The Effect of Education on Old Age Cognitive Abilities: Evidence from a Regression Discontinuity...

THE EFFECT OF EDUCATION ON OLD AGE COGNITIVEABILITIES: EVIDENCE FROM A REGRESSION

DISCONTINUITY DESIGN*

James Banks and Fabrizio Mazzonna

In this article, we exploit the 1947 change to the minimum school-leaving age in England from 14 to15, to evaluate the causal effect of a year of education on cognitive abilities at older ages. We use aregression discontinuity design analysis and find a large and significant effect of the reform on males�memory and executive functioning at older ages, using simple cognitive tests from the EnglishLongitudinal Survey on Ageing as our outcome measures. This result is particularly remarkable as thereform had a powerful and immediate effect on about half the population of 14 years olds. Weinvestigate and discuss the potential channels by which this reform may have had its effects, as well ascarrying out a full set of sensitivity analyses and robustness checks.

The association between schooling and many positive economic, social and healthoutcomes is well documented. Although this association needs to be interpreted withcaution because of reverse causality and the potential indirect effect of unobservedfactors, the economic literature has recently been able to identify a causal effect ofeducation on many of these outcomes, often through the use of an estimation strategybased on exploiting plausibly exogenous variations in schooling. One leading exampleis that of changes to compulsory schooling laws. These laws are ideal instruments notonly because they allow the evaluation of the exogenous effect of one more year ofeducation but also they allow the evaluation of the efficacy of such a policy change. Aseries of articles has systematically investigated the gains to various adult outcomes fromcompulsory schooling, using reforms to schooling laws in both the US and the UK. Themain outcomes studied have been earnings (Angrist and Krueger, 1991; Harmon andWalker, 1995; Acemoglu and Angrist, 2001; Oreopoulos, 2006), crime (Lochner andMoretti, 2004; Machin et al., 2011) and health (Lleras-Muney, 2005; Clark and Royer,2010).

However, not all of the potential benefits from such policies have been explored. Inparticular, the effect of schooling on old age cognitive abilities is missing, though thiseffect should be of an increasing interest in an ageing society. Cognitive abilities

* Corresponding author: Fabrizio Mazzonna, Max Planck Institute for Social Law and Social Policy,Amalienstrasse 33, D-80799 Munich, Germany. Email: [email protected]; [email protected]

We are grateful to Janet Currie and Franco Peracchi, as well as two anonymous referees, for comments onearlier drafts of this work. We are also grateful to the audience of the 2010 RAND Workshop on ComparativeInternational Research Based on HRS, ELSA and SHARE. Banks is grateful to the Economic and SocialResearch Council and the US National Institute on Ageing for funding his research on this project. Data fromthe ELSA were supplied by the ESRC Data Archive. ELSA was developed by researchers based at UniversityCollege London, the Institute for Fiscal Studies and the National Centre for Social Research, with fundingprovided by the US National Institute on Ageing and a consortium of UK government departments coor-dinated by the Office for National Statistics. Responsibility for interpretation of the data, as well as for anyerrors, is the authors� alone.

The Economic Journal, 122 (May), 418–448. Doi: 10.1111/j.1468-0297.2012.02499.x. � 2012 The Author(s). The Economic Journal � 2012 Royal

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are fundamental for decision making and a crucial element for the appropriateformulation and subsequent execution of consumption and saving plans (Banks andOldfield, 2007). Individual or household decision-making skills are arguably becomingmore important for older individuals with the increasing importance of individualprovision, and the declining importance of state provision, in social security andhealthcare systems around the world. More generally, cognitive abilities may be re-garded as one aspect of human capital, along with education, health and non-cognitive abilities.

For this reason, in this article we analyse the 1947 British compulsory school reformwhich increased the minimum school-leaving age from 14 to 15 years old, presentingnew evidence of the causal relationship between the resulting additional years ofeducation and late-life cognitive skills. We use this law change for two main reasons.First, it was targeted at the least educated groups and specifically aimed at affectingsubsequent physical and mental trajectories as is clear from the government’s motiva-tions, initially reported by Oreopoulos (2006): �. . .improve the future efficiency of thelabour force, increase physical and mental adaptability and prevent the mental andphysical cramping caused by exposing children to monotonous occupations at anespecially impressionable age�.1

Second, the 1947 British school law affected a very large proportion of the 14 years oldpopulation – decreasing by around 50% points in one year the proportion of people wholeft full-time education before age 15. We exploit this dramatic change in educationalattainment using a fuzzy regression discontinuity (FRD) design to evaluate the causaleffect of the additional year of schooling induced by the reform on old age cognitiveability. Although it is not a �sharp� design, because the increase in educational attainmentdid not affect the entire population involved by the reform, the large proportion affectedis particularly important in comparison to similar US compulsory school changes thataffected only about 5% of the relevant cohorts (Lleras-Muney, 2005). This difference isparticularly important if the effect of interest is not homogeneous across the populationsince our estimation strategy allows us to recover only local effects (LATE) instead ofaverages across the population (ATE) (Imbens and Angrist, 1994). As a consequence, alocal parameter based on such a large proportion of the population should be morerelevant than one based on a very small subgroup as in the US case.

We find that the compulsory school law change of 1947 had a quite large impact –around half of one standard deviation – on male memory and executive functioning atolder ages measured using a set of cognitive tests from the English Longitudinal Surveyon Ageing (ELSA). Such a magnitude could be rationalised by diminishing marginalreturns to schooling, coupled with the reform being incident only on those in the lowertail of the education distribution and the fact that our estimators focus only on theeffects of the reform on those who were actually �affected�. Nevertheless, given thisperhaps surprisingly large magnitude, we engage in a full battery of sensitivity androbustness tests. In order to test for confounding factors we look for potential effects of

1 This quote also makes it clear that, as well as providing one year of extra schooling, this reform will havetypically led to a one-year delay in entry into the labour force which may be considered beneficial if paid workat young ages is thought to be harmful. Obviously our analysis will not be able to distinguish between which ofthese two changes led to any identified effects on outcomes, although we do return to this issue briefly in ourdiscussion.

� 2012 The Author(s). The Economic Journal � 2012 Royal Economic Society.

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the reform on other variables – in our case childhood health prior to the reform andfather’s occupation – that might be thought to be predetermined and operatingindependently of the reform. In addition we look for discontinuities at dates-of-birthother than the cut-off around which the reform was defined, we consider a broad rangeof linear and polynomial trend controls and we consider subsamples defined bydifferent sized windows on either side of the reform and by the exclusion of those withhigh education levels. None of these tests provides any basis on which to doubt theempirical findings.

Consequently, in our analysis, we also discuss possible explanations for these resultsand the mechanisms and channels through which education may be thought to haveaffected old age cognitive abilities. The income channel is more reasonable due to theestimated large impact of the 1947 reform on earnings (Oreopoulos, 2006). We alsofind some positive effects of the reform on males� social and cultural participation andengagement, although we argue these may themselves only be an artefact of income oremployment effects since such effects are only present for men. Finally, we are able toexclude the health channel. In addition to poor evidence found for the effect of thereform on many health outcomes in other analyses (Jurges et al., 2009; Clark andRoyer, 2010), we do not find significant effect of the reform on late-life subjectivewell-being and quality of life using a measure (CASP 19) that is known to be highlycorrelated with many health outcomes (Wiggins et al., 2008).

The remainder of this article is organised as follows. In the next Section we brieflyreview the literature on the relationship between schooling and cognitive abilities anddiscuss the main features of the 1947 compulsory school reform. Section 2 describesthe data used for our analysis and Section 3 describes the empirical strategy along withthe main identification issues. Section 4 presents our results and, finally, Section 5offers some further discussion of issues arising from the results and presents ourconclusions.

1. Background

1.1. Education and Cognitive Abilities

The relationship between schooling and cognitive abilities is one of the most studiedissues in both psychology and economics. The controversial book The Bell Curve byHerrnstein and Murray (1994) claims that education does not affect cognitive skills.According to their view, intelligence, measured by IQ is fixed at a relatively early age –around age 8. This would imply that intelligence is mainly responsible for studentsstaying in school and for subsequent economic and social achievements. Differentevidence comes from Ceci and Williams (1997) who report some evidence of a bi-directional relationship between schooling and intelligence which affects variations ineconomic outcomes.

In the labour economics literature a large debate concerns whether schooling plays arole mainly as a market signal of innate ability or as way to improve skills. For thisreason, many efforts have been concentrated on assessing the economic return toeducation controlling for endogeneity due to unobserved ability (Ashenfelter andRouse, 1998; Card, 2001; Oreopoulos, 2006). This literature clearly identifies a causal

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effect of education on earnings but even this could not be considered an evidence of aneffect of schooling on cognitive skills since such an effect would also be predicted by asignalling model (Spence, 1973) in which schooling emerges as a signal that an agentsends about her ability level to the employer. In that case, schooling may allow indi-viduals to obtain those formal qualifications required to apply for higher earnings job.

Cunha and Heckman (2007) build an analysis that draws a distinction between in-nate ability and acquired skills. They argue that �abilities are created, not solelyinherited, as interaction between genes and environment� to produce cognitive andnon-cognitive skills that have both a genetic and an acquired character. They showevidence of critical and sensitive periods in skill formation and dynamic complement-arity in investments. The main consequence of their findings is the importance of earlylife intervention in particular for the subsequent evolution of cognitive abilities. Theyshow that returns to late childhood investment in young adolescents from disadvantagedbackgrounds are very low compared with the returns to early investment. No lessimportant is the role of non-cognitive abilities that are responsible for performance inmany economic, health and social achievements. Recently, Heckman et al. (2010) showthat the Perry Preschool Program, which enhanced the subsequent economic and socialperformance of participants, did not boost participant adults IQ but only their non-cognitive abilities.

Even less clear is the relationship between schooling and old age cognitive abilities,which is the main target of our work. Many empirical studies (Le Carret et al., 2003;Mazzonna and Peracchi, 2010) underline the positive association between education andold age cognitive abilities but only Glymour et al. (2008) find evidence of a causal rela-tionship between education and memory. Exploring geographical variation in the UScompulsory school reforms they found a positive effect of an additional year of educationon memory test scores at older ages by using data from the Health and Retirement Study(HRS). In that study, however, the estimated effects are based on an instrument (thecompulsory school reforms in the US) that only affects a very small fraction of thepopulation (see below for more detail) and in addition assumes that the effect of dif-ferent reforms applied in different states in different points in time is homogeneous.Additionally, they use a separate-sample instrumental variable estimator in which the firststep is estimated using the 1980 US census 5% sample and as such, their estimates may besensitive to differential response patterns in the HRS and Census samples.

The specific mechanism through which education might affect old age cognitiveabilities is not clear. Mazzonna and Peracchi (2010) apply the Grossman (1972) modelof health capital to cognitive outcomes in order to generate empirical predictionsabout the evolution of cognitive abilities at older ages. In that framework there aremultiple channels that can be identified: productive efficiency; employment, earningsand occupational choice; or preferences for social and cultural-stimulating activities.The direct effect of the reform in this case would be through productive efficiency,which means that more schooling allows individuals to obtain better health from agiven amounts of inputs. However, this framework seems less directly applicable tocognitive outcomes than to health. In addition, a direct effect of the reform on cog-nitive abilities might seem inconsistent with the results from the previously cited lit-erature on cognitive skill formation that shows poor effect of investment on youngadolescents.

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The occupation channel is perhaps more interesting. In a signalling model schoolingcould, through formal qualifications, allow individuals to apply for higher earning jobsand such jobs could positively affect cognitive abilities, particularly at older ages if theyare more cognitively demanding. However, the changing nature of education signalsover time when cohorts are affected by reform would need to be borne in mind inmaking any more formal statements along these lines. And, as we explain in the nextsubsection, the 1947 reform did not lead to additional formal qualification for theaffected students so signals may not be particularly strong. On the other hand, Oreo-poulos (2006), exploiting the same reform, found a significant and large effect(around 15%) of the additional year of schooling on earnings. To the extent that thesegreater earnings are associated with either higher rates of employment, or more cog-nitively demanding jobs amongst those employed, then these two factors may protectagainst cognitive decline at older ages (Mazzonna and Peracchi, 2010; Rohwedder andWillis, 2010). Given the different labour market pattern of males and females fromcohorts born in the 1930s, with low rates of female labour force participation in par-ticular, differences in the effect of the reform across gender could be thought toindicate support for this channel. To this end, Devereux and Hart (2010), reviewingthe findings in the Oreopoulos’s paper, highlight evidence of positive returns toschooling reform only for males although they estimate the magnitude of the effect tobe smaller – around 4–7% as opposed to the 10–15% estimated by Oreopoulos (2006).2

In Section 4 it will be shown that this last evidence is consistent with our result of apositive effect of the reform only on males’s cognitive abilities at older ages.

A similar set of considerations applies to the third channel, namely social andcultural participation. The positive effects of such activities have been extensivelydescribed by Hertzog et al. (2008) in a comprehensive review of cognitive-enrichmenteffects at old ages. In this case, the general idea would be that education could affectthe parameters of the utility function thus increasing the utility derived from morecognitive demanding activities and consumption (e.g. reading newspapers, using theinternet or engagement in social and cultural organisations, club or societies).

The last channel we consider is health. If the reform improved health trajectories ofthe affected population this may also have an effect on cognitive abilities at older ages.However, using many waves of the Health Survey for England (HSE), Jurges et al.(2009) and Clark and Royer (2010) do not find any significant effects of the same 1947reform on many health outcomes, specifically – mortality, blood pressure, self-assessedhealth and selected biomarkers. Given this lack of evidence on physical health we willexplore a more global measure of subjective well-being and quality of life, the so-calledCASP 19 index which captures Control, Autonomy, Self-Realisation and Pleasure(Appendix A). This measure is particularly important in an ageing society where livinglonger is no longer enough, and quality of life during the old age is recognised to beequally important (Hyde et al., 2003).

2 In a more recent article, Chib and Jacobi (2011) find only very small earnings effects using the samedataset as Oreopoulos but with a Bayesian estimation approach. However, their use of unbalanced month-of-birth windows on either side of the reform (from January 1932 to March 1933 in comparison to May 1933to December 1934) may mean the estimates are not directly comparable in the presence of either unobservedsocioeconomic characteristics that are correlated with month of birth (Buckles and Hungerman, 2010), orage at school entry effects on subsequent outcomes (Crawford et al., 2010).



1.2. The 1947 British School-leaving Age Reform

Legislation from UK’s 1944 Education Act raised the minimum school-leaving age inEngland, Scotland and Wales on 1 April 1947 from 14 to 15 years old.3 This law and itsimplementation has been extensively discussed in the articles which use the sameexogenous variation in compulsory schooling as an instrument for identification of theeffect of education on income and health (Oreopoulos, 2006; Jurges et al., 2009; Clarkand Royer, 2010). For this reason we will only briefly discuss the main points of thisreform here.

Put simply, whilst children born before 1 April 1933 could leave school when theyturned 14, the 1947 reform stated that those born after that date could not leave untilthey turned 15. As stressed by Oreopoulos (2006), this law change affects a largeproportion of the population. Figure 1 shows the fraction of males and females wholeft full-time education by the age of 14. Using the ELSA data described in more detailbelow, the Figure displays averages at quarter of birth level with the vertical black linemarking the exact cut-off point at 1 April 1933. It is evident that before the reformabout 60% of the population left the school at age of 14, whilst after its implementationthis proportion dramatically decreased to below 10%.

This successful implementation was a result of a �national operation that expandedthe supply of teachers, buildings and furniture� (Oreopoulos, 2006). The proportion ofchildren immediately affected by this reform is particularly important when comparedwith similar US compulsory school changes used in the literature (Lleras-Muney, 2005)that affected only 5–10% of the relevant cohorts.

Age of school entry remained unchanged: children had to have started school by theterm in which they reached their fifth birthday.4 Finally, it is worth noting that thisincrease in compulsory schooling did not lead to identifiable formal qualifications for

0

0.2

0.4

0.6

0.8

1.0

1929 1933 1937 1929 1933 1937Frac

tion

Lea

ving

Ful

l−tim

e E

duca

tion

Quarter of Birth

Males Females

Fig. 1. Effect of 1947 Reform on Fraction Leaving Full-time Education at or Before Age 14

3 In Northern Ireland the change was not implemented until 1957.4 Indeed, a similar rule applied also for the age at school exit: students could leave school only at end of

the term in which they reached the minimum school-leaving age (14 before the reform, 15 after).



the cohort involved. At that time, children could not obtain formal higher schoolqualifications before the age of 17. As a consequence, children affected by the increasein compulsory schooling would still have had to stay for at least two further post-compulsory years of education in order to obtain a formal qualification.

A last important remark relates to the timing of the reform, in the context of themain identifying assumption that will allow us to identify the causal effect of educationon cognitive abilities, namely the absence of any other unobserved changes at the timeof the reform (or more precisely, to the cohorts treated by the reform at any point intheir lifetimes) that might also have affected cognitive abilities. Naturally, manyimportant events happened during that period that involve the cohorts of interest.They were born a few years after the Great Depression, and affected by rationing andbombing during WWII, but without being involved in fighting. However, exposure tothese circumstances was very similar for cohorts born on either side of the 1 April 1933cut-off (Clark and Royer, 2010) and we will be including flexible trend variablesthroughout our analysis to control for gradual changes across date of birth cohorts.Moreover, as in Jurges et al. (2009), we will also condition our estimates on adult heightto control for both economic and disease environment in childhood (Case and Paxson,2009). Finally, we take care to ground our estimation strategy on a narrow intervalaround the reform so as not to potentially confound the effect of the reform with thatof other unobservables.

2. Data and Summary Statistics

2.1. Data

Our data come from the first three waves (2002, 2004, 2006) of the ELSA, a multi-disciplinary survey of health, economic position and quality of life as people age. Itstarget population consists of people aged 50þ living in private households in Englandat baseline, plus their co-resident partners. The survey sample was drawnfrom respondents to the HSE. Around 12,000 respondents were recruited from threeseparate years (1998, 1999, 2001) of HSE.

The topic areas covered in the main questionnaire include individual and householdcharacteristics; physical and mental health, cognitive abilities and functioning, sub-jective psychological health and well-being, social participation and social support;housing, work, pensions, income and assets and expectations for the future. All dataare collected by face-to-face, computer-aided personal interviews, supplemented by aself-completion paper-and-pencil questionnaire that is left behind at the interview andsubsequently returned by respondents.

This last element is used to collect information on factors such as quality of life,psychosocial well-being, social participation, mobility, life satisfaction, perceived socialposition, social networks and social capital. Due to the survey design, not all individualsrespond to the self-completion questionnaire – in our sample we have a non-responserate of around 15%. From this questionnaire, we make use of a well-recognisedmeasure of quality of life, the CASP 19, and an index for social and cultural partici-pation. CASP 19 is an acronym for Control, Autonomy, Self-Realisation and Pleasureand it is a 19-item scale derived from questions about aspects of life that older adults



reported as important in qualitative studies. The index for social and cultural partici-pation is based on a selection of 8 questions about social and cultural activities.Appendix A gives more details on the construction of these two variables.

Our analysis uses different subsamples of the ELSA sample for our various empiricalspecifications, although we exclude all immigrants from the sample throughout ouranalysis. Firstly, we define subsamples according to birth cohort. We consider differentcohorts ranges, selecting from one year on either side of the cut-off date of 1 April 1933(i.e. those born from 1 April 1932 to 31 March 1934) to 10 years on either side. Theexact cohort range also depends on the estimation method in use.

Our second sample selection criterion is based on educational attainment. One fea-ture of our data is that education is recorded as the age at which the individual completedfull-time education, with the data being truncated from above and all values of 19 orhigher being grouped together as a single categorical value for 19 or more. Since we aremainly interested in the lower educated groups who will have been the ones affected bythe reform, we construct three different sample selections for analysis. The first is simplythe whole sample, regardless of what age they left education. A second subsample islimited just to those who left full-time education before the age of 19 (age left < 19). Inthis case we exclude from the sample all individuals with at least some college attainment,but still include many respondents that would have left school after the age of 15regardless of the reform (these are sometimes known as �always takers�).

The last and most restrictive education subsample excludes all individuals who leftfull-time education after the age of 15 (age left < 16). Since we can only estimate localaverage treatment effects and this sample should contain the biggest concentration of�compliers�, i.e. those that increase their educational attainment by one year only as aconsequence of the reform, this last group is the most important sample from the pointof view of our estimation strategy. The educational breakdown underlying these threesubsamples is shown in Table 1 which shows the distribution of age left education inour sample for the cohorts born between 1930 and 1936, split by sex and whether thecohorts were born before or after the reforms cut-off date. It is clear that the big changein educational attainment following the reform is from 14 to 15. This is particularly truefor males, where the fractions leaving school at older ages in the �after� cohorts are onlyincreased very slightly. The distribution of educational outcomes across the reform

Table 1

Per cent Distribution of Age Left Full-Time Education by Age and Date of Birth

Age left fte

Males Females

Before After Before After1/4/1930 –31/3/1933

1/4/1933 –31/3/1936

1/4/1930 –31/3/1933

1/4/1933 –31/3/1936

14 58.0 7.4 55.9 5.715 11.8 58.3 12.1 48.316–18 21.0 26.3 25.7 38.519þ 9.3 8.0 6.3 7.5

100.0 100.0 100.0 100.0

Notes. Individuals born three years either side of the cut-off date for the 1947 reform.



dates for women is slightly different with the reduction in the proportion leaving at age14 being accompanied by a large increase in the proportion leaving at age 15 but also anot insubstantial increase in the proportion of women leaving school between 16 and18. We return to this fact later in our discussion.

Some concern may arise with the use of education-restricted subsamples since theyare selected on the value of the endogenous variable. Such sample selection criterionhas, however, already been applied in the literature on the effects of the 1947 Britishcompulsory school reform (Oreopoulos, 2008; Lindeboom et al., 2009) because, asalready evident from Table 1, the reform mainly affected the educational choices ofthose individuals at the lower end of the educational distribution. Nevertheless,throughout the article we will provide evidence to show that such a stringent sampleselection criterion does not affect the validity of our estimation strategy. In particular,the robustness checks in Appendix B show that we cannot reject the hypothesis that theobserved predetermined characteristics of the people born just before and after thecut-off date are the same.

2.2. Cognitive Measures and Descriptive Statistics

The ELSA cognitive function module contains measures of cognitive function based onsimple tests of memory, word-finding ability, executive function, speed of processingand numerical ability. The memory assessment is subdivided into retrospective memory(recalling information that was learned previously) and prospective memory(remembering to carry out an intended action). The executive function tests refer to anumber of cognitive control processes, which include attention, initiation, mentalflexibility, organisation, abstraction, planning and problem solving. The test formatadopted by ELSA is based on the Telephone Interview of Cognitive Status-Modified testwhich utilises a format for the assessment of cognitive functions that can be adminis-tered in person or by telephone and is highly correlated with the Mini-Mental StateExam (MMSE) (Folstein et al., 1975), a screening tool frequently used by health-careproviders to assess overall brain function.

The tests are comparable to cognitive tests implemented in the HRS and in Survey ofHealth, Ageing and Retirement in Europe, and follow a protocol aimed at minimisingthe potential influences of the interviewer and the interview process.5 We exclude fromour analysis the tests of orientation in time and prospective memory because theyexhibit very little variability across respondents. We also exclude the numeracy test as itwas administered only in the first wave of the three waves of ELSA that we use here.

We will therefore evaluate the effect of the increase in compulsory school reform ontwo different cognitive domains: memory and executive functioning. The memory testsconsist of verbal registration and recall of a list of 10 words. The respondent hears thelist only once. The test is carried out immediately after the encoding phase (immediaterecall) and then again after the other cognitive questions have taken place (delayedrecall), usually a period of five or so minutes later. ELSA uses the same word lists as the

5 For instance in the word recall task the words are �read out� by the computer at prescribed intervals asopposed to by the interviewer who may be tempted to slow down, emphasise or repeat words according totheir perception of the demands of the respondent.



HRS in the US. In both studies there are four different wordlists so that different listscan be given to different members of the same household and to the same individualover time. Repeated exposure to the same tests, in fact, may induce learning effectswhich are likely to, if anything, improve the cognitive scores of some respondents overtime. From these two tests we calculate a Memory score as the sum of the number oftarget words recalled in the two recall phases (immediate and delayed). This score can,and does, range from 0 to 20.

Executive functioning is assessed using two different tests, namely verbal fluency andletter cancellation. The verbal fluency test is a test of how quickly participants can thinkof words from a particular category, in this case by counting how many distinct elementsfrom the animal kingdom (real or mythical, excluding repetitions or proper nouns) therespondent can name within one minute. This test requires self-initiated activity, orga-nisation and abstraction and set-shifting (Steel et al., 2003). Letter cancellation is a testof attention, visual search and mental speed. The participant is handed a clipboard witha page of random letters of the alphabet set out in rows and columns, and is asked tocross out as many target letters (P and W) as possible within one minute. The pagecomprises 26 rows and 30 columns, and there are 65 target letters in all. Respondentsare asked to work across and down the page as though they were reading and to performthe task both as quickly and as accurately as possible. After one minute they are asked tomark the point on the page where they stopped. The total number of letters searchedprovides a measure of speed of processing, whilst the number of target letters (P and W)missed by the respondent provides a measure of accuracy.

As in Steel et al. (2003), an executive function index has been derived from theverbal fluency and letter cancellation tests together. Our index is constructed bysumming the two standardised scores (each constructed by subtracting off their meanand dividing for the standard deviation). One attractive feature of the scores obtainedfrom both memory and executive function is the fact that they do not suffer from flooror ceiling effects that usually characterise other measures of cognitive functioning suchas the Mini-Mental State Examination (MMSE; de Jager et al., 2003). Table 2 presentsmeans and standard deviations of our test scores by age of leaving full-time educationand sex, for people born five years before and after the cut-off date of 1 April 1933. Thefirst set of rows reports these statistics for the full sample, while the second and thethird sets report the same statistics conditional on leaving school before 19 and 16 yearsold, respectively. Table 3 reports means comparison between treatment groups for ourcognitive and non-cognitive outcomes and other predetermined individual character-istics. We report these statistics for respondents born five years before and five yearsafter the cut-off date.

The first set of rows of Table 3 (age left < 19) reports the comparison of means forthose who left full-time education before the age of 19, while the second set (ageleft < 16) reports the same comparison for those who left before 16. The predeter-mined characteristics are childhood health (self-assessed by the responded) andfather’s last job. The third column for each sex reports p-values from t-tests on theequality of means. In both educational groups and for both sexes, these tests reject thenull of equality of means (at the 1% level) for both our cognitive test scores. Similarresults are apparent for our measure of social participation where, except for males inthe lower educational subsample, we reject the null of equality of means at least at



5% level. The quality of life measure (CASP 19), however, does not show significantdifferences between the two groups, except for females with higher educationalattainment. Finally, the characteristics we consider to be predetermined – fathers�occupation and respondents� childhood health – seem to be well balanced between the

Table 2

Mean and Standard Deviation of Test Scores by Sex and Age Left Full-time Education

Males Females

Mean SD Mean SD

Full sampleMemory 8.82 3.35 9.60 3.29Exec. func. �0.12 1.56 0.07 1.56N 3,441 4,024

Age left fte <19Memory 8.66 3.30 9.44 3.24Exec. func. �0.19 1.49 �0.01 1.53N 3,110 3,638

Age left fte <16Memory 8.16 3.21 9.01 3.21Exec. func. �0.40 1.40 �0.18 1.52N 2,280 2,528

Notes. We selected all individuals born five years before and after the cut-off date of 1 April 1933.

Table 3

Mean Test Scores Comparison for Those Born Five Years Before and After 1 April 1933, byEducational Attainment

Males Females

Before After p-value Before After p-value

Age left <19Memory 8.32 8.95 0.00 8.99 9.89 0.00Exec. func. �0.40 �0.00 0.00 �0.22 0.21 0.00Soc. part. 2.75 2.93 0.00 2.42 2.58 0.00CASP 19 42.25 42.30 0.88 41.76 42.66 0.00Child health 2.19 2.12 0.16 2.35 2.39 0.42Father job 2.64 2.64 0.93 2.62 2.57 0.14N 1,109 1,171 1,314 1,214

Age left <16Memory 7.87 8.43 0.00 8.65 9.41 0.00Exec. func. �0.59 �0.23 0.00 �0.38 0.04 0.00Soc. part. 2.57 2.66 0.15 2.20 2.31 0.06CASP 19 41.57 41.32 0.53 41.20 41.89 0.08Child health 2.26 2.21 0.34 2.45 2.39 0.28Father job 2.79 2.79 0.92 2.74 2.71 0.41N 1,109 1,171 1,314 1,214

Notes. The p-values are derived from t-tests on the equality of means. Social participation and CASP 19 aretaken from the self-completion questionnaire that shows a lower response rate with respect to the core sampleof about 15%. Social participation ranges between 0 and 8; CASP 19 ranges between 0 and 57; Child healthvalues: 1, excellent; 2, very good; 3, good; 4, fair; 5, poor; father job values: 1, professional and managerial; 2,skilled non-manual; 3, skilled manual; 4 unskilled manual.



two groups. This last finding is important for our analysis as differences would have castdoubt about the �continuity� hypothesis, the main assumption of our estimation strat-egy, as discussed in Section 3.2. However, this kind of comparison is purely descriptive,because it does not take account of cohort trends in such variables so we will return tothis test later when we estimate full models with control variables.

2.3. Graphical Analysis

To examine the effect of law change on educational attainment, we present a set ofdescriptive Figures that shows the relationship between birth cohort and differenteducational outcomes. Each point of each graph represents the sample mean for aparticular quarter of birth cell, with the overall sample covering the period five yearsbefore and after the cut-off date of 1 April 1933.

Purely for descriptive purposes, the fitted lines are based on a local linear fit on fiveyears before and after the reform. The vertical line denotes the cohort of birth cut-offfor the law change (second quarter of 1933). As discussed previously, the discontinuitypresented in Figure 1 on the fraction leaving full-time education by age 14 is clearlyevident for both males and females. Before the reform about 60% of the individuals leftfull-time education by age 14, whilst after the reform this fraction collapses to below10%. At the same time, however, the reform generated a small positive spillover tohigher levels of education. As discussed earlier, Figure 2 shows that the reform hadonly a small effect on the female fraction leaving full-time education before age 16, butno effect on this fraction for males.

The fact that the reform did not affect people with higher educational attainment iseven more clear in Figure 3 which shows no effect of the reform on the fraction leavingeducation before age 19 for both males and females. On the contrary, the discontinuityis amplified if we consider only people who left full-time education before the age of16 as in Figure 4. The jump at the discontinuity point is almost sharp, from about 80%to 10%. The effect of the reform on this subsample is particularly important because

0

0.2

0.4

0.6

0.8

1.0

1929 1933 1937 1929 1933 1937Frac

tion

Lea

ving

Ful

l−tim

e E

duca

tion

Quarter of Birth

Males Females

Fig. 2. Effect of 1947 Reform on Fraction Leaving Before Age 16



this subsample relates to the most affected people, i.e. those who, without the reform,would have been most likely to leave the school by age 14.

The second set of descriptive Figures show the discontinuity in the cognitive scores ofinterest. Figures 5 and 6 show the discontinuity in memory score conditional on leavingschool before the age of 16 and in the full sample, while Figures 7 and 8 show the samediscontinuities for the executive function score. All Figures show a very high variabilityin quarter of birth averages.

This high variability may be the results of different factors. First, it may be due to asmall number of observations per cell (an average of 36 observations for each month ofbirth). Second, as explained in Section 1.2, ages at school entry and exit vary accordingto a set of rules depending on date of birth (Clark and Royer, 2010). These rulesgenerate a lot of variability in the total months spent at school within each cohort but

1929 1933 1937 1929 1933 1937Frac

tion

Lea

ving

Ful

l−tim

e E

duca

tion

Quarter of Birth

0

0.2

0.4

0.6

0.8

1.0

Males Females

Fig. 3. Effect of 1947 Reform on Fraction Leaving Before Age 19

1929 1933 1937 1929 1933 1937Frac

tion

Lea

ving

Ful

l−tim

e E

duca

tion

Quarter of Birth

0

0.2

0.4

0.6

0.8

1.0

Males Females

Fig. 4. Effect of 1947 Reform on Fraction Leaving Before Age 14 (Conditional on Leaving Before 16)



do not affect the validity of our estimation strategy, because the rules themselves didnot change with the compulsory school reform of 1947. Finally, we could have aselection effect due to differential mortality rates, particularly for the older cohort. Thisissue is discussed in more detail in Section 3.2 but it is clear that this selection effect willbecome less important as our estimation strategy focuses on tighter and tighter inter-vals around the discontinuity.

The descriptive analysis presented in Figures 5 and 6 suggests that, even though lessimmediately evident, the discontinuity in memory, especially for males follows the samepatterns that we have seen in the educational Figures. The effect on memory for malesis evident only conditional on leaving before the age of 16, while there are somepositive spillover also for females with higher educational attainment. This consistencybetween the discontinuity in education and cognitive abilities is important becausedifferent evidence would have cast doubt on the unconfoundedness hypothesis. In the

7

8

9

10

1929 1933 1937 1929 1933 1937

Ave

rage

Rec

all S

core

Quarter of Birth

Males Females

Fig. 5. Effect of 1947 Reform on Memory (Conditional on Leaving Before 16)

7

8

9

10

1929 1933 1937 1929 1933 1937

Ave

rage

Rec

all S

core

Quarter of Birth

Males Females

Fig. 6. Effect of 1947 Reform on Memory (Full Sample)



case of executive function, although the fitted lines in Figures 7 and 8 show discon-tinuities in this test very similar to those in memory, they are less convincing due to thehigh variability in quarter of birth averages. For this reason, in Figure 9 we showthe same discontinuities in executive function as in Figure 7, but reporting annualyear-of-birth averages on a 20-year interval. Although the variability across cohorts inexecutive function averages, the discontinuity for males conditional on leaving before16 is now more apparent.

Finally, we note that even using a higher order polynomial fitting or using a year-of-birth instead of quarter-of-birth level of aggregation does not change the messagefrom the graphical evidence. In order to save space this analysis is not presented.Instead we move on to our full empirical models with a more complete set of controlvariables and specification tests.

−1.5

−1.0

−0.5

0

0.5

1929 1933 1937 1929 1933 1937

Exe

cutiv

e Fu

nctio

ning

Quarter of Birth

Males Females

Fig. 7. Effect of 1947 Reform on Executive Functioning (Conditional on Leaving Before 16)

−1.0

−0.5

0

0.5

1929 1933 1937 1929 1933 1937

Exe

cutiv

e Fu

nctio

ning

Quarter of Birth

Males Females

Fig. 8. Effect of 1947 Reform on Executive Functioning (Full Sample)



3. Empirical Strategy

3.1. Regression Discontinuity Design

The nature of the reform clearly makes it a candidate for a regression discontinuity(RD) design providing us the opportunity to estimate the effect of one more year ofschooling on old age cognitive abilities under relative weak conditions that we discussin the next subsection. The general idea in RD design is that the probability ofreceiving a treatment (an additional year of schooling) is a discontinuous function of acontinuous treatment determining variable (day of birth). However, the treatment inour case does not change from 0 to 1 at the cut-off point (1 April 1933). FollowingImbens and Angrist (1994), we have people that, regardless of the reform, decide tostay at school also over the minimum compulsory school-leaving age (�always-takers�).There are also a few people that, regardless of the reform, leave the school before theminimum compulsory age (�never takers�). In such case, the FRD design is appropriatebecause it allows for a smaller jump in the probability of assignment to treatment at thecut-off. In the case of a binary treatment FRD design may be seen as a Wald estimator(around the discontinuity c):

sFRD ¼limx#c EðY jX ¼ xÞ � limx"c EðY jX ¼ xÞ

limx#c EðW jX ¼ xÞ � limx"c EðW jX ¼ xÞ ;

where, in our case, c is the cut-off point; X is the date of birth; W is the treatment (onemore year of education). Specifically, we estimate the following two equations:

Yics ¼ a0 þ a1Eics þ f ðRicÞ þ X 0icsa2 þ uics ; ð1Þ

Eics ¼ c0 þ c1Zc þ g ðRicÞ þ X 0icsc2 þ mics ; ð2Þ

where Yics and Eics are the cognitive scores and the educational level of the individual i,of the cohort c, in the survey year s; Z is a dummy variable to capture whether the

10

11

12

13

1923 1928 1933 1938 1923 1928 1933 1938

Exe

cutiv

e Fu

nctio

ning

Cohort

Males Females

Fig. 9. Effect of 1947 Reform on Executive Functioning (Conditional on Leaving Before 16)



individual is born after the cut-off date, i.e. equal to 1 if the individual is born after 1April 1933 and 0 otherwise; the running variable R is an individual birth cohort(measured in months) relative to the cut-off; the vector X contains predeterminedcharacteristics such as survey year and adult height. Functions f(Æ) and g(Æ) capture therelationship between birth cohort and cognitive outcome and educational attainmentrespectively. Notice that substituting the treatment equation into the outcomeequation yields the reduced form:

Yics ¼ b0 þ b1Zc þ hðRicÞ þ X 0icsb2 þ �ics ; ð3Þ

where b1 ¼ a1 � c1. The parameter of interest is a1 and its estimate is the ratio of thereduced form coefficients b1/c1.

We estimate the parameter of interest a1 using two different methods as suggested byLee and Lemieux (2009). The first is based on a local linear regression around thediscontinuity choosing the optimal bandwidth in a cross-validation procedure that wereport in Appendix C. The second method makes use of the full sample6 using apolynomial regression in which the equivalent of the bandwidth choice is the choice ofthe correct polynomial order (Appendix D). In both cases, we estimate the treatmenteffect using 2SLS which is numerically equivalent to computing the ratio in the esti-mated jump (at the cut-off point) in the outcome variable over the jump in thetreatment variable, provided that the same bandwidth or the same polynomial order isused for both equations. This allows us to obtain directly the correct standard errorsthat are robust and clustered at the individual level.

Controlling for clustering is particularly important in this setting because we havetwo possible sources of serial correlation, within individuals over time and acrossindividuals in the same month of birth.7 The first best in this case would be clusteringat the higher level of aggregation that corresponds to the month of birth level. But inthis case the number of clusters would be too small, particularly when we focus ouranalysis on a very small bandwidth around the discontinuity. For this reason we controlfor the larger source of correlation that is across the same individual over time.8 Lastly,although no less importantly, we fully interact the polynomials f(Æ) and g(Æ). Otherwise,we are imposing the restriction that the slope coefficients are the same on both sides ofthe discontinuity point.

One final estimation issue is the potential effect of panel attrition on our estimators.In an ageing survey like ELSA, panel attrition may be an important concern dependingon the selection mechanism that determines ongoing participation in the panel. In oursample, some individuals are observed three times (62%), others twice (19%) andothers only once (19%). One way of dealing with potential attrition would be to useweights based on the inverse of the number of times people are observed. Althoughsimple, this method should be highly inefficient because gives the same weight to all

6 In reality, we restrict the sample to 10 years before and after the reform because we have few observationsfor cohorts before the 1923.

7 The discreteness of our treatment determining variable (month of birth) can introduce a commoncomponent of variance for all the observations at any given value of this variable (Lee and Card, 2008).

8 When we do cluster at the month of birth level in specifications with large enough bandwidth to supportsuch a specification the standard errors decrease and we always obtain significant results for males. For thisreason we prefer to be conservative and use the individual level clustering in the article.



individuals observed the same number of times. Alternatively, if one were to assume amissing at random (MAR) selection mechanism (Rubin, 1976), inverse probabilityweights could be calculated based on the estimated probability of participating in thesecond and then third waves conditional on observable baseline controls. Neithermethod is particularly satisfactory, nor are there, in the absence of further informationor assumptions on the survey participation process, particular good criteria forchoosing one over the other or for that matter over an unweighted strategy. Never-theless, we experimented with both weighting methods (with the observable variablesin the MAR case being defined as sex, cubic polynomial in age, education and height).In both cases, the results (available from the authors on request) revealed similarcoefficients (albeit with a loss of precision, particularly, as expected, when we use theformer weighting strategy). As a consequence we simply present estimates here that donot account for attrition, essentially assuming a missing completely at random selectionmechanism (Rubin, 1976).

3.2. Identification Issues

The attractive feature of the RD estimation strategy is that it provide estimates that are �ascredible as those from randomized experiment� (Lee and Card, 2008) under relativelyweak assumptions. The key assumption here is that the conditional expectations ofthe potential outcomes (age left full-time education and cognitive scores) with respect tothe treatment determining variable (birth cohort) are smooth (continuous) functions atthe threshold (R ¼ 0). This allows us to attribute any discontinuity in the outcomes ofinterest at the threshold only to the effect of the reform. As with any identificationassumption this is directly untestable but, as common in the literature (Lee and Lemi-eux, 2009), we can employ some indirect tests. First, we can test whether there arediscontinuities in predetermined characteristics for which we have data, but which areknown not to have been affected by the treatment. We have already seen in Table 3 thatthe comparison of means of predetermined characteristics such as childhood health andfather’s last job does not reject the null hypothesis of equal means. We therefore testedthe assumption of zero effects on these predetermined characteristics using the sameestimation strategy used for estimating the treatment effect on cognitive test scores. Aswith the previous comparison of means, the results, reported in Appendix B, do notreject the null of zero effects of the reform on these variables.

Perhaps more importantly, since our population is made up of older individualswhose cognitive abilities are assessed long after the reform took place, the main con-cern about this assumption regards a possible selection effect due to subsequentmortality. This selection effect could have two different sources. The first is thedifferential in mortality rates between cohorts on the two sides of the discontinuity. Inparticular, older cohorts (i.e. on the left-hand side) could be more affected by mortalitybetween the time of the reform and the time our outcome variables were observed (i.e.2002–6). However, focusing our estimation on a narrow interval around the disconti-nuity or conditioning for higher order polynomials of date of birth (when we increasethe bandwidth) should allow us to control for the broad cohort pattern of age-specificmortality rates rather well, and discontinuities are unlikely to remain after these con-trols. Moreover, it is reasonable to assume that this selection mechanism is likely to



affect mainly people with poor health and poor cognitive abilities (i.e. any selectionwould be a positive selection on survival). Since mortality is greater amongst the oldercohorts on the left side of the discontinuity this implies that any estimated effect ofeducation on cognitive abilities would, if anything, most likely be a downward biasedestimate of the true effect.

The second concern about mortality is due to the possible existence of a causal effectof the reform itself (through education) on mortality. However, this second concernwas tested directly in the analysis of Clark and Royer (2010) who looked at the effect ofthe 1947 reform on mortality in detail. They find that, in line with similar results forphysical health, the compulsory school reform had little or no causal effect on mortality.

A final set of robustness tests for the validity of our RD design involves estimatingjumps in outcomes at points where there should be no jumps in the treatment distri-bution. The results, also reported in Appendix B, do not show any evidence for thepresence of jumps in the distribution of the treatment variable in the two subsampleson either side of the cut-off value.

4. Estimation Results

We begin this Section by showing the estimated effect of the reform on schooling usinglocal linear regression. In Appendix C we discuss the cross-validation procedure sug-gested by Imbens and Lemieux (2008) for choosing the optimal bandwidth. Thisprocedure results in an optimal bandwidth that is calculated to be one year (on bothsides of the discontinuity) for our cognitive test scores and three years for education.For this reason, in the following Table we explore the sensitivity of the results to a rangeof bandwidths that goes from one to three years around the discontinuity.

Table 4 shows the estimated effect of the compulsory school reform on school-leaving age conditional on three different samples of educational attainment and threedifferent bandwidths h.

The last row for each sample selection reports the F-test on the excluded instru-ment – the dummy variable indicating the effect of the reform. The first set of rows inthis Table shows the estimated effects for the full sample, where dependent variable isthe age of left full-time education as recorded in ELSA. Such estimates present twomain problems. Firstly, this variable is truncated from above (at age 19). Second, ityields the average effect of the reform across all responders including those with highereducational attainment. Consistent with the result in Lindeboom et al. (2009), theestimated effect of the reform is very poor in this sample. Except for females in thelarger bandwidth specification, in fact, the coefficients are not significantly differentfrom zero.

The second set of rows of Table 4 uses the same model specification but the esti-mation sample excludes people who left full-time education at or after the age of 19.That is, it excludes all individuals with at least some college attainment but it stillincludes many respondents that, regardless of the reform, would leave the schoolafter the age of 15 (the �always takers�). In this case, if we look at the smallest bandwidthh ¼ 1, the estimated effect of the reform is significant only for females. This result isconsistent with Table 1 and Figure 2. Finally, the third set of rows shows the results forthe most concentrated sample, which includes only individuals who left full-time



education before the age of 16. This sample is the most important for our estimationstrategy, because it should contain the biggest fraction of �compliers�, i.e. those whoincrease their educational attainment by one year as a consequence of the reform. Forthis sample, the effect of the reform is large and statistically significant at 1% level foreach bandwidth and for both males and females.

The next step is to evaluate the effect of the exogenous increase in education oncognitive outcomes of interest. Table 5 reports estimates of the education effect oncognitive abilities. All test scores have been standardised by subtracting off their meanand dividing by their standard deviation. We make use of the 2SLS estimator in order toobtain directly the correct standard errors, robust to heteroscedasticity and clustered atthe individual level. The first set of rows shows the estimated education effect for thesample leaving school at or before the age of 16 (that corresponds to the first step inthe third row of Table 4), while the second set shows the estimated coefficients con-ditional on the broader sample including those leaving school up to age 19. We do notreport the results for the full sample because of the weak first step as evident from theF-tests reported in Table 4.

The effect of education on memory seems to be positive for both males and femalesin the smallest sample. However, the standard errors for the female sample are largerand so the corresponding coefficients are significant only at the 10% level when weconsider two or three years around the discontinuity. The results are quite different forexecutive functioning, where the coefficients are statistically significant (at least at the10% level) only for males.

Table 4

Estimated Impact of 1947 Reform on School-leaving Age, by Sex (Local Linear Regression)

Full sample

Males Females

h ¼ 1 h ¼ 2 h ¼ 3 h ¼ 1 h ¼ 2 h ¼ 3

1947 Reform 0.340 0.446 0.136 0.186 0.592* 1.256***(0.598) (0.419) (0.355) (0.463) (0.335) (0.307)

N 703 1,385 2,057 777 1,559 2,369F-test 0.36 1.36 0.12 0.17 2.61 15.14

Age < 191947 reform 0.220 0.440** 0.346** 0.873*** 0.668*** 0.708***

(0.280) (0.204) (0.168) (0.232) (0.174) (0.146)N 636 1,258 1,860 718 1,424 2,163F-test 0.46 3.95 4.33 10.90 11.97 21.00

Age < 161947 reform 0.641*** 0.694*** 0.672*** 0.595*** 0.546*** 0.636***

(0.110) (0.077) (0.062) (0.109) (0.077) (0.063)N 431 928 1,400 491 968 1,435F-test 31.02 76.59 111.75 21.00 49.63 100.03

Notes. Significance levels: * p-values between 10 and 5%. ** p-values between 5 and 1%. *** p-values less than1%. Table reports estimated effects of compulsory school reform on schooling. Columns denote the band-width selection h from one to three years. Rows indicate three different sample selections: full sample;conditional on leaving before the age of 19; conditional on leaving before the age of 16. All regressionsinclude: a linear function of month of birth and its interaction with the reform dummy; controls for adultheight and for survey year. The standard error in parenthesis are robust to heteroscedasticity and clustered atthe individual level.



With regard to the magnitudes of these effects, the effect of education on memory isabout half of a standard deviation for males and around 0.4 for females. The effect onexecutive function for males ranges between 0.37 and 0.63 of the standard deviation.9

When we include individuals with higher level of education attainment in the sample,as in the second set of rows (age left < 19), the sign and in some case also the mag-nitude of our coefficients are similar but the estimated standard errors increase inparticular for males. For males, the inclusion of respondents with higher level ofeducational attainment only increases the standard errors of our estimates. This meansthat there are no gains in increasing the sample size because there are too few malesaffected by the reform who left full time after the age of 16 as already evident in thegraphical analysis in Section 2.3.

To evaluate the robustness of our results further, Tables 6(a) and 6(b) report theestimated treatment effect of education on cognitive abilities using polynomialregression instead of the local linear framework above. We present the resultsaccording to different polynomial orders k and bandwidths h. In the smallest sample(age left education < 16), the Table shows significant coefficients on memory test inparticular for males until the fourth order polynomial. Moreover, the size of thecoefficients are around half their standard deviation, as before, particularly when welook at the main diagonal where we gradually increase the bandwidth and the poly-nomial order. Consistent with the local linear estimates, we have significant coefficientson executive function only for males. But if we also consider higher levels of educationattainment (conditional on leaving before 19), we do not find significant effects ofeducation, although in most cases the coefficient are similar in size (in particular if we

Table 5

2SLS Estimates of the Effect of Education on Cognitive Abilities

Males Females

h ¼ 1 h ¼ 2 h ¼ 3 h ¼ 1 h ¼ 2 h ¼ 3

Age < 16Memory 0.597* 0.511** 0.434** 0.512 0.521* 0.352*

(0.346) (0.227) (0.187) (0.341) (0.274) (0.193)Exec. func. 0.635* 0.547** 0.371** �0.100 0.020 0.093

(0.357) (0.223) (0.185) (0.389) (0.300) (0.210)N 431 928 1,400 491 968 1,435

Age < 19Memory 0.504 0.267 0.174 0.359* 0.213 0.220

(0.872) (0.299) (0.309) (0.214) (0.190) (0.147)Exec. func. 1.085 0.512 0.236 �0.052 �0.047 0.008

(1.470) (0.327) (0.309) (0.229) (0.207) (0.160)N 636 1,258 1,860 718 1,424 2,163

Notes. Significance levels: *p-values between 10 and 5%. **p-values between 5 and 1%. ***p-values less than1%. Table reports 2SLS estimates of the effect of schooling on cognitive test scores. Columns denote thebandwidth selection h from one to three years. Rows indicate two different sample selection: conditional onleaving before the age of 19; conditional on leaving before the age of 16. All regressions include: a linearfunction of month of birth and its interaction with the reform dummy; controls for adult height and for surveyyear. The standard error in parenthesis are robust to heteroscedasticity and clustered at the individual level.

9 When we use different methods of construction of the executive function index the coefficient are verysimilar but the standard errors are usually greater.



Table 6(a)

Polynomial Regression Estimates of the Education Effect on Cognitive Test Scores(Age Left < 16)

Age < 16 Males Females

Memory

Pol. order h ¼ 5 h ¼ 8 h ¼ 10 h ¼ 5 h ¼ 8 h ¼ 10

k ¼ 2 0.491** 0.336* 0.266 0.463** 0.272 0.230(0.221) (0.181) (0.162) (0.227) (0.170) (0.157)

k ¼ 3 0.560* 0.586** 0.516** 0.640* 0.543** 0.425**(0.286) (0.238) (0.217) (0.360) (0.266) (0.214)

k ¼ 4 0.543 0.582** 0.576** 0.658 0.685** 0.582*(0.389) (0.283) (0.257) (0.411) (0.330) (0.303)

Exec. func.k ¼ 2 0.391* 0.112 0.228 0.039 0.112 0.209

(0.217) (0.177) (0.161) (0.250) (0.180) (0.166)k ¼ 3 0.762*** 0.484** 0.238 �0.052 0.099 0.081

(0.295) (0.232) (0.210) (0.398) (0.288) (0.231)k ¼ 4 0.412 0.682** 0.584** �0.166 �0.124 �0.034

(0.395) (0.284) (0.256) (0.467) (0.362) (0.335)

N 2,280 3,430 4,126 2,528 3,837 4,629

Table 6(b)

Polynomial Regression Estimates of the Education Effect on Cognitive Test Scores(Age Left < 19)

Age < 19 Males Females

Memory

Pol. order h ¼ 5 h ¼ 8 h ¼ 10 h ¼ 5 h ¼ 8 h ¼ 10

k ¼ 2 0.414 0.017 �0.059 0.294 0.155 0.159(0.629) (0.235) (0.228) (0.182) (0.122) (0.108)

k ¼ 3 0.242 0.565 0.283 0.270 0.294 0.228(0.384) (0.691) (0.381) (0.189) (0.204) (0.164)

k ¼ 4 0.090 0.326 0.427 0.357 0.366* 0.308(0.523) (0.494) (0.579) (0.218) (0.208) (0.210)

Exec. func.k ¼ 2 0.136 �0.036 0.059 0.008 0.053 0.109

(0.629) (0.238) (0.215) (0.196) (0.129) (0.114)k ¼ 3 0.754 0.425 0.050 �0.086 0.013 0.024

(0.522) (0.675) (0.395) (0.210) (0.218) (0.178)k ¼ 4 0.457 0.719 0.559 �0.132 �0.129 �0.088

(0.586) (0.660) (0.666) (0.239) (0.224) (0.231)

N 3,110 4,720 5,692 3,638 5,546 6,809

Notes. Significance levels: *p-values between 10 and 5%. **p-values between 5 and 1%. ***p-values less than1%. Tables report the 2SLS estimates of the effect of schooling on cognitive test scores using polynomialregression. Columns denote the bandwidth selection h: 5, 8 and 10 years. Inside each sample selection (as in kfrom 2 to 4. All regressions include: a polynomial function of month of birth (of order k) and its interactionwith the reform dummy; controls for adult height and for survey year. The standard error in parenthesis arerobust to heteroscedasticity and clustered at the individual level.



look at the main diagonal of the two Tables). As before, standard errors are larger forfemales, with coefficients in many cases significant only at the 10% level. On balance, theestimated effects of education on cognitive abilities seem to be robust across specifica-tions and for different estimation methods, particularly for the case of memory.

Having estimated the impact of reform on cognitive abilities, the final step of ouranalysis is to evaluate the effect of the same reform on two measures of social parti-cipation and quality of life (CASP 19), each standardised in the same manner as thecognitive function scores. Table 7 reports estimates of the education effect on thesetwo measures using local linear regression method as in Table 5. For completeness,Figures 10 and 11 also provide a graphical analysis of the discontinuities in each of thetwo measures in the same way as was originally presented in Section 2.3 for the cog-nitive measures.

Table 7 shows a positive but weak effect of the increase in education on our measureof social participation for males in the low educational sample but not for females.These results are statistically significant at least at the 10% level only in the lowereducational attainment group when we consider three years before and after the reformimplementation. When we look at the effect of education on quality of life, however,find negative although not statistically significant effects for both males and females.10

Table 7

2SLS Estimates of the Effect of Education on Social Participation and Quality of Life

Males Females

h ¼ 1 h ¼ 2 h ¼ 3 h ¼ 1 h ¼ 2 h ¼ 3

Age < 16Soc. part. 0.484 0.300 0.377* 0.230 �0.141 �0.129

(0.413) (0.263) (0.219) (0.360) (0.313) (0.229)CASP 19 �0.365 �0.011 �0.073 �0.468 �0.468 �0.029

(0.442) (0.289) (0.236) (0.506) (0.388) (0.277)N 393 835 1,237 406 808 1,191

Age < 19Soc. part. 1.136 0.342 0.564 �0.110 �0.564 �0.331

(1.915) (0.445) (0.453) (0.282) (0.389) (0.252)CASP 19 �2.406 �0.372 �0.343 �0.209 �0.252 �0.070

(4.265) (0.499) (0.452) (0.278) (0.280) (0.204)N 583 1,135 1,664 622 1,241 1,883

Notes. Significance levels: *p-values between 10 and 5%. **p-values between 5 and 1%. ***p-values less than1%. Table reports 2SLS estimates of the effect of schooling on social participation and a subjective measure ofquality of life (CASP 19). Columns denote the bandwidth selection h from one to three years. Rows indicatetwo different sample selection: conditional on leaving before the age of 19; conditional on leaving before theage of 16. All regressions include: a linear function of month of birth and its interaction with the reformdummy; controls for adult height and for survey year. The standard error in parenthesis are robust toheteroscedasticity and clustered at the individual level.

10 Since the social participation variables come from the self-completion component of the ELSA instru-ment there is a concern that non-response patterns to this element of the survey may affect our estimates. Inorder to verify this we performed the same estimation of the effect of education on the cognitive measures inTable 5 using just the subsample of respondent to self-completion questionnaire. The results, not reported toconserve space, do show differences for females. In particular, the estimated effect of education on memory isno longer statistically significant which may, in turn, explain why we do not find evidence of social partici-pation mechanism for females in this sample.



5. Conclusions

In this article, we use data from three waves of the ELSA to estimate the causal effect ofeducation on cognitive abilities using the 1947 increase in compulsory school-leavingage that took place in Britain. This school reform had dramatic effects on educationalattainment on a big fraction (around 50%) of the population just after the cut-off pointof 1 April 1947. At the same time this reform shows very small spillover on people withhigher level of educational attainment, particularly for males.

We use a FRD design to estimate the causal effect on the additional year of educationinduced by this policy change. The results show a positive and significant causal effecton old age memory of less-educated people. These results confirm similar findings inGlymour et al. (2008) that found an effect of about 0.33 standard deviation on memory

2.0

2.5

3.0

3.5

1929 1933 1937 1929 1933 1937Cohort

Males Females

Fig. 10. Effect of 1947 Reform on Social Participation (Conditional on Leaving Before 16)

35

40

45

1929 1933 1937 1929 1933 1937Cohort

Males Females

Fig. 11. Effect of 1947 Reform on CASP19 (Conditional on Leaving Before 16)



using compulsory school changes in the US. We found also a positive effect of thereform on males executive function ability measured using an index based on theverbal fluency and letter cancellation tests. These findings seem to be robust to anumber of different specifications and methods of estimation.

Whilst some concern may be raised about the fact that our outcome variables areobserved at older ages and as such differential mortality patterns of various cohorts maybe driving our results, we have argued that our particular econometric method –focusing as it does on discontinuities at the treatment date – is robust to such issuesand, if anything, we may be underestimating the true effect given a plausible signing ofany possible bias. In addition, our full set of date-of-birth and year controls are flexibleenough to adequately capture any broader age-related decline in cognitive abilities thatwill undoubtedly be present in our sample.

In addition to our analysis, we have discussed the possible mechanisms by whicheducation might be thought to affect cognitive abilities at old age. Taking our evidencetogether with the important evidence from other studies on the effect of this reform onother outcomes (Oreopoulos, 2006; Jurges et al., 2009; Clark and Royer, 2010) it seemspossible to say that these effects do not come about via changes to health or mortality.Instead, one needs to look for channels involving earnings (where the reform did havea significant causal effect). Two possibilities emerge. One is that greater earnings andincomes that resulted from the reform have enabled individuals to engage in greatersocial and cultural participation over their life-course (such as membership of clubsand societies, attendance at events and museums etc.), which in turn have staved offage-related cognitive decline. Our analysis provides some weak evidence for the exis-tence of this channel. But given the strength of our main findings, it seems morenatural to conclude that the other possibility is equally if not more important, i.e.increased earnings and incomes from the reform are reflective of either higheremployment or more cognitively demanding and productive occupations whichthemselves have positive implications for life-course trajectories of cognitive function.This would also be consistent with the recent article of Devereux and Hart (2010) thatshows positive financial returns from the same reform only for males and consistentwith the lifetime labour market patterns for these cohorts born in the 1930s that showlower female labour force participation. In order to definitely confirm the importanceof the employment channel one would want to either consider split samples where therelationship between job characteristics and cognitive demands may vary (for example,by occupation or skill group) or to look jointly at life-cycle earnings and cognition. Inthe former cases, we do not have sufficient samples sizes to facilitate a split-sampleanalysis. In the latter, the data currently available only relate to respondents at olderages, mainly when they are already retired. A natural extension of this work, however,would be to exploit the potential of linking ELSA respondents to their NationalInsurance record data in order to investigate life-time labour market patterns and life-time earnings.

The issue of the particular mechanisms through which the effects are transmitted isparticular important given the rather large magnitudes of the effects we estimate in thedata, around half of one standard deviation for one additional year of schooling. Onereasonable explanation for such a magnitude might be diminishing marginal returns toschool inputs – our estimators focus on the effects of the reform on those affected,



which are only those in the lower tail of the education distribution. Whether or notsuch large effects would be found for a reform targeted at a different group, or whetherthe same mechanisms would apply, is not something that we can address with this dataand methodology.

Nevertheless, our findings do add new evidence to that on the evaluation of com-pulsory school laws which continue to exist and are frequently updated in everydeveloped country. Moreover, the evidence is important for broader issues surround-ing the effects of education on old age cognitive abilities which is becoming especiallyimportant in an ageing society where preventing or delaying the age-related declinein physical and cognitive abilities is becoming a fundamental target for health, labourand fiscal policy.

Appendix A. Measure of Quality of Life (CASP19) and Social and CulturalParticipation

The questions in the self-completion questionnaire ask about the respondents� quality of life,social participation and social networks and the respondents� mental and psychosocial health.From this questionnaire, we construct two indexes that we use in our analysis: CASP 19 and socialparticipation.

The CASP 19 is a theoretically grounded measure of quality of life consisting of 19-Likertscaled agreement items spanning four life domains: control, autonomy, self-realisation andpleasure. Each life domain contains four or five items which are presented as statements to ELSArespondents in the self-completion questionnaire. Each statement is assessed in a 4-point Likertscale as to the extent to which the description describes a personal feelings about their life (ratedas this applies to me: often, sometimes, not often or never) applies to the respondent. Theresulting scale scores are summed to form an index of quality of life where a high score indicates�good� quality of life. The range of the scale is from 0, which represents a complete absence ofquality of life, to 57, which represents total satisfaction of all four domains. In our sample theachieved range goes from 7 to 57. The original scale was developed in the context of a postalfollow-up to members of the Boyd-Orr sample in 2000 (Hyde et al., 2003). A complete evaluationof the psychometric properties of this measure in terms of internal consistency and reliability wasmade by Wiggins et al. (2008).

The social participation index is based on a selection of eight questions from two set ofquestions intended to measure the social and cultural engagement of the respondent. Weselect from these questions those activities that should be more cognitive demanding. The firstset of questions is presented as statements that may apply or not to the respondent. From thisset we select the following ones: I read daily newspaper; I have a hobby or pastime; I useinternet and/or email. The second set of question asks the respondent whether or not he is amember of any of organisations, clubs or societies. From this second set, we select the followingones: political party, trade union or environmental groups; tenants groups, resident groups,Neighbourhood Watch; education, art or music groups or evening classes; social clubs; anyother organisations, club or societies. The index is composed summing all the activities ormembership in which the respondent reports to be involved. As a consequence the indexranges from 0 to 8.

Appendix B. Identification Tests

In this Section, we report the results from two different tests that we perform to verify the validityof our RD design. The first test verifies whether there are discontinuity in predetermined



characteristics for which we have data, known not to be affected by the treatment. This test isparticularly important, because in the presence of other discontinuities, the estimated effect maybe attributed erroneously to the treatment of interest. Specifically, we tested the assumption ofzero effects on father’s last occupation and self-reported childhood health, using the sameestimation strategy performed for estimating the treatment effect on cognitive test scores.Table B1 reports the education effect on these two variables using a local linear regressionapproach around the discontinuity using only the first wave, since there is no time variation inthose variables. As shown also in Table 3, the results do not show significant differences in thetwo groups, rejecting the hypothesis of the presence of discontinuity in the observed predeter-mined characteristics. Moreover, this test should overcome most of the concern about the validityof our sample selection based on values of the endogenous variable. The results, in fact, show thatin both the samples the observed predetermined characteristics are the same just before andafter the cut-off.

A second test for the validity of our RD design involves estimating jumps at points where thereshould be no jumps in the treatment distribution. As suggested by Imbens and Lemieux (2008),we test for jumps at the median value of the two subsamples on either side of the cut-off value.Specifically, we test for the presence of jumps five year before and after the cut-off date of 1 April1933. Table B2 reports the results of this test. For each sex, each column reports the estimatedcoefficient of a dummy variable on that identifies cohorts born after one of the two �virtual� cut-off point, namely 1928 and 1938. All regressions include a linear function of month of birth andits interaction with the non-discontinuity dummy, controls for adult height and for survey year.As expected, the results does not show any significant coefficients.

Table B1

2SLS Estimates of the Effect of Education on Predetermined Characteristics

Males Females

h ¼ 1 h ¼ 2 h ¼ 3 h ¼ 1 h ¼ 2 h ¼ 3

Age < 16Father job 0.684 �0.124 0.059 �0.179 0.333 �0.022

(0.547) (0.319) (0.259) (0.524) (0.384) (0.263)Child health 0.537 �0.105 0.020 0.342 �0.007 �0.242

(0.611) (0.408) (0.333) (0.551) (0.426) (0.328)N 165 356 542 183 365 534

Age <19Father job 1.323 �0.300 0.189 0.007 0.362 0.075

(1.803) (0.494) (0.534) (0.313) (0.308) (0.217)Child health �5.236 �1.616 �0.591 0.268 0.091 0.028

(49.677) (3.046) (1.079) (0.388) (0.347) (0.229)N 237 478 713 266 531 795

Notes. Significance levels: *p-values between 10 and 5%. **p-values between 5 and 1%. ***p-values less than1%. Table reports 2SLS estimates of the effect of schooling on father’s occupation when the respondent was14 and self-reported childhood health. Columns denote the bandwidth selection h from one to three years.Rows indicate two different sample selection: conditional on leaving before the age of 19; conditional onleaving before the age of 16. All regressions include: a linear function of month of birth and its interactionwith the reform dummy; a control for adult height. The standard error in parenthesis are robust toheteroscedasticity.



Appendix C. Cross-Validation Procedure

The optimal bandwidth is chosen with a �leave one out� procedure proposed by Imbens andLemieux (2008). Basically, for each observation i on the left of the cut-off point, we run a linearregression using only observation with value of X (the treatment determining variable) on the leftof Xi (Xi � h � X < Xi), while for observation on the right of the cut-off point we use only thoseon the right of Xi (Xi � X < Xi þ h). We repeat this procedure for each i in order to obtain thewhole set of predicted value of Y that can be compared with the actual value of Y. Formally, thecross-validation criterion is defined as

CVY ðhÞ ¼1

N

XNh

i¼1

fYðiÞ � Y ½XðiÞ�g2;

where Y ½XðiÞ� represents the predicted value of Y using the above described regression. Theoptimal bandwidth is that value of h that minimises the criterion function. In our case we have toperform this procedure three times: one for the first stage regression, and two for the twocognitive outcome of interest. However, Imbens and Lemieux (2008) suggest to use samebandwidth for both outcome and treatment equation and use the smallest bandwidth selected bythe cross-validation procedures. To avoid problem with seasonality in month of birth we apply thecross-validation procedure only on bandwidths equal to multiples of year of birth, from 1 to10 years before and after the cut-off point. Results of this procedure, which we do not report toconserve space, suggest that except for females� executive function (where the optimal bandwidthis two years), the optimal bandwidth is equal to one year.

Appendix D. Polynomial Choice

The second estimation procedure is based on polynomial regression. In this case the problem isthe choice of the optimal polynomial order. we make use of the well-known Akaike informationcriteria (AIC):

Table B2

Test of Discontinuities at Non-Discontinuity Points

Males Females

Before After Before After

Age left < 16Non-disc. point �0.006 0.004 �0.046 �0.003

(0.029) (0.023) (0.034) (0.019)N 1,935 2,322 2,312 2,414

Age left < 19

Non disc. point 0.075 0.042 �0.116 �0.017(0.102) (0.055) (0.078) (0.068)

N 2,441 3,428 3,009 3,993

Notes. Significance levels: *p-values between 10 and 5%. **p-values between 5 and 1%. ***p-values less than1%. Table reports the coefficient of a set of OLS regressions with a dummy variable that identifies the cohortsborn after two non-discontinuity points, namely five years before the first cohort affected by the 1947 reform(1928) and the second five years after (1938). In each regression the sample includes respondents born fiveyears before and after the non-discontinuity point. All regressions include: a linear function of month of birthand its interaction with the virtual reform dummy; controls for adult height and for survey year. The standarderror in parenthesis are robust to heteroscedasticity and clustered by month of birth and survey year.



AIC ¼ N lnðrÞ2 þ 2p;

where r is the mean square error of the regression and p is the number of parameters inthe model. The results of this polynomial choice are presented in Table D1. It reports the AICvalue according to different bandwidths and polynomial orders. A defined choice for thepolynomial order does not emerge from the results in the Table. More in general, for both malesand females the optimal order of the polynomial increases as we increase the bandwidth, but it isusually bigger for males than for females.

University of Manchester and IFSMEA at the Max-Planck-Institute for Social Law and Social Policy (MPISOC)

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Table D1

Polynomial Order Choice According to Different Bandwidths (Years)

Memory Years Polynomial

Males Females

N AIC N AIC

5 1 2,322 11988.56 2,576 13270.695 2 2,322 11986.11 2,576 13271.365 3 2,322 11989.93 2,576 13275.225 4 2,322 11992.97 2,576 13278.855 5 2,322 11993.03 2,576 13271.78 1 3,492 17918.27 3,899 20064.68 2 3,492 17904.69 3,899 20060.938 3 3,492 17902.90 3,899 20060.698 4 3,492 17902.36 3,899 20064.188 5 3,492 17900.99 3,899 20062.61

10 1 4,203 21560.50 4,698 24158.7910 2 4,203 21553.79 4,698 24149.7410 3 4,203 21549.53 4,698 24151.2610 4 4,203 21552.44 4,698 24149.4710 5 4,203 21551.56 4,698 24148.66

Exec. func. Years Polynomial N AIC N AIC

5 1 2,322 14574.82 2,576 15856.635 2 2,322 14574.70 2,576 15859.45 3 2,322 14574.42 2,576 15862.745 4 2,322 14576.58 2,576 15866.545 5 2,322 14579.10 2,576 15865.468 1 3,492 21998.15 3,899 23970.388 2 3,492 21997.77 3,899 23972.898 3 3,492 21992.66 3,899 23975.098 4 3,492 21996.23 3,899 23975.368 5 3,492 21996.00 3,899 23975.02

10 1 4,203 26585.13 4,698 28904.1110 2 4,203 26586.59 4,698 28901.7210 3 4,203 26585.41 4,698 28905.2410 4 4,203 26584.27 4,698 28906.1410 5 4,203 26582.06 4,698 28902.69



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