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Does Starting Universal Childcare Earlier Influence Children’s Skill Development?

Abstract

As many developed countries enact policies that allow children to begin universal childcare earlier, understanding how starting universal childcare earlier affects children’s cognitive and noncognitive skills is an important policy question. We provide comprehensive evidence on the multidimensional short- and longer-run effects of starting universal childcare earlier using a fuzzy discontinuity in the age at starting childcare in Germany. Combining rich survey and administrative data, we follow one cohort from age 6 to 15 and examine standardized cognitive test scores, noncognitive skill measures, and school track choice in a unified framework. Children who start universal childcare four months earlier around age 3 do not perform differently in terms of standardized cognitive test scores, measures of noncognitive skills, school track choice, or school entrance examinations. We also find no evidence of skill improvements for children with low socioeconomic status, although we provide suggestive evidence that they may benefit from high-quality care. Our estimates refer to children who start childcare before they become legally entitled, for whom the literature would predict low gains to starting childcare earlier. We provide further evidence on this relationship between parental resistance to and children’s potential gains from childcare. Simply allowing children to start universal childcare earlier is hence not sufficient to improve children’s skill development, particularly for children with low socioeconomic status.

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Notes

  1. 1.

    The literature distinguishes between targeted programs that focus only on certain (disadvantaged) groups and universal programs that do not base eligibility on a measure of disadvantage. See Bernal and Keane (2011), Ruhm and Waldfogel (2012), and Elango et al. (2016) for excellent reviews of the prior literature.

  2. 2.

    In contrast, a policy changing all children’s enrollment preserves children’s relative age. Isolating relative age effects in early childcare hence informs an additional policy question. Although doing so is not possible in our setting, Cascio and Schanzenbach (2016) investigate effects of relative age at kindergarten entry around age 5. They found that being relatively younger did not have a negative effect and that children appear to benefit from having older classmates.

  3. 3.

    The distinction follows Cascio’s (2015) framework to classify ECEC programs. Cascio first differentiated whether a universal program follows a preschool or a childcare orientation: preschool-oriented programs are typically delivered through the public school system with an explicit focus on promoting school readiness, and childcare-oriented programs focus more on providing childcare than on fostering skill development. Second, Cascio also distinguished whether children in the alternative care environment are mainly looked after by their mothers (or receive other types of informal care) or whether children attend another form of center-based childcare. For a comprehensive perspective on both preschool- and childcare-oriented programs, Table A1 in the online appendix concisely summarizes previous studies on the effects of universal childcare on children’s skills, focusing on studies that exploit some form of exogenous variation in universal childcare attendance.

  4. 4.

    Datta Gupta and Simonsen (2016) examined the effect of attending center-based care compared with family day care at age 2 and found positive effects on children’s grade point average in Danish language (+0.2 SD) at age 16. The effects are again larger for children from low-educated mothers and point to the importance of quality differences between the different care environments.

  5. 5.

    We focus on West Germany because of the large differences in early childcare attendance between East and West Germany (Kreyenfeld et al. 2001).

  6. 6.

    For more information on the administration and funding of the German childcare system, see the descriptions by Kreyenfeld et al. (2001) and Evers and Sachße (2002).

  7. 7.

    In 1998, only 1.9 childcare slots, on average, were available for 100 children below the age of 3, and the supply of such slots began to increase only after 2005 because of political reforms. In 2013, children became legally entitled to a slot from their first birthday onward.

  8. 8.

    As a case in point, the city of Offenbach offered 0.84 slots per child in 1998 and had trouble filling these slots (Frankfurter Allgemeine Zeitung (FAZ) 1998).

  9. 9.

    The legal texts are available at https://bage.de/service/links-zu-den-kita-gesetzen-der-einzelnen-bundeslaender/.

  10. 10.

    About 60% of parents completed the parental interview. Hence, we refer to the “full” and “parent” samples in the Results section, where we also provide evidence that our estimated treatment effects are not biased by selective nonresponse.

  11. 11.

    In our sample, 8% of parents did not answer this question, and importantly, this share does not differ significantly across birth months (with a p value above .2). Given that 90% of children already attend childcare by age 5 and that children can still start childcare at this age, not reporting a childcare starting age most likely indicates that the children did not attend at all. Unfortunately, the survey does not include a separate item for whether a child ever attended childcare.

  12. 12.

    Because the alternative form of care at that time was largely maternal care, children of nonnative parents would mainly be exposed to a foreign language in the counterfactual care situation. We are precisely interested in the treatment effect for this group, particularly in terms of language skills, and thus we prefer this linguistic definition of nativity.

  13. 13.

    In Table A2 in the online appendix, we show that starting childcare earlier does not affect the probability of attending grade 9 at age 15. Because the proportion of children retained is fairly constant between adjacent cohorts of children, it is reasonable to assume that the children from the July 1994–June 1995 cohort who repeated a grade would be of similar academic quality to the children from the July 1995–June 1996 cohort. Moreover, we control for cohort differences in ability and interact the running variable by cohort, thereby accounting for ability differences between cohorts. Thus, including children who repeated a grade should not bias our estimates.

  14. 14.

    The NEPS data-use regulations prohibit reporting results for single states, and we thus can show our first-stage relationship only if we combine data for two states. Given this constraint and the limited availability of such data, we combine the data on school entrance examinations from Schleswig-Holstein (the only West German state for which such data are available) with school census data from Bavaria (the largest state for which school census data are available).

  15. 15.

    We later show that our first-stage estimates also hold for these two states. To alleviate concerns about the comparability of samples resulting from differences in urbanicity, we also show that the first-stage estimates do not differ by urbanicity.

  16. 16.

    The scientific-use files contain only the quarter of birth. We negotiated access to month of birth, compromising on more-detailed migration characteristics. The scientific-use file contains the language spoken at home, children’s nationality, and country of birth. Our version includes an indicator whether any of these three characteristics were non-German.

  17. 17.

    Pediatricians assess children’s language based on children’s vocabulary, articulation, and hearing problems. Motor skills are assessed through different exercises, including jumping across a line, standing on one leg, and jumping on one leg. To assess behavioral problems, pediatricians make a clinical assessment based on the child’s behavior and parental information during the medical screening.

  18. 18.

    Because parents voluntarily provide the information, parental education is missing for about 40% of children.

  19. 19.

    Depending on the state, the school and childcare years start either in August or September. Without loss of generality, we focus on August as the starting point for ease of illustration.

  20. 20.

    Unfortunately, official figures on childcare starting age are not available. However, the Federal Ministry for Family Affairs, Senior Citizens, Women and Youth reported that on December 31, 1999, 50% of children aged 3, 82% of children aged 4, and 90% of children aged 5 were enrolled in childcare (BMFSFJ 2005). Assuming that these children started in August/September, their average starting age was 3.7 years, which closely compares to 3.4 years in our data.

  21. 21.

    Figure A3 in the online appendix illustrates these specific enrollment patterns. Panels b and c together imply that about 40% to 50% of children born between October and December start childcare before or on their third birthday. This share compares very similarly to the childcare attendance rates that Bauernschuster and Schlotter (2015: figure 3) reported. Using data from the SOEP on actual attendance, they showed that about 45% to 60% of children born between October and December attend childcare in the first spring after turning 3; these children therefore must have started childcare either before or shortly after turning 3, consistent with our findings both qualitatively and quantitatively. Unfortunately, the SOEP data do not provide information on the month and year when children started childcare.

  22. 22.

    In Germany, children start school at age 6, and the school entrance cutoff during the period of analysis was at the end of June (see Faust 2006). At that time, less than 3% of children started school earlier, and the share of children starting earlier is even lower in December and January (see Fig. A5, online appendix).

  23. 23.

    In section C of the online appendix, we report all main results for a smaller, three-month window from October to March. The results remain the same, although they are estimated less precisely.

  24. 24.

    For the effect of childcare starting age to be isolated from effects of age at testing, age at testing must vary within birth months and ideally overlap between birth months. These requirements are met in the NEPS tests and in the school entrance examinations because each test was administered to children at different dates; the NEPS tests were spread out over three months, and the school entrance examinations took place over five months. Figures A7 and A6 in the online appendix show the resulting variation in age at testing within and between birth months in both data sets. For a robustness check, we also used monthly dummy variables instead of linear age at testing; the results, available upon request, were the same.

  25. 25.

    Ideally, we would estimate the first stage separately for Bavaria and for Schleswig-Holstein. Unfortunately, as mentioned earlier, state-specific analyses are prohibited with the NEPS data, but we can combine at least two states for the analysis. Figure A8 (online appendix) presents the first stage using only observations from Bavaria and Schleswig-Holstein. Table A5 (online appendix) provides the corresponding regression coefficients.

  26. 26.

    For these regressions, we merge additional information on the population density from the German Federal Statistical Office to the NEPS data. We classify a district as rural if the population density (i.e., the population per square kilometer) is below the median of the population-weighted population density, which was 377.5 in 1997. We picked 1997 because this was the year that the cohort children began to enter childcare.

  27. 27.

    Most prominently, Buckles and Hungerman (2013) found seasonal differences in important observable characteristics, such as mothers’ age and education, in the United States. In contrast, Fan et al. (2017) concluded in their cross-country study that seasonality is not omnipresent and showed that seasonality effects for the United States vanished when they appropriately controlled for race.

  28. 28.

    Using information on week of birth yields almost identical reduced- form results, see Table A7 in the online appendix.

  29. 29.

    The first stage also does not differ by the presence of younger siblings, based on the number of children under age 14 in the household at the time of the first survey (results available upon request). As an alternative way to characterize the compliers, we follow Angrist and Pischke (2009) and recode our treatment variable into a binary indicator whether a child started childcare before the third birthday. The results reveal no clear pattern: most of the small differences across subgroups are not statistically significant (see Table A9, online appendix). We also calculate that 54.6% of children who attended childcare before their third birthday did so because they were born in the last quarter of the year. Hence, the compliers make up a substantial share of the children starting before age 3.

  30. 30.

    According to a power analysis at the 10% significance level, we can detect a reduced-form effect of 0.1 SD with a probability of 90%. The calculation uses the STATA command power oneslope, specifying the number of observations (N = 9,100), the conditional standard deviation of the before dummy variable (sdx = 0.244), and the conditional standard deviation of the language test score (sdy = 0.801). We thank one referee for pointing out an inconsistency in our previous power analysis.

  31. 31.

    Figure A10 and Table A10 in the online appendix show the same patterns when we include only children from the parent sample. Because of the smaller sample size, the graphical patterns are noisier, and the estimates are less precise. However, the consistent results between both samples mitigate concerns about combining the first-stage results from the smaller parent sample with the reduced-form results for the full sample. Further, we reach the same conclusions when we replace the linear control function with a quadratic one (see Table A11, online appendix).

  32. 32.

    We focus on the reduced-form effects for two reasons. First, the Wald estimates are less precise, as indicated by the standard errors in Table 3. Second, the Wald estimates give the average marginal effect over the compliers’ changes in childcare starting age. Because the underlying relationship between children’s skills and their childcare starting age is potentially nonlinear, the effect should not be extrapolated to different changes in childcare starting age. Therefore, scaling up the effect does not help in interpreting the results.

  33. 33.

    For the graphical analysis, see Fig. A11 (online appendix). The January dip is mostly driven by children of Turkish mothers. When we remove Turkish children (N = 399) from the sample, the treatment effects become small and statistically insignificant.

  34. 34.

    Because we observe only children who attend grade 9, children born between July 1994 and June 1995 have either started school late or repeated a grade. Hence, they tend to have lower academic skills and a lower probability of attending Gymnasium compared with children in the same grade but born between July 1995 and June 1996.

  35. 35.

    Because the data do not include additional information, we cannot control for additional child and parent characteristics. However, as Tables 2 and 3 show, our results from the NEPS do not depend on including additional control variables.

  36. 36.

    Examples of partial fading-out include the Perry Pre-School trial, in which the initial IQ gains vanished by age 10. However, no fade out occurred for noncognitive skills: children still performed better in achievement tests later because of higher noncognitive skills (Heckman et al. 2013).

  37. 37.

    For this calculation, we assume that children born in December attend childcare five months longer than children born in January and that they attend childcare for five days per week and four hours per day. The additional time spent in childcare then is 430 hours. Even if children missed out on one month (e.g., because of illness and/or holidays), we would arrive at 344 hours, which can be considered a lower bound.

  38. 38.

    For instance, Ichino et al. (forthcoming) showed that for a mixture of full- and part-time attendance, one additional month significantly reduces cognitive skills. Four hundred hours, as in our setting, correspond to 2.5 months of full-time attendance. Furthermore, high-quality preschool programs of similar intensity haven been found to substantially affect children’s skill development (e.g., the Tulsa program; see Gormley and Gayer 2005), as have targeted programs (e.g., Head Start; see Garces et al. 2002). Additionally, Felfe and Zierow (2018) found that switching from half-day to full-day universal programs in Germany increased socioemotional problems by 0.18 SD. Because only 10% of the children in their sample responded to the increased access to full-day slots and full-day slots provide roughly 16 additional hours of care per week, their reduced-form estimates compare children whose average childcare attendance differed by at most 220 hours.

  39. 39.

    The quality of formal childcare ultimately depends on the quality of interactions between children and staff. The child-to-staff ratio determines the types of interactions that are feasible and often serves as one indicator of “structural” childcare quality (e.g., Blau and Hagy 1998; Hofferth and Wissoker 1992). Furthermore, Rege et al. (2018) showed that the child-to-staff ratio explains roughly 30% of the variance in school readiness between childcare centers. Because we are not estimating the causal effect of quality or the child-to-staff ratio but we inspect effect heterogeneities along this dimension, such a proxy should suffice as an indicator of care quality. To compute the ratio, we use administrative data from the German Federal Statistical Office at the district level on (1) the number of formal childcare spots for children aged 3–6 and (2) the number of employed personnel (measured on December 31, 1998).

  40. 40.

    The data sets covering the outcomes at age 15 measure the location only at the time of data collection but do not include information on earlier locations. Even short-distance moves across districts between attending childcare and age 15 would hence introduce measurement error in assigning the district of attendance.

  41. 41.

    According to the regulatory standards, the typical ratio should be close to 11 (Verordnung für Kindertageseinrichtungen Schleswig-Holstein). Local decision-makers can implement lower ratios—say, for political reasons to attract parents who value higher quality. Moreover, the regulations do not state specific sanctions if the ratio is too high, and closures of childcare facilities seem politically infeasible because they would likely deny children access to childcare and/or negatively affect other facilities. This absence of a clear sanctioning mechanism may explain higher child-to-staff ratios in other districts.

  42. 42.

    To support this econometrically, we follow Heckman et al. (2006) and calculate the different weights of observations in an instrumental variable estimation. Because the approach requires a binary treatment, we recode our treatment variable to an indicator whether a child started childcare before the third birthday. Hence, we obtain the weights that our instrument assigns to children with different propensities to start childcare before the third birthday. Figure A15 in the online appendix shows that our instrument puts the most weight on individuals with a low resistance toward childcare and hardly any weight on children with a medium to high resistance to childcare.

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Acknowledgments

We are grateful for helpful comments and suggestions received from four referees; Anna Adamecz-Völgyi, Stefan Bauernschuster, Jan Bietenbeck, Christian Dustmann, David Figlio, Jonathan Guryon, James J. Heckman, Mathias Huebener, Chris Karbownik, Patrick Puhani, Regina T. Riphahn, Claus Schnabel, Stefanie Schurer, Steven Stillman, Konstantinos Tatsiramos, and Rudolph Winter-Ebmer; from participants at the 2015 summer school of the DFG Priority Program 1764, the 2016 Ce2 workshop in Warsaw, the 2016 NEPS User Conference, the 1st IZA workshop on Gender and Family Economics, the 3rd network workshop of the DFG Priority Program 1764, the 2017 Essen Health and Labour Conference, the 2017 annual meeting of the Society of Labor Economics, and the 2017 annual meeting of the European Society of Population Economics; and seminar participants at the Northwestern Applied Micro Reading Group, Bayreuth University, Ludwig-Maximilians-Universität Munich, Lüneburg University, and RWI (Essen). This paper uses data from the National Educational Panel Study (NEPS): Starting Cohort 4–9th Grade, doi: https://doi.org/10.5157/NEPS:SC4:4.0.0. From 2008 to 2013, NEPS data were collected as part of the Framework Programme for the Promotion of Empirical Educational Research funded by the German Federal Ministry of Education and Research (BMBF). As of 2014, the NEPS survey is carried out by the Leibniz Institute for Educational Trajectories (LIfBi) at the University of Bamberg in cooperation with a nationwide network. We thank the Ministry of Social Affairs, Health, Science and Equality of Schleswig Holstein, and Ute Thyen and Sabine Brehm specifically, for granting access to and providing valuable information on the school entrance examinations. Daniel Kuehnle acknowledges financial support by the DFG (grant number RI 856/7-1).

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Kuehnle, D., Oberfichtner, M. Does Starting Universal Childcare Earlier Influence Children’s Skill Development?. Demography (2020). https://doi.org/10.1007/s13524-019-00836-9

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Keywords

  • Universal childcare
  • Child development
  • Skill formation
  • Cognitive skills
  • Noncognitive skills