Great Equalizer or Great Selector? Reconsidering Education as a Moderator of Intergenerational Transmissions

Abstract

A long-standing consensus among sociologists holds that educational attainment has an equalizing effect that increases mobility by moderating other avenues of intergenerational status transmission. This study argues that the evidence supporting this consensus may be distorted by two problems: measurement error in parents’ socioeconomic standing and the educational system’s tendency to progressively select people predisposed for mobility rather than to actually affect mobility. Analyses of family income mobility that address both of these problems in three longitudinal surveys converge on new findings. Intergenerational mobility is significantly lower among high school dropouts than among others, but there are no significant differences in mobility across higher education levels. This is consistent with compensatory advantage processes among the least educated in which individuals from advantaged backgrounds use family-based resources to compensate for their lack of human capital.

Keywords

intergenerational stratification economic mobility educational attainment selection bias

Education plays a dual role as a mediator in intergenerational stratification processes. Because individuals from more advantaged social origins tend to attain more schooling than their less advantaged counterparts, education is an avenue of status transmission; but because many people from disadvantaged origins do achieve educational success and some from advantaged origins do not, education is also an avenue of mobility (Blau and Duncan 1967). Education’s role as a moderator of intergenerational processes is less clear. The issue is whether education alters direct intergenerational transmissions that operate through means other than schooling—for example, the transfer of wealth, genes, or cultural traits (Bowles, Gintis, and Groves 2005; Goldthorpe 2014).

Decades of descriptive analyses show that as educational attainment increases, intergenerational associations—the similarity of children to parents—in class and socioeconomic status decrease (Bernardi and Ballarino 2016; Breen and Jonsson 2007; Hout 1988; Pfeffer and Hertel 2015). This supports a long-standing consensus among sociologists that education has an “equalizing effect” that increases mobility by weakening the role of direct intergenerational transmissions. Several recent studies challenge this consensus, however, by showing surprisingly strong intergenerational associations among college graduates (Chetty et al. 2017; Witteveen and Attewell 2017; Zhou 2019) and graduate-degree holders (Torche 2011).

This study revisits education’s role as an intergenerational moderator. I follow recent work and focus on family income mobility (Torche 2011; Western, Bloome, and Percheski 2008; Zhou 2019). Family income captures economic differences within the occupations often used in past research to measure class or status, and it better incorporates family-level processes that affect economic status and mobility. I begin by distinguishing causal and spurious reasons that family income mobility might differ by education level. Causal explanations cast schooling and background-related resources as complements (as in cumulative advantage) or substitutes (as in compensatory advantage) in the attainment process (e.g., Bernardi and Ballarino 2016). Spurious explanations involve bias from selection or measurement error. In the first case, instead of education actually causing economic mobility, educational systems may “select” people who are predisposed for upward or downward mobility for other reasons (Zhou 2019). In the second case, transitory income fluctuations cause long-term income to be measured unreliably, especially when data provide few observations (Solon 1992). We know that both problems can introduce bias into intergenerational associations, but we do not know how this bias might vary across education levels and thus distort evidence of education’s presumed role as an equalizer.

This study is unique in examining education as an intergenerational moderator while addressing both measurement error and selection bias across the educational distribution. I use a Bayesian hierarchical modeling approach that provides reliable parent income estimates, adjusts for error in these estimates, and controls for observed individual attributes and unobserved family effects relevant to educational selection. I use data from three longitudinal surveys: the National Longitudinal Survey of Young Women (NLS-W), the National Longitudinal Survey of Youth 1979 (NLSY), and the Panel Study of Income Dynamics (PSID). Each has its own strengths and weaknesses, but together, they converge to provide new insights on the relationship between schooling and economic mobility.

Education as an Intergenerational Moderator: Theory and Evidence

Most mobility studies aim to reveal descriptive patterns of intergenerational similarity in class or socioeconomic status that reflect many stratification processes. Studies that explore educational differences in mobility yield a few typical patterns: Direct intergenerational associations decline as schooling increases, and they are often lowest among bachelor’s-degree holders (Bernardi and Ballarino 2016; Breen and Jonsson 2007; Hauser and Logan 1992; Hout 1984, 1988, 2018; Pfeffer and Hertel 2015; Torche 2011). Intergenerational associations appear relatively strong, however, among individuals with graduate and professional degrees (Torche 2011), with the possible exception of doctoral-degree holders (Torche 2018).¹

Does it matter whether these educational differences reflect education’s causal role as an intergenerational moderator? I assume it does if for no other reason than we cannot help ourselves from inferring causation. We do so when we talk about education’s “equalizing effect” (Zhou 2019), which we should distinguish from a descriptive equalization pattern. We also do so when evaluating theories, as when Breen and Jonsson (2007:1798) claimed that European educational expansion increased intergenerational mobility “because labor markets were more meritocratic the higher the level of educational qualifications.” And we do so when considering the real-world implications of empirical findings, as when Hout (1988:1391) wrote, “This finding provides a new answer to the old question about education’s overcoming disadvantaged origins. A college degree can do it.” Although this study is observational and has its own causal shortcomings, it will advance our understanding of how education might causally alter intergenerational transmissions by using rigorous efforts to address alternative explanations.

The moderation of interest manifests statistically as interactions between the effects of children’s social origins (parent attainment) and their education on their long-term attainment. The online Supplement Material provides a conceptual diagram (Figure S1) that adapts the familiar origin-education-destination triangle (e.g., Goldthorpe 2014) to illustrate potential sources of these interactions. Intergenerational associations could vary by education for two causal reasons: Social background may alter education’s effects on attainment, or education may alter the effects of background on attainment. Such interactions have a symmetry that permits both interpretations. This study, like those before it, cannot disentangle the two. Doing so will require testing specific mechanisms underlying these interactions. I aim to isolate either type from spurious alternatives.

Spurious reasons for why intergenerational associations vary with education concern education’s role as a selector—that is, how individuals select or are sorted into different levels of education with respect to qualities that precede high school completion and thus might confound subsequent schooling’s effects on socioeconomic attainment. Likely confounders are related to skills (Cunha et al. 2006; Farkas 2003), motivation (Sewell, Haller, and Portes 1969), and opportunity (Coleman et al. 1966). One possibility is differential selection, which occurs when confounders’ effects on schooling depend on (interact with) one’s social background or when background effects on schooling depend on confounders. Another is that confounders’ long-term effects on socioeconomic attainment depend on social background or that background effects on attainment depend on confounders.

Background and Schooling as Substitutes or Complements

Causal interpretations of parent attainment by schooling interactions correspond to the idea that education is either a substitute for or a complement to background-related resources or opportunities. The equalizer hypothesis implies a substitution or compensatory relationship. A common theoretical proposition along these lines is the notion that high-skill labor market sectors are more meritocratic than low-skill sectors (Breen and Jonsson 2007; Hout 1988). High levels of education supposedly funnel workers into high-skill sectors, where their social origins are relatively unimportant. This could be because schooling actually enhances important skills that substitute for background-related resources or merely because educational credentials signal that an individual likely has such skills (Goldthorpe 2014). Compensatory advantage theory attends more to people with little education, who may end up in less meritocratic sectors where their origins matter more, perhaps because family-based resources can compensate for a lack of schooling (Bernardi and Ballarino 2016). Brand and Xie’s (2010) negative educational selection hypothesis fits here as well; it suggests people who are unlikely to complete college reap the highest economic returns to a degree because they lack other substitutable resources.

Other theories counter that education and social background may be complements in the attainment process. Cumulative advantage (Bernardi 2014; DiPrete and Eirich 2006) and human capital theories (Becker 1964) share this perspective. Being raised in a socioeconomically advantaged family can promote early skill development that enhances learning in school (Sørenson and Hallinan 1977), thus providing incentives to continue further in schooling by heightening its returns (Cunha et al. 2006). Note the assumption of positive selection, which is characteristic of rational choice theories: Individuals who will benefit most from schooling are most prone to attend (Carneiro, Heckman, and Vytlacil 2011; Willis and Rosen 1979). There could also be interactions between the quality and quantity of schooling. If children from advantaged backgrounds attend higher quality schools, they might learn more than their less advantaged peers with the same amount of schooling, yielding a larger payoff (Heckman, Layne-Farrar, and Todd 1996).

There are also grounds to question the idea that high-skill labor market sectors are more meritocratic than lower-skill sectors (Goldthorpe 2014). It has the flavor of functionalist theories that have not fared well in the past. Most notably, the notion that industrialization increases mobility (Treiman 1970) found little empirical support in comparative studies of social fluidity (Erikson and Goldthorpe 1992; Featherman, Jones, and Hauser 1975); any equalizing effects of industrialization appear modest (Breen 2004; Breen and Jonsson 2007). Rivera’s (2012) research on elite professional service firms further challenges the notion of meritocracy in the high-skill labor market: Impressive educational credentials can get a candidate’s foot in the door, but getting hired depends on familiarity with elite status cultures.

Recent empirical findings add weight to any doubts these theories raise about education’s equalizing effects. As mentioned, Torche (2011) found stronger intergenerational associations for many socioeconomic outcomes among adults with graduate or professional degrees than among those with bachelor’s degrees. Moreover, several studies have found sizeable intergenerational associations among college graduates (Chetty et al. 2017; Witteveen and Attewell 2017), and Zhou (2019) found these associations to be similar to those among people without college degrees. A few earlier studies even found positive interactions between education and parent attainment when predicting wages (Altonji and Dunn 1996; Ashenfelter and Rouse 1998).

Bias from Educational Selection

Whether or not education causally moderates intergenerational processes, empirical patterns also depend on spurious sources of moderation. One is differential selection into schooling in ways related to social background, which is tied to the confounding of education effects. Consider separate regressions of child attainment (Y) on parent attainment (P) at two different levels (N for no college, C for college): Differences in the intergenerational associations confound a portion truly moderated by education, $β_{C} - β_{N}$ , with a spurious portion driven by differential selection bias, $\frac{Co v_{C} (p_{i}, u_{i})}{Va r_{C} (p_{i})} - \frac{Co v_{N} (p_{i}, u_{i})}{Va r_{N} (p_{i})}$ . This bias depends on differences across education levels in the association between parent attainment and confounders (U).

The implications for the equalizer hypothesis depend on differential selection across the entire educational distribution. Torche (2011) made important strides considering this problem. She suggested that at higher schooling levels, individuals from disadvantaged backgrounds are increasingly positively selected on things like ability or motivation relative to their more advantaged peers. If so, direct intergenerational effect estimates would become more negatively biased as education increased (also see Hout 2018). This could explain the common descriptive equalization pattern but not the heightened intergenerational effects among individuals with graduate degrees. As Torche (2018) later noted, however, the latter difference could be spurious if selection bias is less pronounced at the postbaccalaureate level than at the baccalaureate level. Suppose bachelor’s degrees are normative in socioeconomically advantaged families, so degree holders from advantaged backgrounds are less selected than their disadvantaged peers on things like ability and motivation. Advantaged youth would become more positively selected at the transition to postgraduate education, possibly even more so than their less advantaged peers who had already survived more stringent selection at prior transitions. Moreover, although usually overlooked, selection processes could also downwardly bias intergenerational associations at the lowest schooling levels, leading us to understate education’s equalizing effects. This would occur if high school dropouts from advantaged origins were especially negatively selected on ability or motivation compared to their more disadvantaged peers, which seems plausible.

Patterns of differential selection across education levels are difficult to predict, and so are the empirical consequences. Zhou (2019) made laudable efforts to account for confounders of bachelor’s degree completion using covariates available in the NLSY data. Zhou revealed similar intergenerational family income associations among people with and without bachelor’s degrees, but his study only focused on that particular distinction, obscuring patterns elsewhere in the educational distribution. Moreover, Zhou and others have noted the limits of addressing selection with observed variables alone: People unlikely to complete college based on observed variables but who nonetheless do may be exceptional on unobserved attributes that affect their attainment (Brand and Xie 2010; Breen, Choi, and Holm 2015).

Two economics studies examining background by schooling interaction effects on wages show how and why we might go further to address selection on unobserved confounders. Altonji and Dunn (1996) eliminated unobserved family-level confounders using family fixed effects (sibling comparisons), and Ashenfelter and Rouse (1998) eliminated even more confounders by comparing identical twins. Both studies found positive interactions between social background and education, consistent with disequalizing educational effects. Yet it is difficult to reconcile these findings with the sociological mobility literature, partly because they use parent education as the background measure and treat education as a continuous variable (years of school).

A less obvious source of spurious background by education interactions is the possibility that background-related resources moderate the effects of confounders, not the effects of education. Another is that confounders, not education, moderate direct background effects. The story here is similar to the prior causal explanations except things like skills or parental support rather than education would be the true substitutes for or complements to background-based resources and opportunities. Additionally, resources derived from a socioeconomically advantaged upbringing may moderate barriers faced by minorities, in which case, racial or ethnic disparities in schooling would create spurious interactions between parent attainment and education. Put simply, anything that influences schooling and is associated with socioeconomic background could be the true source of background by education interactions.

Measuring Attainment

Measuring attainment raises additional issues. Social origins and destinations are broad constructs operationalized in many ways. Sociologists often use occupational measures, which fit class schemas, are reliably reported, and are fairly stable among prime-age workers (Blau and Duncan 1967; Hauser and Warren 1997; Hout 1988, 2018). Yet these measures are difficult to aggregate at the family level and are often based on fathers’ occupations; this obscures variation in resources due to mothers’ attainment, and it presents problems when examining daughters’ mobility, which is affected by occupational segregation (Beller 2009). Occupational measures also obscure pay disparities within occupations, which are greater than between-occupation differences and fluctuate over time (Mouw and Kalleberg 2010).

Family income is an increasingly popular alternative because it accounts for inequality within occupational categories, and it accounts for processes that affect all family members’ well-being (e.g., family formation, resource pooling, household division of labor), which helps mitigate the challenges posed by gender differences in labor force participation and occupational segregation (Torche 2011; Western et al. 2008; Zhou 2019). The downside is that income is volatile over time, and transitory fluctuation introduces error into measures of long-term or “permanent” financial resources. Such error in the parent generation attenuates intergenerational associations.² The typical solution is to average as many measures of parent income as possible. As analysts have incorporated more measures, intergenerational elasticity estimates have climbed from around .2 to around .4 or as high as .6 (Mazumder 2005; Solon 1992).

Differences in parent income measurement error across schooling levels might distort inferences about the equalization hypothesis. This is easiest to show in a bivariate regression with classical measurement error, where errors are uncorrelated with true permanent income: The difference in intergenerational associations across schooling levels N and C is $β_{C} (\frac{σ_{rC}^{2}}{σ_{rC}^{2} + σ_{eC}^{2}}) - β_{N} (\frac{σ_{rN}^{2}}{σ_{rN}^{2} + σ_{eN}^{2}})$ . The $β$ s are the true associations, the $σ_{r}^{2}$ s are the true conditional variances of parent attainment, and the $σ_{e}^{2}$ s are the random-error variances of the parent attainment measures. Attenuation bias will be worse at education levels with more error relative to true variance in parent attainment. It is unclear which levels these would be.

Ideally, we could harness the conceptual advantages of family income while minimizing measurement error. A common approach restricts analyses to cases with a certain number of parent income measures. This is most effective in data with many parent income measures; it is problematic in data with fewer measures (e.g., the NLSY), requiring a trade-off of either using few parent income observations and risking more measurement error or requiring more measures but discarding cases at the risk of nonrandom sample selection bias. My modeling approach better addresses these measurement issues without dropping many cases. It not only eliminates transitory fluctuations, but it provides more reliable permanent parent income estimates and incorporates error in these estimates into intergenerational analyses.

Data and Measures

Data sources include the National Longitudinal Survey of Young Women, the National Longitudinal Survey of Youth 1979, and the Panel Study of Income Dynamics. The NLS-W includes cohorts born in the 1950s, followed 1968 to 2003. I only include the subset of NLS-W respondents with parents in the NLS Older Men or Mature Women surveys, which provide useful parent income information. Prior analyses have included their male counterparts (NLS-M; Altonji and Dunn 1996; Torche 2011); I exclude these men from the intergenerational analyses because they were not followed into their prime earning years. The NLSY includes cohorts born in the 1960s, followed 1979 to 2014. The PSID began with a sample of households in 1968 and has followed members and subsequent generations through 2015 as they formed new households. My PSID sample differs from that of Torche (2011), who only included cohorts born in the 1950s and kept a low-income oversample, which has elsewhere been deemed problematic; I keep subsequent cohorts born through the early 1980s but drop the low-income oversample.³ Supplemental analyses explore the implications of differences in sample construction.

As I will describe, the analyses involve two stages: The first uses models of parent income during childhood to improve its measurement, and the second incorporates parent income measurement error into intergenerational elasticity models.⁴ The parent income analysis includes all person-year observations with parent income data from ages 1 to 18.⁵ The intergenerational analysis includes all person-year observations with adult income data at age 30 or older, restricted to individuals with at least one parent income measure and with valid educational attainment data collected at age 25 or older.

Parent and child attainment are measured as log-transformed total family income, adjusted to 2010 dollars using the Personal Consumption Expenditures deflator. The PSID provides complete parent income data throughout childhood in some cases, the NLS-W provides up to five measures during adolescence, and the NLSY provides up to three during adolescence. I distinguish five categories of educational attainment: less than high school, high school (diploma or equivalent), some college, bachelor’s degree, and graduate or professional degree.⁶

The time at which income is measured is an issue in both generations. Parent income may have more of an effect at certain childhood stages than others (Carneiro and Heckman 2002; Duncan et al. 1998), and such differences could be problematic if the age of measurement is associated with socioeconomic background. Moreover, intergenerational associations tend to be strongest for outcomes in the prime earning years (mid-30s to mid-40s), so differences in the timing of adult income measures could be problematic as well (Haider and Solon 2006). I retain the year and age at each income measure to make appropriate adjustments in both stages of analysis.

I incorporate additional control variables to reduce selection bias. Ideally these would capture differences in skills, motivation, and opportunity. All surveys provide information on gender, race (white, black, other), number of siblings, and parent education (five categories). At best, these are proxies for likely confounders and do little to account for within-family differences. Unfortunately, this exhausts the controls in the PSID, which trades off its limited measures of confounders for superior parent income measurement. From the NLS-W, I also include adolescent cognitive skills (standardized achievement test scores) and occupational aspirations (Duncan’s socioeconomic index) as well as adolescents’ and their parents’ educational aspirations (highest grade). The main limitations of the NLS-W are the lack of noncognitive skill measures and the fact that achievement test scores are often missing (about 50 percent) and are based on different tests for different children. From the NLSY, I include adolescent educational aspirations and expectations, cognitive skills (standardized Armed Forces Qualification Test scores), and a delinquency scale (from a factor analysis of 17 self-reported delinquency/drug use items).⁷ For missing data on these controls, I incorporate imputation models into the analyses (described in the next section).

Methods

My analyses use Bayesian hierarchical models broken into two stages to speed computation. The first stage estimates permanent parent family income, and the second uses these estimates (including their error) in intergenerational models predicting adult income. I use the Stan platform (RStan 2.15.1), which uses Hamiltonian Monte Carlo sampling, an efficient simulation method for complex Bayesian models (Carpenter et al. 2017; Gelman et al. 2013). I use four sampling chains per model, each chain providing 1,000 post-warmup samples. Trace plots and scale reduction factors suggest convergence for all models (Gelman et al. 2013).

In the first stage, I fit the hierarchical model shown in Equations 1a to 1f. Time-specific log-parent income (P) is a function of an intercept and second-order polynomials for age and year ( X ; centered at age 14 and year 1960); random effects for individuals (i), families (f ), and PSID multigenerational clusters (k); and residual (transitory) variance (Equations 1a and 1b).⁸ Each random effect has a variance (Equations 1c–1e). Bayesian analyses require prior distributions for all parameters; I use weak priors (not shown), leaving enough uncertainty to ensure that the likelihood function (the data) dominates the priors.⁹ I estimate “true” parent income ( $P^{*}$ ) by summing the intercept and the individual, family, and cluster effects (Equation 1f); this adjusts for differences in the age and year of measurement and discards transitory error variance.

P ~ N (η, σ_{rt})

(1a)

η = γ_{0} + X γ + r_{k} + r_{f} + r_{i}

(1b)

r_{k} ~ N (0, σ_{rk})

(1c)

r_{f} ~ N (0, σ_{rf})

(1d)

r_{i} ~ N (0, σ_{ri})

(1e)

P^{*} = γ_{0} + r_{k} + r_{f} + r_{i}

(1f)

This approach should yield more reliable estimates than simply averaging available parent income measures, and it does so without dropping cases with few measures. The hierarchical model balances individual-specific information with information from siblings, multigenerational relatives, and the sample as a whole, all according to the precision at each level. More concretely, the fewer parent income measures for an individual, the more data from other family members is used to predict permanent parent income; the fewer measures from the family, the more data from the overall sample is used (and the more uncertainty there is).

At this point, each individual has a posterior distribution of true parent income with a mean ( ${\bar{P}}^{*}$ ) and standard deviation ( $σ_{P^{*}}$ ). To incorporate measurement error into the second stage, I treat the posterior means as draws from sampling distributions centered on the unknown true values ( $P^{*}$ ), with standard errors equal to the posterior standard deviations (Equation 2a). I model adult income ( $Y$ ) as a function of true parent income, education, parent income by education interactions, and a vector of controls ( Z ), all within a hierarchical structure analogous to that in the first stage (Equations 2b–2f), with weak priors on all parameters. I also include imputation models for missing covariates in these analyses (not shown). This avoids sample selection incurred by dropping cases and accounts for uncertainty in the imputations (Little and Rubin 2002).

{\bar{P}}^{*} ~ N (P^{*}, σ_{P^{*}})

(2a)

Y ~ N (μ, σ_{ut})

(2b)

μ = β_{0} + β_{1} P^{*} + β_{2} H S + β_{3} C o l l + β_{4} B A + β_{5} G r a d + β_{6} (H S \times P^{*}) + β_{7} (C o l l \times P^{*}) + β_{8} (B A \times P^{*}) + β_{9} (G r a d \times P^{*}) + Z β + u_{k} + u_{f} + u_{i}

(2c)

u_{k} ~ N (0, σ_{uk})

(2d)

u_{f} ~ N (0, σ_{uf})

(2e)

u_{i} ~ N (0, σ_{ui})

(2f)

The baseline model controls for the main effects of race, gender, and quadratic functions of birth year and age. Age, education, and (log) parent income are fully interacted to account for the effects of education and social background on age-earnings profiles. To maintain comparability with prior work and capture the peak earning years when intergenerational associations are highest, I report age-adjusted elasticities at age 40 (Haider and Solon 2006; Torche 2011; Zhou 2019). In addition to pooled analyses that assume no gender differences in covariate effects, I conduct separate gender-specific analyses.

I address the problems of educational confounding and selection as follows. After adding main effects of the available control variables, I include their interactions with parent income to account for differential selection into schooling and any complementarity or substitutability with social background. I include interactions between race and parent income for similar reasons and interactions between race and education to ensure that race-based moderation of education effects is not misattributed to parent income.

For the gender-pooled PSID and NLSY analyses, I also fit intergenerational models that add family fixed effects (FE) to the controls.¹⁰ These models replace the family and cluster random effects with fixed family-specific intercepts. Families include all children sharing either a mother or father. FE models use sibling comparisons to eliminate unobserved family-level confounders; they do not account for confounding related to sibling-specific attributes, although these models do so to the extent the available individual-level controls allow. I do not conduct gender-specific FE analyses, which only allow same-gender sibling comparisons and lack the power for precise estimates.

Adding controls and family FEs absorbs mechanisms of direct intergenerational effects; in other words, these controls and family effects may be endogenous to family background and create overcontrol problems when estimating the main effects of parent income. Zhou (2019) used reweighting methods to avoid this problem, but those methods do not easily incorporate fixed effects. In any event, this seeming overcontrol issue is not a problem for examining differences in intergenerational effects across schooling levels. As long as education moderates direct intergenerational effects and the mechanisms explaining this educational moderation are not controlled, the interactions of interest remain identified. Given this study’s goals, overcontrol problems would only arise from controlling for interactions between education and variables affected by parent attainment (e.g., cognitive skills, parental expectations).

Results

Descriptive Statistics and Parent Income Analyses

Table 1 summarizes the data used in both stages of the analysis. It also includes key results from the first-stage parent income analysis. Note that parent income is measured an average of only 2 to 3 times per person in the NLS-W and NLSY compared to more than 11 times in the PSID. Hence, adjusted log-parent income (estimated in the first stage and used in the second stage) is estimated less precisely in the NLS-W and NLSY; the posterior standard deviations are two to three times as large in these data (.29 and .24, respectively) as in the PSID (.12). Table 1 also includes variance estimates from the parent income models: 30 to 50 percent of the variance is transitory, and most of the remainder is between families, with almost none between individuals in the same family (e.g., siblings with staggered childhoods).

Table 1.

Summary Statistics.

	NLS-W			NLSY			PSID
Parent Income Analysis
Variables	Mean	SD	% Missing	Mean	SD	% Missing	Mean	SD	% Missing
Parent income (log)	10.46	.89	—	9.59	.85	—	10.90	.84	—
N measures	2.05	.94	—	2.68	1.37	—	11.68	5.85	—
Age	17.05	1.57	—	17.03	1.42	—	10.89	5.30	—
Year of birth	1951	1.42	—	1962	1.31	—	1967	11.00	—
Observations and Variances^a	N	Variance	% Share	N	Variance	% Share	N	Variance	% Share
Person-year (transitory)	6,155	.34	43.88	16,953	.22	30.69	60,332	.35	50.95
Individuals	3,006	.00	.26	6,327	.00	.00	5,393	.00	.00
Families	2,036	.44	55.87	4,571	.50	69.31	1,965	.20	29.37
Clusters	—	—	—	—	—	—	1,259	.13	19.68
Intergenerational Analysis
Variables	Mean	SD	% Missing	Mean	SD	% Missing	Mean	SD	% Missing
Log-income	10.88	.94	—	10.56	1.06	—	11.06	.92	—
Age	41.98	6.40	—	39.96	6.99	—	39.22	7.51	—
Year of birth	1952	1.08	—	1962	1.32	—	1964	9.85	—
Education
< HS	.11	.32	—	.13	.34	—	.19	.39	—
HS	.36	.48	—	.39	.49	—	.11	.31	—
College	.26	.44	—	.25	.44	—	.33	.47	—
Bachelor’s	.18	.38	—	.15	.36	—	.24	.43	—
Graduate	.09	.28	—	.07	.26	—	.13	.33	—
Parent income (log)^b
Posterior mean	10.58	.60	—	9.14	.65	—	10.92	.56	—
Posterior SD	.29	.07	—	.24	.07	—	.12	.06	—
Parent education
< HS	.43	.50	—	.35	.48	3.23	.21	.41	.45
HS	.32	.47	—	.39	.49	3.23	.23	.42	.45
College	.12	.33	—	.12	.32	3.23	.26	.44	.45
Bachelor’s	.08	.27	—	.08	.28	3.23	.17	.38	.45
Graduate	.05	.21	—	.06	.23	3.23	.13	.33	.45
Siblings	4.00	2.67	.66	3.80	2.61	.13	3.54	1.74	3.06
Black	.33	.47	—	.31	.46	—	.09	.29	—
Other	.01	.11	—	.21	.41	—	.02	.14	—
Female	1.00	.00	—	.48	.50	—	.51	.50	—
Cognitive skills	.21	.99	46.74	−.49	.93	3.73	—	—	—
Delinquency	—	—	—	.03	.81	7.72	—	—	—
Educational aspirations	14.05	1.89	—	14.29	2.19	.42	—	—	—
Educational expectations	—	—	—	13.74	2.21	.93	—	—	—
Parent educational aspirations	13.90	2.28	2.46	—	—	—	—	—	—
Occupational aspirations	53.30	18.50	29.71	—	—	—	—	—	—
Observations, N
Person-year	5,244			46,287			36,115
Individuals	1,057			5,260			3,982
Families	914			3,869			1,943
Clusters	—			—			1,252

Note: NLS-W = National Longitudinal Survey of Young Women; NLSY = National Longitudinal Survey of Youth 1979; PSID = Panel Study of Income Dynamics; HS = high school.

Parent income variances are estimates (posterior means) from Bayesian hierarchical models in the first-stage analysis.

Parent income estimates used in the intergenerational analysis are from the first-stage (parent income) analysis.

The online Supplemental Material compares the error-adjusted parent income estimates to the means of available measures in more detail. The correlations between the two are high (over .95), but the adjustments for measurement error entail some shrinkage toward the mean. This shrinkage is driven by imprecise estimates, especially individuals with very high or low averages based on only a few measures. The more uncertainty in the estimate, the more shrinkage. Not surprisingly, there is more uncertainty and more shrinkage in the NLS-W and NLSY than in the PSID.

Measurement Error

Before delving into the intergenerational analyses, it is worth noting a few findings related to measurement error. Figure 1 shows intergenerational elasticity estimates without conditioning on education, adjusted for only race, age, and year. It compares the Bayesian estimates that adjust for measurement error to maximum likelihood estimates that do not (they specify parent income as the average of available measures). As expected, elasticity estimates are lower without adjusting for error, especially in the NLS-W (.15) and NLSY (.29). The Bayesian estimates are much more in line with current knowledge (.4 to .5, although slightly lower in the NLS-W) without restricting the samples based on the number of parent income reports.

Figure 1.

Unconditional elasticity estimates.

Figure 2 better speaks to the implications for educational differences in mobility. In a sample of PSID cases with at least four parent income measures, I fit the baseline intergenerational model via maximum likelihood estimation (MLE) after specifying parent income as the average of either one, two, three, or four randomly selected parent income observations. As expected, using fewer measures attenuates the elasticities. More importantly, this attenuation bias differs across education levels. It is most pronounced among individuals who failed to complete high school. This suggests failure to account for measurement error may overstate mobility among the least educated, which could obscure equalizing effects at the transition to high school completion.

Figure 2.

Sensitivity to measurement error, Panel Study of Income Dynamics.

Intergenerational Analyses

Tables 2, 3, and 4 summarize results from the intergenerational analyses using the Bayesian hierarchical approach. All of these estimates adjust for measurement error; the focus here is on efforts to account for differential selection bias. The PSID and NLSY estimates are pooled across genders (gender-specific estimates appear in Tables S1 and S2 in the online Supplemental Material). These tables include education-specific elasticities (posterior means and standard deviations are comparable to point estimates and standard errors); all pairwise comparisons, reported as posterior mean differences between higher and lower education levels; and posterior probabilities that the latter differences are negative. Negative differences and high posterior probabilities are evidence that elasticities decrease as education increases (equalization); positive differences and low posterior probabilities are evidence that elasticities increase as schooling increases (disequalization). Figure 3 illustrates the results by data set and gender, recentering estimates around the baseline elasticities for high school graduates to facilitate the comparison of trends.

Table 2.

Intergenerational Income Elasticity Estimates: National Longitudinal Survey of Youth 1979, Gender Pooled.

	Baseline		+ Controls		+ Family FE
Elasticities	Mean (β)	SD (β)	Mean (β)	SD (β)	Mean (β)	SD (β)
< HS	.252	.050	−.029	.138	.307	.298
HS	.336	.029	.071	.136	.091	.291
College	.222	.035	.025	.145	.075	.305
Bachelor’s	.219	.044	.057	.153	.132	.312
Graduate	.153	.066	.034	.161	.090	.329
Differences	Mean (Δβ)	p (Δβ < 0)	Mean (Δβ)	p (Δβ < 0)	Mean (Δβ)	p (Δβ < 0)
HS – <HS	.084	.065	.100	.053	−.216	.976*
College – <HS	−.030	.701	.054	.217	−.232	.971*
Bachelor’s – <HS	−.033	.688	.086	.149	−.175	.888
Graduate – <HS	−.099	.883	.063	.264	−.217	.889
College – HS	−.114	.996*	−.045	.823	−.016	.576
Bachelor’s – HS	−.117	.987*	−.014	.584	.041	.359
Graduate – HS	−.183	.995*	−.037	.674	−.001	.508
Bachelor’s – college	−.003	.523	.031	.300	.057	.298
Graduate – college	−.068	.816	.008	.455	.015	.459
Graduate – bachelor’s	−.065	.799	−.023	.612	−.042	.612

Note: Estimates are from posterior distributions of elasticity parameters. FE = fixed effects; HS = high school.

For educational differences, posterior probabilities above .95 are taken as significant evidence of declining elasticities (increasing mobility); posterior probabilities below .05 are taken as significant evidence of increasing elasticities (decreasing mobility).

Table 3.

Intergenerational Income Elasticity Estimates: Panel Study of Income Dynamics, Gender Pooled.

	Baseline		+ Controls		+ Family FE
Elasticities	Mean (β)	SD (β)	Mean (β)	SD (β)	Mean (β)	SD (β)
< HS	.459	.050	.498	.090	.541	.154
HS	.236	.069	.214	.116	.335	.163
College	.244	.041	.264	.093	.372	.152
Bachelor’s	.268	.049	.258	.086	.460	.162
Graduate	.309	.065	.283	.108	.464	.174
Differences	Mean (Δβ)	p (Δβ<0)	Mean (Δβ)	p (Δβ<0)	Mean (Δβ)	p (Δβ<0)
HS – <HS	−.223	.998*	−.283	.999*	−.205	.988*
College – <HS	−.214	1.000*	−.234	1.000*	−.169	.984*
Bachelor’s – <HS	−.190	.999*	−.239	.999*	−.081	.809
Graduate – <HS	−.150	.968*	−.215	.989*	−.077	.741
College – HS	.008	.463	.049	.272	.036	.360
Bachelor’s – HS	.033	.342	.044	.338	.124	.135
Graduate – HS	.073	.211	.068	.259	.128	.173
Bachelor’s – college	.024	.329	−.005	.536	.088	.135
Graduate – college	.065	.186	.019	.410	.092	.185
Graduate – bachelor’s	.040	.305	.024	.382	.004	.492

Note: Estimates are from posterior distributions of elasticity parameters. FE = fixed effects; HS = high school.

Figure 3.

Intergenerational elasticity estimates, adjusted for measurement error.

I focus on four questions. First, how do efforts to account for educational selection alter patterns of intergenerational elasticities across schooling levels? The NLSY is likely superior in accounting for selection because it has many useful individual-level controls and also accommodates family fixed effects. The NLS-W has several useful individual-level controls but does not support family FEs; the opposite is true for the PSID. All data sets have the same family-level controls. Second, is there a general trend of decreasing or increasing elasticities across schooling levels consistent with general substitutability or complementarity between schooling and background-related resources? Third, do particular schooling levels have relatively high or low elasticities? In particular, does a college degree have a unique equalizing effect? Fourth, is the elasticity higher among graduate-degree holders than among bachelor’s-degree holders?

Accounting for selection in the NLSY has two effects. First, looking at Figure 3, adding observed controls rotates the trend in elasticities across education levels counterclockwise such that elasticities decrease less or increase more with schooling than in the baseline model. Among women, this weakens a trend of declining elasticities across schooling levels; among men, it reveals a general increase in elasticities. In the gender-pooled analysis, the controls eliminate a trend of declining elasticities, which in the baseline model had indicated an equalization pattern beyond high school completion. Adding family FEs in the gender-pooled model eliminates most variation in elasticities across schooling levels with one exception: It reveals a markedly higher elasticity among the least educated respondents, and these differences are estimated with a high degree of confidence (see Table 2: Δβ = −.17 to –.23, p > .88 for all comparisons to <high school).

Hence, the NLSY analyses suggest that much purported variation in mobility across schooling levels, particularly the general descriptive pattern of declining elasticities, is an artifact of educational selection. I find no evidence that a college degree has a unique equalizing effect relative to high school graduates or individuals with some college and no evidence of any difference in intergenerational elasticities among graduate-degree holders relative to college graduates. There is evidence, however, of a different variety of equalization than previously noted: Direct intergenerational effects are uniquely strong among high school dropouts, and this seems to be suppressed in descriptive analyses by bias from educational selection.

In the PSID, accounting for selection makes less difference, likely due to the lack of controls for individual-level confounders. Nonetheless, the preferred PSID estimates (controls and family FEs) reveal a relatively high elasticity among the least educated respondents (<high school) with a high degree of confidence for most comparisons (Table 3; Δβ = −.08 to –.21, p > .74). I find no evidence of declining elasticities beyond high school completion or of a bachelor’s degree having an equalizing effect; if anything, elasticities increase gradually between high school completion and college completion. Elasticities are comparable at the baccalaureate- and graduate-degree levels in the pooled FE model.

The NLS-W estimates are only comparable to the female-specific estimates in the other data sets. The baseline model suggests declining elasticities moving from some college to bachelor’s and graduate education. Mirroring the NLSY female estimates, adjusting for observed controls weakens this trend. Mirroring the gender-pooled FE analyses in other data sets, including observed controls also reveals a substantially higher elasticity among high school dropouts than among more educated respondents (Table 4: Δβ = −.13 to –.35, p > .77); these are the only differences estimated with much confidence. There is no unique equalizing effect of a bachelor’s degree and no increase in the elasticity at the postbaccalaureate level.

Table 4.

Intergenerational Income Elasticity Estimates: National Longitudinal Survey of Young Women.

	Baseline		+ Controls
Elasticities	Mean (β)	SD (β)	Mean (β)	SD (β)
< HS	.198	.090	.385	.177
HS	.183	.071	.078	.131
College	.237	.080	.254	.136
Bachelor’s	.090	.102	.104	.172
Graduate	−.017	.177	.034	.220
Differences	Mean (Δβ)	p (Δβ<0)	Mean (Δβ)	p (Δβ<0)
HS – <HS	−.015	.566	−.308	.970*
College – <HS	.039	.367	−.132	.773
Bachelor’s – <HS	−.108	.789	−.281	.924
Graduate – <HS	−.216	.868	−.351	.920
College – HS	.054	.294	.176	.090
Bachelor’s – HS	−.093	.774	.026	.432
Graduate – HS	−.200	.860	−.043	.582
Bachelor’s – college	−.147	.876	−.150	.845
Graduate – college	−.254	.904	−.219	.852
Graduate – bachelor’s	−.107	.702	−.070	.636

Note: Estimates are from posterior distributions of elasticity parameters. FE = fixed effects; HS = high school.

The gender-specific analyses in the NLS-W and other data should be interpreted with caution because of reduced statistical power and the inability to incorporate family fixed effects. Nonetheless, net of observable controls, across data sets, there is more of a tendency for elasticities to increase beyond high school completion in the male-specific analyses, whereas the opposite is true in the female-specific analyses. This could be due to differences in educational selection or to gender differences in the attainment process.

To recap, the most rigorous efforts to address educational selection are in the NLS-W analysis with observed controls and in the gender-pooled NLSY and PSID analyses with controls and family fixed effects. None of these are perfectly comparable, but they all find a few things in common. First, the strongest intergenerational effects appear for high school dropouts, for whom elasticities are .1 to .4 points stronger than for respondents with more education; these are substantial differences and the only ones consistently estimated with a high degree of confidence. That this is only apparent in the NLS-W and NLSY after accounting for selection bias suggests dropouts from advantaged backgrounds are negatively selected on traits that influence later earnings. This is not surprising, but it has been overlooked because prior discussions of selection focus on the highest schooling levels. Failing to account for selection thus obscures strong elasticities (low mobility) among dropouts, which suggests something about an advantaged family background helps compensate for the lack of a high school education.

The preferred analyses provide no compelling evidence of differences in mobility beyond high school completion. The PSID suggests slightly increasing elasticities, the NLS-W reveals fluctuating elasticities, and the NLSY—best suited to address differential selection—shows no apparent differences; in no case are any differences estimated with confidence. I also find no evidence that a bachelor’s degree has a unique equalizing effect; it is never the education level with the lowest elasticity. And I find no evidence of increasing elasticities between the baccalaureate- and postbaccalaureate-degree levels.

Table S3 in the online Supplemental Material provides coefficient estimates for covariates relevant to selection bias based on the NLS-W model with controls and the gender-pooled NLSY and PSID models with controls and family FEs. The most striking findings concern cognitive skills. In both the NLS-W and NLSY, cognitive skills have an independent association with adult family income that varies inversely with parent income (negative interaction, t ratio < –1.96). This suggests substitution or compensation between cognitive skills and background-related resources. Net of education, cognitive skills (or the lack thereof) appear more important to the attainment of individuals from disadvantaged economic backgrounds than to that of their more advantaged peers. From another perspective, direct background effects wane as cognitive skills increase. Given the positive association between cognitive skills and schooling, failing to account for this interaction likely misattributes a potential equalizing effect of cognitive skills to schooling, contributing to spurious patterns of educational equalization. Cognitive skills may be important sources of educational selection and potential moderators of direct intergenerational transmissions.

Additional Analyses

I conducted several additional analyses to assess the importance of measurement error and probe some differences with prior findings. I briefly summarize them here and describe them in more detail in the online Supplemental Material. First, when I replicate my analyses without adjusting for measurement error in parent income, I find less overall variation in elasticities across education levels, lower elasticities among high school dropouts, and more evidence of an uptick in elasticities between the bachelor’s- and graduate-degree levels. Hence, measurement error may both suppress equalization at the transition to high school completion and overstate the rise in elasticities beyond college completion.

Second, when I replicate my analyses using parent education or occupational status rather than income as the background measure, educational differences in background effects are more muted overall, and those that do exist diminish after accounting for selection. An absence of strong background effects among high school dropouts is noteworthy. These alternative background measures may fail to fully capture families’ economic standing, including income disparities within occupations and education levels. Direct intergenerational transmissions among the least educated may depend on parental economic resources that are not captured by these cruder measures of parent socioeconomic status.

Finally, I explored differences between my findings and those of Torche (2011), who also examined family income elasticities in these data sets but used different samples and methods. Torche generally found a U-shaped pattern, with the lowest elasticities in the middle of the educational distribution. I attempted to replicate Torche’s NLSY and PSID samples (with modest success) and subject those samples to my own analytic approach. I found that accounting for measurement error and educational selection accentuates the higher elasticities Torche found among the least educated, but it reduces differences beyond high school completion. In other words, my analysis of the attempted replication sample reveals more of an L-shaped pattern consistent with my main findings. Our different findings appear to be due to the treatment of the data (adjusting for measurement error and educational selection) rather than case selection.

Discussion

Recent research casts doubt on the long-held belief that education is a moderating, equalizing force that fuels intergenerational mobility by breaking the link between one’s social origins and destinations (e.g., Torche 2011; Witteveen and Attewell 2017; Zhou 2019). This study revisits this issue from a causal perspective using methods designed to address multiple sources of bias that may plague prior research. Results from three longitudinal surveys converge on new findings. Most notably, intergenerational economic mobility is uniquely low among high school dropouts, for whom childhood family income is a relatively strong predictor of adult family income. Economic mobility is significantly higher among high school graduates and remains similarly high among individuals with higher levels of education.

More specifically, contradicting prior descriptive mobility research and echoing Zhou’s (2019) recent findings, I find no evidence that a bachelor’s degree has a unique equalizing effect. Unlike Torche’s (2011) descriptive analysis but consistent with her more recent analysis of doctoral-degree holders (Torche 2018), I also find no compelling evidence that a graduate or professional degree has a disequalizing effect. The most unique contribution here is the finding that failing to complete high school seems to leave a strong direct link between family income in childhood and adulthood. Such direct links are substantially weaker among individuals who earn at least a high school degree. In other words, there is evidence that education has an equalizing effect but that it is concentrated at the threshold of high school completion.

This is the first study of this problem to address bias due to both measurement error in parent income and nonrandom selection into different education levels. Both are consequential. Parent income measurement error seems to attenuate intergenerational income elasticities and thus overstate mobility among high school dropouts, and it may also contribute to the spurious appearance of reduced mobility at the postbaccalaureate level. Selection bias further conceals the relatively low mobility among high school dropouts, and it contributes to spurious patterns of increasing mobility beyond high school completion. Analyses further suggest that the most salient sources of selection bias are related to unmeasured family characteristics and adolescent cognitive skills, the latter of which may have its own equalizing effect.

One implication of these findings is that the presumed equalizing effect of educational expansion in the twentieth century, posited to have increased the openness of U.S. society (Hout 1988; Pfeffer and Hertel 2015), is unlikely to have actually been caused by gains in postsecondary attainment. Instead, it may have been due to increases in high school completion or to improved skills and family circumstances that also helped fuel educational expansion (Altonji, Bharadwaj, and Lange 2012). Furthermore, stagnation in the high school dropout rate since the 1970s (Heckman and LaFontaine 2010) may have contributed to the recent stagnation in economic mobility (Hout 2018; Lee and Solon 2009). Overall, my findings suggest efforts to build cognitive skills and promote high school completion among disadvantaged youth may be crucial steps to increasing economic mobility. Such efforts could boost upward mobility and have the added benefit of preparing more students for success in higher education.

Turning to theoretical implications, my findings do not reveal any general substitutability or complementarity between schooling and social background. Hence, if the story is about meritocracy in the labor market, it must involve especially unmeritocratic processes in very low-skill sectors that hire high school dropouts. But the findings seem most consistent with theories of compensatory advantage in intergenerational processes (Bernardi 2014; Bernardi and Ballarino 2016). In combination, the low mobility (strong parental income effects) among high school dropouts and the weaker effects of cognitive skills among individuals from higher-income backgrounds suggest economically advantaged families provide material, social, or cultural resources that help compensate for their children’s lack of human capital.

This study emphasizes the causal status of education’s role as an intergenerational moderator, but it has its own shortcomings in this respect. It is unclear how well I account for educational selection, and my inability to address the problem to the same extent in all analyses leaves questions about the different findings across data sets and genders. It is also unclear how well the model-based adjustments for measurement error work. Administrative data on parent income might be more accurate; the trade-off is that such data often lack measures of skills and traits related to educational selection. Finally, to further understand these processes, we need to test specific mechanisms not only of direct family background effects but also of educational moderation. Likely candidates include family-based employment, intergenerational bequests, and family formation processes that could differ according to educational attainment. There is clearly much left to learn about education’s role as a moderator of intergenerational stratification processes, and hopefully this study provides some footing going forward.

Supplemental Material

EdEqual_SOE_Supplement_clean – Supplemental material for Great Equalizer or Great Selector? Reconsidering Education as a Moderator of Intergenerational Transmissions

Supplemental material, EdEqual_SOE_Supplement_clean for Great Equalizer or Great Selector? Reconsidering Education as a Moderator of Intergenerational Transmissions by Jeremy E. Fiel in Sociology of Education

Footnotes

Acknowledgements

I am grateful for the feedback from participants at the 2017 summer meeting of the Research Committee 28 on Social Stratification and Mobility.

Research Ethics

This research used publicly available anonymized survey data and thus does not constitute human subjects research.

Funding

The author disclosed receipt of the following financial support for the research, authorship, and/or publication of this article: The research reported in this article was made possible in part by a grant from the Spencer Foundation (No. 201700114). The views expressed are those of the author and do not necessarily reflect the views of the Spencer Foundation.

ORCID iD

Jeremy E. Fiel

Supplemental Material

Supplemental material is available in the online version of the journal.

Notes

Author Biography

Jeremy E. Fiel is an assistant professor of sociology at the University of Arizona. His research uses quantitative methods to examine problems of educational inequality and social stratification, with particular interests in contemporary school segregation and in processes of intergenerational educational stratification. Jeremy’s work has been published in American Sociological Review, American Journal of Sociology, American Educational Research Journal, Social Forces, and Demography.

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Supplementary Material

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