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Parental leave benefit and differential fertility responses: evidence from a German reform


This paper examines the causal effects of a major change in the German parental leave benefit scheme on fertility. I use the unanticipated reform of 2007 to assess how a move from a means tested to an earnings-related benefit affects higher-order births. By using data from the Mikrozensus, I find that the reform significantly affected the timing of higher-order births in the first 5 years after a last birth. Overall, mothers “just” eligible for the new benefit for the current birth initially reduce subsequent childbearing and extend birth spacing, compared to mothers “just” ineligible. However, by the end of the third year, mothers start to compensate for the earlier losses. The negative effects are largely driven by the low-income mothers, who are now worse-off and do not display any catch-up effects. The differential fertility responses along the income distribution are in line with the heterogeneous structure of the economic incentives.

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  1. Gauthier (2007) describes family policies as “policies directly targeted at families with children such as direct and indirect cash transfers for families with children, means-tested child welfare benefits, maternity and parental leave benefits, and childcare facilities and related subsidy programs”. Aside these measures, many other policy types such as labor market, monetary and fiscal, education, and social security policies may also affect fertility.

  2. For comparison, at the same time, the relation of GDP and public spending on active labor market programs or unemployment remained constant at the level of 0.5 and 1.1 %, respectively (OECD 2013).

  3. While several studies identify fertility effects of taxation schemes (e.g., Milligan (2005), Azmat and González (2010), and Laroque and Salanié (2013)) or direct per-child cash transfers (e.g., Brewer et al. (2011), González (2013), and Cohen et al. (2013)), causal evidence from parental leave reforms is scarce (e.g., Lalive and Zweimüller 2009).

  4. Demographic research largely attributes the low fertility rate in Germany to a high incidence of childlessness, rather than to insufficient progression rates to higher parities (e.g., Sobotka2011).

  5. The age limit for earlier children was 18 years and 27 years for dependents in education. The means-testing was slightly less rigorous for single parents. Generally, the thresholds referred to annual joint family income from the calender year before the childbirth for benefits in months 1–12 and the year of the childbirth for benefits in months 13–24. In practice, often solely the father’s income was relevant because the income of the leave-taking parent, i.e., usually of the mother, was omitted as long as she did not work during leave-taking. Although the income definition was not derived from tax law, it was comparable to net annual income (BMFSFJ 2005).

  6. The Appendix is available online as Electronic Supplementary Material.

  7. See, e.g., Neugart and Ohlsson (2013) and Kluve and Tamm (2013) for a more detailed description of the core legislative changes and their effect on various socioeconomic groups.

  8. Along the distribution of household income, the proportion of “winners” increases from 42 % in the lowest quartile to 88 % in the highest quartile (Büchner et al. 2006).

  9. Nevertheless, in my empirical analysis, I tested whether first-time and higher-order mothers respond differently. I found that there are no substantial and statistically significant birth order differences in the current child effects.

  10. The “sibling premium” is granted to leave-taking parents with earlier children as long as at least one earlier child is less than 3 years old or at least two children are both less than 6 years old (BMFSFJ 2011).

  11. I borrow the term “speed premium” from previous literature on a similar feature of the Swedish system (e.g., Neyer and Andersson 2008).

  12. Figure A.1 in the online Appendix exemplifies the rather complex mechanism for a first-time mother with average pre-birth earnings of 1250 euros who desires a second child.

  13. Extensive literature discusses the underdeveloped childcare system in Germany and its adverse consequences for maternal labor force participation (e.g., Wrohlich (2008), Hanel and Riphahn (2012), and Bauernschuster et al. (2014)). The studies document a scarce availability of childcare arrangements for infants, the inflexible opening hours, and predominantly part-time manner. Since August 2013, parents have a legal claim to a subsidized daycare slot for children aged 1 year and above. However, authorities and parents still face considerable excess demand for affordable and high-quality childcare that is particularly pronounced in West German states.

  14. For example, in 2010, about 70 % of mothers whose youngest child was less than 3 years old did not work, 23 % worked part-time, and 7 % full-time (Keller and Haustein 2012).

  15. In a descriptive study for Pomerania (a region in North-East Germany), Thyrian et al. (2010) compare aggregate monthly birth rates up to 23 months before and after January 1, 2007. They do not find any significant differences.

  16. Compared to the old system, several mechanisms may drive a faster (re-)entry among the poorer mothers. For example, parents might want to compensate for the sudden benefit drop after the shorter 1-year eligibility. Parents who applied for the optional spreading over 2 years might want to compensate for the less generous benefit because the monthly amount halves. Finally, the reform abolished a work disincentive in the second year, as the old system deducted any labor earnings from the benefit amount (Bergemann and Riphahn 2011a).

  17. Dustmann and Schönberg (2012) use a similar strategy to evaluate expansions in maternity leave duration on children long-term outcomes.

  18. The monthly state-level unemployment rates are from the Federal Employment Agency and the annual state-level childcare and earnings data from the Federal Statistical Office. I calculate public childcare coverage ratio for children less than 3 years old as the number of slots over the respective population of children. The aggregate earnings indicator corresponds to the average annual gross earnings of an employee measured in 1000 euros.

  19. More precisely, Tamm (2012) estimates that 7.8 % and Neugart and Ohlsson (2013) that 5.4 % of births scheduled for the last week of December 2006 were shifted to the first week of January 2007. While Neugart and Ohlsson (2013) emphasize the biological impossibility to postpone birth by more than a few days, Tamm (2012) argues that some deliveries could have been moved by more than 1 week. There is no evidence for shifts in the opposite direction, i.e., speeding-up birth (e.g., by inducement or elective cesarean). Not surprisingly, birth postponement occurred only among mothers who were more likely to gain from the reform.

  20. Specifically, they identify the current child effect by comparing mothers who gave birth 1 month before and 1 month after a reform. Obviously, such approach assumes the absence of any month-specific effects. In contrast, my empirical design captures any seasonal effects in δ, though by using comparisons around a cut-off date, I identify the current child effect essentially in a similar way. To estimate the future child effect, Lalive and Zweimüller (2009) compare mothers who gave birth one month before a policy change and in exactly the same month but three years earlier. The validity of causal inferences rests here on the strong assumption that there are no cohort or year-specific influences that might otherwise explain changes in fertility over a 3-year period.

  21. The indicator for the year 2002/3 may capture the future child effect already in my estimation of probability of having a next child within the first 57 months because women who gave birth in October 2002 might have known about the reform in the middle of 2006. If they immediately changed their higher-order fertility plans, these changes would occur by the end of the first quarter of 2007, i.e., around month 54 after a previous birth. Although such exact timing of births is difficult, the probability of potential anticipation effects increases thereafter.

  22. This information is not available in the scientific use files, thus I use a controlled remote access to the data.

  23. Previous literature emphasizes substantial differences in fertility dynamics, attitudes towards maternal employment, women’s labor market attachment, and subsidized childcare infrastructure (e.g., Goldstein and Kreyenfeld (2011), Hanel and Riphahn (2012), and Wrohlich (2008))

  24. The Mikrozensus 2012 reports the actual number of births, i.e., biological children. This number and the number of children living in a mother’s household are identical for 96 percent of sampled mothers from the wave 2012. Therefore, a potential measurement error is virtually negligible.

  25. The distribution of interviews is random over the entire year. Therefore, if a mother’s interview takes place early in year (e.g., in January), a child born later in the same year is not yet observed in the data.

  26. I was unable to link about 15 % of children to their fathers because they don’t live in the child’s household at the time of interview. I always use a dummy for missing father in regressions that include paternal characteristics.

  27. Specifically, the largest sample used in the analysis for months 12–21 consists of 47,211 mothers who give 52,423 observations. Consequently, I lose 10 % of sample size if I keep only one observation per women. This proportion reduces to 7 % in the smallest sample for months 46–57.

  28. I find similar seasonal patterns for the remaining outcome measures and for the post-reform years.

  29. For illustration, Panel B describes the explanatory variables in my largest sample for months 12–21. The statistics generally suggest that the treated and control groups are comparable with respect to observable characteristics.

  30. Table 1 reports regression results for selected outcome measures because I am not able to present here estimates for all 46 indicators that I use as dependent variables to investigate the entire period from month 12 through 57. The selection of months is related to the design of my sample, which I describe in Section 4.

  31. Because of censoring, the OLS regressions might underestimate the reform effects on birth spacing in columns 9 and 10. I re-run these estimations by using Tobit models, which indeed yielded slightly larger marginal effects.

  32. Save for Panel C, the splitting variables include a separate category for a missing value. Although interacted with the reform indicator and included throughout, the results for these categories are not reported due to serious limitations with their interpretation. Obviously, the missing values could be problematic if their incidence was related to the reform. However, I could exclude such possibility for all regressions reported in Table 2 by regressing the indicators for missing values on the reform indicator (within a framework similar to Eq. 1).

  33. These regressions control for the same set of variables as in Table 1. Given that the reform indicator corresponds to an interaction term between the indicators for first quarter of year and the reform year 2006/2007, each regression in Table 2 additionally includes their interaction terms with the variable defining subgroups.

  34. In Germany, employment with net monthly earnings up to 800 euros is labeled as a “midi job” and qualifies for some wage subsidies. However, more widespread and generously subsidized are “mini jobs” if monthly earnings do not exceed 400 euros. In 2013, the thresholds increased to 850 and 450 euros, respectively.

  35. Again, the effects are a sum of the respective coefficients for the interaction terms to the effects in the first row.

  36. The overall reform effects for later months (columns 7, 8, and 10 of Table 1) are already very imprecise and the result remains unchanged in virtually all performed sensitivity tests.

  37. Nevertheless, given that delaying birth is biologically difficult, I acknowledge that generally, we cannot ignore the shifting and its potentially adverse health consequences for mothers and children.


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I gratefully acknowledge the helpful comments and suggestions from the Editor and two anonymous referees. This paper benefited greatly from the valuable advice provided by Regina T. Riphahn and Guido Heineck. I also thank Barbara Broadway, John Haisken-DeNew, Guyonne Kalb, Yvette Khalil, Sonja Kassenboehmer, Daniel Khnle, Miriam Maeder, Marcel Thum, Michael Zibrowius, and the participants of several seminars for their insightful comments. My special thanks go to the Research Data Centre of the German Federal Statistical Office for the remote data access, in particular to Melanie Scheller for her support in handling the data.

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Correspondence to Kamila Cygan-Rehm.

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Cygan-Rehm, K. Parental leave benefit and differential fertility responses: evidence from a German reform. J Popul Econ 29, 73–103 (2016).

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  • Fertility
  • Family policy
  • Reform
  • Parental leave
  • Elterngeld
  • Germany

JEL Classification

  • J13
  • J18
  • J20
  • K36