Who Actually Crossed the Secondary-School Threshold?
The 1993 Mexican schooling reform did not raise educational attainment by the same amount for everyone. This chapter focuses on the reform’s first-stage result: what changed in literacy, completed years of schooling, and secondary completion, and why the largest gains appeared among people who began with the fewest educational options. That distinction supports a practical judgment: the value of a compulsory-schooling policy cannot be read from its national average alone. We need to know which threshold moved, for whom, and under what access conditions.
The national number is real—but incomplete
For people born just after the reform’s eligibility cutoff, literacy increased by 0.88 percentage points, completed schooling rose by 0.17 years, and the likelihood of completing at least nine years rose by 1.79 percentage points. The baseline levels help give those estimates meaning. In the study’s full sample, literacy was already about 93 percent, average completed schooling was 8.57 years, and 59 percent had completed at least nine years.
These figures describe a discontinuity near the eligibility threshold, not a national time series. They compare cohorts close to the cutoff under the study’s regression-discontinuity design. The estimates therefore answer a focused question about people whose birth timing placed them just on different sides of reform exposure. They do not say that every person born after 1981 experienced exactly the same increase, or that every Mexican locality followed the same trajectory. Keeping the comparison narrow is part of what gives the result its causal force.
These are not trivial changes, but they are also not a mechanical translation of the law’s nominal extension from six to nine compulsory years. A three-year increase in the legal requirement produced an average increase of less than one-fifth of a completed school year. That gap is not evidence that the law did nothing. It tells us that a legal mandate, a student’s exposure to school, and the number of years ultimately completed are different stages in the policy chain.
The reform did not impose sanctions for non-compliance. Schools and households faced different constraints, and secondary provision expanded unevenly. Some children were already likely to continue, some remained unable to do so, and others may have crossed the threshold because the new requirement coincided with a school becoming practically reachable. The national estimate averages across these situations. It is the observed first-stage effect near the cutoff, not a count of the years written into the statute.
The literacy result illustrates another reason to read the indicators together. When a population is already close to universal literacy, a small percentage-point change can still represent people whose basic educational path was altered, but the statistic cannot carry the same interpretation as a large gain in a low-literacy setting. Years of schooling and nine-year completion reveal movement through the lower-secondary threshold more directly. Each measure asks a different question: can a person read and write, how much schooling did they complete, and did they reach the reform’s new compulsory boundary?
A percentage-point estimate also needs its denominator kept in view. A 1.79-point increase in lower-secondary completion is a change in the probability of crossing a threshold, not a claim that every person completed the same number of classes or acquired the same skills. The baseline of 59 percent means that the policy operated in a population where a substantial share already reached nine years, while a substantial minority did not. The average result is compatible with a larger effect for the minority whose schooling was most responsive and a smaller effect for those whose path was already set.
Completion of at least 12 years was not clearly higher in the full sample. Statistically distinguishable gains at that upper-secondary threshold appeared only in small rural localities and among people speaking an Indigenous language. That pattern places a limit on any claim that the reform created a broad automatic pipeline from lower secondary to upper secondary. The mandate’s clearest first-stage effect was at or near the threshold it directly targeted, with further progression visible in settings where the initial gap was largest.
The pattern also prevents a common interpretive shortcut. If lower-secondary completion rises but upper-secondary completion does not rise everywhere, the correct conclusion is not that the first result was illusory. It is that the reform had a specific reach. It moved some people through the grade range it targeted, while later progression depended on additional school capacity, household conditions, and the distance to the next educational threshold. The absence of a clear aggregate upper-secondary effect is a boundary on the claim, not evidence that the lower-secondary change had no later significance.
The visual contrast is the point. The national estimate describes the average response around the cutoff. The subgroup estimates show where the policy changed the educational distribution more sharply. Neither replaces the other. Without the aggregate number, it would be easy to exaggerate the reform’s general reach; without the subgroup numbers, it would be easy to miss its most consequential effects.
Why the margin was largest at the bottom
Among people who spoke an Indigenous language, the reform increased completed schooling by about 0.50 years—roughly three times the national average. Literacy rose by 4.52 percentage points from a baseline of 78 percent. Completion of at least nine years rose by 3.77 percentage points from a baseline of 29 percent, and completion of at least 12 years rose by 1.91 points from a baseline of 10 percent. The comparison is not between a population with no education and one with universal access. It is between different distances from the secondary-school threshold, and those distances change what a mandate can accomplish.
The size of the Indigenous-language estimate is meaningful partly because of its baseline. A 3.77-point increase from 29 percent represents movement in a setting where completing lower secondary was still the exception for many people near the reform threshold. The same number of additional years can have a different social meaning when it moves someone from primary schooling toward secondary completion than when it adds a marginal credential to a person who was already likely to continue. The estimate does not prove that all barriers were removed; it shows that more people crossed the measured boundary.
The rural pattern follows the same logic. Smaller localities generally had lower baseline attainment and weaker access to conventional secondary schools. Where a school was far away, where a family’s work depended on young people’s time, or where language and service barriers made continuation difficult, the legal requirement encountered a large gap between formal entitlement and practical opportunity. Expanding telesecundaria helped extend secondary provision to remote areas. The reform could therefore produce a larger observed jump in places where access had previously been the binding constraint.
By contrast, a locality with high pre-reform attainment offered less room for the mandate to change completed schooling. Many students there may already have continued beyond primary education, so the law could not create a large additional first-stage effect among people whose education would have followed a similar path without it. This is not a claim that urban or non-Indigenous students gained nothing. It is a claim about marginal response: the same policy can have a smaller measured effect where the targeted threshold was already more widely crossed.
The study’s evidence on reform uptake supports this interpretation. Municipalities with lower pre-reform education, larger Indigenous and rural populations, more agricultural employment, and lower migration tended to have higher uptake. In ordinary language, the places where the policy moved schooling most were also places where secondary education had previously been less common and labour-market integration more constrained. That relationship helps explain why the later life-course estimates are concentrated in the same populations. The people whose education was changed are not a random slice of all Mexican adults.
This is also why “who benefited?” cannot be answered by looking only at the legal text. A mandate has to meet a supply system and a household decision. If secondary education is technically free but practically distant, the rule may have little effect until a school or distance-learning service makes attendance possible. If a locality has a school but young people’s labour is central to household survival, the opportunity cost remains. The observed subgroup effect is the joint result of a policy reaching people and of the surrounding conditions allowing that reach to become completed schooling.
But uptake patterns are not a complete explanation of individual treatment effects. A municipality with a large Indigenous population can contain households with very different resources, languages, school access, and expectations. The study’s observable subgroup measure is whether a person speaks an Indigenous language; that is useful for locating unequal reach, but it should not be treated as a complete description of Indigenous identity or community experience. Likewise, “rural” is based on locality size and does not summarize every reason a child remained out of school.
That distinction matters because there are two ways to misuse a distributional result. One is to flatten it into a universal claim: compulsory schooling works the same way everywhere. The other is to treat the subgroup pattern as if it identified a single cause, such as distance, language, poverty, or agricultural work. The evidence supports a more disciplined conclusion. Several constraints were concentrated in the same places, and the reform had more room to operate there. The estimates reveal where the margin was largest; they do not separately measure the contribution of each constraint.
Access is not the same as quality
The first-stage results also help distinguish the value of access from the value of school quality. The reform expanded the obligation to attend lower secondary school, and telesecundaria extended reach to communities without conventional schools. Yet formally trained subject teachers for the new secondary curriculum were not available until a separate teacher-education reform in 1999, six years after the mandate. This timing suggests that the immediate attainment effects were driven primarily by expanded access rather than by a simultaneous, fully developed improvement in instructional quality.
That does not mean quality was irrelevant. A student may complete more years without receiving the same learning benefit as a student in a better-resourced school. Nor does it mean that access and quality can be cleanly separated in practice. A school’s presence, the form of instruction, teacher availability, and a family’s confidence that attendance is worthwhile may interact. The evidence allows us to say that schooling exposure increased and that the reform’s direct first-stage gains were larger in underserved settings. It does not allow us to claim that every additional year delivered identical learning.
The difference between access and quality also clarifies what the later chapters can legitimately ask. If additional schooling changes fertility, employment, or children’s enrolment, those results show that the attainment margin mattered under the reform’s institutional conditions. They do not show that the same result would follow from any school expansion, or that the content of instruction was irrelevant. A mandate may be powerful precisely because it reaches people who were previously excluded, while still needing better teaching and progression opportunities to convert attendance into broader capability.
The distinction is especially important when the policy is described as “three more years of education.” That phrase can hide two separate achievements: remaining in school, and receiving instruction that improves capability. The study measures attainment, literacy, and completion; it does not offer a complete test-score account of instructional quality for the affected adults. Later chapters can therefore examine what the attainment change was associated with, but they should not silently convert completion into equal learning or into a guaranteed wage advantage.
The threshold as a bridge to adult life
Crossing lower secondary is consequential in the study not because nine years is a universal dividing line between success and failure, but because it is the educational margin the reform changed. Once attainment is treated as a policy-generated difference rather than a background characteristic, it can be carried into questions about family decisions, child survival, work, and mobility. The reform’s first-stage result is the bridge that makes those questions interpretable.
It also tells us how to read the later outcomes. If a downstream effect is largest among Indigenous or rural people, that may reflect both a larger schooling gain and different conditions in which schooling is used. The first-stage heterogeneity is therefore not merely descriptive context attached after the fact. It is part of the denominator for understanding every later estimate. A one-year change in education for a person already near upper-secondary completion is not necessarily the same treatment as a one-year change for someone who had previously been unlikely to complete lower secondary.
The first-stage result also gives the life-course analysis a concrete counterfactual. The question is not whether people with more education look different from people with less education; they often do for many reasons. The question is whether the people whose education was nudged upward by this reform later show a different pattern. That is a more demanding comparison, and it is why the subgroup and threshold details must travel with the downstream estimates rather than being left behind as background.
This is why the aggregate 0.17-year result should be held together with the larger subgroup gains. The national average shows the reform’s overall reach under imperfect compliance. The subgroup pattern shows where the law changed the distance between formal entitlement and actual attainment. The two findings point in the same direction: compulsory schooling had a larger marginal return where previous policy and markets had left more educational capacity unused.
The next question is what those threshold-crossing gains did inside adult lives. The answer begins with family formation and child survival, where the reform’s effect is not captured by a classroom statistic or a pay cheque. To interpret those outcomes properly, the reader must keep the attainment margin visible: the study is following people whose schooling changed because the reform reached them, not estimating a universal effect of education for every adult.