under RD. For instance, taking the full sample and including controls, the RD shows an impact of 0.16 _σ_ with a standard error of 8.9, this last one being two a half times larger than the SE under DD which shows an effect of 0.10 _σ_ and SE of 3.5. As we restrict further the bandwidth under RD, the SE increases and the point estimate reduces. The increase in SE or lost precision of the RD estimator can be explained by poor statistical power attributable to the relatively few schools around the cutoff. Notice that although there is a large number of students in our sample, the number of clusters or schools is relatively small, especially when we restrict the sample to schools located within the OB (127 schools). Schochet (2005) estimated that, for the same level of statistical precision, the number of clusters needed under RD are three to four times larger than the sample size required under a randomized controlled trial (RCT). According to Schochet (2005) “[t]he reduction in precision in the RD design arises due to the substantial correlation, by construction, between the treatment status and score variables that are included in the regression models; this correlation is not present under the random allocation design.” Additional evidence in Dragoset and Deke (2012) shows that, under certain conditions, sample requirements are 9 to 17 times larger under RD that for RCTs. In our particular case, the number of clusters required under an RCT with an error of 0.05, power of 0.8, minimum detectable effect of 0.13 _σ_ , an intra-class correlation of 0.05, _R_<sup>2</sup> of 0.05 and an average number of students per school of 250 is equal to 200 clusters, or 100 treatment and control schools. Taking the results of Schochet (2005), to have the same statistical precision under an RD we would need at least three times more clusters, or 600 schools within the OB, a figure considerably higher the 129 schools within the OB. Therefore, the lack of precision under RD when we restrict the sample to schools within the OB is explained by a lack of statistical power due to the low number of schools around the PAE’s information dissemination strategy could have created incentives within schools that can explain a positive impact. First, the pressure put on PAE teachers by being declared low-performing schools may have created incentives to practice some type of “strategic behavior” by school directors or teachers such as cheating or teaching to the test (see (Figlio and Getzler, 2002)). ENLACE uses two algorithms to detect cheating and results are invalidated when it happens.<sup>8</sup> There is no evidence of test scores invalidation by the Ministry of Education of Colima to any PAE school during 2010, 2011 and 2012. In addition, the percentage of students who did not take ENLACE in 2010 and 2011 was equal to non-PAE schools, which suggests that PAE schools did not try to manipulate test scores by choosing the students who took the test. Second, student mobility across schools might have affected the test scores after the PAE schools were identified. But such mobility in Mexico is very difficult without a strong reason such as the geographic reallocation of

> 8Algorithms have also been used in the US to detect cheating, see Jacob and Levitt (2003) for an example using data from Chicago public schools.

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