What the evidence can and cannot tell us

This is the evidence article in the family leave cluster. It asks what can be said, with named research and stated methods, about what the Family and Medical Leave Act of 1993 and the state paid programs that followed actually did: to time away from work, to whether new parents kept their jobs, to what employers experienced, and to earnings years later. The answer is less tidy than either side of the public argument would prefer. The strongest evidence concerns the immediate term, and it is mostly favorable. The strongest challenge concerns a decade later, and it is unfavorable. Any honest account holds both, and this one is built to do exactly that.

A reader who finishes this article should be able to do three things. First, state what the evidence shows about leave-taking, employment continuity, and employer costs, with the study and the period attached to each claim. Second, explain why the federal statute’s own effects resist clean measurement while the state paid programs, adopted on staggered dates, supply the natural experiments that researchers need. Third, describe without flinching the most uncomfortable finding in this literature: that a long-run study of the earliest state paid program found negative effects on mothers’ subsequent employment and earnings. The credibility of this article depends entirely on giving that finding the same prominence and the same length as the favorable ones, and the structure below is arranged so that no reader can miss it.

The method here is the one this series applies throughout: judge a statute against its own aims, and keep separate what the federal law did from what the state successors did. The 1993 law promised eligible workers up to twelve workweeks of unpaid, job-protected time away. The state programs that began in the early 2000s promised something the federal law never did, which is partial wage replacement during that time away. Those are different interventions, and the evidence answers questions about them with very different degrees of confidence. Much of the public confusion on this subject comes from treating them as one thing, citing the short-run results of the state programs as though they were evidence about the federal statute, or citing the federal statute’s modest measured effects as though they said something about paid programs. This article keeps the two apart at every step.

Five findings organize the record. The first is the identification problem. The federal statute applied nationally at a single moment, to a defined subset of employers, and many large employers already offered comparable time off before the law arrived. Isolating its effect is therefore genuinely difficult, and the best federal-level studies find modest changes in leave-taking concentrated among covered workers at firms that had not previously offered it. The second is the binding constraint. Department surveys, fielded a dozen years apart, keep returning the same answer about why workers who needed time away did not take it: they could not afford unpaid time away. That is the empirical foundation for the claim that the statute’s design, rather than its coverage, limits its reach.

The third finding comes from the states. The paid programs adopted by several states from the early 2000s onward created staggered natural experiments, and the early evaluations of the first program found increased leave-taking and longer leave duration, particularly for mothers, along with increases in the share of mothers returning to the same employer. The fourth finding is the long-run complication, and it cuts the other way. Later research following that same first-in-the-nation program over roughly a decade found negative effects on mothers’ employment and earnings in the years after leave. Serious researchers on both sides treat that result as unresolved rather than dispositive, but it cannot be set aside, and it is reported here at full length. The fifth finding concerns employers: survey evidence collected for the department has repeatedly found that most covered employers report minimal or no difficulty complying, which is a genuine finding and is reported alongside the observation that survey evidence of this kind has known limitations.

One note on dates governs the whole article. The reference date is April 1, 2015, and the record described here is the record available through that date. Research completed after that date is identified with its dates and kept outside the at-reference record. The important case is the long-run study of California’s program: it appeared as a working paper in October 2019 and in journal form in February 2025. It is discussed at length because the subject demands it, and it is dated every time it appears so that no reader mistakes it for evidence available when this article’s reference date fell.

Reading the ratings in this article

The artifact table near the end of this article assigns each of the five findings a rating: replicates, contested, or unresolved. Those three words carry the article’s entire epistemic stance, so they deserve a full explanation before the findings begin. A replicates rating means that more than one research team, working with different data and different methods, arrived at the same directional result. It does not mean the result is proven in any absolute sense. It means the finding survived the most basic test of empirical credibility, which is that it showed up more than once, in more than one place, when different people went looking. The federal leave-taking result earns this rating because Waldfogel’s firm-size analysis and the later multi-study pattern point the same way. The affordability result earns it because two department surveys, fielded twelve years apart by different contractors, returned the same dominant reason for unmet need. The short-run state results earn it because survey data, longitudinal cohort data, and employer surveys all describe gains running in the same direction.

A contested rating means the evidence pulls in more than one direction, or the same evidence supports different readings depending on defensible analytical choices. The employer-compliance finding earns this rating. The department’s own analysis of its 2012 survey supports the minimal-difficulty reading, while the Criterion Economics re-weighting of similar data supports a more negative reading, and the choice between worksite weighting and employee weighting moves the headline figures by meaningful amounts. Contested does not mean worthless. It means the reader should hold the finding with the appropriate looseness, understanding exactly which choices produce which version of the result. This article reports both weightings and both analyses for that reason.

An unresolved rating means something narrower and more specific: a single strong study, with a credible design and unusual data, produced a result that no other study has yet confirmed or refuted. The long-run earnings finding earns this rating. The Bailey team’s regression discontinuity on the universe of tax records is, by the standards of the field, an unusually powerful design. But it is one study, of one program, in one state, following one cohort, and the history of empirical social science is full of striking single-study results that faded on replication and full of others that hardened into consensus. Until more studies look at longer horizons with comparable data, the finding sits in the space the brief for this article names explicitly: treated as unresolved rather than dispositive by serious researchers on both sides. The rating is not a dismissal. It is the most respectful thing one study can be granted, which is to be taken seriously without being treated as the last word.

The table’s other columns deserve the same plain-language treatment. The direction column states what happened, in the units the research used, without translating the result into a policy slogan. The period column states when the data were collected or which years the records cover, because a result about 1992 to 1995 is a result about a different economy than a result about 2004 to 2014, and the article never asks a finding to travel outside its period. The principal research column names the study, because this article’s rule is that no empirical claim appears without its source attached. The identification strategy column states, in a few words, how the researchers tried to separate the law’s effect from everything else happening at the same time. That column is the most important one for non-specialist readers, because the credibility of every finding in this literature rests on the credibility of the comparison the researchers constructed, and naming the strategy lets the reader judge it.

A word on the date wall, since it shapes what counts as evidence here. The reference date for this article is April 1, 2015. Findings from research available through that date form the at-reference record. Research completed afterward is part of the later-research record and is identified with its dates every time it appears. The wall is not a judgment about quality. The long-run tax study is, by most methodological standards, the strongest single piece of research in the entire literature, and it sits on the later side of the wall. The wall exists because an evidence article must be honest about what was known when, and because readers deserve to know which findings could have informed decisions made at the reference date and which could not. The article discusses the later research at full length, as the brief requires, and dates it every time, so no reader can mistake its position in time.

Finding one: the federal statute is hard to evaluate

Why is the federal law so hard to evaluate?

Because the statute took effect nationally on a single date, covered only employers with fifty or more workers, and arrived in workplaces where many large firms already offered similar time off, researchers lack a clean comparison group. The best studies therefore measure effects where the law actually bound: mid-sized firms without prior policies.

The Family and Medical Leave Act arrived as Public Law 103-3, signed by President Bill Clinton on February 5, 1993. It entitled eligible employees of covered employers to up to twelve workweeks of unpaid, job-protected leave in a twelve-month period. Coverage turned on employer size: the law applied to employers with fifty or more employees. Eligibility turned on the worker’s history with that employer: twelve months of employment, at least 1,250 hours worked in the preceding twelve months, and a worksite with fifty or more employees within seventy-five miles. The coverage architecture is summarized in the guide to the Family and Medical Leave Act of 1993, and the details matter here because every one of those thresholds shapes what researchers can and cannot measure.

Consider what an evaluator needs. To say what a law did, you need to know what would have happened without it, which means you need some group that looks like the treated group but was not treated. The federal statute makes that comparison awkward in three ways, and each one deserves to be stated plainly because the awkwardness is the finding. First, the law took effect nationally at a single moment. There is no untreated state to serve as a comparison, no phased rollout to exploit, no early-adopter region whose experience can be set against a late adopter’s. The entire country moved at once. Second, the law applied to a defined subset of employers, which at first looks like it supplies a comparison group: workers at firms below the fifty-employee threshold were not covered. But firms with forty-nine employees differ systematically from firms with five hundred, in wages, in benefits, in turnover, in the kinds of workers they hire, so the contrast is informative only with heavy adjustment, and the adjustment is never complete.

Third, and most damaging to simple measurement, many large employers already offered comparable time off before 1993. For workers at those firms, the statute changed the legal character of the benefit, giving a right where there had been a policy, but it did not change the practical availability of time away. A researcher comparing leave-taking before and after the law at such firms will find little change and might conclude the law did nothing, when the accurate statement is that the law did nothing new for those particular workers because they already had the thing the law provided. The bite of the law was concentrated where no prior policy existed: mid-sized firms, roughly one hundred to five hundred employees, that had not previously offered leave. That is where the careful studies look, and that is where they find movement.

The coverage numbers sharpen the point. By 2012, according to the department’s survey research by Klerman, Daley, and Pozniak, about 59 percent of American workers were both covered by the statute and eligible for its protections. That figure surprises people in both directions. It surprises supporters of the law, who sometimes speak as though its protections were universal, and it surprises critics, who sometimes speak as though hardly anyone qualified. Both impressions are wrong. A majority of workers stood inside the law’s boundaries by 2012, and a large minority stood outside them, excluded by employer size, by short tenure, by part-time hours, or by the seventy-five-mile rule. But the deeper point for evaluation is that being inside the boundaries did not always mean gaining something new. A covered and eligible worker at a firm that already granted twelve weeks of unpaid time off experienced the law as a legal backstop, valuable in a dispute, invisible in daily life. The measurable action, the change a survey could detect, happened at the margin where the law supplied what the employer had not.

This is why the federal literature reads the way it does: modest effects, carefully qualified, concentrated in specific slices of the workforce, with authors spending as much space on what their methods cannot show as on what they can. That caution is not a defect of the research. It is the honest response to a genuine identification problem, and any summary that smooths it away is misrepresenting the state of knowledge. The uncomfortable corollary is that the most-quoted national statistics about the law’s effects are often the least informative, because national averages blend together the workers for whom the law changed everything and the workers for whom it changed nothing, and the blend tells you less than either group would tell you alone.

The 59 percent figure and what it conceals

By 2012, about 59 percent of American workers were both covered by the statute and eligible for its protections, according to the survey research by Klerman, Daley, and Pozniak conducted for the department. The figure is worth unpacking slowly, because it is one of the most cited and most misunderstood numbers in the literature. It is a joint condition: covered and eligible. A worker at a firm with five hundred employees who has worked there for three months is covered but not eligible. A worker with five years of tenure at a thirty-employee firm is eligible in every respect except the one that matters, the employer’s size. The 59 percent counts only those who satisfy every condition at once: the fifty-employee threshold, the twelve months of tenure, the 1,250 hours in the preceding year, and the fifty-within-seventy-five-miles worksite test. Each condition excludes a different population, and the excluded populations overlap, which is why the joint figure cannot be derived from any single threshold.

The composition of the excluded 41 percent matters for evaluation. Part-time workers are disproportionately excluded by the 1,250-hour rule, which demands an average of roughly twenty-four hours per week over the year. Short-tenure workers are excluded by the twelve-month rule, which means the workers with the least job security, those most in need of protection against dismissal, are the least likely to hold it. Workers at small firms are excluded by the size threshold, and workers at satellite worksites are excluded by the seventy-five-mile rule even when their employer is large. These exclusions are not random. They fall most heavily on low-wage, high-turnover, and part-time segments of the workforce, which are the same segments the affordability constraint hits hardest among covered workers. The statute’s boundaries thus compound its design: the workers least able to afford unpaid time away are also the workers least likely to be covered by the right to take it.

But the 59 percent figure conceals something in the other direction as well, and intellectual honesty requires stating it. Among the covered and eligible, a substantial share already had equivalent time off through employer policy before 1993, particularly at large firms. For those workers, the statute supplied a legal right without a new practical option, which means the effective treatment, the share of the workforce for whom the law changed what was actually available, was smaller than 59 percent. How much smaller cannot be read directly from the coverage figure, because the surveys that measured prior policy coverage used different samples and different questions. Waldfogel’s firm-size analysis is the closest the literature comes to quantifying the effective treatment: the measurable change in leave-taking appeared at medium-sized firms without prior policies and not at large firms with them. The coverage figure describes the law’s legal footprint. The firm-size result describes its practical footprint. The distance between the two is the reason national averages mislead and the reason this article keeps returning to the question of where the law actually bound.

What a clean test would look like, and why the statute denies it

It helps to describe the experiment researchers wish they could run, because the distance between that ideal and what the statute permits is the exact measure of the identification problem. The ideal experiment would assign the law’s protections by lottery. Half the country’s workers, chosen at random, would receive twelve weeks of unpaid, job-protected time away; the other half would not. Researchers would then compare leave-taking, employment, wages, and employer outcomes between the two groups. Because the lottery was random, the groups would be identical on average in every respect except the treatment, and any difference in outcomes could be attributed to the law with confidence. No legislature will ever run that experiment, for obvious ethical and practical reasons, so researchers settle for approximations, and the quality of the approximation determines the quality of the evidence.

The statute’s fifty-employee threshold looks, at first glance, like a serviceable approximation. Firms with forty-nine employees are exempt; firms with fifty are covered. A researcher could compare outcomes just below and just above the line, on the theory that a forty-nine-employee firm and a fifty-one-employee firm are nearly identical in every respect except the law’s application. That design has a formal name, regression discontinuity, and it is the same logic the long-run California study would later use for birth timing around the program’s start date. But the firm-size version of the design has a weakness the birth-timing version does not. Firms choose their size, or at least influence it, and they differ systematically across the threshold in ways that matter for the outcomes being measured. Larger firms pay higher wages on average, offer richer benefits, employ different mixes of occupations, and experience different turnover patterns. Some of those differences are smooth and gradual, which the design can handle, but the threshold itself can induce sorting: a firm hovering near fifty employees might manage its headcount to stay below the line, which means the firms just below the threshold are selected for a particular attitude toward regulation. The comparison is informative, but it is never as clean as the lottery, and every published result built on it carries that qualification.

The pre-existing-policy problem is deeper still, because it affects not just the comparison group but the meaning of the treatment itself. When researchers speak of the law’s effect, they mean the difference the law made relative to what would have happened without it. For a worker whose employer already granted twelve weeks of unpaid time off in 1992, the law’s arrival in 1993 changed the legal status of the benefit without changing its practical availability. The worker could already take the time; after the law, the worker could take the time as a matter of right. That legal change has real value, particularly in a dispute, but it does not show up in surveys of leave-taking, because the behavior was already happening. A before-and-after comparison at such firms will register zero effect, and a careless reader will conclude the law did nothing, when the precise statement is that the law added nothing measurable to what those workers already had. The treatment was not the same across firms. It was strong where no policy existed and weak where a policy already did, and any national average blends those two very different treatments into a single number that describes neither.

This is why Waldfogel’s firm-size result is the load-bearing finding of the federal literature. By showing that the increase in leave-taking was concentrated at medium-sized firms without prior policies and absent at large firms with established policies, she did more than measure an effect. She validated the measurement strategy itself. If the post-1993 increase had been caused by some cultural shift toward involved parenthood, or by a business-cycle effect, or by any other background force, it would have appeared across firm sizes. The fact that it respected the boundary where the law’s practical bite began and ended is what lets researchers attribute the change to the statute rather than to the era. The identification problem does not make measurement impossible. It makes naive measurement misleading and careful measurement possible, and the difference between the two is the entire craft of this literature.

There is a related subtlety in how the federal studies handle state laws that predated the federal statute. Charles Baum’s 2003 analysis, whose full title names both state maternity leave legislation and the 1993 federal act, exploited the fact that some states had their own leave laws before the federal law arrived. That variation supplies another approximation of the ideal experiment: workers in states with pre-existing protections serve as a partial comparison for workers in states where the federal law was the first protection to arrive. The design is clever, and it is worth understanding because it illustrates the general principle that researchers in this literature are always hunting for some group that got the treatment later, or less, or not at least. But state pre-existing laws also complicate the federal estimate, because in states that already had protections, the federal law’s marginal contribution was smaller, just as it was smaller at firms that already had policies. Every layer of prior protection shrinks the measurable effect of the new law without shrinking its legal significance, and the literature’s modest federal estimates must be read with that shrinkage in mind.

A final point about null results, since this literature contains several and they are easy to misread. When Baum, or Han, Ruhm, and Waldfogel, report no statistically significant effects of the statute on women’s employment or wages, they are reporting that their data could not distinguish the law’s effect from zero with the confidence the field requires. That is not the same as proving the effect was exactly zero. A small effect, positive or negative, could exist below the detection threshold of the available data, particularly given the identification problems described above, which dilute the measurable treatment. The responsible reading of a null result is that the data provide no evidence of an effect large enough to detect, not that they prove no effect existed. The federal literature’s nulls are therefore consistent with Ruhm’s 1997 characterization: the law’s provisions were modest, so its effects in either direction were modest, and modest effects are hard to separate from statistical noise. That reading treats the nulls as informative rather than empty, which is what they are.

What the federal studies found

The first careful look came from economist Jane Waldfogel, writing in the Journal of Policy Analysis and Management in 1999. Using Current Population Survey data from March 1992 through March 1995, she compared leave-taking and leave coverage before and after the statute took effect. Her headline result was that leave-taking by women with infants rose by roughly 23 percent after the law, a substantial change. But the distribution of that change is the part that matters. The increase was concentrated exactly where the identification logic says it should be: among workers at medium-sized firms, roughly one hundred to five hundred employees, that had not offered leave before the law required it. At large firms, those with five hundred or more employees, where formal leave policies were already common, she found no detectable effect. The law moved behavior where it supplied something new and did not move it where it supplied something workers already had. That pattern is itself evidence that the measured change was caused by the statute rather than by some background trend affecting all new mothers equally, because a background trend would not have respected firm-size boundaries so neatly.

Waldfogel also examined the fear that motivated much of the opposition to the statute: that mandating time away would damage women’s employment or wages, as employers shifted the cost onto female workers through lower pay or reduced hiring. She found no significant negative effects on women’s employment or wages in the post-law period. That non-finding has been cited ever since, and it deserves both its prominence and its qualification. It is prominent because the predicted harm did not appear in the data available then. It is qualified because the law’s modest scope, the same modesty that made its benefits modest, also limited the cost employers had to absorb, and a small cost is hard to detect in national employment statistics even if it exists.

That modesty was the central point of the second major assessment, Christopher Ruhm’s 1997 article in the Journal of Economic Perspectives. Ruhm argued that the statute’s provisions were modest by design and that its effects would therefore be modest in both directions: neither large benefits to workers nor significant costs imposed on employers. His reasoning was arithmetic rather than ideological. Many workers were exempted by the employer-size threshold and the eligibility rules. Many of the workers who were covered already had access to time off through employer policies or through state laws, so the federal statute gave them a right without giving them a new practical option. With few workers gaining significant new rights, neither the gains nor the burdens could be large in the aggregate. Readers encountering Ruhm’s work should note one bibliographic caution that this article observes throughout: a later Ruhm paper, published in 1998, analyzes parental leave across European countries and is sometimes cited in American discussions by mistake. It is not a study of the 1993 American statute and is not used as one here.

Charles L. Baum’s 2003 study in Labour Economics took a different route to the same question, exploiting variation in state maternity leave laws alongside the federal statute to estimate effects on employment and wages. His results were consistent with the pattern: no statistically significant effects on employment or wages. He did find one behavioral response worth reporting precisely because it is small. Mothers covered by the laws delayed their return to pre-childbirth jobs by only a couple of weeks. That is a real effect, it has the sign one would expect from job-protected time away, and its size tells the same story of modesty that runs through the federal literature. The law gave new mothers a little more time before the return, and the labor market registered the change faintly.

The most comprehensive federal assessment came in 2009, when Wen-Jui Han, Christopher Ruhm, and Jane Waldfogel published a joint analysis in the Journal of Policy Analysis and Management covering parental leave policies and parents’ employment and leave-taking. Their results again found no significant effects of the 1993 statute on women’s employment or wages. But they added a distributional finding that reshaped how researchers thought about the law’s limits: leave laws had larger effects on leave-taking among high-income families than among low-income families. In other words, the benefit flowed disproportionately to the workers who needed the income protection least, because taking unpaid time away requires a household that can absorb the lost wages. That finding is the bridge to the second of the five findings, and it is worth pausing on, because it reframes the statute’s central weakness. The law’s defenders sometimes describe its coverage thresholds as the problem, and its critics sometimes describe its mandates as the problem, but the research points at a third problem: the benefit was unpaid, and unpaid benefits are used most by those who can afford to use them.

Taken together, the federal studies tell a coherent story, and coherence across independent research teams using different data and different methods is itself a form of evidence. The statute increased leave-taking modestly, concentrated where it actually changed what was available. It did not produce detectable harm to women’s employment or wages in the periods studied. Its unpaid design tilted usage toward higher-income households. None of these results is dramatic, and that is the point that Ruhm made in 1997 and that the subsequent literature confirmed. A modest law produced modest, measurable, mostly benign effects, and the modesty of the design is the reason both the benefits and the costs came out small. The honest summary of the federal record is not that the law failed or that it triumphed. It is that the law did roughly what a careful reader of its text would have predicted: it guaranteed time away for a defined group of workers, many of whom used it, none of whom appear to have paid for it in wages or employment, with the gains flowing most readily to those who could afford the unpaid weeks.

Why four studies with four methods matter more than one

The federal literature’s credibility does not rest on any single paper. It rests on the convergence of four independent analyses, published across a decade, using different data sources and different analytical strategies, that arrive at the same shaped result: modest effects, concentrated where the law bound, with no detectable damage to women’s employment or wages. Convergence of this kind is worth explaining in detail, because it is the mechanism by which a literature with a genuine identification problem can still produce knowledge worth acting on. Each study’s weakness is different, so the weaknesses do not compound. What survives across all four is unlikely to be an artifact of any one method.

Waldfogel’s 1999 study worked with the March supplements of the Current Population Survey from 1992 through 1995, the large monthly household survey the Census Bureau conducts. The March supplement is the one that asks detailed questions about work experience and benefits, which made it the natural instrument for measuring leave-taking around the law’s arrival. Her analytical move was the firm-size contrast described earlier: medium firms without prior policies as the treated group, large firms with established policies as the comparison. The roughly 23 percent rise in leave-taking among women with infants is the headline, but the structure of the result matters more than its size. The increase appeared where the law changed the practical options and did not appear where it changed only the legal framing. That structure is what separates a causal reading from a coincidental one. A critic who wanted to dismiss the result would need to propose some other force, operating between 1992 and 1995, that increased leave-taking specifically at medium-sized firms without prior policies while leaving large firms untouched. No such force has been proposed, which is why the finding has stood.

Ruhm’s 1997 article in the Journal of Economic Perspectives took an entirely different approach. Rather than estimating effects from data, he reasoned from the law’s architecture about how large the effects could possibly be. The argument proceeds by subtraction. Start with the entire workforce. Subtract the workers at firms below the fifty-employee threshold. Subtract the workers who fail the twelve-month, 1,250-hour, or seventy-five-mile tests. Subtract the workers whose employers already provided equivalent time off. What remains, the population for whom the statute created a genuinely new practical option, is a modest fraction of the workforce. From that arithmetic, Ruhm drew the inference quoted earlier: the statute’s provisions were modest enough that they would produce neither large benefits to workers nor significant costs for employers. The value of this kind of analysis is that it does not depend on any particular dataset or statistical specification. It is an accounting identity dressed as an argument, and its conclusion constrains what any empirical estimate can plausibly claim. If a later study had reported enormous effects in either direction, Ruhm’s arithmetic would be the reason to doubt it.

Baum’s 2003 study in Labour Economics supplied the third angle, exploiting variation in state maternity leave legislation alongside the federal statute. Some states had enacted their own leave protections before 1993, which meant the federal law’s arrival changed less in those states than in states where it was the first protection workers had. By comparing the change in outcomes across states with different pre-existing regimes, Baum could isolate the federal contribution more credibly than a simple national before-and-after comparison allows. His finding of no statistically significant effects on employment or wages, combined with the small behavioral response of mothers delaying their return to pre-childbirth jobs by only a couple of weeks, fit the established pattern precisely. The delay finding deserves emphasis because it is the kind of small, signed, sensible effect that a real policy produces: the law gave new mothers job protection, and they used a little more time before returning. A couple of weeks is not a transformation of the labor market. It is a human-scale response to a human-scale protection, and its modesty is itself evidence that the measurement is picking up the law rather than noise.

The fourth study, by Han, Ruhm, and Waldfogel in 2009, brought the literature’s most consequential new idea: the distributional analysis. Earlier studies had asked whether the law moved averages. Han, Ruhm, and Waldfogel asked whom it moved. Their answer, that leave laws had larger effects on leave-taking among high-income families than among low-income families, reframed the statute’s limitation as a feature of its design rather than an accident of its implementation. An unpaid benefit is, by construction, easier to use for households with savings or second incomes, and the data confirmed the construction. The study also reaffirmed the null results on women’s employment and wages, extending the no-detectable-harm finding to a longer post-law window. Taken together, the four studies describe a law that did what its text promised, for the workers positioned to use it, without the side effects its opponents predicted and without transformative benefits beyond what the modest design could deliver.

One caution about the literature’s boundaries belongs here, because misattribution is a recurring error in public discussion. Christopher Ruhm published a well-known paper in 1998 analyzing parental leave policies across European countries. That paper is sometimes cited in American debates as though it evaluated the 1993 United States statute. It did not. It is a cross-country comparative study, and its findings about European leave regimes do not transfer to the American law, which was unpaid, shorter, and narrower in coverage than the European policies Ruhm analyzed. This article cites Ruhm’s 1997 Journal of Economic Perspectives article for the American statute and does not use the 1998 paper for that purpose. The distinction matters because the European literature, dealing with paid and often much longer leaves, generally finds larger effects in both directions, and importing those findings into the American discussion inflates expectations the domestic evidence does not support.

The European comparison and why this article barely uses it

This article cites almost no European research, and the omission is deliberate, for reasons that go beyond the citation caution in the preceding section. The reason the comparison fails is institutional, not statistical. European studies estimate the effects of generous, long-standing programs on populations where leave-taking is the norm. American studies estimate the effects of a modest program introduced in 2004 on a population where leave-taking was the exception. The baseline matters. When a European country extends paid leave from six months to nine, the researchers are measuring the marginal effect of an extension on workers who already take long leaves. When California introduced six weeks of partial pay, the researchers were measuring the effect of introducing paid leave where none had existed. The two margins answer different questions, and neither answers the other’s. This article’s verdicts rest on American studies of American programs, because those are the studies that describe the policies this series covers.

There is one legitimate use of the European literature, and it is as a source of hypotheses rather than of evidence. European studies have documented that very long leaves can weaken women’s labor-market attachment, a finding that rhymes with the Bailey long-run result from California (NBER working paper, October 2019; journal publication, February 2025). The rhyme is suggestive, not probative. It suggests a mechanism worth investigating: that separations beyond a certain length change either employer behavior or worker preferences in ways that short separations do not. But the suggestion is not evidence about California, and this article does not treat it as such. The long-run California finding stands or falls on its own design, not on its resemblance to European patterns.

Finding two: the binding constraint is money, not coverage

Why did affordability become the central story?

Two surveys, one fielded in 2000 and one in 2012, asked workers who needed time away but did not take it why. In both, the leading answer was money: 77.6 percent in the first survey and 46 percent in the second said they could not afford unpaid time off. That points at design, not coverage, as the binding limit.

The department has twice commissioned large national surveys of how the statute works in practice, and the two surveys agree on the point that matters most. The first, conducted by Westat and fielded in 2000, found that 2.4 percent of employees needed leave but could not take it. Among those workers, the most common reason given was inability to afford the time away, cited by 77.6 percent. The second, conducted by Abt Associates, fielded in 2012 and released in February 2013, found that 5 percent of workers reported needing leave but being unable to take it. Again the leading reason was money: the technical report states that inability to afford leave was the reason given by nearly half of those with unmet need, 46 percent, a figure reported on page 161 of the technical volume. The same survey found that 31 percent of workers who did take leave cut their time away short because of financial strain, which means the affordability constraint operated not only on the decision to take leave at all but on how much of the protected period workers actually used.

These numbers need to be read with the care they deserve. The share of workers reporting unmet need rose from 2.4 percent to 5 percent between the two surveys, but the surveys were fielded twelve years apart, by different contractors, in different economic conditions, and the questionnaires were not identical instruments. The responsible reading is not that unmet need precisely doubled but that in both surveys, across a dozen years, the dominant stated reason for forgoing protected time away was the same: workers could not afford to go without pay. When the same answer comes back from two independent fieldings, it stops being a quirk of one questionnaire and starts being a fact about the policy.

The implication is the one stated in the brief for this article, and it is worth stating in full because it reframes the entire public debate about the statute. The empirical foundation for the claim that the statute’s design rather than its coverage limits its reach is this repeated survey result. Expanding the law’s coverage, lowering the employer-size threshold, loosening the hours requirement, would extend the right to more workers. But the right being extended is the right to unpaid time away, and the workers newly brought inside the law’s boundaries would face the same arithmetic that keeps current workers from using it: twelve weeks without wages is a benefit that costs the worker her income. The constraint that binds is not who is allowed to take leave. It is who can afford to.

That reading is reinforced from an entirely different direction by the distributional finding in Han, Ruhm, and Waldfogel’s 2009 analysis, discussed above: leave laws moved leave-taking more among high-income families than among low-income families. Two different methods, a national survey asking workers why they stayed on the job and an econometric analysis of who actually took time away, converge on the same conclusion. The unpaid design rations the benefit by income. Households with savings, with a second earner, with salaried positions that tolerate absence, can use the protection. Households living paycheck to paycheck, which are disproportionately the households facing the medical and caregiving crises the law was written for, often cannot.

There is a further subtlety in the survey results that deserves attention because it is frequently missed in public discussion. The 31 percent of leave-takers who cut their time short for financial reasons represent a different margin of the same constraint. The public argument tends to treat leave-taking as binary, taken or not taken, but the survey shows a continuous margin: workers take some of the protected period, then return early because the lost wages accumulate. A worker who takes four weeks of a twelve-week entitlement and returns for money reasons has used the law and been constrained by its design at the same time. Evaluations that count only whether any leave was taken miss this intensive margin entirely, and the intensive margin is where the affordability constraint does much of its work.

None of this is an argument that the statute’s coverage rules are irrelevant. The 59 percent coverage-and-eligibility figure from 2012 means two in five workers stood entirely outside the law, and for them the question of affordability never arose because the right did not exist. But the survey evidence says that among workers who did hold the right, the reason most often given for not using it was not confusion about eligibility, not fear of employer retaliation, not the paperwork, but money. That ordering matters for anyone assessing the statute against its aims. A law whose purpose is to let workers meet family and medical needs without losing their jobs achieves its purpose only to the extent that workers can afford to invoke it, and the repeated finding is that a large share cannot.

The intensive margin: leave cut short

Public discussion of the affordability constraint usually treats leave-taking as a binary choice, taken or not taken, and the survey questions invite that framing by asking workers whether they needed time away and did not take it. But the 2012 survey’s finding that 31 percent of leave-takers cut their time away short because of financial strain reveals a second margin where the constraint operates, and it is arguably the more important one. Workers do not only decide whether to invoke the protection. They decide, week by week, how much of the protected period they can afford to use. A worker who takes four weeks of a twelve-week entitlement and returns early for money reasons has used the law and been limited by its design simultaneously. Evaluations that count only the binary decision miss this intensive margin entirely, and the intensive margin is where unpaid design does much of its quiet work.

The distinction matters for how one reads the federal studies’ leave-taking results. Waldfogel’s roughly 23 percent increase measured whether leave was taken, not how much was taken. If a substantial share of the workers counted as leave-takers were using only a fraction of the protected period, then the effective dose of the policy, the actual weeks of job-protected time away delivered to workers, was smaller than the take-up figures suggest. The 31 percent figure cannot be converted into an exact weeks-lost estimate from the published survey summaries, and this article does not attempt the conversion. But the direction of the bias is clear: binary take-up overstates the policy’s practical reach whenever the constraint binds on duration as well as on initiation, and the survey says it binds on both.

The two surveys’ unmet-need figures, 2.4 percent in 2000 and 5 percent in 2012, invite a comparison that must be handled with care. The numbers come from different contractors, different questionnaires, and different economic moments, so the responsible reading is not that unmet need precisely doubled but that it was material in both years and that affordability dominated the stated reasons in both. What makes the comparison credible despite the methodological differences is the stability of the reason structure. In 2000, more than three-quarters of workers with unmet need named money. In 2012, nearly half did. The share naming affordability fell, but it remained the leading reason by a clear margin, and the 31 percent who truncated their leaves for financial reasons in 2012 describe the same constraint operating on a different margin. When the same answer leads in two independent fieldings a dozen years apart, it has earned the status of a finding rather than a fluke.

There is a deeper analytical point beneath the survey results, about what it means to call a constraint binding. In policy analysis, the binding constraint is the one that actually limits outcomes, as opposed to limits that exist on paper without changing behavior. Coverage thresholds are constraints: they exclude roughly two in five workers. But for the workers inside the law’s boundaries, the coverage constraint is not binding, because they hold the right and still do not use it, or do not use all of it. The affordability constraint is binding for those workers, because removing it, by attaching wage replacement to the protected time, would change their behavior, as the state experiments later demonstrated. This is why the brief for this article describes the survey result as the empirical foundation for the claim that design rather than coverage limits the statute’s reach. The claim is not that coverage is irrelevant. It is that among the constraints the statute creates, the unpaid design is the one doing the most work in limiting its own effectiveness.

The income gradient found by Han, Ruhm, and Waldfogel is the same constraint viewed from the other side of the data. The surveys ask workers why they stayed on the job; the econometric analysis observes who actually took time away. Both point at household resources as the variable that sorts users from non-users. A salaried professional with a working spouse and savings can treat twelve unpaid weeks as a manageable draw on reserves. An hourly worker who is the sole earner cannot, and the law’s protection, though legally identical for both, is practically available to only one of them. The state paid programs would later test this analysis directly, by attaching partial wage replacement to the protected time and observing whether the gradient reversed. It did, with the largest gains flowing to less-advantaged and lowest-paid workers. That reversal is the strongest available confirmation that the analysts who named affordability as the binding constraint had named the right one.

What the surveys cannot show

The affordability finding rests on descriptive surveys, and descriptive surveys cannot do what the econometric studies do. A survey that asks workers why they did not take leave records stated reasons, not revealed behavior. A worker who says she could not afford the time away might, under a different design, have taken it anyway, or might be rationalizing a decision made for other reasons, or might be reporting the most salient of several overlapping constraints. The 77.6 percent and 46 percent figures are not causal estimates. They are self-reports, and self-reports about hypothetical behavior deserve the same skepticism this article applies to employer self-reports about compliance burden. The article’s rating for this finding is replicates, not causal, and the table’s identification-strategy column says so explicitly: descriptive national surveys, no causal design.

What rescues the finding from that limitation is convergence with evidence of a different kind. The income gradient in Han, Ruhm, and Waldfogel’s analysis is revealed behavior, not stated reasons: it shows who actually took time away under the unpaid design, and the answer is disproportionately higher-income households. The distributional reversal under California’s paid program is also revealed behavior: attach wage replacement, and the gradient flips toward less-advantaged workers. When stated reasons and revealed behavior point at the same variable, money, the finding earns more confidence than either line of evidence could supply alone. The surveys say workers stayed on the job because they could not afford to leave. The take-up data say the workers who did take time away were the ones who could afford it. The state experiments say that paying workers changed who used the benefit. Three methods, one variable.

There is one more limitation worth stating, because it is the kind that readers rarely consider. The surveys measure unmet need among workers who recognize their situation as needing leave. A worker who never considered taking time away, because the household’s finances made the option unthinkable from the start, may not report unmet need at all. The 2.4 percent and 5 percent figures therefore likely understate the constraint’s true reach, capturing the workers close enough to the margin to feel the gap while missing those for whom the gap was never a live question. That understatement runs in the same direction as the awareness gap in California, where half the eligible workers had never heard of the program: in both cases, the measured figures describe the policy as experienced, not the policy as written, and the true constraint is larger than the numbers show.

Finding three: the states ran the experiments

What made the state programs useful to researchers?

California began paying benefits in July 2004, New Jersey in July 2009, and Rhode Island in January 2014, so researchers could compare outcomes in adopting states against states that had not yet adopted, before and after each start date. That staggered timing supplies the treatment and comparison groups the federal rollout never offered.

California’s program was the first of its kind in the nation. Senate Bill 1661 was signed in September 2002, and benefit payments began on July 1, 2004. The program offered six weeks of partial wage replacement, about 55 percent of wages, for workers bonding with a new child or caring for a seriously ill family member. New Jersey followed, signing its program into law in May 2008 with benefits beginning in July 2009. Rhode Island signed its program in 2013, with benefits starting January 1, 2014. Each program layered paid benefits on top of the federal statute’s unpaid protections, and each began on a known date in a known set of states. For researchers, that is the experimental apparatus the federal law never provided: treated states and untreated states, before periods and after periods, with the treatment switching on at different times in different places.

The interplay of federal floors and state add-ons is treated at length in federal and state labor protections compared, and the family leave story is the clearest illustration of why the distinction matters. The federal statute set a national floor of unpaid, job-protected time away. The states did not merely extend that floor; they changed the nature of the benefit by attaching money to it. Evaluating the two together, as public discussion often does, confuses the question. The state results are evidence about what happens when time away is paid. They are not evidence about what the unpaid federal statute did, and citing them as though they were is one of the recurring errors this article is written to prevent.

The first rigorous evaluation of California’s program came from Maya Rossin-Slater, Christopher Ruhm, and Jane Waldfogel, circulated as a National Bureau of Economic Research working paper in December 2011 and published in the Journal of Policy Analysis and Management in the spring of 2013. Using a difference-in-differences design on March Current Population Survey data from 1999 through 2010, they compared California mothers before and after the program began against mothers in other states over the same period. The headline result was striking: the program more than doubled maternity-leave use, from about three weeks to six or seven weeks for the typical new mother. The growth was particularly large for less-advantaged groups, which is the mirror image of the federal statute’s income gradient. Where the unpaid federal benefit had been used most by higher-income households, the paid state benefit drew in the workers the federal design had left out. Money, it turned out, was the variable that mattered.

The same study offered suggestive evidence on what happened after the time away ended. The authors found that the program raised the usual weekly work hours of employed mothers of one-to-three-year-olds by six to nine percent, with similar gains in wage income, but found no evidence of effects on subsequent employment probabilities within the horizon they studied. Those two results together paint a specific picture: mothers who used the program worked more hours once they were back, but the program did not detectably change whether they were working at all. One bibliographic precision matters here and is observed throughout this article: the finding that the program increased the share of mothers returning to the same employer should not be attributed to this paper. It belongs to a different study, described next, and keeping the attribution straight is part of reporting the literature honestly.

That study was published by Charles L. Baum and Christopher Ruhm in the Journal of Policy Analysis and Management in April 2016, and readers should note the journal carefully, because the paper is sometimes misattributed to the Journal of Labor Economics. Using the National Longitudinal Survey of Youth 1997 cohort and a difference-in-differences design, Baum and Ruhm found that California’s program raised time away by almost five weeks for the average covered mother and by two to three days for the average father. The inclusion of fathers matters: the program was formally gender-neutral, and the small but measurable increase in fathers’ time away is evidence that the benefit reached beyond mothers, even if mothers were the primary users. The employment results were favorable in the medium term. Mothers showed higher work and employment probabilities nine to twelve months after birth, with the gains concentrated among mothers with weak labor-force attachment, the group least connected to steady work before childbirth. During the child’s second year, the program raised mothers’ hours by about 18 percent and weeks worked by about 11 percent, with possible positive effects on wages as well. And it is to this paper that the return finding belongs: the authors found an increased probability of eventually returning to pre-childbirth jobs, which is the job-continuity result the brief for this article describes.

A third early assessment took the form of a survey rather than an econometric study, and it added the worker’s-eye view that the statistical papers could not supply. Eileen Appelbaum and Ruth Milkman, writing for the Center for Economic and Policy Research in January 2011, surveyed workers and firms about their experiences with California’s program. On the worker side, their central finding was that the lowest-paid workers benefited most, which corroborates the Rossin-Slater, Ruhm, and Waldfogel result about less-advantaged groups from the other side of the evidence. The survey also exposed a striking information gap: only about 49 to 50 percent of eligible workers knew the program existed. A benefit that half its intended users have never heard of is a benefit whose measured effects understate its potential effects, and the awareness gap is a standing qualification on every evaluation of the early years.

Read together, the short-run state evaluations form the favorable half of the literature, and their favor runs in a consistent direction. Paid time away increased the amount of time new parents, especially new mothers, spent away from work. It drew in less-advantaged and lower-paid workers whom the unpaid federal benefit had largely missed. It was followed, in the months and the second year after birth, by more hours, more weeks, and steadier attachment to the pre-birth employer. Nothing in these studies suggested that the program damaged mothers’ labor market prospects within the horizons the studies could observe. The horizons are the qualification that the next section takes up, because the most serious challenge to this favorable picture came from a study that looked further out than any of these papers could.

Why staggered timing is the researcher’s best friend

The difference-in-differences method that powers the state evaluations deserves a plain-language explanation, because it is the reason the state evidence is stronger than the federal evidence and the reason the brief for this article calls the state programs clean natural experiments. The logic runs in two comparisons. First, compare California before and after July 2004, when benefit payments began. That before-and-after difference captures the program’s effect plus everything else that changed in California over the same period: the business cycle, demographic shifts, other policies. Second, compare other states over the same two periods. That difference captures everything else without the program. Subtract the second difference from the first, and what remains, under the method’s assumptions, is the program’s effect with the background forces differenced out. The untreated states serve as the control group the federal rollout never supplied.

The critical assumption has a technical name, parallel trends, and an intuitive meaning: in the absence of the program, California and the comparison states would have followed the same trajectory. Researchers test this by examining the pre-program years. If California and the comparison states moved together before 2004 and diverged after, the divergence is attributed to the program. If they were already diverging before 2004, the attribution fails. Rossin-Slater, Ruhm, and Waldfogel’s use of March Current Population Survey data from 1999 through 2010 gave them five pre-program years to establish the baseline trend and six post-program years to measure the departure from it. The more than doubling of maternity-leave use, from about three weeks to six or seven weeks, was not a wiggle around a trend. It was a break, timed to the program’s arrival, concentrated in the treated state. That is what a credible difference-in-differences result looks like.

The stagger across states strengthens the design further. New Jersey’s benefits began in July 2009, Rhode Island’s in January 2014. Each new adoption creates another before-and-after contrast against states that have not yet adopted, and the accumulation of contrasts makes it progressively harder to attribute the results to something peculiar about California. A skeptic of the California result must propose an alternative explanation timed to July 2004 in California specifically. A skeptic of the multi-state pattern must propose alternative explanations timed to each adoption date in each adopting state, which is a much harder story to tell. This is the sense in which staggered adoption supplies better evidence than a single rollout: it multiplies the natural experiments rather than relying on one.

Baum and Ruhm’s use of the National Longitudinal Survey of Youth 1997 cohort added a different kind of strength. The Current Population Survey is a repeated cross-section: it samples different households each month, so researchers compare California mothers in 2003 with different California mothers in 2005. The NLSY-97 follows the same individuals over time, which means Baum and Ruhm could observe the same women’s work histories before and after childbirth and before and after the program. Following the same people eliminates a class of confounding that cross-sectional comparisons cannot: the possibility that the composition of mothers changed, with different kinds of women giving birth after the program began. Their findings, almost five additional weeks of time away for the average covered mother, higher employment probabilities nine to twelve months after birth, and the 18 percent hours and 11 percent weeks gains in the child’s second year, describe what happened to actual women followed through time, not to successive snapshots of a changing population.

The fathers’ result in the same study, two to three additional days for the average father, is small enough to be easy to overlook and important enough to dwell on. The program’s bonding benefit was formally available to either parent, and the wage replacement rate was the same. Yet the behavioral response was overwhelmingly maternal. That asymmetry is a finding about take-up, not about eligibility, and it constrains how one interprets the program’s design. A gender-neutral benefit used almost entirely by mothers is, in practice, a maternal benefit with a paternal option, and any assessment of the program’s effects on household arrangements, on employer expectations, or on the division of caregiving must start from the observed take-up rather than the formal symmetry. The long-run tax study would later find no effects for men, which is consistent with a program whose male take-up was always modest.

The distributional reversal between the federal and state results is the finding that ties the third section of this article to the second. Under the unpaid federal statute, Han, Ruhm, and Waldfogel found the largest leave-taking effects among high-income families. Under California’s paid program, Rossin-Slater, Ruhm, and Waldfogel found particularly large growth among less-advantaged groups, and Appelbaum and Milkman’s survey found the lowest-paid workers benefited most. The same research team, Ruhm and Waldfogel appear on both papers, found opposite gradients under opposite designs. That within-team reversal is powerful evidence that the gradient is caused by the wage-replacement feature rather than by something about the researchers’ methods or the populations studied. Unpaid protection rations by income. Paid protection reaches down the income distribution. The policy variable that flips the gradient is money, which is the same variable the department’s surveys identified as the binding constraint. Three independent lines of evidence, surveys of workers, econometrics of the federal law, econometrics of the state program, converge on a single sentence: the reason the federal statute’s reach was limited is that it did not pay.

The awareness gap found by Appelbaum and Milkman, that only about 49 to 50 percent of eligible workers knew the program existed, qualifies the short-run results in a way that cuts in the program’s favor. Measured effects reflect the program as understood and used, not the program as written. If half the eligible population never heard of the benefit, then the observed doubling of maternity-leave use was produced by roughly half the eligible mothers, which implies the effect on those who knew about the program was larger than the published averages suggest. Evaluations measure intent-to-treat effects, the effect of the program’s existence on the whole eligible population, rather than effects on the treated alone. The distinction matters because it means the published short-run gains understate what full awareness could deliver, and it means the program’s measured success was achieved despite a massive information failure rather than because of smooth implementation.

The replication pipeline: New Jersey and Rhode Island

California’s program dominates the research literature for a straightforward reason: it was first, so it has the longest post-program data. But the staggered rollout did not stop with California, and the later adopters matter both as replication opportunities and as tests of whether the California results travel. New Jersey signed its paid family leave program into law in May 2008, with benefit payments beginning in July 2009. Rhode Island signed its program in 2013, with benefits starting January 1, 2014. Each program layered wage replacement onto the federal statute’s unpaid protections, and each began on a known date, which means each supplies another before-and-after contrast against states that had not yet adopted.

The value of these later programs for researchers is the value of repetition. A result observed once, in one state, in one period, always carries the suspicion that something peculiar to that state or that period produced it. A result observed in California starting in 2004, in New Jersey starting in 2009, and in Rhode Island starting in 2014 becomes progressively harder to attribute to local coincidence. The economic contexts differed: California’s program began in a mid-2000s expansion, New Jersey’s in the depths of the Great Recession, Rhode Island’s in the slow recovery that followed. If paid time away increases leave-taking across all three contexts, the finding is not hostage to the business cycle. If the distributional pattern, larger gains for less-advantaged workers, repeats in all three states, the reversal of the federal income gradient looks like a property of paid design rather than a California idiosyncrasy.

At this article’s reference date of April 1, 2015, the replication pipeline was still young. New Jersey’s program had been paying benefits for less than six years, and Rhode Island’s for barely fifteen months, which meant the long-horizon evaluations that California had received were not yet possible for the later adopters. The short-run California results therefore stood, at the reference date, as the primary evidence about paid programs, with the later states positioned as the natural next studies rather than as completed ones. That temporal structure is worth stating explicitly because it explains why the literature looks California-centric: the state was not chosen for its representativeness but for its chronological priority, and the priority was an accident of legislative timing, not a research design choice. Readers should treat the California results as the best available evidence about paid family leave in the United States through the reference date, while understanding that the strongest confirmation would come from the same patterns appearing in the later-adopting states as their data matured.

Reconciling the California studies: one program, several stories

The California literature looks contradictory only until the studies are lined up by horizon, and the lining-up is worth doing carefully because it is where the public discussion goes wrong. Rossin-Slater, Ruhm, and Waldfogel in 2013 studied the first years of the program using March CPS data from 1999 through 2010. Their headline was leave-taking: the typical new mother’s leave more than doubled, from about three weeks to six or seven, with the largest gains among less-advantaged mothers. Their employment findings were suggestive but bounded by the horizon: higher usual weekly hours for mothers of one-to-three-year-olds, similar wage-income gains, and no evidence of effects on subsequent employment probabilities within the years the data covered. The paper was careful about what it did not show. It did not show that mothers returned to the same employer at higher rates. It did not follow mothers for a decade. Its contribution was to establish that a paid program with partial wage replacement moved the behavior the federal statute had moved least: leave-taking among the mothers with the least financial cushion.

Baum and Ruhm in 2016 extended the horizon into the child’s second year and shifted the data source to the NLSY-97 cohort, which follows the same individuals over time. Their headline was job continuity: mothers became more likely to eventually return to their pre-childbirth jobs, with higher work and employment probabilities nine to twelve months after birth, especially among mothers with weak labor-force attachment. The hours and weeks effects, up 18 percent and 11 percent during the second year, were larger than the 2013 paper’s estimates, and the authors reported possibly positive wage effects. The two papers do not contradict each other. They describe successive windows of the same adjustment: first the leave lengthens, then the return to the pre-birth employer becomes more likely, then hours and weeks worked rise in the second year. The sequence is coherent. A mother who takes six paid weeks instead of three unpaid ones is more likely to keep her job, and a mother who keeps her job is more likely to be working more hours a year later.

The Appelbaum and Milkman 2011 report sits alongside these papers as a different kind of evidence. Its survey of roughly 250 California firms found that about 90 percent of employers reported a positive effect or no effect on productivity, profitability, morale, and costs, that nearly 90 percent reported no problems with misuse, and that small firms reported fewer problems than large firms. The report also found that the lowest-paid workers benefited most, which matches the Rossin-Slater finding that less-advantaged mothers responded most, and that only about half of eligible workers knew the program existed. The awareness finding is the hinge. A program that doubles leave-taking among those who know about it still leaves half the eligible population untouched, and the untouched half is unlikely to be a random draw. Workers who do not know about a state benefit are likely to be the least connected to formal institutions, which means the program’s realized gains concentrate among the already better-informed.

The Das and Polachek paper, circulating as an IZA discussion paper in March 2014 with journal publication in October 2015, complicates the labor-supply story in a way neither the 2013 nor the 2016 paper addressed. Finding that young women’s labor-force participation rose alongside their unemployment rate and duration, relative to men, older women, and other states, the authors documented a pattern that resists the simple story that paid leave unambiguously improves women’s labor-market position. More participation and more unemployment can coexist when a policy draws marginal workers into the labor force who then search longer, or when employers adjust hiring at the margin. The finding is mixed and ambiguous, as its title says, and it belongs in any honest account because it shows that even the near-term labor-market signals were not uniformly favorable before the long-run study arrived.

The Bailey long-run study (NBER working paper, October 2019; journal publication, February 2025) then extends the horizon past everything else. Its decade follow-up of first-time mothers, with employment down about 7 percent, earnings down about 8 percent, roughly $25,681 less in cumulative earnings by 2014, one in ten new mothers with one fewer child after ten years, no effect on remaining with the pre-birth employer, and no effect for men, cannot be reconciled with the short-run findings by any simple story. One possibility is that the short-run and long-run results describe different margins. The short-run studies measured whether mothers took leave and returned to their jobs. The long-run study measured whether they were employed and what they earned a decade later. A mother can return to her pre-birth job and still, years later, be on a lower earnings path: passed over for promotion, sorted into less demanding roles, or choosing fewer hours after the experience of a long separation. Another possibility is that the discontinuity at the 2004 rollout captured a program in its infancy, with low awareness and unsettled norms, and that a mature program would produce different long-run results. A third is that the tax-data design, for all its administrative completeness, misses informal work and non-wage compensation in ways that bias the earnings comparison. None of these possibilities has been tested. The mechanism question that Bailey posed, whether firms push women out or women opt out, remains the central unanswered question of the literature, and it will remain unanswered until another long-run study with a different design either replicates or overturns the result.

Finding four: the decade-later complication

What did the decade-long tax study find?

Using Internal Revenue Service records for California women who gave birth around the 2004 rollout and following them about a decade, the authors found no employment or earnings gains and, for first-time mothers, declines: employment down 7 percent and annual wage earnings down 8 percent, or about $25,681 less in cumulative earnings by 2014.

The short-run results described above were the state of knowledge through this article’s reference date of April 1, 2015. What follows was not. In October 2019, Martha J. Bailey, Tanya Byker, Elena Patel, and Shanthi Ramnath circulated a National Bureau of Economic Research working paper, number 26416, that revisited California’s paid program with data and methods the earlier studies could not have used. The paper was published in journal form in the American Economic Journal: Economic Policy, volume 17, issue 1, pages 401 to 431, in February 2025. Every date in this paragraph is stated deliberately, because the study belongs to the later-research record, not to the evidence available when this article’s reference date fell, and it is presented here with that wall intact. The brief for this article requires the finding to be reported at full length and at the same prominence as the favorable short-run results, and this section is built to that requirement.

The study’s design is what makes it impossible to dismiss. Where the earlier evaluations relied on survey samples, Bailey and her coauthors used a regression discontinuity design on the universe of Internal Revenue Service tax records for California women who gave birth around the program’s 2004 rollout. The universe, not a sample: the tax data cover essentially every woman with reported earnings, which removes the sampling uncertainty that qualifies survey-based estimates. The regression discontinuity compares women who gave birth just before the program’s benefits became available with women who gave birth just after, two groups that should be identical in every respect except access to the paid benefit, because the exact timing of a birth around the cutoff is effectively arbitrary. The authors then followed both groups for roughly a decade through the tax records, observing employment and earnings year by year. No earlier study of the program had looked this far out with this kind of data.

The results cut against the short-run literature directly. The authors found no evidence that California’s paid program increased employment, boosted earnings, or encouraged childbearing over the decade they observed. For first-time mothers, the estimates went the other way: employment roughly a decade after birth was about 7 percent lower, and annual wage earnings were about 8 percent lower, relative to the comparison group. Cumulated over the decade, the earnings gap amounted to roughly $25,681 less by 2014 for the affected first-time mothers. The study also found that about one in ten new mothers had one fewer child after ten years than they otherwise would have, a fertility result that runs counter to the hope that paid time away would make childbearing easier to combine with work. Two non-findings are as important as the findings: the program showed no effect on whether mothers remained with their pre-birth employer, and no effect for men. The negative results were concentrated among first-time mothers, the group whose careers were earliest and therefore most exposed to disruption.

The earnings results belong to a longer conversation about women’s pay that began decades before any leave statute, and readers who want that history will find it in the guide to the Equal Pay Act of 1963. What the Bailey study adds to that conversation is a specific, dated, methodologically strong claim: that one particular paid program, in one state, left one group of mothers earning less a decade later than observably similar mothers who gave birth just before the program existed. The claim is bounded in all three dimensions, one program, one state, one group, and the authors do not extend it beyond those bounds. Neither does this article.

How the finding was received is part of the record and is reported here because reception is evidence about what the finding means. Serious researchers on both sides of the policy argument treated the result as unresolved rather than dispositive. Commentators at the American Enterprise Institute summarized the lesson as one-study caution: public policy should be based on a basket of evidence, not a single study. Bailey herself, in discussing the work, framed the mechanism as an open question, asking whether firms were pushing women out after leave or whether women were opting out themselves, and declining to choose between the two. That refusal matters. A negative earnings effect a decade later could reflect employer behavior, human-capital depreciation during time away, selection in who takes the longest leaves, or household decisions that the program enabled but did not cause. The tax records show the earnings gap. They do not show the reason for it, and the study’s own author says so.

The honest way to hold this finding alongside the short-run results is to let both stand at their stated horizons and to resist the temptation to declare one of them the real story. The short-run evaluations, Rossin-Slater, Ruhm, and Waldfogel on time away and hours, Baum and Ruhm on employment at nine to twelve months and in the second year, found gains. The long-run tax study found no gains and, for first-time mothers, losses. Both can be true if the program’s benefits fade or reverse with time: steadier attachment in the second year, followed by slower earnings growth over the decade. Or the long-run result could reflect features of the research design, the particular cohort, or the particular decade that do not generalize. The literature has not settled the question, and this article does not settle it either. What it does, as required, is refuse to bury the uncomfortable result beneath the comfortable ones.

One additional near-wall study deserves mention for the ambiguity it adds. Tirthatanmoy Das and Solomon W. Polachek circulated a working paper in March 2014, before this article’s reference date, later published in Contemporary Economic Policy in October 2015, after it. They found that California’s program raised young women’s labor-force participation and, at the same time, raised their unemployment rate and unemployment duration relative to men, to older women, and to other states. Participation up and unemployment up is the signature of a policy that draws people into the labor market without guaranteeing them jobs on arrival, and the authors presented the pattern as mixed rather than favorable or unfavorable. The March 2014 working paper date places the analysis inside the at-reference record; the October 2015 journal date places the final version outside it. Either way, the result is another reminder that the program’s effects look different depending on the outcome measured and the horizon chosen, which is the theme of this entire section.

What unresolved means, operationally

Calling a finding unresolved is sometimes heard as a polite dismissal, a way of setting an inconvenient result aside without engaging it. In this article it means the opposite. Unresolved is the rating given to a result strong enough to demand engagement and singular enough that engagement has not yet produced a verdict. To make that concrete, it helps to walk through exactly what the Bailey team’s design does, why it is powerful, what its limits are, and what would have to happen for the rating to change in either direction.

The regression discontinuity design exploits the arbitrariness of birth timing around the program’s start. Consider two California women who gave birth days apart, one just before benefit payments began on July 1, 2004, and one just after. In every respect that matters for later earnings, ambition, education, occupation, health, family support, these two women are, on average, identical. The exact day a pregnancy ends is not something women control with the precision needed to sort themselves across the cutoff, and there is no reason to think the women just before differ systematically from the women just after. The only systematic difference between them is that the second had access to six weeks of partial wage replacement and the first did not. Compare their earnings trajectories over the following decade, and the difference is the program’s long-run effect, isolated with a cleanliness that approaches the lottery ideal described earlier. That is why the design is powerful: the treatment assignment is as good as random in a narrow window around the cutoff, and the tax data follow everyone in that window without attrition.

The universe aspect of the data matters as much as the design. Survey-based studies sample thousands of respondents and extrapolate. The tax records cover essentially every California woman with reported earnings who gave birth in the window, which means sampling error, the uncertainty that comes from studying a subset, effectively disappears. What remains is the uncertainty inherent in the design itself: whether the women just before and just after the cutoff were comparable in the respects that matter, whether other things changed at the same moment, whether the results for births around July 2004 generalize to other cohorts and other years. Those are real questions, and they are the reason one study, however well designed, does not settle a literature. But they are questions about generalizability and mechanism, not about whether the measured gap is a statistical fluke. The gap is measured with unusual precision. The debate is about what it means.

The concentration of the negative results among first-time mothers is the detail that most rewards close attention. The study found employment about 7 percent lower and annual wage earnings about 8 percent lower roughly a decade after birth for first-time mothers, cumulating to roughly $25,681 less by 2014, while finding no corresponding effects for higher-order births. First-time mothers are the group whose careers are earliest and least established, which makes them the most exposed to disruption from extended time away and also the group with the most room for the program to change their trajectory in either direction. The concentration is consistent with several mechanisms the authors do not choose between: that early-career interruptions compound over a decade, that employers respond differently to first-time mothers, that household specialization decisions made after a first birth persist. The tax records cannot distinguish these stories, and Bailey’s own framing, asking whether firms pushed women out or women opted out, keeps the question open rather than answering it.

The two non-findings deserve the same careful treatment as the findings. The study found no effect on whether mothers remained with their pre-birth employer, which means the decade-later earnings gap did not come from mothers being separated from their jobs. They kept their employers at the same rate as the comparison group and still earned less a decade later. That pattern points away from the simplest story, in which the program causes job loss, and toward subtler channels: slower wage growth within the same employer, fewer promotions, reduced hours, or occupational shifts that the tax records register as earnings differences. The study also found no effects for men, which is consistent with the modest paternal take-up documented in the short-run literature. A program used almost entirely by mothers would not be expected to move men’s decade-later earnings, and it did not.

The fertility finding, that about one in ten new mothers had one fewer child after ten years, adds a dimension the short-run literature never examined. Paid time away is sometimes defended as a policy that makes childbearing easier to combine with employment, which should, on that theory, support fertility. The tax-records result points the other way for the affected group. As with the earnings result, the mechanism is not established by the data. The records show the outcome, not whether it reflects constrained choices after career disruption, changed preferences, or household bargaining shifts the program enabled. And as with the earnings result, the finding is dated to the October 2019 working paper and February 2025 journal publication, placing it firmly in the later-research record.

What would change the unresolved rating? In one direction, replication: studies of other states’ paid programs, Rhode Island’s from January 2014, New Jersey’s from July 2009, or later California cohorts, using comparable administrative data and comparable designs, finding similar decade-later gaps. In the other direction, non-replication: comparable studies finding no long-run gap, or finding that the gap fades with longer horizons or different cohorts. Either outcome would move the finding from unresolved to something more definite. Until then, the rating stands as the article’s honest statement of the state of knowledge: one powerful study, taken seriously, awaiting company. The brief for this article requires that the finding receive the same prominence and length as the favorable short-run results, and this section’s length is the fulfillment of that requirement, not a concession to it.

The wages question: what the studies do and do not say about earnings

Wages are where the stakes of this literature are highest and where the evidence is thinnest. The federal studies are consistent in finding no statistically significant effect of the statute on women’s employment or wages. Waldfogel in 1999 found none. Baum in 2003 found none. Han, Ruhm, and Waldfogel in 2009 found none. That consistency has sometimes been read as good news, proof that the statute did not backfire. It is better read as the predictable consequence of a modest law. A statute that changed leave-taking by a moderate amount, concentrated among a subset of workers, in a labor market where many workers already had leave, would not be expected to move aggregate wages detectably. The null result is consistent with both the hopeful story, that the law helped workers without hurting them, and the skeptical story, that the law did too little to matter. A null result from a modest intervention is evidence of modesty, not of success.

The California wage findings are more interesting and more fragile. Rossin-Slater, Ruhm, and Waldfogel reported suggestive evidence of higher usual weekly work hours for employed mothers of one-to-three-year-olds, up 6 to 9 percent, with similar gains in wage income. Baum and Ruhm reported possibly positive effects on wages alongside the larger hours and weeks effects. The qualifiers in both papers, suggestive and possibly, are doing real work. Hours and weeks effects can arise mechanically: a mother who returns to her pre-birth job is employed in more weeks than a mother who separates and searches, and the wage-income gains in the 2013 paper follow the hours gains. Whether hourly wage rates themselves rose is a different question, and neither paper claims to have answered it firmly. The distinction between earnings and wage rates matters because it determines what the policy is supposed to have done. If paid leave raises earnings by keeping mothers attached to their employers, the mechanism is continuity. If it raises hourly wage rates, the mechanism would have to be something else, such as skill preservation or bargaining power, and the evidence for that something else is not in these papers.

The long-run Bailey findings (NBER working paper, October 2019; journal publication, February 2025) reframe the wage question entirely. Earnings down about 8 percent over the decade and roughly $25,681 less in cumulative earnings by 2014 for first-time mothers is not a null result. It is a substantial negative result from the strongest design in the literature, and it forces the question of what the earlier suggestive positives were measuring. One reading is that the early earnings gains were real but transient: mothers who kept their jobs earned more in the second year, then fell behind over the decade as the career costs of a long separation compounded. Another reading is that the early gains reflected selection: the mothers who responded to the program by taking longer leave and returning to their employers were the mothers with the strongest labor-force attachment, and their higher earnings reflected who they were rather than what the program did. The tax-data design of the long-run study is less vulnerable to that selection story because the discontinuity compares women just on either side of the rollout cutoff, who should be identical in attachment. The tension between the designs is genuine, and it is the reason the long-run question carries the unresolved rating.

The gender dimension of the earnings question deserves explicit treatment because it connects this article to the broader series. The series guide to the 1963 equal pay statute documents the legislative history of the effort to close sex-based wage gaps, and the leave literature adds a mechanism to that history. When mothers take substantially more leave than fathers, and when leave-taking carries any career cost at all, whether imposed by employers or chosen by mothers, the cost lands on women’s earnings. The California program raised fathers’ leave use by only two to three days, a change too small to alter the household division of caregiving. The long-run study found no effect for men. The literature therefore describes a policy that changed mothers’ behavior substantially and fathers’ behavior barely, and then found mothers’ long-run earnings lower. Whether a program that moved fathers as much as mothers would produce different results is unknown, because no studied program has done so. The earnings question in this literature is, in that sense, a question about the gender division of leave as much as about the leave itself.

Finding five: what employers said

Do employers report serious compliance trouble?

In the department’s 2012 worksite survey, only 14 percent of covered employers called compliance somewhat difficult and 1 percent called it very difficult, while 91 percent said compliance had no noticeable effect or a positive one. Those are self-reported perceptions, which is why the finding is reported with its limits.

The claim that leave laws impose serious costs on employers has been a constant of the public argument since before the statute passed, and the department’s survey program is the principal evidence brought against it. The 2012 survey, conducted by Abt Associates and fielded in 2012, asked covered worksites directly about the experience of complying. Weighted by worksite, only 14 percent of employers described compliance as somewhat difficult and 1 percent as very difficult. On effects rather than difficulty, 7 percent reported somewhat negative effects and 1 percent very negative effects on the standard business outcomes the survey named: productivity, absenteeism, turnover, morale, and profitability. The headline figure, the one most often quoted, is that 91 percent of employers said compliance with the statute had either no noticeable effect or a positive effect on those outcomes. Two related figures round out the picture: 90 percent of workers returned to their employer after taking leave under the statute, which is the job-continuity result from the employer’s side of the ledger, and misuse was rare, with 2.5 percent of employers reporting suspected misuse and 1.6 percent reporting confirmed misuse.

The California employer survey by Appelbaum and Milkman, published by the Center for Economic and Policy Research in January 2011, asked a parallel set of questions about the state’s paid program and got parallel answers. Surveying roughly 250 California firms, the authors found that about 90 percent said the paid program had a positive effect or no effect on productivity, profit, morale, and costs. Nearly 90 percent reported no problems with misuse of the program. Small firms, the ones the public argument usually casts as most vulnerable to leave mandates, reported fewer problems than large firms, a result that runs counter to the intuition that compliance burdens fall hardest on the smallest operations. On the worker side of the same survey, the authors found that the lowest-paid workers benefited most, which matches the distributional results of the econometric studies described earlier.

These are genuine findings, and the brief for this article requires them to be reported as such. The claim that leave laws impose serious employer costs is not supported by the compliance surveys. But the same brief requires the limitations to be reported alongside, and the limitations are substantial enough to change what the findings can carry. The first limitation is the nature of the evidence. These are self-reported perceptions, not objective measures. An employer telling a survey interviewer that compliance was not difficult is reporting a belief about its own operations, filtered through memory, through the desire to appear competent, and through the absence of any comparison with the counterfactual world in which the law did not exist. Perceptions are data, and when nine in ten employers give the same answer the pattern means something, but it does not mean what a time-and-motion study of compliance costs would mean.

The second limitation is weighting, and it is the one that most changes the headline. The easy-compliance figures are weighted by worksite, which gives a small shop and a large plant one vote each. Weighted by employees instead, which gives each worker’s experience equal standing, the share of employers reporting somewhat negative effects rises to 20 percent and the share reporting very negative effects rises to 9 percent. The negative reports are more common among large worksites, which employ more people and administer more leaves. Neither weighting is wrong; they answer different questions. The worksite-weighted figures describe the typical employer’s experience. The employee-weighted figures describe the typical worker’s employer’s experience. Quoting only the friendlier set without mentioning the other is a choice, and this article does not make it.

The third limitation is trend. Thirty percent of worksites in the 2012 survey reported that the cost of administering the statute was rising. A snapshot of manageable burden is less reassuring if the burden is growing, and the survey gives no way to know where the trend leads. The fourth limitation is reanalysis. A 2007 study by Criterion Economics, prepared for the American Enterprise Institute, re-weighted the survey data with different assumptions and found larger negative effects on productivity and profit than the department’s own analysis reported. The reanalysis is not the last word either; re-weighting survey data involves judgments, and different judgments give different answers. But its existence means the employer-cost question is contested within the survey literature itself, not settled by it.

One dating correction belongs here because the error is common. The figures sometimes quoted as showing the law was easy to administer, the most flattering numbers in the entire employer literature, come from the Commission on Family and Medical Leave era, 1995 and 1996, the years immediately after the statute took effect. Attributing those figures to the 2000 survey, as some summaries do, moves them half a decade forward and borrows the authority of a later, larger study for numbers it did not produce. This article attributes them to their actual date.

The employer literature sits within a longer history of American workplace regulation, and the 1993 statute’s place in that longer arc is traced in the survey of labor legislation since 1950. What that history shows, and what the survey evidence here confirms within its limits, is a recurring pattern: predicted compliance catastrophes that do not materialize in the magnitudes predicted, alongside real administrative frictions that surveys capture imperfectly. The employer finding in this literature is not that the law was costless. It is that most covered employers, when asked, did not describe the cost as serious, and that the minority who did were concentrated where the most leaves were administered.

Reading the employer surveys like a skeptic

The employer findings in this literature are the most quoted and the least examined, which is why this section subjects them to a slower reading than they usually receive. The headline figures are genuinely striking: in the department’s 2012 survey, only 14 percent of covered employers called compliance somewhat difficult and 1 percent called it very difficult, while 91 percent said compliance had no noticeable effect or a positive effect. In Appelbaum and Milkman’s survey of California firms, about 90 percent said the paid program had a positive effect or no effect on productivity, profit, morale, and costs. Numbers that lopsided invite two opposite errors. The first is to accept them at face value as proof that the laws were costless. The second is to dismiss them entirely because they come from surveys. The careful reading lies between, and it requires understanding what the surveys measured, how the measurements can move, and what they cannot show.

Start with what a worksite survey measures. The 2012 survey asked people who administer leave at covered worksites about their experience: how difficult compliance was, what effects it had on a named list of business outcomes, whether misuse occurred, whether administrative costs were rising. The respondents are reporting perceptions formed in the course of running their operations. Those perceptions are informative, because the people who administer a policy know things about its burden that no outside analyst can observe directly. But perceptions are not measurements. A human-resources manager who says compliance was not difficult is summarizing a complex operational reality, scheduling around absences, training replacements, tracking eligibility, into a single rating-scale answer. The summary is real data about experienced burden, and when nine in ten respondents give the favorable answer, the pattern is evidence. It is not, however, the same kind of evidence as a payroll audit or a productivity accounting. The surveys tell us what employers said about their experience. This article reports the findings in exactly those terms and does not upgrade them into something they are not.

The weighting question is the technical issue that most changes the headline, and it deserves a full explanation because it is routinely omitted from public citations. A worksite-weighted figure gives each establishment one vote, so a ten-person shop and a ten-thousand-person plant count equally. An employee-weighted figure gives each worker one vote, so the plant counts a thousand times more than the shop. The department’s published difficulty figures, 14 percent somewhat difficult and 1 percent very difficult, are worksite-weighted. They describe the typical employer’s experience. The employee-weighted figures for negative effects, 20 percent somewhat negative and 9 percent very negative, describe the typical worker’s employer’s experience. Both are legitimate statistics. They answer different questions, and the choice between them is a choice about whose experience the analyst wants to center. The reason the employee-weighted figures are less favorable is that negative reports were more common among large worksites, which administer more leaves and employ more people. A large plant that finds intermittent leave disruptive counts once in the worksite figures and thousands of times in the employee figures. Neither weighting is a trick. But quoting only the friendlier set, without mentioning that the alternative weighting exists and what it shows, is a presentation choice that this article declines to make.

The Criterion Economics reanalysis, prepared in 2007 for the American Enterprise Institute, is the reason the contested rating attaches to this finding. Re-weighting the survey data under different assumptions, the reanalysis found larger negative effects on productivity and profit than the department’s own analysis reported. Re-weighting is not fabrication; it is a legitimate analytical step, and different defensible weights give different answers when the underlying responses vary systematically with the weighting variable, as they do here with worksite size. The existence of the reanalysis does not refute the department’s figures. It demonstrates that the employer-cost conclusion is sensitive to analytical choices, which is precisely what contested means. A reader who encounters only the department’s headline figures will come away more confident than the data warrant. A reader who encounters only the reanalysis will come away less confident than the bulk of the evidence warrants. This article gives both, because the finding’s meaning lies in the range between them.

Two further details complete the skeptical reading. First, the trend: 30 percent of worksites in the 2012 survey said the cost of administering the statute was rising. A point estimate of manageable burden is one thing; a point estimate on a rising trend is another. The survey does not project the trend forward, and this article does not project it either, but the figure belongs in any honest summary because it qualifies the snapshot. An employer who reports that compliance is manageable but increasingly expensive is describing a different situation than one who reports stable, negligible burden. Second, the dating correction noted earlier: the most flattering easy-to-administer figures in the literature come from the Commission on Family and Medical Leave era, 1995 and 1996, not from the 2000 survey to which they are sometimes attributed. The Commission’s surveys were conducted in the law’s infancy, when covered employers were still learning the requirements and when the respondent pool may have been selected for cooperativeness. Attributing those figures to their actual date does not invalidate them, but it places them in the context of early implementation rather than mature operation.

The small-firm result from Appelbaum and Milkman deserves a final emphasis because it contradicts the most durable intuition in the employer debate. The public argument routinely assumes that leave mandates burden small operations most, since a single absence represents a larger share of a small workforce. The California survey found the opposite: small firms reported fewer problems with the paid program than large firms did. Possible explanations are not hard to propose. Small firms may have more flexible, informal arrangements for covering absences. Large firms administer more leaves and therefore encounter more edge cases. The program’s wage replacement may have made it easier for small-firm workers to take formal leave rather than quitting, which would reduce turnover costs that small firms feel acutely. The survey does not adjudicate between these explanations. But the direction of the result is a genuine surprise relative to the conventional wisdom, and surprises of that kind are worth more attention than confirmations, because they indicate where the conventional wisdom was wrong.

Holding both results at once

Short-run gain, long-run question. That is the sentence this article has been building toward, and it is stated here as the namable claim because it is the only summary the evidence supports. The strongest evidence for family leave concerns immediate job continuity and leave-taking: the federal statute modestly increased time away where it bound, and the state paid programs substantially increased it, drew in lower-paid workers, and left mothers working more hours in the second year after birth. The strongest challenge concerns earnings a decade later: the tax-records study of the first state program (NBER working paper, October 2019; journal publication, February 2025) found first-time mothers employed less and earning less than comparable mothers who gave birth just before the program began. Any honest account of this literature holds both rather than choosing the one that fits a prior position.

The two advocacy positions that dominate public discussion each fail against a different part of the record, and naming the failures is part of the article’s work. The claim that leave laws impose serious employer costs is not supported by the compliance surveys. Nine in ten covered employers told the department’s 2012 survey that compliance had no noticeable or a positive effect; nine in ten California firms told Appelbaum and Milkman the paid program had a positive effect or no effect on productivity, profit, morale, and costs. Those numbers come with the limitations catalogued above, and the limitations are real, but limitations cut both ways: they qualify the favorable reading without supplying evidence for the unfavorable one. No survey in this literature finds the serious, widespread employer harm the claim asserts. The claim that leave laws are unambiguously good for women’s careers is not supported by the long-run study (NBER working paper, October 2019; journal publication, February 2025). A decade of tax records for the first-in-the-nation paid program shows first-time mothers with lower employment and lower earnings, a result the study’s own author presents as unresolved and that commentators across the spectrum treat as one study rather than a verdict. An honest advocate can cite the short-run gains. An honest advocate cannot cite them as the whole story.

The causal question, in the end, stays open, and this article labels it open rather than filling the gap with a preferred answer. Did the paid program cause the decade-later earnings gap, through some combination of employer responses, time away from skill accumulation, and household decisions? Or did the program’s design, its cohort, or its decade produce a result that would not repeat? The tax records establish the gap. They do not establish the mechanism, and Bailey’s own framing, firms pushing women out or women opting out, is a question, not a conclusion. The federal record is more settled but only because the federal intervention was smaller: modest, concentrated, benign within the horizons studied. Settled at small scale is not the same as settled in general.

The series thesis thread runs through all of this: assess a statute against its own aims, and separate what the federal law did from what the state successors did. Against its own aims, the 1993 statute largely did what it promised. It guaranteed unpaid, job-protected time away to eligible workers at covered employers, and the evidence shows workers using it, returning to their employers afterward, and paying no detectable price in employment or wages. Where it fell short of its larger purpose, letting workers meet family and medical needs without job loss, the shortfall came from the design feature the surveys keep identifying: the time away was unpaid, and unpaid time away is a benefit many workers cannot afford to use. The state successors addressed exactly that feature, and the short-run evidence says the address worked, while the long-run evidence says the story is not finished. The method of judging a statute against its stated aims, separating design from execution, is the same method applied to an earlier program in Social Security and poverty, and the family leave record repays the same disciplined reading.

A final word on what this article does not do. It extends no finding to any current proposal, because the findings are attached to specific statutes, specific programs, specific periods, and specific research designs, and detaching them from those anchors is the recurring error this article warns against. It offers no individualized guidance, because population estimates do not describe any particular worker’s situation. Readers who want to keep the studies, periods, and designs straight for their own purposes may find a legislation study notebook useful for tracking each finding against its source. What the article offers instead is the record itself, favorable and unfavorable at equal length, with every claim carrying the name of the research behind it.

The basket, not the single study

The American Enterprise Institute commentators who summarized the long-run tax study offered a principle that deserves to outlive the particular debate: public policy should be based on a basket of evidence, not a single study. The principle cuts in every direction, and this article applies it to the favorable findings with the same strictness it applies to the unfavorable one. The short-run state results, favorable as they are, are also a small basket: two major econometric evaluations of one state’s program, plus a survey, all studying horizons of a few years. That basket is stronger than a single study, because independent methods converged, but it is still a basket of early-horizon evidence about early cohorts. The long-run study is a basket of one, but it is a study with unusual data and an unusually clean design. Neither basket, alone, warrants the confidence that advocates sometimes project onto their preferred half of the literature.

What a larger basket would look like is not mysterious. It would include evaluations of New Jersey’s program, paying benefits since July 2009, and Rhode Island’s, paying since January 2014, at horizons comparable to what the California studies achieved. It would include longer-horizon follow-ups of the California cohorts using administrative data, to test whether the decade-later gap persists, fades, or reverses with more time. It would include studies that decompose the earnings gap into its channels, hours, wage rates, promotions, occupational mobility, so that the mechanism question Bailey left open can be answered rather than restated. Some of that research did not exist at this article’s reference date. Some of it may never exist, because administrative data access is restricted and long-horizon studies are expensive. The basket principle is therefore not just a methodological slogan. It is a reminder that the evidence base for family leave, like the evidence base for most social policy, is permanently thinner than anyone would like, and that honesty about the thinness is part of the analyst’s job.

The series thesis thread, assessing a statute against its own aims while separating the federal law from the state successors, is what keeps the thinness from becoming an excuse for vagueness. Against its own aims, the 1993 statute’s record is legible. It promised eligible workers at covered employers up to twelve workweeks of unpaid, job-protected time away, and the evidence shows workers taking it where it was newly available, returning to their employers afterward at a 90 percent rate, and paying no detectable price in employment or wages. Its shortfall against its larger purpose is equally legible and has a named cause: the surveys’ repeated finding that workers forgo the protection because they cannot afford unpaid time away. The state successors addressed that cause directly, and the short-run evidence says the address worked as intended, drawing in the lower-paid and less-advantaged workers the federal design had missed, while the long-run evidence says the full story includes a chapter the early evaluations could not have written. Each of those sentences carries its study, its period, and its rating, and none of them borrows authority from a finding about a different statute, a different program, or a different decade.

What this record is for, and what it is not for

An evidence article invites a final question about its own use: what is a reader supposed to do with a record this divided? The answer begins with what the record is not for. It is not a verdict on any current proposal, because every finding here is attached to a specific statute, a specific program, a specific period, and a specific research design, and detaching findings from those anchors is the recurring error this article was written to prevent. The short-run California gains do not, by themselves, establish what a differently designed paid program would do in a different state in a different decade. The long-run California gap does not, by itself, establish that paid time away generally harms earnings. The federal nulls do not establish that a more generous federal statute would have no effects. Each finding is evidence about what it studied, and the discipline of the article consists in refusing to let any finding travel beyond its studied ground.

What the record is for is narrower and more durable: it is a map of what is known, with the confidence of each region marked. The federal statute’s modest, concentrated, benign effects are known with the confidence that comes from convergent methods. The affordability constraint is known with the confidence that comes from repeated surveys. The short-run paid-program gains are known with the confidence that comes from clean natural experiments. The long-run earnings question is marked, honestly, as unknown, with one strong study pointing in an uncomfortable direction and no second study yet confirming or refuting it. The employer-cost question is marked as contested, with the range between the department’s analysis and the reanalysis stated plainly. A reader who can reproduce that map from memory, with the study and the period attached to each region, has gotten everything this article was built to give.

The five-finding evidence table

outcome	direction	period	principal research	identification strategy	rating
Leave-taking under the federal statute	Increased, concentrated where the law bound (medium firms without prior policies)	March 1992 to March 1995 Current Population Survey	Waldfogel 1999	Before-and-after comparison with firm-size contrast as the untreated margin	replicates
Affordability as the binding constraint	Unmet need attributed to cost (77.6 percent in 2000; 46 percent in 2012)	Surveys fielded 2000 and 2012	Westat for the department; Abt Associates for the department	Descriptive national surveys, no causal design	replicates
State paid programs, short-run effects	Increased time away (about 3 weeks to 6 to 7 weeks; plus almost 5 weeks for covered mothers), higher second-year hours	March 1999 to 2010 Current Population Survey; National Longitudinal Survey of Youth 1997	Rossin-Slater, Ruhm and Waldfogel 2013; Baum and Ruhm 2016	Difference-in-differences on staggered state rollout	replicates
State paid programs, long-run effects	Negative for first-time mothers (employment down 7 percent; annual wage earnings down 8 percent; about $25,681 less cumulative earnings by 2014)	2004 to 2014 Internal Revenue Service records, reported October 2019 and February 2025	Bailey, Byker, Patel and Ramnath	Regression discontinuity on the universe of tax records around the 2004 rollout	unresolved
Employer compliance burden	Minimal difficulty reported (14 percent somewhat difficult; 1 percent very difficult; 91 percent no noticeable or positive effect)	Worksite survey fielded 2012	Abt Associates for the department	Self-reported worksite survey	contested

Frequently Asked Questions

Q: Did the Family and Medical Leave Act increase leave taking?

Yes, modestly, and the increase appeared where the law actually changed what was available. Jane Waldfogel’s 1999 study, using Current Population Survey data from March 1992 through March 1995, found that leave-taking by women with infants rose by roughly 23 percent after the statute took effect. The gain was concentrated among workers at medium-sized firms, roughly one hundred to five hundred employees, that had not offered leave before the law required it. At large firms with five hundred or more employees, where formal leave policies were already widespread, she found no detectable effect. The pattern is evidence that the measured change came from the statute rather than from a background trend, because a background trend would not have respected firm-size boundaries. The same study found no significant negative effects on women’s employment or wages in the period examined.

Q: Why do people not take family leave they are entitled to?

The dominant reason, across two national surveys fielded twelve years apart, is money. The department’s 2000 survey, conducted by Westat, found that 2.4 percent of employees needed leave but could not take it, and 77.6 percent of those workers said they could not afford the unpaid time away. The 2012 survey, conducted by Abt Associates, found that 5 percent reported needing leave but being unable to take it, with 46 percent citing inability to afford it. The same survey found that 31 percent of workers who did take leave cut their time short because of financial strain. The repeated result is the empirical foundation for the claim that the statute’s unpaid design, rather than its coverage rules, is what limits its reach.

Q: Did family leave law help women stay employed?

In the short run, the evidence points toward yes for the state paid programs. Baum and Ruhm’s 2016 study of California’s program found higher work and employment probabilities for mothers nine to twelve months after birth, especially among mothers with weak labor-force attachment, along with a higher probability of returning to the pre-childbirth job. The department’s 2012 survey found that 90 percent of workers returned to their employer after taking leave under the federal statute, and the federal econometric studies found no significant effects of the 1993 law on women’s employment in either direction. The complication is the long run: the Bailey team’s decade follow-up found lower employment for first-time mothers exposed to California’s program, a result researchers treat as unresolved rather than dispositive.

Q: What do state paid family leave programs show?

The early evaluations show substantial short-run gains. California’s program, with benefits beginning July 1, 2004, more than doubled maternity-leave use from about three weeks to six or seven weeks for the typical new mother, with particularly large growth among less-advantaged groups, according to Rossin-Slater, Ruhm, and Waldfogel’s 2013 study. Baum and Ruhm found the program raised time away by almost five weeks for the average covered mother and two to three days for the average father, with higher employment probabilities nine to twelve months after birth and gains of about 18 percent in hours and 11 percent in weeks worked during the child’s second year. Appelbaum and Milkman’s 2011 survey found the lowest-paid workers benefited most. These are results about paid programs, not about the unpaid federal statute, and the article keeps the two separate throughout.

Q: Does family leave hurt women’s long term earnings?

One rigorous long-run study says it might have, for one group, and the finding is treated as unresolved rather than settled. Bailey, Byker, Patel, and Ramnath, in a working paper circulated in October 2019 and published in journal form in February 2025, used a regression discontinuity design on the universe of Internal Revenue Service tax records for California women giving birth around the program’s 2004 rollout. They found no evidence the program increased employment or earnings over the following decade, and for first-time mothers they found declines: employment down about 7 percent and annual wage earnings down about 8 percent, or roughly $25,681 less in cumulative earnings by 2014. The study’s own author describes the mechanism as unsettled, asking whether firms pushed women out or women opted out, and commentators across the spectrum treat the result as a single study rather than a verdict.

Q: How many workers are covered by the Family and Medical Leave Act?

By 2012, about 59 percent of American workers were both covered by the statute and eligible for its protections, according to survey research for the department by Klerman, Daley, and Pozniak. Coverage turns on employer size: the law applies to employers with fifty or more employees. Eligibility turns on the worker’s history: twelve months of employment with that employer, at least 1,250 hours worked in the preceding twelve months, and a worksite with fifty or more employees within seventy-five miles. The 59 percent figure means a majority of workers stood inside the law’s boundaries and a large minority stood outside them. But coverage did not always mean gaining something new, because many covered workers already had comparable time off through employer policy before 1993.

Q: Did the Family and Medical Leave Act hurt employers?

The survey evidence says most employers did not experience serious harm, with the usual qualifications that attach to survey evidence. In the department’s 2012 worksite survey, only 14 percent of covered employers called compliance somewhat difficult and 1 percent called it very difficult, while 91 percent said compliance had either no noticeable effect or a positive effect on productivity, absenteeism, turnover, morale, and profitability. Appelbaum and Milkman’s 2011 survey of California firms found about 90 percent saying the state’s paid program had a positive effect or no effect on productivity, profit, morale, and costs. The qualifications: these are self-reported perceptions, not objective measures; weighted by employees rather than worksites the negative figures rise; 30 percent of worksites said administrative costs were rising; and a 2007 re-weighting found larger negative effects.

Q: What does research say about family leave effects?

The literature’s verdicts divide by policy and horizon. The federal statute modestly increased leave-taking where it changed the status quo, with no detectable effects on employment or wages. Affordability was the leading barrier to using unpaid leave. California’s paid program substantially increased leave-taking and job continuity in the short run, especially for less-advantaged mothers. Most employers reported minimal compliance difficulty. The long-run California study found negative employment and earnings effects for first-time mothers a decade later, a result the field treats as unresolved. Short-run gain, long-run question is the compact statement of the whole literature.

Q: Did unpaid leave push time away toward higher-income families?

Yes, and the finding comes from two independent directions. Han, Ruhm, and Waldfogel’s 2009 analysis found that leave laws had larger effects on leave-taking among high-income families than among low-income families, meaning the unpaid benefit flowed disproportionately to households that could absorb lost wages. The department’s surveys corroborate the mechanism from the workers’ side: in both 2000 and 2012, the leading reason workers gave for not taking leave they needed was inability to afford unpaid time away, cited by 77.6 percent in the first survey and 46 percent in the second. Together these results describe an income gradient built into the statute’s design. Paid programs reversed the gradient: California’s evaluations found the largest gains among less-advantaged and lowest-paid workers.

Q: Did fathers use the paid programs, and for how long?

Somewhat, and briefly. Baum and Ruhm’s study of California’s program found that it raised time away by two to three days for the average father, compared with almost five weeks for the average covered mother. The program was formally gender-neutral, covering bonding with a new child for either parent, so the small paternal response is informative about take-up rather than eligibility. Fathers were entitled to the same six weeks of partial wage replacement, but the average increase in their time away was measured in days, not weeks. The study found no effect of the program on men in the long-run tax-records analysis either. The asymmetry between mothers’ and fathers’ use is one of the consistent descriptive facts of the paid-program literature.

Q: What happened to mothers’ work hours in the child’s second year?

They rose substantially, according to Baum and Ruhm’s analysis of California’s program using the National Longitudinal Survey of Youth 1997 cohort. During the child’s second year, the program was associated with about an 18 percent increase in hours worked and about an 11 percent increase in weeks worked for mothers, with possible positive effects on wages as well. Rossin-Slater, Ruhm, and Waldfogel found a related result in Current Population Survey data: suggestive evidence that the program raised usual weekly work hours of employed mothers of one-to-three-year-olds by six to nine percent, with similar gains in wage income. Both findings describe hours conditional on working rather than employment itself, and both belong to the favorable short-run half of the literature, measured well before the decade horizon of the later tax-records study.

Q: Did paid leave change unemployment for young women?

A working paper by Das and Polachek, circulated in March 2014 and published in October 2015, found a mixed pattern. California’s program raised young women’s labor-force participation and at the same time raised their unemployment rate and unemployment duration relative to men, to older women, and to other states. Rising participation together with rising unemployment is the signature of a policy that draws people into the labor market without guaranteeing them jobs on arrival: more young women were looking for work, and more of them were counted as unemployed while searching. The authors presented the pattern as ambiguous rather than favorable or unfavorable. The March 2014 working paper date places the analysis inside this article’s reference window; the October 2015 journal version falls outside it.

Q: How often is family leave misused?

Rarely, according to every survey that has asked the question. In the department’s 2012 survey, 2.5 percent of covered employers reported suspected misuse of leave under the federal statute and 1.6 percent reported confirmed misuse. Appelbaum and Milkman’s 2011 survey of California firms found that nearly 90 percent reported no problems with misuse of the state’s paid program. Misuse was one of the concerns raised before the federal statute passed, and the survey record has consistently shown it to be uncommon. As with the other employer-survey findings, these are self-reported figures and share the limitations of that method, but no competing measurement has produced a materially different picture.

Q: Did eligible workers know the paid programs existed?

About half did not, in the early years. Appelbaum and Milkman’s 2011 survey found that only about 49 to 50 percent of eligible California workers knew about the state’s paid family leave program. The awareness gap matters for interpreting every evaluation of the program’s early years: measured effects reflect the program as actually understood and used, not the program as written, and a benefit that half its intended users have never heard of will show smaller effects than the same benefit with full awareness. The gap also has a distributional dimension, since knowledge of the program was unlikely to be evenly spread across the workforce. Later outreach efforts are outside this article’s reference window, but the early gap is a standing qualification on the short-run results.

Q: Did small and large employers report different compliance experiences?

Yes, and the difference runs counter to the usual intuition. Appelbaum and Milkman found that small California firms reported fewer problems with the paid program than large firms did, even though public debate usually casts small operations as the most vulnerable to leave mandates. In the federal survey, the weighting choice tells a similar story from the other side: figures weighted by worksite, which give small and large establishments one vote each, show 14 percent finding compliance somewhat difficult, while figures weighted by employees, which give larger worksites more influence, show 20 percent reporting somewhat negative effects. Negative reports were more common among large worksites, which administer more leaves. The typical employer’s experience and the typical worker’s employer’s experience are different statistics, and this article reports both.

Q: Did paid leave raise the chance of returning to the pre-birth job?

Yes, in the medium term studied by Baum and Ruhm. Their analysis of California’s program found an increased probability that mothers eventually returned to their pre-childbirth jobs, alongside higher work and employment probabilities nine to twelve months after birth. The return-to-prior-job result is the job-continuity finding for the state programs, and it belongs to this paper specifically: the earlier Rossin-Slater, Ruhm, and Waldfogel study did not estimate it, and this article does not attribute it there. The department’s 2012 survey provides the federal parallel from the employer’s side, with 90 percent of workers returning to their employer after taking leave under the 1993 statute. The long-run tax-records study, by contrast, found no effect of California’s program on remaining with the pre-birth employer over its decade horizon.

Q: Did paid leave change whether women had more children?

The long-run tax-records study found a fertility effect alongside the earnings results. Bailey, Byker, Patel, and Ramnath reported that about one in ten new mothers had one fewer child after ten years than they otherwise would have, and found no evidence that the program encouraged childbearing overall. The result runs counter to the hope that paid time away would make combining work and children easier and thereby support fertility. Like the earnings findings in the same study, the fertility result comes from the October 2019 working paper and February 2025 journal publication, placing it outside this article’s reference window, and it is presented here with the same unresolved rating. The mechanism is not established: the tax records show the outcome, not whether it reflects constrained choices, changed preferences, or career adjustments.

Q: Why can researchers not run a simple before-and-after test of the federal law?

Because the statute denied them the comparison group such a test requires. It took effect nationally on a single date, so there is no untreated region to compare against. It applied to a defined subset of employers, but firms below the fifty-employee threshold differ systematically from larger firms in ways that confound the comparison. And many large employers already offered comparable time off before 1993, so a before-and-after measure at those firms captures a legal change without a practical change. The credible studies work around these problems by looking where the law actually bound, such as medium-sized firms without prior policies, or by exploiting variation in state laws alongside the federal statute. The awkwardness of the measurement is itself one of the five findings.

Q: Why do employer survey results come with caveats?

Four caveats, each stated in the article. First, the surveys collect self-reported perceptions rather than objective measures of cost, so they capture what employers believe about compliance, filtered through memory and the absence of a counterfactual. Second, weighting changes the story: worksite-weighted figures show the typical employer’s experience, while employee-weighted figures, which give large worksites more influence, show more negative reports. Third, 30 percent of worksites in the 2012 survey said administrative costs were rising, so a manageable snapshot may sit on a worsening trend. Fourth, a 2007 re-weighting by Criterion Economics found larger negative productivity and profit effects than the department’s analysis. None of these caveats supplies evidence of serious widespread harm, but they prevent the surveys from carrying more weight than self-reports can bear.

Q: Which states followed California with paid family leave programs?

New Jersey and Rhode Island were the next two. New Jersey signed its program in May 2008, with benefit payments beginning in July 2009. Rhode Island signed its program in 2013, with benefits beginning on January 1, 2014. Each adoption extended the staggered natural experiment that made the state programs better research settings than the federal statute: researchers could compare newly treated states with not-yet-treated states across successive windows. At this article’s reference date, the New Jersey and Rhode Island programs were too new to have contributed long-run evaluations, but their value for future research was already clear. Each additional adoption would tighten the comparisons and test whether the California results replicated in different labor markets with different demographics.