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Do selective schooling systems increase
inequality?
By Simon Burgess
a
, Matt Dickson
b
, and Lindsey Macmillan
c
a
Department of Economics, University of Bristol, 2 Priory Rd, Bristol BS8 1TX;
e-mail: simon.burgess@bristol.ac.uk
b
Institute for Policy Research, University of Bath, BA2 7AY; e-mail: m.dickson@bath.ac.uk
c
Department of Social Science, UCL Institute of Education, 20 Bedford Way, London, WC1H 0AL;
e-mail: l.macmillan@ucl.ac.uk
Abstract
We investigate the impact on earnings inequality of a selective education system in
which school assignment is based on initial test scores. We use a large, representa-
tive household panel survey to compare adult earnings inequality of those growing
up under a selective education system with those educated under a comprehensive
system in England. Controlling for a range of background characteristics and the
current location, the wage distribution for individuals who grew up in selective
schooling areas is substantially and significantly more unequal. The total effect sizes
are large: 24% of the raw 90–10 earnings gap and 19% of the conditional 90–10 earn-
ings gap can be explained by differences across schooling systems.
JEL classifications: I24, J31.
1. Introduction
One of the key roles of any education system is to define the mechanism that assigns chil-
dren to schools. The choice of mechanism is likely to affect the level and distribution of
schooling outcomes and therefore later life outcomes. One such mechanism is to assign stu-
dents based on test scores: those with high scores attend one school, those with lower scores
go elsewhere. This is like tracking, but across schools rather than within school. In England
this is known as the grammar school system, and was used to allocate children to schools
from the time of a unified system of education in the 1940s through the 1980s; now only a
few areas still use this as the main system (see Appendix A for full details of institutional
background). Nevertheless, grammar schools continue to be a prominent policy issue in
England, with the UK government consulting in 2016 on the possibility of reintroducing or
expanding selection by ability and £50million being allocated to the expansion of new
grammar schools in May 2018. There is a parallel debate in the US about elite or exam
schools, reviewed below.
V
COxford University Press 2019.
This is an Open Access article distributed under the terms of the Creative Commons Attribution License
(http://creativecommons.org/licenses/by/4.0/), which permits unrestricted reuse, distribution, and reproduction in any medium,
provided the original work is properly cited.
Oxford Economic Papers, 2019, 1–24
doi: 10.1093/oep/gpz028
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Much of the research on grammar schools has focused on two important questions:
who gets into grammar schools (is access ‘fair’?), and what is the impact of attending a
grammar school (is there a causal gain in attainment?). There is much less evidence focusing
on the system as a whole, namely comparing the outcomes of students assigned by one
mechanism (by ability) compared to another (choice, or ‘by house prices’). That is the con-
tribution of this article: we examine the impact of a grammar school system on earnings
inequality.
We use data from a large and representative household panel data set for England and
compare the spread of the earnings distribution in middle age. We match existing selective
systems to very similar comprehensive systems, based on a wide range of area characteris-
tics such as political control, average wages and proportion of highly educated individuals
living in the area. The richness of our individual-level data means that we know where an
individual grew up and can map this back to the nature of the education system in that
place at that time. This allows us to categorize respondents as growing up in a selective sys-
tem or not, and to compare the earnings distribution they experience as adults, separating
the effect of grammars from the local labour market effect using variation in those who
move across local education authorities (LEAs). We can also control for the parental back-
ground of the individual, as well as their current geographic location.
We show that individuals who grew up in areas operating a selective schooling system
have a more unequal wage distribution in later life. Those growing up in selective systems
who make it to the top of the earnings distribution are significantly better off compared to
their similar non-selective counterparts. For those at the bottom of the earnings distribu-
tion, those growing up in a selective system earn significantly less than their matched non-
selective counterparts. These differences remain after controlling for a range of background
characteristics and current local area. In summary, there are both winners and losers from
the grammar system: the additional earnings differential between the 90
th
and 10
th
percen-
tiles in selective systems accounts for 24% of the total raw 90–10 earnings gap and 19% of
the conditional 90–10 earnings gap. This article establishes this new fact for policy discus-
sion. We do not attempt to unpack this into different component mechanisms here (though
obviously, the impact on educational attainment is likely to be key).
In the next section we review the related literature on the impact of selective systems on
later outcomes before describing the framework for our analysis in Section 3. Our empirical
approach and the data used are outlined in Section 4 and our results are presented in
Section 5. We end with some brief conclusions.
2. Related literature
Much of the previous literature on selective schools focuses on the benefit to the marginal
student of attending a grammar school compared to not attending. In Great Britain, Clark
(2010) uses access data from East Riding (a local government district in the north of
England) to estimate the causal impact of attending a grammar school on attainment at 16,
the types of course taken and university enrolment. He finds small effects of grammar
schools on test scores at 16 but larger effects on longer-run outcomes such as taking more
academic courses—which allow access to A levels and university enrolment. Similarly,
Clark and Del Bono (2014) implement a regression discontinuity design to assess the impact
of attending a grammar school for a cohort of young people born in Aberdeen, Scotland, in
the 1950s. They find large effects on educational attainment, and for women there are
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longer-term impacts on labour market outcomes and reduced fertility. For men there were
no long-term impacts identified.
Abdulkadiroglu et al. (2012) and Dobbie and Fryer (2011) assessed the impact of
attending exam schools in Boston and New York on attainment and test scores. Both stud-
ies found limited impacts on student achievements from attending these selective schools,
though Dobbie and Fryer (2011) found that these students were more likely to choose more
academically rigorous subjects. Dustmann et al. (2014) similarly found little impact of the
marginal student attending a more advanced track on their longer-term outcomes.
Sullivan and Heath (2002) and Galindo-Rueda and Vignoles (2005) used the National
Child Development Study (NCDS) data from the UK to compare the outcomes of those
attending grammar schools to comprehensive schools and secondary moderns. Both use a
value-added approach alongside school-level controls to assess the impact of the different
schools on educational attainment. In addition, Galindo-Rueda and Vignoles (2005) also
instrument school type with the political power of the LEA at the time, arguing that the pol-
itical power of the LEA at the time of reform affected the speed at which the systems were
switched from selective to mixed schooling. Both studies find significant positive effects on
attainment of grammar education compared to comprehensives although Manning and
Pischke (2006) use a falsification test of value-added from age 7 to 11 to show that these
studies are still affected by selection bias.
A slightly different question is addressed by Guyon et al. (2012), who use data from
Northern Ireland and exploit a policy change that compelled grammar schools to increase
the number of children admitted each year. The change induced a discontinuous increase in
the proportion of the school year group going to grammar schools, and this is used to iden-
tify the effect of school segregation by ability on the average performance in examinations
taken at age 16, at age 18 and on university entrance rates. Rather than the impact on the
marginal students who are shifted into the grammar school by the policy change, the esti-
mates provide an assessment of the impact on the whole distribution. Guyon et al. (2012)
find substantial positive impacts of the increased grammar attendance on average examin-
ation results and university entrance. However, as we might anticipate, disaggregating this
into the impact on the grammar school results and the impact on the non-grammar school
results, reveals a negative impact on the average results in the non-grammar schools as a
consequence of the change in student composition induced by the policy.
While each of these approaches have clear strengths, and Guyon et al. in particular look
at the distribution of results not just the effect on the marginal student, these studies say lit-
tle about differences across selective and non-selective systems. Closer to our study are
those of Atkinson et al. (2006) and Jesson (2000), who use data from the National Pupil
Database (NPD) for England and Wales, to compare LEAs that are still selective now to
non-selective LEAs. These studies are therefore more in line with our research, comparing
the outcomes of pupils in systems as a whole rather than the outcomes of the marginal pupil
who makes it into a grammar school. Both Jesson (2000) and Atkinson et al. (2006) use
NPD data to compare value added attainment across selective and non-selective LEAs.
While Jesson (2000) is open to the critique of Manning and Pischke (2006) that value-
added alone does not remove selection bias, Atkinson et al. (2006) match LEAs to attempt
to control for this. They show that prior attainment when comparing selective LEAs to the
comprehensive population as a whole is much higher in the selective LEAs but when com-
paring prior attainment in the matched LEAs, this is very similar. While neither study finds
evidence of higher attainment across selective and non-selective systems as a whole,
S.BURGESS,M.DICKSON,AND L.MACMILLAN 3
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Atkinson et al. (2006) find that grammar-educated children in selective LEAs outperform
similar children in non-selective LEAs on average while non-grammar-educated children in
selective LEAs underperform compared to similar children in non-selective LEAs. This is in
line with our findings of greater inequality in earnings later in life for those from selective
LEAs.
3. Framework
A selective school system, assigning individuals to schools based on their performance on a
test, is one way of assigning students to schools. In England, the grammar school system
assigns students to schools based on their performance on a test at age 11, commonly
referred to as the ‘11þ’ test. Typically in LEAs that operate a grammar system, students
who achieve above a certain threshold are entitled to a place at a grammar school while stu-
dents below the threshold are entitled to a place at a secondary modern school.
We compare the outcome of this system to the main alternative in England, namely
school choice. In England, this involves families stating their preferred schools. However,
given that the better schools quickly become over-subscribed and the criterion for assigning
students in this case becomes proximity of the student’s home to the school, school choice
quickly reduces down to neighbourhood schooling or ‘selection by house prices’. We there-
fore consider the differences in outcomes between two systems where, in their simplest
form, one allocates pupils to schools based on ability
1
and one allocates pupils to schools
based on proximity.
We present a very simple framework for thinking about the earnings inequality implied
by each system.
Think of a population, where students have ability, a, and parental resources, r.
These have distributions with variances r
2a
and r
2r
; they are positively correlated with
covariance r
ar
.
The schooling outcome, s, for student idepends on ability, school quality, q, and peer
group ability a:
si¼sðai;ai;qiÞ:
Later adult earnings depend on both the ability of the student and her schooling outcome:
yi¼aiþc:si
where cis the relative weight on schooling.
To determine the relative impacts of the alternative schooling systems on earnings in-
equality, we must evaluate how each system translates ability into outcomes and therefore
what each system implies for a(a) and q(a)—that is, how each system relates student ability
to peer group ability and to school (teacher) quality.
The school assignment mechanism is different in the two systems. In a grammar school
system, each student is assigned to the grammar school if a potentially noisy function of her
ability is above some threshold (determined by the number of places in the grammar
schools relative to the population). In a choice-based comprehensive system, admission
1 Of course, there are issues concerning whether the tests used actually measure ability. Given the
role of ‘tutoring to the test’, they are more likely to be measuring some mix of ability and attainment
although this is not central to our analysis here.
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depends on preferences and on priority. We could either assume random preferences or that
all have preferences for high quality schooling; in either case, the driving force is priority.
The most common priority rule in England is proximity: students living closest to the
school are admitted. Under standard assumptions, the operation of the housing market
means that houses nearby high performing schools are valued more highly
2
and so the like-
lihood of admission to the higher performing schools depends on family resources, r.
3.1 Grammar system—assignment through selection on ability
By definition, grammar school systems sort pupils based on their ability: so a(a) will be
positive and very strong. Schools with high ability pupils are attractive to high ability teach-
ers, hence we assume grammar schools attract and retain high quality teaching staff, hence
q(a) will be positive and strong.
si¼sðai;aiðaiÞ;qiðaiÞÞ ¼ sgðaiÞand earnings will be:yi¼aiþc:sgai
ðÞ
3.2 Comprehensive system—assignment through residential proximity to school
We assume that the high-quality schools are randomly distributed around an area.
However, because of the proximity rule, the quality of the school attended depends on par-
ental resources: q(r). As a covariance exists between rand a, we can write this as q(r(a)).
This also induces variation in peer groups, so a(a) again, but only through r. Therefore,
there is also a positive association between peer groups and ability and teaching quality and
ability in this system, although these work through the correlation between rand arather
than directly as in the grammar system.
si¼sðai;aiðrðaiÞÞ;qiðrðaiÞÞÞ ¼ scðaiÞand earnings will be :yi¼aiþc:scai
ðÞ
:
Using these, we can express the variance of earnings in each system as:
varkya
i
ðÞðÞ
¼1þcsk0la
ðÞ
no
2r2
a
where k¼g(grammar) or c(comprehensive). Consequently, var
g
(y) <or >var
c
(y) depend-
ing on whether dSgðaÞ
da <or >dScðaÞ
da .
Therefore, how the schooling system creates more equal or unequal wage distributions
depends, among other things, on how the two systems translate individual ability into
schooling outcomes. As we have seen, this will depend on how individual ability is related
to peer group ability and how individual ability is related to school (teacher) quality in each
system, both directly and indirectly via parental resources. These are empirical questions
that we bring to the data.
4. Empirical analysis
To perfectly estimate the impact of selective systems compared to non-selective systems we
would need to be living in an ideal world. This is the thought experiment: imagine two
communities of identical families, growing up separately. One community has a grammar
school system; the other has a comprehensive system (allocation by proximity). Following
2 This has repeatedly been shown to be the case for England, for a recent contribution see Gibbons
et al. (2013).
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their education, both sets of individuals go on to work in the same labour market. A com-
parison of the distribution of wages amongst those who grew up in the selective system
with the distribution for those who grew up in the non-selective system, would tell us some-
thing about the impact of selective schooling on the whole distribution of wages.
Unfortunately, this thought experiment cannot be run in practice and we therefore have
to use empirical methods to get as close to this ideal world as possible. In order to empiric-
ally test our model, we need to be able to compare the distribution of wages for individuals
who grew up in LEAs
3
operating a selective mechanism for allocating students to schools,
with the distribution amongst individuals who grew up in areas that were very similar along
a number of relevant dimensions but that were operating the comprehensive system. This
should ensure that we are not incorrectly attributing the effects of other area characteristics
on later wages to the effect of growing up in a selective school area.
We use Understanding Society for our empirical analysis. This is a large longitudinal panel
study following approximately 40,000 households in the UK, beginning in 2009. Information
is collected from all individuals in the household aged 16 and over, on a wide range of topics,
including parental background, labour market status and earnings. We make use of the spe-
cial license release of the data, which includes the individual’s age, current local authority of
residence and crucially for our purposes, the local authority district where the individual was
born. Each wave is collected over 24 months: the first was collected between January 2009
and January 2011, the second between January 2010 and January 2012—we make use of
both of these waves in our analysis. Given our sample requirements and matching process,
our final analysis focuses on 2033 individuals who were born in 33 selective or similar non-
selective LEAs from 1961–1983 (from these 33 LEAs we have observations from 111
LEA*years that were selective, and observations from 172 LEA*years that were non-
selective). Appendix C Fig. C1 illustrates how these LEAs are distributed between those al-
ways selective (14), those always non-selective (15) and those that are selective in some years,
non-selective in others (4). The birth year range means that the individuals in our sample are
aged between 25 and 50 and so are of prime working age.
4.1 Defining selectivity
We begin by defining LEAs of birth as selective or non-selective. Selectivity of an area is cal-
culated using school level data from the Annual Schools Census: schools are allocated to
their LEA then the aggregated LEA data is used to calculate the percentage of children aged
13
4
in the LEA who had a place allocated by the selective system (grammar or secondary
modern places).
5
The time-series of data runs from 1967 to 1983, however post-1983 there
3 There are currently 152 LEAs, or local authorities as they are now known, in the UK (Department
for Education, http://www.education.gov.uk/, last accessed 10 July 2018). The average population
in a Local Authority in 1998 was 140,000 individuals ranging from 25,000 to just over 1,000,000
individuals.
4 The proportions were measured at age 13 rather than 11 or 12 because in some secondary schools
(upper secondaries) children didn’t start in the school until they were 13.
5 We are extremely grateful to Damon Clark for providing this data. The figures for each LEA in each
year are gender specific as there were/are a non-trivial proportion of single-sex schools in select-
ive areas. For our purposes, we average the male and female figures to give us an average meas-
ure of selectivity for an LEA in a year. For the LEAs in our sample, the difference between the male
and female figures is very small or zero (the mean is 0.65 percentage points and median is 0.19 per-
centage points).
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has been very little further comprehensivization (see Crook, 2013) and so we make the as-
sumption that the proportion of selective school places within an LEA has remained similar
to the 1983 level henceforth. The upper panel of Fig. 1 shows that between 1983 and 1996
there is only a very slight change in the proportion of grammar school pupils across
England as a whole.
6
We do not model the process by which LEAs retained or abandoned
selective schools. It is likely to have been influenced by fixed factors such as the size and
Fig. 1. (a) Proportion of pupils in state-funded grammar schools in England 1947–2016.
Source: House of Commons Library Briefing Paper 1398 (March 2017), Fig. 2; see Bolto n (2017).
(b) Distribution of selectivity across LEAs in 1983.
6 Despite the total number of grammar school places increasing as grammar schools have
expanded, this phenomenon has also been witnessed to a similar extent in other schools, leaving
the overall proportion of pupils in grammar schools increasing only ‘very gradually’ over the past
25 years (see Bolton, 2017).
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geography of the area (population density and the like) as well as local political control.
Our assumption is that the matching of LEAs, discussed below, takes account of most of
the statistical force of these factors, and within the matched set, the retention of selection is
as good as random.
We define an LEA as selective if more than 20% of children in the LEA were assigned
their school place by selection. We define non-selective LEAs as those where less than 5%
of 13-year-old children were assigned by selection. As illustrated in the lower panel of
Fig. 1, given the distribution of levels of selectivity, these thresholds mark a clear delinea-
tion between what were selective and non-selective areas. Table 1 illustrates the distribution
of selectivity in 145 LEAs across the time-period considered (i.e. 1974 to 1996). Sixty per
cent of LEA*time observations were 100% non-selective. Of those with any selectivity,
52% had greater than 20% selective schools within the LEA and 43% had greater than
30% selective schools. We consider whether our results are sensitive to these cut-offs at the
end of the results section.
4.2 Matching
Having defined selectivity, we proceed by matching selective and non-selective LEAs by
LEA*year on the basis of local political, socio-demographic, labour market and school
market characteristics: the political party in control of the local government,
7
the propor-
tion of the area’s residents holding a degree, the proportion in social classes 1 or 2 (profes-
sional and managerial), the proportion of people economically active,
8
the local
unemployment rate,
9
the local male hourly wage rate,
10
and the proportion of children
Table 1. Distribution of selectivity in all 145 LEAs for which we have data across all time-periods
1974–1996
Selective % Selective %
conditional on >0
N 3,335 1,350
Mean 15.13 37.4
SD 29.25 35.8
10
th
0.0 2.4
25
th
0.0 5.6
50
th
0.0 21.7
75
th
11.3 70.0
90
th
73.0 99.7
Source: Authors’ calculations using Understanding Society waves 1–2.
7 This information comes from the data from the Elections Centre (www.electionscentre.co.uk, last
accessed 10 July 2018) recorded in 1981. We are grateful to Colin Rallings for providing this data.
8 These three variables are from the 1981 census.
9 Taken from the Employment Gazette, 1979 to 1998, county-level tables. Unemployment rates are matched
to LEAs within counties with two LEAs in the same county taking the same unemployment rate.
10 Taken from the New Earnings Survey, 1974 to 1996, region and sub-region tables. The specific earn-
ings variable used to match is the average hourly earnings excluding the effect of overtime for full-
time male workers over the age of 21 whose pay for the survey pay-period was not affected by
absence.
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who attend private schools in the area.
11
Individuals turned 13 in different years in our
data and hence the matching of LEAs is done separately for each year of our period of inter-
est from 1974 to 1996. We select the three nearest neighbour non-selective LEAs for each
selective LEA with replacement and retain only matches that share common support.
Following the matching, we retain individuals who grew up in one of the selective or
matched non-selective LEAs.
The key to success of our empirical strategy is to ensure that the selective and non-
selective areas are matched with respect to characteristics that could impact upon the later
earnings of individuals who grew up in these areas. Our matching variables capture essen-
tial features of the labour market, private school market, socio-demographics, and the pol-
itical environment of the local area. These could all influence the propensity for an area to
retain a selective system and also impact upon the later labour market outcomes of those
growing up in the area. Matching on this broad set of covariates means that we are able to
consider the impact of the school system on the earnings distributions of individuals who
grew up in areas featuring the same local political control, the same socio-demographic mix
and the same labour market conditions but differing in the selectivity of the school system.
The ideal experiment would compare identical areas along all relevant dimensions bar the
school system, but given data limitations, we believe that this combination of characteris-
tics does a job of capturing the relevant dimensions that could affect later earnings.
Appendix B contains summary statistics for the quality of the covariate balancing after
the matching process in each year. These show that for every year and for each of the varia-
bles used in the matching, t-tests unanimously and comprehensively fail to reject the hy-
pothesis that there is no difference in the means of the variables between the selective and
non-selective areas (the average of the absolute value of the t-stat across all variables and
years is 0.37, median 0.32). Moreover, Kolmogorov-Smirnov tests of the equality of the dis-
tributions of the matching covariates between the selective and matched non-selective areas
fail to find a significant difference in the distributions in all but 13 of 161 tests (average
p-value over the 161 tests was 0.462).
12
Hence the post-match test statistics suggest that se-
lective and non-selective LEAs are very well matched with respect to the levels and distribu-
tion of their labour market and school market characteristics.
4.3 Data and methodological issues
Ideally the characteristics that we match on would all be measured at exactly the time that
the individuals attended secondary school and for much of our data this is the case.
However, due to the non-availability of some of this information—in part due to the
restructuring of local authority organization during the 1970s—there is some limit to the
time-variation in some of the matching variables. For the local unemployment data, 15 of
the 23 years of data are unaffected, but for eight of the years that we include in our analysis
we have to assign the value for the nearest available year (which is a maximum of five years
11 Compiled using the National Pupil Database 2002. Results are robust to the exclusion of private
schools from the matching process, see the Appendix Figs B2a and B3a and Tables B2a and B3a.
12 This is 8% of the tests, which is slightly above the type I error rate we would expect when con-
ducting multiple hypothesis tests, however testing equality of distributions with small numbers
(n <15) in each distribution makes the test vulnerable to outliers skewing one distribution and
leading to a rejection of the null of equality. All individual test statistics available from the authors.
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distance and in the majority of cases three or fewer).
13
Our results are robust to the exclu-
sion of years in which the unemployment information has to be mapped from a nearby year
(see Appendix Figs B2b and B3b,Tables B2b and B3b).
Information on the proportion of children attending private/independent schools is only
available at the local authority level from 2002 and so there is no time-variation in this vari-
able. However, given that the proportion of full-time pupils in private/independent schools
in England and the proportion of English schools that are private/independent has changed
very little between the time we have our measure of private school density (2002) and the
relevant period for our data (1974 to 1996),
14
it is reasonable to assume that the local pri-
vate school density has not changed too dramatically and thus our measure is relevant for
matching.
15
Similarly, the information on the political party in control of local government comes
from a single measure in 1981, and the information on the proportion of the area’s resi-
dents holding a degree, the proportion in social classes 1 or 2, and the proportion of people
economically active comes from the 1981 census. While time-variation in these variables
would be preferable, to the extent that these measures capture persistent, slowly changing,
characteristics of a local area, they will improve the matching mechanism. All of our results
are robust to the exclusion of non-time-varying matching variables, see Appendix B.
It may be a concern that areas that had a selective schooling system were more diverse
than those with a non-selective system and thus differences in prime-age earnings later in
life reflect existing inequality rather than being a result of the differing systems. However,
to the extent that the diversity of an area is captured by the unemployment rate, average
wages, independent school density, local political control, the proportion of the area’s resi-
dents holding a degree, the proportion in social classes 1 or 2 (professional and manager-
ial), and the proportion of people economically active, we will be comparing similarly
diverse areas. The post-matching balancing tests suggest that for each of these variables we
achieve a close match, hence the selective and non-selective areas we compare are on aver-
age as diverse as each other. Moreover, since our wage regressions include fixed effects for
the current local labour market area, the estimated effects are identified by those who move
area between the time of their schooling and their later wage observations, therefore the
estimates cannot simply reflect existing inequality in earnings between selective and non-
selective areas, a point we return to below.
An obvious concern with our data is that we observe the LEA at birth rather than the
LEA that the individual is enrolled into in secondary school. This raises two issues: children
may attend a school across the LEA ‘border’ and so be educated under a different system;
or families may move areas between the birth of the child and the start of secondary school.
Regarding the first issue, we investigate the extent to which pupils cross borders in the
NPD. On average around 11% of pupils attend a school in a different LEA from their LEA
of residence. This is most likely to occur in London (over 20% cross-borders on average)
where LEAs are small and close together, however given our preferred set of matching
13 In practice this means that for the years 1974 to 1978 each LEA has their 1979 level of unemploy-
ment and for the years 1994 to 1996 each LEA has their 1993 level of unemployment.
14 See Ryanand Sibieta (2010).
15 As a robustness test we perform the analysis when matching without private school proportion as
a matching variable. Our results are robust to this test, see Appendix Figs B2a, B3a and Tables
B2a and B3a.
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covariates, London does not feature in the analysis. In robustness checks in which the
matching covariates are changed and London does become a matched LEA, the results re-
main consistent and this is the case whether London is included or not in these checks. We
argue that as our main results do not include London the potential of border crossing influ-
encing the findings is much reduced. Moreover, if our alternative specification results are
robust to the inclusion/exclusion of London where border crossing is most relevant, then
our results are not likely to be driven by border crossing elsewhere which will be much less
prevalent.
16
We also argue that border crossing is likely to understate our findings to the extent to
which border crossing across systems is made by: (i) those that are the most able in non-
selective systems crossing borders to attend grammar schools; and (ii) those who do not
make it into grammars in the selective areas crossing borders to attend comprehensives ra-
ther than secondary moderns. In the first case, these individuals will push up the top end of
the non-selective earnings distribution if grammars increase earnings relative to comprehen-
sives, and in the second case, these individuals will push up the bottom end of the selective
earnings distribution if comprehensives increase earnings relative to secondary moderns.
Both of these effects would lead us to understate the effects of the selective system at the
top and bottom of the earnings distribution.
To consider the issue that families may move areas, we use data from two birth cohort
studies, the British Cohort Study (BCS) following children born in 1970, the Millennium
Cohort Study (MCS) following children born in 2000, and the NPD to investigate the ex-
tent to which we can observe families moving from birth to starting secondary school. The
birth cohort studies provide information on movements from birth to age 10 in the BCS
and from birth to age seven in the MCS, both at Government Office Region (GOR) level.
The NPD provides information on moves from age five to 11 at the postcode level and
Travel to Work Area (TTWA) level. As can be seen from Table 2, the vast majority of fami-
lies do not move during childhood with 10% moving to a different postcode in the NPD
data and 1% moving to a different TTWA. The data from the cohort studies suggests that
while more families move before children start school, the numbers moving are still small
with 7.3% in the BCS and 5.4% in the MCS moving before the cohort member is five.
17
Similar arguments to those regarding border crossing to attend a different school also apply
to the potential for families to move between a child’s birth and schooling and that this
movement might be driven by parents’ desire for their child to be educated under a particu-
lar system. However, it is again the case that this would lead us to understate the effect of
the selective system. If ambitious parents who believe their child will get into the grammar
school move from a non-selective to a selective area between a child’s birth and schooling,
we will include them in the non-selective distribution and if they attend the grammar school
and it increases their earnings, this will be recorded as increasing the earnings at the top
end of the non-selective distribution, biasing the selective effect downwards. Similarly if
parents living in a selective area fear that their young child will fail to make the grade for
the grammar school and move to a comprehensive area, this would be picked up as an
16 These additional robustness checks are available from the authors on request and are also con-
tained in an earlier version of the article, see Burgess et al. (2014).
17 Families that move are typically slightly more affluent than families that do not move in both cohort
studies. For example, in the BCS, families that moved between birth and age 10 had an average
family income of £1462 a month compared to an average of £1304 for families who did not move.
S.BURGESS,M.DICKSON,AND L.MACMILLAN 11
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increase in earnings at the lower part of the selective distribution, again leading us to under-
state any negative effect of the selective system on the bottom of the distribution.
A final concern with our data is that we need individuals to move between school and
when they are observed in the labour market as an adult in order to be able to separate out
the effect of the schooling system from that of the local labour market. If everyone stayed
where they went to school, our findings could be driven by the characteristics of the LEA
that are related to labour market earnings and selection of the schooling system. For ex-
ample, if selective LEAs were typically more diverse, thus had a more unequal earnings dis-
tribution, and individuals from selective LEAs stayed where they were from as adults, we
would attribute the spurious association, or indeed reverse causation of inequality in select-
ive areas, to selective areas causing inequality. Fortunately in our data, over 50% of the
sample move LEAs between birth and adulthood. As illustrated in Table 3, looking at the
largest LEAs operating each type of system the extent of movement is almost identical:
53.3% for those growing up in selective LEAs, 53.8% for those growing up in non-selective
LEAs.
18
We therefore argue that we have enough variation in our data to be able to separ-
ate the effect of the school system from the effect of the LEAs’ labour market
characteristics.
4.4 Measuring earnings inequality
To compare earnings distributions in adulthood, we use hourly wages calculated from the
recorded usual gross monthly pay including overtime, usual weekly hours and overtime
hours, deflated to year 2000 £s.Zero earnings are included for individuals who are
Table 2. Proportion moving across different geographical areas during primary school
Stay Move
Postcode
NPD 5–11 90.0 10.0
Travel to Work Area
NPD 5–11 99.0 1.0
Government Office Region
BCS
0–5 92.7 7.3
5–10 95.5 4.5
010 89.4 10.6
MCS
0–3 96.6 3.4
3–5 98.0 2.0
5–7 98.5 1.5
7–11 98.2 1.8
0–11 92.6 7.4
Source: Authors’ calculations using British Cohort Study 1970, Millennium Cohort Study; NPD figures from
Allen et al. (2010).
18 Note that selective schooling systems can affect adult wages in a number of ways including po-
tentially increasing the likelihood of students moving away from home after school to attend uni-
versity and enter the labour market. This is all part of the effect that we are trying to measure.
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unemployed or long-term sick or disabled at the time of the survey
19
as these are viewed as
valid labour market outcomes. Given two waves of data, each individual has either one or
two observations. Rather than discarding information, where we have two wage observa-
tions for an individual we average them and include that individual as a single observation.
This averaging moves us towards a more permanent rather than transitory measure of indi-
viduals’ earnings. Sixty-five per cent of the main estimation sample (1,325 of 2,033 individ-
uals) have two wage observations. Prior to the averaging, an initial regression is run to
remove any year of survey effects from wages.
We begin by estimating an OLS wage regression (1) where yir is the average hourly wage
of individual iin LEA r,selectiveir, is a dichotomous variable equal to 1 if the individual
was born in a selective LEA and 0 if they were born in a matched non-selective LEA and
the regression includes a gender (g) specific quadratic in age (a). This ensures that in our
baseline specification we are comparing the earnings of similarly aged males and similarly
aged females.
yir ¼aþbselectiveir þcaigiþda2
igiþuir (1)
In addition to the effects of age and gender, there are other factors—unrelated to
schooling—that may affect current wages. In our second specification (2), the conditional
model, we control for personal characteristics (gender, ethnicity, plus the quadratic in age
interacted with gender), controls for the individual’s parental background (parental occu-
pational class and parental education measured when the individual was 14-years-old
20
),
dummies for the current local labour market (county), and dummies for the year of
the survey (2009–2012).
21
Given this range of pre-determined control variables we
are able to compare the earnings of observably similar individuals from similar family
Table 3. Proportion of people who move between birth and adulthood from the five largest se-
lective and non-selective LEAs
Selective Non-Selective
LEA Proportion move LEA Proportion move
Kent 55.6% Essex 65.1%
Lancashire 44.3% Hertfordshire 58.3%
Gloucestershire 41.5% Bedfordshire 51.2%
Buckinghamshire 66.2% Leicestershire 29.0%
Warwickshire 64.9% Northamptonshire 33.8%
Weighted average 53.3% Weighted average 53.8%
Source: Authors’ calculations using Understanding Society waves 1–2.
19 Results are robust to the exclusion of the long-term sick and disabled, see Appendix Figs B2b and
B3b and Tables B2b and B3b.
20 Notes to Appendix Table B4 detail the parental occupational categories which are dummies for
the 10 major groups of the standard occupational classification (SOC 2000).
21 Appendix Table B4 contains the coefficient estimates for the main estimation sample conditional
specification. Robust standard errors are obtained in all regressions, clustering at the individual
level in cases where more than one observation is used per person.
S.BURGESS,M.DICKSON,AND L.MACMILLAN 13
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backgrounds but who experienced different education systems in areas that were other-
wise very similar.
yir ¼aþbselectiveir þcaigiþda2
igiþf0Xir þuir (2)
In both specifications, we recover the residuals from our wage regressions and compare the
distribution of earnings for those growing up in selective and non-selective systems. As we
are interested in the relative distributions rather than the effects on the average, we remove
the global mean from the residual before calculating the deciles of the distribution—allow-
ing us to compare individuals at different points in each distribution with the overall aver-
age.
22
We use unconditional simultaneous quantile regressions (eq. 3), regressing adjusted
earnings on the dichotomous selection variable to estimate whether growing up in a select-
ive system has a significant effect on earnings at each decile (d) of the distribution of
earnings.
23
Qdð^
yirÞ¼aþbdselectiveir where d¼½1;2;...;9(3)
Finally, we perform tests on linear combinations at the 90
th
and 10
th
percentiles and 75
th
and 25
th
percentiles to test whether there are significant differences in the effect of selective
systems on earnings inequality.
5. Results
Table 4 shows the raw mean and variance statistics for the selective versus non-selective
areas: overall, average hourly earnings 2009–2012 are very similar across the two groups
although slightly (insignificantly) higher amongst those from the non-selective areas (£8.76
versus £8.75).
24
The variance of earnings is considerably higher for selective areas (£35.49
versus £26.79). Figure 2 illustrates the impact of selective schooling across the whole distri-
bution, plotting the deciles of age*gender adjusted hourly earnings for each system. As can
be seen in this figure, the impact of the selective system has a positive effect on earnings at
the top of the distribution and a negative effect on earnings at the lower end of the distribu-
tion. For those at the top of the earnings distribution, individuals who grew up in selective
schooling areas earn more than their non-selective counterparts. At the bottom of the earn-
ings distribution, this is reversed.
Panel A of Table 5 presents the simultaneous quantile regression estimates correspond-
ing to Fig. 2. These estimates show that the differences between the distributions are statis-
tically significant at the 10
th
percentile, the 20
th
percentile, the 30
th
percentile, the 75
th
percentile, the 80
th
percentile and the 90
th
percentile.
Figure 3, and Panel B of Table 5, present the results using the conditional earnings resid-
uals. The qualitative nature of the results remains largely unchanged: at the lower end of
the distribution, individuals born in a selective schooling area earn less than those from the
matched non-selective areas, while this reverses for the top deciles. The distributions are
significantly different at the 10
th
percentile, the 20
th
percentile, the 40
th
percentile and the
22 As we are removing a constant the results hold for non-mean-adjusted earnings. Note the aver-
age earnings are not significantly different across groups indicating a good match.
23 We implement the sqreg command in Stata, which provides bootstrapped standard errors.
24 Appendix Table B5 contains summary statistics for the individuals in the main estimation sample
and shows that exogenous characteristics are balanced between the two groups.
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50
th
percentile. At the top of the distribution there is a statistically significant positive effect
of selective schooling at the 90
th
percentile.
These results are robust to including all observations (i.e. not averaging where an indi-
vidual has two observations), to including just a single observation per individual, to
including only the observations of individuals with two observations, and to altering the
definition of selective and non-selective areas—in each case the pattern and levels of signifi-
cance remain essentially unchanged.
25
Table 6 presents estimates of the difference in the effect sizes found at the 90
th
and 10
th
percentile and 75
th
and 25
th
percentiles for both the unconditional (Panel A) and condition-
al (Panel B) models. Focusing first on Panel A, the 90–10 earnings gap of individuals grow-
ing up in a selective LEA is £3.77/hour larger than the 90–10 earnings gap of individuals
from a non-selective system. This accounts for 24.1% of the overall 90–10 earnings gap in
our sample, and the test against zero has a p-value below 0.001. Focusing on the 75
th
–25
th
Table 4. Raw earnings distribution by schooling system type
Selective Non-Selective
Hourly wage: mean 8.75 8.76
variance 35.49 26.79
N 962 1,071
Note: hourly earnings in year 2000 £s.
Source: Authors’ calculations using Understanding Society waves 1–2.
Fig. 2. Deciles of the raw earnings distribution by scho oling system type.
Notes: residuals from a regression of wage on a gender specific quadratic in age and a selective
schooling area dummy, with the global mean of the residual removed. Before averaging wages for
individuals with two wage observations, year of survey effects are removed via a regression.
25 See Appendix Figs B2a, B2b, B3a and B3b plus Tables B2a, B2b, B3a and B3b.
S.BURGESS,M.DICKSON,AND L.MACMILLAN 15
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Table 5. Quantile regression estimates of selective schooling effect on wages
A: Without controls B: With controls
coeff. std. error t coeff. std. error t
10 2.195 0.559 3.93*** 10 1.019 0.399 2.56**
20 0.465 0.268 1.73* 20 0.592 0.335 1.77*
25 0.308 0.233 1.32 25 0.284 0.259 1.09
30 0.415 0.216 1.92* 30 0.300 0.247 1.21
40 0.173 0.204 0.85 40 0.482 0.258 1.87*
50 0.227 0.151 1.50 50 0.494 0.259 1.91*
60 0.317 0.287 1.11 60 0.153 0.308 0.50
70 0.325 0.369 0.88 70 0.052 0.310 0.17
75 0.699 0.394 1.77* 75 0.103 0.361 0.29
80 0.705 0.427 1.65* 80 0.400 0.355 1.13
90 1.574 0.637 2.47** 90 1.312 0.559 2.35**
N¼2,033 N¼2,033
Note: residuals from a regression of wage on a gender specific quadratic in age and a selective schooling area
dummy (Panel A); and residuals from a regression of wage on a gender specific quadratic in age, a selective
schooling area dummy, gender, ethnicity, parental occupational class when the individual was 14, parental
education and current county of residence (Panel B). Global means of the residual removed. Before averaging
wages for individuals with two wage observations the year of survey effects are removed via a regression.
***,**, * indicate significance at the 1%, 5%, and 10% level, respectively.
Source: Authors’ estimates using Understanding Society waves 1–2.
Fig. 3. Deciles of the conditional earnings distribution by schooling system type.
Notes: residuals from a regression of wage on a gender specific quadratic in age, gender, ethnicity,
parental occupational class when the individual was 14, parental education, current county of resi-
dence and a selective schooling area dummy with the global mean of the residual removed. Before
averaging wages for individuals with two wage observations, year of survey effects are removed via a
regression.
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percentile earnings difference, the gap is 15.6% of the total raw gap, with a p-value of
0.010 for the test against zero.
Panel B shows that in the conditional model, there is a quantitatively and statistically
significant difference in the 90–10 earnings gap between the two education systems. This is
£2.33/hour, or 19.3% of the total conditional 90–10 gap in the sample, with a p-value of
below 0.001. However, the difference at the 75
th
–25
th
percentiles is smaller and no longer
significantly different.
5.1 Differences by gender
While there is no a priori reason to think that schooling systems will have differential
effects on inequality by gender according to our descriptive framework, it is interesting to
consider this question for males and females separately. Tables 7 and 8and Figs 4 and 5
present the results by gender (showing the conditional model only, for each gender the un-
conditional model results follow the same pattern and significance of the pooled results).
Table 8 shows that the differences in inequality for both males and females in the condition-
al model also mirror those seen in the pooled sample though somewhat smaller (18.3% of
total 90–10 gap for males and 10.6% of total 90–10 gap for females). However, the detail
in Table 7 and the figures show a slightly more complex picture: for males, the difference is
concentrated at the top of the distribution, whereas for females, the gap is particularly evi-
dent at the bottom of the distribution in the conditional specification. It may well be that
this is because there was a significant gender difference in school assignment in selective
areas. That is, the grammar school era was a time when boys typically outperformed girls
at school, and being in a selective area meant that female students disproportionately went
to secondary modern schools and male students disproportionately went to grammar
schools.
5.2 Robustness
To test whether our results are robust to changes in the definition of selective and non-
selective areas we redefine selective LEAs as those assigning more than 30% of places by se-
lection whilst retaining the definition of non-selective as those that assign less than 5% by
this method. Appendix Tables B2a and B3a shows the quantile regressions for the models
with and without controls. The results are qualitatively and quantitatively similar to the
corresponding figures in Table 5 (the 90–10 gap in the conditional results is £2.50 which is
19.4% of the conditional 90–10 difference). Figure 6 illustrates the results of the model
with controls and comparison with Fig. 3 provides visual confirmation of the robustness of
Table 6. Estimated effects sizes
Sample
wage gap
A: Without controls Sample
wage gap
B: With controls
coeff. std. error Effect size coeff. std. error Effect size
90–10 15.66 3.768 0.808*** 24.06 12.07 2.331 0.615*** 19.31
75–25 6.45 1.007 0.390*** 15.61 5.77 0.387 0.354 6.71
Note: earnings differentials estimated by testing the linear combination from the simultaneous quantile regres-
sions. The effect size is calculated as the estimated difference divided by the total earnings differential in the
sample. ***,**, * indicate significance at the 1%, 5%, and 10% level, respectively.
Source: Authors’ estimates using Understanding Society waves 1–2.
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the results. Further robustness tests are illustrated in Figs B2a and B2b (both for the condi-
tional model) and B3a and B3b (raw model), in which the selectivity definition, the inclu-
sion/exclusion of private school percentage and other time-invariant variables from the
matching, the treatment of multiple observations for an individual, the treatment of long-
term sick/disabled and the restriction of sample years are all tested. The figures all illustrate
the same pattern of results and the corresponding quantile regression results in Tables B2a,
B2b, B3a and B3b confirm the robustness of our results.
As one further robustness test, we take our main estimation sample and re-assign at ran-
dom the indicator for growing up in an area operating the selective system, though main-
taining the same proportion of the sample in each system. We then carry out the same
exercise in comparing the distribution on earnings for individuals ‘growing up’ in each
Table 7. Quantile regression estimates of selective schooling effect on wages, by gender
A: Males B: Females
coeff. std. error t coeff. std. error t
10 0.057 0.568 0.10 10 1.069 0.552 1.94*
20 0.212 0.555 0.38 20 1.309 0.339 3.86***
25 0.126 0.460 0.27 25 1.192 0.315 3.78***
30 0.311 0.410 0.76 30 1.190 0.267 4.46***
40 0.493 0.402 1.23 40 0.952 0.305 3.12***
50 0.706 0.382 1.85* 50 0.994 0.218 4.56***
60 0.797 0.399 2.00** 60 1.059 0.289 3.67***
70 1.189 0.401 2.97*** 70 1.066 0.32 3.34***
75 1.131 0.581 1.95* 75 1.032 0.391 2.64***
80 1.594 0.476 3.35*** 80 0.608 0.478 1.27
90 2.386 0.917 2.60*** 90 0.111 0.524 0.210
912 1,121
Note: residuals from a regression of wage on a gender specific quadratic in age, a selective schooling area
dummy, ethnicity, parental occupational class when the individual was 14, parental education and current
county of residence. Men only (Panel A) and Women only (Panel B). Global means of the residual removed.
Before averaging wages for individuals with two wage observations the year of survey effects are removed via a
regression. ***,**, * indicate significance at the 1%, 5%, and 10% level, respectively.
Source: Authors’ estimates using Understanding Society waves 1–2.
Table 8. Estimated effects sizes for conditional specification by gender
Sample
wage gap
A: Males Sample
wage gap
B: Females
coeff. std. error Effect size coeff. std. error Effect size
90-10 13.37 2.442 1.030** 18.27 11.09 1.180 0.722* 10.64
75-25 6.02 1.005 0.566* 16.74 5.14 0.160 0.441 3.10
Note: earnings differentials estimated by testing the linear combination from the simultaneous quantile regres-
sions. The effect size is calculated as the estimated difference divided by the total earnings differential in the
sample. ***,**, * indicate significance at the 1%, 5%, and 10% level, respectively.
Source: Authors’ estimates using Understanding Society waves 1–2.
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Fig. 5. Deciles of the conditional earnings distribution by schooling system type, females.
Notes: residuals from a regression of wage on a gender specific quadratic in age, ethnicity, parental
occupational class when the individual was 14, parental education, current county of residence and a
selective schooling area dummy with the global mean of the residual removed. Before averaging
wages for individuals with two wage observations, year of survey effects are removed via a
regression.
Fig. 4. Deciles of the conditional earnings distribution by schooling system type, males.
Notes: residuals from a regression of wage on a gender specific quadratic in age, ethnicity, parental
occupational class when the individual was 14, parental education, current county of residence and a
selective schooling area dummy with the global mean of the residual removed. Before averaging
wages for individuals with two wage observations, year of survey effects are removed via a
regression.
S.BURGESS,M.DICKSON,AND L.MACMILLAN 19
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system. As can be seen visually in Appendix B Fig. B1, whether the conditional or raw mod-
els are used, there is now no significant difference between the distributions at any point—
in contrast to our main estimates, which are reproduced to allow comparison. Similarly,
Appendix B Table B1 shows the corresponding coefficient estimates, none of which are
statistically significant.
6. Conclusion
In this article, we have investigated the impact on earnings inequality of a selective educa-
tion system in which school assignment is based on initial test scores. In England, this was
the system in place until the 1970s, when the comprehensive system started to become the
norm. Despite this ever-receding historical background, the role of grammar schools con-
tinues to be a lively and contentious issue in the current education policy debate, with the
UK government recently consulting on reintroducing or expanding existing grammar
schools. This finds a parallel in the US where a similar literature concerns the merits of
exam schools.
We have used a large and representative household panel survey with information on
each respondent’s childhood to compare adult earnings inequality of those growing up
under a selective education system with those educated under a comprehensive system.
Given the inevitable time-lag between schooling and prime-age earnings, assembling the
data required to match local areas on their characteristics at the time of schooling is a non-
trivial task. Nevertheless, we believe that we have constructed the best possible data set
available to address this question for England and the robustness of the results to different
Fig. 6. Deciles of the conditional earnings distribution by schooling system type, selective defined as
>30% assigned by selection, non-selective <5% assigned by selection.
Notes: residuals from a regression of wage on a gender specific quadratic in age, gender, ethnicity,
parental occupational class when the individual was 14, parental education, current county of resi-
dence and a selective schooling area dummy with the global mean of the residual removed. Before
averaging wages for individuals with two wage observations, year of survey effects are removed via a
regression.
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sets of matching covariates and the covariate balance we achieve between the selective and
non-selective areas gives confidence that we are making a valid comparison.
Our data allows us to add new information into the selective schooling debate in Britain
and beyond. Controlling for a range of background characteristics and their current labour
market context, we find that the wage distribution for individuals who grew up in selective
schooling areas is substantially more unequal, with this difference being statistically signifi-
cant. The total effect sizes are large: 24% of the raw 90–10 earnings gap and 19% of the
conditional 90–10 earnings gap can be explained by schooling system. These results are ro-
bust to a wide range of specification checks. In terms of magnitude, we can compare the
proportion of the 90–10 earnings gap that is explained by the schooling system, to the gen-
eral increase in wage inequality in the first part of this century. Between 1997 and 2009,
the 90–10 earnings gap increased by almost 60%, so our results are equivalent to around
five years’ worth of change.
26
Given this context, it is clear that the schooling system is re-
sponsible for a sizeable share of wage inequality.
These results are consistent with previous findings by Atkinson et al. (2006) who find
that selective systems lead to wider disparities in educational attainment compared to com-
prehensive systems: grammar-educated children in selective LEAs outperform similar chil-
dren in non-selective LEAs on average while non-grammar-educated children in selective
LEAs underperform compared to similar children in non-selective LEAs. Our findings res-
onate with this, suggesting that these exam performance disparities carry through into the
labour market and are reflected in subsequent earnings. This is one potential mechanism
for our findings. Our modelling framework highlighted the role of other potential mecha-
nisms including peer groups and school (teacher) quality in magnifying inequality in ability
in a selective education system. The evidence on peer effects is mixed, whereas the UK evi-
dence on the wide variation of teacher effectiveness mirrors that in the US (Slater et al.,
2012). It seems likely therefore that the main mechanism generating greater inequality is
the sorting of the more effective teachers to the highest ability students. Unfortunately,
there is no historical data available to test this, and a comparison of the few contemporary
grammar schools in England may not be that relevant to this study.
We have shown that cohorts of students growing up in areas with a selective education
system experience greater earnings inequality once in the labour market. If higher earnings
inequality is coupled with socially graded access to grammar schools then it seems likely
that selective systems will also reinforce inequalities across generations. Previous analysis of
the impact of the grammar system as a whole, by Atkinson et al. (2006), suggested that this
is indeed the case. They found that access to grammar schools is heavily skewed towards
more affluent families even after taking into consideration prior attainment. High ability
children from low-income families are approximately half as likely to go to grammar school
as children of comparable ability from better off families (32% versus 60%). This finding
has been replicated more recently by Cribb et al. (2014), who find 66% of high achieving
children from better-off families attend grammar schools, while only 40% of similarly able
but lower income children do. Importantly for the debate around the merits of grammar
schools for promoting social mobility, these findings, taken with our findings, imply that
26 Authors’ calculations using the Annual Survey of Hours and Earnings, 2013. Percentile values of
hourly earnings for 1997–2013 available in Table 5 of ‘ASHE 1997 to 2014 selected estimates (Excel
sheet 408Kb)’ see: http://www.ons.gov.uk/ons/rel/ashe/annual-survey-of-hours-and-earnings/
2013-revised-results/index.html, last accessed 10 July 2018.
S.BURGESS,M.DICKSON,AND L.MACMILLAN 21
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while children from poorer families who make it to the grammar school do well—in exam
and earnings terms—those who grow up in selective areas but do not attend grammar
schools do worse than they would have done, had they not been schooled in a selective
area. Given the disproportionate numbers of low-income families whose children do not
make it to the grammar school, the implication is that the selective system is in fact regres-
sive with respect to social mobility.
There may, in theory, be positive effects of earnings inequality that may off-set some of
the negative effects identified here—a social welfare function may accept higher earnings in-
equality as a cost worth paying for generally higher earnings, for example. However, look-
ing at the mean earnings of those growing up in selective versus non-selective areas (which
are almost identical) there is no evidence of higher inequality being accompanied by
increased average earnings in this case. Moreover, though it is mostly only for the lower
percentiles of the distribution that the negative effect of the selective schooling system is
statistically significant, the point estimates are generally negative throughout the distribu-
tion up to the 60
th
or 70
th
percentile. Thus these findings suggest that the benefits of earn-
ings inequality are narrowly focused on those at the very top of the distribution. Setting up
a formal model to weigh the positive and negative effects of earnings inequality is beyond
the ambition of this article. Our contribution is to add a new fact to the debate on grammar
schools: selective schooling systems do appear to increase inequality.
Supplementary material
Supplementary material is available on the OUP website. The supplementary material com-
prises the replication files and the Online Appendix. The Appendix includes information on
the institutional background of the schooling system in the UK along with additional ro-
bustness tests, sample statistics and matching balancing tests.
The main data used in the analysis, from Understanding Society, is not provided as we
used a special licence extract: Understanding Society: Waves 1–2, 2009–2011: Special
Licence Access, study number 6931. This data can be applied for via the UK Data Service,
for further details of the access procedure see https://beta.ukdataservice.ac.uk/datacata
logue/studies/study? id¼6931#!/access.
The selectivity of LEAs was defined using Annual Schools Census data 1974–1983,
aggregated from school level to LEA level. The Annual Schools Census data is freely avail-
able here: http://discovery.nationalarchives.gov.uk/details/r/C7066.
These ASC files contain information on the number of pupils in each school, the type of
school, and the LEA of the school. This allows creation of the LEA level indicator of the
percentage of children assigned their school place by selection in each LEA in each year.
The authors would be available to assist further with this process should this be required.
A link file to match LEA code numbers in the ASC files to the area of birth codes in
the Understanding Society data is contained in the supplementary materials. Once created,
the LEA level selectivity indicator can be merged into the Understanding Society data using
the code contained in the replication file.
Bespoke data on political control of counties was provided to the authors by the elec-
tions centre: http://www.electionscentre.co.uk. The data used is uploaded in the supplemen-
tary materials.
All other data sets used in the analysis are provided in the supplementary materials.
22 DO SELECTIVE SCHOOLING SYSTEMS INCREASE INEQUALITY?
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Funding
This work was supported by the Economic and Social Research Council [grant number:
ES/H005331/1].
Acknowledgements
The authors gratefully acknowledge the helpful comments of the editor and two anonymous ref-
erees whose insights were invaluable in revising the article. Many thanks to Damon Clark for
compiling the data on selectivity of local education authorities, and to Colin Rallings for provid-
ing data on area-level political control. Thanks also to Stephen Jenkins, John Hills and John
Micklewright for their comments and to seminar participants at the Bristol-Bath applied micro-
workshop, the IOE Department of Quantitative Social Science, the University of Sydney, the
CASE Research Workshop and the EALE annual conference 2014 (Ljubljana), Social Policy
Association Annual Conference 2017 (Durham).
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