INTRODUCTION
Amidst the uncertainty ushered in by Brexit, refugee inflows in Germany and Sweden, and the electoral strength of far-right candidates in France or the Netherlands, one fact stands out as undisputed: a citizen’s level of education is one of the best predictors of support for populist far-right candidates (Becker and Fetzer Reference Becker and Fetzer2016). To explain this pattern, researchers and pundits have emphasized the mediating role of anti-immigration attitudes. Because less-educated voters are more hostile to immigration, they are also more likely to embrace platforms that link immigrants to criminality, stagnating wages, higher taxes, or to the decline of “native culture” (Hainmueller and Hopkins Reference Hainmueller and Hopkins2014). Such assertions prompt the following question: is the relationship between education and anti-immigration attitudes causal? In other words, does education decrease an individual’s likelihood of holding anti-immigration attitudes later in life?
Two noncompeting sets of theories contend that education’s effect on anti-immigration attitudes is indeed causal. One focuses on ethnocentrism and argues that schooling because it “explicitly promote(s) tolerance, improve(s) knowledge of and appreciation for foreign cultures, and create(s) cosmopolitan social networks,” generates “more pro-immigrant sentiment among more educated individuals” (Hainmueller and Hopkins Reference Hainmueller and Hopkins2014, 79). In this “education-as-character-shaping” literature, the experience of education directly translates into attitudinal differences: “education changes outlook,” providing “one of the few known social brakes against intolerance and other antidemocratic sentiments” (Napier and Jost Reference Napier and Jost2008, 614).
A second line of argument highlights the emergence in advanced democracies of a new structural cleavage pitting those adversely affected by deindustrialization, automation, and globalization—both materially and symbolically—against those benefiting from these structural changes (e.g., Kitschelt Reference Kitschelt1997). Individuals without qualifications fall on the losing side of this cleavage. For such voters, the activation of physical and cultural boundaries—signified by economic protectionism and ethnocentric policies—may boost their disposable income (Mayda Reference Mayda2006; Scheve and Slaughter Reference Scheve and Slaughter2001), in addition to their self-worth and social status (Lamont and Molnar Reference Lamont and Molnar2002; Shayo Reference Shayo2009). In this “education-as-cleavage” literature, education not only matters because of what happens while one is getting an education but also because of everything else that happens after exiting the educational system: the successful completion of additional degrees translates into different life expectations and experiences—e.g., lower unemployment risks, higher wages, and different occupational choices—that make one less likely to hold anti-immigration attitudes.
Both theories rest on the assumption that the negative correlation between education levels and anti-immigration sentiment (e.g., Citrin et al. Reference Citrin, Green, Muste and Wong1997; Hainmueller and Hiscox Reference Hainmueller and Hiscox2007; Mayda Reference Mayda2006) is, at least partly, causal. However, the validity of this underlying premise has not been definitively established (Hainmueller and Hopkins Reference Hainmueller and Hopkins2014). First, educated individuals may be less likely to exhibit anti-immigration attitudes due to unobserved differences in their upbringing, opportunities, or peers (Kam and Palmer Reference Kam and Palmer2008). Comprehensively controlling for such differences represents a major challenge, not least because political attitudes already differ across first-year high-school students that ultimately complete different levels of schooling (Jennings and Niemi Reference Jennings and Niemi1981). Second, researchers risk introducing upward and downward biases by including variables as controls that are themselves consequences of education. For instance, extant studies often control for income, residential location, and partisanship (e.g., Citrin et al. Reference Citrin, Green, Muste and Wong1997; Hainmueller and Hiscox Reference Hainmueller and Hiscox2007; Mayda Reference Mayda2006); each post-treatment variable is likely to be determined by education while also affecting immigration attitudes.
In this research letter, we leverage quasi-experimental variation to identify the effect of compulsory education reforms and an additional grade of high school on anti-immigration attitudes in five Western European countries currently facing significant anti-immigration movements. We use a regression discontinuity (RD) design to exploit six major compulsory schooling reforms that significantly impacted cohorts in Denmark, France, Great Britain, the Netherlands, and Sweden. The reforms, on average, increased a student’s secondary schooling by 0.29 years, without affecting tertiary education. This set of reforms contrasts with d’Hombres and Nunziata (Reference d’Hombres and Nunziata2016), who conduct a similar analysis including reforms that did not significantly increase schooling among the same survey respondents.Footnote 1
Pooling across countries, we find that reforms inducing individuals to remain in secondary education significantly decrease their hostility to immigration. On average, an additional year of schooling reduces support for immigration restrictions and the belief that immigration makes the country a worse place to live by 8- and 18-percentage points, respectively, and ultimately reduces closeness to far-right anti-immigration parties by more than a quarter of its mean. While lacking statistical power, our country-by-country analyses suggest that education induced greatest tolerance for immigrants in Denmark, France, and the Netherlands, and may have produced larger effects in Great Britain after the emergence of the United Kingdom Independence Party (UKIP). These findings thus indicate that the widely cited attitudinal differences between those without high school education and the rest of the population cannot be solely attributed to selection bias. The paper concludes by considering possible mechanisms and implications for future research.
RESEARCH DESIGN
After World War II, countries across Western Europe passed laws raising the legal age at which a child is permitted to leave compulsory education. Individuals belonging to the first cohorts subject to higher leaving ages are assigned a strong incentive to remain in school for at least an additional year. Compulsory schooling laws are widely used in labor economics to estimate the returns to schooling (e.g., Brunello, Fort, and Weber Reference Brunello, Fort and Weber2009; Oreopoulos Reference Oreopoulos2006). Using a RD design, we follow these approaches to identify the effects of education on anti-immigration attitudes.
Data
We focus on six major compulsory schooling reforms across five countries; namely, one reform in Denmark, France, the Netherlands, and Sweden, and two reforms in Great Britain.Footnote 2 Table 1 lists these reforms, highlighting the date and nature of the reform, and the cohorts affected. Detailed information on each reform is provided in Appendix Section A.1. Importantly for our question at hand, each country in our sample has since experienced politically influential anti-immigration movements.
Compulsory Education Reforms
Notes: †The second reform in Great Britain was first passed in 1962, but not implemented until a 1972 statutory instrument. The British reforms did not affect Northern Ireland.
Our empirical strategy relies on a large sample of respondents from cohorts born just late enough and not quite late enough to be affected by the reform. Accordingly, we pool seven waves of the European Social Survey (ESS) collected between 2002 and 2014, restricting our sample to adults aged 30 and above and born after 1915.Footnote 3 A key feature of the ESS is its battery of immigration questions repeated in each survey wave. Since the reforms generally occurred in the 1960s and 1970s, these surveys capture downstream attitudes once anti-immigration movements developed and respondents reached middle-age.
Outcome of Interest: Anti-Immigration Attitudes
To measure anti-immigration attitudes, we derive our dependent variables from the seven survey items listed in Table 2. The first three items reflect preferences for the number of different types of immigrants allowed into the country. The second set of three items reflects beliefs about the consequences of immigration on the economy, national culture, and quality of life. The final item captures self-identified closeness to far-right anti-immigration parties; Appendix Section A.2 details our coding of such parties.
Immigration Item Wording
Simply examining the raw responses encounters two issues. The first issue is that responses to identical questions may not be comparable because reference points and the interpretation of nonextreme responses are likely to vary by country and wave. Furthermore, ordinal scales impose a linear relationship that may not hold if the causal relationship is actually nonlinear or because differences between levels are not perceived to be linear by respondents. Our solution is to recode survey responses as binary variables anchored around reference points that are likely to be interpreted similarly across countries and time. Specifically, we transform items 1–3 into indicators for respondents that answer “none.” Because social desirability bias might induce respondents to avoid offering such an uncompromising answer, we also define indicators for respondents answering either “none” or “few.” Answers to items 4–6 bunch at 5, suggesting that respondents generally understood this as the point of indifference. We consequently recode items 4–6 each as an anti-immigration indicator for respondents selecting an anti-immigration response category (i.e., 0–4). Finally, we code closeness to a far-right party as an indicator for any level of closeness among respondents that feel closest to such parties. Individuals who do not feel close to a party, or who feel close to a non-far-right party, are coded as 0.
The second issue regards the likelihood that preferences for different types of immigrant (items 1–3) cannot be examined separately. Respondents that oppose immigration may express their opposition differently across items, depending on whether they demand restrictions based on income, race, or both. Appendix Section A.2 explains in detail why we prefer a holistic approach distinguishing between unconditional support for any type of immigrants and wanting to restrict entry to one or more type(s) of immigrant(s). To capture anti-immigration preferences, we thus define an anti-immigration indicator for respondents who express support for limiting entry to at least one type of immigrant. We implement this approach using both the “none” and the “none or few” indicators mentioned above. Appendix Tables A.14–A.16 report broadly similar—but, as anticipated, weaker—results when using coding approaches that treat items 1–3 as if independent.
Finally, we aggregate across the resulting six binary variables to produce an additive scale of anti-immigration sentiment designed to capture an individual’s latent disposition toward immigration. By averaging across these outcomes, standardized both across and also within countries, we reduce the measurement error arising from individual items. More information on these scales—which, for the across- and within-country standardizations, have high inter-item reliability coefficients of 0.78 and (a cross-country average of) 0.75, respectively—is available in Appendix Section A.2.Footnote 4
Identification Strategy
To identify the effects of compulsory education reform eligibility, we use an RD design to compare cohorts just young enough to be affected by the reforms to cohorts just too old to have been affected. We thus define our treatment—being affected by a compulsory education reform—for respondent i from cohort b in country c as
$${\rm{refor}}{{\rm{m}}_{bc}} = \left\{ {\matrix{ 0 \eqalign{{{\rm{if}}\;{\rm{birth}}\;{\rm{yea}}{{\rm{r}}_{bc}} - {{\rm{birth}}\;{\rm{year}}\;{\rm{first}}\;}}\cr{\rm{affecte}}{{\rm{d}}_{bc}} \,\,\lt\,\, {\rm{0}}} \cr 1 \eqalign{{{\rm{if}}\;{\rm{birth}}\;{\rm{yea}}{{\rm{r}}_{bc}} - {\rm{birth}}\;{\rm{year}}\;{\rm{first}}\;}\cr{\rm{affecte}}{{\rm{d}}_{{{bc}}}} \,\,\ge\,\, 0} \cr} } \right.\hbox,$$where birth year first affectedbc is the birth year of the first cohort affected by a reform. We then identify the local average treatment effect of our compulsory education reforms, among cohorts just young enough to be affected by the reforms, by estimating the following regression:
$${y_{ibc}} = \beta \;{\rm{refor}}{{\rm{m}}_{bc}} + f\left( {{x_{bc}}} \right) + {\varepsilon _{ibc}}\hbox,$$where y ibc is anti-immigration attitudes of an individual and f is a function of our running variable x bc := birth yearbc − birth year first affectedbc. In our baseline specification, f is a local linear regression using a triangular kernel and the optimal bandwidth recommended by Calonico, Cattaneo, and Titiunik (Reference Calonico, Cattaneo and Titiunik2014). Intuitively, this entails controlling for trends across (around ten) cohorts separately either side of the discontinuity, while assigning greater weight to cohorts immediately around each discontinuity. We emphasize our analysis of the pooled data, which maximizes the design’s power. However, because the nature and beneficiaries of the reforms differ across countries, we also report results by country.
This design enables us to estimate the causal effect of raising the school leaving age among the first students to be affected, provided that potential outcomes are continuous through the cohort eligibility threshold. We validate this assumption in Appendix Section A.3. First, Appendix Figure A.2 and the associated density tests indicate that individuals born around the discontinuity did not manipulate their birth year to sort into receiving the reform. Second, Appendix Table A.5 shows that affected and unaffected cohorts around the reforms are similar across 13 predetermined covariates. Third, Appendix Section A.1 describes the context of the reforms, highlighting that the compulsory education reforms are unlikely to be confounded by other changes differentially affecting those subject to the reform.
Many students would have stayed in school absent a reform. To identify the local average treatment effect of an additional year of secondary education on those that only completed additional schooling because of a reform, we estimate a “fuzzy” RD by using the reforms to instrument for the number of completed years of schooling using an analogous local linear regression:Footnote 5
$${y_{ibc}} = \beta \;{\rm{years}}\;{\rm{of}}\;{\rm{completed}}\;{\rm{schoolin}}{{\rm{g}}_{ibc}} + f\left( {{x_{bc}}} \right) + {\varepsilon _{ibc}}\hbox,$$where years of completed schoolingibc is instrumented using the following first stage regression:
$$\eqalign{{\rm{years}}\;{\rm{of}}\;{\rm{completed}}\;{\rm{schoolin}}{{\rm{g}}_{ibc}} = \;\alpha \;{\rm{refor}}{{\rm{m}}_{bc}} \cr+ f\left( {{x_{bc}}} \right) + {\varepsilon _{ibc}}.$$Identification of the local average treatment effect at the cutoff requires two additional assumptions: the reforms do not decrease education levels for any student (monotonicity), and only affect anti-immigration attitudes through their effect on completing additional years of schooling (exclusion restriction). These assumptions are plausible in this context, as students are unlikely to respond by completing less education and it is hard to see how the reforms could influence downstream attitudes without working through the additional time spent in school (Marshall Reference Marshall2016b). We nevertheless discuss possible exclusion restriction violations in Appendix Section A.5.
RESULTS
Compulsory Schooling Increases Secondary Education
We first verify that the compulsory education reforms indeed increased schooling among affected cohorts. We measure formal education as the number of completed years of education up to a limit of 13 years. This limit captures the end of secondary education, after which the kind of additional education varies across students.Footnote 6
Figure 1 shows a notable discontinuity in the number of years of completed schooling around all six reforms. The reform-by-reform RD estimates in column (1) of panels A–F in Table 3 confirm that each reform significantly increased the average number of years of completed schooling among affected cohorts by at least 0.2 years. Figure 2 and panel G show that the pooled estimate across countries—of 0.29 years—is also statistically significant. Appendix Table A.6 shows that these increases in education are concentrated around students’ eighth to thirteenth years of schooling, but do not systematically affect tertiary education. In sum, the reforms achieved their goal of raising secondary education levels among many students that would not have otherwise remained in school.
Years of Completed Schooling among Cohorts around Compulsory Schooling Reforms, by Reform (Third-Order Polynomials Either Side of the Reform)
The Effect of Compulsory Education on Years of Completed Schooling and Anti-immigration Attitudes
Notes: All specifications are estimated using local linear regression using the Calonico, Cattaneo, and Titiunik (Reference Calonico, Cattaneo and Titiunik2014) optimal bandwidth and a triangular kernel. The reported optimal bandwidth is rounded down to the nearest integer. Robust standard errors are in parentheses. + denotes p < 0.1, * denotes p < 0.05, ** denotes p < 0.01, and *** denotes p < 0.001.
Years of Completed Schooling among Cohorts around Compulsory Schooling Reforms, Pooled across Reforms (Third-Order Polynomials Either Side of the Reform)
Compulsory Schooling Decreases Anti-Immigration Attitudes
Figure 3 and columns (2)–(9) of Table 3 compare anti-immigration attitudes between pre- and post-reform cohorts. We start by examining preferences for restricting one or more type of immigrants, considering both our coding rules [“none” in column (2), and “none” or “few” in column (3)]. The point estimates are generally negative: affected cohorts are less likely to oppose expanding immigration later in life. These estimates are greatest in France and the Netherlands, but predominantly negative across reforms. Pooling across countries to increase the precision of our estimates, panel G shows that the difference in attitudes is statistically significant and indicates that, on average, affected students are almost three-percentage points—or 15%, relative to the stronger anti-immigration sample mean—less likely to oppose immigration later in life.
Anti-immigration Attitudes among Cohorts around Compulsory Schooling Reforms, Pooled across Reforms (Third-Order Polynomials Either Side of the Reform).
Note: The y-axis differs across outcomes
Columns (4)–(6) next consider the possible roots of such decreased opposition to immigration by examining its perceived socioeconomic impacts. The most consistent finding is that the reforms reduce the probability that an affected respondent later in life expresses that immigration makes one’s own country a worse place to live by 6.1-percentage points—an 18% decrease on the sample mean. This pooled estimate is driven primarily by Denmark, France, and the Netherlands. Although the pooled estimates in columns (4) and (5) are also negative, the point estimates for economic and cultural considerations are smaller in magnitude. These results could suggest that local factors—potentially reflecting reduced day-to-day interaction or weaker community impacts, like house price shocks—may be more important than reduced economic or cultural threat in explaining education’s effects, or instead that elite messaging engenders vague anti-immigration sentiment that educated respondents are more resistant to.
Pooling across countries, column (7) shows that reduced opposition to immigration translates into lower support for far-right anti-immigration parties. This primarily reflects the pronounced differences in Denmark, Great Britain (after the 1972 reform), and the Netherlands, where the reform roughly halved the probability of feeling close to far-right parties. The low frequency of such responses—5% on average in our pooled sample—reduces the precision of these estimates, but our validation of the results in a larger France-specific survey (Appendix Table A.20) supports this finding.
Finally, columns (8) and (9) examine two anti-immigration attitude scales—the mean of the preceding six items, standardized first across and then within countries. Although we observe similar heterogeneity across countries, the pooled results ultimately demonstrate that anti-immigration sentiment significantly declined among affected cohorts by around 0.06 standard deviations on average.
Secondary Education Decreases Anti-Immigration Attitudes
Because the educational attainment of many students in affected cohorts was unaltered by the reforms, we now estimate the effects of an additional year of schooling itself using our instrumental variables (IV) strategy. The results in panel H of Table 3 show that secondary education substantially decreases anti-immigration attitudes among students that complied with the reform.Footnote 7 For such students, an additional year of schooling reduces the probability of expressing anti-immigration attitudes by eight-percentage points, the probability of stating that immigration negatively affects the quality of life in the country declines by 18-percentage points, the probability of feeling close to the far right by six-percentage points, and the overall anti-immigration scales by 0.2 standard deviations.
These large average effects indicate that secondary education has played an important role in inducing tolerant attitudes toward immigration later in life among students that would otherwise have left secondary education. Our estimates—which are around three times larger than the cross-sectional correlations reported in Appendix Table A.18—also suggest that relatively uneducated reform-compliers could be particularly susceptible to education’s tolerance-inducing effects.
Robustness Checks
The pooled reduced form estimates are robust to various potential concerns, which Appendix Sections A.5, A.6, and A.8 address in detail. First, specification tests show that all findings are robust across bandwidths ranging from two to 15, the choice of kernel weighting, the inclusion of local quadratic and cubic cohort trends, and placebo reforms occurring five and ten years earlier. Second, the results are robust to “leave one out” checks removing any particular reform or any item from the anti-immigration scales. Third, we find similar results for several alternative operationalizations of our outcomes. Fourth, we validate our findings by replicating our analysis using larger country-specific surveys in France and Great Britain. Finally, our examination of alternative potential channels suggests that plausible exclusion restrictions are not driving our IV estimates.
DISCUSSION
The transition out of high school has attracted significant attention from researchers and journalists highlighting the substantial gap in immigration attitudes between those that did not complete secondary education and the broader population. Leveraging exogenous variation in exposure to compulsory schooling reforms in five Western European countries that subsequently experienced significant anti-immigration movements, we demonstrate that an additional year of secondary education substantially decreases anti-immigration attitudes.
By establishing that this relationship is indeed causal, this research letter lays the groundwork for future studies trying to disentangle the mechanisms driving secondary education’s potential role in explaining and addressing the rise of far-right anti-immigration parties.Footnote 8 To help frame this agenda, we conclude by discussing our preliminary exploration of these mechanisms using this paper’s identification strategy; Appendix Section A.9 comprehensively details the analysis we now summarize.
According to the “education-as-character-shaping” literature, secondary education directly triggers attitudinal change. This could occur via the promotion of motivational values in teenage-hood that translate into lasting lower levels of prejudice. However, our examination of a battery of ESS items capturing basic human values fails to detect any evidence that affected cohorts embrace values associated with lower levels of prejudice more generally.
Similarly, based on the widely cited economic returns to education (e.g., Brunello, Fort, and Weber Reference Brunello, Fort and Weber2009; Oreopoulos Reference Oreopoulos2006), the “education-as-cleavage” literature might predict that reduced anti-immigration sentiment reflects lower individual exposure to competition from immigrant labor. Yet, research shows that anti-immigration preferences are poorly predicted by objective and subjective measures of immigration’s consequences on individuals’ pocketbooks (Hainmueller and Hopkins Reference Hainmueller and Hopkins2014), which is reinforced by our finding that education does not significantly alter perceptions of immigration’s economic effects. Rather, what appears to matter is whether individuals think immigration policy serves immigrants’ interests at the expense of their country’s interests. Over their lifetime, educated voters may become more exposed to worldviews discouraging of such sociotropic and ethnocentric zero-sum reasoning (Hainmueller and Hopkins Reference Hainmueller and Hopkins2014). However, we also find little evidence to suggest that the relatively pro-immigration attitudes of affected cohorts extend to broader liberal-cosmopolitan positions (Kitschelt Reference Kitschelt1997) on women and gay rights or support for EU integration.
The cross-country heterogeneity in the effects of compulsory schooling reforms suggests that differences in receptivity to elite-messaging across education levels could also be a key mechanism. The starkest contrast in our findings is between Great Britain’s negligible effects and systematic changes in Denmark, France, the Netherlands, and—to a lesser extent—Sweden. This difference mirrors the comparatively weaker institutionalization of far-right parties in Britain, where its majoritarian system has (until recently) enabled the major parties to depoliticize immigration debate. Consistent with this potential mechanism, Appendix Table A.19 tentatively suggests that cohorts affected by Britain’s 1947 reform developed less anti-immigration attitudes after UKIP emerged. This messaging explanation might also explain why the relatively nonspecific sentiment that immigration has reduced local livability is most affected by secondary education. There are, of course, alternative explanations for cross-country heterogeneity based on the reforms themselves and other contextual features. Ultimately, these sources of spatial and temporal heterogeneity merit further research.
This analysis of causal mechanisms is only tentative. Future studies might benefit from recovering survey data collected closer to the reforms themselves to separate whether tolerance toward immigration emerges quickly after leaving school, as “education-as-character-shaping” suggests, or only later in life, as “education-as-cleavage” and elite messaging suggest. Future research might also exploit survey-specific contextual variation to examine how education’s effects may be amplified by changes in the return to education or anti-immigrant elite messaging. Regardless, we hope that this letter inspires rigorous analysis seeking to understand a defining issue of contemporary Western politics.
SUPPLEMENTARY MATERIAL
To view supplementary material for this article, please visit https://doi.org/10.1017/S0003055418000588.
Replication material can be found on Dataverse at: https://doi.org/10.7910/DVN/YDSRWF.
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