to either hide money from their spouses (in wave 1) or whether to control money themselves (in wave 2).

I also investigate possible heterogeneity of effects along two dimensions that have been suggested as important in the intra-household bargaining literature, namely women’s initial bargaining power and women starting to earn more than the husband.<sup>59</sup> I am underpowered to identify interaction terms between the selected variable and the heterogeneity variables, but the sizeable coefficients provide suggestive evidence that the increase in decision-making and female assignable expenditures is larger for selected women with above median initial decision-making involvement. In contrast, the selected women who started earning more than their husbands between factory baseline and household surveys appear to spend less on female expenditures and remittances. This is in line with the results in Bertrand et al. (2015), which found that US couples in which a woman earns more than her husband are less satisfied with their marriage, more likely to divorce and more likely to have a higher gender gap in non-market work.

# **4.4 Robustness checks**

The large positive effects on expenditures on women’s assignable goods and remittances are robust to different estimation approaches, placebo tests and checks for attrition, as well as different specifications, variable definitions and data sources, though the impacts on women’s involvement in decision-making in wave 1 and girls’ expenditures are somewhat more sensitive to those checks. I also demonstrate that the effects are not mainly driven by the training that was delivered as part of the promotion program.

I implement a regression discontinuity design (RDD) relying on the factory rankings of candidates<sup>60</sup> as well as a matching approach<sup>61</sup> as robustness checks. Figure 1 compares the coefficients between the PDS Lasso results and these two different approaches for the impacted variables, where the decision-making index is expressed in tenths of a standard deviation for exposi-

> 59Results are shown in Tables C.16 and C.17 in the Online Appendix.

> 60I use the ranked shortlist of operators provided by each factory after removal of any ineligible candidates, as explained in Section 3.1. Recall that only those operators with a rank better than the factory-specific cutoff were assigned to the program. Since factories nominated different numbers of operators, I scale the rank of operators by the total number of operators nominated in each factory to make the ranks comparable across factories. I use the distance of this scaled rank variable from the factory-specific cutoff as the running variable. I determine the optimal bandwidth following Imbens and Kalyanaraman (2012) for each outcome variable. Using the observations within this bandwidth, I then allow for a linear function of the running variable separately on either side of the cutoff when estimating the effect of being selected for the promotion program. Standard errors are clustered at the individual level.

61I implement the nearest-neighbor matching estimator suggested by Abadie et al. (2004), with one-to-one matching with replacement and using the matrix of the inverse sample standard errors of the matching variables as weights in the matching. I use all balance variables in Table 1, as well as all factory, enumerator and month dummies as matching variables. To include balance variables which are missing for some observations, I set these to zero if they are missing and also include indicators if they are missing in the matching.

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