STUDY 1: NEW AND EXPECTING PARENTS The Estonian parental leave reform is exceptional in that it did not include changes to any other entitlements besides the fathers’ leave extension, allowing us to isolate its effect (see Dataverse Appendix [DA] 5 for details of the reform and Estonian leave policy). In addition to this design strength, Estonia is also a case with features that generalize: prior to the reform, attitudinal support for gender equality in Estonia was close to the European Union average,Footnote 2 and its generous maternity versus scant paternity leave reflected the reality in most developed democracies where parental leave policies still overwhelmingly treat women as the main carers of young children.Footnote 3 Like many OECD democracies, Estonia additionally offered shared parental leave. However, as in other countries, this leave is disproportionately taken by women. We pair this policy discontinuity with an original survey of new and expecting parents to measure their attitudinal support for gender equality. Our study was fielded with the help of the Estonian survey firm Kantar Emor, preregistered (see DA4 for the pre-analysis plan) and approved by the Institutional Review Board. The control group (N = 614)—new and expecting parents whose children were (due to be) born up to 6 months before the reform—were interviewed from January to June 2020. The treatment group (N = 748)—parents whose children were (due to be) born up to 6 months after the reform—were interviewed from July to December 2020. Our final sample consists of 1,362 new parents, which amounts to interviewing at least one parent of about 10% of all children born in Estonia in 2020, and has a good gender balance (750 new mothers and 612 new fathers). Achieving this remarkable sample required considerable effort and resources given that our target population was very specialized, hard to reach, and challenging to recruit. The survey firm recruited subjects from their own subject pool and from the general population by advertising the study in outlets targeted to new and expecting parents, using the snowball method, and offering incentives. We discuss the recruitment process in Section SM1 of the Supplementary Material and present information on the demographic characteristics of respondents in Section SM2 of the Supplementary Material. The research design enables us to evaluate the overall attitudinal effects of the policy among new parents based on eligibility and irrespective of uptake by comparing the attitudes of parents in the treatment group (i.e., eligible to benefit from the reform) to those in the control group (i.e., not eligible to benefit). This is important because uptake confounds the effect of the policy with the effect of selecting into the extended fathers’ leave, which would cause us to overestimate the overall attitudinal effects of the policy. Our approach is similar to a regression discontinuity design with a discrete running variable—birth month—and cutoff in July, which relies on the assumption that parents did not plan pregnancies strategically to benefit from the new policy. Since the policy change was initially adopted in December 2017, with final implementation announced in June 2019, strategic pregnancy planning was in principle possible and would be evidenced by depressed birth rates before the July 1, 2020 cutoff date, and inflated birth rates thereafter. Analyzing monthly birth rates in 2020, we are unable to detect such a pattern (Figure SM2.1 in Section SM2 of the Supplementary Material). The difference in the number of births between June (1,211) and July (1,287) is not sizable or statistically significant and the monthly birth rates are similar in the first and second half of the year. Additional comparisons to birth records from 2010 to 2020 also reveal no evidence of strategic pregnancy planning (see Section SM2 of the Supplementary Material for more details). Balance tests (see Section SM2 of the Supplementary Material) show some imbalances in sociodemographic and other background characteristics across treated and control parents in our sample. Our estimation strategy accounts for these imbalances in two ways. First, our main model specification includes all our sociodemographic covariates as control variables. This approach eliminates any potentially concerning linear relationships between treatment assignment and the covariates (Gerber and Green Reference Gerber and Green2012). Second, we employ a Lasso-based post-double-selection method to account for more complex, nonlinear ways in which our covariates might affect treatment assignment (Belloni, Chernozhukov, and Hansen Reference Belloni, Chernozhukov and Hansen2014). Section SM3 of the Supplementary Material additionally reports models without any covariate adjustment. We start by testing new parents’ awareness of the reform, which is a precondition for any effects that the reform may have on attitudes toward gender equality. Three questions served as our manipulation checks (sequenced before the gender equality items). These asked respondents how many days of paid fathers’ leave (i) they thought a father was currently entitled to take (Entitlement), (ii) they thought an average new father would take (Average use), and (iii) how much paid parental leave they were planning on taking with their new baby (Uptake). Table 1 presents the mean responses of new parents in the control and treatment groups with t-tests and confirms that the reform had the expected effect on beliefs and anticipated behaviors (see Section SM3 of the Supplementary Material for additional robustness checks): Post-reform respondents correctly identified that men were entitled to more fathers’ leave, expected an average new father to take significantly more paid fathers’ leave, and post-reform fathers (but not mothers) were planning on taking significantly longer paid leave (11.5 days more) than their peers pre-reform, suggesting high awareness of the reform. Our outcome questions measure gender bias in subjects’ descriptive and prescriptive attitudes toward women and their role in society and politics. The full list of items measuring different aspects of this concept, which is latent in nature, is available in DA1. Existing literature offers no single, universally accepted set of measures of gender equal attitudes and studies use different items depending on their context and focus. We rely on measures that have been shown to capture gender bias in the World Values Study and on prior work conducted in Estonia (Pérez and Tavits Reference Pérez and Tavits2019; Reference Pérez and Tavits2022), and that yield meaningful variation in our research context (see Section SM1 of the Supplementary Material). Our measures assess attitudinal gender bias in (a) the social and economic sphere (two items, e.g., agreement/disagreement that “a preschool child is likely to suffer if his or her mother works”), (b) the political sphere (three items, e.g., agreement/disagreement that “men make better political leaders than women do”), and (c) support for pro-female positive action policies to increase the representation of women in political leadership roles (two items, e.g., agreement/disagreement with requiring “political parties to reserve some space on their lists of candidates for women, even if they have to exclude some men”). To minimize measurement error, we combine responses to individual survey items in each of these three categories into scales using the first component of a principal component analysis. Note that the first two outcomes measure attitudes toward gender parity and make no connection between women’s and men’s prospects in society. In contrast, the last outcome captures support for pro-female interventions that potentially displace men—a subtle but potentially relevant difference. We run OLS models with Fathers’ Leave Reform as the treatment indicator (coded “1” for the parents whose child was born on or after July 1, 2020, “0” otherwise). Choosing a bandwidth of monthly data pre- and post-reform to include in the analysis poses a tradeoff between bias and sample size. Including fewer months strengthens the identification assumption and minimizes bias; including more months maximizes sample size with the associated advantages. We balance these concerns by using 3 months of data pre- and post-reform in our main analysis (see Section SM3 of the Supplementary Material for analyses using all other possible bandwidths). Figure 1 presents the results of our analysis examining whether the fathers’ leave reform affects attitudinal gender bias and support for positive action among new parents. Starting with the Socio-Economic Equality Scale at the top, we see that the reform significantly increases attitudinal support for gender equality in the social and economic spheres ( $ p=0.01 $ for both specifications). Our scales have a standard deviation of 1, meaning that estimates of 0.21 and 0.20 are sizeable—approximately 20% of a standard deviation. To put this treatment effect in context, the reform affects gender-equal attitudes as much as respondents’ gender. This treatment effect is notable but not unrealistic for a real-world social policy intervention with significant implications for life choices, earnings, and time use. Other work demonstrates similarly large effects of an educational intervention that engaged adolescents in discussions about gender equality (Dhar, Jain, and Jayachandran Reference Dhar, Jain and Jayachandran2022). The second set of estimates in Figure 1 indicates that this effect also applies to preferences about women in politics. Our Political Equality Scale shows positive treatment effects that are similar in magnitude to the Socio-Economic Equality Scale: 16% and 17% of a standard deviation ( $ p=0.06 $ and $ p=0.04 $ , respectively). Substantively, new parents who were eligible to benefit from the reform were significantly more supportive of women’s engagement in the traditionally male-dominated domain of politics. The estimates at the bottom of Figure 1 focus on our Positive Action Policies Scale and indicate that the reform had no equivalent positive effect on support for policies to increase women’s representation in political leadership positions at the expense of men. Although the estimates are positive, the effect sizes are smaller than for the items discussed above—only about 7% of a standard deviation—and do not reach conventional levels of statistical significance. This null finding adds important nuance to the understanding of attitudinal support for gender equality. Jointly, these results suggest that direct exposure to the reform that disrupted traditional gender roles encouraged more gender-equal attitudes, but not support for action to promote women at the expense of men, a subtle but consequential difference. In Section SM3 of the Supplementary Material, we present additional analyses that further substantiate our argument and results, including a placebo test in which we employ two hypothetical policy reform dates (April 1, 2020 and October 1, 2020) instead of the true date (July 1, 2020). As expected, we find null effects across both placebo tests. Note that the first placebo test also addresses—and helps to refute—any concerns about the potential impact of any COVID-19-related restrictions to hospital access for new fathers in the spring of 2020.
SUBGROUP HETEROGENEITY: MOTHERS VERSUS FATHERS Next, we examine whether mothers and fathers responded differently to the reform. By giving fathers the choice to expand their caring role, the reform challenged both parents to conceive of their own and their partner’s care-giving role in a less traditional fashion. Nonetheless, mothers’ and fathers’ responses to the reform may diverge for several reasons: their perceptions of the scope, acceptability, and suitable remedies for gender inequality may differ. The reform also affected fathers’ choices directly and mothers only via those of their partners. Figure 2 presents the results of the analysis split by sex and reveals interesting similarities, but also some differences. Across mothers and fathers the reform increases attitudinal support for gender equality on the Socio-Economic Equality Scale (0.26 and 0.24 for mothers vs. 0.18 and 0.16 for fathers), and on the Political Equality Scale (0.16 and 0.14 for mothers vs. 0.17 and 0.18 for fathers). On neither scale are the differences between mothers and fathers statistically significant (see Table SM3.6 in Section SM3 of the Supplementary Material for interaction models). Note that the point estimates are close to those in our main analysis, but less precisely estimated, which is not surprising given that splitting our sample by sex halves the sample size and reduces statistical power. However, striking differences arise on the Positive Action Policies Scale. Among mothers, the reform’s effect on support for such policies is positive, very large (26% and 27% of a standard deviation), and statistically significant. Among fathers we find no such increase in support for positive action. In fact, the effects are negative but small (−0.05 and−0.08) and fail to reach statistical significance. The interaction models in Table SM3.6 in Section SM3 of the Supplementary Material confirm that these differences between the sexes are statistically significant. In sum, while both groups respond to the change in social roles promoted by the fathers’ leave reform by expressing more gender equal attitudes, support for positive action to bring it about rises only among women. This finding calls for further research into better understanding the differences between women and men in their attitudinal support for various dimensions of gender equality. Disrupting traditional gender roles may not be sufficient to increase men’s support for positive action. This could be because of differences in the perceived cost: after all, positive action implies the promotion of women at the expense of men. We perform additional sub-group analyses by comparing (i) expecting parents to parents after they had their baby (Table SM3.13 in Section SM3 of the Supplementary Material), and (ii) first-time parents to experienced parents, who already had at least one prior child (Table SM3.14 in Section SM3 of the Supplementary Material). These additional analyses do not reveal significant sub-group heterogeneity in responses to the treatment.
STUDY 2: GENERAL PUBLIC In a separate Study 2, we examine the effect of indirect (as opposed to direct) exposure to the reform. While Study 1 shows that the reform affects the attitudes of new parents, who could benefit personally by choosing less traditional social roles, it may also affect attitudes among the general public through informational, indirect exposure. Study 2, conducted before the reform, employs a survey experiment on a representative sample of the general public. Respondents in the control group were told about the preexisting leave policy, whereas the treatment group received information about the reform’s extension of fathers’ leave (full treatment wording available in Section SM4 of the Supplementary Material, outcome measures replicate those in Study 1). Like Study 1, Study 2 was preregistered (see DA4) and approved by the IRB. The theoretical expectations about the effect on the general public are less clear. On the one hand, information about the reform might signal a social norm change regarding gender roles, prompting the general public to update their gender attitudes accordingly (Tankard and Paluck Reference Tankard and Paluck2017). On the other hand, indirect and informational exposure may be less effective (compared to new parents’ direct exposure to nontraditional gender role choices) in changing attitudinal gender biases, which tend to be resilient. Figure 3 presents the main results of Study 2. It shows that the treatment, which passively exposed individuals to information about the extension of paternity leave, and altered respondents’ perceptions of fathers’ leave entitlement (see manipulation check in Table SM4.3 in Section SM4 of the Supplementary Material), had no effect on gender-equality attitudes. A full description of the study and additional analyses are available in Section SM4 of the Supplementary Material. Taken together, our two studies, which contrast direct with indirect, informational exposure to the same policy change, demonstrate that informational exposure is clearly a less effective means for increasing attitudinal support for gender equality. A policy intervention can produce attitudinal change among the target population whose life choices it alters, but may not have the same effect among the general public, who are only passively and informationally exposed to the reform. This is an interesting result that invites further research. For instance, future work might investigate whether repeated and sustained informational exposure to nontraditional gender roles can change attitudes, which our finding does not rule out.