Abstract
Using a state panel from 1940–2010, I examine the impact of immigration on the high school completion of natives in the United States. Immigrant children could influence native children’s educational experience as well as their expected future labor market. I find evidence for both channels and a positive net effect. An increase of one percentage point in the share of immigrants in the population aged 11–64 increases the probability that natives aged 11–17 eventually complete 12 years of schooling by 0.3 percentage point. I account for the endogeneity of immigrant flows by using instruments based on 1940 settlement patterns.
I. Introduction
The extent to which the children of low-education or low-income parents are able to achieve their full potential in the United States is a cause for concern. Contrary to popular mythology, there is less intergenerational mobility in earnings and education in the United States than in continental Europe and Canada, and no more than in the United Kingdom.1 Corak (2013) warns that rising income inequality in the United States may further reduce intergenerational mobility absent changes in public policy. An important step upward for many children from low socioeconomic status families is graduation from high school, yet U.S. high school graduation rates have only recently begun rising again after decades of stagnation.2 In this paper, I contribute to our understanding of the determinants of high school educational attainment by investigating the role of immigration. Increasing immigration in recent decades has led to popular concern that immigration is reducing the quality of K–12 education. If this concern is well founded, rising immigration could reduce native high school graduation rates. Conversely, immigration-induced changes in labor market incentives for educational attainment could have the opposite effect. I seek evidence for these two channels and assess their net effect.
Immigrants and the young children of immigrants generally have a more limited command of English than natives. If immigrants and natives are taught in the same classes, teachers of some subjects may slow the pace of instruction to accommodate nonnative speakers. If immigrant students have had worse quality prior education or have less education than their native classmates, teachers may lower expectations for all students. Chin, Daysal, and Imberman (2013) provide evidence for such within classroom negative externalities by showing that non-Spanish speaking students in Texas have higher test scores when Spanish speakers with limited English proficiency are taught in separate classes rather than integrated into the regular classes, despite an associated shift in spending toward Spanish speakers. In other settings, a diversion of financial resources from native students to support the needs of immigrants could lower the quality of native education. For example, Fix and Zimmerman (1993) find that federal Chapter I spending per economically disadvantaged student fell due to the immigration-induced expansion in the number of eligible children. If poorly educated immigrants moving to a school district reduce the tax base, the total available resources also could fall (whether or not the immigrants have children).
A lower educational quality for natives will reduce their earnings capacity at a given number of years of education, and this lower return to education in turn may induce natives to complete fewer years of high school. This prediction is not unambiguous, however. If high school becomes easier, the fall in marginal cost may outweigh the fall in the marginal benefit and lead to higher native completion rates. Furthermore, if immigrant students are better educated or harder working than their native classmates, they will provide positive peer effects and may relax the resource constraint, and could increase native completion rates.
Immigration does not only influence natives’ high school educational attainment through schools, however. Incentives to complete high school are influenced by the wage structure, which is in turn affected by the entry of immigrant workers: This is modelled formally by Chiswick (1989) and Chiswick, Chiswick, and Karras (1992). Immigration will affect wage inequality among natives if the distribution of immigrant skill differs from that of natives. Compared to natives, immigrants to the United States are very disproportionately poorly educated and somewhat disproportionately highly educated. Immigrants are underrepresented among workers with an intermediate level of education, such as a high school diploma. The effect of immigrants entering the labor market should therefore be to increase wage inequality in the lower half of the native distribution, particularly the wage gap between high school dropouts and high school graduates. Empirical studies confirm this.3 The effect of the changes in the wage structure is likely to be to increase the return to completing high school, and hence native completion rates.4 Native-born youth are likely to be well informed about the dropout labor market even while still high school students, since this is the market in which many seek part-time jobs.5
Any negative effects on the schooling quality of natives will affect the children of low socioeconomic status (SES) parents more than children of high SES parents. Families, whether immigrant or native, tend to locate near other families of similar SES, and the immigrants encountered by poorer native children in their local public school are more likely to have inadequate previous education than the immigrant classmates of richer natives. Richer parents may more easily move their child to a learning environment with either fewer immigrants or immigrants with better language skills and educational background, by using private schools (Betts and Fairlie 2003; see also Hoxby 1998) or by moving to a different school district (Cascio and Lewis 2012). Furthermore, the educational quality of a child’s school is likely to have a smaller impact on the children of high SES parents, as such parents can compensate in part for a school’s deficiencies by providing the child with instruction at home. At the same time, any positive effects of immigration on high-school graduation rates are likely to be larger for groups with graduation rates that leave substantial room for improvement. Thus, effects through both channels are more likely to affect low SES natives and, consequently, to affect minorities more than non-Hispanic whites. Furthermore, native minorities live in closer proximity to immigrants than native non-Hispanic whites, as I show below, increasing their likely responsiveness to immigration. Minority boys, who have particularly low high-school graduation rates (Orfield et al. 2004; National Center for Education Statistics 2008; Noguera 2008; Noguera, Hurtado and Fergus 2011), may be particularly sensitive to immigration.
I study the impact of immigration on natives’ completion of 12 years of schooling and on natives’ enrollment status at ages 16 and 17, comparing results across ethnicity, race, gender, and parental education. I use the decennial censuses of 1940–2000 and the pooled 2008–2010 American Community Surveys (ACS) to construct a state panel. For the analysis of the completion of 12 years schooling, I extend two closely related papers, Betts (1998) and Betts and Lofstrom (2000), in several ways. The most important extensions in practice are the distinction between immigrants of different educational attainment, the measurement of the immigrant inflows at the time natives were of school age, rather than later, and the use of a dependent variable consistent over time. The extension to the use of instrumental variables based on historical immigrant settlement patterns is important in principle but less important in practice.
My work complements that of McHenry (2015), who supplements census information on immigration with the National Education Longitudinal Study of 1988 for information on a native cohort. While McHenry does not distinguish the two channels of immigration’s impact and must rely on cross-section geographic variation in immigrant density, he is able to examine a wider range of native educational outcomes and use richer controls for the characteristics of natives and their schools. He finds that natives improve their performance in school and acquire more years of schooling in response to low-education adult immigration.
Some of the analysis in Smith (2012) also is closely related to my paper. Smith (2012) focuses on the effects of adult low-education immigration on young natives’ employment rates, finding a negative effect operating principally through the employment rate of native high school students. As part of establishing this mechanism, he presents a regression for the probability of natives being enrolled at ages 16–17. The estimates are imprecise, however—the coefficient is statistically insignificant for three of the four samples studied. I also go beyond Smith (2012) by examining the effect of child immigration and skilled adult immigration, and by assessing the net effect of immigrants of all ages and education levels.6
My paper is related to the structural analyses of two other papers in the literature, those of Eberhard (2012) and Llull (2014). These papers use simulations to calculate the extent to which (adult) natives adjust their education as a consequence of immigration, and how much this affects the overall adjustment of their labor market outcomes. My paper focuses exclusively on the adjustment in educational attainment, but has the advantage of isolating an elasticity of educational attainment with respect to immigration. Eberhard (2012) finds that, for native males 18–65, educational adjustments play an important role in the overall labor market impact of immigration. Llull (2014) also finds an important role in the overall impact of immigration, but, on aggregate, education does not seem to react much. This is the result of two offsetting forces: While individuals that are close to indifference between more and less skilled occupations tend to increase their education substantially, individuals who are less attached to the labor market reduce their education significantly.
In the main analysis, I measure native educational attainment at ages 21–27 and measure the shares of immigrants in the population when these natives were aged 11–17. Unlike Betts (1998) and Betts and Lofstrom (2000), who find a detrimental net effect of immigration on native high school attainment for each native racial and ethnic group, I find the net effect of immigration to be positive for natives generally, and especially for blacks: An increase of one percentage point in the share of immigrants in the population aged 11–64 (0.13 standard deviations) increases the probability natives complete 12 years of schooling by 0.3 percentage points and increases the probability for blacks by 0.4 percentage points. I estimate a detrimental net effect for native-born Hispanics of -0.2 percentage points that is statistically insignificant. All effects are rather small compared to the average native completion rate of 87.8 percent (81.0 percent for native blacks; 81.3 percent for native Hispanics) and given the average immigrant share of 8.9 percent (8.1 percent for blacks, 15.5 percent for Hispanics).
I support this analysis by examining how the enrollment rates of native 16–17-yearolds are affected by contemporaneous immigration, similarly to Smith (2012). I find that an increase of one percentage point in the share of immigrants in the population aged 6–64 increases the probability natives complete 12 years of schooling by 0.2 percentage points, effects concentrated among natives with poorly educated parents. The smaller magnitude compared to the analysis of the older native sample might reflect simply sampling error, or that effects for 18-year-old high school students are larger than for the 16–17-year-olds; it does not appear to reflect later acquisition of GEDs by natives. The increase in the enrollment rate comes from a reduced share of 16–17-year-olds who are employed but not enrolled, with no effect on the share idle.
The finding that natives who would have dropped out of high school upgrade their education in response to immigration adds to our understanding of why the wages of high school dropouts decline so little in the face of immigration.7 Peri and Sparber (2009) have previously documented that unskilled natives exploit their comparative advantage to avoid competition with immigrants, by shifting to more communication-intensive occupations. By distinguishing among immigrants by age and education, I find support for the labor market channel for education upgrading: A one percentage point increase in the share of immigrants with less than 12 years school in the population aged 18–64 (0.27 standard deviations) increases the eventual native completion rate by 0.8 percentage points, a somewhat smaller effect than found by McHenry (2015), with larger effects for nativeborn blacks.8 Effects of more educated adult immigrants are not precisely estimated, nor are effects for native-born Hispanics. The upgrading finding is echoed in the analysis of enrollment at ages 16–17, though for this sample the finding is not robust to instrumental variables; points estimates are similar to those of Smith (2012).9
Investigation of the schooling channel indicates that child immigrants have at most a small negative effect on the high school education of natives as a whole, an effect that appears to be the result of immigrant students’ diverting resources rather than having a direct effect in the classroom: In the enrollment analysis, the effect of immigrants aged 6–17 is much larger than the effect of immigrants aged 16–17 who would be direct peers of the natives. A one percentage point increase in the share of immigrants in the population aged 6–17 (0.31 standard deviations) reduces the enrollment rate of natives by 0.3 percentage points, with a more negative for children of less educated parents. A similarly sized effect is found in the analysis of 21–27-year-olds, though the coefficient is not statistically significant in instrumental variables.
The results support Singer’s (2008) call for increased resources for schools in areas with high immigration, especially where natives are disproportionately black or of low SES. The implementation of best practices regarding improving language skills of nonnative speakers, remedying educational deficiencies of immigrants, and integrating immigrants with native students also would be valuable (García, Kleifgen, and Falchi 2008).
II. Data and Descriptive Statistics
The principal data for regression analysis are the IPUMS microdata samples for the 1940–2000 decennial censuses and the pooled 2008–2010 American Community Surveys (which I refer to as the 2010 ACS data), from which I construct a panel of states.10 I supplement them with data from the Bureau of Economic Analysis on state personal income per capita. I choose the census and ACS data for the large sample sizes they afford. I check the sensitivity of the analysis to using metropolitan areas instead of states (the construction of the metropolitan area panel is described in the Appendix).
The simpler analysis involves studying the enrollment status of a sample of nativeborn 16–17-year-olds and the effect of contemporaneous immigration. I do not include 18-year-olds in the sample because the focus is on high school enrollment, and some 18-year-olds have graduated high school. In addition to simplicity, analysis of this sample has the advantage that parental education and immigrant status may be observed for most members of the sample. The disadvantage is that samples become small when divided by race or ethnicity or parental education.
I therefore prefer to stress analysis of the completed education at older ages of a larger number of birth cohorts. In order to have a consistent outcome variable over all years, I define the outcome of interest as the completion of 12 years of schooling, with or without the obtention of a high school diploma, as the two may be distinguished only from 1990 onward.11 I focus on the native-born who were aged 11–17 in the previous census: This implies current ages of 21–27 (20–26 in 2009, 19–25 in 2008). Most covariates are lagged one census, to correspond to the time when natives were aged 11–17. I construct samples of all races and ethnicities pooled, blacks, Hispanics, and non-Hispanic whites. Being black and Hispanic are not mutually exclusive, so there is some overlap in the two minority samples. Immigrants are defined as those born abroad, including those born in U.S. territories. I drop the states of Alaska and Hawaii, as their absence from the 1940 and 1950 censuses complicates the use of the instruments and covariates measured in 1940.
Figure 1 depicts the shares of native-born 21–27-year-olds who have completed at least 12 years of schooling, by race and ethnicity, for 1940–2010.12 The shares increase strongly over the early decades, then level off around 1990. Minorities begin the period with much lower education, and converge toward non-Hispanic white rates from 1960 until 1980 or 1990. At the start of the period, both blacks and Hispanics (concentrated in different regions) were educated in segregated, inferior schools. As a result of court decisions in the 1940s and 1950s, the Civil Rights Act of 1964 and the Coleman Report (Coleman et al. 1966), educational quality, integration, and attainment increased for minorities.13 Evans, Garthwaite, and Moore (2012) argue persuasively that convergence ended due to the incentives for black males to drop out of high school to earn large sums and risk death selling crack cocaine.
Share of Natives with at Least 12 Years of Schooling, by Race and Ethnicity
Source: U.S. Census 1940–2000, American Community Survey 2008–2010
Note: The share of natives aged 21–27 who have completed at least 12 years of schooling
Heckman and LaFontaine (2010) have cautioned that both the increase in high school completion observed in the census and the convergence between whites and minorities mask an increasing share of individuals receiving a General Equivalency Degree (GED). For the purposes of this paper, it is desirable to know whether any response in native education is coming through time in regular high school, or the propensity to obtain a GED. The measurement difficulty is that, unlike in the ACS, is it impossible to identify GED holders in the census microdata. In early censuses, when GEDs were uncommon, no specific instructions concerning GEDs were given to the respondents. In 1980, GED recipients were instructed to respond they had completed 12 years of high school, while in 1990 and 2000 they were instructed to respond that they had a high school diploma. I therefore correct the 12-year completion rates using annual published tables on GEDs awarded by state and age, and using the Heckman and LaFontaine appendix for methodological guidance. However, the GED recipients I am subtracting, while not holders of regular high school diplomas, do have the possibility of attending college, so the adjusted measure understates final educational attainment. The adjustment for GEDs becomes increasingly crude as the data get older, as explained in the Appendix, and I do not attempt to adjust 1970 and earlier years.14 Appendix Table 1 shows the 12-year completion rates measured in different ways.
Figure 2 shows the evolution of the share of immigrants over the period, by age group. The share of immigrants in the population of working age, 18–64, traces out a U shape, falling from 12.1 percent in 1940 to 6.1 percent in 1970, before rising to 18.4 percent in 2010 (top line). The share of immigrants in the school-age population, 11–17, traces a different path, rising almost monotonically from 1.6 percent in 1940 to a still modest 7.2 percent in 2010 (bottom line).
Immigrant Share in Various Age Groups
Source: U.S. Census 1940–2000, American Community Survey 2008–2010
Note: Immigrants as a share of each age group
Figure 3 shows the time paths of three additional key covariates: the shares of the population aged 18–64 composed of immigrants with less than 12 years of education, exactly 12 years of education, and more than 12 years of education. The share of the lowest education immigrants falls from a high of 10.1 percent in 1940 to a low of 2.8 percent in 1980, before rising again to 4.8 percent in 2010. The shares of the immigrants from the two more educated groups rise monotonically from 0.7–1.1 percent in 1940 to 5.4 percent in 2010 for those with exactly 12 years of education and 8.1 percent for those with more than 12 years education. Appendix Tables 2–4 give further means of variables measured at the individual level, while Appendix Tables 5 and 6 give means of variables measured at the state level.
Immigrant Education Groups as Share of the Population, Ages 18–64
Source: U.S. Census 1940–2000, American Community Survey 2008–2010
Note: Immigrants 18–64 with various education levels as share of the total population aged 18–64
The Census Bureau produces tabulations of their census data at the school district level. The 1990 tabulations, known as the School District Database (SDDB), may be used to assess which native children are most likely to interact with immigrants in school.15 The first four Columns of Table 1 are based on samples of children of kindergarten, primary, or secondary school age, from which I have discarded the small number of school districts with no high school. Panel A, Column 1 shows that the share of immigrants among such children is 4.2 percent, but that a native-born child is on average in a school district with only 3.8 percent immigrants, with corresponding numbers of 2.5 percent for white non-Hispanic natives, 5.2 percent for black natives, 10.7 percent for Hispanic natives, and 14.3 percent for immigrants.
Interaction of Natives by Ethnicity with Immigrants, School District Level 1990
However, this does not necessarily show that Hispanic natives interact more with immigrants than non-Hispanic white natives within a given state (the relevant question given that my subsequent analysis will rely on within-state variation). This pattern could emerge if Hispanic immigrants and Hispanic natives were concentrated in one region of the country and white natives in another. I therefore compute the Panel A numbers for each state, calculate differences between groups for each state, and report the population-weighted average differences across states in Panel B. Column 1 shows that while native blacks and native Hispanics are both more likely than native whites to be in school districts with many immigrants, black and Hispanic shares are more similar to each other than Panel A indicates. On average (within state), a native black child is in a school district with 2.7 percentage points more immigrants than a native white child, while a native Hispanic child is in a school district with 3.6 percentage points more immigrants. Column 2, Panel B shows that the black–Hispanic difference is larger when proximity to Hispanic immigrants is measured, but Columns 3 and 4 show there is no sizeable difference in the black–Hispanic exposure to white non-Hispanic immigrants or Asian immigrants. Columns 5 and 6 are based on data on the parents of children of school age. The share of immigrants among parents is higher than among children, but generally similar patterns prevail.
These statistics suggest that any effect of child immigration and probably also adult immigration to a given state will be larger for native blacks and especially Hispanics than for non-Hispanic whites, as native minorities interact more with immigrants in their schools and neighborhoods, and probably labor markets. The implication of the high degree of contact between Hispanic natives and Hispanic immigrants is unclear: Immigrants may have less impact on natives similar to themselves, or they could have more impact—for example, by encouraging native-born Hispanics to speak more Spanish, possibly at the expense of English, or by straining resources directed at those native-born Hispanics who have limited English proficiency.
III. Estimation
Rather than analyze native schooling determinants at the individual level, I reduce the sample size by calculating state schooling variables adjusted for individual characteristics, and conduct the main analysis on a panel of states. Appropriate weighting means the coefficients are the same as if all regressions had been run at the individual level with state-level variables included. Specifically, for natives aged 21–27 (20–26 in 2009 and 19–25 in 2008) at time t and born in state s, I first run the following linear probability regression for each of the samples, for 1940–2010.

where i indexes individuals, E represents years of completed schooling, F is a gender dummy, Aa are dummy variables for age, δs are state dummies and nt are year dummies. I match individuals to their birth state to avoid endogenous moves of young adults that would plague the use of state of current residence. In some specifications, I also control for race (Asian, black, race missing) and Hispanic ethnicity (Mexican, Puerto Rican, Cuban, other, Hispanic ethnicity missing).
I weight this regression using weights based on the census weights. The census weights sum to the U.S. population of the census year, while I wish the standard errors to reflect the variation in sample sizes from year to year. I adjust the census weights so that the ratios of their sums for each year reflect the ratio of the census sample sizes, resulting in considerably more weight being put on recent years. The average year in the weighted data is 1989 for non-Hispanic whites, 1991 for blacks, and 1995 for Hispanics.16
In a second step, I use the coefficients as the dependent variable in a state panel analysis:

I weight the regressions with the inverse of the squared standard errors on the in the first step, and cluster the standard errors by state.
represents the share of the population aged 11–17 that is foreign-born in the previous census, when the native-born cohort was itself aged 11–17, and is designed to capture natives’ exposure to immigrant classmates. Ideally, an additional covariate would capture the presence of immigrants when nativeswere of elementary school age, but the ten-year spacing of the census precludes this. The null hypothesis to be tested is that β1 is negative because immigrant children reduce current school quality. However, β1 also may reflect the behavior of sophisticated native students who factor the presence of immigrant schoolmates into their predicted return to high school. Measurement error, including errors in matching individuals to the state in which they went to school, may bias the coefficient toward zero.
represents the share of the population aged 18–64 when natives were aged 11–17 that was immigrants with less than 12 years of schooling, and
and
are defined similarly. The null hypothesis to be tested is that β2 is positive, because the presence of immigrants with less than 12 years education increases the return to completing 12 or more years of education, and because high school students use the return among current adults as a proxy for the return they themselves will face in the labor market. The necessity of using multiyear birth cohorts is likely to bias β2 toward zero because the younger members of the age range 11–17 are likely to base their years of schooling decision on thewage structure, and hence immigration rates, of later years. The signs of β3 and β4 are ambiguous, as the inflows of more educated immigrants have opposite effects on the return to exactly 12 years of education versus more than 12 years of education (relative to less than 12 years).17
It proves useful to further distinguish among immigrants in Equation 2. Immigrant students could have either positive or negative spillovers on their native classmates, depending on the quantity and quality of their prior education, their English skills, their industriousness, and the extent to which their parents contribute to their education. Parental education is likely to be a proxy for some of these characteristics, and because most children aged 11–17 live with their parents, we can observe their parents’ education in the census data. It is therefore possible to split the share of the population 11–17 that is immigrant into immigrants whose parent or parents in the household have less than 12 years schooling, immigrants with at least one parent with 12 years or more, and immigrants with neither parent living in the household. The expectation is that children of more educated parents will make better peers and require fewer resources than children of less educated parents. The difficulty with regressions distinguishing child immigrants according to parental characteristics is that the number of endogenous variables becomes too large for the use of 2SLS.18
Whilemost immigrants aged 11–17 arrive in the United States with their parents, most immigrants 18–64 do not arrive with children aged 11–17. The correlation between I11–17 and IE<12 is 0.76 (weighted with the weights for all natives), and between the tenyear differences of these covariates is 0.41. It should therefore be possible to identify their effects separately, at least if least squares is an adequate estimation method.
This regression suffers from endogeneity problems, however. Native high school educational attainment and high shares of low-education immigrants in a state may be spuriously negatively correlated. What makes the state economically attractive for immigrants, such as the availability of low-skill jobs, may by the same token mean that natives have a low incentive to complete 12 years of schooling. For example, a downturn in a state’s low-skill industries could deter unskilled immigrants from moving to the state and encourage its natives to graduate from high school, leading β2 to be biased down (the same direction as the measurement error bias, if β2 > 0). Similar reasoning suggests that β3 and β4 could be biased up by endogeneity. β1 could be biased up if immigrants with children choose states with high educational attainment (the same direction as the measurement error bias, if β1 < 0), but there may be other biases due to endogeneity in their parents’ choice of state if these have not been controlled for properly.
These considerations lead me to implement an instrumental variables strategy using ten-year differences of Equation 2:

I estimate this using weights 1/(1/ws,t+1/ws,t-10), where w is the weight used in Equation 2. I devise instruments for the differenced immigration covariates, based on the flows of immigrants to a state that would have been expected given the 1940 geographic distribution of immigrants from different regions and the subsequent national inflows from those regions.19 To illustrate, if immigrants from Europe prefer the northeastern United States because it is closer to home and because other Europeans are already there because of geography, and Mexican immigrants prefer the southern border states for analogous reasons, the large national increase since 1940 in the share of immigrants that are Mexican will be associated with an increase in immigration to the southern border states relative to the Northeast. The predicted flows captured in the instrumental variable will therefore be strongly, though not perfectly, correlated with actual immigrant flows to states. Furthermore, since the national increase in Mexican immigration appears to be the result of increasingly large birth cohorts entering the Mexican labor market,20 and the national decrease in European immigration is due to Europe’s having become richer, the decrease in immigration to the Northeast relative to the border states is unrelated to nonimmigration factors affecting native education choices.
I define an instrument for each of the education-specific immigration variables as follows. For a state s, the predicted change in the number of immigrants of education level E (aged 18–64), caused by changing origin regions k, can be written as

where μsk is state s’s share in 1940 of the national total of immigrants who originate from region k, and is the national change in the number of immigrants with education E (aged 18–64) from that region. I use 18 source regions or countries, listed in Appendix Table 7. Because the variables to be instrumented are percentage point changes, I convert
to percentage points by dividing by the population level (aged 18–64) at the start of the period to which Δ refers, to define the final instrument as:

I deliberately base the μsk on immigrants of all educations (and ages) to emphasize the role of geography and taste and minimize the role of economic factors that might disproportionately attract workers of a specific education level. The instrument will be invalid if nonimmigration shocks to high school completion are correlated with 1940 immigrant densities; for example, if improvements to the California and Texas school systems caused a national-level increase in Mexican immigration.21 By defining an instrument for each education level, I assume that improvements to the California and Texas school systems did not cause a national-level increase in Mexican immigration of any education group.
I can further reduce the likelihood that the instrument is correlated with the error term by following Wozniak and Murray (2012) in removing the state’s interdecadal flow of a particular immigrant type from the national flow. This corresponds to rewriting Equation 4 as

The instrument based on this, which I refer to as the adapted instrument, also will be more weakly correlated with the endogenous variable, however, and is not my preferred instrument.
It is easy to construct instruments for different immigrant age groups, in particular for ΔI11–17, by replacing the education-specific variables in Equations 4–6 with age-specific variables, and I do so. However, the intuition of the instruments extends less easily to subdivisions by age group, as immigrant numbers in an age group are strongly influenced by aging as well as immigration, and changes in the inflows of the 11–17 age group will be not be independent of those of adult immigrants.
I choose to use a common first stage for all four race/ethnicity samples, weighting each first stage with the denominator of its dependent variable (the population 11–17 or the population 18–64) in order to improve efficiency. This approach also means the first stage always includes all states and years: Some early state–year cells have no nativeborn blacks or Hispanics aged 21–27.
Estimation for enrollment of 16–17-year-olds is similar to the analysis of 21–27-year-olds, except that I can include more controls in the individual–level regression, and state explanatory variables are contemporaneous rather than lagged one census. The individual–level regression estimated is

In addition to containing race and ethnicity variables, X includes dummies for residence in a metropolitan area, whether a parent is present in the household, having immigrant parents, the greater of the two parents’ education, and the interaction of second generation and parental education (and dummies indicating missing values for any of these covariates). The state-level analysis is then

The unemployment rate used in X is for 16–17-year-olds, and the youth immigration variable is the share of all school-age (6–17) children or the share of 16–17- year-olds who are immigrants (the instrumental variable is adjusted appropriately), but otherwise the controls are the same as for the sample aged 21–27 (with contemporaneous rather than lagged immigrant and X controls). The use of a narrower cohort of natives and contemporaneous covariates allows the age ranges of the immigrants to be defined in a more meaningful way, and allows a test of whether it is overall numbers of student-aged immigrants who influence native schooling decisions, which would point to the importance of school resource constraints, or the number of immigrant classmates, which would point to classroom-level effects. I complete the analysis of this sample by examining outcomes other than enrollment: the probability of living with one or both parents, the probability of working, the probability of working and not being enrolled, and the probability of neither working nor being enrolled (idleness).
Although the natural level at which to examine school quality is the school, there are some reasons to use more aggregated data beyond the limited availability of school-level data. If some natives move out of their school and neighborhood when immigrants move in, analysis at the school or school-district level will not attribute any change in schooling of the native movers to the arrival of the immigrants. If public school data are used, even natives who move to private schools in the same school district will cause the same problem. Also, it is difficult to find an instrument at the school level that accounts for immigrants’ potentially endogenous choice of location (and school). I base the main analysis on states, but also repeat the estimates using metropolitan areas (cities). The advantages of using cities rather than states are that the analysis is slightly closer to the ideal school or labor-market level analysis, while still permitting the construction of instruments, and that there may be enough observations to identify the effects for more recent years. The disadvantages are that the city of birth is not known, constraining the analysis to be based on city of current residence, and that rural areas are excluded.
IV. Results
I examine the impact of immigration on the probability of natives completing 12 years of schooling, by race and ethnicity and by gender, first assessing the net impact of immigration, then decomposing the impact into school quality versus labor market channels. I perform similar analysis for the impact of immigration on enrollment rates of native 16–17-year-olds, and perform other robustness checks.
A. The Effect of Immigrants Ages 11–64 on Completed Schooling
In Table 2, I investigate the impact of the immigrant share of the population aged 11–64, initially using as the dependent variable the 12-year completion rate adjusted for age and sex only. With only state and year effects in Column 1, or with unemployment rates and native cohort size (see Card and Lemieux 2001) as additional controls in Column 2, immigration’s coefficient is small and statistically insignificant. Neither the youth unemployment rate nor the prime-age unemployment rate has a statistically significant coefficient, possibly because many of the respondents were some years from graduation when the unemployment rate was measured.22 However, once controls allowing for convergence amongst states, and linear trends for eight BEA regions are included in Column 3, immigration’s coefficient rises to a statistically significant 0.20. The 1940 share of non-Hispanic whites aged 21–27 who had less than 12 years education is statistically significantly positive, capturing convergence. The trend in the 1940 share of workers in agriculture is included to capture convergence for minorities, and its coefficient is insignificant for the full sample of natives.
Effects of Immigrants in Population 11–64 on Native Probability of Completing 12 Years Education
Changing the dependent variable to one also adjusted at the individual level for race and ethnicity in Column 4 raises the immigration coefficient from 0.20 to 0.29 (though this difference is not statistically significant). This indicates that increases in immigration are positively correlated with increases in native-born minorities, not surprisingly in the case of Hispanics, and that once this is controlled for and immigration no longer picks up the under-performance of native minorities, immigration appears a more positive force. In Column 5, I take into account that one would expect richer states to be able to afford better educational systems. However, states with better educational systems should become richer, so the coefficient on a control for state income would be biased up. The results show that the correlation between log state personal income per capita and completion of 12 years of schooling is indeed positive and statistically significant, and that the coefficient on the immigrant variable, now a lower bound on the true coefficient, is reduced somewhat from 0.29 to 0.22.
I base the differenced specifications of Columns 6–8 on the specification of Column 4. Differencing does not change the coefficients greatly (Column 6), while the preferred 2SLS coefficient in Column 7 is the largest of all specifications, at a statistically significant 0.34. The instrument is strong in the first stage, as evidenced by its associated F-statistic of 25. A coefficient of 0.34 implies that an increase of one percentage point in the share of immigrants in the population 11–64 increases the native probability of eventually completing 12 years of education by 0.34 percentage points. This is a small effect considering that the (weighted) mean completion rate is 87.8 percent, and the share of immigrants in the population 8.9 percent (the implied elasticity is 0.035).
The results using the adapted instrument, in Column 8, are very similar, with a point estimate on the share of immigrants of 0.31. As expected, the standard error is larger than in Column 7, with a smaller associated F-statistic of 21. For consistency with some earlier authors, I present in Column 9 the results of using the Column 7 instrument for the level of immigration (fixed effects 2SLS), rather than the difference. One would expect the instrument to be weaker in this scenario (and to be valid only under stronger conditions), and indeed the first-stage F statistic is only 4.0. The point estimate is 0.00 with a standard error twice as large as in the preferred Column 7.
In Table 3, I analyze natives by race and ethnicity as well as by gender, reporting only the coefficient on the immigrant covariate. I report the same specifications as Table 2, omitting only the column controlling for personal income per capita. I retain the column using the fixed 2SLS specification despite the weakness of the first stage, but I deemphasize these results. For reference, I reproduce the coefficients from the first row of Table 2, for all natives, in the first row (A) of Table 3. The coefficients for non-Hispanic whites, in the second row (B), are always smaller than those for all natives; the preferred 2SLS coefficient in Column 6 is 0.21, significant only at the 10 percent level. The coefficient is even smaller using the adapted instrument in Column 7: 0.13 and statistically insignificant. For blacks in the third row (C), once state-specific trends and convergence are controlled for in Column 3, there is a robust positive coefficient. The 2SLS coefficients are 0.38 in Column 6 and 0.43 in Column 7, small compared to the mean black completion rate of 81.0 percent and a black–white completion gap of 8.5 percentage points, but statistically significant. For Hispanics, in the fourth row (D), an effect of 0.31–0.53 is robust in the least squares Columns 3–5, but it disappears with 2SLS: The coefficients are -0.21 in Column 6 and -0.63 in Column 7, both statistically insignificant.23
Effects of Immigrants in Population 11–64 on Native Probability of Completing 12 Years Education, by Race and Ethnicity
I conclude that the net effect of immigration on native completion of 12 years of schooling is positive and small for natives generally, blacks, and non-Hispanic whites and is possibly negative for Hispanics, though also small, as moderately sized negative effects can be ruled out. Rows E and F show the results to be similar for men and women.
B. Decomposing the Impact of Immigration into School Quality and Labor Market Channels
I now turn to decomposing the impact of immigration into school quality and labor market channels. I return in Table 4 to the sample of all natives, presenting the same specifications as in Table 3, except with immigrants split into four categories. The first row shows that the least squares effect on natives of immigrants aged 11–17, likely to have been natives’ classmates, is negative: The coefficient is in the range -0.29 to -0.45 in Columns 3–5. At the same time, 2SLS causes the point estimate to become less negative in the preferred specifications (-0.18 in Column 6 and -0.11 in Column 7), confounding my expectation that least squares would be biased toward zero. The 2SLS coefficients are not statistically significant, however, since the standard error rises considerably to 0.17 in Column 6 and 0.29 in Column 7. Whereas the instruments are apparently not sufficiently powerful to allow identification of small effects, it is possible to rule out moderately sized negative effects with the preferred instrument of Column 6. As the system is exactly identified, 2SLS itself introduces no bias.
Effects of Immigrants by Age and Education on Native Probability of Completing 12 Years Education
The first-stage information for the 2SLS regressions of Column 6 is presented in Table 5, Column 2 (in Column 1, I present the first stage used for immigrants 11–64 in Column 7 of Table 2 and Column 6 of Table 3). Although the predicted share of the population 11–17 has a statistically significant coefficient, it is not much more significant than those of the other excluded instruments, suggesting that I have not managed successfully to instrument the share of immigrants in the population 11–17. The F-statistic for the joint significance of the excluded instruments is only 8, while the more appropriate Angrist and Pischke (2008) F-statistic (an F-statistic adapted for multiple endogenous variables) is somewhat higher at 15. Appendix Table 8 Column 2 shows a similar issue for the adapted instruments, while Appendix Table 9 Column 2 shows that the key instrument is only statistically significant at the 10 percent level for fixed effects 2SLS.
First Stage of Two-Stage Least Squares (Preferred Instruments)
The second row of Table 4 shows that the effect on natives’ acquiring 12 years of schooling of immigrants aged 18–64 with less than 12 years of schooling is positive and statistically significant in every specification (except fixed effects 2SLS), with coefficients of 0.81 and 0.82 in the 2SLS in Columns 6 and 7. This is consistent with the hypothesis that the presence of unskilled immigrants in the labor market alters the wage structure in such a way as to give natives an incentive to complete 12 years of schooling. A comparison of Column 5 with Columns 6 and 7 shows that using 2SLS does not increase the coefficient greatly, despite the expectation it would be biased down in least squares. Column 3 of Table 5 shows that the preferred predicted share of immigrants with less than 12 years of schooling in the population 18–64 is a strong predictor in the first stage, much stronger than the other excluded instruments, and the Angrist–Pischke F-statistic is very high at 103. (By contrast, Column 3 of Appendix Table 9 shows none of the instruments is statistically significant in the first stage of the fixed effects 2SLS, and the joint F-statistic is only 4.2.)
The third row of Table 4 shows that the impact of adult immigrants with exactly 12 years of education is imprecisely estimated. In the fourth row, the impact of adult immigrants with more than 12 years of education appears positive and significant until 2SLS is employed, when the coefficient falls to essentially zero (Column 6) or slightly negative (Column 7). The instruments associated with these covariates are fairly strong in their respective first stages (Table 5 Columns 4 and 5) (see also Appendix Table 8; Appendix Table 9 shows the fixed effects 2SLS instruments are weak, albeit less so for immigrants with exactly 12 years of education.)
I have repeated all the specifications of Tables 3 and 4 with completion of 16 years of education as the outcome and find the coefficients on the immigrant covariates to be almost uniformly statistically insignificant (these coefficients are not reported). As the focus of the paper is on high school, I do not attempt to reconcile these results with the more complex analysis of Jackson (2016).
I next study the effect of immigration by race and ethnicity of natives. I continue to report fixed effects 2SLS in the final column, but no coefficient in this column is ever statistically significant, and I deemphasize these results. For native non-Hispanic whites in Table 6, the least squares results are qualitatively similar to those for all natives, but the absolute values of the coefficients are smaller. For this sample, however, 2SLS raises the point estimate on child immigrants to zero or a statistically insignificant positive (0.03 in Column 5 and 0.11 in Column 6), suggesting there is no negative effect on native non-Hispanic whites through the schooling channel (or that it is cancelled out by natives’ anticipation of their immigrant classmates’ future labor market effect). Nevertheless, the WLSand 2SLS coefficients are not statistically significantly different. The coefficient on the adult immigrants with less than 12 years of education is a statistically significant 0.41 under 2SLS (Column 5; 0.39 in Column 6), half the size for the whole sample in Table 4.
Effects of Immigrants by Age and Education on Native Non-Hispanic Whites’ Probability of Completing 12 Years Education
In Table 7, I turn to native-born blacks, for whom the negative effect of immigrants 11–17 is larger in absolute value than for non-Hispanic whites. As for the previous samples, 2SLS renders this coefficient statistically insignificant, although in this sample the point estimates are almost unchanged at -0.34 in Column 7 and -0.35 in Column 8. The positive effect of adult immigrants with less than 12 years of education is robust and larger than for non-Hispanic whites, with a moderately sized, statistically significant 2SLS coefficient of 1.05 (Column 6; 1.13 in Column 7). The effects of adult immigrants with exactly 12 years education and with more than 12 years are imprecisely estimated. Prompted by the Evans, Garthwaite, and Moore (2012) finding of the importance of the crack epidemic for black schooling, I also have estimated regressions controlling for the murder rate. The unreported coefficient on murder is statistically insignificant, for the whole sample and for men and women separately: It is probably necessary to have yearly data to identify the effect successfully.24
Effects of Immigrants by Age and Education on Native Blacks’ Probability of Completing 12 Years Education
From Tables 4–7, I conclude that the labor market channel through which immigration might operate works as expected, with a larger effect for native blacks than non- Hispanics whites, also as expected. There is evidence for the schooling channel in least squares estimation, but it is imprecisely estimated under 2SLS, and while moderately sized effects can be ruled out for natives generally and for non-Hispanic whites, this is not the case for blacks. The results for males and females are similar even when estimated separately by race and ethnicity; I report the results for all natives in Appendix Table 10.25
Finally, I examine native-born Hispanics in Table 8. Whereas the sign of the coefficient on immigrants aged 11–17 is always negative, it is imprecisely measured in many specifications (first row). The evidence of a positive effect of adult immigrants with less than 12 years of education is even less robust, since in differenced specifications the sign is negative (Columns 5–7). Another difference from results for other native groups is that immigrant adults with more than 12 years of education have relatively large positive effects, even under 2SLS. The results for Hispanics therefore appear to provide only weak support for the hypotheses being tested. Regressions in Hunt (2012) indicated that the Hispanic regressions were misspecified due to a failure to distinguish between child immigrants on the basis of their parents’ education: Native Hispanics are hindered by children of immigrants with less than 12 years education and spurred on by children of immigrants with more education as well as by adult immigrants with less than 12 years education. However, the results are not robust to examining enrollments among 16–17-year-olds. Nor are the different Hispanic results explained by heterogeneity among types of Hispanic (results not presented).
Effects of Immigrants by Age and Education on Native Hispanics’ Probability of Completing 12 Years Education
Before performing robustness checks on these results, I extend the specification to allow for more age groups among adult immigrants with less than 12 years education. If prospective native dropouts are considering only early-career earnings, their decision might bemost influenced by the youngest immigrants with low education, if these immigrants are their closest substitutes. On the other hand, close substitutability could extend into older immigrant age ranges given that premigration experience is less valuable than U.S. experience. To maintain sufficiently large sample sizes, I simply split the 18–64 age group approximately in half: 18–39 and 40–64. Two-stage least squares are no longer feasible, and I present single stage least squares in Table 9.
Effects of Immigrants by Education and More Detailed Age Group on Native Probability of Completing 12 Years Education
Columns 1 and 2, for all natives, show equally sized effects for the two immigrant dropout age groups. This is the result of the expected larger effect for the 18–39 age group for native-born non-Hispanic Whites (Columns 3 and 4), an unexpected smaller effect of 18–39 for native-born Blacks (Columns 5 and 6), and oppositely signed effects for native-born Hispanics (Columns 7 and 8). The differing results by ethnic group mirror the heterogeneous results of Llull (2014), who found that some workers respond to immigration by increasing their years of education, and some by reducing them.
C. Robustness Checks
In Table 10, I provide some robustness checks for the sample of all native-born, with the first three columns reproducing the preferred results from Table 4 (fixed effects, ten-year differences, and instrumental variables). The specifications of Columns 4–6 allow for state-specific rather than region-specific trends. The net effects of immigration become more positive (first panel), though far from statistically significantly so. The coefficients from the specifications distinguishing the labor market and schooling channels (second panel) show the same pattern as the baseline results, with some statistically insignificant changes in coefficient magnitudes but no change in which coefficients are statistically significant.
Sensitivity of Results to Trends and Sample Period—All Native-Born
In Columns 7–9 of Table 10, I repeat the baseline specifications using data only from 1970 or later, which means that the dependent variable is based on 1980–2010 data. The least squares coefficients of most interest are smaller in absolute value than the baseline coefficients, but this is not the case for the 2SLS coefficients, which are larger in absolute value in some cases. The unreported results for native-born blacks indicate smaller coefficients in absolute value than the baseline results in both least squares and 2SLS, making the coefficients similar to those for the full sample of native-born. (The unreported results for native-born Hispanics are qualitatively unchanged from the baseline results.) There is thus a hint that it was only in the more distant past that the impacts of immigration on the native-born were stronger for blacks, but the much larger standard errors when the sample period is restricted preclude certainty in this regard.
I can test the sensitivity of the results to classifying GED holders as having less than 12 years of education. There is no apparent way to do this for the 12-year completion rate adjusted for sex and age (and race and ethnicity), so I use the unadjusted 12-year completion rate as the basis for the state panel analysis. The analysis in Appendix Table 11 shows the results are robust to this, and schooling adjustment is not driven by changes in the propensity to obtain a GED. The analysis of school enrollment below also may be viewed as a robustness test, assuming those studying for a GED do not respond that they are enrolled (or that they do not do a GED immediately).
I also have conducted further robustness checks on regressions with the original dependent variable. The student–teacher ratio for all grades in public schools always has a statistically insignificant coefficient (the sources are the Digest of Education Statistics and the Biennial Survey of Education, various years). Matching state characteristics to natives’ state of current residence, rather than state of birth, does not change the qualitative picture: For all races and ethnicities together, coefficients are smaller in absolute value, while for minorities there is no clear pattern to the quantitative differences. These results are not reported.
Finally, I reestimate the regressions using 130 metropolitan areas (cities) instead of 49 states, reporting results for each race and ethnicity sample in Table 11. The upper panel shows the effect of overall immigration in the 11–64 age group. In Column 1, the fixed effects specification shows a very small positive and statistically significant effect of 0.09 for all natives. 2SLS increases the coefficient substantially to a statistically significant 0.26 in Column 2, similar to the 0.34 found for the states sample in Table 2 Column 7 and Table 3 Column 6. The F-statistic for the excluded instrument in the first stage is 14. However, the 2SLS coefficients for the separate race and ethnic groups are statistically insignificant (Columns 4, 6, and 8).
Sensitivity of Results to Using Metropolitan Areas and Restricting the Sample to 1980–2010
In the lower panel, where types of immigrant are distinguished, the odd columns show that fixed effects estimation yields small, insignificant coefficients whose point estimates do not correspond to the hypotheses of the paper. On the other hand, the even columns, containing 2SLS coefficients, indicate point estimates larger in absolute value than in the odd columns, and similar to those for the states sample. For all natives in Column 2, the coefficient on adult immigrants with less than 12 years education is a statistically significant 0.70, compared to a corresponding coefficient of 0.81 for the states sample (Table 4 Column 6), and the point estimates on child immigration are identical for cities and states (-0.18). The coefficients for the separate race and ethnic groups are statistically insignificant, however, and as the tables notes indicate, the instruments are weak in the first stage for the 2SLS regressions of the lower panel, leading to generally high standard errors in the second stage. It is noteworthy that when the native Hispanics regression of Column 7 (lower panel) is run with state data confined to 1980– 2010, the point estimates of the coefficients are almost unchanged compared to the regression using all years of state data.
It appears that analysis at the level of the city introduces more endogeneity to be repaired by 2SLS, and the 2SLS results are similar to those at the state level using all years. However, generally standard errors are large due to weak first stages when types of immigrant are distinguished.
D. The Effect of Immigrants on Native Enrollment
In Table 12, I begin the analysis of the enrollment probability of 16–17-year-old natives. The upper panel examines the net effect of all immigrants of school and working age (6– 64). With no other covariates (other than state and year dummies), the coefficient on the immigrant variable is a statistically insignificant 0.10 in Column 1, while adding the state variables in Column 2 reduces both the coefficient and the standard error. Adjusting the dependent variable for a large number of individual characteristics in Column 3 raises the coefficient to 0.11, rendering it statistically significant. Differencing in Column 5 cuts the coefficient, while 2SLS raises it again, to 0.17, and statistical significance in the case of the adjusted instruments in Column 7. This makes the overall impact slightly lower than estimated with the sample of 21–27-year-olds (0.3 in Table 4), which could reflect measurement error or the omission of the effect for those students still in high school when they turn 18.
Effects of Immigrants by Age and Education on Native Enrollment—All Natives
The lower panel seeks the separate effects of the school and labor market channel. In Columns 1–3, the coefficient on child immigrants age 6–17 is statistically significant and between -0.27 and -0.36, less negative than the effects for 21–27-year-olds. The effect of adult immigrants with less than 12 years education is positive and significant and ranges from 0.44–0.58, smaller than the effects for 21–27-year-olds and not very different from the magnitude found by Smith (2012).26 In Column 4, I use young immigrants 16–17, instead of 6–17, and show that the coefficient is smaller (as it is in whichever specification I make the substitution). This suggests that the negative effect of child immigrants operates through a diversion or dilution of resources in a school district, rather than through classroom or neighborhood interactions that would be observed primarily via the coefficient on 16–17-year-olds.
As was the case in the upper panel, differencing reduces absolute value of the coefficients in the lower panel (Column 5): This is consistently the case in regressions with the sample of 16–17-year-old natives. The negative effect of immigrants age 6–17 is robust to instrumenting in Columns 6 and 7, with a coefficient of -0.15 to -0.27, while the positive effect of adults with less than 12 years of schooling is an insignificant 0.20 in these two columns. Generally, the results from the sample of 21–27-year-olds are confirmed by this analysis.
With the sample of 16–17-year-olds, it is possible to study how effects vary by respondent English proficiency (for the years since 1970) and parental characteristics. One might hypothesize that natives whose English is imperfect, or whose parents are immigrants, might be more affected by immigration. The results of unreported regressions using interactions do not support this. This is not surprising, given that the main effect on enrollment of having two immigrant parents in the (unreported) individual-level regression is positive, not negative, and even the signs on the English proficiency dummies (if included) do not point clearly to worse outcomes for natives with worse English. I instead focus on whether immigrants have greater effects on natives whose parents are less educated because greater parental education does lead to higher enrollment rates.
Table 13 presents the results of regressions with the native sample split by parental education. The number of observations is reduced because in 1950 only one person per household was asked about education. The upper panel shows that the positive effect on enrollment is driven by natives with no parent with 12 years or more of education (Column 1); this effect is significant in 2SLS at the 10 percent level in Column 5. Columns 1 and 5 of the lower panel show that this effect on natives with poorly educated parents does not come through one of the hypothesized channels, but is instead driven by the presence of adult immigrants with more than 12 years of education. The negative effect of young immigrants ages 6–17 is stronger for natives whose parents have less education (Columns 2 and 3), but standard errors are large, and the results are not robust to differencing or 2SLS. The positive effect of adult immigrants with less than 12 years education operates through natives who are not living with their parents (and whose parental education is therefore unknown), according to the least squares regression of Column 4. Although this effect is also not robust to differencing or 2SLS (Column 6), it hints that immigration of adults may change the composition of the group of natives aged 16–17 who do not live with their parents.
Effects of Immigrants by Age and Education on Native Enrollment, by Parental Education
To assess this, I run regressions for the probability of a native not living with his or her parents. The covariates are the same, except that the individual adjustments for parental characteristics cannot be made, and I also do not control for whether the native lives in a metropolitan area, as this could be jointly determined. Table 14 Columns 1 and 2 (lower panel) suggest that this is indeed the case: A one percentage point increase in adult immigrants with less than 12 years education reduces the probability a native lives with his or her parents by 0.07–0.17 percentage point in fixed effects and 2SLS estimation respectively, significant at the 10 percent level. Immigration of children aged 6–17 increases the share of natives living with their parents. These results support the idea that immigrant-induced increases in native enrollment are accompanied by increases in cohabitation with parents, and vice versa. The net effect of immigration 6–64 on living arrangements is zero, however (upper panel, Columns 1 and 2).
Effects of Immigrants on Native Household Composition, Work, and Idleness
I next turn to investigating whether immigrant-induced changes in enrollment reflect changes in the employment status of natives, or changes in the degree to which natives are idle (neither enrolled nor employed). Column 3 of the upper panel of Table 14 (fixed effects) indicates that a one percentage point increase in immigration of 6–64-year-olds reduces the share of natives who work without being enrolled by 0.15 percentage point. The lower panel shows that this is the result of immigration of adults with both less than 12 years education and exactly 12 years of education. There is no statistically significant effect of child immigrants on native employment. None of these statistically significant results is robust to instrumental variables in Column 4, however. The examination of idleness in the lower panel of Column 5 (fixed effects) indicates that child immigrants increase native idleness, while immigration of adults with less than 12 years education reduces it (significant at the 10 percent level). These effects cancel out so that immigration has no net effect on idleness (upper panel). However, no coefficient is statistically significant in the 2SLS of Column 6.
The final regressions of Table 14, in Columns 7 and 8, examine the outcome that is the main one of interest to Smith (2012): whether the native is working, whether or not he or she is also enrolled. The lower panel of Column 7 (fixed effects), confirms Smith’s result that native employment is reduced by immigration of adults with 12 years or less of education. It also shows that young immigrants aged 6–17 increase employment (lower panel) and that the net effect of all immigration is nevertheless negative (upper panel). The 2SLS results (Column 8) indicate that the negative effect is coming principally through immigrants with exactly 12 years of education.
I have also estimated enrollment regressions by race and ethnicity, though I do not report the results. The fixed effects results indicate, as for the analysis of 21–27-yearolds, that both net and gross effects of immigration are larger for native-born blacks than non-Hispanic whites, and that no clear pattern emerges for native-born Hispanics. As usual for the enrollment regressions, differencing reduces the coefficients to insignificance.
V. Conclusion
In this paper, I have shown that natives’ probability of completing 12 years of education and of being enrolled when aged 16–17 are increased by immigration, albeit by a small magnitude. This helps explain why immigration does not have large negative effects on the wages of natives. The schooling effect is larger for blacks than non-Hispanic whites and for children of low-education parents. The effect for Hispanic natives, on the other hand, is zero or a small (statistically insignificant) negative one. Consistent with the hypothesis that this education upgrading is prompted by a higher return to high school due to immigration of high school dropouts, I find that natives’ probability of completing 12 years of education or of being enrolled is increased by a greater presence of adult immigrants with less than 12 years of education. This effect is larger for native-born blacks than for non-Hispanic whites, and for children not living with either parent when aged 16–17. The latter effect is in part a composition effect, as the lower dropout rate is associated with more youth remaining in the parental household, which reduces the share of dropouts among youth not living with their parents. The effects are small even for the most affected groups, however.
Child immigrants have a small negative effect on the schooling of non-Hispanic white natives, one more robust in the analysis of enrollment than completion of 12 years of education. The effect on black natives and natives whose parents are poorly educated is more negative than for other groups. The effect appears to work through a diversion of resources to immigrant students rather than through classroom interaction or a neighborhood effect, as the effect of immigrants aged 6–17 is much larger than the effect of immigrants aged 16–17, who would be direct peers of the natives. This points to the need for additional financing for school districts with many immigrants, particularly those whose native-born students are disproportionately black or children of low-education parents.
The results are generally similar for males and females, even for minority groups. The results for Hispanics are generally imprecisely estimated, allowing no firm conclusions to be drawn, and the difference cannot be attributed to heterogeneity of Hispanic ethnicity, second-generation immigrant status, or lack of English proficiency for a minority of native-born Hispanics. However, the labor market channel may be masked by native Hispanics’ differential response to child immigrants whose parents are well or poorly educated.
Acknowledgments
She thanks Daniel Parent, Leah Brooks, David Figlio, Tommaso Frattini, James Heckman, John Eric Humphries, Ethan Lewis, Marguerite Lukes, James MacKinnon, Steve Pischke, and participants in numerous seminars for comments and data advice. She is grateful to the Social Science and Humanities Research Council of Canada for financial support. The data used in this article can be obtained beginning May 2018 through May 2021 from Jennifer Hunt, Department of Economics, Rutgers University, 75 Hamilton Street, New Brunswick, NJ 08901, jennifer.hunt{at}rutgers.edu.
Appendix
A. Analysis of Metropolitan Areas
I have linked metropolitan areas (cities) across the 1980–2000 censuses and the 2010 ACS using code generously provided by Ethan Lewis. It is only from 1980 onward, when the census sample rises from 1 percent to 5 percent, that samples are large enough to perform the analysis by city. I use the 130 cities (excluding Honolulu, for consistency with the state analysis) for which there are at least 75,000 observations on native 21–27- year-olds in the whole period; even using so few cities, some city–year cells are very small, especially for minorities. I retain the same specifications as for the state–level analysis, merely replacing trends based on 1940 values of certain variables with trends based on their 1980 values. I calculate the instruments in a parallel way, computing national shares of immigrants from different countries across cities in 1980, and retaining the same set of countries as for the state-level analysis. The means of the citybased samples are available upon request.
B. GED Analysis
I correct the 12-year completion rates using annual published tables on GEDs awarded by state and age, using the Heckman and LaFontaine (2010) appendix for methodological guidance. I scale down the published figures so as to reflect only native-born GED recipients with the help of the pooled 1999–2001 October supplement to the Current Population Survey and the 2008–2010 pooled ACSs, but the CPS samples sizes do not permit a breakdown by race and ethnicity. The published GED data indicate that only a small minority (less than 5 percent) of GED recipients had completed 12 years of high school, so I reduce the reported number of native completers by the estimated number of native GED recipients to obtain a “true” number of native completers of 12 years of schooling.
1. Official GED data
The basic data on GEDs are taken from the annual GED Statistical Reports (“Who Took the GED?” accessible at http://www.gedtestingservice.com/educators/historical-testingdata). From 1989 onward, statistics are available for the age distribution by state of GEDs awarded. A few missing and implausible values are filled in with linear interpolation, and for a number of states that began reporting the statistics only later, linear extrapolation back to 1989 is used. From 1974 to 1988, the age distribution is only available for those tested, rather than those who were awarded a GED. For these years, I compute for each age group the pass rate in the most recent year for which both the distribution of test-takers and the distribution of credentials awarded are available (1989 for most states), and use the pass rates to adjust the distribution of test-takers in 1974–88 to obtain the age distribution of GEDs awarded. New York begins reporting information by age only from 1984, and I impute 1974–83 values by extrapolating the 1984–88 trends. Before 1974, no information is provided by age and state, and for 1969–73, I assume the age distribution is the same as in 1974.
The age categories are not the same in all years, and the age categories for test-takers are not always the same as those for GEDs awarded. When the age categories change (in general they become finer over time), I split the coarser categories based the distribution in the nearest year with finer categories. Even the finest divisions do not give the age distribution for each year of age (above age 19), so after I harmonize the data at the finest categorization, I assume that GEDs are uniformly distributed within an age group. I assume that recipients 16 or younger are age 16. The final age distributions are combined with statistics for total GEDs awarded by state and year to obtain GEDs awarded by state and year for each year of age.
I use these numbers to calculate how many 21–27-year-olds held GEDs in 1980, 1990, and 2000, assuming that by the census date, one-third of the year’s GEDs had been received. For “2010,” I average the age 19–25 stock in 2008, the age 20–26 stock in 2009, and the age 21–27 stock in 2010.
2. Birthplace of GED recipients
The official GED statistics give no breakdown by birthplace, a breakdown necessary since I seek statistics for natives only. The October supplement to the CPS allows those whose highest degree is a GED to be identified, and from 1994 onward, the basic monthly CPSs contain birthplace. The ACS contains both the GED and birthplace information. I therefore use the pooled 1999–2001 October CPSs and the pooled 2008– 2010ACSs to estimate the immigrant share among those who completed a GED but had no college. The sample sizes are too small, however, to do this for each state (and too small to allow the calculation of the shares of minorities, which I do not attempt). I instead distinguish three groups of states in the CPS and six groups in the ACS, based on the share of immigrants in the population aged 21–27.
3. Combining the data sources
For 2000 and 2010, it is straightforward to adjust the total GED stocks calculated from official GED data with the share of immigrants from the census and ACS data to reflect natives only. For 1980 and 1990, I assume that the share of immigrants among GED holders aged 21–27 changes proportionately to immigrants’ share in the 21–27 population. I calculate the latter shares for the three state groups using the 1980 and 1990 censuses.
I then calculate the share of the native population aged 21–27 that holds a GED by dividing the GED stocks of natives 21–27 by the native population aged 21–27 (or the equivalent for 2008–2010), the latter computed by summing the census weights for natives, including those whose native status is imputed. I subtract this fraction from the fraction of natives with 12 years of schooling or more, which had been calculated based on a sample with nonmissing (and nonimputed) education and birthplace.
4. GED-adjusted statistics
The first row of Appendix Table 1 shows the national rawnative 12-year completion rates, while the second row shows the rates adjusted to count GED holders as noncompleters. The adjustment reduces the completion rate by five percentage points in 1980, and by more in later years. Nevertheless, the adjusted completion rate is estimated to have increased between 1980 and 2010, with stagnation between 1990 and 2000. The third row provides the 12-year completion rate as directly measured in the 2010 ACS. This rate of 87.8 percent lies between the rates of the first two rows (84.9 percent adjusted, 92.3 percent unadjusted), indicating that too many GEDs have been subtracted in the adjustment. One reason for this would be that some of the GED holders subtracted in fact went on to obtain more education, and do not appear as GED holders in the 2010 ACS. In Panel B, I consider high school graduation rates, which must be lower than 12-year completion rates. I measure this rate directly in the pooled 2008–2010 ACSs as 86.3 percent.
In Panel C, I present for comparison the Heckman and LaFontaine (2010) high school graduation estimates for 1970–2000. They use age groups that do not quite match mine, and remove only recent immigrants from their GED counts. I assume that their raw numbers for 1970 and 1980 include 12-year completers, since they cannot be distinguished from high school graduates, and that their raw numbers from 1990 onward exclude them. This would account for the lack of progress between 1980 and 1990 in their graduation rates, in contrast tomy adjusted 12-year completion rates in Panel A. Our 1980 rates should be similar, which they are. The graduation rate for 2010 measured directly (Panel B) appears high compared to the estimated Heckman and LaFontaine rates for 2000.
Native High School Completion and Graduation Rates 1970–2010
Means of Individual Level Variables—All Natives and Non-Hispanic White Natives
Means of Individual Level Variables—Black and Hispanic Natives
Means of Individual-Level Variables in Enrollment Sample
Means of Immigration-Related State-Level Covariates
Means of Other State-Level Covariates
1940 Shares of National-Level Immigrants from Various Origins, All Ages and Educations
First Stage of Two-Stage Least Squares (Adapted Instruments)
First Stage of Two-Stage Least Squares (Instrumenting Immigration Level)
Effects of Immigrants by Age and Education on Natives by Gender
Sensitivity of Results to Treatment of GED Holders
Footnotes
Jennifer Hunt is the James Cullen Professor of Economics at Rutgers University and a Research Associate at the National Bureau of Economic Research. She is also affiliated with the CEPR (London), DIW (Berlin) and IZA (Bonn).
↵* Supplementary materials are freely available online at: http://uwpress.wisc.edu/journals/journals/jhr-supplementary.html
↵2. Heckman and LaFontaine (2010); Murnane (2013).
↵3. For example, Borjas and Katz (2007); Ottaviano and Peri (2012). Card (2009) views the induced increase in wage inequality as small, which he attributes to high school dropouts and high school graduates being perfect substitutes.
↵4. If high school dropout workers and workers with less than college are perfect substitutes, it is the return to college that will rise, which also will increase high school completion rates.
↵5. Smith (2012) presents evidence that adult immigrants with high school or less reduce the employment rate of native high school students. This reduction could provide an additional channel for immigration to affect native graduation rates if such employment affects scholastic performance.
↵6. Jackson (2016) finds that when a greater share of adult immigrants is unskilled, native college enrollment rises, though the number of immigrant students has no effect; the effect of these variables on contemporaneous completed high school is not robust. Borjas (2007) finds that foreign students do not reduce native enrollment in graduate school. Neymotin (2009) finds native SAT scores and probability of applying to top colleges are not negatively affected by the school’s share of immigrant test-takers. See also Diette and Uwaifo Oyelere (2012). Guryan (2004) and Angrist and Lang (2004) find little or no effect of school desegregation on white students remaining in their school. Also relevant for my research are the mixed results in several papers examining the impact of immigrants on native test scores in Europe and Israel: Gould, Lavy, and Paserman (2009); Jensen and Rasmussen (2011); Brunello and Rocco (2013); Geay, McNally, and Telhaj (2013); Ohinata and van Ours (2013).
↵7. Card (2009) and Ottaviano and Peri (2012) believe the wage declines to be small. Borjas, Grogger, and Hanson (2012) disagree.
↵8. My results are not strictly comparable to those of McHenry (2015), who examines the effect of changes in the immigrant flow rather than the immigrant stock (as well as examining immigrants with higher education), but he notes that the results are similar using stocks. He finds that a 53.7 percent increase (a standard deviation) in (the increase in) adult immigrants with high school or less raises the native high school graduation rate by two percentage points. My results imply a 53.7 percent increase in adult immigrants with less than 12 years of education would raise native completion of 12 years of education by 1.4 percentage points: The mean of the immigrant density is 3.3 percent, and the effect is therefore (0.033)(1– 0.033)(0.8)(53.7) = 0.014.
↵9. In the Peri and Sparber (2009) model, immigrants might depress native wages (depending on the behavior of capital) if natives did not respond in any way, but because natives respond to the threat of a wage decline by specializing in language-intensive occupations and by upgrading their education, the realized effect on wages is small. In the extreme, it could even be zero. There is no inconsistency between a wage decline if natives do not respond, and little or no realized wage decline because natives do respond.
↵10. Ruggles et al. (2010).
↵11. Betts (1998) appears to use 12 years of schooling for 1980, and obtention of a high school diploma in 1990. This discrepancy drives the negative effect he finds of immigration on native Hispanics.
↵12. For the purposes of the graph, I use the 21–27 age group for all years including 2008–2010.
↵13. Valencia, Menchaca, and Donato (2002); MacDonald and Monkman (2005).
↵14. Heckman and LaFontaine report in their appendix that the adjustment for 1970 is small; furthermore, in 1970 GED holders may not have claimed to have completed 12 years of high school.
↵15. The data are accessible at www.nber.org/sddb/.
↵16. The 1940, 1960, and 1970 censuses are 1 percent samples, the 1980–2000 censuses are five percent samples, the ACS has a more complicated sampling scheme, which results in the pooled 2008–2010 sample being smaller than the 2000 sample. The 1950 census only asked education questions of a subset of the main one percent sample.
↵17. The adult immigrant shares are not highly correlated with Is,t–1011–17: for example, the correlation between Is,t–1011–17 and Is,t–10E<12 is 0.37 in differences.
↵18. I have experimented with using the (OLS) state–year return to completing 12 years schooling as the independent variable of interest, instrumenting it with actual or predicted immigrant flows. The coefficient on the return is always very imprecisely estimated, and the first-stage immigrant coefficients are often wrongly signed.
↵19. These instruments are similar to the instrument developed by Card (2001) and also used by Jackson (2014), McHenry (2015), and Hunt and Gauthier-Loiselle (2010). Because the instrument predicts flows, it is natural to use it to instrument the change in immigrant share. However, some authors use it to instrument the stock of immigrants, and I present these results as well.
↵21. See Beaudry, Green, and Sand (2012) for a formal treatment.
↵22. State-level unemployment rates are not available from other sources for earlier decades, so the unemployment rate cannot be matched to the year the respondent was aged 17, for example. In the enrollment regressions below, the coefficient on unemployment is strongly significantly positive.
↵23. For blacks and Hispanics, there is a large positive coefficient on the share of agricultural workers in 1940, which captures convergence among states: agricultural states in 1940 had large shares of either blacks or Hispanics in the population, who were poorly educated. I do not control for the educational attainment of blacks and Hispanics in 1940, as they are based on very small samples for many states. White educational attainment in 1940 is statistically insignificant in the regressions for minorities.
↵24. The murder data are from the Federal Bureau of Investigation’s Uniform Crime Reports accessible at www.ucrdatatool.gov/Search/Crime/Crime.cfm. The data are available from 1960 only, so the relevant regressions have fewer observations than those in Table 7.
↵25. In British schools, Lavy, Silvar, and Weinhardt (2012) find greater sensitivity of girls than boys to peer effects in British schools, while Gibbons and Telhaj (2015) find no difference.
↵26. Smith’s coefficient for whites 16–17 (he does not present results for all races and genders) indicates that a 10 percent increase in high school or less immigration raises enrollment by 0.1 percentage point. The mean of my immigrant density variable is 0.033, so the effect of a 10 percent increase in immigrants is (0.033)(1 – 0.033) (0.44)(10) = 0.14 percentage point (or 0.19 for the upper bound).
- Received January 2015.
- Accepted June 2016.