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4.2Empirical Strategy

We will analyze the impact of AGEs on schools in terms of process outcomes – parental participation – comparing the average outcomes of schools in the treatment group to those in the control group 12 and 24 months after the intervention begins. We will obtain the impacts of the program using differences-in-differences estimation using multivariate regression to condition on baseline sociodemographic and economic characteristics. We will further test for differential impacts by gender, being indigenous, and parental background (for example, maternal education, economic status).

Our second set of analyses will estimate the impact of AGEs on intermediate outcomes – teacher effort, repetition, dropout, failure – 24 and 36 months after the intervention. Again, we will control for economic characteristics, gender, being indigenous, and parental background, and we will use the difference-in-difference method. Our final set of analyses will focus on learning outcomes, expecting to see changes only after 36 months of exposure to the program. We will use difference-in-difference methods. We will control for economic characteristics, being indigenous, gender and parental background. We will also control for exposure to other programs operating in those communities, such as federal programs (for example, Oportunidades, Carrera Magisterial, PARIEB, etc.) and any relevant state initiative.
The benefits of this experiment over previous research include: (a) its randomized design; (b) the direct testing of the impact on teacher absenteeism; (c) the direct testing of the impact on student learning achievement; and (d) the estimate of the marginal contribution of extra resources.
Because treatment has been randomly assigned and is thus orthogonal to unobserved heterogeneity, a standard least squares (LS) procedure should yield unbiased estimates of the program impact. Our estimates will not suffer from endogenous program placement bias, or self-selection bias, at the school level, two of the main threats to identification in SBM studies. Nonetheless, we will add baseline and/or current averaged student, school and community characteristics as controls. In all regressions, we will also control for the number of periods the school has received AGEs as well as for exposure to the other compensatory education components (namely school infrastructure, didactic materials, teacher training and teacher incentives) and other relevant federal programs and state initiatives.
We will be able to measure the impact of the enhanced AGE. We will also be able to test for the impact of enhanced parental participation on outcomes. However, it is possible that parental participation is affected by other channels and that parental participation is endogenous to the expected outcomes. We will attempt to control for characteristics that may influence the parental decision to participate in school activities. These will include, for instance, parental education, parental occupations, and so on, which we will measure in the survey instruments that will be applied each year. More importantly, taking advantage of the fact that the enhanced AGE is randomized, we will use that parameter as an instrument for participation. Since we expect variations in participation and that participation will be greater in the treated schools, then this becomes a valid instrument for testing the impact of participation. This approach gives us an accurate measure of the impact of the enhanced AGE, and the instrumental variable approach allows us to test for the impact of participation. Our survey instruments will measure changes in behaviors of the various actors, including parental participation.
When evaluating the program impacts on student learning the analysis will be performed at the student level on fourth and fifth graders. As the program is implemented at the school level, we will cluster standard errors for that level, as we still may have unobservable effects common to students in the same school. For fourth grade students, this analysis will allow us to follow their progress until they finish primary school; in addition, for fifth grade students we will also be able to study whether AGEs has had any impact on the students’ individual choice to transition to secondary school. Despite increased demand for secondary education, large numbers of students still drop out. In fact, low transition rates into secondary school are one of the major weaknesses of the education system. The lower secondary school completion rate is only 80 percent. Moreover, only 85 percent of completers continue to upper secondary. Therefore, 20 percent of those in lower secondary drop out and another 15 percent do not transition to upper secondary. In this set of analyses, we will additionally control for a more a comprehensive set of baseline and current student individual, household and community characteristics.1
We will attempt to minimize or dismiss any potential source of bias that might threaten the validity of the identification strategy adopted despite the randomized nature of the treatment variable. In particular, we will explore the existence of student sorting bias (students entering or exiting the school as a result of treatment) by studying total enrollment and differential changes in total enrollment in treatment and control schools. We will also check whether we observe students migrating from treatment to control schools or vice versa, in our data. This might not only generate high student migration rates and large spillovers, but might also imply that parents (or the students themselves) are likely to have a certain choice on which school to send their children. We will thus endogenize the school choice decision and correct for student selection bias using selection methods and exclusion restrictions included in the students surveys such as distance to school, lack of school materials at home, position among siblings at home, parent’s education, etc. We will use Manski bounds for treatment effects (Manski 1990) to fit the magnitude of our estimates whenever the potential for bias is non-negligible and we lack a better way (an appropriate instrument) to correct for it.
In addition, we will also have a set of student progressing to higher levels of schools and new students entering the system. That is, different samples of students with differential exposures to the program. For this, we will stratify the analysis by cohort, in order to evaluate program effects by length of exposure.

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