Table 2 reports the estimates of the effects of an increase in household exposure to conflict during the Second Intifada on children’s primary school achievement obtained from an OLS regression (column 1) and from a 2SLS regression (column 4). In addition, we show the corresponding results from the reduced form (column 2) and first stage (column 3) regressions. As described in the previous section, in each regression we include individual-level, school-level, and locality-level control variables.
The OLS coefficient suggests a negative and significant association between households’ exposure to conflict and their children’s school performance: an additional event of parents’ experience of conflict is associated with a 1.32 point decrease in student GPA in primary school, which corresponds to approximately 8% of a standard deviation. The reduced form regression suggests that GPA drops by approximately 2.4 points per one hundred fatalities in the locality.
The first stage regression shows that one hundred more fatalities in the locality increase parents’ exposure to conflict by 0.37 events on average. With a first stage F statistic of 55, our instrument easily passes conventional thresholds for strong instruments. The 2SLS coefficient on parents’ exposure to conflict remains negative and statistically significant. We find that one additional event of parents’ exposure to conflict induced by the Second Intifada reduces the primary school GPA of their children by 6.46 points. This effect represents a decline of about 35% of a standard deviation.
The 2SLS estimate is much larger in absolute value than the OLS estimate. Although we have no theoretical prior as to the direction in which OLS would be biased compared with the true causal effect of exposure, the size of our 2SLS coefficients may raise concerns about the validity of our results. Large 2SLS—compared with OLS—estimates are quite common in applied research and three explanations can be put forward. The first is measurement error in the explanatory variable, which (if classical) attenuates the OLS coefficients. Clearly, if some households who have experienced violence do not report this in our survey, whereas others over-report events, and if misreporting is uncorrelated with the error term, OLS estimates would be biased towards zero. However, it seems at least equally plausible to assume that misreporting is in some way related to unobserved determinants of student achievement. The second explanation is that the IV approach identifies (a weighted average of) complier-specific causal effects, which can potentially be larger than OLS estimates. It is plausible that at least among always-takers (households prone to conflict events no matter what the level of conflict in the locality) the effect is smaller than among compliers (households only affected if the level of conflict in the locality is high). If this also holds for never-takers is unclear. A third explanation—potentially damaging to the IV approach—is that the exclusion restriction does not hold. Of course, this cannot be entirely ruled out in our setting. To partially address this concern, we note that the reduced form coefficients for all specifications clearly show that locality-level conflict intensity during the Second Intifada is associated with worse educational attainment more than seven years later, and that this association is robust to a number of specification changes (reduced form results are shown in Tables 14 and 15 in our Appendix B). Thus, even if the exclusion restriction did not hold, there was robust evidence that the violent political conflict has long-term consequences for educational attainment. This reduced form analysis is similar to what most of the literature has done when data on individual experience of conflict are lacking (see, for instance, Brück et al. (2019)).
To compare our results with those obtained in the literature, we note that Brück et al. (2019), analyzing the short-term effects of conflict on individual test scores for the high school final exam, find that a one standard deviation increase in the number of fatalities reduces average test scores by about 1% relative to the overall mean. Our findings are very similar: the reduced form coefficient implies that a one standard deviation increase in the number of fatalities reduces student GPA in primary school by 1.2% relative to the overall mean.Footnote 19
As previously mentioned, we also estimate a range of regressions with alternative operational definitions of the exposure variable, obtaining very similar results. Importantly, our instrument does not predict exposure to conflict before or after the Second Intifada (see columns E and F of Table 13 in our Appendix B). We interpret this as evidence that the instrument does not pick up any trends in location-specific levels of violence.
Robustness checks and heterogeneous effects
We assess the robustness of our main results to a number of further specification changes.
First, in column (1) of Table 3 we check the sensitivity of our results to a change in the functional form of the first stage and reduced form regressions. The major concern here is that exposure to conflict and GPA may not follow linear functions of the number of fatalities. To allow for this possibility, we have recoded our instrument into 4 categories (as shown in Fig. 1): 0 fatalities, 1–10 fatalities, 11–50 fatalities, and > 51 fatalities. Our point estimate changes somewhat, we lose precision and the first stage F statistic decreases, but the qualitative result remains.
Second, to investigate heterogeneous effects across the distribution of GPA, in columns (2) to (4) we report the treatment effects at the 25th, 50th and 75th percentiles. Our results suggest that the effect of family exposure to conflict induced by the Second Intifada is concentrated in the lower quantiles of the GPA distribution. In other words, the long-term effects of family exposure to conflict induced by the Second Intifada seem to be driven by poor academically performing students.
Third, another concern regards the sensitivity of our findings with respect to the year in which school achievement in primary school is measured. As previously mentioned, our dataset provides information on student GPA not only for the school year 2012/2013 but also for the two preceding school years, i.e., 2010/2011 and 2011/2012. Hence, we run two additional 2SLS regressions of model (1) using student GPA for the school years 2010/2011 (column 5) and 2011/2012 (column 6) as alternative outcomes. Results remains qualitatively unchanged relative to the main specification: the coefficient on family exposure to conflict has negative and significant effects on children’s GPA in primary school. Note, however, that point estimates are actually smaller in the two earlier years than in 2012/13. This suggests that effects on student GPA do not tend to subside over time. We interpret this as corroborating evidence for the plausibility and usefulness of our long-term analysis.
Fourth, in column (7) we verify the robustness of our results when using a broader measure of conflict intensity that includes the locality-level number of all Palestinian and Israeli victims during the Second Intifada. The reason for this check is that both sides of the conflict may react in a regular and predictable way to violence against them. This would imply that an increase in the number of conflict-related Israelis fatalities may lead to more violent actions against the civilian population in the West Bank. Again, the estimated parameter resembles closely the one obtained in the benchmark specification.
Next, we check what happens when we include governorate fixed effects (Column 8) in model (1). Identification then rests on within-governorate variation in the intensity of conflict. Differences in exposure to violence or children’s educational attainment that are linked to the larger region are hence controlled for—addressing potential concerns about the validity of our instrument. We find that the coefficient of interest is not only quantitatively similar to the benchmark specification (see column 4 of Table 2), but also preserves the statistical significance at the 10% level, hence strengthening the confidence in our identification strategy.
In a related robustness check, we exclude single governorates one at a time to examine whether the results are driven by a specific governorate. This exercise, of which we do not report detailed results, confirms that our main results are robust to this change (Tables 4 and 5).
Furthermore, in columns (9) and (10) we split the sample in two parts based on the date of birth of the children in our sample. Specifically, in column (9) we restrict the sample to all children born before February 2000. These children have attended school for at least one year during the Second Intifada. One might argue that some part of the effect we measure is not due to parental exposure to conflict but rather to disruptions to teaching, such as closing of schools, detainment of teachers, road closures keeping children from reaching schools and so on Brück et al. (2019). In column (10) we focus on children born in February 1999 or later, who have entered school in September 2005 (after the end of the Second Intifada), and whose schooling has not been directly affected by the conflict. Taken together, the results in columns (9) and (10) do not provide any evidence for differential effects of household exposure to conflict by date of birth. In column (11) we show that our main effect is qualitatively similar when we control for the log of the area of the locality (in square kilometer).Footnote 20 An additional concern regards the sensitivity of our findings with respect to the most violent localities included in the sample and whether these are driven by a specific locality. We have thus selected the ten most violent localities (in terms of the number of fatatlities) during the Second Intifada (i.e., Nablus, Jenin, Tulkarm, Hebron, Ramallah, Qualquiliya, Tulkarm Camp, Al Bireh, Askar Camp and Qabatiya). Our results still hold when we exclude from our sample one locality at a time (see Table 18 in our Appendix B).
In Table 6 we conduct a set of balancing tests, aimed at verifying that localities that have been exposed differently by fatalities during the Second Intifada are similar with respect to a number of pre-Second Intifada characteristics at the locality level. To this end, we collected information on a set of pre-Second Intifada locality-level characteristics in 1999.Footnote 21 Overall, we find that the pre-Second Intifada rate of unemployment and the pre-Second Intifada fraction of Palestinian workers employed in Israel are not significantly correlated with the number of fatalities during the Second Intifada (see columns 1 and 2). At the same time, we find a significant relationship between the number of fatalities and the average daily wage, the proportion of low-skilled workers and urban area (see columns 3, 4 and 5). While we cannot rule out the possibility that fatalities during the Second Intifada are not randomly assigned across localities, we note that similar results have also been found by previous studies, e.g., Calì and Miaari (2015) and Miaari et al. (2012). To partially address this concern, in Table 7 we control for all the pre-Second Intifada covariates included in the balancing tests. Reassuringly, our main result remains negative and highly statistically significant, although the point estimate becomes larger (see column 2). This result mitigates concerns related to omitted variables bias. We thus argue that selection issues should not be a major source of concern for our analysis (Tables 8 and 9).
A remaining issue about the identification of the long-run effect of family exposure to conflict on education concerns the fact that families have continuously been exposed to conflict even after 2005. To dispel this issue, in columns 2 and 4 of Table 10 we consider the 2SLS and reduced form relationships once we control for fatalities after the conclusion of the Second Intifada. In both cases we show that the coefficient on fatalities during the Second Intifada changed little relative to the benchmark specification, whereas the coefficient on fatalities after the Second Intifada is much smaller in magnitude and not statistically significant. We interpret this as evidence that the number of fatalities after the end of the Second Intifada does not play any role in shaping student educational outcomes as for 2012/2013.
In what follows, we present some heterogeneity analyses along several dimensions. We provide detailed regression results of these analyses in our Appendices A, B and C (see https://tinyurl.com/yb3v6tvh). First, we consider grade retention as an alternative outcome. Specifically, we exploit the fact that grade repetition in primary school occurs when students obtain a grade below 50 in at least 4 subjects. In case students fail up to 3 subjects, they sit for a make-up exam at the beginning of the next school year (MoEHE, 2015). Since our dataset provides information on student GPA not only for the school year 2012/2013 but also for the two preceding school years, i.e., 2010/2011 and 2011/2012, we constructed the outcome for grade retention using the three academic years, i.e., if the student failed to pass to the next grade in one of these three years. Results displayed in Table B.5 show that family exposure to conflict significantly increases the probability of grade retention by 14 percentage points. We obtain a similar result if we construct the outcome for grade repetition using the most recent school year, i.e., 2012/2013.
Second, we estimate the models separately by student gender, by grade achieved distinguishing between elementary vs. middle schools, by paternal education, by number of siblings, household income and type of school (see Tables 19 and 20 in our Appendix B). The overall picture reveals that there are no significant differences between male and female students. At the same time, we detect no significant heterogeneous effects between elementary school (grades 1–6) and middle school (grades 7–10). Furthermore, we carry out the analysis after splitting the sample between more educated fathers (i.e., with an upper preparatory secondary education) and less educated fathers (i.e., with an education below upper preparatory secondary education). Although the difference is seemingly large, we cannot tell it apart from a statistical zero. Although our dataset does not contain information on household size, it does include information on the number of siblings in the household. We perform the analysis controlling for the number of siblings and splitting the sample by the median number of siblings. The 2SLS coefficient of interest is not sensitive to the inclusion of the number of siblings among the set of controls. Similarly, the estimated coefficient is similar when the sample is divided into the two groups. We conclude that the number of siblings leaves our main result substantially unchanged. In our dataset, household income is a categorical variable representing the net monthly income with the following categories measured by the local currency in Palestine “New Israeli Shekel” (NIS): (1) under NIS 1500; (2) NIS 1500–NIS 2499; (3) NIS 2500–NIS 3999; (4) NIS 4000–NIS 5000; (5) NIS 5000 and over. Reassuringly, theinclusion of household income among the set of the controls does not affect our main result. We also conduct heterogeneity analyses using an alternative definition of the dependent variable, i.e., an indicator taking value one (and zero otherwise) if the individual reported an income above the midpoint of the categories (i.e., 2500 and over). We find the effects to be concentrated among the household with income above the median. Finally, when we split the sample by school authority (public vs. UNRWA schools), we find that the effects are concentrated among the public schools.