unconditional annual exit rate in the sample is 30.0%, and the promotion rate is 3.96%. In the first year of tenure, exit is 43.8% among employees who never hold equity in the focal firm and 14.2% among those who do. Equity holders also have higher promotion rates across tenure. If these numbers were read as treatment effects, they would suggest a dramatic power for ownership. But equity may be allocated to employees with higher expected productivity, stronger attachment, or different outside opportunities. Firms that grant equity may also have better prospects, more resources, or a different approach to management. The gap tells us that equity and mobility are related; it does not tell us which direction the relationship runs.
That is why the study's descriptive evidence must be kept separate from its causal evidence. The first-year comparison is useful as a diagnostic: it identifies the outcome that a compensation mechanism might plausibly affect and shows how much selection could matter. It is not evidence that giving equity to a randomly chosen non-holder would reduce their probability of exit by the same amount.
The regulatory change supplies outside variation
The causal design begins with collective-bargaining extensions. In Finland, a negotiated agreement can be extended so that its occupation–experience wage schedule becomes legally binding across an industry, including firms that were previously uncovered. The relevant firms are not all treated in the same way. A previously unionized firm was already subject to the schedule and should experience little discrete change at the extension date. A previously non-unionized firm may have to raise cash wages for workers whose prior compensation is below the schedule.
The study uses pre-extension union status to define exposure. That timing matters: the firm's status is measured before the regulatory event, rather than being chosen after the firm has adjusted its equity plan. The industry-level extension is therefore an external change in the cash requirement for the firms newly brought under the schedule. Removals provide additional variation by restoring wage-setting discretion, although they need not undo the original response. A wage increase imposed by law does not automatically disappear when the floor is removed, and equity allocations may reflect multi-year contracts and financing history.
The design becomes more informative by using differences among workers within a firm. The negotiated schedule itself is not directly reported in the administrative data, so the study estimates it using the modal annual wage bin among unionized firms in the same occupation, experience, industry, and year cell. For a worker in a non-unionized firm, the proportional shortfall between their prior wage and that modal schedule measures how far below the likely floor they were. The interaction between the extension and this predetermined shortfall should be larger for workers who face a larger mechanical wage increase.
This is not a generic before-and-after comparison. A recession, a hiring change, or a new workplace policy could affect every employee in an exposed firm. Such a change would not automatically line up with the worker's wage shortfall before the extension. The design instead combines industry-level regulatory timing, firm-level prior coverage, and worker-level pre-existing exposure. Each layer answers a different concern: when the shock occurs, which firms face a new obligation, and which workers should feel it most directly.
The first-stage evidence follows the predicted sequence. Extension exposure raises wages and reduces logged individual employee shares by about 0.114 log points in the baseline share equation. The extension-by-wage-shortfall interaction produces strong within-firm variation in wages. Event-time results show no anticipatory movement in equity before the extension, while equity adjusts around the event and declines persistently afterward. The reported pre-extension equity coefficients are jointly insignificant, with an F-statistic of 0.65 and a p-value of 0.629 for the years five through two before the extension. These results do not prove that nothing else changed, but they are difficult to reconcile with a story in which equity had already been falling in response to an anticipated employee outcome.
The instrument is useful only if the regulatory change affects exit and promotion through the compensation variables being instrumented. That is the exclusion restriction. Collective agreements contain provisions besides wages, including hours, leave, and dismissal procedures. An extension could also coincide with an industry demand shock, a broad change in labor demand, or the failure of a financially weak firm. The paper addresses these possible paths with firm-by-tenure and year fixed effects, specifications with industry-by-year effects, worker-level exposure, and checks designed to distinguish firm survival from individual separation. Exit observations exclude firm-years in which the startup exits in the following year, and promotion is measured among people who remain employed.
These tests strengthen the interpretation without making the assumption disappear. The worker-level wage-shortfall interaction is especially helpful because a firm-wide institutional change should not mechanically produce a pattern aligned with each employee's prior position relative to the wage schedule. But an identification strategy is still a structured argument about what did not happen through another channel. The relevant question is whether the remaining alternatives are plausible enough to overturn the compensation interpretation, not whether a statistical design can remove all uncertainty.
The diagram separates what is observed from what is used for identification. The raw gap travels directly from ownership status to an outcome, which is why selection is a concern. The regulatory path instead runs through predetermined exposure and the first-stage changes in wages and equity. The exclusion restriction is not another outcome; it is the condition that makes the second-stage path interpretable as an equity effect rather than a direct effect of the extension or an unrelated shock.
What the instrumental-variable estimate means
The resulting estimate is local. It applies to employees whose ownership stakes respond to changes in binding cash compensation constraints induced by extensions and removals—especially workers in previously uncovered firms whose wages fall below the negotiated occupation–experience schedule and whose firms adjust compensation in response. It does not describe the average effect of equity for every employee, including someone who receives a grant voluntarily in a firm with ample liquidity or someone whose wage already exceeds the schedule.
This local interpretation also explains why the study instruments both shares and wages in its baseline outcome equations. Wages and equity are jointly determined components of compensation. If the extension raises cash pay directly and the firm changes equity at the same time, attributing the whole outcome to ownership would be too strong. The design uses the regulatory variation to isolate the components of both variables that are induced by the wage constraint. In the baseline specifications, the reported Kleibergen–Paap statistics are 29.38 for exit and 28.74 for promotion, supporting instrument relevance under the stated model. Relevance is necessary, however; it is not the same as validity.
The outcome definitions matter as well. Exit is a one-year indicator for leaving the startup, conditional on the firm surviving, regardless of the destination employer. Promotion is upward movement to a higher-ranked one-digit occupational category, or promotion to CEO for managers, conditional on continued employment. A lower exit rate under these definitions means fewer observed departures in the following year. It does not establish that employees are happier, that they will never leave, or that their outside opportunities have become less valuable. A higher promotion probability means more measured upward occupational movement among continuing employees, not necessarily higher lifetime earnings or broader professional development.
The paper's reduced-form checks provide another consistency test. In the reported accounting, the observed extension effects on exit and promotion are closely matched by the combined first-stage changes in shares and wages multiplied by their second-stage coefficients. The implied residual direct effects are described as negligible. This supports the view that the extension's effect on the outcomes is largely transmitted through the measured compensation changes. It remains a test within the study's specification, not a proof that every non-wage consequence of collective bargaining is irrelevant.
The correct conclusion is therefore more precise than “equity makes people stay.” The Finnish design supports the claim that, for a local group of workers exposed to binding wage constraints, an exogenous reduction in employee equity is associated with a rise in one-year exit and a fall in internal advancement, after accounting for the instrumented wage component. That is meaningful causal evidence. It is also bounded evidence: it concerns a particular response margin, a particular institutional shock, and outcomes observed over one year.
This distinction prepares the harder judgment. A one-year effect may reflect a real incentive that changes behavior during a critical period, but it may also coexist with a later departure once the claim vests or its value is realized. The force of the claim may differ in a high-technology labor market where outside options are stronger. A firm-level ownership structure may correlate with stability or growth for reasons that are not identified by the employee-level IV design. The causal chain is credible enough to study these questions, but not broad enough to answer them automatically. Any serious evaluation of employee equity must carry forward both parts of the result: ownership can matter, and the circumstances that generate that effect matter just as much.