Kurigram students.

Second, we exploited the insight obtained from Baird et al. (2014) that the fraction of those offered treatment in a cluster (i.e., treatment saturation) could be used to estimate the spillover effects on the non-treated population. Recall from Section I in the article that in the 17 sample schools that participated in our experiment, 1,665 students were enrolled in the 4<sup>_th_</sup> to 8<sup>_th_</sup> grades. We initially selected 1,292 children (belonging to 1,292 different households) among these students. The remaining 373 students were excluded, either because they were known to have access to electricity, because a sibling was one of the 1,292 students (in each household, only one child was included in our study sample), or because they were not considered regular students because their school attendance had been lower than 80% during the last four months. From these 1,292 students, we further excluded 381 students who were found to have access to electricity, when the research team visited their homes, resulting in 911 target students, which eventually turned into 882 effective sample students.

Consequently, each grade at each school potentially consisted of four types of students: (whether treated or not) our study sample, their siblings, those with access to electricity at the baseline, and those with poor attendance. This experimental design enabled us to explore whether the fraction of treated students and their siblings in each school grade (i.e., treatment intensity) influenced the students’ educational achievement, after controlling for the school grade fraction of regularly attending students with no access to electricity at the baseline (i.e., eligible fraction), whereby both fractions varied across grades within a school. Note that the latter fraction was endogenous. However, given this control, the former fraction was expected to have random variation. This approach is similar to that adopted by Miguel and Kremer (2004) and Oster and Thornton (2012). Having no statistically significant relationship between treatment intensity and educational achievement reduces any concern about spillover effects.<sup>32</sup> To calculate the aforementioned fractions, we needed to know exactly why the 373 students were excluded during the first screening process, as well as the treatment status of their sibling if that sibling was eventually part of our study sample. Unfortunately, this information was not collected. We therefore considered the following four distinctive scenarios: (Case A) all 373 students had a sibling belonging to our treatment sample; (Case B) all 373 students had a sibling belonging to our control sample; (Case C) all 373 students had access to electricity at the baseline; and (Case D) none of the 373 students were regularly attending school. The treatment intensity takes the mean values of 0.49 (std. 0.09), 0.27 (std. 0.04), 0.27 (std. 0.04), and 0.36 (std. 0.05) in Case A, Case B, Case C, and Case D, respectively, along with the eligible fraction taking the mean values of 0.77 (std. 0.09), 0.77 (std. 0.09), 0.55 (std. 0.09), and 0.71 (std. 0.10), corresponding to each of the four cases.<sup>33</sup> Acknowledging its limitations, considering these cases, and

> 32We are grateful to one anonymous referee for recommending this exercise.

> 33The maximum (minimum) value of the treatment intensity was 0.71 (0.23), 0.38 (0.04), 0.38 (0.13), and 0.50 (0.18) in Case A, Case B, Case C, and Case D, respectively. Similarly, the maximum (minimum) value of the eligible fraction was 1.00 (0.50), 1.00 (0.50), 0.77 (0.23), and 1.00 (0.31) in Case A, Case B, Case C, and Case D, respectively. Note that in order to calculate the treatment intensity, we included only students who regularly attended school in the total number of students in each school grade (i.e., the denominator).

37