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Pseudo-Panel Event Studies: Econometric Foundations for Credible Applications
\maketitle
\begin{abstract}
Event studies with panel data are widely used to estimate treatment effects. With repeated cross-sections, future treatment dates are unobserved for untreated individuals. Pseudo-panel event studies impute pre-treatment outcomes of the treated using matched untreated individuals. This paper establishes identification in such designs and characterizes bias when identification conditions fail. I show that the pseudo-panel regression is equivalent to weighted least squares with group means. This representation simplifies computation and yields analytical inference. In simulations, analytical confidence intervals attain near-nominal coverage, whereas conventional intervals substantially undercover. I also develop a doubly robust estimator using richer covariates, a symmetric matching design with synthetic type fixed effects, and a fully nonparametric estimator that accommodates heterogeneous treatment effects. In a Korean panel survey, the pseudo-panel regression yields an employment child penalty of 42.1\%, close to 46.9\% in the actual panel. Applications to repeated cross-sections yield employment penalties of about one-third.
\end{abstract}
\noindent{\it Keywords:} pseudo-panel, event study, repeated cross-section, child penalty, doubly robust estimation.
\newpage
\section{Introduction}
The labor-market impact of having a child is typically estimated by comparing outcomes before and after childbirth. For instance, using Danish administrative data and an event study, \citet*{kleven2019children} estimate sharp and persistent ``child penalties'' in earnings, employment, and hours worked. \citet{kleven2019cross} apply the same approach and find similar patterns across six countries. However, panel data that follow individuals long enough to estimate child penalties are rare. In many settings, researchers have access only to repeated cross-sections, where different individuals are sampled in each wave. In such data, a childless respondent's future birth date (and hence their negative event time) is never observed. To overcome this limitation, \cite{kleven2025child} and \citet*{kleven2025atlas} develop a pseudo-panel event study design that imputes pre-birth outcomes of parents from observed outcomes of childless individuals matched on age, survey year, and discrete characteristics, under the assumption that the childless provide a valid comparison for parents. The design is attractive because it makes event studies possible with repeated cross-sections, which are widely available and typically have much larger samples than panels.\footnote{The approach builds on the classic pseudo-panel method of \cite{deaton1985panel}, who proposed tracking cohort means through repeated cross-sectional surveys. \cite{verbeek1992can}, \cite{moffitt1993identification}, and \cite{mckenzie2004asymptotic} develop identification and asymptotic theory for cohort-based pseudo-panels.}
This paper develops an econometric framework for pseudo-panel event studies. I establish identification in such designs under conditions that ensure matched childless individuals serve as a valid control group for parents, and characterize the bias when these conditions fail. I then show that the pseudo-panel regression is equivalent to a weighted least squares (WLS) regression with group means, and use this representation to derive its analytical variance. I also extend the design in three directions: (i) a doubly robust estimator that admits richer covariates in pre-birth outcome imputation; (ii) symmetric matching with synthetic type fixed effects (FE); and (iii) a fully nonparametric estimator that accommodates heterogeneous treatment effects.
The design has become popular in applied research. \cite{zhou2022rising} estimate the rising child penalty in China and \cite{huang2025china} investigate the association between the penalty and declining fertility. \cite{marchionni2025last} find persistent earnings losses after childbirth in Latin America and \cite{nguyen2026vietnam} in Vietnam. \cite{jessen2025child} apply the approach to a single cross-section and document larger cognitive skill losses for women after childbirth. Beyond childbirth, \cite{wu2025marriage} finds that both men and women in China become more supportive of traditional gender roles after marriage. In policy research, \cite{bussolo2024marriage} estimate marriage and child penalties in South Asia, and \cite{baez2026motherhood} document a lasting decline in mothers' labor force participation after childbirth in Turkey. More generally, the framework applies to cross-sectional data in which treatment dates are observed only for treated individuals.
A pseudo-panel is constructed by matching parents observed at birth to childless individuals (donors). The donor pool is a mixture of future parents and people who will never have a child. If these groups differ in unobserved determinants of the outcome, the imputed pre-birth outcome can be biased. I establish identification of the average treatment effect on the treated (ATT) in a potential-outcomes framework under no anticipation, parallel trends, and comparability between parents and childless donors conditional on the matching characteristics, and derive the bias when that comparability condition fails. This bias cancels in the gender difference only if it is the same for women and men. I also clarify the additional restrictions on untreated outcomes and treatment-effect heterogeneity needed to interpret the resulting regression coefficients as causal effects.
I then show that the ordinary least squares (OLS) regression using the pseudo-panel yields the same coefficients as WLS using mean outcomes within cells defined by discrete matching variables. I use this equivalence to derive the estimator's probability limit and asymptotic variance. A donor can supply several imputed outcomes, and an individual can appear in different years as both donor and parent. Conventional inference using heteroskedasticity-robust standard errors ignores this dependence because it treats the imputed pre-birth outcomes as independent observations. The analytical variance I derive accounts for this dependence, along with sampling variation in cell weights. Under regularity conditions, the approach applies to the baseline estimator and all three extensions. Using cell means also reduces regression time in large samples.
The original design matches on discrete variables, so continuous covariates must be discretized. Matching on many variables or variables with many categories can produce sparse or empty cells. I use a doubly robust (DR) estimator to impute the pre-birth cell means that enter the pseudo-panel regression. It combines an outcome model estimated on the donor sample with inverse-probability weights from a propensity score model for group membership. When parents and donors are comparable conditional on the richer covariates and overlap holds, the estimator consistently estimates these cell means if either model is correctly specified. With both models correctly specified, the estimator is semiparametrically efficient for the imputed mean when the parent and donor samples are independent.
I also consider an alternative symmetric pseudo-panel construction that matches parents observed at birth both backward to donors and forward to parents of the same observed type, defined by gender, first-birth year, age at first birth and matching characteristics. In the baseline design, post-birth outcomes come from whichever parents appear at each event time, so the composition of parents can change over event time. This symmetric matching extension, developed from the idea in \cite{kleven2025child}, weights each type at each event time by the number of parents within the type observed at birth. I include synthetic type fixed effects to absorb persistent differences in untreated outcome levels and state the additional identifying restriction they require.
For the last extension, I consider a fully nonparametric estimator in the spirit of \citet{callaway2021difference}. Under conditional parallel trends and the same comparability condition, I estimate the ATT by comparing parents and childless individuals observed in the same year, at the same age and with the same matching characteristics. The estimator needs no pre-birth donor observations and aggregates type-specific effects with positive weights, thereby accommodating heterogeneous treatment effects.
I conduct Monte Carlo simulations in a child-penalty setting to examine the performance of the proposed estimators. When selection into parenthood differs between women and men, the DR estimator reduces root mean squared error using additional covariates in the pre-birth imputation. Synthetic type fixed effects remove bias caused by persistent differences in untreated outcome levels across types. Restricting the sample to a balanced panel can increase selection bias. When treatment effects differ across cohorts, the pseudo-panel regressions remain biased even with type fixed effects, whereas the nonparametric estimator recovers the average effect. Conventional 95\% confidence intervals for the pseudo-panel regression cover the true penalty in only 47--51\% of replications. Analytical inference and the cluster bootstrap show coverage close to the nominal level. With the matching cells held fixed, the individual-level pseudo-panel regression takes 1.8 times as long as the cell-mean regression with 10,000 people, and 25.5 times as long with 200,000, demonstrating computational improvements delivered by the cell-mean approach.
The proposed estimators are then applied to three South Korean datasets. Korea has the largest gender wage gap among OECD countries \citep{oecd2026korea}, and offers both a long-running household panel and several repeated cross-sectional surveys. The Korean Labor and Income Panel Study (KLIPS) provides the panel validation. Over years 0--10 after birth, the standard pseudo-panel regression, matched on age, year, marital status and education, yields an employment penalty of 42.1\%, close to the 46.9\% from the actual-panel regression. For annual earnings, the pseudo-panel penalty (64.7\%) is close to the panel penalty (65.6\%). The DR estimator and symmetric matching with synthetic type fixed effects give employment penalties of 40\% and 41\%, respectively, and earnings penalties of 64\% and 65\%. Across matching specifications, the nonparametric estimator gives employment penalties of 35--38\% and substantially lower earnings penalties of 42--47\%. The method is then applied to two repeated cross-sections, the Household Income and Expenditure Survey (HIES) and the Household Finance and Living Conditions Survey (HFLC). The pseudo-panel regression gives employment penalties of 33.5\% in HIES and 32.0\% in HFLC.
Recent work clarifies several methodological issues of this design. \cite{worldbank2024nonparametric} and \cite{balcazar2025nonparametric} match mothers to fathers based on their observed characteristics at childbirth and reweight observations at each event time to match the covariate distribution of the matched mothers. \cite{balcazar2025nonparametric} use this approach to address negative regression weights. \cite{bussolo2024marriage} use matching in both directions, as in the symmetric matching design considered here, but without synthetic type fixed effects.\footnote{Their post-marriage matches come from earlier marriage cohorts observed in the same survey year. My post-birth matches retain the same first-birth cohort across survey years.} They also use cohort means weighted by cohort size and note that this gives the same regression coefficients as using individual observations, without a formal proof or asymptotic analysis. \cite{thakral2026child} derive identifying restrictions for child-penalty regressions with age-at-first-birth or individual fixed effects. None of these papers provides a unified framework for identification, estimation, and inference in pseudo-panel event studies and their extensions.
The remainder of the paper is organized as follows. Section~\ref{sec:framework} sets up the framework, establishes identification and characterizes selection bias. Section~\ref{sec:estimation} develops the cell-level WLS equivalence and analytical inference. Section~\ref{sec:extensions} develops extensions. Section~\ref{sec:simulation} reports the Monte Carlo evidence. Section~\ref{sec:empirical} applies the proposed estimators to Korean panel and repeated cross-sectional data. Section~\ref{sec:conclusion} concludes. Technical proofs, additional results for symmetric matching, additional simulations and further empirical results are in the Supplementary Appendix.
\section{Framework and Identification}\label{sec:framework}
I adopt the potential outcomes framework of the staggered treatment literature, closely following the notation in \citet{kleven2025child}. Let $F_i$ denote the calendar year of individual $i$'s first childbirth, with the convention that $F_i = \infty$ if $i$ never has children. Outcomes are observed in calendar years $t = 1, \ldots, T$. The potential outcome of $i$ at time $t$ when first birth occurs in year $f$ is $Y_{it}(f)$ and the untreated potential outcome is $Y_{it}(\infty)$. The realized outcome is $Y_{it} = Y_{it}(F_i)$. Individual $i$ has gender $g \in \{w, m\}$ (women, men) and a vector of discrete pre-treatment characteristics $X_i$, including year of birth.\footnote{The matching variables $X_i$ are considered fixed: their values must remain the same in the birth year and in the earlier years from which pre-birth outcomes are imputed. Education or marital status can enter this vector only if their measurements satisfy that requirement.} The age $a_{it}$ at time $t$ is determined by $(X_i, t)$. For parents, the age at first birth is $\tilde{a}_i = a_{i,F_i}$, and the event time is $\tau_{it} = t - F_i$.
The parameter of interest is the average treatment effect on the treated:
\begin{equation}\label{eq:ATT}
\text{ATT}(f,t) = \mathbb{E}[Y_t(f) - Y_t(\infty) \mid F = f], \quad \text{for } 2 \le f \le t \le T.
\end{equation}
I suppress the gender superscript and the individual subscript when the context is clear. In practice, the estimator is applied separately by gender, and the child penalty is defined as $\text{ATT}^m(f,t) - \text{ATT}^w(f,t)$.
For parents observed at childbirth, the pseudo-panel imputes pre-birth outcomes using the mean outcomes of childless donors observed in the corresponding earlier year with the same characteristics. I establish identification of the ATT under three assumptions governing untreated outcome trends, anticipation and donor comparability. I assume that the observed cross-sections identify the relevant conditional means and covariate distributions of a common target population. All conditional expectations used below are well defined on the relevant support.
\begin{assumption}[Parallel Trends, PT]\label{assu:PT}
For all dates $t \neq t'$ and all cohorts $f \neq f'$, including $f=\infty$:
\begin{equation}\label{eq:PT}
\mathbb{E}[Y_t(\infty) - Y_{t'}(\infty) \mid F = f] = \mathbb{E}[Y_t(\infty) - Y_{t'}(\infty) \mid F = f'].
\end{equation}
\end{assumption}
\begin{samepage}
\begin{assumption}[Conditional No Anticipation, NA]\label{assu:NA}
For all $t < f$ and all $x$ in the support of $X \mid F = f$:
\begin{equation}\label{eq:NA}
\mathbb{E}[Y_t(f) \mid F = f, \, X = x] = \mathbb{E}[Y_t(\infty) \mid F = f, \, X = x].
\end{equation}
\end{assumption}
\end{samepage}
\begin{samepage}
\begin{assumption}[Conditional Independence, CI]\label{assu:CI}
For every date $s$, cohorts $f,f'>s$, including $\infty$, and $x$ in their common support:
\begin{equation}\label{eq:CI-alt}
\mathbb{E}[Y_s(\infty) \mid F = f, \, X = x] = \mathbb{E}[Y_s(\infty) \mid F = f', \, X = x].
\end{equation}
\end{assumption}
\end{samepage}
Assumption~\ref{assu:PT} requires the same mean untreated outcome trends across first-birth cohorts. Assumption~\ref{assu:NA} requires that anticipation of parenthood have no effect on mean pre-birth outcomes within each first-birth cohort and covariate cell.\footnote{This is weaker than the pointwise no-anticipation condition $Y_t(f) = Y_t(\infty)$ for all $t < f$ used in \cite{roth2023s}.} Assumption~\ref{assu:CI} requires that, conditional on $X$, people who are childless at a given date have the same mean untreated outcome regardless of when or whether they later have a child. Since $X$ includes year of birth, this comparison also holds age fixed. Assumptions~\ref{assu:NA} and~\ref{assu:CI} state two economic restrictions separately. CI equates untreated means across future first-birth cohorts within $X$, while conditional NA sets each cohort's mean anticipation effect to zero within $X$.\footnote{Assumption~3 in \citet{kleven2025child}, Equation~(5), directly equates parents' pre-birth mean outcomes with those of matched donors. In my notation, $\mathbb{E}[Y_s(f) \mid F=f, X=x] = \mathbb{E}[Y_s(F) \mid F>s, X=x]$ for $s<f$. This equality can hold when differences in untreated means are offset by differences in anticipation effects. Assumptions~\ref{assu:NA} and~\ref{assu:CI} exclude such offsetting and imply Kleven's condition on the relevant support. Kleven's condition also suffices for Theorem~\ref{thm:identification} when combined with Assumption~\ref{assu:PT} and no anticipation in cohort means, $\mathbb{E}[Y_s(f)-Y_s(\infty) \mid F=f]=0$ for $s<f$.} The following theorem establishes identification of the ATT under these assumptions.
\begin{samepage}
\begin{theorem}[Identification of ATT]\label{thm:identification}
Let Assumptions~\ref{assu:PT}--\ref{assu:CI} hold. Then for any $(f,t)$ with $2 \le f \le t \le T$,
\begin{multline}\label{eq:identification}
\text{ATT}(f,t) = \mathbb{E}[Y_t \mid F = f] - \mathbb{E}[Y_t \mid F > t] \\
- \mathbb{E}_x\!\big[\mathbb{E}[Y_{f-1} \mid F > f-1, X = x]\big| F = f\big] + \mathbb{E}_x\!\big[\mathbb{E}[Y_{f-1} \mid F > f-1, X = x]\big| F > t\big].
\end{multline}
\end{theorem}
\end{samepage}
All expectations on the right-hand side of \eqref{eq:identification} are identified from observable data. The first two terms are mean observed outcomes of parents and childless individuals at time $t$, and the last two terms are outcomes of childless individuals at time $f-1$ integrated over the covariate distributions of parents ($X \mid F = f$) and those still childless at $t$ ($X \mid F > t$), respectively. The last two terms subtract the pre-birth outcome difference attributable to the groups' different covariate distributions. If parents and childless individuals have the same covariate distribution, this adjustment is zero.
\begin{remark}[Comparison with panel data]\label{rem:panel-did}
With panel data, each parent's own pre-birth outcome is observed, and applying Assumptions~\ref{assu:PT} and~\ref{assu:NA} within gender $g$ yields
\begin{equation}\label{eq:panel-att-g}
\text{ATT}^g(f,t) = \mathbb{E}[Y_t - Y_{f-1} \mid F = f, \, g] - \mathbb{E}[Y_t - Y_{f-1} \mid F > t, \, g],
\end{equation}
so cohort-level parallel trends and no anticipation suffice and Assumption~\ref{assu:CI} is not needed. In repeated cross-sections, these pre-birth means must instead be recovered from matched childless donors. Assumption~\ref{assu:CI} justifies this substitution.
\end{remark}
I now derive the bias that arises when Assumption~\ref{assu:CI} fails. This assumption is restrictive because career and fertility decisions are jointly determined. For instance, women in high-paying professions may delay or forgo childbearing. If permanently childless individuals in the donor group differ in unobserved labor market ability from future parents, the imputed pre-birth outcomes are biased.
To illustrate the bias, consider the following additive model for observed outcomes:
\begin{equation}\label{eq:outcome-model}
Y_{it}^g = \pi_g(\tau_{it}) + \underbrace{\phi_{a_{it}}^g}_{\text{age FE}} + \underbrace{\psi_t^g}_{\text{time FE}} + \underbrace{\alpha_i^g}_{\text{ind.\ FE}} + X_i'\beta^g + \underbrace{\varepsilon_{it}^g}_{\text{shock}}.
\end{equation}
Here $\pi_g(\tau)$ is the common effect of parenthood at event time $\tau$. It is zero for never-parents and before childbirth. The terms $\phi_a^g$, $\psi_t^g$ and $\alpha_i^g$ are age, calendar-year and individual fixed effects.\footnote{The coefficient of year of birth in $\beta^g$ is normalized to zero because it is collinear with the age and calendar-year fixed effects.} I assume $\mathbb{E}[\varepsilon_{it}^g \mid F_i, X_i] = 0$, so selection on unobservables operates through $\alpha_i^g$.
With panel data, comparing each person's outcome after childbirth with their own outcome in the year before childbirth removes both $\alpha_i^g$ and $X_i'\beta^g$. For $\tau\geq0$ and $s=F_i-1=t-\tau-1$,
\[
\mathbb{E}[Y_{it}^g-Y_{is}^g\mid\tau_{it}=\tau,a_{it}=a]
=\pi_g(\tau)+(\phi_a^g-\phi_{a-\tau-1}^g)+(\psi_t^g-\psi_s^g).
\]
After accounting for age and calendar-year effects, this mean change equals $\pi_g(\tau)$ even if the timing of childbirth is related to $\alpha_i^g$.
In repeated cross-sections, however, parents observed at childbirth in year $t$ at age $a$ are compared with donors observed at $s=t-1$. This donor pool includes both future parents and never-parents. Conditional on $(a-1,x,g)$, let $\omega_k^g=\Pr(F=s+k\mid F>s,a-1,x,g)$ for $k\ge1$, and let $\omega_\infty^g=\Pr(F=\infty\mid F>s,a-1,x,g)$.\footnote{These shares sum to one. Their dependence on $s$, $a-1$ and $x$ is suppressed in the notation.} Define $d_g(t,a)=(\phi_a^g-\phi_{a-1}^g)+(\psi_t^g-\psi_{t-1}^g)$ and
\[
\Delta_g(t,a,x)=\mathbb{E}[\alpha_i^g\,|\,F=t,a,x]-\sum_{k\ge1}\omega_k^g\,\mathbb{E}[\alpha_i^g\,|\,F=t-1+k,a-1,x]-\omega_\infty^g\,\mathbb{E}[\alpha_i^g\,|\,F=\infty,a-1,x],
\]
which is the difference in means of individual fixed effects between parents observed at birth and their donor pool. $\Delta_g(t,a,x)$ also equals their gap in mean untreated outcomes at $t-1$. The pseudo-panel comparison of parents observed at birth with the donor pool one year earlier is
\begin{multline}\label{eq:pseudo-bias}
\mathbb{E}[Y_{it}^g\mid F=t,a,x]-\mathbb{E}[Y_{i,t-1}^g\mid F>t-1,a-1,x]
=\pi_g(0)+d_g(t,a)+\Delta_g(t,a,x).
\end{multline}
Within this model, Assumption~\ref{assu:CI} implies $\Delta_g(t,a,x)=0$.
As in the panel case, the pseudo-panel regression absorbs $d_g(t,a)$ through age and year fixed effects. However, $\Delta_g(t,a,x)$ may remain when Assumption~\ref{assu:CI} is violated, and this bias cancels in the gender difference only if it is the same for women and men. For example, if childless women have higher untreated outcomes than mothers and the corresponding male gap is zero, the child penalty from this comparison is overestimated. Richer matching variables can reduce this bias.\footnote{\citet{kleven2025child} finds positive jumps in men's outcomes at $\tau=0$ when matching only on age, year and gender, which he attributes to selection rather than childbirth. These jumps disappear when education, marital status, race and state are added.}
\section{Estimation}\label{sec:estimation}
I first describe the pseudo-panel regression of \citet{kleven2025child}. All regressions are estimated separately by gender, and $g$ is suppressed when no confusion arises. The first-birth year $F_i$ (and hence $\tau_{it}$) for parents is typically inferred from the oldest child's age. Define a \emph{cell} as $c = (X, t)$: all individuals with demographics $X$ observed in year $t$. Within each cell, let $N^C_c$ denote the number of childless individuals and $\bar{Y}^C_c$ their mean outcome. Estimation is restricted to an event-time window $\tau \in \mathcal{T} := \{-\underline{T}, \dots, \overline{T}\}$.
Consider a parent $i$ observed at $\tau = 0$ in cell $(X_i, F_i)$. For each pre-birth event time $\tau < 0$, the \emph{donor cell} is $(X_i, F_i + \tau)$: childless individuals with the same demographics observed in year $F_i + \tau$. Since $X_i$ includes year of birth, they have the same age as the parent had $|\tau|$ years earlier. The parent's pre-birth outcome is imputed as the donor-cell mean, $\tilde{Y}_{i\tau}=\bar{Y}^C_{(X_i,\, F_i + \tau)}$. This backward matching restricts which parents can be used. The donor cell at event time $\tau < 0$ requires childless observations in year $F_i + \tau$, before the parent's first child is born, so when the data begin in calendar year $\underline{t}$, parents with $F_i + \tau < \underline{t}$ have no donors at that event time.\footnote{With $\underline{T} = 5$ pre-birth years and data starting in 2006, for instance, only first-birth cohorts with $F_i \ge 2011$ have complete pre-birth donor coverage.} For post-birth event times $\tau \ge 0$, the observed outcomes of all parents are used. Any parent $j$ observed in year $t$ with $\tau_{jt} = \tau$ contributes $\tilde{Y}_{j\tau} = Y_{jt}$.
Using the constructed pseudo-panel, the following regression is estimated by OLS, and the estimator is referred to as pseudo-OLS:
\begin{equation}\label{eq:event-study}
\tilde{Y}^{g}_{i\tau}
=
\sum_{\tau' \in \mathcal{T}} \beta^{g}_{\tau'}
\, \mathbf{1}\{\tau = \tau'\}
+ \phi^g_{a_{i\tau}} + \psi^g_{t_{i\tau}} + \nu^{g}_{i\tau}.
\end{equation}
Here $t_{i\tau}=F_i+\tau$ is the year of observation $(i,\tau)$, and $a_{i\tau}$ is the parent's age in that year. The terms $\phi_a^g$ and $\psi_t^g$ are age and calendar-year fixed effects. The coefficient $\beta^g_{\tau^\star}$ is normalized to zero for a base period $\tau^\star < 0$. The child penalty at event time $\tau$ is $\beta^m_\tau - \beta^w_\tau$. Penalties are also reported in percentage terms. For each gender, the estimated counterfactual mean $\hat c^g_\tau$ is obtained by averaging the predicted outcome net of the estimated event-time effect, $\widehat{\tilde Y}^g_{i\tau}-\hat\beta^g_\tau$, across pseudo-panel observations at event time $\tau$. The scaled penalty is $\hat\beta^m_\tau/\hat c^m_\tau-\hat\beta^w_\tau/\hat c^w_\tau$.\footnote{For event studies with panel data, \cite{leventer2026identification} shows that the gender gap in normalized event-study effects is not identified under his normalized triple-difference framework when parallel trends fails within gender, and proposes the effect of parenthood on the gender earnings ratio as an alternative estimand.}
Assumptions~\ref{assu:PT}--\ref{assu:CI} identify the cohort-time ATT nonparametrically. The event-study regression in \eqref{eq:event-study} approximates untreated outcomes by additive age and year effects and aggregates treatment effects across cohorts into a common event-time profile. If this specification is correct, the population event-time coefficients equal the ATT. Otherwise, the coefficients need not recover the average causal effects.
Although the pseudo-panel is constructed at the individual level, its regressors and imputed pre-birth outcomes are constant within each \emph{regression cell} $r=(X,t,\tau)$. The pseudo-OLS regression can therefore be rewritten as an equivalent WLS regression using cell means. Let $\mathcal{R}^g$ denote the set of regression cells for gender $g$. For $r=(X,t,\tau)$ with $\tau\geq0$, let $N^P_r$ denote the number of parents observed in that cell. Define
\[
\bar{Y}_r =
\begin{cases}
\displaystyle
\frac{1}{N^P_r}\sum_{j:(j,t)\in r} Y_{jt}, & \tau \ge 0,\\[2ex]
\displaystyle
\bar{Y}^{C}_{(X,\, t)}, & \tau < 0,
\end{cases}
\qquad
w_r =
\begin{cases}
N^{P}_{r}, & \tau \ge 0,\\
N^{P}_{(X,\, t-\tau,\, 0)}, & \tau < 0,
\end{cases}
\]
where $N^P_{(X,\, t-\tau,\, 0)}$ is the number of parents with characteristics $X$ observed at childbirth in year $F=t-\tau$. Each of these parents receives the same donor-cell mean as the imputed outcome at $\tau<0$, so the mean appears once per parent in the individual-level regression. Let $\mathbf d_r$ be the vector of event-time, age and year dummies for cell $r$, omitting the dummy for $\tau^\star$ and one year dummy, and let $\mathbf b^g$ collect their coefficients. The regression assigns the same value, $\mathbf d_r'\mathbf b^g$, to all observations in a cell. Since their deviations from the cell mean sum to zero,
\[
\begin{aligned}
\sum_{r\in\mathcal R^g}\sum_{(i,\tau)\in r}
(\tilde Y_{i\tau}-\mathbf d_r'\mathbf b^g)^2
&=\sum_{r\in\mathcal R^g}\sum_{(i,\tau)\in r}
(\tilde Y_{i\tau}-\bar Y_r)^2\\
&\quad+\sum_{r\in\mathcal R^g}w_r
(\bar Y_r-\mathbf d_r'\mathbf b^g)^2.
\end{aligned}
\]
The first term on the right does not depend on $\mathbf b^g$, while the second is the WLS objective using cell means and weights $w_r$. Minimizing either regression objective therefore gives the same coefficients under full column rank: $\widehat{\mathbf b}^{g}_{\mathrm{WLS}}=\widehat{\mathbf b}^{g}_{\mathrm{OLS}}$.
This cell representation makes the regression weights explicit and expresses the estimator as a function of cell means and counts, which I use to derive its analytical variance. It also reduces the size of the regression. With the covariates, calendar years and event window held fixed, the number of regression cells is bounded, while the number of individual-level observations grows with the number of parents. The cell regression can therefore be much faster in large samples.
\subsection{Consistency of the Cell-Mean Estimator}\label{sec:consistency}
I now show that, as cell sizes grow, the pseudo-panel OLS estimator converges to the probability limit of the infeasible ``oracle'' OLS estimator that uses the true (never observed) panel data. The convergence relies on two population objects. For post-birth cells ($\tau \ge 0$), the cell mean converges to the population conditional mean among parents at that event time:
\[
\bar{Y}_r \to_p \mathbb{E}[Y_{it} \mid X_i = x, \, \tau_{it} = \tau].
\]
For pre-birth cells ($\tau < 0$), the donor-cell mean converges to the childless population mean:
\[
\bar{Y}_r \to_p \mathbb{E}[Y_{it} \mid X_i = x, \, F_i > t].
\]
Under Assumptions~\ref{assu:NA} and~\ref{assu:CI}, the childless conditional mean equals the untreated potential outcome mean for parents:
\begin{equation}\label{eq:CI-cell}
\begin{aligned}
\mathbb{E}[Y_{it} \mid X_i = x, \, F_i > t]
&= \mathbb{E}[Y_{it}(\infty) \mid X_i = x, \, F_i > t] \\
&= \mathbb{E}[Y_{it}(\infty) \mid X_i = x, \, F_i = f] \quad \text{for any } f > t,
\end{aligned}
\end{equation}
so that each pre-birth cell mean consistently estimates the mean untreated outcome of parents with the same characteristics.
Define the oracle outcome for each observation in the pseudo-panel as
\[
Y^*_{i\tau} =
\begin{cases}
Y_{i,F_i+\tau}(\infty), & \tau < 0,\\
Y_{i,F_i+\tau}(F_i), & \tau \ge 0.
\end{cases}
\]
Let $\mathbf d_{i\tau}$ denote the corresponding event-time, age, and year dummies. Expectations for the oracle regression are taken over the limiting distribution of its observations, with cell probabilities $p_r=\operatorname{plim}\{w_r/\sum_{r'}w_{r'}\}$.
\begin{assumption}[Sampling and Design]\label{assu:lln}
Let $n_s$ denote the sample size of the year-$s$ cross-section. (i) As $\min_s n_s \to \infty$, the parent and donor counts and outcome sums of every included cell, normalized by the cross-section sizes, converge jointly in probability to their population values, and the relative sizes $n_s/\sum_{s'}n_{s'}$ converge to positive limits. For each included pre-birth cell with first-birth cohort $f$, covariates $x$ and date $s<f$, the mean of $Y_{is}(\infty)$ among the parents counted by $N^P_{(x,f,0)}$ also converges in probability to $\mathbb{E}[Y_s(\infty)\mid F=f,X=x]$. (ii) The set of included cells is fixed in the limit, and every cell has positive population mass. (iii) The limiting design matrix $Q^* := \mathbb{E}[\mathbf d_{i\tau} \mathbf d_{i\tau}']$ is nonsingular.
\end{assumption}
\noindent Part (i) of Assumption~\ref{assu:lln} is a joint law of large numbers for the observed cell sums and the unobserved pre-birth means used in the oracle regression. The latter condition requires parents observed at birth to represent their cohort and covariate group in mean untreated pre-birth outcomes. Stable relative sizes of the cross-sections give limits for the regression weights. Part (ii) keeps every cell mean well defined in the limit, and part (iii) makes the probability limit unique. The following proposition establishes consistency.
\begin{prop}[Convergence to Oracle OLS]\label{prop:oracle}
Suppose Assumptions~\ref{assu:NA}--\ref{assu:lln} hold. Then, as $\min_s n_s \to \infty$,
\[
\widehat{\mathbf b}^{\textup{OLS}} \to_p \mathbf b^*_0 := (Q^*)^{-1} \mathbb{E}[\mathbf d_{i\tau} Y^*_{i\tau}],
\]
which is the probability limit of the infeasible oracle OLS regression of $Y^*_{i\tau}$ on $\mathbf d_{i\tau}$.
\end{prop}
\subsection{Asymptotic Theory for the Cell-Mean Estimator}\label{sec:cell-inference}
The sampling variation of the pseudo-panel comes from both outcomes and the counts that determine its weights. The same donor-cell mean can be used to impute pre-birth outcomes for parents from different first-birth cohorts. In surveys that reinterview respondents, an individual can contribute as a donor in one year and as a parent in another. Spouses can also contribute to opposite sides of the gender difference. Conventional standard errors treating the constructed cells as independent observations do not account for this variation.
Let $N$ denote the number of independent clusters, each of which contains all observed years and all parent and donor roles of its members.\footnote{In a repeated cross-section with independent individual sampling, each observation is its own cluster.} For cluster $\ell$, let $n^P_{r,\ell}$ be the number of its parent observations in regression cell $r$ with $\tau\ge0$ and $S^P_{r,\ell}$ the sum of their outcomes, and let $n^C_{c,\ell}$ and $S^C_{c,\ell}$ be the same quantities for its childless records in donor cell $c$. Collect these over all included cells of both genders in $H_\ell=\big((S^P_{r,\ell},n^P_{r,\ell})_{r},\,(S^C_{c,\ell},n^C_{c,\ell})_{c}\big)$ and write $\hat\eta=N^{-1}\sum_{\ell=1}^N H_\ell$, $\eta=\mathbb{E}[H_\ell]$. Cell means are ratios of coordinates of $\hat\eta$, $\bar Y_r=\sum_\ell S^P_{r,\ell}/\sum_\ell n^P_{r,\ell}$ for post-birth cells and $\bar Y^C_c=\sum_\ell S^C_{c,\ell}/\sum_\ell n^C_{c,\ell}$ for donor cells, and the regression weights are obtained from these parent counts.
\begin{assumption}[Regularity]\label{assu:reg}
(i) Clusters are i.i.d., and $H_\ell$ has finite second moments.
(ii) The event window and the set of included cells are fixed. Every denominator used for a cell mean or normalized weight has a strictly positive population limit.
(iii) The limiting weighted design matrix $Q^*=\sum_r p_r\mathbf d_r\mathbf d_r'$, where $p_r$ is the probability limit of $w_r/\sum_{r'}w_{r'}$, is nonsingular.
(iv) The sample rule that determines which cells are included selects the set of (ii) with probability tending to one.
\end{assumption}
Assumption~\ref{assu:reg} supplies the law of large numbers for the observed cell moments and the finite second moments and independence across clusters needed for a central limit theorem. The additional law of large numbers for unobserved pre-birth means in Assumption~\ref{assu:lln}(i) is used only for the oracle comparison. The sets of regression cells $r=(X,t,\tau)$ and donor cells $c=(X,t)$ retained in the limit remain fixed as $N$ grows.\footnote{Allowing the number of cells to grow with $N$ would require additional rate and bias conditions \citep{mckenzie2004asymptotic}.}
\begin{prop}[Asymptotic Normality]\label{prop:cell-clt}
Under Assumption~\ref{assu:reg}, write the child penalty at an event time, or a scaled penalty averaged over post-birth event times, as $\hat P=G(\hat\eta)$ and its probability limit as $P^*=G(\eta)$, for a $G$ that is continuously differentiable in a neighborhood of $\eta$. Then
\[
\sqrt N(\hat P-P^*)\ \xrightarrow{d}\ N(0,V),\qquad
V=J\Sigma J',\quad J=DG(\eta),\quad \Sigma=\operatorname{Var}(H_\ell).
\]
Partition the coordinates of $H_\ell$ into the parent coordinates $(S^P,n^P)$, labeled $P$, and the donor coordinates $(S^C,n^C)$, labeled $D$, and partition $J$ and $\Sigma$ conformably. Then
\begin{equation}\label{eq:two-sample-var}
V=J_P\Sigma_{PP}J_P'+J_D\Sigma_{DD}J_D'
+J_P\Sigma_{PD}J_D'+J_D\Sigma_{PD}'J_P'.
\end{equation}
Moreover, let $\hat J=DG(\hat\eta)$, $\hat\psi_\ell=\hat J(H_\ell-\hat\eta)$ and $\bar\psi=N^{-1}\sum_\ell\hat\psi_\ell$. The covariance estimator
\begin{equation}\label{eq:analytical-block-cov}
\widehat{\operatorname{Var}}(\hat P)
=\frac{1}{N(N-1)}\sum_{\ell=1}^N
(\hat\psi_\ell-\bar\psi)(\hat\psi_\ell-\bar\psi)'
\end{equation}
satisfies $N\widehat{\operatorname{Var}}(\hat P)\to_p V$.\footnote{For independent annual samples with fixed numbers of clusters, replace $\Sigma$ by the weighted average of the within-year covariances. Remark~\ref{rem:fixed-year-sampling} gives the variance estimator and the corresponding bootstrap.}
\end{prop}
The first two terms in \eqref{eq:two-sample-var} account for sampling variation in the parent and donor moments, and the cross terms arise when the same cluster enters both, as when a person is observed as a donor and later as a parent. $\Sigma_{PP}$ also includes covariances across genders and event times. The child penalty is the difference between the male and female estimates. When spouses belong to the same cluster, a household shock moves both, so the variance of the difference is not the sum of the two variances, and positive covariance lowers it while negative covariance raises it. Covariances across event times also enter the variance of an average penalty. Conventional regression standard errors that ignore donor reuse and dependence within sampling clusters can therefore be too small or too large.
The Jacobian $J$ in Proposition~\ref{prop:cell-clt} makes explicit that the regression coefficients vary with the sample through two channels.\footnote{Appendix~\ref{app:analytical-implementation} gives the complete derivatives, including those of the counterfactual denominator.} For the unscaled regression, let $\mathbf D$ be the matrix with rows $\mathbf d_r'$, $w$ the limiting row weights, $\mu$ the vector of distinct population cell means, $L$ the matrix that assigns each row its cell mean, $Q=\mathbf D'\operatorname{diag}(w)\mathbf D$ and $\mathbf b^*=Q^{-1}\mathbf D'\operatorname{diag}(w)L\mu$. Then
\[
d\mathbf b=Q^{-1}\!\left\{\mathbf D'\operatorname{diag}(w)L\,d\mu
+\mathbf D'\operatorname{diag}(dw)(L\mu-\mathbf D\mathbf b^*)\right\}.
\]
The first term is the effect of sampling variation in the cell means. The second is the effect of the estimated weights, which vanishes when the additive regression fits the cell means exactly. Scaled penalties add a third channel, the sampling variation of the counterfactual denominator, which \citet{kleven2025child} treats as nonstochastic. $J$ includes the derivative with respect to the denominator, so $V$ accounts for this variation too.
A cluster bootstrap that resamples clusters and repeats the full estimation has the same first-order limiting distribution under the conditions of Proposition~\ref{prop:cell-clt}, provided that bootstrap samples also select the limiting set of cells with conditional probability tending to one.\footnote{Consistency of bootstrap SEs additionally requires the uniform-integrability condition in Remark~\ref{rem:bootstrap} in Appendix~\ref{app:proof-cell-clt}. This condition can fail when the counterfactual denominator of a scaled penalty is close to zero in some bootstrap samples.} The analytical standard error (SE) I derive is practically useful since it avoids the repeated estimation required by a bootstrap.
\section{Extensions}\label{sec:extensions}
The baseline design matches on discrete cells, constructs pre-birth outcomes from childless donors while post-birth outcomes come from whichever parents appear at each event time, and extrapolates age/year effects through an additive regression specification. This section develops three extensions, each addressing one of these limitations. The first is a doubly robust imputation that admits richer covariates. The second matches parents observed at birth both backward and forward and adds synthetic type fixed effects. The third is a fully nonparametric estimator that accommodates heterogeneous treatment effects.
\subsection{Doubly Robust Estimation}\label{sec:dr}
The pseudo-panel estimator can be biased by the parent--donor gap $\Delta_g$ because of unobserved heterogeneity. Here I develop a doubly robust (DR) imputation that accommodates richer, possibly continuous, covariates. It does not weaken conditional independence. Rather, it makes the assumption more credible by conditioning on a richer covariate vector. I view the imputation as a two-sample problem because pre-birth outcomes of parents are imputed using a sample of childless individuals observed at an earlier date, whose covariate distribution may differ from that of the parents.\footnote{\cite{santanna2026composition} develop doubly robust DiD estimators for repeated cross-sections whose covariate composition changes over time. Treatment-group membership is observed before treatment in their setting.} Fix a gender $g$, a first-birth cohort $f$ and a pre-birth event time $\tau < 0$, so the donor year is $t=f+\tau$. Let $S_i = 1$ indicate membership in the target sample of cohort-$f$ parents observed at birth, and $S_j = 0$ membership in the donor sample of childless individuals observed in year $t$. The fixed cohort and donor year are suppressed in the notation.
Let $Z_i=(X_i, V_i)$ denote a \emph{rich} covariate vector that includes both the discrete variables $X_i$ and additional covariates $V_i$, which may include finely discrete variables and continuous variables. Conditioning on $V_i$ is useful when it is correlated with the unobserved heterogeneity. The DR framework adjusts for $V_i$ through models. The goal is to produce an improved pre-birth imputation $\hat{Y}^{DR}_{i,\tau}$ that replaces the donor-cell mean $\bar{Y}^C_{(X_i, F_i+\tau)}$. The DR-imputed pseudo-panel is then fed into the same event-study regression \eqref{eq:event-study}.
For DR estimation, I maintain Assumptions~\ref{assu:NA} and~\ref{assu:CI} with the richer pre-treatment vector $Z = (X, V)$ in place of $X$. Neither restriction at this finer conditioning level follows automatically from its original version conditional on $X$.\footnote{Conditional mean independence is not monotone in the conditioning set, and mean anticipation effects that vanish within an $X$ cell need not vanish within its $Z$ subcells.} An overlap condition is also required.
\begin{assumption}[Overlap]\label{assu:overlap}
For all $z$ in the support of $Z_i \mid S_i = 1$:
\begin{equation}\label{eq:overlap}
0 < \Pr(S_i = 1 \mid Z_i = z, \, g) < 1.
\end{equation}
\end{assumption}
Assumption~\ref{assu:overlap} requires that for every covariate profile $z$ observed among parents, there exist childless donors with similar profiles. Weak overlap is commonly addressed by trimming.\footnote{Trimming can exclude parents observed at birth, whose counts determine the pre-birth cell weights. It can therefore change the population represented by the estimate.}
The imputation combines two nuisance models. The first models the conditional mean outcome among childless donors as a function of the covariates:
\begin{equation}\label{eq:outcome-model-dr}
m_g(z) = \mathbb{E}[Y_i \mid S_i = 0, \, Z_i = z, \, g] \ \textit{(Outcome model, OM)}.
\end{equation}
The second models the probability that an individual belongs to the parent sample, conditional on the covariates:
\begin{equation}\label{eq:propensity}
e_g(z) = \Pr(S_i = 1 \mid Z_i = z, \, g) \ \textit{(Propensity score, PS)}.
\end{equation}
Both models are directly estimable. The outcome model is estimated by regressing outcomes on $Z$ within the donor sample. The propensity score is estimated by a binary choice model (e.g., probit or logit) for $S_i$ on $Z$ in the pooled sample of parents and donors. Intuitively, the propensity score measures how ``parent-like'' a covariate profile is. Donors resembling parents (high $e_g(z)$) receive larger weights.
For each parent $i$ at pre-birth event time $\tau < 0$, the DR imputation is:
\begin{equation}\label{eq:dr-estimator}
\hat{Y}^{DR}_{i,\tau}
=
\hat{m}_g(Z_i)
+
\frac{\sum_{j \in \mathcal{D}} \hat{w}_g(Z_j) \big(Y_{jt} - \hat{m}_g(Z_j)\big)}{\sum_{j \in \mathcal{D}} \hat{w}_g(Z_j)}, \quad \hat{w}_g(Z_j) = \frac{\hat{e}_g(Z_j)}{1 - \hat{e}_g(Z_j)},
\end{equation}
where $\mathcal{D}$ denotes the donor pool in the donor year, and $\hat{w}_g(Z_j)$ is the inverse probability weight, an estimate of the odds $w_g(z) = e_g(z)/(1-e_g(z))$. The weights are normalized to sum to one. The first term predicts the untreated outcome at parent $i$'s covariates using the outcome model. The second term corrects for misspecification of $m_g$ by adding a weighted average of donor residuals.\footnote{The weighted residual correction follows the augmented inverse-probability-weighting approach of \citet{robins1994estimation}. \citet{santanna2020doubly} use this principle to construct DR estimators of the ATT in panel and repeated-cross-section DiD settings.} When $V_i = \emptyset$ and $m_g$ is saturated in covariates, the expression reduces to the donor-cell mean $\bar{Y}^C_{(X_i, F_i+\tau)}$, recovering the baseline pseudo-OLS. The average imputation over parents is doubly robust as it remains consistent if either the outcome model or the propensity score is correctly specified.
The DR estimator of the mean pre-birth outcome also has an efficiency property when both nuisance models are correct. I state it for an independent two-sample setting, separating the precision of one imputed mean from inference for the subsequent event-study regression.
\begin{prop}[Double Robustness and Efficiency]\label{prop:dr}
Fix $g$, $f$ and $\tau$ as above, and let $\mu^0_{g,\tau}(z) := \mathbb{E}[Y_{i,f+\tau}(\infty) \mid Z_i = z, S_i = 1, g]$ and $\mu^0_{g,\tau} := \mathbb{E}[\mu^0_{g,\tau}(Z_i) \mid S_i = 1, g]$ be the parents' conditional and mean untreated pre-birth outcomes. Write $E_s$ and $\operatorname{Var}_s$ for expectation and variance conditional on $S=s$, and $P^Z_s$ for the distribution of $Z$ given $S=s$. Suppose Assumptions~\ref{assu:NA} and~\ref{assu:CI} hold with $Z$ in place of $X$, together with Assumption~\ref{assu:overlap}. Let the estimated nuisance functions have probability limits $m^\dagger_g$ and $w^\dagger_g$ with $E_0[w^\dagger_g]>0$ and finite second moments, and suppose that sample averages of the estimated functions and of the weighted residuals converge to their population limits. Write $\hat\mu^{DR}_{g,\tau}=n_1^{-1}\sum_{i:S_i=1}\hat Y^{DR}_{i,\tau}$ for the average imputation over the $n_1$ parents. Then:
\begin{enumerate}
\item[\textup{(a)}] If the outcome model is correctly specified, so that $m^\dagger_g=m_g$ and $\hat{m}_g(Z_i)-m_g(Z_i) \to_p 0$ for each parent $i$, and the weights are uniformly bounded, then $\hat{Y}^{DR}_{i,\tau} \to_p \mu^0_{g,\tau}(Z_i)$ for each parent $i$, and consequently $\hat\mu^{DR}_{g,\tau} \to_p \mu^0_{g,\tau}$.
\item[\textup{(b)}] If $w^\dagger_g \propto w_g$, as when the propensity score is correctly specified, then $\hat\mu^{DR}_{g,\tau} \to_p \mu^0_{g,\tau}$.
\item[\textup{(c)}] Suppose the parents' covariates $\{Z_i: S_i=1\}$ and the donor observations $\{(Y_j,Z_j): S_j=0\}$ are two mutually independent i.i.d.\ samples with sizes $n_1,n_0$, where $n_s/N\to\lambda_s\in(0,1)$ and $N=n_1+n_0$. Under correctly specified, smooth finite-dimensional nuisance models and the regularity conditions stated in Appendix~\ref{app:proof-dr}, the estimator $\hat\mu^{DR}_{g,\tau}$ is semiparametrically efficient for $\mu^0_{g,\tau}$ in the unrestricted two-sample observed-data model. Writing $\rho_g=dP_1^Z/dP_0^Z$, its limiting variance is
\begin{equation}\label{eq:dr-eff-bound}
\begin{aligned}
\sqrt N(\hat\mu^{DR}_{g,\tau}-\mu^0_{g,\tau})
&\xrightarrow{d}\mathcal N(0,V^{\mathrm{eff}}_{g,\tau}),\\
V^{\mathrm{eff}}_{g,\tau}
&=\frac{\operatorname{Var}_1[m_g(Z)]}{\lambda_1}
+\frac{E_0[\rho_g(Z)^2\operatorname{Var}_0(Y\mid Z)]}{\lambda_0}.
\end{aligned}
\end{equation}
\end{enumerate}
\end{prop}
\noindent In part~(c), the two terms of \eqref{eq:dr-eff-bound} reflect uncertainty about the parents' covariate distribution and about donor outcomes given those covariates. Under the correctly specified parametric models and regularity conditions assumed there, nuisance estimation has no first-order effect on the estimated pre-birth mean. The estimator therefore attains the efficiency bound.
To implement the DR estimator while controlling for the cell variables $X$ nonparametrically, I apply the correction within donor cells. For a donor cell $c=(X,t)$, let $\mathcal D_c$ contain its childless donors. The additional covariates $V$ vary within $c$. Both nuisance models are indexed by $c$, so a parent's covariates are compared with donors observed in the donor year. Write $m_{g,c}(v)=\mathbb{E}[Y\mid S=0,c,V=v,g]$ and let $w_{g,c}(v)$ be proportional to the within-cell density ratio $dP(V\mid S=1,c,g)/dP(V\mid S=0,c,g)$. The within-cell imputation is
\begin{equation}\label{eq:cell-dr}
\hat Y^{DR}_{i,\tau}=\hat m_{g,c}(V_i)+
\frac{\sum_{j\in\mathcal D_c}\hat w_{g,c}(V_j)\{Y_j-\hat m_{g,c}(V_j)\}}
{\sum_{j\in\mathcal D_c}\hat w_{g,c}(V_j)},
\end{equation}
which gives larger weights to donors whose covariate profiles are more typical of the parents in the cell. Proposition~\ref{prop:dr} applies cell by cell, with $Z=(X,V)$ and overlap within each cell.
DR replaces the pre-birth donor-cell means with imputed outcomes but leaves the event-study regression unchanged. The cell-level regression still applies, because regressors and weights remain constant within regression cells even though DR imputations differ across parents. If every imputed cell mean is consistent, the coefficients converge to the oracle projection of Section~\ref{sec:consistency}. DR imputations depend on the estimated outcome and propensity models. Valid inference must account jointly for their estimation errors and the sampling variation in cell means, counts and the counterfactual means used to scale the penalty.
For finite-dimensional nuisance models, let $\zeta$ collect the cell moments, OM and PS parameters, and nuisance-dependent sums entering the child penalty or scaled penalty. Now write the estimator as $G_{DR}(\hat\zeta)$ in place of $G(\hat\eta)$ in Proposition~\ref{prop:cell-clt}. Let $\Psi_\ell(\zeta)$ collect cluster $\ell$'s contributions to the estimating equations for the outcome and propensity models, cell moments, and sums. The following proposition derives the asymptotic distribution of the DR penalty estimator and a consistent estimator of its variance.
\begin{prop}[Parametric DR Inference]\label{prop:dr-inference}
Under Assumption~\ref{assu:reg} and the regularity conditions in Appendix~\ref{app:proof-dr-inference}, let $\hat\zeta\to_p\zeta^*$ satisfy
\[
N^{-1}\sum_\ell\Psi_\ell(\hat\zeta)=o_p(N^{-1/2}),
\qquad E[\Psi_\ell(\zeta^*)]=0.
\]
Assume that $\zeta$ is finite dimensional, $A=E[\partial_\zeta\Psi_\ell(\zeta^*)]$ is nonsingular, and $G_{DR}$ is continuously differentiable in a neighborhood of $\zeta^*$. Then
\[
\sqrt N\{G_{DR}(\hat\zeta)-G_{DR}(\zeta^*)\}\ \xrightarrow{d}\ N(0,V_{DR}),\qquad
V_{DR}=E[\psi^{DR}_\ell\psi^{DR}_\ell{}'],
\]
where $\psi^{DR}_\ell=-DG_{DR}(\zeta^*)A^{-1}\Psi_\ell(\zeta^*)$. Define
\[
\hat A=N^{-1}\sum_{\ell=1}^N
\partial_\zeta\Psi_\ell(\hat\zeta),
\qquad
\hat\psi^{DR}_\ell
=-DG_{DR}(\hat\zeta)\hat A^{-1}\Psi_\ell(\hat\zeta).
\]
Let $\widehat{\operatorname{Var}}\{G_{DR}(\hat\zeta)\}$ be
the covariance estimator \eqref{eq:analytical-block-cov}
computed using $\hat\psi^{DR}_\ell$. Then
\[
N\,\widehat{\operatorname{Var}}\{G_{DR}(\hat\zeta)\}
\xrightarrow{p}V_{DR}.
\]
\end{prop}
\noindent The proposition centers the DR penalty estimate $G_{DR}(\hat\zeta)$ at its pseudo-true value $G_{DR}(\zeta^*)$ without assuming that both models are correct. The variance estimator accounts for estimation of both nuisance models, since these estimation effects need not vanish when only one model is correctly specified.
\begin{remark}[Cross-fitting]\label{rem:crossfit}
The nuisance functions can be estimated by machine learning with Neyman orthogonalization following \citet{chernozhukov2018double}, without imposing parametric restrictions. This procedure requires cross-fitting. Clusters are divided into folds, and the estimating equations for each fold are evaluated using nuisance models estimated on the other folds.
\end{remark}
\subsection{Symmetric Matching and Synthetic Type FE}\label{sec:symmetric}
The baseline pseudo-panel construction is asymmetric. Pre-birth outcomes are imputed for the parents observed at birth, whereas post-birth outcomes come from whichever parents are observed at each event time, so the composition of parents can change with event time. I consider an alternative construction that matches the parents observed at birth symmetrically in both directions.\footnote{This construction is suggested in footnote~13 of \citet{kleven2025child}.} For pre-birth outcomes, parents observed at first birth are matched to childless donors, as in the baseline. For post-birth outcomes, they are instead matched to parents with the same first-birth year and observed characteristics. This symmetric construction produces a synthetic history for each parent type, defined by gender, first-birth year, age at first birth and matching characteristics. At each event time, each type is weighted by the number of its parents observed at birth, limiting changes in composition across event times. These synthetic histories also allow type fixed effects to absorb persistent differences in outcome levels across types.
The symmetric construction uses fewer post-birth parents than the baseline. A post-birth parent contributes to the pseudo-panel only if a parent of the same type is observed at birth. For example, if the parents observed at birth are drawn only from 2011 onward, symmetric matching cannot use post-birth outcomes of parents who gave birth before 2011, even when those outcomes are observed after 2011. The baseline construction still uses these cohorts at later event times. In the repeated-cross-section applications, I therefore include parents observed at birth from the first survey year, even if their full pre-birth history cannot be reconstructed. For these parents, pre-birth outcomes are imputed only for event times with available donors.
For gender $g$, define the synthetic type as $\theta=(F_\theta,\tilde a_\theta,X_\theta)$, containing first-birth year, exact age at first birth and the matching characteristics. Let $N^P_{\theta,g,0}$ be the number of its parents observed at birth. For each available event time, form the outcome
\[
\bar Y^{B,g}_{\theta,\tau}=
\begin{cases}
\bar Y^C_{(X_\theta,\,F_\theta+\tau)},&\tau<0,\\
\bar Y^P_\theta(\tau),&\tau\ge0.
\end{cases}
\]
The first line uses the same backward mapping as the baseline, and the second averages observed parents of that type. Each type’s mean outcome at each available event time is weighted by $W^g_{\theta,\tau}=N^P_{\theta,g,0}$, the number of parents observed at birth.\footnote{By the WLS equivalence of Section~\ref{sec:estimation}, this cell regression reproduces the regression on individual-level imputations in which each parent observed at birth carries the synthetic history of his or her type.} These weights replace changing post-birth parent counts in the baseline pseudo-panel. Let $\Theta^g_\tau$ denote the set of types included at event time $\tau$. The realized type share is then $N^P_{\theta,g,0}\mathbf1\{\theta\in\Theta^g_\tau\}/
\sum_{\kappa\in\Theta^g_\tau}N^P_{\kappa,g,0}.$
The share is constant only when the same types are included at every event time.
When the composition of observed types changes, persistent differences in their untreated outcomes can appear as changes caused by childbirth. Type fixed effects absorb these differences. Including type fixed effects, however, requires an additional restriction to identify the event-time coefficients. Because $t=F_\theta+\tau$, the type, year and event-time effects are linearly dependent. With only the base-period (e.g., $\tau^* = -2$) coefficient normalized to 0, adding $c(\tau+2)$ to every event-time coefficient, subtracting $ct$ from the year effects, and adding $c(F_\theta-2)$ to the type effects leaves all cell means estimated by the regression unchanged for any constant $c$. Footnote~12 of \citet{kleven2025child} raises this concern for individual fixed effects and argues that additivity makes separate identification feasible. It does not, as \citet[Section~2.3]{thakral2026child} establish for that case.
To identify the event-time coefficients, I set two pre-birth coefficients to zero. For instance, one can impose $\beta^g_{-3}=\beta^g_{-2}=0$ and estimate
\begin{equation}\label{eq:anchored-synth-fe}
\bar Y^{B,g}_{\theta,\tau}
=\alpha^g_\theta+
\sum_{k\notin\{-3,-2\}}\beta^{g}_k\mathbf1\{\tau=k\}
+\phi^g_{\tilde a_\theta+\tau}+\psi^g_{F_\theta+\tau}+u^g_{\theta,\tau},
\end{equation}
using the weights $W^g_{\theta,\tau}$. The two zero restrictions determine the event profile's level and linear trend. They require childbirth to have no effect at the restricted base periods.\footnote{Since each type fixes the individual's year of birth, $t-a=F_\theta-\tilde a_\theta$. For any constant $d$, adding $da$ to the age effects, subtracting $dt$ from the year effects and adding $d(F_\theta-\tilde a_\theta)$ to the type effects leaves both the event-time coefficients and the cell means estimated by the regression unchanged. Hence the two zero restrictions do not remove this dependence. The remaining collinearity is handled by choosing a linearly independent set of age, year and type indicators, without imposing further restrictions on the event-time coefficients.} The following conditions connect the constructed outcomes to population cell means and ensure a well-defined regression. Let $\mathcal R^{S,g} =\{(\theta,\tau):\tau\in\mathcal T,\ \theta\in\Theta^g_\tau\}$. For $r=(\theta,\tau)\in\mathcal R^{S,g}$, write $a_r=\tilde a_\theta+\tau$ and $t_r=F_\theta+\tau$.
\begin{assumption}[Representativeness of Observed Parents]\label{assu:sym-repr}
For every $r\in\mathcal R^{S,g}$ with $\tau\ge0$,
\[
\mathbb{E}[Y_{t_r} \mid r,\; \text{observed},\; g]
=
\mathbb{E}[Y_{t_r}(F_\theta) \mid r,\; g].
\]
\end{assumption}
\begin{assumption}[Symmetric Matching Regularity]\label{assu:sym-reg}
For every $r\in\mathcal R^{S,g}$, Assumption~\ref{assu:lln} holds and $N^P_{\theta,g,0}/N\to_p p^g_\theta>0$ for every included type, where $N$ is the number of clusters. For each regression considered, impose its zero restrictions on event-time coefficients and drop redundant age, year and type indicators. Each omitted indicator must be a linear combination of the retained fixed-effect indicators. Let $\mathbf d_r^{S,g}$ denote the resulting regressor vector. Assume that
\[
\frac{
\sum_{r\in\mathcal R^{S,g}}N^P_{\theta(r),g,0}\,
\mathbf d_r^{S,g}(\mathbf d_r^{S,g})'
}{
\sum_{r\in\mathcal R^{S,g}}N^P_{\theta(r),g,0}
}
\xrightarrow{p}Q^{S,g},
\qquad Q^{S,g}\succ0.
\]
\end{assumption}
\begin{prop}[Oracle Projection]\label{prop:sym-fe-oracle}
Let $\mu^{S,g,*}_r$ be the untreated pre-birth or treated post-birth population mean of $r$, and let Assumptions~\ref{assu:NA}--\ref{assu:CI} and~\ref{assu:sym-repr}--\ref{assu:sym-reg} hold. The event-time coefficient estimates and the cell means estimated by regression~\eqref{eq:anchored-synth-fe} converge to those of the weighted population projection
\begin{equation}\label{eq:anchored-synth-proj}
\min_{\alpha,\beta,\phi,\psi}\sum_{r\in\mathcal R^{S,g}}p^g_{\theta(r)}
\left(\mu^{S,g,*}_r-\alpha_{\theta(r)}
-\sum_{k\notin\{-3,-2\}}\beta_k\mathbf1\{\tau_r=k\}
-\phi_{a_r}-\psi_{t_r}\right)^2,
\end{equation}
which are unique even though the nuisance effects are not.
\end{prop}
As for the baseline regression, the coefficients recover causal effects if (i) each type's untreated mean is the sum of a type-specific constant and common age and year effects; and (ii) the treatment effect at each event time is the same across types. When treatment effects differ across types, part of that variation can be absorbed by the age and year effects. An event-time coefficient can then contain effects from different event times with weights that may be negative, so it need not equal an average effect at that event time. Appendix~\ref{app:bidirectional-comparisons} shows how the regression weights treatment effects and illustrates why its coefficients can differ from average effects, with or without type FE.
\subsection{A Fully Nonparametric Cohort-Time Estimator}\label{sec:np}
So far I have focused on alternative constructions of the pseudo-panel on which an additive regression is run. I now propose a nonparametric estimator that relies neither on backward or forward matching nor on the regression. Instead of imputing a parent's pre-birth outcome, it estimates parents' mean untreated current outcome from childless donors observed in the same year with the same characteristics, under a parallel-trends assumption as follows.
\begin{assumption}[Conditional Parallel Trends, CPT]\label{assu:CPT}
For all $s < f \le t$, and all $x$ in the common support of $X$ given $F=f$ and given $F>t$:
\begin{equation}\label{eq:CPT}
\mathbb{E}[Y_t(\infty) - Y_s(\infty) \mid F = f, \, X = x] = \mathbb{E}[Y_t(\infty) - Y_s(\infty) \mid F > t, \, X = x].
\end{equation}
\end{assumption}
Assumption~\ref{assu:CPT} is neither weaker nor stronger than Assumption~\ref{assu:PT} (PT). Equal cohort averages can hide within-cell differences that offset across cells. Conversely, equal trends within cells need not aggregate to equal cohort averages because each cohort differs in the distribution of $X$ and untreated trends vary with characteristics.\footnote{Write $\Delta_f(x)=\mathbb{E}[Y_t(\infty)-Y_s(\infty)\mid F=f,X=x]$ and $\Delta_{>t}(x)=\mathbb{E}[Y_t(\infty)-Y_s(\infty)\mid F>t,X=x]$. Assumption~\ref{assu:CPT} sets $\Delta_f(x)=\Delta_{>t}(x)$ for every $x$, but the cohort-level trends are $\sum_x\Pr(X=x\mid F=f)\Delta_f(x)$ and $\sum_x\Pr(X=x\mid F>t)\Delta_{>t}(x)$, which can differ when $\Pr(X=x\mid F=f)\neq\Pr(X=x\mid F>t)$ and $\Delta_f(x)$ varies with $x$.} Conditioning on covariates is the standard way to make parallel trends more credible when treated and control units differ in characteristics that predict their untreated trends \citep{heckman1997matching,santanna2020doubly,callaway2021difference}.
\begin{prop}[Conditional ATT]\label{prop:conditional ATT}
Let Assumptions~\ref{assu:NA}, \ref{assu:CI}, and \ref{assu:CPT} hold. For every cohort $f\ge2$, post-birth date $t\ge f$ and $x$ in the common support, the conditional cohort-time ATT is identified by a within-period comparison:
\begin{equation}\label{eq:np-identification}
\begin{aligned}
\text{ATT}_x(f,t) &:= \mathbb{E}[Y_t(f) - Y_t(\infty) \mid F = f, X=x] \\
&= \mathbb{E}[Y_t \mid F=f, X=x] - \mathbb{E}[Y_t \mid F > t, X=x].
\end{aligned}
\end{equation}
\end{prop}
The nonparametric estimator aggregates parent--donor differences across cohorts and types with the numbers of parents observed at birth as weights, as in symmetric matching and in the spirit of \citet{callaway2021difference}. Let $\theta = (X, \tilde{a})$ be a type defined by the discrete matching variables $X$ and exact age at first birth $\tilde{a}$. For cohort $f$, type $\theta$, and event time $\tau$, the current age is $a = \tilde{a} + \tau$ and the calendar year is $t = f + \tau$. The type-specific post-birth effect is
\[
\widehat{\text{ATT}}^g(f,\tau \mid \theta)
=
\bar{Y}^{P,g}_{f,\tau}(\theta) - \bar{Y}^{C,g}_{t}(X_\theta, \tilde{a}_\theta + \tau),
\qquad t = f + \tau,
\]
where $\bar{Y}^{P,g}_{f,\tau}(\theta)$ is the mean outcome of cohort-$f$ parents of gender $g$ and type $\theta$ observed at event time $\tau$, and $\bar{Y}^{C,g}_{t}(X_\theta, \tilde{a}_\theta + \tau)$ is the mean outcome of childless donors in the corresponding current-age/current-year cell. For a fixed set $\mathcal S_g$ of cohort--type pairs, common to all reported post-birth event times, define
\[
\hat q^g(f,\theta)=\frac{N^{P,g}_{f,\theta,0}}
{\sum_{(f',\theta')\in\mathcal S_g}N^{P,g}_{f',\theta',0}},
\qquad (f,\theta)\in\mathcal S_g,
\]
where $N^{P,g}_{f,\theta,0}$ is the number of cohort-$f$ parents of gender $g$ and type $\theta$ observed at birth. The aggregate is
\[
\widehat{\mathrm{ATT}}^g(\tau)=\sum_{(f,\theta)\in\mathcal S_g}
\hat q^g(f,\theta)\widehat{\mathrm{ATT}}^g(f,\tau\mid\theta).
\]
The scaled effect divides $\widehat{\mathrm{ATT}}^g(\tau)$ by the average of the donor means $\bar{Y}^{C,g}_{t}(X_\theta, \tilde{a}_\theta + \tau)$ under the same weights, which estimates the counterfactual level, and the scaled penalty is the difference between the scaled effects of men and women. When included types change over event time, I average the effects of the included types within each cohort, weighting by the numbers of parents observed at birth. I then average the included cohort effects using each cohort’s total number of parents observed at birth, including those from types unavailable at that event time (Appendix~\ref{app:analytical-implementation}). Proposition~\ref{prop:cell-clt} applies to the nonparametric estimator and its scaled penalty for inference because both are smooth functions of the cluster sums and counts.
This estimator has advantages over the standard pre-birth imputation approach. First, as its donors are contemporaneous, the estimator needs no pre-birth years for imputation. Parents observed in the first few years of the survey remain usable, which enlarges the sample.\footnote{For parents observed with first birth in the first survey year, date $f-1$ precedes the data. Proposition~\ref{prop:conditional ATT} then requires Assumptions~\ref{assu:NA}, \ref{assu:CI} and~\ref{assu:CPT} to hold from that date.} Second, it takes differences within cells and therefore does not extrapolate age and year effects through an additive regression. Third, it allows treatment effects to differ across cohorts and types. It estimates the effect of each cohort and type separately and averages them using positive weights constructed from the counts of parents observed at birth and normalized to sum to one. Hence it avoids the negative-weights problem in the baseline regression approach.
However, using contemporaneous donors also means that, at later event times, parents are compared with older childless individuals, who are more likely to be never-parents. These donors may have different untreated outcomes from parents. Assumptions~\ref{assu:CI} and~\ref{assu:CPT} may therefore be harder to justify at later event times. The pseudo-OLS regression instead uses donors at pre-birth ages, where the pool still contains many future parents, at the cost of imposing an additive specification.
\section{Monte Carlo Simulation}\label{sec:simulation}
Parents and childless individuals may differ in ways that matching variables cannot capture. The composition of parents observed can also change after birth, and treatment effects may differ across cohorts. I examine these problems by simulating individual fertility and outcome histories, including proxies for the unobserved characteristics that drive selection. I use these individual histories to compare panel and pseudo-panel estimates, examine when synthetic type FE help, assess the coverage of conventional, analytical and bootstrap confidence intervals, and measure computation time for individual-level pseudo-OLS and cell-level WLS. Appendix~\ref{app:sim-coverage-all} reports additional inference results for the remaining estimators.
\subsection{Benchmark Design and Selection}\label{sec:sim-design}
I generate Monte Carlo samples of $N=50{,}000$ people for $20$ years, $t=0,\ldots,19$. Gender and $X_i\sim\operatorname{Bernoulli}(0.5)$ are independently drawn, initial age is uniform on $\{22,\ldots,30\}$, and the latent individual component is $\alpha_i\sim N(0,1)$. Two observed continuous proxies are $V_{1i}=0.7\alpha_i+\eta_{1i}$ and $V_{2i}=0.5\alpha_i+\eta_{2i}$,
with independent $\eta_{1i}\sim N(0,0.5^2)$ and $\eta_{2i}\sim N(0,0.4^2)$. Untreated potential outcomes are computed by:
\[
Y^0_{it}=1.2+0.065a_{it}-0.0007a_{it}^2+0.16X_i
+0.018t+\zeta_t+0.70\alpha_i+\varepsilon_{it},
\]
where $\zeta_t\sim N(0,0.04^2)$ is a common calendar shock and $\varepsilon_{it}\sim N(0,0.25^2)$ is individual noise. The continuous proxies predict outcomes through their correlation with $\alpha_i$. For $t=2,\ldots,18$, the first-birth hazard is
\[
\Pr(F_i=t\mid F_i\geq t,X_i,\alpha_i,g_i)
=\operatorname{logit}^{-1}\{-2.1+0.18X_i-0.016(a_{it}-30)^2+\lambda_{g_i}\alpha_i\}.
\]
The female first-birth effect is $\pi_w(\tau)=-0.30(1-e^{-0.55(\tau+1)})$ and the male effect is $\pi_m(\tau)=0.02(1-e^{-0.45(\tau+1)})$ for $\tau\geq0$. Both are zero before birth. The positive male-minus-female penalty averages $0.28$ over event times 0 to 10. I call this the benchmark design, and use variations of the design for further simulations.
I use the event-time window $[-5,10]$. The panel and pseudo-panel regressions use first-birth cohorts $F_i=5,\ldots,9$, whose full event window falls inside the observation period. The nonparametric estimator (NP) retains the additional cohorts $F_i=2,3,4$ as it does not require pre-birth imputations. I match parents to donors based on gender, $X$, age and calendar year. I use the available cells at each event time, without requiring every type to be observed throughout the event window. Panel OLS uses parents’ observed outcome histories to estimate a regression with event-time, age and year indicators, omitting the indicator for $\tau=-2$. Panel FE additionally includes an individual fixed effect and normalizes the coefficients at $-3$ and $-2$ to zero. Pseudo-OLS, DR, and DR with cross-fitting (DR-CF) regress the constructed pseudo-panel outcomes on event-time, age and year indicators, omitting the indicator for $\tau=-2$. NP uses the contemporaneous donor comparison.
DR uses both continuous proxies. Within each gender, covariate cell, and pre-birth event time, its donor outcome model is
\begin{equation}\label{eq:sim-outcome}
m_c(V)=\alpha_c+b_1V_1+b_2V_2+b_3V_1^2+b_4V_1V_2,
\end{equation}
and its propensity model includes cell intercepts:
\begin{equation}\label{eq:sim-propensity}
\Pr(S=1\mid c,V)=\operatorname{logit}^{-1}(\gamma_c+\gamma_1V_1+\gamma_2V_2).
\end{equation}
DR-CF divides individuals into two folds, estimates both models on each fold and evaluates them using the other fold. All observations of an individual are assigned to the same fold, regardless of whether they appear as a parent or a donor.
I generate 500 replications in each of three scenarios: no selection with $(\lambda_m,\lambda_w)=(0,0)$, symmetric selection with $(0.25,0.25)$, and asymmetric selection with $(0.25,0.15)$. Under symmetric selection the donor bias is the same for both genders, so the biases cancel in the gender difference. Under asymmetric selection, positive selection into parenthood is stronger for men, so the bias does not cancel in the difference.
\begin{table}[htbp]
\centering
\setlength{\belowcaptionskip}{6pt}
\caption{Selection scenarios and estimation error}\label{tab:mc-summary}
\footnotesize
\setlength{\tabcolsep}{3pt}\begin{tabular}{lrrrrrrrrrrr}
\toprule
& \multicolumn{3}{c}{Selection gap} & \multicolumn{6}{c}{RMSE} & \multicolumn{2}{c}{Pseudo-OLS bias} \\
\cmidrule(lr){2-4}\cmidrule(lr){5-10}\cmidrule(lr){11-12}
Scenario & Men & Women & M$-$W & \shortstack{Panel\\OLS} & \shortstack{Panel\\FE} & \shortstack{Pseudo\\OLS} & NP & DR & DR-CF & $\tau=0$ & $\tau=5$ \\
\midrule
No selection & 0.000 & 0.000 & 0.000 & 0.053 & 0.042 & 0.045 & 0.011 & 0.051 & 0.051 & 0.001 & 0.002 \\
Symmetric & 0.370 & 0.371 & -0.001 & 0.051 & 0.044 & 0.045 & 0.011 & 0.050 & 0.050 & -0.001 & -0.002 \\
Asymmetric & 0.370 & 0.227 & 0.143 & 0.071 & 0.042 & 0.108 & 0.094 & 0.078 & 0.078 & 0.065 & 0.101 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} 500 replications with $N=50{,}000$. The selection gap is the difference in the mean of $\alpha_i$ between parents and childless individuals. RMSE is the root mean squared error of the unscaled penalty over event times 0--10, computed within each replication and averaged over replications. The last two columns report the bias of pseudo-OLS at event times 0 and 5.\end{minipage}
\end{table}
\begin{figure}[p!]
\centering
\includegraphics[width=\textwidth]{generated/main_history_20260912/profiles.pdf}
\caption{Scaled event-time paths in the simulations. Rows show the men-minus-women penalty, women and men. NP has no pre-birth path and is shown only after birth.}
\label{fig:sim-profiles}
\end{figure}
For each scenario, Table~\ref{tab:mc-summary} reports the selection gap (the difference in mean $\alpha_i$ between parents and individuals who remain childless throughout the observation period) by gender and the average root mean squared error (RMSE) of each estimator across the eleven post-birth event times, and over replications. Without selection, or with symmetric selection, every estimator is unbiased and they differ only in precision. Under asymmetric selection, pseudo-OLS acquires a bias, and DR lowers the RMSE by more than a quarter.\footnote{In a version of the asymmetric design with 30,000 people, the RMSE of DR rises from 0.086 to 0.111, the value for pseudo-OLS in that design, as the proxy loadings fall from $(0.7,0.5)$ to zero, so the gain from DR depends on how informative the covariates are about $\alpha_i$, and uninformative covariates do no harm in this design. Cross-fitting gives the same results.} Panel OLS is also biased in the same direction, and its bias grows with event time. The mean of $\alpha_i$ differs across first-birth cohorts. At a given calendar year, parents who had their first child earlier are observed at later event times. Comparisons across event times therefore also involve comparisons across first-birth cohorts with different average $\alpha_i$. Panel FE removes this bias and has the lowest RMSE among the regression estimators in every scenario.
Figure~\ref{fig:sim-profiles} reports the scaled penalties and the separate effects for women and men. Under symmetric selection, pseudo-OLS shifts both women's and men's estimated effects upward, understating women's loss and overstating men's gain. The biases cancel in the unscaled gender difference, but the scaled penalty remains above the true value because the counterfactual means used as denominators are underestimated.
\subsection{Type Fixed Effects and Heterogeneous Treatment Effects}\label{sec:sim-type-fe}\label{app:sim-fixed-cell}
I first examine the role of type FE when untreated outcome levels differ across types. I use the benchmark design without selection. I add a type-specific constant, \(\lambda h(B_i)\), to women's untreated outcomes. Here \(B_i\) is the individual's year of birth. I use a quadratic function so that age and year fixed effects alone cannot absorb these differences across types. The function is standardized to have mean zero and variance one, so \(\lambda\) measures the standard deviation of the added constant across types.\footnote{With initial ages uniform on $\{22,\ldots,30\}$, the years of birth are $B_i\in\{-30,\ldots,-22\}$ and $h(B_i)=\{(B_i+26)^2-20/3\}/\sqrt{308/9}$. I use $\lambda\in\{0,0.2,0.4,0.6\}$.} The level is identical for a parent and her matched donors, who share her age and calendar year, so the donor comparison remains valid and the effect on women is unchanged. I use the same 500 simulated samples for every value of $\lambda$.
\begin{table}[htbp]
\centering
\caption{Persistent type levels and type fixed effects}\label{tab:fe-type-benefit}
\small\setlength{\tabcolsep}{6pt}\begin{tabular}{@{}lrrrr@{}}
\toprule
& \multicolumn{2}{c}{Pseudo-OLS / Sym} & \multicolumn{2}{c}{Sym+FE} \\
\cmidrule(lr){2-3}\cmidrule(lr){4-5}
Type-level SD ($\lambda$) & Bias & RMSE & Bias & RMSE \\
\midrule
0.0 & 0.003 & 0.050 & 0.002 & 0.046 \\
0.2 & 0.012 & 0.052 & 0.002 & 0.046 \\
0.4 & 0.022 & 0.059 & 0.002 & 0.046 \\
0.6 & 0.032 & 0.068 & 0.002 & 0.046 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} 500 replications with $N=50{,}000$. Unscaled 0--10 average with true value 0.28. Sym+FE fixes $-3,-2$ and the other regressions omit $-2$.\end{minipage}
\end{table}
Table~\ref{tab:fe-type-benefit} reports the bias and RMSE of the average penalty for increasing values of $\lambda$. The bias of pseudo-OLS grows with $\lambda$ and reaches 0.032 at $\lambda=0.6$, because additive age and year effects cannot absorb the type-specific level.\footnote{Symmetric matching without FE (Sym) gives the same estimates as pseudo-OLS here, because the parents observed at birth are observed at every later event time and no compositional change occurs.} These biases arise even when every parent is observed at every event time. I also shorten the observation period by discarding the last four survey years, so that only earlier first-birth cohorts remain observable at later event times. At \(\lambda=0.6\), the bias of pseudo-OLS and Sym increases from 0.032 to 0.040.
Sym+FE absorbs the added levels exactly through type fixed effects, so its penalty estimates do not change with $\lambda$. Adding type fixed effects requires estimating a separate intercept for each type and identifying event-time effects from changes within types. This can reduce precision when few observations are available for each type. However, in this design, the type FE cost no precision. With or without added levels, the RMSE of Sym+FE is lower than that of pseudo-OLS. The 90 types per gender have about 78 parents observed at birth on average.
I next allow treatment effects to differ across first-birth cohorts, using the benchmark design without selection and with no added type levels ($\lambda=0$). I multiply women's post-birth effects by 0.5, 0.75, 1, 1.25 and 1.5 for cohorts $F=5,\ldots,9$, respectively, and leave men's effects unchanged. All estimators, including NP, use these same cohorts. Every parent is observed at every event time.
\begin{table}[htbp]
\centering
\caption{Matching regressions and cohort heterogeneity}\label{tab:bidirectional-mc}
\small\setlength{\tabcolsep}{4pt}\begin{tabular}{@{}lrrrrrr@{}}
\toprule
& \multicolumn{2}{c}{Pseudo-OLS / Sym} & \multicolumn{2}{c}{Sym+FE} & \multicolumn{2}{c}{NP} \\
\cmidrule(lr){2-3}\cmidrule(lr){4-5}\cmidrule(lr){6-7}
Design & Bias & RMSE & Bias & RMSE & Bias & RMSE \\
\midrule
Common effect & 0.003 & 0.050 & 0.002 & 0.046 & -0.001 & 0.015 \\
Heterogeneous effects & -0.313 & 0.317 & -0.299 & 0.303 & -0.001 & 0.015 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} 500 replications with $N=50{,}000$. All estimators use first-birth cohorts 5--9. Errors are measured against their common ATT, averaged over event times 0--10 in unscaled units: 0.280 with common effects and 0.257 with heterogeneous effects. Sym+FE fixes $-3,-2$; pseudo-OLS and Sym omit $-2$.\end{minipage}
\end{table}
As reported in Table~\ref{tab:bidirectional-mc}, all estimators have little bias under common effects. With heterogeneous effects, the biases of pseudo-OLS and Sym are $-0.313$ and that of Sym+FE is $-0.299$, against an average true penalty of 0.257. The estimated penalties are therefore negative even though the true penalty is positive in every cohort. Type FE cannot absorb differences in treatment effects that begin at birth. NP shows no bias in either case and a low RMSE of 0.015 with heterogeneous effects, which it is designed to accommodate.
\subsection{Inference from Complete Histories}\label{sec:sim-coverage}
I examine whether confidence intervals using analytical inference attain their nominal coverage for pseudo-OLS and NP when complete histories are available. The data are generated from the benchmark design without the continuous proxies, with $N=10{,}000$ people and 500 replications under either no or symmetric selection. I compare three inference methods for pseudo-OLS: heteroskedasticity-robust standard errors from the individual-level pseudo-panel regression, the analytical inference of Proposition~\ref{prop:cell-clt}, and a cluster bootstrap that resamples complete individual histories with 199 bootstrap samples per replication. NP is assessed with the analytical and bootstrap standard errors. The 95\% confidence intervals are computed for the average unscaled penalty across event times from $0$ to $10$.
\begin{table}[htbp]
\centering
\caption{Coverage of 95\% confidence intervals for pseudo-OLS and NP}\label{tab:coverage}
\footnotesize\setlength{\tabcolsep}{3pt}\begin{tabular}{@{}llcccccc@{}}
\toprule
& & \multicolumn{3}{c}{No selection} & \multicolumn{3}{c}{Symmetric selection} \\
\cmidrule(lr){3-5}\cmidrule(lr){6-8}
Estimator & Variance estimate & SD & Mean SE & Cov. (\%) & SD & Mean SE & Cov. (\%) \\
\midrule
Pseudo-OLS & Robust SE & 0.112 & 0.039 & 51.0 & 0.115 & 0.039 & 47.4 \\
& Analytical SE & 0.112 & 0.113 & 94.4 & 0.115 & 0.111 & 94.8 \\
& Cluster bootstrap & 0.112 & 0.113 & 94.8 & 0.115 & 0.112 & 94.2 \\
\addlinespace
NP & Analytical SE & 0.025 & 0.027 & 96.6 & 0.027 & 0.026 & 94.4 \\
& Cluster bootstrap & 0.025 & 0.027 & 96.4 & 0.027 & 0.026 & 95.0 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} 500 replications with $N=10{,}000$. The target is the unscaled penalty averaged over event times 0--10. SD is the standard deviation of the estimates across replications, Mean SE is the average estimated standard error, and Cov.\ is the coverage of the 95\% confidence interval. Robust SE is the heteroskedasticity-robust standard error of the individual-level regression. The cluster bootstrap resamples complete person histories with 199 bootstrap samples.\end{minipage}
\end{table}
Table~\ref{tab:coverage} reports the Monte Carlo dispersion of the estimate, the mean standard error from each method and the coverage of the resulting confidence intervals. Confidence intervals based on robust standard errors from the individual-level pseudo-panel regression cover the truth only about half of the time. Confidence intervals based on the analytical inference and the cluster bootstrap both attain nominal coverage, for NP as well as for pseudo-OLS, and they agree with each other. Coverage is unchanged under symmetric selection. Appendix~\ref{app:sim-coverage-all} applies the analytical inference to DR, Sym+FE and the scaled penalty. Coverage is between 94\% and 97\%, except for the scaled NP penalty under symmetric selection.
\subsection{Selective Response and Compositional Drift}\label{sec:sim-symmetric}
In the benchmark design without selection on $\alpha_i$, I allow parents in first-birth cohorts 2--9 not to respond to survey waves from time to time. At event times $\tau=1,\ldots,10$, their response probability is $\operatorname{logit}^{-1}\{3-0.5\tau+2X_i+\mathbf1(\tilde a_i>27)\}$. Conditional on $X_i$ and age at first birth, responses are independent across waves, so a parent can return after missing a wave. All outcomes at and before childbirth and all donor observations remain available.
I consider three scenarios. In S1, all parents respond in every wave, and treatment effects at each event time are the same across types within each gender. S2 introduces selective nonresponse and retains homogeneous effects. S3 additionally allows women’s treatment effects to depend on $X_i$ and age at first birth:
\[
\pi_w(\tau,X_i,\tilde a_i)=
[-0.45+0.35X_i+0.18\cdot\mathbf1(\tilde a_i>27)](1-e^{-0.55(\tau+1)}).
\]
Parents with $X_i=1$ or an age at first birth above 27 are more likely to respond and have smaller penalties. Panel OLS, Panel FE, pseudo-OLS, Sym and Sym+FE all use first-birth cohorts 5–9. I estimate the two panel regressions using all available observations and, separately, only parents observed at every post-birth event time. For NP, I report estimates using cohorts 2–9 and the common cohorts 5–9.
\begin{table}[htbp]
\centering
\caption{Selective response and heterogeneous effects}\label{tab:symmetric-sim}
\small\setlength{\tabcolsep}{6pt}\begin{tabular}{@{}lrrrr@{}}
\toprule
& \multicolumn{1}{c}{S1} & \multicolumn{1}{c}{S2} & \multicolumn{2}{c}{S3} \\
\cmidrule(lr){2-2}\cmidrule(lr){3-3}\cmidrule(lr){4-5}
Estimator & RMSE & RMSE & RMSE & Bias (in S3) \\
\midrule
Panel OLS & 0.061 & 0.061 & 0.063 & -0.010 \\
Panel OLS, balanced & 0.061 & 0.130 & 0.183 & -0.128 \\
Panel FE & 0.046 & 0.046 & 0.046 & 0.005 \\
Panel FE, balanced & 0.046 & 0.099 & 0.169 & -0.137 \\
\addlinespace
Pseudo-OLS & 0.051 & 0.051 & 0.054 & -0.012 \\
NP (cohorts 2--9) & 0.011 & 0.011 & 0.022 & 0.018 \\
NP (cohorts 5--9) & 0.015 & 0.015 & 0.015 & -0.001 \\
Sym & 0.051 & 0.052 & 0.056 & 0.019 \\
Sym+FE & 0.047 & 0.048 & 0.050 & 0.015 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} 500 replications with $N=50{,}000$. RMSE and bias of the unscaled penalty averaged over event times 0--10, relative to the full population of first-birth cohorts 5--9. S1 has full response and common effects, S2 selective response and common effects, and S3 selective response and heterogeneous effects. In S2 and S3, cohorts 2--9 follow the same response rule. The balanced versions keep only parents who respond at every post-birth event time. Panel FE and Sym+FE fix the coefficients at $-3$ and $-2$.\end{minipage}
\end{table}
Table~\ref{tab:symmetric-sim} reports RMSE and bias relative to the average penalty of the full parent population in cohorts 5--9. In S3, selective nonresponse lowers the average penalty among respondents by 0.027, but all estimators using the unbalanced data have absolute biases below 0.02. Pseudo-OLS has a lower RMSE than Panel OLS in all three scenarios. On the common cohorts, NP has an RMSE of 0.015 in all three scenarios and a bias of $-0.001$ in S3. Balancing the panel excludes more than three quarters of parents and disproportionately retains those with smaller penalties. Both panel regressions then underestimate the full-population penalty by about 0.13.
\subsection{Computational Comparison}\label{sec:sim-computation}
Lastly, I compare the regression time of individual-level pseudo-OLS and cell-level WLS as the sample size and the number of matching categories increase. I modify the benchmark design so that first-birth probabilities depend only on age. The matching covariate has $K$ equally sized categories. At a given sample size, I vary $K$ while keeping each individual's fertility and outcome histories fixed, so that only the matching partition changes.
\begin{table}[htbp]
\centering
\caption{Regression time of the individual-level and cell-level regressions}\label{tab:timing}
\footnotesize\setlength{\tabcolsep}{5pt}\begin{tabular}{@{}rrrrrrr@{}}
\toprule
& & \multicolumn{2}{c}{Regression rows} & \multicolumn{2}{c}{Seconds} & Time ratio \\
\cmidrule(lr){3-4}\cmidrule(lr){5-6}
People $N$ & $K$ & Individual & Cell & Individual & Cell & \\
\midrule
\multicolumn{7}{l}{\emph{A. Increasing people, $K=4$}} \\
10,000 & 4 & 43,840 & 5,744 & 0.044 & 0.024 & 1.8 \\
25,000 & 4 & 108,240 & 5,760 & 0.086 & 0.024 & 3.6 \\
50,000 & 4 & 214,320 & 5,760 & 0.158 & 0.024 & 6.6 \\
100,000 & 4 & 430,224 & 5,760 & 0.297 & 0.024 & 12.4 \\
200,000 & 4 & 865,664 & 5,760 & 0.612 & 0.024 & 25.5 \\
\midrule
\multicolumn{7}{l}{\emph{B. Increasing matching categories, $N=50{,}000$}} \\
50,000 & 2 & 214,320 & 2,880 & 0.157 & 0.019 & 8.5 \\
50,000 & 4 & 214,320 & 5,760 & 0.158 & 0.024 & 6.6 \\
50,000 & 8 & 214,320 & 11,520 & 0.155 & 0.035 & 4.4 \\
50,000 & 16 & 214,320 & 22,976 & 0.153 & 0.056 & 2.7 \\
50,000 & 32 & 214,320 & 44,896 & 0.154 & 0.096 & 1.6 \\
50,000 & 64 & 214,320 & 80,400 & 0.157 & 0.166 & 0.9 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.35em}\footnotesize\textit{Notes:} Medians of six runs on one thread. $N$ is the number of people, and the data contain $20N$ person-year records. $K$ is the number of categories of the matching covariate. Times cover the regressions for both genders and the scaling, and exclude data preparation and inference. The time ratio is individual over cell.\end{minipage}
\end{table}
Table~\ref{tab:timing} reports the number of observations used in each regression and the computation time. Panel A increases the number of people from 10,000 to 200,000 at $K=4$. Panel B varies $K$ from 2 to 64 at $N=50{,}000$. Both regressions use the window $[-5,10]$, the base period $-2$, and the same parents and donors. The computational advantage of WLS grows with sample size. At a fixed $K$, the number of cells remains nearly constant, while the number of individual observations increases with the number of parents. Finer matching categories create more cells and reduce this advantage. At $K=64$, the two regressions take about the same time.
\section{Empirical Application: Child Penalties in Korea}\label{sec:empirical}
I apply the proposed estimators to three Korean survey datasets and estimate the child penalties for employment and earnings. Korea provides an interesting setting. It has the largest gender wage gap among OECD countries \citep{oecd2026korea}, and offers both a long-running household panel and several repeated cross-sectional surveys. Korea is also the country with the largest child penalty and the largest gap between pseudo-panel and panel estimates in the validation of \citet[Figure~3]{kleven2025atlas}.
For the panel validation, I use the 2006--2024 waves of the Korean Labor and Income Panel Study (KLIPS), an annual household panel run by the Korea Labor Institute. It follows household members aged 15 and over, recording their employment and earnings over time. I also use two repeated cross-sectional surveys. The Household Income and Expenditure Survey (HIES), conducted by Statistics Korea, collects information on household income and spending. The Household Finance and Living Conditions Survey (HFLC) interviews around 20,000 households annually about their assets, debts and income, as well as the employment of household members. The samples cover 2006--2025 for HIES and 2012--2025 for HFLC.
\subsection{Implementation}\label{sec:empirical-data}
In KLIPS, the first-birth year comes from the respondent's direct report and, when there is none, from the earliest birth year of an own child in the household roster. I exclude respondents who report different first-birth years across waves and those whose roster child was born at least two years before the reported first birth.\footnote{Dating the excluded respondents from the roster changes either penalty by at most 0.09 percentage points. Excluding respondents who reported no previous birth although an own child was listed in the household roster in the same wave changes the employment and earnings penalties by at most 0.51 and 0.80 percentage points, respectively.} Employment equals one for respondents who worked in the week before the interview or were temporarily absent from a job. Event time is the number of years since childbirth at the interview. For matching, I subtract event time from the survey year and the parent's age to obtain cohort year and age at birth. Earnings are annual pretax labor income for the preceding calendar year, deflated to 2020 prices using the consumer price index. Event time for earnings is therefore computed based on income year. The earnings sample includes respondents with zero labor income. The donor pool includes observations before the assigned first-birth year. It also includes respondents without an assigned birth year whose most recent fertility response, as of the interview, indicates no previous birth.
HIES and HFLC record household heads and spouses. I infer the first-birth year from the age of the oldest unmarried child in the household roster, and use respondents with no such child as donors.\footnote{The HIES roster includes only co-resident children, whereas HFLC also records children living apart for work or study. In HIES, I also exclude donors with reported nonresident unmarried children. Birth years inferred from children's ages in whole years can be off by one year.} HFLC provides annual records with household identifiers. For HIES employment, I use the annual file, whereas for earnings I use monthly average labor income from the quarterly files. This is because the annual files contain no individual labor income from 2017 onward.\footnote{Household serial numbers do not link the two sets of files. Re-estimating the pseudo-OLS and DR employment penalties on the quarterly files changes them by less than two percentage points.}
As in the simulations, the event window is $[-5,10]$ with base period $-2$. I use two years before birth as the base period because employment may already change during pregnancy in the year before birth. I study first births at ages 20--45, use pre-birth donors aged 15--45, and follow parents up to age 55. Following \citet{kleven2025child}, I use parent observations from five years after each survey begins for pseudo-OLS and DR: 2011 in KLIPS and HIES, and 2017 in HFLC. In KLIPS, I also restrict first births to 2011 onward. The KLIPS panel regression applies the same first-birth cohort restriction, keeps all pre-birth observations, and requires at least one outcome before and one after birth.
For matching, I use two covariate resolutions. \textit{Coarse} cells are defined by gender, age, survey year and marital status or spouse presence, and \textit{fine} cells further condition on education in four broad categories.\footnote{The categories are below elementary school, elementary or middle school, high school or two-year college, and university or above in KLIPS, and below high school, high school, college or university, and graduate school in HIES and HFLC. Observations without a matching variable are dropped.} In KLIPS, parents observed at birth for both outcomes are interviewed less than one year after the first birth. Table~\ref{tab:data-summary} reports the survey years, the numbers of household interviews, parents observed at birth and donor records, and the share of those parents with donors one year before birth. Nearly all parents are matched with coarse cells, and adding education to the cell definition lowers the match rate by 1 to 5 percentage points.
\begin{table}[t]
\centering
\caption{Data and estimation samples}\label{tab:data-summary}
\footnotesize
\begin{tabular}{llrrrr}
\toprule
Survey & Years & \shortstack{Household\\interviews/year} & \shortstack{Parents at\\birth (W/M)} & Donors & \shortstack{Match rate\\(coarse / fine)} \\
\midrule
KLIPS & 2006--2024 & 4,999--12,132 & 970 / 972 & 45,539 & 96.1\% / 92.0\% \\
HIES & 2006--2025 & 8,947--13,529 & 1,413 / 1,352 & 33,888 & 99.2\% / 95.6\% \\
HFLC & 2012--2025 & 17,863--19,744 & 820 / 793 & 33,099 & 99.6\% / 98.5\% \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.3em}\footnotesize\textit{Notes:} Employment samples for pseudo-OLS and DR. Parent counts (women/men) and donor counts are observations pooled across years using coarse cells. For Sym and Sym+FE, the parent counts are 2,154/2,068 in HIES and 1,896/1,850 in HFLC; KLIPS is unchanged. The match rate is the share of parents observed at birth with at least one donor one year before birth.\end{minipage}
\end{table}
I apply the DR correction in KLIPS using additional covariates including detailed education (the survey's original attainment code with nine levels), urban residence, province and the spouse age gap. I use detailed education in HIES, and detailed education, metropolitan residence and the spouse age gap in HFLC. The correction is applied within coarse cells, because the median number of donors per fine cell is only 4 to 11 (Appendix Table~\ref{tab:dr-overlap}). Province is excluded from the propensity model because some province categories contain only parents or only donors within matching cells.
Symmetric matching with type fixed effects (Sym+FE) weights each type by its number of parents observed at birth. Parents observed after birth are included only if their type is also represented at birth. If I excluded parents observed at birth in the first five years, all later observations of those first-birth cohorts would also be excluded. Together with other types not represented at birth, this would remove 45\% of the post-birth employment observations used by pseudo-OLS in HIES and 69\% in HFLC. For symmetric matching in HIES and HFLC I therefore include parents observed at birth or after birth from the first survey year onward. I impute pre-birth outcomes whenever matching donors are available. With coarse cells, symmetric matching then has 93--97\% as many post-birth records as pseudo-OLS and includes 77--82\% of the post-birth records used by pseudo-OLS. NP compares parents with childless donors of the same age and matching characteristics in the same survey year. I therefore extend the donor age limit to 55. NP excludes first-birth cohorts with fewer than two parents observed at birth. In KLIPS, both Sym+FE and NP use first births from 2011 onward, matching the panel's cohort restriction.
I report both unscaled and scaled penalties, averaged over event times $0$--$10$. Standard errors are computed using the analytical variance formulas in Propositions~\ref{prop:cell-clt} and~\ref{prop:dr-inference}. I define a cluster for inference as a set of respondents connected by person or household identifiers across waves in KLIPS, a household in HFLC, and a household--year for employment or a household--quarter for earnings in HIES.
\subsection{Estimation Results}\label{sec:empirical-results}\label{sec:empirical-klips}\label{sec:empirical-rcs}
\begin{table}[t]
\centering
\caption{KLIPS child penalties: estimation window $[-5,10]$}\label{tab:klips}\label{tab:balanced-sensitivity}
\footnotesize\setlength{\tabcolsep}{4pt}\begin{tabular}{@{}lrrrr@{}}
\toprule
& \multicolumn{2}{c}{Employment} & \multicolumn{2}{c}{Annual earnings} \\
\cmidrule(lr){2-3}\cmidrule(lr){4-5}
Estimator & Unscaled (SE) & Scaled (SE) & Unscaled (SE) & Scaled (SE) \\
\midrule
\multicolumn{5}{l}{\emph{Actual-panel estimators, first births from 2011}} \\
Panel OLS & 0.389 (0.036) & 46.9\% (2.94) & 2,014 (190) & 65.6\% (4.96) \\
Balanced [-5,10] & 0.797 (0.229) & 66.3\% (7.94) & 3,282 (1,880) & 126.2\% (133.61) \\
Balanced [-2,10] & 0.747 (0.196) & 70.1\% (10.67) & 3,149 (1,458) & 114.3\% (79.75) \\
Balanced [-2,5] & 0.407 (0.060) & 48.5\% (4.34) & 2,201 (354) & 72.3\% (9.90) \\
\addlinespace
\multicolumn{5}{l}{\emph{Pseudo-panel estimators}} \\
Pseudo-OLS (fine) & 0.315 (0.027) & 42.1\% (2.53) & 1,861 (158) & 64.7\% (4.26) \\
Pseudo-OLS (coarse) & 0.291 (0.027) & 40.1\% (2.62) & 1,756 (164) & 62.2\% (4.46) \\
DR (coarse) & 0.296 (0.027) & 40.5\% (2.60) & 1,834 (155) & 64.1\% (4.22) \\
Sym+FE & 0.298 (0.077) & 41.1\% (6.90) & 1,862 (405) & 65.4\% (11.91) \\
NP (fine) & 0.266 (0.023) & 37.9\% (2.62) & 1,122 (197) & 46.9\% (5.33) \\
NP (coarse) & 0.240 (0.026) & 35.4\% (2.97) & 970 (187) & 42.5\% (5.32) \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.3em}\footnotesize\textit{Notes:} First births from 2011. Men-minus-women penalties averaged over event times 0--10, with base period $-2$. Sym+FE also fixes the coefficient at $-3$. Unscaled employment penalties are differences in employment rates, and unscaled earnings penalties are in 10,000 won at 2020 prices. Standard errors of the scaled penalties are in percentage points. Balanced $[a,b]$ keeps parents observed at or before $a$ and at or after $b$. The four panel rows use 870/827, 116/115, 195/208 and 455/440 women/men for employment and 944/903, 111/107, 201/200 and 490/471 for earnings.\end{minipage}
\end{table}
Table~\ref{tab:klips} reports the estimated penalties in KLIPS. Pseudo-OLS with fine cells gives penalties close to the panel estimates for both outcomes.\footnote{I also estimate the panel regression with individual FE, which performs well in the simulations. Here it is imprecise and gives penalties of 37.4\% (SE 9.84) for employment and 27.9\% (SE 11.60) for earnings. I normalize the coefficients at $-3$ and $-2$ to zero. The estimates are sensitive to these restrictions, and the panel shows strong pre-birth trends for both men and women.} Relative to fine-cell pseudo-OLS, pseudo-OLS with coarse cells gives slightly lower penalties, while DR and Sym+FE give similar penalties for both outcomes. Sym+FE has a standard error about three times as large as those of the other estimators.\footnote{With type FE, the restrictions at $-3$ and $-2$ identify the linear trend in the event-time coefficients. Sampling error in the donor means at these dates and in the numbers of parents observed at birth used as weights affects the post-birth coefficients.} These estimates lie within the panel's 95\% confidence intervals, except for the employment estimates from coarse-cell pseudo-OLS and DR. NP employment penalties are close to the other estimates, although the fine- and coarse-cell estimates fall 3.2 and 5.7 percentage points below the lower bound of the panel's confidence interval. For earnings, NP estimates substantially lower penalties.\footnote{With fine cells, pseudo-OLS estimates that fathers' earnings rise by 16.8\% after the first birth and NP estimates 4.5\%. Mothers' losses are estimated at 47.9\% and 42.3\%, respectively. The gap for fathers arises because childless men of the same age in the same year earn more than the counterfactual that the regression extrapolates from pre-birth donors.} As in the simulations, balancing the panel can sharply reduce the sample and substantially change the estimate. Requiring $[-2,10]$ leaves only around 200 parents of each gender from the earliest cohorts, raises the employment penalty to 70.1\% and makes the earnings penalty insignificant. The shorter window $[-2,5]$ keeps about half of the parents and stays close to the unbalanced estimate.
\begin{table}[t]
\centering
\caption{Repeated-cross-section child penalties: $[-5,10]$}\label{tab:rcs-results}
\footnotesize
\begin{tabular}{lcccccc}
\toprule
& \multicolumn{2}{c}{HFLC employment} & \multicolumn{2}{c}{HIES employment} & \multicolumn{2}{c}{HIES earnings} \\
\cmidrule(lr){2-3}\cmidrule(lr){4-5}\cmidrule(lr){6-7}
Estimator & Scaled & SE & Scaled & SE & Scaled & SE \\
\midrule
Pseudo-OLS (fine) & 32.0\% & 2.1 & 33.5\% & 1.5 & 49.7\% & 1.3 \\
Pseudo-OLS (coarse) & 30.9\% & 2.0 & 33.3\% & 1.4 & 51.1\% & 1.3 \\
DR (coarse) & 32.3\% & 2.0 & 34.3\% & 1.4 & 51.1\% & 1.3 \\
Sym+FE & 37.5\% & 5.2 & 35.1\% & 6.5 & 59.8\% & 4.4 \\
NP (fine) & 26.7\% & 2.0 & 32.6\% & 1.3 & 52.6\% & 1.6 \\
NP (coarse) & 27.1\% & 1.8 & 32.4\% & 1.3 & 56.0\% & 1.6 \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.3em}\footnotesize\textit{Notes:} Scaled penalties in percent, averaged over event times 0--10, with analytical standard errors in percentage points. Sym+FE fixes the coefficients at $-3$ and $-2$. Sym+FE and NP use parents from the first survey year.\end{minipage}
\end{table}
For the two repeated cross-sections, Table~\ref{tab:rcs-results} reports the penalties. Pseudo-OLS and DR estimates for employment penalties are 31--34\% in both surveys, below the KLIPS estimates, and move by less than two percentage points with the cell specification or the DR adjustment. HIES earnings penalties are about 50\%. NP is close to the other estimates for HIES employment, 4 to 5 percentage points lower in HFLC and up to 5 percentage points higher than pseudo-OLS for HIES earnings. Sym+FE is again imprecise, with standard errors about two and a half to four and a half times those of pseudo-OLS.\footnote{Relative to Sym on the same coarse cells, the employment SE increases by factors of 2.6 in KLIPS, 5.0 in HIES and 3.0 in HFLC. HIES and HFLC have larger samples of parents observed at birth and smaller absolute SEs.}
Figure~\ref{fig:klips} plots the scaled event-time coefficients for the three surveys. In the KLIPS panel, women's employment falls by almost 50\% in the birth year and recovers only slightly over the next decade, while men's employment rises slightly after birth. The pseudo-panel estimators trace similar post-birth paths, but after the first few years they generally lie above the panel for both genders.\footnote{Averaged over years 0--10, pseudo-OLS estimates women's loss at 41.1\% against 46.2\% in the panel and men's gain at 1.0\% against 0.7\%.} Both shifts are upward, so they partly offset in the gender difference. The repeated cross-sections show similar patterns. Women's outcomes drop by 37--67\% in the birth year and then recover partly, faster than in KLIPS. The estimators agree for women and differ for men. Sym+FE estimates a larger post-birth rise for men, up to 8\% for HIES employment and 18\% for HIES earnings, which is why its penalty estimates are larger than the others.
Pseudo-panel methods estimate different pre-birth behaviors from the actual panel. In the KLIPS panel, men's employment rises over the five years before birth, while women's falls, by 24\% in the year before birth alone. Among parents whose year of marriage is observed in KLIPS, 56\% have their first child in the year of marriage or the year after, so for most parents the years before birth are the years of marriage and pregnancy. Men's employment rises from 92\% to 95\% around marriage, regardless of when the first birth occurs. Women's employment falls near marriage mainly when they have their first birth soon, from 81\% to 40\% for women who give birth in the year of marriage or before and from 87\% to 81\% for women who give birth two or more years later (Appendix~\ref{app:marriage}). The pseudo-panel shows no such patterns. Its donors are matched on the parents’ marital status at birth and are therefore mostly married. With fine cells, women’s imputed employment rate two years before birth is 67\%, already lower than the 76\% observed in the panel.
\begin{figure}[p]
\centering
\includegraphics[width=\linewidth,height=.83\textheight,keepaspectratio]{generated/main_bidirectional_20260911/event_profiles.pdf}
\caption{Scaled event-time paths in the panel and the pseudo-panel. The window is $[-5,10]$ with base period $-2$, and Sym+FE also fixes $-3$. Pseudo-OLS uses fine cells, and DR and Sym+FE coarse cells.}\label{fig:klips}
\end{figure}
In sum, I revisit the country with the largest discrepancy between panel and pseudo-panel estimates in the validation of \citet{kleven2025atlas}. In my KLIPS sample, the pseudo-panel estimates are close to the average panel penalties.\footnote{My sample differs from theirs in the survey years, the first-birth cohorts and the employment measure, so my results are not directly comparable to theirs.} Women's employment in the panel begins to fall before birth, while the pseudo-panel places most of the decline at birth. Measured relative to two years before birth, the average post-birth penalties are nevertheless close to each other. The Japanese panel in \citet[Figure~3D]{kleven2025atlas} also shows similar average penalties despite differences in the pre-birth estimates.
\subsection{Robustness Analysis}\label{sec:empirical-robustness}
To assess the robustness of the headline results, I conduct seven additional analyses, each changing one element of the pseudo-panel implementation: the donor pool, the DR specification, the composition of parents, the event window, the cohorts used by NP, the survey weights and the method of inference. I also report the penalties by subgroup.
\emph{Donor pool.} The donor pool has two distinct groups, future parents and never-parents. One might suspect that future parents are a more comparable control group than never-parents. In Appendix~\ref{app:future-never}, using the KLIPS panel, I compare donors with an observed later birth and donors observed to remain childless through age 45. Within cells defined by age, year, marital status, education and urban residence, future fathers are 8.7 percentage points (SE 4.2) more likely to work and earn 5.0 million won (SE 2.2 million) more per year than men who remain childless, while the differences for women are statistically insignificant. Using fine cells and keeping the same parents and pre-birth event times, restricting donors to respondents with an observed later birth lowers the pseudo-OLS employment penalty from 42.1\% to 41.8\% and lowers the earnings penalty from 65.8\% to 65.7\%. The corresponding DR estimates fall from 41.5\% to 40.9\% and from 66.1\% to 65.4\%. All these changes are smaller than two percentage points.
\emph{DR specification.} The DR estimates are not sensitive to the model specification. Across five outcome and propensity specifications the KLIPS employment penalty stays at 40.5--40.7\%.\footnote{The specifications include a saturated or a cubic-age, linear-year outcome model with propensity scores on detailed education and urban residence, on broad education and urban residence, or on detailed education alone, and one uses the outcome model only.} Dropping the spouse age gap from both models changes the KLIPS penalties from 40.5\% to 40.8\% for employment and from 64.1\% to 63.0\% for earnings. Two-fold cross-fitting changes the penalties by 0.3 to 4.6 percentage points in KLIPS and by at most 1.5 points in HIES and HFLC on the same samples (Appendix~\ref{app:coarse-cell}).
\emph{Composition.} In pseudo-OLS, the composition of parents changes over event time. Table~\ref{tab:composition-restored} shows that, among the mothers it uses, the share who gave birth after age 30 falls from 66\% at birth to 57\% ten years later in KLIPS, from 62\% to 38\% in HIES and from 67\% to 46\% in HFLC. Weighting each post-birth cell by the number of parents of that type observed at birth reduces the fall to 7 percentage points in KLIPS, 9 in HIES and 6 in HFLC. Some types observed at birth have no observations ten years later, so symmetric matching does not fully preserve the composition at birth. Nevertheless, the penalty estimates differ little from pseudo-OLS (Appendix~\ref{app:bidirectional-comparisons}).
\begin{table}[htbp]
\centering
\caption{Composition of mothers by event time}\label{tab:composition-restored}
\footnotesize
\begin{tabular}{llrrrrrr}
\toprule
& & \multicolumn{3}{c}{Mean age at birth} & \multicolumn{3}{c}{Share above age 30 at birth} \\
\cmidrule(lr){3-5}\cmidrule(lr){6-8}
Survey & Weights & 0 & 5 & 10 & 0 & 5 & 10 \\
\midrule
KLIPS & Pseudo-OLS & 32.1 & 31.6 & 31.1 & 66.2\% & 63.6\% & 56.9\% \\
& Sym & 32.1 & 31.8 & 31.2 & 66.2\% & 64.7\% & 59.0\% \\
\addlinespace
HIES & Pseudo-OLS & 31.6 & 30.5 & 29.7 & 62.0\% & 47.9\% & 38.2\% \\
& Sym & 30.9 & 30.4 & 30.0 & 52.6\% & 48.0\% & 43.2\% \\
\addlinespace
HFLC & Pseudo-OLS & 32.3 & 31.1 & 30.3 & 67.4\% & 56.4\% & 46.2\% \\
& Sym & 31.5 & 31.1 & 30.8 & 60.5\% & 57.5\% & 54.1\% \\
\bottomrule
\end{tabular}
\begin{minipage}{\linewidth}\vspace{0.3em}\footnotesize\textit{Notes:} Women in the employment samples, coarse cells. Columns are event times. Pseudo-OLS weights the post-birth records that are observed, and Sym weights each type by its number of parents observed at birth.\end{minipage}
\end{table}
\emph{Event window.} Appendix~\ref{app:tau05} re-estimates every model on the window $[-2,5]$, except Sym+FE, which also requires one more pre-birth date. Employment penalties averaged over years 0--5 are larger than the ten-year averages, consistent with larger employment losses in the first years after birth. The KLIPS employment penalty is 51.3\% in the panel and 45.3\% in the standard pseudo-panel regression, and its HIES and HFLC employment penalties rise to 40.8\% and 37.6\%. The gap between NP and the regressions for KLIPS earnings shrinks from about 18 to about 5 percentage points, so the two counterfactuals for fathers diverge mainly at later event times.
\emph{NP cohorts.} For comparison with the panel, the main KLIPS NP estimates use first births from 2011 onward. Since NP requires no pre-birth donors, I also estimate it including parents observed at birth from 2006. Without the cohort restriction the coarse NP penalty is 34.5\% instead of 35.4\% for employment and 52.5\% instead of 42.5\% for earnings. With fine cells the penalties are 36.9\% instead of 37.9\% and 54.9\% instead of 46.9\%.
\emph{Survey weights.} Using the survey weights in the donor means, the parent counts and the regressions changes the HIES and HFLC pseudo-OLS penalties by at most 1.3 percentage points (Appendix Table~\ref{tab:weighted-rcs}).
\emph{Inference.} I compare the analytical standard errors with the standard deviations of a cluster bootstrap that repeats the entire estimation procedure on each bootstrap sample (Appendix~\ref{app:resampling-restored}). For coarse cells, the bootstrap standard deviations are within 19\% of the analytical standard errors in most cases. For Sym+FE, they are 46\% larger for KLIPS employment, 26\% for KLIPS earnings and 35\% for HIES employment. For NP, they are 55\% larger for KLIPS earnings. The analytical standard errors use a first-order approximation that may miss some finite-sample variation, while bootstrap standard deviations can be sensitive to extreme estimates in relatively small samples.
\emph{Subgroups.} By education and age at first birth, the pseudo-panel employment penalties in KLIPS vary less than the panel estimates, and the panel penalty is 61.9\% for parents aged 30 or younger at birth against 44.6\% under pseudo-OLS, so the agreement in the aggregate penalty does not extend to every subgroup (Appendix~\ref{app:heterogeneity}).
\section{Conclusion}\label{sec:conclusion}
Pseudo-panel event studies are widely applicable to settings where only repeated cross-sections are available. Even where panel data are available, small samples and limited coverage over time or across population groups can restrict the analysis. Selective attrition can also introduce survivor bias. Larger repeated cross-sections, therefore, can support more detailed analyses. In this paper, I show that the pseudo-panel design identifies cohort-time treatment effects when untreated pre-birth outcomes can be imputed from matched childless donors to future parents. I compute the pseudo-panel estimates using weighted least squares with covariate-cell means and derive analytical standard errors that account for the repeated use of observations. In simulations, the resulting confidence intervals attain near-nominal coverage, while conventional intervals cover about half as often. I therefore recommend the cell-level WLS regression with analytical standard errors as the default inference option.
The proposed extensions each address distinct weaknesses of the baseline approach. Doubly robust estimation accommodates continuous covariates and variables too detailed for exact matching. Symmetric matching limits changes in composition among the types that remain observed, and synthetic type FE absorb persistent differences in their untreated outcomes. When treatment effects are heterogeneous, the nonparametric estimator computes cohort- and type-specific effects and aggregates them with positive weights. In the Korean panel, the standard pseudo-panel regression gives an employment penalty close to the panel estimate. For applied work, I recommend reporting both unscaled and scaled penalties together with the event-study estimates for women and men. With pseudo-panels, pre-birth coefficients close to zero do not rule out anticipation among parents. Comparing analytical standard errors with standard deviations from a cluster bootstrap is particularly useful for the extensions such as Sym+FE and NP when estimates depend heavily on a few observations or small counterfactual denominators.
The validity of the pseudo-panel design hinges on the conditional independence assumption, which rules out selection on unobservables. A fruitful avenue for future research would be a sensitivity analysis that bounds the penalty when this assumption is relaxed. The framework can also be applied to other settings such as divorce, retirement, and the onset of a disability, where surveys record past event dates but cannot reveal when untreated respondents will experience the event. The marriage application in Appendix~\ref{app:marriage} illustrates the importance of informative matching variables. Marital status helps account for differences between parents and childless donors, but cannot be used for matching when marriage itself is the event. Where panel data are available, examining pre-event paths and subgroup estimates can reveal differences that are not apparent in the average effects.
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