From a Legal Mandate to a Causal Test
The Mexican reform is useful as evidence only if we can separate what the 1993 legal change did from everything else that distinguishes one birth cohort from another. This chapter focuses on that separation. It explains how an age rule around the 1981 cohort created a comparison, how eligibility differed from actual schooling, and how the study carries the resulting schooling difference into adult and intergenerational outcomes. The aim is not to turn the reader into an econometrician, but to make clear what the estimates mean before we interpret them.
A legal threshold that changed exposure
The reform extended compulsory education from six to nine years and made lower secondary schooling mandatory. Its eligibility rule was tied to age at the start of the 1993 school year: children younger than 12 were covered. Because age is closely linked to year of birth, the rule created a boundary around the 1981 birth cohort. People born just on one side of that boundary were more likely to have been exposed to the new requirement than people born just on the other.
That boundary is not the same thing as a national before-and-after comparison. A simple comparison of older adults with younger adults could mistake the reform for any other change that occurred over time: economic growth, changing family norms, new labour demand, or gradual expansion of schools. The cohort comparison instead asks a narrower question. Among people close to the eligibility threshold, did outcomes jump at the point where exposure to the reform changed?
The logic resembles comparing neighbouring steps on a staircase rather than comparing the bottom step with the top. People born a year apart can still differ, but the assumption is that their potential outcomes would otherwise change smoothly across the cutoff. A sudden change at that point is then evidence consistent with the reform. The assumption cannot be observed directly, so the study tests whether other characteristics also jump. It reports no meaningful discontinuity in gender, Indigenous status, locality type, household size, water access, or remittance receipt. That pattern gives the schooling discontinuity a more credible interpretation: the cohorts look similar on measured predetermined features, while their reform exposure differs.
This is a narrower claim than saying the reform created a perfectly comparable experiment. The people near the threshold were not assigned to a laboratory, and the country did not pause other changes in 1993. The design works because a small difference in birth timing is less likely to line up exactly with a sudden change in all the other forces that shape adult life. The closer the comparison is kept to the eligibility boundary, the less room there is for long-run cohort differences to masquerade as a reform effect. Wider comparisons can be useful for checking whether the pattern is stable, but they also require more care about gradual trends.
The institutional setting complicates the picture in an important way. The reform did not come with identical schools in every locality. Public lower-secondary education was already free, but access still depended on distance, infrastructure, and local capacity. Telesecundaria expanded as a way to reach remote communities, while the formally trained subject teachers needed for the new secondary curriculum were not available until a separate teacher-education reform in 1999. The change in completed schooling therefore reflects a policy package in which access expanded, but quality did not immediately move in lockstep.
That distinction matters for causal interpretation. If a remote community gained a school at the same time that the law changed, a later outcome may reflect both the student’s additional attendance and the fact that a new service became available. The study cannot peel those components apart perfectly. It can, however, ask whether the timing, gradual rollout, municipality controls, and narrow cohort comparison make a competing explanation more or less plausible. The result should be read as the effect of schooling induced within this institutional setting, not as a pure estimate of a law floating free of schools.
That is why imperfect compliance is not a technical footnote. Some eligible children did not complete additional schooling, and some ineligible people may have continued their education for other reasons. The legal rule changed the probability of exposure; it did not assign everyone the same number of completed years. This makes the reform less like a switch that turns education on and more like a lever that moves some people across a threshold. The study’s estimates describe the people for whom that lever actually changed schooling.
Two questions, two statistical stages
The study’s design separates two questions that are often blurred in discussions of education policy. The first is: what did eligibility for the 1993 reform do to educational attainment? The answer comes from the discontinuity in schooling near the cohort threshold. The second is: what did the additional schooling induced by the reform do to later outcomes? The answer uses reform eligibility as an instrument for completed years of schooling.
In plain language, the first stage looks for a jump in education at the eligibility boundary. Did people just after the cutoff complete more years, become more likely to finish lower secondary school, or show higher literacy? This is the direct effect of reform exposure on attainment. It is the foundation for every later estimate because without a schooling difference there is no reform-induced variation to carry forward. The first stage also tells us whether the policy reached people in practice. A statute can be ambitious on paper and weak in the data; the schooling jump is where the legal change becomes an observed treatment.
The second stage asks what happens when the schooling difference generated by that threshold is used to compare later outcomes. It examines fertility, child survival, employment, sector of work, migration, remittance exposure, and children’s schooling. The instrument is useful because it isolates a portion of educational attainment that came from the reform rather than from a person’s prior motivation, family resources, or local opportunity alone. The study is not comparing people who simply chose different levels of education and then declaring the difference causal. It is using the policy-generated shift as the source of comparison.
A simple thought experiment helps. Suppose two people close to the cutoff would otherwise have followed similar paths, but the person eligible under the new rule stayed in school for longer. If later outcomes differ, the design asks whether that difference follows the schooling variation created by eligibility. It does not claim that every difference between the two people disappears, or that the reform is the only event in their lives. The credibility comes from the cutoff, the balance tests, and the robustness checks taken together—not from the idea that birth year itself is magical.
That distinction also defines the interpretation. The result is not “one extra year of schooling has exactly this effect for everyone.” It is the local average treatment effect for compliers: people whose educational attainment increased because the reform reached them. Those people are more likely to come from lower-attainment, rural, and Indigenous settings, where the policy had more room to operate. A person who would have completed secondary school without the mandate is not represented in the same way as someone for whom the new obligation and available school place made the difference.
The word “local” has two meanings here. It refers to people near the eligibility threshold, and it refers to a particular population of compliers within that comparison. It does not mean the result is unimportant. These are precisely the people a compulsory-schooling expansion is designed to reach. But it does mean that a policymaker should not take the estimate and apply it mechanically to students already likely to complete secondary school, or to places where schools, labour markets, and household constraints differ sharply.
The design includes several checks to make this interpretation more credible. The study examines narrower and wider birth-cohort windows, allows for different age trends on either side of the cutoff, and uses false cutoffs as placebos. If any arbitrary cohort boundary produced the same pattern, the true threshold would be less persuasive. The reported placebo tests do not show systematic schooling discontinuities at the shifted cutoffs, and the main attainment estimates remain similar under alternative bandwidths. Municipality fixed effects absorb stable local differences, while controls for locality size and sex reduce additional measured differences relevant to the outcomes.
These checks answer different concerns. Balance tests ask whether predetermined characteristics jump where treatment changes. Placebos ask whether the result appears at a threshold the reform did not create. Bandwidth checks ask whether the estimate depends on including cohorts farther from the policy boundary. None proves the identifying assumptions, but together they make it harder for a single accidental trend to explain the attainment result. A careful reading therefore treats the estimates as strong local causal evidence conditional on the design, not as an unqualified description of all educational change in Mexico.
The evidence is strongest for the reform’s local effect near the threshold. It is not a certificate that every later outcome must be attributed only to individual schooling. The IV interpretation requires an exclusion restriction: eligibility should affect downstream outcomes primarily through the schooling it changes. But the 1993 policy environment also included infrastructure expansion and telesecundaria. The study argues that delayed teacher training, gradual rollout, municipality controls, narrow cohort windows, and placebo results limit the concern that unrelated cohort changes drive the estimates. Still, the exclusion restriction cannot be verified directly. The safest reading is the effect of reform-induced schooling as delivered under the 1993 institutional package.
The diagram’s sequence matters. Eligibility is the source of variation; schooling is the treatment whose downstream effects are estimated; later outcomes are not simply compared across generations without adjustment. Controls do not manufacture causality, and the instrument does not reveal which internal pathway—skills, preferences, household bargaining, or opportunity costs—dominates. They help define the comparison and reduce measured sources of difference, while the identifying assumptions do the remaining work.
There are also limits created by the data itself. The study uses the 2020 census because the affected cohorts were 37 to 42 years old, old enough for much of adult life and fertility to be visible and for some child outcomes to be observed. It cannot eliminate all concerns about selective migration, mortality, or which children remain in the parental household. Those concerns are examined through balance and co-residence checks, but a check can bound a problem without proving that it is absent. The paper is also an IZA discussion paper that describes itself as preliminary work intended for academic debate, so the estimates should be treated as serious but revisable evidence rather than a final institutional verdict.
This is the discipline the causal design adds to the life-course question. It does not make the reform’s story simple. It tells us which part of the story is anchored to a defined threshold, which part is an estimate for compliers, and which part remains a judgment about mechanisms and context. With that distinction in place, the first substantive result can be read correctly: the mandate did not produce a uniform educational lift. It changed attainment most where schools and families had previously faced the largest gap between what education required and what it made possible.