Anotaciones sobre interferencia técnica 37

The identification of causal effects typically requires to imagine a counterfactual sit- uation in which the individuals exposed to the reform would not have been exposed. We exploit the exogenous variation induced by the parental leave reform to define an indicator variable D ∈ {0, 1} such that D = 0 whenever a mother gave birth shortly before July and D = 1 whenever the mother gave birth shortly after that date. A possible identification strategy could be to compare mothers in D=0 with those in D = 1 in case many data points are available exactly at the cut-off. Any difference in the employment outcomes of interest Y could now be attributed to the change of the part-time subsidy scheme if nothing else drives a potential difference in the outcomes.6 _{However, any estimation strategy, that exploits information away}

from the cut-off date to increase the sample size, might potentially be exposed to seasonal patterns and time trends. In our setting the starting date of the school year could invalidate such an analysis. Depending on the federal state, the school year usually starts in August or September and child care attendance follows this time plan. Children who are already one year old have better chances to get a child care slot. This implies that children born before the cut-off date who are slightly older than those born after the cut-off date might have a higher probability to attend child care. If employment decisions of mothers systematically differ shortly before and after the cut-off date due to the availability of public child care, then a measured difference in the outcomes can not be purely attributed to the reform. We account for this by comparing the difference in outcomes in 2015 (T=1) to the difference in the previous year (T=0). Similar to prior articles (Cygan-Rehm, 2016; Cygan-Rehm et al., 2018; Schönberg and Ludsteck, 2014), this DiD identification strategy yields an average treatment effect on the treated (ATET) in T=1 under certain assumptions. To clarify things, consider the potential outcomes framework proposed by Rubin (1973). In general, denote variables with capital letters and its realizations with low- ercase letters. Define the potential outcome for the two time periods as Y₀d and Y₁d such that for every observation in the sample only the potential outcome with D=d of the realized outcome is observed. Further, we observe some covariates which we denote by X. Then, Heckman et al. (1997) show that our parameter of interest ATET = θ = E Y₁1−Y₁0|D=1 is identified under the following set of assump- tions.

Assumption 1(Common trends): E Y0

1 −Y00|X, D =0



=E Y0

1 −Y00|X, D =1.

In words, conditional on X the average outcomes for D = 0 and D = 1 would have followed parallel trends in the absence of the treatment. In our setting this means that the difference in outcomes between mothers giving birth shortly before

6_{This identification strategy was applied by some studies in the context of parental leave imple-}

and after the cut-off date stays constant between 2014 and 2015 in the absence of the reform. In general, the assumption is empirically not testable and there might be evi- dence that can raise doubts concerning the validity of the assumption. Following the standard in the literature, in our sensitivity analysis we estimate effects for periods where we would not expect an effect (placebo reform). Crucially, the assumption might only hold conditional on some covariates X. For example, local economic differences or personal characteristics of mothers might affect the trends differently. The inclusion of a rich set of covariates may therefore help to make the assumption more credible. For our analysis we use geographic information as well as personal characteristics like education or the employment history. If the unconditional mean differences drastically differ from an estimator with many included controls, this may at least be interpreted as a non-robustness against the chosen specification. In other words, if specifications with many control variables shift the results, it is very likely that some form of observed common trend confounding, that may or may not be fully adjusted for, takes place. Clearly, this argument does not rule out some form of common trend confounding, that is unrelated to the rich set of control variables included.

Assumption 2(Observational rule): The outcome process follows the observational rule Yt =    Y_t0 if Dt =0 Y_t1 if Dt =1.

Hence, we require that reform exposure of one mother does not affect the outcome of another mother. The assumption can be violated if being exposed to the reform has an impact on a colleague’s or a friend’s reemployment decision. While we cannot completely rule out this kind of peer effect, we argue that the narrow birth interval of four weeks for reform exposure makes the occurrence of peer effects very unlikely.7

Assumption 3(No anticipation):E Y₀1−Y₀0|D=1

=0.

This assumption requires that being exposed to the reform has no effect prior to the reform and thus rules out anticipation effects. It might be violated if mothers plan to give birth to their child in order to benefit from the new regime. This kind of anticipation can occur in two different forms. Firstly, women considering to become mothers could have tried to plan conception and secondly, they could have tried to postpone the birth shortly before the calculated birthdate. The first type of antici- pation is relevant for those mothers knowing about the reform before they are preg- nant. However, the German parliament approved the law only in November 2014. Hence, knowledge on the reform becoming definitely effective for births from July 2015 onwards was less than nine months before the cut-off date available when con- cerned mothers have already been pregnant. To rule out the possibility that mothers might have heard from the draft and waited for another few months, we analyzed

7_{Welteke and Wrohlich (2019) identify peer effects for mothers with births between a much longer}

4.4. Estimation strategy 69 FIGURE4.2: Birth numbers in 2014 and 2015

(a) Official birth numbers (b) Birth numbers from BeH

Source: Own calculations from BeH and the German Federal Statistical Office (2014a, 2015a).

monthly birth numbers from 2015 in comparison with the previous year. Both statis- tics from the German Federal Statistical Office and the imputed birth numbers from the Employment History (BeH) used in the subsequent analysis show a similar move- ment in 2014 and 2015 and one cannot detect any sudden increase in July 2015 (see Figure 4.2). We handle the second type of anticipation, trying to postpone the birth- date that might especially relevant for planned Caesarian sections, by dropping in- dividuals with births two weeks around the cut-off date. Obviously, the two weeks rule is arbitrary and we check the sensitivity against it in Section 4.6. Furthermore, the share of mothers wanting a Caesarian section is rather low in Germany (at max- imum two to three percent). The concrete definitions of the indicators D and T are summarized in Table 4.3.

Assumption 4(Common support): 0< p(X) <1 where p(X) =E[D|X].8

It follows that we exclude perfect predictability for belonging to group D = 0 or D= 1. For our estimation procedure we enforce support by dropping observations with no overlap.

TABLE4.3: Treatment definition

Cut-off 01/07/2015 Control group Treated group

T=0 mid May - mid June 2014 mid July - mid August 2014 T=1 mid May - mid June 2015 mid July - mid August 2015

Source: Own representation.