ABSTRACT
This work examines a schooling expansion in Romania that increased educational attainment for successive cohorts born between 1945 and 1950. We use a difference-in-regression discontinuities (D-RD) design based on school entry cutoff dates to estimate impacts on mortality using 1994–2016 Vital Statistics data, self-reported health in the 2011 Romanian Census, and hospitalizations from 1997–2017 in-patient registers. We find that the schooling reform led to significant increases in years of schooling but did not affect mortality, hospitalizations, or self-reported health. These estimates provide new evidence for the causal effect of education on mortality and health outside of high-income countries and at lower margins of educational attainment.
I. Introduction
There is substantial evidence showing that more educated people have better health and longer life expectancies. However, whether this correlation reflects a causal relationship remains an open question. A number of recent studies have used changes in compulsory schooling requirements to identify the causal impact of schooling on mortality in the United States (Lleras-Muney 2005; Mazumder 2008), the United Kingdom (Clark and Royer 2013; Davies et al. 2018), France (Albouy and Lequien 2009), the Netherlands (van Kippersluis, O’Donnell, and van Doorslaer 2011), Sweden (Meghir, Palme, and Simeonova 2018), and Taiwan (Kan 2016). While this empirical approach can be compelling, the findings have been mixed and sometimes contradictory, even when based on the same educational expansions. Moreover, most of these studies are focused on high-income countries, where compulsory schooling laws usually affect students already enrolled in secondary school. As a result, we know relatively little about the causal effect of education on health and mortality in low- or middle-income countries and at lower margins of educational attainment.
We examine the impact of a schooling expansion in Romania during the late 1950s and early 1960s, which sought to provide all students with at least seven years of compulsory education. We show that successive cohorts of individuals, born between 1945 and 1950, who were affected by this schooling expansion, experienced rising educational attainment. We first consider a regression discontinuity (RD) design at the day level to compare individuals born just before the school entry cutoff of January 1 with those born just after, who were almost identical in age but began school later and therefore had greater opportunities to extend their education. However, since students born immediately before and after January 1 were also the oldest and youngest in their respective cohorts, we draw on cohorts born after the systematic schooling expansion had concluded and utilize a difference-in-regression discontinuity (D-RD) design to separate the effect of increased education from that of relative age and other confounding shocks.
Using the complete count (100 percent) Romanian Census in 1992, we demonstrate that Romania’s schooling expansion led to significant increases in years of schooling for the affected cohorts born between 1945 and 1950. This is driven by an increase in the fraction of students who continue beyond the four years of primary school to complete an additional three years of lower secondary education, with some students continuing even further onto upper secondary schools.
To calculate our mortality and health outcomes we use high-quality data from Vital Statistics records, which are rarely available in middle- and low-income countries. Detailed information on deaths from 1994 and 2016 indicates that the schooling expansion did not reduce the mortality of affected cohorts up to the age of 71, nor are there reductions in mortality from more specific causes of death. We also examine two health outcomes that may affect the quality of life and life expectancy: the total number of days spent in hospital (overall and by specific cause of hospitalization) based on individual-level Romanian Inpatient registers from 1997–2017 and a measure of self-reported health problems using data from the 2011 Romanian Census. For both of these outcomes, the estimated effects are small and insignificant, suggesting that the schooling expansion had no discernable impacts on health.
While we have good measures of mortality and health, we lack data on socioeconomic outcomes, such as income or earnings. We examine several outcomes available in the 1992 census, such as employment or occupational skills, but these do not vary much in Romania’s highly centralized economic system in the immediate period following the fall of communism. The results for these socioeconomic outcomes, as well as fertility, suggest positive effects but are not robust across all specifications.
Our main findings indicate that more education does not help individuals avoid or postpone deaths during middle and old age. This is consistent with the null results in the most recent papers by Clark and Royer (2013) for the United Kingdom and Meghir, Palme, and Simeonova (2018) for Sweden. However, to the best of our knowledge, this is the first work to provide compelling estimates for the causal effect of education on mortality outside of high-income countries and at lower margins of educational attainment. We do not interpret these estimates as an argument against further educational expansions in the developing world. But they do suggest the need to be more circumspect about the potential for such expansions to improve health and increase life expectancy, at least at lower margins of educational attainment.
In the following, Section II reviews the related literature. Section III provides a background of the Romanian educational system and the schooling expansion. Section IV describes the data. Section V explains the empirical strategy. Section VI presents the results, and Section VII concludes.
II. Related Literature
This section reviews some of the previous literature estimating the causal impact of education on health and mortality. We begin with a discussion of studies that take advantage of changes in compulsory schooling requirements. Then we describe some of the alternative empirical approaches used for identifying the causal effect of education at higher margins of educational attainment. For more detailed reviews of these and other studies, see Grossman (2006), Mazumder (2012), and Galama, Lleras-Muney, and van Kippersluis (2018).
For the United States, Lleras-Muney (2005) uses census data to examine the impact of changes in compulsory schooling laws between 1915 and 1939 that affected students older than 14 years of age. Her instrumental variables (IV) estimates indicate that an additional year of schooling leads to significant declines in the probability of dying in the subsequent ten years. In a follow-up study, Mazumder (2008) notes that these results are not robust to the inclusion of state-specific trends but presents evidence from the Survey of Income and Program Participation (SIPP) showing positive impacts of education on self-reported health status. Relatedly, Black et al. (2015) argue that virtually all of the variation in mortality rates is captured by cohort effects and state effects, making it difficult to reliably estimate the effects of changing educational attainment due to state-level changes in compulsory schooling.1
For the United Kingdom, Clark and Royer (2013) use changes to British compulsory schooling laws in 1947 and 1972 that increased the minimum school leaving age from 14 to 15 and then from 15 to 16. Their regression discontinuity design does not indicate a positive impact of education on mortality or other health outcomes. Davies et al. (2018) reexamine the 1972 change in compulsory schooling using UK Biobank data and find a statistically significant decline in mortality, but their results are somewhat sensitive to functional form.
Other studies are mostly focused on other European countries. For Sweden, Meghir, Palme, and Simeonova (2018) do not find improvements in mortality and other health measures for affected cohorts following an educational reform in Sweden that raised the number of years of compulsory schooling from seven or eight to nine, eliminated early selection based on academic ability, and introduced a national curriculum. Arendt (2005) and Albouy and Lequien (2009) also find no statistically significant impact of compulsory school reforms on health outcomes in Denmark or mortality in France, respectively. Yet van Kippersluis, O’Donnell, and van Doorslaer (2011) do find that increasing compulsory school beyond Grade 6 in the Netherlands leads to a significant reduction in mortality in old age.
Outside of the United States and Europe, Kan (2016) studies Taiwan, which looks like a developed country by most measures, and finds that the extension of compulsory education from six to nine years reduced the mortality rate for men but did not affect women’s mortality. In a paper contemporaneous with ours, Dursun, Cesur, and Mocan (2018) examine the effect of a Turkish schooling expansion on measures of health, but not on mortality.
A different set of studies use draft avoidance behavior in the United States during the Vietnam War to estimate the impact of college education on mortality and health outcomes. Buckles et al. (2016) show that the increased college-going among men in cohorts associated with greater draft avoidance also leads to lower mortality in subsequent years. Grimard and Parent (2007) and De Walque (2007) use a similar identification strategy to estimate impacts on smoking behavior and find evidence suggesting that more education reduces the take-up of smoking and current smoking. That the causal impact of education on mortality at the college margin appears to differ from the impact at the margin of compulsory schooling suggests that looking at another margin of educational attainment could also be informative.
In our review of the literature, and in those by Grossman (2006) and Galama, Lleras-Muney, and van Kippersluis (2018), we have not found any papers that provide compelling causal estimates for the impact of education on mortality in low- and middle-income countries and at lower margins of schooling.2
III. Background on Education in Romania
A. Historical Context
During the post-war period, the structure and the organization of education in Romania were largely based on that of the Soviet Union, as codified by Decree No. 175 of 1948 (Braham 1972). There were several types of schools offering elementary and secondary education. First, there were four-year primary schools that offered compulsory primary education from Grades 1–4. Second, there were seven-year general schools, called gymnasiums, which offered the same first four grades as primary schools, but also Grades 5–7 (that were later extended to include Grade 8). These gymnasiums corresponded to lower secondary education according to the International Standard Classification of Education (ISCED) and are still referred to as such today.3 However, not all localities provided lower secondary education, especially in rural areas.4
Third, there was upper secondary education that included vocational and technical schools, often operated under the supervision of the large state enterprises or collective agricultural farms, and (academic) high schools that provided education (Grades 8–11) and prepared students for the baccalaureate exam, which was a prerequisite for entry into higher education (university).5 These upper secondary options were available only to graduates of gymnasiums, that is, those who completed Grade 7 of lower secondary schools.
Upon completing their education, individuals entered a labor market characterized by a centralized wage-setting process, with standard rules based on occupation and industry (Andrén and Andrén 2015). Similar to other communist countries, the highly centralized political system maintained small wage differentials that only varied with the workers’ education, experience, and occupation (or industry). Many individuals with lower levels of education worked on collective agricultural farms that paid fixed wages. Thus, while wages did differ by occupation or experience, returns to education under communism were substantially lower than in free-market economies.
During the late 1940s and early 1950s, Romania’s government focused on providing basic literacy education for all ages.6 By the mid-1950s, it turned its attention towards increasing enrollment beyond the first four grades. According to Giurescu, Ivanov, and Mihaileanu (1971, p. 351), the five-year plan of 1955–1960 specified that the extension of compulsory schooling to seven years was to be given special attention by the party and government. Thus, the directives of the Communist Party’s Second Congress of 1955, which outlined the second five-year plan, envisioned a “situation under which, by 1960–1961, the fifth grade would enroll 90 percent of the four-year school graduates; and under which, according to the Third Five-Year Plan, the seven-year school would be universal and compulsory” (Braham 1963).
The extension of compulsory schooling from four to seven years meant that lower secondary schools (that is, gymnasiums) had to take in a surplus of children who graduated primary school and who otherwise would not have continued their education. Braham (1963) notes, “At first, only the first four grades were made compulsory, but villages and rural communities having seven-year schools were required by virtue of Decision No. 1035/1958 to make the seven year schooling period universal beginning with the 1958–1959 academic year.”7 Nevertheless, the process to provide graduates of four-year schools access to lower secondary education was not immediate and was constrained by a lack of enough schools offering seven years of compulsory schooling.8 Filipescu and Oprea (1972) confirm the gradual process of expanding education at the lower secondary level. They explain that the expansion of seven-year compulsory education began in 1956 within towns and larger villages that already had schools beyond the fourth grade and that it gradually expanded until it was close to universal by 1961–1962.
B. Patterns over Time
We can document some of these changes in schooling levels using aggregate administrative data on enrollment from the Annual Statistics of the Socialist Republic of Romania. Figure 1 shows the number of students graduating from lower secondary schools (gymnasiums) between 1951 and 1969. During this period, graduation from these lower secondary schools increased sharply from 116,698 in 1959 to 329,739 in 1963 and stayed at similar levels through the late 1960s. Braham (1963) confirms that during the period 1960–1965 the state boosted the funds for education, which led to the construction of more than 15,000 classrooms (of which about 70 percent were in rural areas). The number of teachers employed also increased, especially between the 1960–1961 and 1967–1968 academic years, with the largest increase of 70 percent in Grades 5–11 (Braham 1972). Accordingly, the overall pupil-to-teacher ratio remained largely similar during this period.9
Graduates from Lower Secondary (Gymnasium) Schools by Year of Graduation
Source: Romanian Statistical Yearbook
Notes: The figure plots the number of students graduating from seven-year gymnasium between 1951 and 1969.
Further evidence for these dramatic changes can be observed at the cohort level. By law, students entered Grade 1 in September of the year following the calendar year in which they reached six years of age. Thus, the cohort born in 1945 was six years of age in 1951, entered first grade in the fall of 1952, entered fifth grade in the fall of 1956, and would have graduated with seven years of schooling in the spring of 1959. This cohort should be the first cohort that could have been affected by the policy reform. Similarly, the cohort born in 1947 was the first cohort to have potentially benefited from the 1958 Government Decision that made seven-year of schooling compulsory. Finally, the cohort that entered fifth grade in 1961–1962, which was the first cohort to have achieved universal seven years of compulsory education, according to Filipescu and Oprea (1972), was born in 1950.10
Figure 2 shows the highest education level completed by year of birth in the Romanian Census of 1992. For our main cohorts of interest, born 1945–1950, we see a sharp decline in the proportion of individuals with primary education only and a sharp increase in the proportion of individuals who have secondary education. For the cohort born in 1950, the fraction with only a primary education was below 8 percent, suggesting that seven years of compulsory schooling was nearly universal. For cohorts born after 1950, the levels of primary and secondary schooling are much more stable, with only gradual changes over time. It is also apparent that cohorts born before 1944 experienced large increases in educational attainment, which were mainly driven by the successful literacy campaigns mentioned earlier.
Educational Attainment in Romania by Year of Birth
Source: 1992 Romanian Census (complete count).
Notes: The figure plots the highest educational attainment by year of birth for cohorts of individuals.
It is important to note that graduation from lower secondary schools opened up opportunities for further educational attainment at the upper secondary level and potentially even higher education.11 In other words, Romania’s schooling expansion enabled individuals to continue beyond primary education. In Online Appendix Figure 1, we plot the “residual” percent of individuals born between 1944 and 1955 who completed primary education or less by their month of birth, after accounting for calendar month of birth effects. Consistent with Figure 2, we observe a large decrease in the proportion of individuals who have only primary education or less among those born between 1945 and 1950. More importantly for our empirical strategy, these declines in primary education occur discontinuously, with disproportionately large decreases for those born after January 1. At the same time, no declines are visible for the cohorts born between 1951 and 1953, which we will use as controls in our empirical strategy. The patterns in this figure suggest that we can use detailed information on date of birth to estimate the impact of the schooling expansion using a regression discontinuity design.
To summarize, the graphical evidence shown here is broadly consistent with the historical record of educational reforms in Romania. Educational attainment beyond the first four years of primary schooling expanded from the 1956–1957 school year such that, by 1961–1962, enrollment in lower secondary education was nearly universal. Thus, the schooling expansion affected cohorts born starting in 1945 and was essentially completed for cohorts born after 1950. Though we do not have a direct measure of changes in the quality of schooling during this period, Braham (1972) confirms that the curriculum and the educational standards in general schools did not undergo any major changes until 1969.12 Moreover, as in other communist countries, the school curriculum and standards in Romania were centrally planned and standardized across schools (see also Braham 1972).
IV. Data
Our main sample consists of individuals born in Romania between 1945 and 1953.13 Those born in 1945–1950 were enrolled in the affected grades during the period of schooling expansion, while those born in 1951–1953 were enrolled after the expansions had already been completed. As we explain in our discussion of the empirical strategy in Section V, we use the three subsequent cohorts born immediately after the end of the schooling expansion to account for the independent effect of relative age, to address the possibility of school-cohort-specific shocks, and to deal with the misreporting of births.14 Moreover, as shown in Figure 2, these cohorts did not experience any large changes in the level of the highest completed education.
We compiled information on these cohorts from several different data sets. We use the complete count (100 percent) 1992 Romanian Census, when individuals were 38–47 years of age, to estimate the impact of the schooling reform on the level of completed education and certain labor market outcomes and to conduct specification checks of our empirical strategy. Two features make this data set especially useful for our analysis. First, with more than 300,000 observations in each yearly birth cohort, we have substantial power to employ a regression discontinuity design. Second, there is detailed information about the day, month, and year of birth, so we can identify the discontinuity induced by the policy within a narrow window.
The 1992 census provides detailed information about the highest level of completed education for each respondent according to the following categories: none, primary, lower secondary (gymnasium), upper secondary (measured separately as academic high school, vocational, and technical schools), and university or higher education. For simplicity, we impute years of schooling by assigning the number of years associated with each level of education.15 This serves as our main measure of schooling when estimating the impact of the schooling expansion. The census also has information on the socioeconomic characteristics of our respondents, such as gender, ethnicity, and region of birth. We use these variables to validate our research design. Furthermore, it contains information on labor force participation and occupational status (for those employed), as well as the fertility of women, which serve as useful ancillary outcomes. We can also reconstruct household composition to look at spousal schooling if spouses live in the same household.16
Panel A of Table 1 presents summary statistics for the individuals in cohorts born between 1945 and 1953. However, we also collapse the data to the day-of-birth level (3,240 observations) because that is the relevant unit of analysis for our regression discontinuity design. The average age at the time of the 1992 census is 42.5 years, and the fraction of female respondents is almost half. Approximately 90 percent of the sample is ethnic Romanian, with 7.7 percent ethnic Hungarians, and about 1.2 percent Roma. The average years of schooling in our sample is 9.9, which is imputed based on the highest level of education completed. The employment rate is just below 85 percent, while the average level of occupational skill is based on the classification suggested by the International Labour Office (ILO), ranging from 1 to 4.17 Note that only 3 percent of the sample are unemployed, and most of the other nonemployed individuals were housewives (women working in household and agricultural activities). The average number of children born to women in our sample is 2.3.
Summary Statistics
We use the 1994–2016 Vital Statistics Mortality files (VSM) to estimate the impact of the schooling expansion on mortality. These individual-level data cover the universe of deceased persons in Romania with detailed information on the day of birth and death and the main cause of death, as well as some socioeconomic characteristics.18 Thus, we can observe mortality for the cohorts used in our analysis between the ages of 41 and 71 by day and year of birth.19 We compute mortality by day of birth as follows: (i) we sum the number of deaths at each day of birth from 1945 to 1953 over the period 1994–2016; (ii) we estimate the population at risk by calculating the number of people alive in 1992 at each day of birth from 1945 to 1953; then we take the ratio of (i) to (ii). This yields a mortality rate by day of birth that is at the finest level of our running variable.
Our calculation of the mortality rate could differ from the true mortality because of migration in and out of Romania. However, the number of migrants into and out of Romania was very small prior to 1992 because of the closed borders during communism. Thus, the denominator described in (ii) above, based on the complete count in the 1992 census, is likely to be an accurate measure of the population at risk. Moreover, the VSM files include people deceased abroad as long as they still have a Romanian residence and/or citizenship. Therefore, our mortality files should account for the majority of the Romanian migrants abroad who are temporary emigrants and do not change their permanent residence.20 Still, we will directly examine the potential for bias due to migration by checking whether the schooling expansion affects the probability of migration.
The VSM files also provide detailed information on the main cause of death (ICD codes), so we can look separately at deaths associated with circulatory diseases and cancer. These are the two most important causes of death in Romania, accounting for 44.6 percent and 26.5 percent, respectively, of all deaths. Following Meghir, Palme, and Simeonova (2018), we also classify diseases according to the epidemiological literature as preventable and treatable; preventable causes of death may reflect health behaviors, while the treatable causes of death may be related to access to healthcare.21
Panel B of Table 1 shows the overall mortality rate and the mortality rate by category for our main sample. Approximately 25 percent of our sample died between 1994 and 2016. The largest category of deaths was associated with circulatory diseases, which account for 10 percentage points, followed by cancer at 7.4 percentage points. Preventable deaths accounted for 5.7 percentage points, while treatable diseases only for 3.8 percentage points.
We use the 1997–2017 National Inpatient Registers to calculate the number of nights spent in hospitals by day of birth. The National Inpatient register contains individual-level data on duration and ICD codes for all hospital stays in Romanian hospitals beginning with January 1, 1997. Based on about 7,892,000 hospital entries for our cohorts of interest, we calculate that individuals in our cohorts aged 54–72 spent an average of 24.7 days in the hospital, as shown in Panel C of Table 1.
Finally, in the 2011 Romanian Census, all respondents are asked whether they have any health-related problems that may affect their daily life (at work, school, at home, etc.). Thus, we can compute a measure of self-reported health for individuals who survived until 2011. Approximately 7.7 percent of people in our cohorts of interest reported having such problems. Those who answered affirmatively were given a set of six follow-up questions—whether they were (i) visually, (ii) hearing, or (iii) movement impaired; (iv) whether they had any memory or concentration problems; (v) self-care; or (vi) difficulties in communication with their peers.
V. Empirical Strategy
We are primarily interested in the effect of education on mortality and other health outcomes, which can be expressed most simply as follows:
1
where Yi is a measure of mortality or health for individual i, Si is a measure of schooling, Xi represents observed individual characteristics, and εi represents unobserved factors (such as ability or motivation) that influence mortality and health. Since the unobserved factors may also be correlated with schooling and therefore bias our estimates of σ, we use the schooling expansion in Romania to generate exogenous variation in the level of schooling.
A. A Regression Discontinuity Design
The schooling expansion that we study occurred over a five-year period, 1956–1961, and affected those born between 1945 and 1950. Since the government rapidly expanded access to schooling during this time, a child born just after the school entry cutoffs of January 1 of 1945, 1946, 1947, 1948, 1949, and 1950 would have benefited from the additional schools’ slots created by the government over the course of a year, as compared to a child born just before January 1 who would have been part of an earlier cohort. We can estimate these differences in schooling across successive cohorts during the period of schooling expansion using a regression discontinuity design:
2
where Si is our measure of (imputed) completed schooling for individual i, AFTERi is an indicator for individuals born just after January 1, and f (dayi) is a parametric or nonparametric function of the day of birth, which serves as our running variable. For simplicity, our preferred specifications do not include any covariates except for a constant β0, although including them does not affect our results. We stack the discontinuities from 1945–1950 to estimate the average impact of the educational reforms for the affected cohorts. Thus, the coefficient on α is an estimate for the effect of being born just after the school entry cutoff on schooling—in other words, it represents the “first-stage” effect of the schooling expansion on completed schooling.
We can also estimate a version of Equation 2 using our main outcome variables, such as mortality and health, as dependent variables. In this case, the corresponding estimates represent the “reduced-form” effects of the schooling expansion on mortality and health. Given that children born just before and after January 1 should have very similar background characteristics, we expect that our regression discontinuity design (if correctly specified) to yield causal estimates for the effect of the schooling expansion on these outcomes. If we also assume that the exclusion restriction holds—that is, that being born after the school entry cutoff affects mortality and health only through years of schooling—the ratio of the reduced-form and first-stage coefficients provides an estimate for the impact of education on mortality.
However, children born just after the school entry cutoff are generally the oldest children in their school cohort. Therefore, the exclusion restriction will not hold if relative age has an independent effect on health or mortality.22 Our estimates may also be confounded by school-cohort-specific shocks affecting health and mortality that are correlated with the increase in schooling generated by the schooling expansion. For example, if labor market conditions at entry affect later health and mortality, and these are improving over time, those born just after the school entry cutoff will benefit more than those who are born before it and enter the labor market earlier. Finally, as we document later, there may be some differential reporting of births around the first of every month (and especially around January 1), which cannot be addressed with a standard regression discontinuity design.
B. A Difference-in-Regression Discontinuities (D-RD) Design
In order to account for a (stable) independent effect of relative age on health and mortality, to address certain confounding school-cohort-specific shocks, and to deal with differential reporting around the January 1 cutoff, we use individuals who were born just before and after the school entry cutoff during 1951 and 1953, when lower secondary education was already universal for all the primary school graduates, as a comparison group (that is, these cohorts form our “control years”). We can do this by estimating an analogous regression model to Equation 2 for the discontinuities in the control years and then comparing the impact of being born just after the school entry cutoff in treatment years with control years. This is our preferred specification, and it can be estimated directly with the following “difference-in-discontinuities” (D-RD) regression model:
3
where TREATi is an indicator for individuals born during years of schooling expansion 1945–1950, AFTERi is defined as before, and f (dayi) now includes the interactions of our running variable with both TREAT and AFTER, allowing for different relationships between the outcome and day-of-birth both before and after the threshold, and in the treatment and control periods.23 In this specification, the coefficient on the interaction term, δ, yields the impact of being born just after the school entry cutoff during treatment years over and above the effect in control years that did not experience a compulsory schooling expansion, which is captured by γ. Given our model, the effect of being born just after the school entry cutoff during the treatment years, coefficient α in Equation 2, is equivalent to the sum of γ and δ.
As before, we can estimate a “reduced-form” version of Equation 3 for our main outcome variables. We can also take the ratio of these reduced-form and first-stage coefficients to generate an estimate for the impact of education on mortality. Alternatively, we can estimate a two stage least squares (2SLS) model where we instrument for schooling with the interaction of AFTER*TREAT. The main identification assumptions underlying this empirical strategy are threefold: (i) that the relative age effects are stable across treatment and control years; (ii) that school-cohort-specific shocks, other than the schooling expansion, are balanced across treatment and control years; and (iii) that the misreporting of births is similar for both treatment and control discontinuities.24
We have no reason to expect the relative age effects to vary between treatment and control years, nor are we aware of school-cohort-specific shocks, other than the schooling expansion, that would affect school quality or entry into the labor market. As mentioned earlier, the labor market in communist Romania was strictly controlled and highly regulated, so there were few differences in labor market opportunities for students entering the labor market over short time horizons. Nevertheless, while we estimate and report 2SLS estimates, we do not consider them as our main specification because of the possibility that there were changes in school quality that are not captured by our imputed measure of years of schooling.25 Instead, we follow Clark and Royer (2013) and Meghir, Palme, and Simeonova (2018), by focusing on the reduced-form effects of our school expansion policy.
C. The Regression Discontinuity Specifications
A key consideration when implementing a regression discontinuity design is the functional form of the forcing variable, f (dayi). We estimate our impacts using local linear regressions with a triangular kernel, as suggested by Hahn, Todd, and van der Klaauw (2001). While many recent papers adopt the Calonico, Cattaneo, and Titiunik (2014) optimal bandwidth procedure, this appears to yield excessively small bandwidths in our setting.26 Instead, we present our findings for a fixed bandwidth of 180 days on either side of the cutoff for every specification, while plotting the RD estimates for our main outcomes over a broad range of alternative bandwidths from 180 to 30 days.27 We also confirm that our main results are robust to using parametric specifications that include higher-order polynomials, such as linear, quadratic and, cubic trends in day of birth.
To avoid the issues associated with clustering on a discrete running variable, we collapse the data to the day-of-birth level and estimate our regressions with heteroskedastic-robust standard errors (Lee and Card 2008; Kolesár and Rothe 2018). Thus, as implemented in our regressions, the subscripts i in Equations 1, 2, and 3 refer to cohorts of individuals born on a particular day of birth. However, we also verify that our results hold when we estimate our regressions at the individual level.
A common specification check for the regression discontinuity design is to verify that the density of observations is continuous around the cutoff (McCrary 2008). When we examine the density, we find substantial heaping on January 1 and on some of the days immediately preceding it. This can be seen in Panels A and B of Online Appendix Figure 2, which plot the density around the January 1 cutoff (normalized to Day 0) or the first week of January (normalized to Week 0). We believe that this heaping is mainly due to delays in the reporting of births that occurred during the holiday period between Christmas and New Year’s Day when government offices are closed.28 Indeed, Panels C and D of Online Appendix Figure 2 show similar patterns for our control years.29
As mentioned earlier, we account for the issue of heaping around January 1 with our D-RD specifications that use both sets of years. Accordingly, there are less visible discontinuities in the density in Panels E and F, which difference the impacts of the discontinuities in the control years from those in the treatment years.30 We further attempt to deal with this issue using a “donut-RD” design, as suggested by Barreca, Lindo, and Waddel (2016). In particular, our preferred specification drops individuals born within seven days of January 1 in order to be symmetric around the cutoff (shown in light gray in the figure). We will also show our main results when dropping individuals born within 14 days of January 1, although that does take us further from the ideal of the regression discontinuity design.
A formal test for differences in density around the January 1 school cutoff is shown in Column 1 of Online Appendix Table 1. This reveals no significant differences for either the full sample in Panel A, or the seven-day and 14-day donut specifications in Panels B and C, respectively. In Columns 2–7, we examine whether the covariates available in the 1992 census vary smoothly around the January 1 discontinuity by estimating Equation 3 using these covariates as dependent variables. Among the covariates indicating gender, categories for the main ethnic groups in Romania, and an indicator for being born in Bucharest, only gender is statistically significant across the three specifications.31
VI. Results
In presenting our results, we focus on the impact of the schooling expansion captured by δ, the coefficient on the interaction term of AFTER*TREAT in Equation 3. This represents the effect of being born just after January 1 during the treatment years over and above the effect in control years that did not experience the schooling expansion. We also present the coefficient γ on AFTER, which represents the effect of being born just after the school entry cutoff during control years. As noted earlier, the effect of being born just after January 1 during the treatment years, coefficient α in Equation 2, is equivalent to the sum of γ and δ.32
A. Effects on Educational Attainment
We begin by using the 1992 census to estimate the impact of Romania’s schooling expansion on years of completed schooling (Table 2, Column 1) and for specific educational categories (Table 2, Columns 2–5): completed primary, lower secondary, upper secondary, and higher education.33 We report these first-stage results for our preferred bandwidth of 180 days around the January 1 cutoff. The estimates in Panel A, using the full sample, indicate that each successive cohort during the school expansion period 1945–1950 received an additional one-fifth of a year of schooling relative to later cohorts. Our preferred specification in Panel B, which excludes observations within seven days of the January 1 cutoff, shows an increase of one-ninth of a year of schooling.
Effects of Educational Expansion on Schooling Outcomes
The increase in educational attainment is driven by an increase in the fraction of students who continue beyond the four years of primary school (Column 2) to complete an additional three years of lower secondary education (Column 3), with some students continuing even further onto upper secondary schools (Column 4). The pattern of results is broadly similar across all three panels, including Panel C where we exclude observations within 14 days of the January 1 cutoff.34
Our significant effects on completed years of schooling are robust to alternative bandwidths. Panel A of Online Appendix Figure 6 plots the values of δ from Equation 3 for bandwidths between 180 and 30. The range of these estimates is not altogether surprising given the large number of different specifications that we consider. Overall, these estimates, while being quite precisely estimated, are smaller than those in Clark and Royer (2013) who show first stages between two-fifths and one-half of a year of schooling for the change in compulsory education in Britain, and those in Meghir, Palme, and Simeonova (2018), who show that the schooling reform in Sweden led to an increase of about one-fourth of a year of schooling.35
We also present our first-stage results graphically in Figure 3. Panels A, C, and E plot average years of schooling by day of birth for individuals born six months before and after January 1 of each year; Panels B, D, and F plot the same data by week of birth, which makes it easier to discern the patterns. The graphs are normalized so that Day 0 corresponds to January 1 and Week 0 corresponds to the week of January 1–7, and the fitted lines are based on linear spline regressions. Panels A–D show clear discontinuities after January 1 for both the treatment and the control years. Lastly, Panels E and F use both treatment and control years in an attempt to estimate a version of Equation 3 that differences out the impacts of the discontinuities in the control years from those in the treatment years. While these panels still show some outliers around the January 1 cutoff (shown in lighter gray), these are excluded from our seven- and 14-day donut specifications.36
Regression Discontinuity (RD) Plots of Years of Schooling
Source: 1992 Romanian Census (complete count).
Notes: Panels A and B are restricted to individuals born in the treatment years (1944–1950). Panels C and D are restricted to individuals born in the control years (1950–1953). Panels E and F are restricted to individuals born in both treatment and control years (1944–1953). The open circles indicate the mean of the outcome by day of birth (Panels A, C, and E) or week of birth (Panels B, D, and F). The solid lines are based on linear spline regressions. The light gray lines and circles show our preferred seven-day donut specification (when we drop individuals born within seven days of January 1 in order to be symmetric around the cutoff).
B. Effects on Socioeconomic Outcomes
While the focus of this work is on the effects of education on mortality and health, it is useful to examine whether the expansion also had an impact on other relevant outcomes, such as labor market and household outcomes. These factors represent potential mechanisms for understanding the relationship between education and mortality (as discussed in Galama, Lleras-Muney, and van Kippersluis 2018) and are interesting outcomes themselves.
Table 3 reports estimates for the impact of the schooling expansion on several available socioeconomic outcomes measured in the 1992 census. For labor market outcomes, we consider the effects on employment and occupational skill. Column 1 of Panel A shows the estimates for the likelihood of being employed using the full sample, suggesting that each successive cohort during the schooling expansion was 0.4 percentage points more likely to be employed. The analogous estimates using the donut specifications in Panels B and C are smaller and insignificant. Similarly, Column 2 indicates large increases in occupational skill that are significant in the full sample (Panel A) but not significant in the donut specifications (Panels B and C).
Effects of Educational Expansion on Socioeconomic Outcomes
For household outcomes, Column 3 shows that Romania’s schooling expansion had some significant effects on women’s fertility. For the full sample in Panel A, we estimate that women who were affected by the schooling expansion had 0.03 fewer children. However, the estimated impacts again become smaller and insignificant for the donut specifications in Panels B and C. There are also some significant effects on spousal schooling in the full sample, but these are not robust when dropping observations close to the cutoff.37
We provide a graphical presentation of the impacts of the educational reform on employment, occupational skill, fertility, and spousal schooling in Panels A–D of Online Appendix Figure 4, which plot the difference between treatment and control discontinuities for these outcomes at the weekly level.38
Our estimated impacts of the schooling expansion on labor market and household outcomes suggest that the schooling expansion may have had some consequential impacts, but the effects are not robust across all samples. We consider four possible explanations for these findings. First, because we lack good data on income or wages, we have to rely on somewhat crude measures of labor market outcomes, such as employment, in a setting where labor market participation was very high for both men and women. As a result, we have relatively little variation in these outcomes.39
Second, our cohorts graduated and entered a labor market characterized by a highly centralized wage-setting process, with small wage differentials and high employment. Similar to other communist leaders in the former Eastern Bloc, Ceausescu promoted a policy of equalizing income and material wealth such that socioeconomic conditions were similar across people.40 Equality was one of the fundamental ideological tenets in socialist states, and many individuals (especially at the lower end of the skill distribution) worked on collective agricultural farms and state industries. Therefore, it is not surprising that the effects of education on the probability of employment or occupational skills are small in magnitude and therefore sensitive across different specifications.
Third, it is possible that treated cohorts gained few useful skills despite their additional years of schooling, similar to the findings of Pischke and Von Wachter (2008) for Germany. While we cannot measure the quality of schooling directly, there is no evidence of any major changes in the curriculum and educational standards across schools (Braham 1972). Moreover, as mentioned earlier, there were commensurate increases in the number of teachers, leaving the pupil-to-teacher ratios quite similar over time.
Fourth, the relatively weak impacts of the Romanian schooling expansion on labor market and household outcomes are within the range observed in the broader literature on this topic. Galama, Lleras-Muney, and van Kippersluis (2018) review notes that the estimates of the returns to schooling from educational expansions vary widely from null effects to large effects, depending on the country, the period when the reform took place, and the institutional and labor market conditions at the time of the reform.41
C. Effects on Mortality and Health Outcomes
This section examines whether the school expansion policy had an impact on mortality, our main outcome of interest in this paper. We focus on the mortality rate calculated from Vital Statistics data between 1994 and 2016, as described earlier. Column 1 of Table 4 reveals no evidence of a statistically significant effect of being born after the school cutoff of January 1 on mortality in any of the specifications. These estimates are remarkably stable across the three specifications. Given our preferred estimates using the seven-day donuts, we can rule out, with 95 percent confidence, that the schooling expansion reduced mortality by more than 0.4 percentage points between 1994 and 2016 when the average mortality rate was 25 percent.
Effects of Educational Expansion on Mortality and Health Outcomes
The null effect on mortality is robust to alternative bandwidths. Panel B of Online Appendix Figure 6 plots the values of δ from Equation 3 for bandwidths between 180 and 30. None of the estimates are statistically significant.42 We also present a graphical analysis of the mortality results in Figure 4, which is structured similarly to the one for years of schooling. The patterns in Panels A–F provide a visual interpretation of the regression estimates from Table 4. We do not see evidence for large discontinuities in the mortality rate between 1994 and 2016, and, if anything, they point against the finding that education reduces mortality.
Regression Discontinuity Plots of the Mortality Rate
Source: 1994–2011 Vital Statistics Mortality files and 1992 Romanian Census (complete count).
Notes: Panels A and B are restricted to individuals born in the treatment years (1944–1950). Panels C and D are restricted to individuals born in the control years (1950–1953). Panels E and F are restricted to individuals born in both treatment and control years (1944–1953). The open circles indicate the mean of the outcome by day of birth (Panels A, C, and E) or week of birth (Panels B, D, and F). The solid lines are based on linear spline regressions. The light gray lines and circles show our preferred seven-day donut specification (when we drop individuals born within seven days of January 1 in order to be symmetric around the cutoff).
In addition to the impact of the schooling expansion on mortality, we examine its effect on other measures of health that may affect the quality of life: the total number of days spent in hospital from 1997–2017 based on in-patient registers and self-reported health measured from the 2011 Romanian Census, described in Section IV. We do not find an impact of the schooling expansion on the number of days spent in a hospital, as shown in Column 2 of Table 4, nor are there significant impacts on the number of hospitalizations or on the duration of hospitalizations by a specific cause such as cancer and circulatory diseases (results available upon request).
In Column 3 of Table 4, we show that there are no significant impacts of the schooling expansion on self-reported health problems among individuals who survived until 2011.43 These null effects are estimated with substantial precision in all specifications. Given the standard errors in the seven-day donut specification, we can rule out with 95 percent confidence that the schooling expansion reduced the fraction of people with health-related problems by more than 0.5 percentage points, which corresponds to 0.019 standard deviation units. We also explored the specific dimensions of health problems associated with our variable of self-reported health (that is, vision, hearing, impaired movement, memory, self-care, and communication) and did not find any meaningful impacts for these specific categories.
Finally, we examine the effect of the schooling expansion on specific causes of death. First, we focus on mortality from the two most common causes of death in Romania: cancer and circulatory diseases. The regression estimates for these causes of death are shown in Columns 1 and 2 of Table 5. Second, we classify certain causes of death as preventable or treatable, similarly to Meghir, Palme, and Simeonova (2018), and show them in Columns 3 and 4. These results do not indicate a consistent effect of the schooling expansion on specific causes of mortality.44 Similarly, none of the corresponding graphs in Online Appendix Figure 5 show clear discontinuities around the regression discontinuity cutoffs. Thus, we do not find any more evidence for the impact of the schooling expansion on specific causes of death than on the mortality rate as a whole.
Effects of Educational Expansion on Mortality by Cause of Death
We can express the impacts on mortality and health outcomes as the effect of an additional year of schooling using a two-sample 2SLS framework, where we instrument for schooling with the interaction of AFTER*TREAT following Inoue and Solon (2010). These are shown in Columns 1–3 of Table 6. Our preferred estimates for the seven-day donut specifications suggest that we can rule out, with 95 percent confidence, that an additional year of schooling reduced mortality by more than 1.2 percentage points. Similarly, we can rule out that an additional year of schooling reduced self-reported health problems by more than 0.19 of a standard deviation based on the seven-day donut specifications.
2SLS Estimates of Years of Schooling on Mortality and Health Outcomes
D. Robustness
We consider a number of robustness checks of our main results. These include the following: (i) we only consider treated cohorts born 1949–1952 that are relatively similar in age to our control cohorts; (ii) we drop the 1945 cohort due to the possibility of being affected in utero by WWII; (iii) we separately examine mortality between 1994–2005 and 2006–2016; (iv) we look at mortality rates for people aged 52–62 only; (v) we use alternative polynomial functions of our running variable, instead of local linear regressions; and (vi) we use the uncollapsed individual-level data.
Our findings remain qualitatively similar in each of these alternative specifications. The parametric specifications are shown in Online Appendix Table 4, and the individual-level specifications are shown in Online Appendix Table 5, with all other robustness checks available upon request. We also considered a placebo test in which we looked for discontinuities around July 1 rather than January 1 in treatment and control years. There were no significant effects for years of schooling, socioeconomic outcomes, or on our measures of health and mortality.
To address concerns about bias due to migration, we consider whether our school expansion directly affected the probability of external migration. The 2011 census contains information on all persons who migrated abroad for a period of at least 12 months (at the time of the census). Hence, the vast majority of the Romanian emigrants are covered, that is, all individuals working abroad who maintained their houses, identity cards, and/or remained registered by the Romanian administrative bodies.45 Using a similar strategy as before, Column 1 of Online Appendix Table 6 confirms that the effects are similar for both the treatment and control years. Thus, there is no overall impact of the schooling expansion on the likelihood that individuals (who survived until 2011) have emigrated.
These migration results, while reassuring, are not able to capture the possible effects of the schooling expansion on permanent migration. We address this possibility through an indirect test. Using information from the 1992 and 2011 census samples, we calculate the number of people born on a given day who are in the 2011 census as a fraction of the number in the 1992 census. This ratio should capture a combination of both mortality and migration between 1992 and 2011. Column 2 of Online Appendix Table 6 presents the results and confirm that there is no impact of the school expansion on this combined measure of mortality and migration.
E. Discussion
Our findings indicate that the Romanian schooling expansion led to significant increases in educational attainment but did not improve health or reduce mortality. We estimate null effects on health and mortality measured up to the age of 71 that are reasonably precise. In this section, we attempt to understand and explore the mechanisms underlying these findings.
One potential channel through which education can affect mortality and health is by increasing income and thereby enabling individuals to purchase more health services or better health insurance. While we observe some positive impacts on employment (in the 1992 census) and income (in the LSMS data), these effects are relatively small and sensitive to alternative specifications. As we discussed in Section VI.B, this is likely because of the low labor market returns in communist Romania and could explain why, in our setting, the schooling expansions did not translate into health and mortality effects. However, studies from other European countries also show that education expansions had no impacts on health outcomes, despite more flexible labor markets. One possible explanation is that, compared to the United States, most European countries, including Romania, have had universal public healthcare, so that income differences are potentially less relevant (see also Galama, Lleras-Muney, and van Kippersluis 2018).
Even if more education would have led to better labor market outcomes, the impact of income on health would not necessarily be positive (through access to better healthcare). For example, more income may lead to an increased consumption of unhealthy goods, such as alcohol and smoking. While we find positive and significant correlations between education and smoking in our LSMS surveys, we find no significant effects of education on smoking behavior when we attempt to estimate our regression discontinuity specifications using this data (see Online Appendix Table 3).
It is also possible that our schooling expansions could affect mortality and health through other channels. For example, we find some evidence that Romania’s schooling expansion may have increased occupational skill, although these findings are also sensitive to alternative specifications. Whether this should have led to improved health is not completely clear.46 Similarly, we also observe some positive impacts of the schooling expansion on nonlabor outcomes. We show in some specifications that women with more education have fewer kids. This could also lead to a direct impact on mothers’ health.
Another important channel is skill formation in school. This is especially relevant when an educational expansion affects a large fraction of the population, as in Romania, which may result in lower quality or a different style of instruction (see Galama, Lleras-Muney, and van Kippersluis 2018). Measuring school quality directly is extremely difficult in our setting. However, in communist Romania, the curriculum and syllabuses were centrally prepared and distributed across schools. Moreover, the curriculum of the general schools was standard and suffered no major changes for our cohorts (Braham 1972). Lastly, as we discussed in Section III, during the period we study, the number of employed teachers also increased a lot, especially for the general schools, leaving the pupil-to-teacher ratios largely unchanged over time.
Finally, access to more education could lead to improvements in health and longevity via channels that are not linked directly with standard socioeconomic outcomes, such as monetary resources or fertility. For example, noncognitive skills, peers, social norms, social status, and increased informal connections could all impact health. Given the data we have available, it is very difficult for us to test for these channels.
Thus, while our analysis does not yield any strong conclusions about the role of specific mechanisms in explaining our results, we believe that the null effects of more schooling on health and mortality may be due to both the limited effects of the schooling expansion on labor market outcomes and the free access to healthcare in Romania, consistent with the arguments that this relationship depends on country-specific institutional and political conditions (see Galama, Lleras-Muney, and van Kippersluis 2018).
VII. Conclusion
We analyze a schooling expansion in Romania, which aimed to ensure that all students received at least seven years of compulsory schooling. The schooling expansion affected five consecutive cohorts born between 1945 and 1950 and opened up opportunities for further educational attainment. We use a difference in regression discontinuities design to estimate impacts by comparing the impacts of the schooling expansion in successive cohorts of affected individuals with later cohorts who entered school after the expansion was completed.
We find that beginning school in a (one year) later cohort increases educational attainment by approximately one-ninth to one-fifth of a year of schooling. On the other hand, we do not find any consistent and significant impacts of the schooling reform on mortality, hospitalizations, or self-reported health. Moreover, we can rule out that the schooling expansion reduced mortality by more than 0.4 percentage points between 1994 and 2016, or that it reduced self-reported health problems as measured in 2011 by more than 0.019 standard deviation units for the full sample of individuals in the affected cohorts.
Whether education causally affects health and mortality is an important question for both developed and developing countries alike. However, most of the previous work has focused on the United States and Western Europe. The findings in this literature are mixed, and we lack strong evidence about whether education significantly improves health or decreases mortality. We extend the literature by estimating causal impacts for a population that is substantially poorer and that experienced changes at a lower margin of educational attainment. Our findings indicate the absence of a causal effect of education health and mortality, even in this setting. While we attempted to examine the underlying mechanisms for these findings, more work needs to be done to better understand why we do not observe a strong relationship between education and health across a variety of different settings.
Footnotes
The authors thank Andreea Balan-Cohen for her work on the schooling reform in Romania in an earlier project. They also appreciate comments by Doug Almond, Robert Kaestner, and Bash Mazumder, as well as participants at the ERMAS 2017, the CHERP conference at the Federal Reserve Bank of Chicago, and the NBER Health Economics Spring 2018 program meeting. Andreea Mitrut gratefully acknowledges support from Jan Wallanders and Tom Hedelius Fond and Riksbanken Jubileumsfond. All errors are those of the authors. They have no additional disclosures to report. This paper uses confidential data from Statistics Romania. Researchers can obtain the data for scientific purposes upon sending a formal request (see http://www.insse.ro/cms/en/content/nis-microdata-scientific-purposes). The statistical code necessary to replicate our results is available to researchers as an additional Online Appendix of Replication Materials.
Color versions of some graphs in this article are available through online subscription at: http://jhr.uwpress.org
Supplementary materials are freely available online at: http://uwpress.wisc.edu/journals/journals/jhr-supplementary.html
↵1. In a paper that considers the effect of school quality on health, Aaronson et al. (2021) find that childhood exposure to Rosenwald schools in the Jim Crow South increased life expectancy, after accounting for the negative effects of migration.
↵2. We have limited our review of the literature to the effects of education on own health and mortality. A separate literature has explored the impact of parental education on child health outcomes; see, for example, McCrary and Royer (2011) and Chou et al. (2010).
↵3. See https://eacea.ec.europa.eu/national-policies/eurydice/content/romania_en (accessed August 23, 2022).
↵4. Children who did not have a school offering Grades 5 and above in their locality would have had to commute to a nearby town. The cost of commuting prevented many families from sending their children to acquire additional education, especially in rural areas where children were also expected to help their families with agriculture-related activities and household chores.
↵5. In some large cities, the government provided 11-year schools, which offered Grades 1–11 (four grades of primary + three grades of gymnasium + four grades of high school) in one school building. Note, there were no differences in curricula for Grades 1–4 whether in a primary school, a gymnasium, or an 11-year school, nor were there any differences for Grades 5–7 in a gymnasium or in an 11-year school.
↵6. The Ministry of Education organized literacy courses lasting one to two years for people aged 14–55 and, in some cases, authorized the establishment of two-year elementary schools for literacy.
↵7. Decision No. 1383/1948 had made the first four grades compulsory, but it was only enforced in 1955.
↵8. Braham (1963) notes that “with rural communities retaining the 4-year compulsory level, the lack of detailed planning to elevate their schools to the seven-year compulsory level has left an irregular pattern of schooling in the provinces.”
↵9. Our calculations using the 1967 Romanian Yearbook Statistics reveal quite stable student-to-teacher ratios for the academic years 1960–1961 to 1966–1967: an average of 28 students per teacher for Grades 1–4, and about 21 students per teacher for Grades 5–7 (or 8). We do not have yearly data for the cohorts in school before the 1960–1961 academic year.
↵10. Additional sources indicate that enrolments in fifth grade included 99 percent of the fourth-grade graduates by the 1961–1962 school year, confirming that the seven years of compulsory schooling became universal by this time (Braham 1963).
↵11. The communist regime wished to train “politically reliable workers,” especially in vocational and technical schools that admitted only students who completed seven years of compulsory education. They often offered the possibility of taking evening or correspondence courses such that workers could attend them without leaving the field of production.
↵12. In 1968, a new reform introduced ten years of compulsory schooling, but this does not affect our cohorts of interest.
↵13. Strictly speaking, because our empirical strategy considers individuals born within 180 days of January 1 for the years 1945–1953, we include those born between mid-1944 and mid-1953.
↵14. The three subsequent cohorts born immediately after the end of the schooling expansion are most similar in age to the cohorts affected by the schooling expansion and offer sufficiently large samples. However, our results are mostly unchanged if we use two, four, five, or six subsequent cohorts as our comparison group.
↵15. We also use data collected by the Romanian National Statistics Institute in 1995 and 1996 with reports of actual years of schooling (rather than educational attainment) in order to validate our imputed measure of years of schooling. These data come from surveys based on the 1994 World Bank’s Living Standards Measurement Studies (LSMS) for Romania.
↵16. Unfortunately, it is not feasible to examine the intergenerational transmission of education using the 1992 Census because (i) we do not observe completed education for all children, and especially for the youngest cohorts in our control years, (ii) we cannot measure schooling for children that no longer live with their parents, especially for the oldest cohorts in our treatment years, and (iii) some of the impacts on fertility raise concerns about changes in the composition of births.
↵17. See more on the classification of occupational skill at: https://www.ilo.org/wcmsp5/groups/public/---dgreports/---dcomm/---publ/documents/publication/wcms_172572.pdf (accessed August 23, 2022).
↵18. The information on day of birth and death is from official records (death certificates, identity cards).
↵19. Lleras-Muney (2005) and Clark and Royer (2013) suggest that the largest effects of education on mortality occur before the age of 64. Life expectancy in Romania was 69.5 years in 1994, 74.2 in 2011, and 75.5 in 2016.
↵20. According to Statistics Romania, these emigrants are the vast majority (more than 95 percent) of emigrants.
↵21. We use the ICD 10 codes for defining cancer and circulatory diseases, as well as treatable and preventable causes of death. See the notes at the end of Table 5 for more information.
↵22. See Bedard and Dhuey (2006) for a discussion on the long-term effects of the relative age effects induced by cutoff date for school eligibility. Cascio and Schanzenbach (2016) also provide evidence on the impacts of relative age in Tennessee, while Black, Devereux, and Salvanes (2011) estimate the effect of starting school younger in Norway.
↵23. This specification is similar to ones used by other recent papers that estimate a difference in RD discontinuities across cohorts. Grembi, Nannicini, and Troiano (2016) provide a more formal presentation of the standard assumptions underlying this setting.
↵24. These factors can be made explicit by writing Equation 1 as Yic = β0 + ηBi + ρcRic + θc + σSi + εic, where Yic is now our outcome for individual i in cohort c, Bi are background characteristics, Ric is relative age, and θc are school-cohort specific shocks. Our RD design assumes that Bi is smooth around the cutoff. Our D-RD design further assumes that ρc and θc − θc–1 (the differences in shocks across successive school cohorts) are similar between treatment and control years.
↵25. Relatedly, Stephens and Unayama (2019) discuss some issues when using instrumental methods with imputed endogenous variables. The recent review by Galama, Lleras-Muney, and van Kippersluis (2018) also mentions that when using education reforms as instrumental variables to study mortality and health the results are, with few exceptions, very imprecise.
↵26. The estimates using CCT bandwidths generally suggest larger impacts of the schooling expansions on educational attainment and socioeconomic outcomes but continue to indicate null effects on health and mortality. Thus, our choice of specification yields more conservative estimates than the CCT bandwidths.
↵27. Our standard errors become extremely large for bandwidths below 30, especially in the donut specifications described below.
↵28. In contrast to most other orthodox denominations, Christmas always remained on December 25 for the Romanian Orthodox. Consistent with this explanation, the spike in observations occurs on January 2 in years when January 1 is a Sunday.
↵29. Torun and Tumen (2016) document a similar pattern of heaping for January 1 in Turkey. Barreca, Lindo, and Waddel (2016) document some heaping at the beginning of each month in the California Vital Statistics records used by McCrary and Royer (2011), which we also observe in our data.
↵30. Any remaining discontinuities in the density could be due to a change in the degree of heaping over time. Given our understanding of the institutional setting, as more children were born in clinics rather than at home, and as the state institutions created by the communist government expanded to rural areas, the correct reporting of the exact date of birth may have improved over time.
↵31. To understand the extent to which this is a problem, we conduct a heterogeneity analysis by gender that yields analogous results for our main outcomes among males and females.
↵32. The results from estimating Equation 2 directly are available upon request.
↵33. Online Appendix Table 3 uses the 1994–1996 LSMS household surveys to estimate the impact of the schooling expansion on reported years of schooling rather than an imputed measure based on completed educational levels. However, one drawback of the LSMS data is that we cannot look at donut specifications. The result on years of schooling shows an increase of about two-thirds of a year of schooling, which is substantially larger than in our specifications in Table 2.
↵34. The coefficient on higher education in Column 5 is positive and significant for the full sample in Panel A, but, in contrast to all the other coefficients, it falls to zero in Panels B and C.
↵35. When estimating our models using the optimal CCT bandwidths, we generate bandwidths that are smaller than 30 days with point estimates of 0.66 for the full sample and 0.34 for the seven-day donut.
↵36. Note, we also examine the effects of Romania’s schooling expansion on each education category recorded in the 1992 census in Online Appendix Figure 3. While there is a clear reduction in the likelihood of completing primary school, the increases are spread throughout the higher levels of educational distribution. This is consistent with our understanding of Romania’s schooling expansion, which required students to complete lower secondary education and opened up opportunities for further educational attainment.
↵37. This is also relevant for the possibility of intergenerational transmission of human capital since parental education has been shown to improve a broad range of child outcomes, including health and education (see, for example, Almond and Currie 2011). Also, as mentioned, we do not find different results when we look separately at our results by gender.
↵38. We can also express the impacts on socioeconomic outcomes as the effect of an additional year of schooling using a 2SLS framework where we instrument for schooling with the interaction of AFTER*TREAT. These are shown in Columns 1–4 of Online Appendix Table 2, where most of the coefficients show significant effects in the full sample but insignificant effects in the seven-day and 14-day donut specifications.
↵39. We do use a set of household (LSMS) surveys collected during the mid-1990s to examine whether the impact of the school expansion affected income and find positive but insignificant effects (see Online Appendix Table 3). Note that, using the 1994–1994 and 1996 LSMS data, we find positive and significant impacts of the schooling expansion on employment. These estimates may be higher than in Table 2 because of the large fluctuations in Romania’s labor market during the early 1990s or because of specification issues in the LSMS where we only observe the month of birth.
↵40. The transition from a centrally planned to a market system resulted in a major but gradual increase in the rates of return to education in the former Eastern Bloc: Munich, Svejnar, and Terrell (2005) show that, in the Czech Republic, the rates of return to education reached the Western European levels in only after 1990.
↵41. Given the findings in Aaronson et al. (2021), we also examined the role of internal migration. However, we did not find significant effects of the schooling expansion on internal migration, measured as an indicator for whether the person lives in the locality of birth in 2011.
↵42. As a result, it is not surprising that our main results on mortality are also small and statistically insignificant when using optimal CCT bandwidths.
↵43. Note that our self-reported health index is explicitly linked with the ability to work and thus with labor market outcomes. However, fewer than 40 percent of individuals who reported an impairment (hearing, visually, or movement impaired, memory or concentration problems, self-care, or difficulties in communication with their peers) also ranked the gravity of their impairment as “great” or “complete insufficiency,” which could arguably impact the ability to be active in the labor market.
↵44. There are some significant (but positive) effects for mortality from circulatory diseases.
↵45. According to Statistics Romania, 95 percent of Romanian emigrants are temporary migrants, who keep their Romanian IDs, and whose death is reported in the Romanian Mortality Files.
↵46. Moreover, skilled occupations may imply better peers, better working conditions, and higher social status which might have a positive impact on health. At the same time, some more skilled occupations may be associated with more stress than certain less-skilled occupations, or it is possible that some relatively skilled manufacturing jobs may have worse working conditions than jobs in the informal sector, such as agriculture; these might have a negative impact on health.
- Received November 2018.
- Accepted December 2020.
