Selective Schooling Systems Increase Inequality

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, representative household panel survey to compare adult earnings inequality of those growing up under a selective education system with those educated under a comprehensive system. Controlling for a range of background characteristics and the current location, the wage distribution for individuals who grew up in selective schooling areas is quantitatively more unequal, and the difference is statistically significant. The total effect sizes are large: 14% of the raw 90-10 earnings gap and 18% of the conditional 90-10 earnings gap can be explained by differences across schooling systems.


Introduction
One of the key roles of any education system is to define the mechanism that assigns children 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 students 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. Nevertheless, grammar schools continue to be a prominent policy issue in England. There is a parallel debate in the US about elite or exam schools.
Much of the research on grammar schools has focussed 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 focussing on the system as a whole, namely comparing the outcomes of one student assignment mechanism (by ability) with those of another (choice). That is the contribution of this paper: we examine the impact of a grammar school system on earnings inequality.
We use data from a large and representative household panel dataset and compare the spread of the earnings distribution in middle age. The richness of the data means that we can control for the parental background of the individual, as well as the current labour market status and location of the individual. We also know where the 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 categorise respondents as grammar school system students or not, and to compare the earnings distribution they experience as adults.
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 non-selective counterparts. For those at the bottom of the earnings distribution, those growing up in a selective system earn significantly less than their 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 percentiles in selective systems 2 accounts for 14% of the total raw 90-10 earnings gap and 18% of the conditional 90-10 earnings gap.
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 three. Our empirical approach and the data used are outlined in section four and our results are presented in section five. We end with some brief conclusions.

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 courseswhich 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 longer-term impacts on labour market outcomes and reduced fertility. For men there were no long-term impacts identified. Abdulkadiroglu, Angrist and Pathak (2011) and Dobbie and Fryer (2011) assessed the impact of attending exam schools in Boston and New York on attainment and test scores. Both studies 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 3 school type with the political power of the Local Education Authority (LEA) at the time, arguing that the political 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, Maurin and McNally (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 identify 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 estimates provide a assessment of the impact on the whole distribution. Guyon et al. find substantial positive impacts of the increased grammar attendance on average examination 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 little about differences across selective and non-selective systems. Closer to our study are those of Atkinson, Gregg and McConnell (2006) and Jesson (2000), who use data from the more recent 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 nonselective LEAs. While Jesson (2000) is open to the critique of Manning and Pischke (2006) that value-added alone does not remove selection bias, Atkinson, Gregg and McConnell (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 comparing prior attainment in the matched LEAs, this is very 4 4 similar. While neither study finds evidence of higher attainment across selective and nonselective systems as a whole, Atkinson, Gregg and McConnell (2006) find that grammareducated 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.

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, the '11+'.
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 students 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. We therefore consider the differences in outcomes between two systems where, in their simplest form, one allocates pupils to schools based on ability 2 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 σ 2 a and σ 2 r ; they are positively correlated with covariance σ ar .
The schooling outcome, s, for student i depends on ability, school quality, q, and peer group ability, ̅: Later adult earnings depend on both the ability of the student and her schooling outcome: where γ is the relative weight on schooling.
To determine the relative impacts of the alternative schooling systems on earnings inequality, we must evaluate how each system translates ability into outcomes and therefore what each system implies for ̅(a) and q(a)that is, how each system relates student ability to peer group ability and to 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 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 these nearby houses are valued more highly 3 and so the likelihood of admission to the higher performing schools depends on family resources, r.

Grammar systemassignment through selection on ability
By definition, grammar school systems sort pupils based on their ability: so ̅(a) will be positive and very strong. Schools with high ability pupils are attractive to high ability teachers, hence we assume grammar schools attract and retain high quality teaching staff, hence q(a) will be positive and strong.
s i =s(a i , ̅ i (a i ), q i (a i )) =s g (a i ) and earnings will be: ( )

Comprehensive systemassignment 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 parental resources: q(r). As a covariance exists between r and a, we can write this as q(r(a)). This also 6 induces variation in peer groups, so ̅(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 r and a rather than directly as in the grammar system. s i =s(a i , ̅ i (r(a i )), q i (r(a i ))) =s c (a i ) and earnings will be: ( ).
Using these, we can express the variance of earnings in each system as: where k = g (grammar) or c (comprehensive). Consequently, var g (y) < or > var c (y) depending on whether ( ) < or > ( ) .
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.

Empirical analysis
To estimate the impact of selective systems compared to non-selective systems we would need to be living in an ideal world. 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 their education, both sets of individuals go on to work in the same labour market. A comparison of the distribution of wages amongst those who grew up in the selective system with the distribution for those who grew up in the nonselective system, would tell us something about the impact of selective schooling on the whole distribution of wages.
Unfortunately such a 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 empirically test our model, we need to be able to compare the distribution of wages for individuals who grew up in LEAs 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 7 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 and 51 and so are of prime working age.

Defining selectivity
We begin by defining LEAs of birth as selective or non-selective. Selectivity of an area is calculated 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 has been very little further comprehensivisation (see Crook, 2013) and so we make the assumption that the proportion of selective school places within an LEA has remained similar to the 1983 level henceforth. 6 We do not model the process by which LEAs retained or 8 abandoned selective schools. It is likely to have been influenced by fixed factors such as the size and 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 Figure 1, given the distribution of levels of selectivity, these thresholds mark a clear delineation between what were selective and non-selective areas. Table 1 illustrates the distribution of selectivity in LEAs across the time period considered. 43% of LEA*time observations were 100% non-selective. Of those with any selectivity, 65% had greater than 20% selective schools within the LEA and 60% had greater than 30% selective schools. We consider whether our results are sensitive to these cut-offs at the end of the results section.

Matching
Having defined selectivity, we proceed by matching selective and non-selective LEAs on the basis of labour market and school market characteristics: the local unemployment rate 7 , the local male hourly wage rate 8 and the proportion of children who attend private schools in the area 9 . We select the three nearest neighbour non-selective LEAs for each selective LEA with replacement and retain only matches that share common support. Individuals turned 13 in a number of different years in our data and hence the matching of LEAs is done separately for each year of our period of interest from 1974 to 1996. Following the matching, we retain individuals who grew up in one of the selective or matched non-selective LEAs. pupils in grammar schools increasing only 'very gradually' over the past 25 years, (see Figure 2: www.parliament.uk/briefing-papers/SN01398.pdf , accessed 12.51pm, 13th May 2014). 7 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. 8 Taken from the New Earnings Survey, 1974 to 1996, region and sub-region tables. The specific earnings 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. 9 Compiled using the National Pupil Database 2002. Results are robust to the exclusion of private schools from the matching process, see the appendix Figures A2a and A3a and Tables A3 and A4. 9

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 the majority of our data this is the case.
However, due to the non-availability of some of this informationin part due to the restructuring of local authority organisation during the 1970sthere is some limit to the time-variation in the local unemployment data. In our data, only eight of the 23 years that we include in our analysis are affected. In these cases, we have to assign the value for the nearest available year (which is a maximum of five years distance and in the majority of cases three or fewer). 10 Our results are robust to the exclusion of years in which the unemployment information has to be mapped from a nearby year (see Appendix Figures A2b and A3b,   Tables A3 and A4).
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 variable. 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) 11 , it is reasonable to assume that the local private school density has not changed too dramatically and thus our measure is relevant for matching. 12 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. where border crossing is most relevant, then our results are not likely to be driven by border crossing elsewhere which will be less prevalent.
We also argue that border crossing is likely to understate our findings to the extent to which border crossing across systems is made by 1) those that are the most able in non-selective systems crossing borders to attend grammar schools and 2) those who do not make it into grammars in the selective areas crossing borders to attend comprehensives rather than secondary moderns. In the first case, these individuals will push up the top end of the nonselective earnings distribution if grammars increase earnings relative to comprehensives 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 underestimate the effects of the selective system at the top and the bottom of the earnings distribution.
To consider the second 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 extent 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 7 in the MCS, both at Government Office Region (GOR) level. The NPD provides information on moves from age 5-11 at the postcode level and Travel to Work Area (TTWA) level. As can be seen from Table 2, the vast majority of families do not move during childhood with 10 per cent moving to a different postcode in the NPD data and 1 per cent moving to a different travel to work area. The data from the cohort studies suggests that while more families move before children start school, the numbers moving are still small with 8.6 per cent in the BCS and 5.5 per cent in the MCS moving before the cohort member is 5.
<<Insert Table 2 here>> 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 example, if selective LEAs were typically more unequal 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 selective 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, this varies slightly by the type of system enrolled in with 56.9% of those growing up in selective LEAs moving while 43.8% of those growing up in non-selective LEAs move. We therefore argue that we have enough variation in our data to be able to separate the effect of the school system from the effect of the LEAs' labour market characteristics.

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 unemployed or long-term sick or disabled at the time of the survey 13 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 observations 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 individuals' earnings. Sixty-five per cent of the main estimation sample (1,621 of 2,511 individuals) 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 is the average hourly wage of individual i in LEA r, , 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 is a gender specific quadratic in age. This ensures that in our baseline specification we are comparing the earnings of similarly aged males and similarly aged females. (1) In addition to the effects of age and gender, there are other factorsunrelated to schoolingthat may affect current wages. In our second specification (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. 15 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.  Figure 2 illustrates the impact of selective schooling across the whole distribution, 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 14 Appendix Table A5 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. 15 As we are removing a constant the results hold for non-mean-adjusted earnings. Note the average earnings are not significantly different across groups indicating a good match. 16 We implement the sqreg command in Stata, which provides bootstrapped standard errors.

Results
distribution. 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 earnings distribution, this is reversed.
<<Insert Table 4 here>> <<Insert Figure 2 here>> Panel A of Table 5 presents the simultaneous quantile regression estimates corresponding to Figure 2. These estimates show that the differences between the distributions are statistically significant at the 10 th percentile, the 50 th percentile, the 75 th percentile and the 90 th percentile. <<Insert Table 5   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 £2.21/hour, or 18.0% 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.

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 8 Table 8 shows that the differences in inequality for both males and females in the conditional model also mirror those seen in the pooled sample (19.6% of total 90-10 gap for males and 13.2% 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 really particularly evident 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.

Robustness
Given that we only observe the LEA that individuals lived in at birth, rather than the LEA that they attended school in, we repeat our analysis from Tables 5 and 6 excluding London.
We argue that if our results are robust to the exclusion of London from the analysis, it is unlikely that our results are driven by children crossing borders into selective systems when we classify them as non-selective and vice versa. Figure 6 replicates Figure 3, our conditional model, for this more restrictive sample (full results reported in Appendix Table A1). Table 9 presents the differences in the effect sizes found at the 90 th and 10 th percentile and 75 th and 25 th percentiles as seen in Table 6. The results are robust: Figures 3 and 6 are very similar and the total 90-10 and 75-25 earnings gaps found in Tables 6 and 9 are almost identical, suggesting that London is not driving the result. 18 <<Insert Table 9 here>> <<Insert Figure 6 here>> To test whether our results are robust to changes in the definition of selective and nonselective areas we redefine selective LEAs as those assigning more than 30% of places by selection whilst retaining the definition of non-selective as those that assign less than 5% by this method. Appendix Table A2 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 £1.76). Figure Tables A1, A2, A3 and A4 confirm the robustness of our results.

Conclusions
In this paper we have investigated the impact on earnings inequality of a selective education 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 became the norm. Despite 18 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. Controlling for a range of background characteristics and the current labour market, the wage distribution for individuals who grew up in selective schooling areas is quantitatively more unequal, with this difference being statistically significant. The total effect sizes are large: 14% of the raw 90-10 earnings gap and 18% of the conditional 90-10 earnings gap can be explained by schooling system. These results are robust to a wide range of specification checks.
Our modelling framework highlighted the roles of 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 evidence on the wide variation of teacher effectiveness mirrors that in the US (Slater, Burgess and Davies, 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. Setting up a model to weigh the positive and negative effects of earnings inequality is beyond the ambition of this paper. Our contribution is to add a new fact to the debate on grammar schools: selective schooling systems increase inequality.     Notes: 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.   Notes: earnings differentials estimated by testing the linear combination from the simultaneous quantile regressions. The effect size is calculated as the estimated difference divided by the total earnings differential in the sample.    Figure A2a: Deciles of the raw earnings distribution by schooling system type, robustness analysis 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. Source: Understanding Society. From top left: "Main estimates" (see Figure 2), "Excluding London" excludes from matching all London LEAs, "Matching without % private" excludes % of private schools from the matching criteria, "Selective >30% sample" defines an area as selective is 30% or more of places are assigned via selection (non-selective if fewer than 5% are), "Selective >30% sample, excl. London" as previous only excluding London LEAs from the matching. Figure A2b: Deciles of the raw earnings distribution by schooling system type, further robustness analysis 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. Source: Understanding Society. From top left: "Main estimates" (see Figure 2), "All obs." includes all of an individuals wage observations if they have more than one (max 2); "First ob." includes just the first wage observation of an individual; "No disabled/l-t sick" excludes the disabled and long-term sick from the non-earner category; "Years 1979-1993 only" only includes individuals turning 13 in these years. Figure A3a: Deciles of the conditional earnings distribution by schooling system type, robustness analysis 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 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. Source: Understanding Society. From top left: "Main estimates" (see Figure 2), "Excluding London" excludes from matching all London LEAs, "Matching without % private" excludes % of private schools from the matching criteria, "Selective >30% sample" defines an area as selective is 30% or more of places are assigned via selection (non-selective if fewer than 5% are), "Selective >30% sample, excl. London" as previous only excluding London LEAs from the matching. Figure A3b: Deciles of the conditional earnings distribution by schooling system type, further robustness analysis 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 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. . Source: Understanding Society. From top left: "Main estimates" (see Figure 2), "All obs." includes all of an individuals wage observations if they have more than one (max 2); "First ob." includes just the first wage observation of an individual; "No disabled/l-t sick" excludes the disabled and long-term sick from the non-earner category; "Years 1979-1993 only" only includes individuals turning 13 in these years.   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 residence and a selective schooling area dummy with the global mean of the residual removed. In all cases, year of survey effects are removed via an initial regression. Source: Understanding Society. Column (1) "Selective >30%, excluding London" defines an area as selective is 30% or more of places are assigned via selection (non-selective if fewer than 5% are) and excludes from matching all London LEAs; (2) "Matching without % private" excludes % of private schools from the matching criteria; (3) "All observations included per individual" includes two observations for those with two observations, clustering at the individual level; (4) "Just first observation per individual", includes one observation per individual, their first; (5) "Disabled/long-term sick not in non-earner category" excludes the disables/long-term sick from the estimations; (6) "Years 1979-1993 only included" uses only 1979-1993 as year individuals are age 13 since these are the years when the local wages and unemployment rate data are exactly contemporary, note this reduces the sample size substantially. 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. In all cases, year of survey effects are removed via an initial regression. Source: Understanding Society. Column (1) "Selective >30%, excluding London" defines an area as selective is 30% or more of places are assigned via selection (non-selective if fewer than 5% are) and excludes from matching all London LEAs; (2) "Matching without % private" excludes % of private schools from the matching criteria; (3) "All observations included per individual" includes two observations for those with two observations, clustering at the individual level; (4) "Just first observation per individual", includes one observation per individual, their first; (5) "Disabled/long-term sick not in non-earner category" excludes the disables/long-term sick from the estimations; (6) "Years 1979-1993 only included" uses only 1979-1993 as year individuals are age 13 since these are the years when the local wages and unemployment rate data are exactly contemporary, note this reduces the sample size substantially. Notes: also included dummies (84) for current county region. Parental occupation class groups refer to when the individual was aged 14 and the categories are: 1 "managers or administrators", 2"professional occupations", 3 "associate professional or technical occupations", 4"clerical/secretarial occupations", 5"craft and related occupations", 6 "personal/protective services", 7 "sales occupations", 8 "plant and machine operatives", 9 "other unskilled", 10 "missing". Omitted categories: born in comprehensive area, male, non-white, father and mother occupational class "other unskilled", father and mother education "no qualifications". An initial regression is run to remove the year of survey effects.