Decomposing Learning Inequalities in East Africa: How Much Does Sorting Matter?

Abstract

1. Introduction

Children in low- and middle-income countries face a wide range of educational and developmental challenges (Pritchett 2013; Black et al. 2017; Lu et al. 2020). Even so, average national conditions often mask considerable within-country variation, evidenced by large gaps in educational achievement along dimensions typically associated with household income inequalities (e.g., Watkins 2012; Behrman 2020). Inequalities associated with educational achievement feed into subsequent labor market inequalities, as well as longer-term differences in social mobility. And while the presence of such educational inequalities has motivated increasing calls for investments in public services, espoused by the UN’s Sustainable Development Goals to “leave no child behind,” the drivers of educational inequalities are still only partly understood, particularly in lower-income countries.

This article focuses on educational inequality arising from one potentially important yet understudied source: sorting between schools and households (pupils). While a vast literature attests that both household and school factors are key determinants of educational achievement (e.g., Coleman 1966; Björklund and Salvanes 2011; Hanushek and Rivkin 2012), these factors are unlikely to be independent. Various processes, such as residential segregation (Hanushek and Yilmaz 2007; Benabou 1993) or endogenous selection of teachers into schools (Pop-Eleches and Urquiola 2013; Hanushek et al. 2005), have been connected to differences in the quality of public goods. Sorting between households and schools—defined generically as the covariance in quality-adjusted inputs—may thus accentuate inequalities in educational opportunities. Where material, sorting may not only confound precise estimation of the unique contribution of individual factors of educational outcome, such as that of teachers or households, but it would justify enhanced attention to how existing inputs are distributed.

To date, the vast bulk of research on educational sorting pertains to richer countries. For instance, various studies have shown that children from disadvantaged families disproportionately attend lower-quality schools (Hsieh and Urquiola 2006; Nechyba 2006). While this may reflect a range of factors, including peer effects, the evidence suggests teachers serving schools in socioeconomically deprived areas tend to be less experienced or less qualified (Jackson 2009; Clotfelter, Ladd, and Vigdor 2011; Sass et al. 2012; OECD 2018). For the United States, Jackson (2013) shows that the quality of the match between teachers and children is economically important, representing around two-thirds the explanatory power of teacher effects with respect to student learning outcomes. Even so, the overall significance of these processes remains unsettled. Kremer (1997) argues that eliminating neighborhood segregation would decrease long-run educational inequality in the United States by less than 2 percent. In contrast, Fernández and Rogerson (2001) develop a model where enhanced sorting can have much larger effects on inequality (also Fernandez 2003), and data from Canada suggest that elimination of sorting either by home language or by parental education could reduce test-score variance by as much as 40 percent in some subjects, at least in locations where school segregation is substantial (Friesen and Krauth 2007).

In developing countries, indirect evidence indicates that educational sorting may often aggravate educational inequalities. A small literature supports the conjecture that children from disadvantaged backgrounds tend to receive lower-quality schooling inputs. For Guatemala, McEwan and Trowbridge (2007) decomposes the large achievement gap between indigenous and nonindigenous children, arguing this is predominately attributable to schooling attributes not family background. There are similar findings for other Latin American countries (McEwan 2004), but Vietnam stands out as providing a more equitable treatment of disadvantaged children (Glewwe, Krutikova, and Rolleston 2017).

Estimating the contribution of sorting to variation in educational outcomes presents a number of methodological challenges, especially where the factors of interest are incompletely observed. To address these, our first contribution—applicable in various domains—is to develop a new two-way fixed-effects variance decomposition procedure, which has some advantages over existing methods, especially in low-income country contexts where data are limited. Second, this procedure is applied to a large dataset on educational achievement, comprising over one million children in three East African countries. This analysis yields some of the first estimates of the impact of household–school sorting on educational inequalities, as well as the magnitude of the stand-alone variance contributions of household and school factors. Finally, we simulate the long-term gains for educational equality were the magnitude of sorting to be reduced.

A preliminary review of the East African data reveals a very substantial degree of spatial segregation in age-adjusted educational outcomes across communities: i.e., location matters for educational achievement. But even after controlling for this form of spatial clustering, the contribution of sorting of children across schools within communities is positive, accounting for around 8 percent of the total test-score variance. As such, almost a fifth of the joint variation in test scores due to systematic supraindividual circumstances—i.e., due to schools, communities, and households—can be attributed to sorting. Further analysis of heterogeneity suggests that the same sorting contribution tends to be larger among families at both the top and bottom ends of the socioeconomic distribution and among those sending their children to private schools, as well as in specific locations.

Our simulations show that for the average district in the region, the steady-state level of educational inequality would fall by around 15 percent if sorting between households and schools were fully eliminated and up to 30 percent if sorting across communities were also cut to zero. Roughly speaking, this would be equivalent to cutting the magnitude of the intergenerational persistence of education by more than half. Moreover, in a significant number of districts, the reduction in inequality from eliminating all forms of sorting would be over 40 percent of the total variance. Together, our results suggest that to be effective, educational policies in lower-income countries must counter the consequences of household sorting.

2. Drivers of Educational Inequality

At a most general level, the drivers of educational inequality encompass any factor that produces differences in learning outcomes across children. However, following Roemer (1996) who advocates for a focus on equality of opportunity as the most universally supported conception of justice in advanced societies, we narrow our attention to inequality of educational opportunity (IEO), defined as those factors beyond the influence of individual children that affect learning outcomes.

Without attempting to cover the vast literature concerning the different sources of IEO (for discussion see Reynolds and Teddlie 2000; Gamoran and Long 2007; Raffo et al. 2007; Watkins 2012), as a prelude to the remainder of the article, table 1 provides a selective sample of existing studies that shed light on the contribution of supraindividual factors to inequalities in test scores, where the studies were chosen to cover the predominant range of methods and (to the extent possible) consider developing country contexts. As Ferreira and Gignoux (2014) note, the variance is generally the preferred metric of dispersion in such accounting procedures. This reflects two attractive properties: the variance is ordinally invariant to standardization procedures often used to express test scores on a comparable scale, and the linear additive nature of the variance makes it straightforward to isolate the contributions of individual factors (Shorrocks 1982) and permits subgroup decomposability (Chakravarty 2001).

The studies in the table are classified according to four distinct methodological approaches. Panel (i) highlights studies that focus on a single main factor, such as households or schools. In most cases, these studies recognize that observed dimensions of the chosen factor (e.g., parental education or books per pupil) are partial, necessitating use of random (RE) or fixed-effects (FE) procedures that treat the specified factors as unobserved. Panel (ii) highlights two recent studies that take the fixed-effects approach further. Namely, based on a first-stage regression containing a single main unobserved fixed effect (classrooms), the authors are able to further partition each estimated effect into two or more subcomponents, focusing in particular on the “permanent” contribution of individual teachers. The studies in panel (iii) use mixed-effects estimators, which represent an alternative and popular means to estimate unobserved effects at multiple levels. But this necessitates making strict assumptions about the correlation structure of the unobserved factors, including their mutual independence.

The studies in panel (iv) relax this latter assumption, but do so by combining one unobserved factor (estimated via fixed effects) and proxying the other factor by observed covariates (OE). In so doing, they are able to estimate the covariance between the two factors (the sorting contribution; see below). For instance, in his analysis of rich test-score data from North Carolina, Mansfield (2015) finds that student background (which includes family and individual characteristics, as well as past performance) accounts for 60 percent of the variation in outcomes, while overall school quality (including teachers) accounts for about 6 percent and the covariance of these factors is also positive and similar in magnitude to the school effect at 4 percent of the variance.

Our classification underlines some of the persistent methodological challenges plaguing identification of the drivers of IEO. First, treating a factor as unobserved requires multiple observations for each element (index) of each factor. Data limitations thus explain why measures of the contribution of family background to IEO in developing countries have predominantly relied on observed proxies (Ferreira and Gignoux 2014). To our knowledge, in such contexts sibling correlations have only been estimated for income and educational attainment (e.g., Dahan and Gaviria 2001; Louw, Van Der Berg, and Yu 2007; Emran and Shilpi 2015), not learning outcomes. Second, while scholars have largely converged on value-added models to identify the causal effects of specific inputs within education production functions (see Todd and Wolpin 2003), these models cannot easily incorporate multiple high-dimensional unobserved factors. Under conventional OLS estimation methods, combining a lagged outcome with fixed effects introduces bias (Nickell 1981), which will only be negligible if a large number of observations (at least 20) are available to identify each unobserved effect. And in mixed-effects estimators, strict exogeneity of the (initial) unobserved effects must be assumed for value-added specifications to be consistent.

Third, from the perspective of estimating the contribution of sorting, existing studies must either rule this out by assumption or reduce one of the factors to its observed components, implying that only a partial view of this factor and its (co)variance contribution can be captured. For this reason, such models have rarely been used either to consider questions of sorting or to estimate the relative importance of different components of IEO. Historically, technical challenges in accurate estimation of multiple unobserved fixed effects have limited the development of more flexible models. Early on, Abowd, Creecy, and Kramarz (2002) showed that the joint contribution of two-way fixed effects can be obtained fairly easily (for implementation in Stata see Correia 2017). The drawback is that where the individual effects themselves are of direct interest, their pairwise correlation tends to be biased downwards. Andrews et al. (2008) demonstrate this is driven by a quasi-mechanical relation, whereby if one factor (e.g., household effects) is overestimated then on average the other factor (e.g., schools) is underestimated. And, as Jochmans and Weidner (2019) prove, this bias is larger where there is limited mobility or overlap of units across different effects, the limiting case being where their bipartite graph is disconnected.

Development of two-way fixed-effects estimators has focused predominantly on bias-corrections in the context of the contribution of workers and firms to the variance of log-earnings. Bonhomme et al. (2020), for instance, show that the variance contribution due to the sorting of workers across firms increases from around zero to 30 percent when bias corrections are applied. Even so, not only do these methods remain work in progress but also they demand rich (longitudinal) data, with a very large connected set of factors. In our case, this would require observations of members of the same household across multiple different schools, including connections that span different geographic locations. This kind of data is rarely available even in high-income countries (for an exception, see Thiemann 2018), motivating an alternative approach to identify sorting, addressed in the next section.

Before doing so, a comment on the findings summarized in table 1 is warranted. While it is inappropriate to compare effect sizes across studies, due to differences in tests, methods, and populations, it is nonetheless clear that variation in school (teacher) quality constitutes just one part of overall IEO. As also summarized by Hanushek and Rivkin (2012) for the United States, less than a quarter of the variance in test scores can be attributed to dispersion in teacher quality. In contrast, as stressed early on by the Coleman Report (1966), the home environment seems consistently of much greater importance, often accounting for more than half of the overall test-score variance (see also Björklund and Salvanes 2011). And this broad pattern appears to extend to lower-income countries, although previous studies have not covered both types of factors simultaneously.

3. Decomposition Framework

3.1. Preliminaries

To make this framework tractable for an empirical analysis of inequality, some structure must be placed on the IEO term f(·). With respect to the levels expression in equation (1), we adopt a simple additive linear model. However, without further assumptions, this specification does not pin down the (co)variance structure. To make this point clear, table 2 describes four alternative cases, where each row invokes specific assumptions about the level and variance of t. Row 1 invokes a zero-covariance assumption, corresponding to the most restrictive random-effects models described earlier: e.g., table 1, panel (iii). However, this effectively rules out a range of sorting processes, including residential segregation, school choice (by parents), and teacher allocation rules.

3.2. Methods

Interpreting upper-bound variance contributions as gross effects (including sorting) and lower bounds for the same factor as net effects (excluding sorting), a natural approximation to the overall contribution of the factor covariance is just their arithmetic difference. This is similar in spirit to approaches used to tighten estimated teacher-effect variance estimates (as in McCaffrey et al. 2009; Hoffmann and Oreopoulos 2009).¹ Formally, appendix S1 of the supplementary online appendix shows how to reexpress both the household and school lower-bound variance contributions in terms of their “true” effects: |$\sigma ^2_{\omega } = (1 - \rho _{hs}^2)\sigma _h^2$| and |$\sigma ^2_{\nu } = (1 - \rho _{hs}^2)\sigma _s^2$|⁠, where ρ_hs is the pairwise factor correlation.

3.3. Implementation

The ultimate objective of the variance decomposition is to estimate the three primitives. As already suggested, however, upper- and lower-bound estimates of household and school effects can be derived using separate one-way fixed-effect models. These directly permit calculation of the sorting approximation (equation (3)), and the correlation parameter can be derived in an additional step. Details of this procedure, which we refer to as indirect fixed effects (FEi), are set out in the supplementary online appendix S2.

An advantage of this procedure, which is useful for triangulation, is that it relies on a single estimation equation. A drawback is that the random effects are assumed to be orthogonal to the set of included covariates, implying equation (5) may remain misspecified.² Furthermore, while the variances of the random effects are estimated as model parameters, their associated best-linear-unbiased predictors (BLUPs or conditional modes) typically do not share the same variance–covariance structure as the estimated population-level moments (see Morris 2002). Consequently, the BLUPs may not be reliable for the purposes of investigating systematic patterns in the random effects (e.g., subgroup heterogeneity).³ Consequently, as an additional validation procedure, we extend the AM18 approach to incorporate fixed- as opposed to random-effects terms. As described in supplementary online appendix S2, this involves modifying the indirect estimation procedure whereby the sorting proxies are used directly to account for variation in test scores before estimation of the (one-way) household and school fixed effects. This procedure is denoted FEd.

4. Data

Since 2010, the Uwezo initiative has undertaken large-scale household-based surveys of academic achievement in Kenya, mainland Tanzania, and Uganda.⁵ The surveys target children residing in households aged between the official starting-school age and 16 and are representative at both national and district levels. Excluding the initial surveys, five rounds of the Uwezo surveys are publicly available (2011–2015) and used here. For each household, the surveys collected information covering general characteristics, as well as the demographic and educational details of resident children (e.g., age, gender, whether or not attending school). Also, all children of school age were individually administered a set of basic oral literacy and numeracy tests, which were tailored to each country and varied by survey round based on a common template, to reflect competencies stipulated in the national curriculum at the grade 2 level.

Importantly, the Uwezo tests are not adapted to the children’s ages or their completed level of schooling. Given that they focus on basic competencies, there are strong age-related differences, which affect both the level and variance of scores between age cohorts. Consequently, we exclude children above 14 years old since they tend to perform at the upper end of the tests (and show much lower variance). Our analytical sample also excludes observations that can be perfectly predicted using either household or school fixed effects: i.e., singletons have been removed. Table 3 summarizes alternative metrics of learning for this sample, pooling data from all countries and rounds. The first part shows the raw literacy and numeracy test scores, described in detail in Jones et al. (2014). The literacy tests refer to the national languages of instruction in which pupils are tested at the end of primary school: i.e., English and Kiswahili in Kenya and Tanzania, and just English in Uganda. For consistency, we then take the main language as the overall literacy score, which is combined with the score in math to give the overall mean.

Simple averages of scores on different tests may provide poor guidance to underlying levels of ability, particularly where tests are composed of questions of variable difficulty ( Bond and Lang 2013). Thus, we use two other approaches to combine the information on math and literacy into an overall test score. First, we take the first principal component of the suite of tests answered by each child (denoted PCA); second, in line with recommendations in the literature, we apply a graded response IRT model to the same tests, where the empirical Bayes mean of the latent trait is taken as the metric of achievement (ability).⁶ Since neither the PCA or IRT scores have a natural scale, for each country and survey round we standardize them to have a mean of 0 and standard deviation of 1. These scores are shown in the second part of table 3. Notably, they are extremely highly correlated with one another and with the overall mean (correlation >0.90).

Since the same Uwezo test forms are administered to children of all ages in each household, there is likely to be remaining between-cohort variation in test scores. From the present perspective, however, this can be considered unwanted noise (see Mazumder 2008). Thus, to ensure the score standard deviations are constant across cohorts over time, we further standardize the overall scores by age group within each country and survey year. These scores are shown in the final part of table 3. They continue to be highly mutually correlated and, reflecting their attractive theoretical properties and widespread usage, we focus on the IRT scores henceforth.

Table S4.2 in the supplementary online appendix further reports regional means and standard deviations of the raw and IRT test scores for the analytical sample. The first column reports the simple means of the raw competency tests (ordinal scores), column (2) reports the IRT scores standardized by country and round, but not age, and column (3) reports the final measures, including age standardization. As can be seen, movement from the second to the third metric constitutes a simple monotone transformation. Also, as per the methodological discussion of the Methods section , the rank position of each region according to its test-score variance is largely preserved, regardless of the transformation applied.

To implement the decomposition procedures, household and school indexes must be defined. The former is trivial: unique indexes are ascribed to all siblings in the same household (in each year).⁷ The school effects are less straightforward. In the present data, limited information about schools is provided. Nonetheless, we know the kind of school attended (none, public, or private) and whether or not children attend the specified main public school in their local community (catchment area). Consequently, for each enumeration area, we categorize children into one of four school categories: (1) those not attending school; (2) those attending the main local public school, which we denote as “matched”; (3) those attending other public schools; and (4) those attending private schools.

The advantage of our definition of school effects is that, within each household, children can be mapped to different school effects: i.e., the school and household effects are crossed. The main downside is that for the last two school categories we do not identify which specific school they attend. Further, the first category is composed of a mix of children that either never enrolled or dropped out. Recognizing that estimates of the school effects for these three groups are likely to be noisy averages of multiple underlying effects, unless otherwise indicated we present our main results for the matched group only. In doing so, however, we first run estimations on the full sample (e.g., to ensure household effects are identified correctly), but then report variance decompositions for the chosen subgroup.⁸ Full results are also presented for comparative purposes.

Further descriptive statistics for the dataset are reported in table S4.3 in the supplementary online appendix. This shows the number of unique children (i), households (j), and schools (k) covered in the dataset. Additionally, the table reports summary statistics, including average child characteristics and schooling status indicators (those out of school, the shares attending the specific matched public schools, and those attending private schools). Overall, these indicate the sample is comprehensive and balanced (by age and gender).⁹ It also reveals there are systematic differences in schooling among countries as well as across regions within each country: e.g., in all countries enrolment rates differ substantially across regions (e.g., from 80.0 to 96.5 percent in Kenya), as do the shares of children attending private school.

5. Results

5.1. Spatial Clustering

Motivated by our interest in sorting, we begin with a preliminary review of the degree of spatial clustering or segregation: i.e., the extent to which similar types of children are found in the same schools or communities. To do so, we compare the correlation in educational outcomes between individuals within different aggregate units, which is equivalent to the proportion of the variance attributable to the between-group structure of the data (for similar exercises see Fryer and Levitt 2004; Friesen and Krauth 2007, 2010; Lindahl 2011; Emran and Shilpi 2015). The magnitude of the correlation across members of the same group, and how quickly this declines as we move to higher levels of aggregation, thus indicates the extent to which variables are spatially segregated (clustered). For instance, if local communities only contained households with exactly the same socioeconomic status, then the proportion of variance in socioeconomic status accounted for by communities would be equal to that accounted for by households, indicating a very high degree of clustering.

Results from this exercise are reported in table 4, covering a range of variables and using the full sample of children. As might be expected, assuming child gender is approximately random, the between-group variance share accounted for by households is extremely low. For the remaining variables, however, clustering by households, schools, or communities is much higher. For instance, more than two-thirds of the variation in access to clean water is accounted for both by schools and by communities. Overall, a little more than half of the total variation in aggregate socioeconomic status in the region (SES) is attributable to (average) differences between distinct communities, implying substantial levels of residential clustering or economic segregation.

Turning to the educational outcomes at the bottom of the table, we observe somewhat lower but nonetheless substantial magnitudes of clustering across communities and schools, in part reflecting variation in schooling status between children within households.¹⁰ In terms of achievement on the Uwezo tests as measured by the age-adjusted IRT scores, the correlation between siblings is almost 50 percent, which is highly comparable to magnitudes found in a range of other countries (see Decomposition Framework). More notably, however, the correlation between pupils attending the same schools, as well as between children in the same communities, is only moderately smaller. Nearly 40 percent of the overall variation in achievement is accounted for by the schooling effects, and 30 percent between distinct residential locations. And although the definition of communities is not equivalent across studies, these latter magnitudes appear to be a factor larger than encountered in developed countries. That is, the degree of clustering of both economic and educational outcomes in East Africa appears to be large.

5.2. Variance Bounds

Moving to the variance decomposition, table 5 presents results from the upper-bound models for households (HUB) and schools (SUB), estimated using separate one-way fixed-effects estimators (the FEi approach) as described in supplementary online appendix S2. Panel (a) focuses attention on the subsample of individuals attending the matched public school, and panel (b) refers to the full sample. To account for observed individual-level covariates, such as gender, grade-for-age, birth order, and whether they have ever attended school, these variables are added to the factor models, and their combined variance contribution is calculated manually from the corresponding estimates, denoted the “individual” effect. Given that both these and the community-level effects are estimated before extracting the separate contributions of the unobserved factors, their variance shares are fixed across the two models: i.e., following the section Decomposition Framework, the difference between the household and school models only concerns where the factor covariance is attributed. Both absolute and relative variance contributions are reported in the table, where the former is reported in standard deviation units (×100). Standard errors are calculated via a clustered bootstrap procedure.

Three immediate findings merit comment. First, our models are able to account for about half of the variation in test scores. This is broadly consistent with studies elsewhere (see below), but confirms most variation in outcomes occurs between children in the same household. Second, as expected following table 4, while the community effect is sizeable, both the household and school upper-bound variance contributions are large. For the full sample these represent 32 percent and 20 percent of the total variance, respectively; however, in the matched sample, the school effect contribution drops to 13 percent. This gap implies almost half of the variation associated with schooling relates to differences across types of schools, including not being enrolled, a point to which we return below. Even so, the variation between matched public schools remains sizeable: a 1 standard deviation increase in school quality corresponds to a 0.34 standard deviation improvement in test scores.

Last, the (upper-bound) approximation to the sorting component is highly material. For the matched sample this equals 13 percent of the variance, or 16 percent for the full sample. These magnitudes are far from trivial, being just marginally smaller than the upper-bound estimates for the school effects or about half the upper-bound household effect contribution. According to the Uwezo data, an additional year of schooling is associated with an approximate 0.18 standard deviation increase in a child’s test score ceteris paribus. Against this benchmark, a shift of 1 standard deviation in either the quality of (public) schools or degree of sorting would be roughly equivalent to about two years of schooling. However, since this estimate of the sorting term is expected to be biased upwards, we now turn to results from the full decomposition.

5.3. Complete Decomposition

Using these lower-bound estimates, table S4.4 in the supplementary online appendix reports estimates for the three primitives required to identify the within-community sorting component. It also sets out the corresponding estimates from the two other empirical methods, based on AM18 (see Methods; also supplementary online appendix S2): namely, the MLM and the FEd approaches.¹¹ Together these form the basis for the complete decomposition, the results of which are reported in table 6 for both the matched and full samples. The relative contributions of the different constitutive components to total IEO, defined as the overall variance contribution of systematic components above the level of the individual, are further illustrated in figure 1.

Figure 1.

Variance Components (in Percent of Inequality of Opportunities), Alternative Methods, All East Africa

Source: Authors’ elaboration.

Note: Bars indicate the percentage contribution of each factor to inequality of educational opportunity (IEO), which is the variance accounted for by systematic supraindividual factors (households, schools, communities plus their covariance); matched subsample refers to children attending the main local public school in each location; abbreviations for methods: FEi is indirect fixed effects, MLM is the mixed-effects model, and FEd is direct fixed effects (FEd).

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As can be seen from the primitives, the three decomposition methods yield highly consistent results and, hence, the different methods provide similar estimates for the various final variance components. Despite some differences in precise magnitudes, discussed further below, this suggests the present results are robust to the method chosen (e.g., mixed versus fixed effects) and, more specifically, that our simple indirect approach (FEi) performs very adequately. In the full sample, we find a positive correlation between the household and school effects, ranging between 0.32 and 0.43. Consequently, the derived within-community sorting component, shown in table 6, remains substantial and is often similar in magnitude to the stand-alone contribution of schools. And although the estimates for this component are all lower than the earlier approximation (as expected), they nonetheless confirm that within-community sorting makes a nontrivial contribution to the total variance in test scores, equal to around 8 percent.

Five further points stand out. First, as before, the primary difference between the matched and full sample estimates refers to the contribution of schools. And, as this variance component feeds into the sorting component, the latter also remains somewhat smaller in the matched sample. The main implication is that sorting of children from distinct types of households across different types of schools, as well as at the extensive margin of schooling, is a material aspect of the overall covariance between household and school effects.

Second, differences between the three empirical methods appear to derive from two main sources. On the one hand, some of the differences for the correlation and sorting components reflect the sensitivity of calculations based on equation (4). Recall we estimate ρ_hs from the household- and school-effect lower bounds. Thus, even minor differences in either of these components, such as estimates for school effects under the FEi procedure, influence the estimates for the correlation term.

On the other hand, the mixed- and fixed-effects approaches treat the community effects in a slightly different fashion. In the latter case, community effects are removed from the joint fixed effect (households plus schools) in the first of the series of orthogonal projections (supplementary online appendix S2). As such, and in similar fashion to the upper-bound models discussed in Decomposition Framework, the estimated community variance contribution will capture both the direct effect of shared community-level factors on outcomes (e.g., via environmental conditions) plus any covariance with either household or school factors. Thus, any possible sorting of households (or teachers) across different communities will be absorbed by the community effect.¹² In the mixed-effects approach, all terms are estimated simultaneously, meaning that a strict distinction between within- and between-community components is not enforced ex ante. Although we implement a correction for this to obtain the uncorrelated school and household components (see above), this methodological difference is likely to explain some of the disparities in our estimates of the community effect and the uncorrelated variance components. However, overall, the qualitative differences in the results from the different approaches are trivial.

Third, in absolute and relative terms, the stand-alone contribution of schools might be deemed moderate, representing no more than 10 percent of the total variance and even less for the matched sample (7 percent). However, these magnitudes are not small when compared with school-effects estimates in the literature (see table 1). Also, AM18 estimate that both school and community effects jointly explain around 5 percent of the variation in high-school graduation rates (lower bounds) in the United States. Here, schools alone account for roughly the same amount of variation in achievement, and combined with community effects the joint contribution is nearly 20 percent (table 6). Similarly, the joint contribution of schools and communities taken from the school upper-bound estimates (table 5), which are generally more directly comparable to estimates found elsewhere (e.g., Freeman and Viarengo 2014) are substantial. Our estimates for East Africa place this joint effect at around 25 percent, which is similar to the average school-effect variance contribution calculated by Pritchett and Viarengo (2015) for a range of countries. Thus, while the present results show some similarities with findings elsewhere, the material contribution of residential location within the joint school/community effect stands out.

Fourth, as partly indicated, while all sources of inequality are substantial, systematic environmental and institutional factors that lie at levels above the household clearly merit consideration in the assessment of IEO. As shown in figure 1, the combination of schools, communities, and sorting is typically greater than the household contribution alone, accounting for around half of the total IEO. Not only does this reinforce our interest in quantifying multiple sources of IEO simultaneously, but also, assuming that household-based inequalities are generally persistent, it suggests the scope for policy measures to reduce such inequalities are substantial.

Last, we recognize the residual component remains large, accounting for roughly 50 percent of the test-score variance. On the one hand, this may well reflect the limitations of our explanatory variables. For instance, we do not measure the extent to which children within the same household receive different parental inputs, nor do we capture differences in the quality of teachers within each school. These factors will effectively remain in the residual, thereby implying we may be underestimating the magnitude of IEO, which underlines the importance of the research agenda on measuring teacher effects (e.g., Buhl-Wiggers et al. 2018; Bau and Das 2020) and variable household inputs (e.g., Das et al. 2013). On the other hand, a large residual is not inconsistent with substantial differences in ability and effort, as well as other idiosyncratic factors at the individual level. Indeed, studies elsewhere suggest these effects are likely to be highly material (see Troncoso, Pampaka, and Olsen 2016, table 1). For instance, on the PISA tests, Zamarro, Hitt, and Mendez (2019) find that around a third of the cross-country variation in scores might be explained by variation in effort across countries. Put differently, a large residual confirms that not all outcome inequality necessarily reflects opportunity inequalities.

5.4. Heterogeneity

Averages can often hide substantial heterogeneity. Thus, to look behind the pooled results, we take advantage of the properties of the variance and calculate the decomposition for specific subgroups. These results are presented in table 7, where we stratify individuals along various dimensions: gender, age group, schooling effect category, and household SES quintile. For simplicity, and given the broad consistency across the empirical procedures, hereafter we only present results for the direct fixed-effects method. This is chosen as it gives variance component estimates that lie mostly in between those of the two other methods (e.g., see table S4.4 in the supplementary online appendix).¹³

Focusing on the main insights, there large differences in the variance components over the subgroups.¹⁴ Nonetheless, the four explained variance components above the level of the individual are all generally larger for younger children as well as among children who are not in school. Recall that the school effects treat all children within each community who are not enrolled as a separate category. Thus, the variance decomposition for the various categories of enrolled children captures variation between schools within each category, while results for the subgroup of nonenrolled children captures variation in environmental effects outside the schooling system. In this sense, as the correlation coefficient and the school effects are largest in the nonenrolled category, this suggests schools do play a role in reducing inequality of opportunity. At the same time, among the three school-type categories, the contribution of variation between schools is moderately larger in the private sector. While this may reflect measurement error, it may also reflect differences between lower- and higher-cost private schools, where these segments serve children of quite different backgrounds.

A related form of heterogeneity runs along spatial lines, which is particularly relevant from the perspective of pursuing geographically targeted interventions. Here, an advantage of the Uwezo data is that we can run the same analysis at the district level. Figure S5.1 in the supplementary online appendix plots the cumulative empirical district-level distributions of the relative variance shares for the four main IEO components taken from the FEd estimates, by country. These show substantial variations across all components within each country, but country-specific differences are also evident. The structure of (relative) IEO appears most distinct in Tanzania, where the contributions of communities, sorting, and households tend to be much larger (on average). Even so, within countries, the variance contributions of the different components all display a wide range in comparison to the mean.