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The Effect of Schooling on Mortality: New Evidence From 50,000 Swedish Twins

  • Published:
Demography

Abstract

By using historical data on about 50,000 twins born in Sweden during 1886–1958, we demonstrate a positive and statistically significant relationship between years of schooling and longevity. This relation remains almost unchanged when exploiting a twin fixed-effects design to control for the influence of genetics and shared family background. This result is robust to controlling for within-twin-pair differences in early-life health and cognitive ability, as proxied by birth weight and height, as well as to restricting the sample to MZ twins. The relationship is fairly constant over time but becomes weaker with age. Literally, our results suggest that compared with low levels of schooling (less than 10 years), high levels of schooling (at least 13 years of schooling) are associated with about three years longer life expectancy at age 60 for the considered birth cohorts. The real societal value of schooling may hence extend beyond pure labor market and economic growth returns. From a policy perspective, schooling may therefore be a vehicle for improving longevity and health, as well as equality along these dimensions.

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Notes

  1. More studies have used the twin fixed-effects design to study the effect of schooling on various health outcomes, such as self-reported health, smoking, and obesity (e.g., Amin et al. 2013, 2015a; Behrman et al. 2015; Fujiwara and Kawachi 2009; Lundborg 2013; Madsen et al. 2014; Webbink et al. 2010).

  2. Economists have recently considered the relationship between education and a range of nonmonetary outcomes, such as health, criminal behavior, marriage, and political participation (see Lochner 2011 for an overview). This recent evidence points to the importance of education for a much wider range of outcomes than those observed on the labor market and thus suggests that the value of educational investments in society may be greater than previously thought.

  3. Later empirical research has found limited support for this specific mechanism (Cutler and Lleras-Muney 2010).

  4. Other twin studies, however, have found no significant association (Bonjour et al. 2003; Miller et al. 2005; Petersen et al. 2009).

  5. We impose the upper limit of 1958 because data for more recent cohorts of twins were not available to us.

  6. Selection issues are much less serious for those born in 1926–1958: average life expectancy had increased, and most twins would have survived until 1972–1973, when the first survey was conducted for these cohorts.

  7. The register does not cover Swedes who emigrated from Sweden and who no longer hold a civil registration in Sweden, however. Because we classify individuals who do not have a death date by 2009 in our data as still alive, we risk wrongly classifying individuals who emigrated and died abroad as still being alive. We believe this to be of little concern in our analyses, however, given that the number of emigrants in the cohorts used in our analyses is small. Although we cannot observe emigration directly in our data, we can draw on external sources. Statistics Sweden calculated the number of Swedes living abroad in 2003 for different age groups between 0 and 80 years (Nilsson 2004). For those aged 45 to 80 in 2003 (i.e., born between 1923 and 1958), the number of emigrants ranged from 250 among the early cohorts to 1,500 among the later cohorts; that is, only a small fraction of each birth cohort had emigrated. This fraction in our sample is substantially smaller because inclusion in our sample is conditional on surviving to 1972 and living in Sweden in 1972. We checked the number of potential emigrants by investigating how many individuals in our sample who lack income records in the last year of our income data (i.e., in 2007) had not died by 2007. The income records cover every source of income, including pensions. If there are no data, it is likely that the person either is dead or has emigrated. With this procedure, we found that 0.72 % (348 individuals) have no income and no death date. We reran our main regressions excluding this group, but the results were basically unchanged (results available on request).

  8. The information in these registers is reported from the various educational institutions directly to Statistics Sweden. Using the Swedish Standard Classification of Education (Svensk Utbildningsnomenklatur, SUN 2000), we impute years of schooling as follows: 6 for old primary school (“folkskola”) (born before 1935), 7 for old primary school (born 1935 onward), 9 for (new) compulsory primary school, 10 for one year of high school, 11 for two years of high school, 12 for three years of high school, 13 for one year of university studies, 14 for two years of university studies, 15 for three years of university studies, 16 for four years of university studies, 17 for five years of university studies, 18 for a licentiate, and 20 for a PhD.

  9. To impute years of schooling from the information in the 1970 census, we use the SUN codes in the census, which are somewhat less detailed than the SUN 2000 codes used in the 1990 and 2007 registers, together with information from Statistics Sweden. We assign years of schooling as follows: 6 for old primary school (“folkskola”) (born before 1935), 7 for old primary school (born in 1935 and onward), 9 for (new) compulsory primary school, 11 or two years of high school, 12 for three years of high school, 14 for two or fewer years of university studies, 15 for three or more years of university studies, and 18 for a licentiate or a PhD.

  10. In the 1973 survey, education was coded in the same way as in the 1970 census, and we impute years of schooling in the same way. For the 1961 survey, we assign years of schooling for the majority of the sample based on the self-reports. We impute the following way: 6 for old primary school (“folkskola”) (born before 1935), 7 for old primary school (born 1935 and onward), 9 for (new) compulsory primary school, 9 for “realskola,” and 12 for secondary school. For three of the categories (“occupational school,” “other,” and “unknown”), we are unable to directly impute years of schooling. We calculate the average years of schooling associated with these three categories for the subsample of people for whom we have data on education from both the 1990 register and the survey in 1963. We then impute these averages for the individuals for whom the only source of education data is the 1963 survey. We use this imputation procedure for only 2 % of the sample.

  11. Our figures on the fraction of pairs who differ in schooling corresponds relatively well with figures from previous studies using a twin design to study the returns to education (see, e.g., Ashenfelter and Rouse 1998; Holmlund et al. 2011).

  12. We do not include cohorts born before 1911 because the 1970 census does not include educational information for cohorts born earlier than 1911—that is, for those who were 60 and older in 1970. For comparability, we therefore restrict the comparison to cohorts born in 1911–1931.

  13. An alternative would have been to run fixed-effects regressions on the probability of surviving until certain ages or to study 5- or 10-year survival. We prefer duration models in our main specification because they better exploit the variation in the data. For 10-year survival, for instance, two related twins who die within the same 10-year period but on different dates would not contribute to the identification of the estimates in a fixed-effects model. In our preferred duration model, however, any differences in the death dates contribute to the identification of the estimates. To shed more light on the magnitude of our estimates, however, we also exploit fixed-effects models.

  14. See Ridder and Tunali (1999) for a thorough exposition of the SPL model.

  15. One cannot rule out that IQ differences between twins are generated through earlier differences in schooling inputs, such as teachers. In fact, this is what two Swedish studies found when using the same data Sandewall et al. (2014) used (Carlsson et al. 2013; Meghir et al. 2013).

  16. In principle, this possibility is testable if a good instrument exists to generate random variation in schooling between members of twin pairs. To the best of our knowledge, there are no twin data containing such instruments.

  17. In contrast, a few studies found that parents reinforce endowment differences between children (see, e.g., Behrman et al. 1994).

  18. The opposite would be true, implying upward bias, if the twin with less schooling rebelled by behaving differently from the better-educated co-twin.

  19. For comprehensive overviews of common criticisms to twin studies and the circumstances under which the estimated results are unbiased, see Amin et al. (2015b), Boardman and Fletcher (2015), and Kohler et al. (2011).

  20. We tested for statistically significant differences in the coefficient of schooling between MZ and DZ twins by pooling the samples and including an interaction term between schooling and being a MZ twin. This interaction term was insignificant, however (p = .34).

  21. The similarity in results with and without including twin fixed effects does not mean that genes are not important determinants of schooling or mortality. Instead, it suggests that the genes affecting schooling are not the same as those affecting mortality.

  22. However, an often mentioned potential advantage of within-twins estimates is that they might have less of a LATE flavor than IV estimates that depend on changing minimum schooling or school-leaving age requirements. The reason is that the twin fixed-effects estimates use variation in schooling over the entire schooling distribution, whereas many IV studies only use limited variation in schooling induced by the instrument (Amin et al. 2015b; Behrman et al. 2011).

  23. We also checked whether the twin pairs that differed in schooling also differed from other twin pairs in terms of observable characteristics. The results suggested that differences within twin pairs have become more common over time, as the average birth year of twin pairs that differed in schooling was 1937 compared with 1927 for twin pairs who did not differ. This difference was statistically significant. We return to the issue of changes in the estimates over cohorts/ages in subsequent sections.

  24. We also ran regressions excluding people who survived the ages of 100 and 90, respectively. We lost about 3,000 individuals by imposing this restriction, but the results barely changed.

  25. When we pool genders and interact an indicator for being male with schooling, the interaction term is insignificant in the SPL model (p = .68).

  26. The differences are not statistically significant, as revealed by insignificant interaction terms in both the SPL and in the standard Cox model (p = .68 and p = .17, respectively).

  27. We also tried alternative specifications of the birth weight variable, such as an indicator of low birth weight (birth weight <2,500 g). The indicator of low birth weight is significant, but when we included both this indicator and the birth weight variable, the latter always dominated and the former became insignificant.

  28. This would be true as long as at least some part of the variation in such preference traits is due to genetics. This is also what the studies by Cesarini et al. (2009) and Jang et al. (1996) suggest. A difference in results between MZ and DZ twins could also be explained by the greater role that measurement errors play among MZ twins than DZ twins. However, the bias resulting from relying on purely self-reported measures for education in estimating the association between schooling and health has been found to be of limited importance (e.g., Amin et al. 2015a, b). In addition, because data on education in this study are taken from registers for a large part of our sample, we do not believe that measurement errors play a great role.

  29. We also repeated the sensitivity tests of the previous sections, controlling for birth weight and height. The results were again robust.

  30. We cannot rule out that a strong downward bias from selection is offset by a strong upward bias from unobserved ability in the older cohorts. In later cohorts, a weaker selection bias would then also be offset by a weaker ability bias. It appears likely to us that improved access to education over time leads to less rationing of education according to skills. Moreover, when credit constraints are less binding, parents could more easily afford to send both twins to higher education institutions, whereas more binding constraints may lead parents to invest more in the more able twin. We can shed some light on this possibility by examining if the effect of height, which partly picks up cognitive ability, on education decreases over time. This is not the case, however; if anything, the effect is greater for the post-1940 birth cohorts.

  31. We tested this by including interaction terms between schooling and birth cohort indicators in the SPL model. For cohorts born in 1946–1958, the interaction term was significant for males and females combined (p < .01) and for males (p < .01), but was not significant for females (p = .36).

  32. The interaction terms between schooling and the cohort indicators for the age groups 60–70 and 70–80 were insignificant (p = .63 and p = .91, respectively)

  33. We test the proportional hazards assumption using Schoenfeld residuals (see the phtest option in Stata). For the age groups 50–60, 60–70, and 70–80, the Prob > χ2 are 0.55, 0.93, and 0.51, respectively.

  34. The Gompertz distribution has been shown to describe old age mortality rather well. This model is a parametric proportional hazard model in which the baseline hazard takes the following form:

    $$ {\uptheta}_0\left(t,a,b\right)=a{e}^{t/b}, $$
    (3)

    where a and e are shape and scale parameters, respectively, of the baseline; and t is, just as in the Cox and SPL models, the randomly distributed death time. Hence, the model can be expressed in terms similar to the Cox model with the addition that the baseline is specified according to a Gompertz distribution with specified shape and scale parameters.

  35. The main purpose of this exercise is not to exactly capture specific remaining life expectancies for different subgroups but rather to illustrate the differences in these expectancies—that is, to illustrate how the impact of education on mortality translates to longevity.

  36. On a computational level, the studied time/age profile is rescaled so that entrance in the relevant risk set occurs at time (t) 0 (at age 60) in order to more accurately capture old age mortality. The resulting estimates of the shape and scale parameters are then used to calculate life expectancies by integrating the random variable t with respect to its probability measure given by the estimated Gompertz density, over its support (0, inf)—that is, from age 60 (t = 0) onward.

  37. Around the millennium, the overall difference in life expectancy between the two countries was about three years, which has been attributed to a more unhealthy Danish lifestyle, especially in terms of alcohol and tobacco consumption (Juel 2008). Depending on its distribution within the population, this lifestyle may well interfere with the potential channels through which education may affect longevity.

  38. When we restrict our sample to the period 1921–1950 (the cohort studied by Behrman et al. (2011)) and run our SPL model on MZ and DZ twins, our estimate does not change much (0.950) and remains statistically significant.

  39. Another difference is that we are able to follow individuals until death in many cases, whereas they followed up until late adulthood. However, this difference seems to play a less important role because we find that the relationship between education and mortality becomes weaker with age rather than stronger.

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Acknowledgments

We thank participants at the 22nd European Workshop on Econometrics and Health Economics and at the 23rd EALE conference for useful comments. We are also grateful for comments by seminar participants at Lund University and Linneaus University.

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Authors and Affiliations

  1. Centre for Economic Demography, IZA, HEP, Lund University, Lund, Sweden

    Petter Lundborg

  2. Lund University, HEP Lund, Lund, Sweden

    Carl Hampus Lyttkens

  3. Jönköping Academy, Jönköping International Business School, Jönköping University, Jönköping, Sweden

    Paul Nystedt

Authors
  1. Petter Lundborg
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  2. Carl Hampus Lyttkens
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  3. Paul Nystedt
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Correspondence to Petter Lundborg.

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Lundborg, P., Lyttkens, C.H. & Nystedt, P. The Effect of Schooling on Mortality: New Evidence From 50,000 Swedish Twins. Demography 53, 1135–1168 (2016). https://doi.org/10.1007/s13524-016-0489-3

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