## Abstract

I characterize China’s one-child policy as an individually tailored pricing system allowing women to have second and third children. The average policy price for having a second or third child is 13,900 dollars (2020, purchasing-power parity). It varies by age and other individual characteristics. I estimate policy elasticities exploiting within-individual price variation in a sample of women that annually replicates the national total fertility rate between 1979 and 2000. A 1 percent increase in the policy price decreases the probability of having a child by 0.7 percent (SE 0.1 percent). Without the policy, the total fertility rate would have been 2.7 children. The policy lowered this rate by 0.3 (SE 0.4) by curbing the number of girls born. This gendered policy impact further distorted the sex ratio at birth. Without the policy, the excess of boys per 100 girls born would have been 4.3. The policy increased the excess by 1.1 (SE 0.4).

## I. Introduction

The one-child policy regulated the fertility outcomes of approximately 500 million Chinese women between 1979 and 2010.^{1} Academics disagree on the impact of the policy on fertility. Duflo (2008) describes it as “a great success in terms of controlling fertility,” and several studies argue that the impact on fertility in turn affected other outcomes like crime, education, and marriage (Zhang 2017). Chen and Fang (2018) summarize the current literature as finding a “fairly limited impact on lifetime fertility.” Figure 1 illustrates the challenge in identifying the impact of the policy on fertility. Fertility was already decreasing before 1979 in China and neighboring countries, and it continued to decrease smoothly after the policy’s implementation. It is challenging to isolate the impact of the policy when other factors could have potentially caused fertility to further decrease after 1979 (for example, wage growth, increasing educational attainment, agricultural reforms).^{2}

The one-child policy did not mandate that only one-child families were to be created. Instead, it introduced a system that priced permits for having children.^{3} Permits for having a first child were free. Permits for having a second or third child had a price. Permits for having more than three children were generally unavailable. I characterize the pricing system building on two sources. I use the province-level, year-specific prices documented by Ebenstein (2010a) as a baseline. Then, I include province-level, year-specific policy “exemptions” documented from archival records by Scharping (2003). These exemptions set the prices of permits for having second or third children to zero based on 17 individual characteristics (for example, age and sex of the first child, ethnicity, scarcity of males in the family, type of job).

I map the policy characterization to a sample of women surveyed by the China Health and Retirement Longitudinal Study (CHARLS, National School of Development 2017). I construct the fertility histories of the women in this sample and show that they annually replicate the national total fertility rate during the period analyzed, 1979–2000. Mapping the policy characterization to longitudinal fertility and other demographic information allows me to observe within-woman variation in the policy prices. I perform two exercises to validate my policy characterization. First, I use digitized records from city gazetteers and yearbooks collected by Suárez-Serrato, Wang, and Zhang (2019) to verify that the pricing system was used to enforce aggregate fertility objectives of the Communist Party.^{4} Second, I verify that my policy characterization aligns with information from a nationally representative survey that posed questions about policy implementation to more than 400 village and town government officials.

I estimate policy-price elasticities using dynamic panel models, accounting for individual and age × year × province invariant characteristics. The models regress the flow of fertility on the policy price and the stock of children in the previous year. Individual-level event studies based on price spikes justify the identification assumption of price exogeneity. A generalization of the Arellano and Bond (1991) moment estimator accounts for the endogeneity of the stock of children. The survey posing questions to government officials about policy implementation allows me to construct an instrument to account for measurement error in the documentation of the pricing system. I find that a 1 percent increase in the policy price decreases the probability of having a child by an average of 0.052 (SE 0.007) percentage points. The fraction of women having a child at any point in the sample is 0.072, implying a policy-price elasticity of 0.052/0.072 ≈ 0.7 (SE 0.1). The policy impact is driven exclusively by a reduction in the number of girls born. I estimate the average reduction in the probability of having a girl after a 1 percent increase in the policy price by age. This semi-elasticity increases monotonically from −0.1 (SE 0.02) percentage points at age 20 to −0.0004 (0.0006) at age 40, passing through −0.02 (SE 0.004) at age 30. The analogous semi-elasticities for the probability of having a boy are all virtually zero.

The sex ratio at birth of first children is not distorted in China (Almond, Li, and Zhang 2019; Ebenstein 2010a). This fact holds in the sample of women that I analyze. The gendered policy-price semi-elasticities are driven by mothers whose first children are girls. Women whose first children are boys are virtually unaffected by the policy. Mothers thus respond to the policy by combining a stopping rule with sex-selective abortions. Suggestive evidence using longitudinal data on abortions is consistent with this explanation. Mothers of first-child boys are unaffected by the policy because they do not pursue fertility after their first child. Upon a policy-price increase, their likelihood of aborting a pregnancy is unaffected. Mothers of first-child girls pursue fertility further. Upon a policy-price increase, their likelihood of aborting a pregnancy increases. Aborting allows them to pursue their preferred sex combination (girl–boy). This evidence is suggestive because the results for mothers of first-child girls have large standard errors. However, both the results for mothers with first-child girls and mothers with first-child boys yield the same conclusion across several specifications.

The age-specific policy-price semi-elasticities enable prediction of the decrease in the total fertility rate due to the policy. The total fertility rate in the sample of women that I analyze is 2.37 children.^{5} In the absence of the policy, this rate would have been 0.30 (SE 0.04) children higher—that is, 11.4 percent (SE 1.2 percent) higher. I qualify this calculation as stylized in the body of the paper, as it requires additional, strong assumptions. A similar calculation indicates that the policy increased the excess of boys born per 100 girls born. The observed ratio is 110.4 boys per 100 girls born. In the absence of the policy, it would have been 1.1 (SE 0.4) lower. That is, 109.3 boys per 100 girls born. This phenomenon of fertility decreasing while the sex ratio at birth increases has also been documented in India (Anukriti 2018; Jayachandran 2017).

Zhang (2017) surveys economic studies of the one-child policy. Most use the temporal variation in province-level prices documented by Ebenstein (2010a). Generally, they map this variation into various census waves to study policy impacts on the marriage market (Huang and Zhou 2015), the sex ratio at birth (Ebenstein 2010b), urban–rural migration (Huang, Lin, and Zhang 2019), and other household outcomes (Huang, Lei, and Sun 2021). They exploit province × cohort price variation in repeated cross-sections.^{6} Qian (2009) uses gender of the first child, one of the 17 exemptions that set the policy price to zero, to study the intergenerational impact of the policy on education. I combine the temporal variation in province-level prices with most of the exemptions. Mapping this characterization to longitudinal data enables exploiting within-individual price variation to estimate policy-price elasticities.

Recent research argues that population-control policies were an important driver of the global decrease in fertility observed during the second half of the 20th century (for example, De Silva and Tenreyro 2017). Others argue that the opportunity cost of raising children and the increasing demand for high-skilled human capital are the main drivers of demographic transitions (for example, Galor 2012). In the context that I analyze, where the government had thorough control over household economic decisions, the response to the policy was inelastic. This does not imply that the one-child policy did not reduce fertility. Instead, it implies that large prices were required to reduce fertility. The restrictions implied by the policy interacted with the strong preference of Chinese families for having male children (Sen 1991), which contributed to the sex-ratio imbalance in the population.^{7} China’s one-child policy aimed to curb the number of children born per household—it only curbed the number of daughters.

## II. Context and Data

### A. Economic and Institutional Setting

The economic and institutional setting was inflexible during the era of the one-child policy. Although the government implemented a series of reforms based on market principles beginning in 1979, it still exerted considerable control over household economic activities.

During the period that I analyze, the hukou (residency) dictated the location at which an individual could live, which was usually the location of birth, and assigned them either an agricultural or a nonagricultural status, which was usually the status of their parents. Government rules, taxes, and subsidies were tied to the individual hukou. The hukou system is so fundamental to the organization of the Chinese economy that the book detailing its rules is referred to as zhongguo diyi zhengjian, or “China’s Number 1 Document” (Tian 2003). Until 2000, individuals with nonagricultural hukou belonged to a danwei (working unit). Membership to a danwei was regulated by the central government. The danwei provided permanent employment and dictated total labor income, including access to food, healthcare, pensions, children’s education, and housing (Tang and Parish 2000; Whyte and Parish 1985). Individuals remained in their danwei for life (Lu and Perry 1997). After the liberalization of the economy in 1979, the danwei system continued to regulate economic decisions (Naughton 2007).

Individuals with an agricultural hukou mostly worked as farmers in collective systems, until 1984. The collective to which they belonged dictated labor income through a point system. Individuals earned points per work day and received basic in-kind payments. At the end of the harvest year, the government procured the grain. The surplus was sold at fixed prices, and the money was divided according to work days. An agrarian reform began in 1978. After the reform, the land was divided as part of a contract between the collective and households, allowing for centralized control of grain prices (Cai 2003). In locations where agricultural activities lost importance, individuals became part of town and village enterprises, or other centralized activities that regulated decision-making, in a similar way to the danwei system (Naughton 2007).

Online Appendix Figure A.2 illustrates how the institutional setting limited decision-making. For the sample of women that I describe and analyze below, there is virtually no variation in the probability of supplying full-time labor. It is 0.90 in the full sample and remains at that level when only considering women who gave birth during the year observed or one or two years before. In 80 percent of the villages and towns across China, 10 percent or fewer household heads report to have ever migrated or relocated. Migration was mostly temporary, regulated by government permits, and within villages and towns (Chan 2001).^{8} The inflexibility implied by the institutional setting is useful in my empirical analysis. The simultaneity of decisions like labor force participation, migration, and education is a concern when analyzing fertility (Hotz, Klerman, and Willis 1997). In this setting, government mandates fixed labor supply and migration. They also fixed education to specific levels (Fan, Heberer, and Taubmann 2015; Postiglione 2015). Simultaneity of these decisions with fertility is thus a second-order concern in my analysis.

After establishing the People’s Republic of China in 1949, Mao Zedong encouraged population growth. Birth control, which would reduce the size of the workforce, was condemned. Imports of contraceptives were banned. Abortions were illegal. After unfettered population growth and events like the Great Famine, the government launched family-planning campaigns in the 1970s, which encouraged the use of contraception, the delay of marriage, and the formation of smaller families (Powell 2012). Towards the end of the decade, abortions became legal (Scharping 2003). Before 1979, specific fertility limits were suggested and enforced in some regions of the country. For people with agricultural hukou, which constituted the majority of the population before 1979, there were no limits (Wang, Zhao, and Zhao 2017).^{9} Women had to register any new pregnancy beginning in the early 1960s. Family-planning policies that preceded the one-child policy further established a bureaucracy for population control.^{10}

In 1979, the government announced the one-child policy at the federal level. The mandate placed local authorities in charge of the timing and implementation of the policy. Local authorities had the incentive to implement the policy because their effectiveness in curbing fertility factored into their job evaluations. Failing to implement the policy effectively resulted in administrative penalties, such as disaffiliation from the Chinese Communist Party (Scharping 2003). Online Appendix Table A.1 shows an example of the forms used to evaluate local authorities. Aggregate fertility and citizens’ knowledge of the policy were evaluation criteria. Local authorities also faced opposition to the policy from citizens (Hardee-Cleaveland and Banister 1988). Arguably, the trade-off between conforming to national policy and mitigating social discontent at the local level led officials to design the policy as a pricing system allowing women to have second and third children. Greenhalgh and Winckler (2005) document support for this interpretation. For instance, in 1989, Premier Li Peng addressed provincial governors, stating that: “To achieve substantial compliance, policy must be supplemented with more detailed management by objectives. . . .Targets should be evaluative.”

### B. Empirical Characterization of the Pricing System

China’s one-child policy implemented the following pricing system. Permits for having a first child were free, permits for having a second or third child had a price, and permits for having more than three children were unavailable. Children born without a permit had no hukou registration and, thus, no rights (for example, education and health services). Their parents were subject to punishments such as being dismissed from their danwei, therefore permanently losing their jobs.

The price per permit for second or third children was either a proportion of household labor income or a lump sum. In either case, the price had to be paid for a fixed number of years for each child additional to the first. Let 𝓘 index women. I analyze discrete annual periods and do not observe the onset of menarche or menopause. I let 𝓐_{i} index the ages when woman *i* ∈ 𝓐_{i} is observed between ages 15 and 45. A woman *i* of age *a* ∈ 𝓐_{i} had to register her pregnancy to the local birth-planning authority before her fourth month of pregnancy for it to be legal. If she did not want to keep her child, she was able to get an abortion for free. If she wanted to keep her child and was in her second or third pregnancy, she needed to sign a “one-child policy contract” with the government. The contract stipulated the price and form of payment. A signed contract was not revised if the policy were to change after its terms were agreed upon.

I refer to the present value of the price per permit for second or third children as policy price and denote it by Ξ_{ia}, which summarizes the one-child policy contract:
1

where κ_{ia} is the fraction of household labor income to be paid in proportional-policy provinces and τ_{ia} is the amount to be paid in lump-sum-policy provinces. and are the number of years in which the prices were paid in the respective regimes. *y _{ia}* is household labor income and β is a discount factor. When signing the contract, households had perfect certainty about either κ

_{ia}and or τ

_{ia}and . I define Ξ

_{ia}using a constant value of household labor income

*y*, which assumes that women calculated the present value of the price using age-

_{ia}*a*(current) household labor income. This assumption is consistent with stationary expectations. The price Ξ

_{ia}condenses the information of a contract establishing multiple payments into a present value. It is a function of an unknown discount factor and involves assumptions about the evolution of household labor income. I discuss these two features as potential disadvantages in Section III. For now, I set β to 0.98 (that is, discount rate = 0.02).

Local officials announced the values of κ_{ia} and or τ_{ia} and each year. They also specified whether the price was proportional or lump sum. I follow two steps when constructing Ξ_{ia}. First, I set the value of Ξ_{ia} to the province- and year-specific value documented by Ebenstein (2010a).^{11} For example, if a woman was 34 years old in 1987 and lived in the province of Sichuan, I set Ξ_{ia} to the value reported by Ebenstein (2010a) for the year 1987 in that province. Second, I set Ξ_{ia} to zero if woman *i* qualified for an exemption when she was *a* years old using the documentation in Scharping (2003). Table 1 lists 17 exemption criteria that applied for at least one year in at least one province. There is province and time variation in the criteria that applied. I list this variation and the empirical construction of the criteria in the Online Appendix. I construct Ξ_{ia} for a longitudinal sample of women with rich, annual demographics available. This enables observing within-woman variation in Ξ_{ia}, even when accounting for individual and age × year × province invariant characteristics.^{12}

Figure 2 displays the time series of the average Ξ_{ia} for the sample of women that I analyze, in units of annual average household labor income during the year labeled (for example, if the average of Ξ_{ia} is two in 2000, then the price equals two years of average household labor income in 2000). The rules were uniform across demographics before exemptions became widespread. After an initial period of strict implementation, the government relaxed the policy and reinforced local, incentive-based implementation. It encouraged exemptions by issuing “Document 7” in 1984 (Qian 2009). In the late 1980s, Premier Li Peng addressed governors and stated that population growth was still economically unsustainable and advocated for a more rigid implementation (Greenhalgh and Winckler 2005). Figure 2 is consistent with these facts. It shows that the prices were uniform across demographic groups in 1980, decreased and diverged in the 1980s, and started to quickly increase after Li Peng made public his concerns about population growth.

### C. Analysis Sample

I use data collected by the China Health and Retirement Study (CHARLS) (National School of Development 2017) on a sample of women (household heads or spouses of household heads) who were 45 years old or older in 2010. The sample was collected in 443 villages and towns of 27 provinces. It is nationally representative. Retrospective fertility and employment data were collected, including the number and sex of children (dead or alive), the number of (induced) abortions, and extensive margin labor-force participation.^{13} I analyze these variables in longitudinal format. The sample includes the 6,950 women who were between 15 and 45 years old between 1979 and 2000. I observe them annually for an average of 16.7 times. The sample is an unbalanced panel because women were born in different years. A number of women turn 15 and enter the sample during the window of observation. Similarly, a number of women turn older than 45 and exit the sample. Online Appendix Figure A.1 shows that the sample analyzed annually replicates the time series of the national total fertility rate reported by The World Bank (2017a). This suggests that the sample analyzed is accurate at depicting the aging and fertility profiles of the women “treated” by the one-child policy.^{14}

Table 2 describes the sample for the entire period analyzed and by five-year subperiods. Panel A describes the sample size, and Panel B describes the demographics of the sample. Panel C describes the fertility variables. Panel D summarizes policy variables. My preferred specifications contain one-year lags, so observations from the year 1979 are only included through these lags. The stocks are the number of children and abortions up to the current period. The flows are the first-differences of the stocks. Only 0.18 percent of first-differences are greater than one due to twinning or higher-order births. I thus reclassify the flows of children and code them as indicators of changes in the stocks. Reclassifying the flow of abortions is unnecessary because no woman in the sample has more than one abortion in a year.

Panel D of Table 2 summarizes the policy price, Ξ_{ia}, labeled as “price, documentation” in the table. The unit of the policy price is years of average household labor income.^{15} To aid interpretation, the description in the table standardizes the price by its average in 1979 and then multiplies it by my estimate of average household labor income for each year. In the period 1980–2000, the policy price averages 3,319 dollars (2020), after the appropriate exchange rate and inflation adjustments.^{16} Before multiplying the price by my estimate of average household labor income, it averages two years of 1979 household labor income.

I match a panel of prefecture mayors for the years between 1990 and 2000 collected by Suárez-Serrato, Wang, and Zhang (2019) to the sample. These authors digitized city gazetteers and yearbooks to obtain the variables described in Panel E of Table 2. Their data contain a measure of mayoral performance at implementing aggregate fertility objectives (net target birth rate less net realized birth rate) and an indicator of being an experienced mayor (>2.5 years in office).^{17} I also construct and match a data set characterizing the economic environment using two sources: province-level, year-specific data from *China Statistical Yearbooks* available in China Data Center (2017) and village or town, year-specific data from CHARLS. Online Appendix Table A.8 provides a full description. I construct variables describing aggregate employment, education, agriculture, trade, and others. I elaborate on these variables in the empirical analysis.

### D. Validation of the Pricing System’s Empirical Characterization

Before turning to the main analysis, I provide two validation exercises of the pricing system described so far.

#### 1. Policy prices and the official fertility targets

I provide suggestive evidence indicating that the pricing system documented above was used by local officials to regulate fertility. I consider the model 2

where mayor performance_{ia–1} is the measure of mayoral performance in Panel E of Table 2, and η_{ia} is an error term. A positive correlation (that is, ζ_{performance} > 0) between the price Ξ_{ia} and the performance of the mayor during the previous year is consistent with the pricing system reflecting fluctuations in aggregate phenomena related to fertility. For example, prefectures where fertility is low could be those in which prices are high. This would simply be a reflection of an aggregate taste for smaller families and not necessarily a stringent policy. A negative correlation (that is, ζ_{performance} < 0) aligns with the pricing system being used to enforce the trade-off between conforming to national policy and mitigating social discontent discussed in Section II.A. For instance, if a mayor performs well at imposing low fertility in a given year, he would then dictate a lower price for the following year.

Figure 3 provides various estimates indicating that the correlation is negative. I standardize the mayor performance measure to a mean of zero and a standard deviation of one. The full sample estimate indicates that a one standard deviation performance increase in the previous period is associated with an average decrease in the individual-level policy price of almost 10 percent. When obtaining these estimates, I include age × year × province fixed effects and drop the constant in Equation 2. I do this because my preferred specification for obtaining the main results below includes these fixed effects, which enable accounting for temporal variation in province-specific fertility patterns.

#### 2. Comparison to an alternative measure of the pricing system

The empirical characterization of the pricing system described so far is prone to measurement error (recall that it involves assumptions about the discount rate and the evolution of household income). Further, the policy implementation could have differed from what historical documentation indicates—for example, local authorities could have been corrupt or more ruthless at implementing the policy than what official documents acknowledge.

I use a nationally representative survey with 443 village and town government officials in 27 provinces of China that was conducted by CHARLS in 2011 as a complement to its household surveys. The survey asked village and town officials to provide a retrospective annual estimate of the total amount that a woman had to pay in order to get a permit to have a second or third child. Put differently, the survey asked the officials to provide a village- or town-specific time series of estimates of Ξ_{ia}. I match these estimates by village or town and year to each woman in the sample and denote them by .^{18}

I convert to 2020 dollars using the same conversion procedure applied to Ξ_{ia}. Panel A of Table 2 indicates that the two measures of the prices closely align. A strong empirical relationship between Ξ_{ia} and is a useful method for corroboration, given the independence of the sources. I test the strength of this relationship by estimating the model
3

where I reuse the notation from above. When estimating this model, I also include age × year × province fixed effects and drop the constant. Figure 4 displays the estimation details and plots the associated binned scatterplot. The difference in the *R*^{2} of a model allowing ζ_{price} ≠ 0 and the *R*^{2} of a model imposing ζ_{price} = 0 is eight percentage points. The residual relationship between the two measures of the pricing system is remarkably strong.

## III. Policy-Price Elasticities

### A. Event Study

I use an event study for an initial exploration of the relationship between the pricing system and fertility. Let *n _{ia}* denote the number of children of woman

*i*∈ 𝓘 at age

*a*∈ 𝓐

_{i}. Her flow of children is Δ

*n*:=

_{ia}*n*–

_{ia}*n*

_{ia}_{–1}: the first difference of her stock. Recall from Section II that a woman was required to register her pregnancy by the end of the first quadrimester. If she already had one or two children and decided to continue with the pregnancy, she needed to obtain a permit. The price of this permit was set by the policy when she was

*a*– 1 years old. This is the policy price that most immediately impacts her flow of fertility at age

*a*. I denote its first difference by when using the price based on documentation and when using the price based on surveys.

^{19}

I classify a woman *i* of age *a* as facing a price spike if the first difference of the policy price when she is *a* – 1 years old is above the 80th percentile of the in-sample distribution of the price first difference. I relabel age to event time, denoted by *s*, so that years are counted relative to when the price spike occurs. Then, I consider event-time periods *s* = –5,. . .,5 to estimate the model
4

where γ_{s} is the average of Δ*n _{is} s* years from a price spike, and ɛ

_{is}is an error term. The event study is based on variables in first differences, so individual or woman fixed effects are implicit in this model. Additionally, I residualize the flow of children and the price first differences from age × year × province fixed effects using ordinary least squares (OLS) in the full sample before defining the price spike and estimating the model. Price spikes are woman-specific. The age at which they occur varies across women, but not within. The coefficients γ

_{s}are thus relative to

*s*= –1 and identified off within-woman price variation.

^{20,}

^{21}

I estimate the model in Equation 4 two times, one time defining price spikes using (documentation) and one time using (surveys). Figure 5 displays the estimates of γ_{s}. In both cases, a price spike generates a sudden and sustained average decrease of approximately 0.12 standard deviations in the average (residual) flow of children. The figure suggests that innovations in the pricing system, occurring through policy changes that generate within-woman price variation, are potentially exogenous to the fertility process. It thus accumulates evidence against women manipulating their eligibility to qualify for exemptions or timing their fertility process to face lower prices (for example, opting for an abortion in a given period to get a permit for a lower price in the future). If this manipulation had happened, their response to price spikes would not appear as sudden and sustained in the figure.^{22} I now explore a parsimonious specification allowing me to interpret the relationship between the pricing system and the flow of children as a price elasticity.

### B. Empirical Framework and Main Estimates

I postulate the model 5

where Δ*n _{ia}*, Ξ

_{ia-1}, and

*n*

_{ia}_{–1}are defined as before, ɛ

_{ia}is an error term, and

*γ*

_{Ξ}and γ

_{n–1}are coefficients. In this model,

*n*

_{ia}_{–1}summarizes the dependency of the fertility process on policy prices realized before

*a*– 1. Conditional on

*n*

_{ia}_{–1}, Ξ

_{ia-1}is the policy price that most immediately affects the flow of children at age

*a*. To interpret the model, assume for a moment that ɛ

_{ia}is mean independent and that γ

_{n–1}= 0. If this holds,

*γ*

_{Ξ}is a semi-elasticity (that is, the percentage-point change in the probability of having a child upon a 1 percent increase in the policy price Ξ

_{ia-1}).

^{23}is the corresponding policy-price elasticity in expectation. If γ

_{n–1}≠ 0 and mean independence still holds, the semi-elasticity and elasticity are conditional (they hold fixed the stock of children

*n*

_{ia}_{–1}). If mean independence does not hold, solutions to endogeneity are required to maintain a causal interpretation.

I estimate the model in Equation 5 including all women in the sample independently of their stock of children *n _{ia}*

_{–1}. If

*n*

_{ia}_{–1}= 0, woman

*i*does not need to pay a price associated with the policy when having a child at age

*a*. Still, Ξ

_{ia-1}is observed both by her and the econometrician. That is, both she and the econometrician observe the price that she would have needed to pay if she had at least one child, given her demographic characteristics and the calendar year when she is

*a*years old. Including women with

*n*= 0 in the estimation allows the current policy price to affect all margins determining completed fertility and the total fertility rate.

_{ia}I construct a preferred specification for estimating Equation 5 progressively in Panel A of Table 3. I first use a logit model because the dependent variable is binary. Instead of displaying in the table, I show the corresponding marginal effect at the mean of Ξ_{ia-1} and *n _{ia}*

_{–1}. The estimates obtained using the analogous linear-probability specification are in the next column (OLS). The logit and OLS specifications yield essentially the same estimates (a policy-price semi-elasticity of 0.03 and a corresponding elasticity of 0.4). I thus use linear-probability specifications henceforth, as they enable convenient, well-known solutions to the challenges discussed next. Transforming the model to 6

provides additional flexibility and yields identical estimates.^{24} The third column of Panel A in Table 3 verifies the equivalence of the two models by showing OLS estimates based on the transformed model.

The estimates discussed so far are based on specifications without controls. Age, temporal, or unobserved regional components, such as market conditions determining the costs of having children, could correlate with prices and introduce omitted-variable bias. Other aspects, like local aggregate preferences, could also shift fertility, correlate with prices, and, if omitted, also introduce bias. Multiple conjectures about how these unobserved components enter the fertility process are plausible. It is thus necessary to account for them comprehensively. The relatively large number of observations and periods observed for each woman in the sample allow me to consider a datum-intensive specification with age × year × province fixed effects. The column “Fixed Effects” in Table 3 displays OLS estimates that include these fixed effects when estimating the model in Equation 6. The parameter estimates change, making it relevant to keep these fixed effects in the remainder of the paper.

I then tackle a major source of potential endogeneity. The stock of children *n _{ia}*

_{–1}in Equation 6 violates mean independence by construction. This biases the estimates discussed so far. I consider a generalization of an estimator that accounts for stock endogeneity in dynamic panel models proposed by Arellano and Bond (1991). These authors propose a general method of moments (GMM) estimator by first differencing Equation 6 and exploiting the condition 𝔼[

*n*

_{ia}_{–b}· Δɛ

_{ia}] = 0 for

*a*≥ 3 and

*b*≥ 2.

^{25}The restrictions on

*a*and

*b*guarantee that the moment condition holds as long as , for which Figure 5 provides evidence. The generalization of the Arellano and Bond (1991) estimator that I employ considers the additional moment condition 𝔼[Δ

*n*

_{ia}_{–1}· ɛ

_{ia}] = 0 for

*a*≥ 3, as in Blundell and Bond (1998). Including the additional moment condition is recommended when working with persistent processes because some of the lagged outcomes

*n*

_{ia}_{–b}may be weak instruments.

^{26}The column “System GMM” in Table 3 shows the estimates exploiting all of the moment conditions. The next column presents estimates based on the same estimator and model, except up to five lags of the stock of children are included. The similarity of the estimates, with the inclusion of the additional lags, discards the omission of higher-order persistence in the fertility process.

^{27}

Logit and OLS estimates of the policy price semi-elasticity based on Equation 6 are similar. They halve in magnitude when accounting for age × year × province fixed effects. They increase to a similar magnitude to that of the logit and OLS estimates once the potential endogeneity of *n _{ia}*

_{–1}is taken into account. The system-GMM estimator is based on the first difference of Equation 6. It thus directly communicates with the evidence in Figure 5, which indicates that the policy price variation identifying the semi-elasticities is plausibly exogenous.

The estimates discussed so far only use the policy price based on documentation, Ξ_{ia}. I exploit the price based on surveys, , to account for potential measurement error in Ξ_{ia} by including the moment conditions and for *b* ≥ *a* in the system GMM.^{28} The validity of these additional moment conditions rests on prices being plausibly exogenous (Figure 5) and on the close relationship between the two measures of the prices (Figure 4). The validity of the moment conditions used to account for the endogeneity of the stock of children rests on the structure of Equation 6 and on the persistence of the fertility process. The last column of Panel A of Table 3 shows the estimates. The policy price semi-elasticity increases in magnitude and indicates that the measurement-error correction is relevant.

The last column of Panel A of Table 3 presents my preferred estimates. They are based on a system-GMM estimation of Equation 6 that includes age × year × province fixed effects, accounts for the endogeneity of the stock *n _{ia}*

_{–1}, and addresses measurement error in Ξ

_{ia-1}.

^{29}The system-GMM estimator is based on the first difference of Equation 6. It thus implicitly differences out woman fixed effects. Identification of the semi-elasticities thus relies on within-woman price variation. Panel B of Table 3 provides checks for this specification and addresses the robustness of the corresponding System GMM estimator. I provide estimates that include time-varying current (Column 1), current and one-year lagged (Column 2), and current, one-year lagged, and two-year lagged (Column 3) controls describing the state of the economy when women make fertility decisions. These controls are based on a comprehensive set of economic indicators that are classified by category, and then dimension-reduced into principal factors. They vary within age × year × province cells because they contain village and town information (see Section II). The estimates of the semi-elasticities are insensitive to including these controls.

Section II documents that, for some women, the policy prices were charged as a fraction of household labor income. For them, the price variation could reflect fluctuations in labor income and not only policy intensity. In standard models of fertility (for example, Hotz, Klerman, and Willis 1997), an increase in labor income would disincentivize fertility by raising the opportunity cost of having children. An increase in labor income would generate an increase in the policy price and make a negative relationship between this price and fertility spurious. However, household labor income is unlikely to drive the price variation that I exploit. This variation differences out individual fixed effects and age–year regional economic characteristics. Further, governmental policy largely fixed the individual-level labor supply (see Section II). Women who faced lump-sum permit prices help to verify this. For them, there is no potential spurious relationship between the prices and fertility induced by labor income. Panel B of Table 3 shows that the policy semi-elasticity is virtually the same across the subsamples of women who faced proportional and lump-sum permit prices. Furthermore, when estimating a model analogous to Equation 6 with full-time labor force participation as the dependent variable, there is a precise, null relationship between this variable and the policy price.

My preferred estimate (the last column of Panel A of Table 3) indicates that a 1 percent increase in the policy price decreases the probability of having a child by percentage points. I reject the null hypothesis of this semi-elasticity differing from zero when employing standard significance levels.^{30} The corresponding elasticity is . I estimate this to be 0.724 (SE 0.094).

Bergsvik, Fauske, and Hart (2021) review the literature analyzing policies targeting fertility since 1970 in several countries. They classify the policies into childcare, health services, parental leave, and universal transfers. My study relates to universal transfers (that is, policies directly shifting the price tag of having a child, as opposed to indirectly subsidizing it). Milligan (2005) reports that a 1 percent increase in lump-sum fertility benefits increases the rate at which women have children by 0.107 percent. He exploits a reform in Quebec, Canada during the 1990s when estimating this policy-benefit elasticity. His estimate is consistent with the cross-country policy-benefit elasticity of 0.16 for the period 1970–1990, as documented by Gauthier and Hatzius (1997). It is also consistent with the policy-benefit elasticity ranging between 0.05 and 0.11 reported by Zhang, Quan, and van Meerbergen (1994), who analyze Canadian policies in the period 1921–1988. Whittington, Alm, and Peters (1990) report similar elasticities for the United States for the period 1913–1984. Their estimates range between 0.12 and 0.24. My estimate of the elasticity is greater in magnitude. Still, it indicates that fertility responds inelastically to benefits and (negative) transfers, even when the government has thorough control over economic decisions.^{31}

### C. Demographic Heterogeneity

Table 4 shows estimates for different subgroups of the population. I discuss the three main patterns. Women in rural areas or with agricultural hukou face lower policy prices by design (they were exempted from paying prices more often, and that lowers their average price). Their decrease in the probability of having a child upon a 1 percent increase in the policy price is not too far off from the analogous decrease for women in urban areas. However, their elasticities are lower than the elasticities of urban women because urban women have a lower average flow of fertility at any given time. For urban women, the probability of having a child is more price-sensitive in percentage terms. As a consequence of policy design, the price increases as a function of education. More educated women are more price elastic. This greater elasticity results from their lower propensity to have children and lower average flow of children at any given time. Finally, the prices increase over time as discussed in Section II. The price elasticity displays the same pattern, which is not necessarily due to a greater price sensitivity given a fixed average flow of children. Instead, the decreasing secular trend in fertility generates an increasing price sensitivity in percentage terms.

### D. Age Profiles by Gender

I now use my preferred specification of Equation 6 and the corresponding system-GMM estimator replacing the number of children *n _{ia}* with the number of girls or the number of boys. This allows me to display the policy-price semi-elasticities of the flow of girls or boys in Panel A of Figure 6. For each age between 20 and 40 years old, I estimate the semi-elasticity using the observation at that age, as well as observations from five periods before and five periods after. I include the periods before and after to exploit within-woman price variation. A 1 percent increase in the policy price has virtually no effect on the probability of having children. The semi-elasticity estimates are precisely estimated and very close to zero. A 1 percent increase in the policy price decreases the probability of having a girl by 0.1 percentage points at age 20. This semi-elasticity decreases in magnitude as women age. There are two plausible explanations. First, households are more resource-constrained and thus more price-sensitive when women are relatively young. Second, as women age, their natural propensity to have children decreases and restrictions imposed by the policy prices become less relevant.

Panel B of Figure 6 investigates further the gendered impact of the policy. I only consider women with at least one child. Women with at least one child have larger semi-elasticities because policy prices more immediately restrict them. The figure shows that the policy only impacts women whose first children are girls. This follows because women whose first children are boys are fine having only one male child (that is, they use a stopping rule). Women whose first children are girls are restricted by the policy. They would like to have a boy after having a girl because of cultural norms (Sen 1991) and also because of economic incentives like having additional land workers at home (Almond, Li, and Zhang 2019). The sex ratio at birth of first children in China is balanced, and that holds in the sample analyzed. Panel B of Figure 6 thus indicates that the policy’s contribution to the sex-ratio imbalance is through a distortion of the flow of children for women with at least one child.

### E. Abortions

Longitudinal data on abortions provide evidence consistent with my interpretation of the policy’s gendered impact. Table 5 displays estimates using my preferred specification of Equation 6 and the corresponding system-GMM estimator, replacing the number of children with the number of (induced) abortions on both sides of the equation. I also add into the model the stock of female and male children. For estimation, I use moment conditions analogous to those discussed before for the stocks of abortions and female and male children.^{32}

Panel A of Table 5 shows estimates for women whose first children are girls. The estimates of the policy semi-elasticity are noisy, though they imply large elasticities. Their semi-elasticities consistently indicate that a 1 percent increase in the policy price increases the probability of having an abortion by between 0.04 and 0.06 percentage points. Panel B of Table 5 shows the analogous estimates for mothers whose first children are boys. These estimates are inconsistent across women with different stocks of children. They generate semi-elasticities and elasticities that are all close to zero. Table 5 indicates that women whose first children are girls sex-select using abortions when restricted by the policy. Sex-selective abortions are known to skew the sex ratio at birth in China (Almond, Li, and Zhang 2019; Chen, Li, and Meng 2013). Table 5 also indicates that mothers whose first children are boys do not pursue fertility further. Thus, their probability of having an abortion is essentially unaffected by policy price changes.

## IV. Interpreting the Aggregate Relevance of the Policy Elasticities

I now estimate the aggregate fertility implications of the policy elasticities. Recall that only a handful of women in the sample have twins or higher-order births. I thus reclassify Δ*n _{ia}*, the flow of children, as an indicator of whether woman

*i*∈ 𝓘 has a child when she is age

*a*∈ 𝓐

_{i}years old. 𝔼[Δ

*n*] is the probability that she gives birth at age

_{ia}*a*. 𝔼[Δ

*n*] is also known as the age-

_{ia}*a*(specific) fertility rate. In principle, only women who are fertile when they are

*a*years old should be considered when estimating 𝔼[Δ

*n*]. However, I do not observe the onset of menarche or menopause. I thus assume that all women are fertile when they are between 15 and 45 years old. In that case, the total fertility rate is 7

_{ia}By definition, the cumulative age-*a* fertility rate (that is, the sum of all age-specific fertility rates up to age *a*) at age 45 is the total fertility rate.

Online Appendix Figure A.1 displays annual estimates of the total fertility rate using the sample analyzed. For estimation, I use the formula in Equation 7 and the women who were between 15 and 45 years old at least during one year between 1979 and 2000. The time series of the estimates closely aligns with the time series of the total fertility rate reported by the World Bank (2017a). I pool calendar years and analyze the sample as representing the main, large cohort of fertile women impacted by the policy. Pooling instead of analyzing annual total fertility rates increases the precision of the counterfactual estimates discussed below. Panel A of Figure 7 displays estimates of the realized cumulative age-specific fertility rates. The point estimate at age 45 is the total fertility rate in the sample, 2.37 (SE 0.01) children.^{33}

The model in Equation 5 suggests a straightforward no-policy counterfactual age-specific fertility rate: , where the conditioning of the expectations is omitted to avoid notation cluttering.^{34} This expression is the probability that woman *i* has a child at age *a* less the corresponding probability predicted by the policy price; that is, the age-*a* specific fertility rate in the absence of the policy. Cumulative at age 45, this statistic provides the no-policy counterfactual total fertility rate. Throughout the paper, I assume that the price was the only device used for implementing the policy. I then correct the price for measurement error. If there were an additional fixed cost for having children associated with the policy, that would go into the model’s constant. This additional cost would not compromise the identification of *γ*_{Ξ}; its derivative with respect to the price would be zero. However, it would compromise the identification of the no-policy counterfactual, which is a prediction in levels. The prediction would be off by the fixed cost. If the additional cost were age-specific or time-varying, the identification compromise would be similar and appear annually. Evidence regarding costs associated with the policy in addition to the price is anecdotal. However, I am cautious about their potential existence and qualify the no-policy counterfactual estimates as stylized.

The age-specific and total fertility rates can be calculated using Equation 7. They can also be calculated by gender using the age-specific probability of having a son (daughter) to obtain the male (female) total fertility rate. The sum of the male and female age-specific fertility rates yields the age-specific total fertility rate 𝔼[Δ*n _{ia}*]. The sum of the cumulative gender-specific rates at age 45 yields the total fertility rate. Recall from Section III that the policy has essentially no impact on the probability of having a son. I thus set the no-policy male age-specific fertility rate to be identical to its realized counterpart. For the female age-specific fertility rate, I adapt the no-policy counterfactual formula discussed in the previous paragraph to the flow of girls. When doing so, I use the age-specific semi-elasticities of the flow of girls in Panel A of Figure 6, and the average price in the subsample employed in the estimation of each of the age-specific semi-elasticities. Panel A of Figure 7 displays the no-policy counterfactual cumulative age-specific total fertility rate. At age 45, this provides the no-policy counterfactual total fertility rate: 2.68 (SE 0.04). The results indicate that the policy decreased the total fertility rate by 0.30 (SE 0.04) or 11.37 percent (SE 1.20 percent).

The quotient between the male and female age-specific fertility rates provides the age-specific sex ratio. Panel B of Figure 7 displays the realized and no-policy counterfactual cumulative age-specific sex ratios. The age pattern shows how the policy distorts the sex ratio over the ages in which women are fertile.^{35} At age 45, the figure displays the “final” sex ratio at birth for the sample analyzed. If the sex ratio were not distorted, the age profile would be flat at the natural sex ratio (1.055).^{36} To aid interpretation, I subtract 1.055 from the age-specific quotients and multiply the resulting quantity by 100. That yields the excess of boys over the natural sex ratio for every 100 girls born. As discussed in Section III, the sex ratio at birth was distorted in China before the one-child policy for cultural and economic reasons. The policy distorted the ratio further by 1.15 (SE 0.36) boys for every 100 girls born. The semi-elasticities in Section III indicate that the distortion results from the policy curbing the probability of having daughters for mothers whose first children are girls.

## V. Summary and Implications for Fertility after 2000

I characterize China’s one-child policy as an individually tailored pricing system allowing women to have second and third children. I map this characterization to a longitudinal sample of women that annually replicates the national total fertility rate during the period 1979–2000. This allows me to exploit within-woman price variation to identify policy elasticities using a dynamic panel data model. The model has the flow of children as the dependent variable. That is convenient because the age-specific expectation of the dependent variable is the age-specific total fertility rate in the sample. The cumulative age-specific fertility rate at age 45 is the total fertility rate. Subtracting the prediction associated with the policy price from these age-specific fertility rates enables computing the no-policy counterfactual total fertility rate and sex ratio.

I find that the response to the policy was price-inelastic. Nonetheless, my estimates indicate that the one-child policy lowered the total fertility rate by 11 percent, for a large cohort of women who were in their fertile years between 1979 and 2000. This decrease resulted entirely from a decrease in the probability of having a girl. The policy priced all children, but it only curbed the number of daughters that women had. It did not affect their number of sons. The evidence in this paper indicates that the gendered impact of the policy was generated by a combination of a stopping rule and sex-selective abortions. Women whose first children were boys did not pursue fertility further. Women whose first children were girls pursued fertility further. Restricted by policy prices, they used sex-selective abortions to increase their chances of getting at least one son.

Below-replacement fertility rates are now a policy concern in China (Morgan, Zhigang, and Hayford 2009). The Chinese government recently announced relaxations of the one-child policy (BBC 2021). In 2015, it announced that essentially all couples would be able to have two children. In 2021, it increased the limit to three children. Figure 1 shows that the total fertility rate remained remarkably stable in China after 2000. I speculate that in 2000, fertility reached a level in which restrictions were no longer binding. The relaxations to the policy are likely nonbinding and will have little effect on fertility. The inelastic response to China’s one-child policy indicates that only large monetary incentives would be effective at increasing fertility. Such incentives would need to consider the potential of fertility policies to imbalance the sex ratio.

## Acknowledgments

The author thanks Stéphane Bonhomme, James J. Heckman, Alessandra Voena, and Anna L. Ziff for feedback and guidance during different stages of this project, as well as Nancy Qian for useful comments. The author has no relevant conflicts of interest to disclose. The data used in this article can be obtained from the website of the China Health and Retirement Longitudinal Survey (http://charls.pku.edu.cn/index/en.html). Replication materials are provided in the Online Appendix.

## Footnotes

↵1. The precise statistic is 504.3 million. It is the total number of women who were between 15 and 45 years old for at least one year between 1979 and 2010 according to the 1982, 1990, and 2000 census (Minnesota Population Center 2017).

↵2. Sen (2015); Whyte, Feng, and Cai (2015); and Huang, Lin, and Zhang (2019) elaborate on this argument.

↵3. Throughout the paper, I refer to “women,” “women and their partners,” and “households” as the units of observation who are making fertility decisions and paying the prices.

↵4. Anecdotal evidence indicates that reductions in social security, forced abortions, and sterilization were other policy-enforcement mechanisms. These mechanisms were not official and are impossible to formally quantify. I discuss how ignoring them could bias my results in the body of the paper.

↵5. This rate may appear to be high. However, note that the total fertility rate considers all women who were 15–45 years old between 1979 and 2000. Some women could have had a relatively large number of children before the policy and still be included in the calculation of the total fertility rate. More importantly, women were allowed to have two or three children if they paid the policy prices. Especially in rural areas, average completed fertility in the later part of the 20th century is well known to be greater than one.

↵6. Li, Zhang, and Zhu (2005) study the impact of the policy on fertility using this same variation and one of the exemptions that I use (based on ethnicity). Other studies use similar designs to study the policy impact on fertility as a first stage when analyzing outcomes such as migration and intergenerational quantity–quality trade-offs (for example, Li and Zhang 2017; Liu 2014; Wang, Zhao, and Zhao 2017). McElroy and Yang (2000) use county-level variation in policy intensity to study fertility in a cross-section of households from a handful of provinces surveyed in 1992.

↵7. This male-biased preference is widespread in China and East and South Asia (for example, Das Gupta et al. 2003). Anukriti (2018) reports a male-biased sex ratio beyond the natural rate in Albania, Armenia, Azerbaijan, China, Georgia, India, South Korea, Macedonia, Montenegro, Nepal, and Vietnam. Between 1980 and 2015, the percentage of the world’s population inhabiting these countries remained stable at 40 percent (World Bank 2017b), which illustrates how widespread sex-selection practices are. Anukriti (2018) reports the same bias in Asian populations in Canada, Greece, Spain, the United Kingdom, and the United States.

↵8. Massive waves of rural-to-urban migration began in the mid-1990s (Chan 2001). These waves happened too late to affect the core of the sample that I analyze.

↵9. The empirical analysis here relies on within-woman policy variation. Including policies that preceded the one-child policy requires documenting and justifying other types of variation, which falls outside the scope of this study. Babiarz et al. (2018) and Banerjee et al. (2014) are examples of studies that analyze or include policies that preceded the one-child policy.

↵10. Given the size of China’s population, registering every single birth and later enforcing the pricing system associated with the one-child policy suggests the need for an immense bureaucracy. Employment in birth-planning commissions grew from fewer than 5,000 employees in 1970 to approximately 400,000 in 1995 (Scharping 2003).

↵11. Ebenstein (2010a) documents province-level, year-specific values of Ξ

_{ia}for the period 1979–2000. He uses a 2 percent discount rate.↵12. It is possible to construct Ξ

_{ia}for any woman, independently of her stock of children, given her demographic characteristics and the calendar year when she is*a*years old. If she has no children, Ξ_{ia}is the policy price that she would have needed to pay to have a second or third child, if she would have had one or two children instead of zero.↵13. Retrospective fertility information could be advantageous in this context. Chinese parents underreported their number of children when the children were between ages zero and four in the 1990 and 2000 census (for example, Goodkind 2004, 2011). Underreporting is less prevalent as children become older (Yi et al. 1993).

↵14. An important caveat is worth noting. Life expectancy for the older cohorts in the sample was relatively high (World Bank 2021). Thus, the samples analyzed by the World Bank (2017a) to calculate the annual fertility rates and the sample analyzed in this paper could be selected. This selection would compromise the validity of the estimates as representative of the women affected by China’s one-child policy. The average age in the sample that I analyze is 32 (right around the middle of the assumed ages in which women are fertile). This fact together with the replication of the annual fertility rate in the World Bank (2017a) ameliorate this concern, but do not discard it definitively.

↵15. After accounting for the policy exemptions, the price is zero for 24 percent of the (longitudinal) sample observations. My empirical analysis uses the price in logarithmic form. I follow the common practice of adding one to the price before taking the natural log of the price throughout the paper. This transformation enables straightforward interpretation of my estimates as elasticities, but is not necessarily innocuous. I justify this decision by comparing results using prices in logarithmic form and prices in levels in the Online Appendix. The checks show that my main estimates remain stable when calculating elasticities from the estimates obtained using regressions in levels. The reason for this robustness is that the distribution of the prices is tight, containing most of the values greater than zero in the interval (0,3]. An alternative is to estimate specifications using geometric transformations. I do not explore this alternative given that the regressions in levels yield results that are very similar to the results obtained from regressions using the logarithmic transformation that I employ.

↵16. This price amounts to 13,898 if adjusted for purchasing-power parity. I round this adjusted price to 13,900 in the abstract of the paper.

↵17. The birth rate targets that the mayors intended to impose were part of the Five-Year Plans of the local Communist Party. The net birth rate is the crude birth rate minus the crude death rate. Suárez-Serrato et al. (2019) digitized the Provincial Five-Year Plans in 1985, 1990, and 1995. A province’s 1985 plan set the target for 1986–1990, and similarly for the 1990 and 1995 plans. The years documented between 1985 and 1990 by Suárez-Serrato, Wang, and Zhang (2019) are sparse, and that impedes estimating Equation 2 below. I thus only consider the panel of mayors for the years between 1990 and 2000.

↵18. The survey asked the officials for estimates of the value of Ξ

_{ia}for the general population. It also asked them for estimates for ethnic minorities and for women with first-child girls. The survey did not ask for estimates for the other cases in Table 1. For these other cases, I apply the exemptions to the policy and set to zero in the cases that I set Ξ_{ia}to zero. In the empirical analysis, I apply to the same logarithmic transformation applied to Ξ_{ia}.↵19. For a small number of women getting pregnant late in the calendar year, the price at age

*a*could be the most immediately relevant. This imprecision is another motivation to account for measurement error.20. I consider at most 11 periods (

*s*= –5,. . .,5) per woman (recall that the panel is unbalanced). I drop observations before −5 or after 5. Only a handful of women in the sample face more than one price spike. When this occurs, I consider the first spike for estimating the model in Equation 4. Online Appendix Figure A.4 shows that defining the events using other percentiles yields the same conclusions as those summarized by Figure 5. Only a handful of women do not face a price spike based on either Ξ_{ia-1}or included in the exercise discussed here or in the exercises of Online Appendix Figure A.4.↵21. There is individual-level variation in the timing of treatment in this design. Recent research points out that variation in the timing of treatment compromises the interpretation of difference-in-difference designs constructed in a way similar to Equation 4 (for example, Callaway and Sant’Anna 2021; de Chaisemartin and D’Haultfoeuille 2020; Goodman-Bacon 2021). My identification strategy below is not based on difference-in-differences. Figure 5 only aims to illustrate a trend break in the (residual) flow of children after a price spike. The stability at zero before the spike could be driven by across-individual averaging out of increasing and decreasing trends, as pointed out by Sun and Abraham (2021). However, the objective of Figure 5 is only to illustrate the break after the price spike, and not to show that trends are parallel before such a spike.

↵22. Examples of studies using price spikes to justify exogeneity in prices determined by policies include Simon (2016) and Fuest, Peichl, and Siegloch (2018).

↵23. To see this, note that mean independence and γ

_{n–1}= 0 imply that . Consider two prices and with (that is, is 1 percent larger than ). Then, . If Δ*n*is an indicator of having a child, it follows that_{ia}*γ*_{Ξ}is the percentage point change in the probability of having a child upon a 1 percent price increase (recall that twins and higher-order births are minimal in the sample, so I reclassify Δ*n*as an indicator of whether woman_{ia}*i*has a child at age*a*).↵24. The transformation uses the definition of Δ

*n*:+_{ia}*n*–_{ia}*n*_{ia}_{–1}and moves the term*n*_{ia}_{–1}to the right-hand side of Equation 5. I subtract one from estimates of (1 + γ_{n–1}) to obtain estimates of γ_{n–1}from Equation 6.↵25. Two practical aspects of this estimator are worth clarifying. First, its consistency properties hold when the number of individuals is large and the number of periods in which these individuals are observed is fixed. The sample analyzed satisfies this requirement. Second, exploiting the moment condition 𝔼[

*n*_{ia}_{–b}·Δɛ_{ia}] = 0 for*a*≥ 3 and*b*≥ 2 requires observing at least three periods for each women in the sample. All of the 6,950 women in the sample satisfy this requirement. If more lags are considered in Equation 6, more periods of individual observation are required. The average number of periods in which women are observed in the sample is 16.5, which allows including multiple lags with little loss of individual observations.↵26. Table 3 provides evidence of the persistence of the fertility process. Across specifications, , the coefficient estimate characterizing persistence, is at least 0.84.

↵27. When using GMM, I employ the standard two-step efficient weighting of the system of moment conditions.

↵28. Note that these moment conditions are weaker than strict exogeneity. Identification is possible under these weaker conditions because of the rest of the additional moment conditions in the system discussed before.

↵29. The fact that the system-GMM estimator yields similar estimates to the OLS and logit estimator when not accounting for measurement error does not imply an instrumental-variable estimator correcting for measurement error suffices to tackle the challenges at hand. My preferred system-GMM estimator accounts for all of the issues

*simultaneously*. Using instrumental variables without solving the endogeneity of the stock is an incomplete solution that leads to different point estimates than those that I present as preferred.↵30. The standard errors in the last column of Panel A of Table 3 are robust to heteroskedasticity, as in White (1980). They include the finite-sample correction of Windmeijer (2005), which is relevant when using two-step GMM. The standard error of the semi-elasticity 0.052 is 0.007. Alternatively, I compute bootstrap standard errors clustered at the province × cohort level and at the province level and find that they are 0.005 and 0.006, respectively.

↵31. Inelastic policy-benefit responses have been documented in Australia, Canada, Europe, the United States, and the United Kingdom (Bergsvik, Fauske, and Hart 2021). Studies documenting related elasticities in France, Germany, Israel, and Spain are Cohen, Dehejia, and Romanov (2013); Ebenstein, Hazan, and Simhon (2016); Gathmann and Sass (2018); González (2013); Laroque and Salanié (2014); and Manski and Mayshar (2003).

↵32. The moment conditions are 𝔼[

*x*·Δɛ_{ia}_{ia}] = 0 for*x*= {abortions_{ia–b}, boys_{ia–b}, girls_{ia–b}} with*a*≥ 3 and*b*≥ 2, the additional moment condition of the system-GMM estimator 𝔼[Δabortions_{ia–1}· ɛ_{ia}] for*a*≥ 3, and the measurement-error correction moment condition on the prices discussed before.↵33. Throughout this section, I display province × cohort clustered bootstrapped standard errors. The bootstrap allows me to account for the sampling variation in the multiple steps required to calculate the realized and no-policy age-specific and total fertility rates, as well as the excess of boys above the sex ratio.

↵34. The interpretation and construction of no-policy counterfactuals is based on Equation 5, while I obtain my preferred estimate of

*γ*_{Ξ}using Equation 6. That is not an issue because, in Section III, I show that Equations 5 and 6 yield identical estimates of*γ*_{Ξ}.↵35. The low age-specific fertility rates between ages 15 and 20 make the estimates of the sex ratio before age 20 unreliable. I thus set estimates before age 20 to zero and omit them from Panel B of Figure 7.

↵36. The natural (male-to-female) sex ratio at birth is between 1.05 and 1.06. I set it to 1.055 for my calculations.

- Received August 2020.
- Accepted February 2022.

This open access article is distributed under the terms of the CC-BY-NC-ND license (https://creativecommons.org/licenses/by-nc-nd/4.0) and is freely available online at: https://jhr.uwpress.org.