How a Birthday Becomes a Natural Experiment
This chapter explains how the California school-entry study turns a narrow birthdate boundary into evidence about women’s education, careers, and children. The key task is to follow the chain from birthdate to school entry to the particular schooling margin that changes, then ask whether later outcomes fit education better than alternative explanations. Understanding that chain lets the reader interpret the study’s estimates as local causal evidence rather than as a general comparison between more- and less-educated women.
From a birthdate to more schooling
California’s school-entry rule supplied the first link. For the women studied, children generally could enter kindergarten only if they turned five by December 1 or December 2, depending on the period. A girl born just before the applicable date was therefore expected to enter school roughly a year earlier than a girl born just after it. The two girls might be nearly identical in every characteristic relevant to later work; the administrative rule nevertheless placed them in different school-entry schedules.
The rule did not simply change a label on the first day of kindergarten. California also required students to remain in school until age 18 or high-school graduation. Under normal grade progression, an early entrant could finish twelfth grade before turning 18, while a late entrant would finish only eleventh grade by that age. Earlier entry thus created a route to more completed schooling before the age-based exit condition took effect. The mechanism runs through the interaction of entry and exit rules, not through an assumption that being younger in a classroom is inherently advantageous.
In practice, the rule was strong but not perfectly binding. The expected school-entry gap was about one year, while the actual gap was about 0.75 years. Some families did not follow the default schedule, and individual circumstances could affect enrollment. That imperfect compliance is not a fatal flaw. It means that the clean comparison is between being born just before and just after the cutoff—the policy’s intent-to-treat effect—rather than between two groups whose school starting ages differ by exactly one year.
The distinction matters. Suppose the cutoff raises average schooling by a small amount because some marginal students complete an additional post-secondary credential while others do not change their path. The outcome difference across the cutoff reflects the average effect of being assigned to the more education-favorable side of the rule. It is not automatically the effect of one standardized year of college for every woman. The authors later rescale some results by the education discontinuity, but that derived interpretation depends on treating education as the operative channel and on assumptions about how outcomes vary with years of schooling.
The schooling response is also specific. In the California birth-records sample, being born just before the cutoff increases completed education by about 0.16 years in early career and about 0.05 years in mid-career. The corresponding estimates in the recreated earnings sample are very similar. More importantly, the lasting difference is concentrated in “some college.” By mid-career, college attendance rises by about 1.2 percentage points in the birth-records sample and 1.5 points in the earnings sample, roughly a 2 percent increase over the local baseline. Early in the life cycle, high-school completion and college graduation also move somewhat, but those other margins are smaller or no longer prominent by mid-career.
That pattern gives the later career results a precise reference point. The study is not testing a vague proposition that education makes women more capable or more ambitious. It is asking what happens when a school-entry rule makes some women more likely to complete the particular post-secondary margin that remains visible years later. The possibility that many marginal students attended two-year or community colleges is plausible from the occupation evidence, especially the rise in jobs associated with some college, but the researchers do not observe each woman’s institution directly.
The diagram’s central point is that the cutoff creates a comparison, not a perfect treatment assignment. The two sides differ in their expected school entry and, on average, in completed schooling; later outcomes are compared at that boundary. The credential pattern then becomes a diagnostic. If the career change were mainly caused by being younger relative to classmates, there would be less reason for it to appear specifically in jobs whose requirements match the schooling margin that moved.
Why the comparison can be credible
A regression-discontinuity design relies on a continuity idea: absent the cutoff treatment, potential outcomes would change smoothly with birthdate. A woman born one day before the boundary is not assumed to be identical to a woman born one year earlier. The claim is narrower. Around the boundary, the date itself should be as good as arbitrary with respect to the later outcome, so a sharp jump exactly at the boundary can be attributed to the rule if no other discontinuity is present.
This assumption could fail in several ways. Families might deliberately time births around the date. Birth season could correlate with parental health, work, or resources. The rule could affect who later appears in the mother sample through fertility or interstate mobility. And even if birthdates are as-if random, an early school start could influence careers through relative age in the classroom, not through additional schooling. Each possibility requires a different check; no single balance test settles all of them.
The authors first look for jumps at the exact cutoff rather than gradual seasonal patterns. The underlying outcomes are residualized for birth-year effects and plotted on either side of the boundary. A seasonal pattern would usually change across a broader calendar interval. A discontinuity that appears precisely where the school rule changes is more consistent with the policy mechanism. The visual evidence is paired with a density check: the distribution of birthdates is continuous around the cutoff, which provides no sign that births were manipulated at the threshold.
They also test whether the cutoff changes who becomes a mother or when motherhood occurs. Across the earnings and birth-records samples, there are no significant effects on having any birth, a first birth, or a second birth, nor on average age at those births. By race, 47 of 48 estimates are null; the one marginally significant result concerns age at first birth for Black women in the birth-records sample. As a conservative choice, the baseline analysis excludes Black women. Including Black women slightly attenuates the education estimate but leaves most other outcome estimates similar. This is an example of how a study can narrow its headline population to protect the comparison rather than quietly treating an imperfect balance result as irrelevant.
The data also show balance in predetermined characteristics and no visible sorting at the boundary. The analysis uses exact days from the relevant entry cutoff as the running variable, a before-cutoff indicator, birth-year fixed effects, and controls appropriate to the woman’s age and, for child outcomes, the child’s parity and multiple-birth status. The baseline estimates use a 70-day bandwidth with triangular weights, giving observations nearest the cutoff more influence. These choices do not make the design universally valid; they make its local comparison explicit and testable.
The study’s population is part of the causal claim. It centers on women born in California who had a first birth in California and, in the main analysis, had that birth by age 31. The women are observed from ages 16 to 40 through California birth records and linked IRS-Census administrative records. The earnings panel uses cohorts born from 1977 through 1987 to obtain relatively balanced age-specific coverage. This is a rich design for mothers’ careers and infants, but it is not a random sample of all U.S. women or a direct test of every type of college attendance.
The first-stage result should therefore be stated in two layers. First, the birthdate rule changes school-entry timing. Second, that timing changes completed schooling, especially some college. The later career discontinuity is then evidence about the consequences of the policy-induced schooling difference. If one skips the first two layers and simply says “college raises earnings,” the design has been turned into a claim it did not estimate.
Education or simply being younger for the grade?
Relative age is a credible alternative because the cutoff affects more than the calendar date of school entry. A child who starts earlier may be younger than classmates, and age within a grade can affect early test performance, diagnosis, confidence, or peer relationships. Some of those effects might persist even if completed schooling did not change. The fact that a career outcome jumps at a school-entry boundary, by itself, cannot tell us which pathway is responsible.
The paper’s most informative test compares job requirements with the schooling margin shifted by the cutoff. If additional education is the main channel, the effects should be strongest in jobs requiring exactly some college. They might spill into jobs requiring less schooling if the credential makes a worker more attractive, but they should not create a comparable increase in jobs that require a completed college degree. A relative-age mechanism, by contrast, has no obvious reason to respect that credential boundary. It would be more likely to spread across occupations with different formal requirements.
The observed pattern follows the education prediction. Mid-career employment gains are concentrated in jobs requiring some college but no degree, which account for about 62 percent of the total increase in employment. The estimate is imprecise enough that the confidence interval can extend as high as 100 percent, so the appropriate conclusion is that these jobs can explain a majority of the increase, not that exactly 62 percent of every individual’s outcome has been mediated by a credential. At the same time, the study finds precise zero effects on jobs requiring a BA and on jobs requiring less education but an exam. It can rule out even a 0.2 percentage-point increase in degreed jobs with 95 percent confidence, equivalent to about 16 percent of the total job increase.
This is not a perfect mediation experiment. The job classification is built from occupation requirements and does not reveal every worker’s skill or path. Younger age-for-grade could still have small effects that the study cannot detect, and education could carry consequences beyond formal requirements. But the sharp alignment between the shifted schooling margin and the affected job margin is difficult to reconcile with a purely age-for-grade explanation. It is evidence about the mechanism, not merely another outcome.
The researchers examine a second alternative: partner selection. Schooling or relative age could alter whom women meet, whom they marry or partner with, or the resources available through a partner. Yet the study finds no cutoff effect on whether a partner is present, whether the partner is a high-school graduate, whether the partner works, or whether the partner holds a professional job. There is a small increase in partner age, consistent with school-cohort matching, but it is not large enough to account for the main career discontinuity. These tests do not describe every household relationship; they make a substantial change in partner composition an unlikely primary explanation for the observed career gains.
The broader lesson is methodological and substantive at once. A causal design is strongest when it combines a credible assignment boundary with predictions that differ across mechanisms. Here, the entry rule predicts a schooling jump, and the occupation data allow the authors to ask where the career effect should appear if schooling is doing the work. The same margin changes on the way in and on the way out: some college becomes more common, and jobs requiring some college become more common later.
That logic also clarifies what the study cannot say. It cannot show that every woman who delays or accelerates college would experience the same return. It cannot identify the exact community college, certificate, course, or skill that mattered for each marginal student. It does not eliminate all consequences of relative age, family background, or local labor-market conditions. And because compliance is imperfect, the most defensible direct result remains the local effect of being born just before the California cutoff for the study population.
The design nevertheless earns its role as the foundation for the career findings. It links a narrow administrative rule to a measurable education shift, tests whether the change is concentrated where that shift predicts, and checks whether the people near the boundary appear balanced on important pre-treatment characteristics. Once that foundation is in place, the central question changes. We no longer need to ask only whether the cutoff changes schooling. We can ask how the resulting career return evolves: whether it is immediate or delayed, whether it concerns employment as well as pay, and whether it remains visible when women become mothers.