Abstract
We ask whether employer learning in the wage-setting process depends on skill type and skill importance to productivity, using measures of seven premarket skills and data for each skill’s importance to occupation-specific productivity. Before incorporating importance measures, we find evidence of employer learning for each skill type, for college and high school graduates, and for blue-and white-collar workers, but no evidence that employer learning varies significantly across skill or worker type. When we allow parameters identifying employer learning and screening to vary by skill importance, we identify tradeoffs between learning and screening for some (but not all) skills.
I. Introduction
The term “employer learning” is typically associated with a class of empirically testable models in which employers learn the productivity of workers over time. In these models, employers are assumed to use schooling attainment and other readily observed signals to predict productivity and set wages at the start of the career; as workers’ careers evolve, true productivity is revealed and the role of schooling in the wage-setting process declines. Building on the work of Spence (1973) and others, Farber and Gibbons (1996) and Altonji and Pierret (2001) were the first to demonstrate that the relationship between a test score and wages is expected to increase with experience in the face of employer learning—where the test score can, in principle, be any measure that is correlated with premarket productivity but unobserved by employers. Variants of this test have been used by Lange (2007) to assess the speed of employer learning, by Schönberg (2007) and Pinkston (2009) to study asymmetric employer learning, and by Bauer and Haisken-DeNew (2001), Arcidiacono, Bayer, and Hizmo (2010), and Mansour (2012) to investigate differences in employer learning across schooling levels, occupational type (blue-versus white-collar) and initial occupations, respectively.
In the current study, we ask whether the role of employer learning in the wage-setting process depends on the type of skill potentially being learned over time as well as the skill’s importance, by which we mean its occupation-specific contribution to productivity. Basic language skills might be readily signaled to potential employers via the job interview process while other skill types such as “coding speed” (the ability to find patterns of numbers quickly and accurately) might only be revealed over time in the absence of job applicant testing. Moreover, a skill’s importance is likely to affect both ex ante screening technologies and the extent to which employers learn about the skill over time. If the ability to solve arithmetic problems is irrelevant to the work performed by dancers and truck drivers, for example, then the true productivity their employers learn over time should be uncorrelated with a measure of arithmetic skill. Stated differently, the relationship between arithmetic test scores and wages should not increase with experience for dancers and truck drivers. In reverse situations where a particular skill is essential to job performance, it is unclear whether signaling or learning will dominate the wage-setting process. Given that arithmetic skill is critical to accountants’ job performance, for example, should we expect arithmetic ability to be a key component of what their employers learn over time? Or do employers customize their screening methods to ensure that the most critical skills are accurately assessed ex ante?
To address these questions, we begin by identifying the channels through which skill importance enters a standard model of public employer learning. Using the omitted variable bias strategy of Altonji and Pierret (2001), we demonstrate that by using the portion of a test score (referred to as Z*) that is orthogonal to schooling and other regressors, the Z*-experience gradient in a log-wage model is expected to depend solely on the test score’s correlation with performance signals that lead to learning, while the coefficient for Z* is expected to depend both on skill importance and the extent to which the skill is signaled ex ante. These derivations motivate our empirical strategy: First, we empirically assess the role of employer learning for alternative skills by inserting skill-specific test scores (Z*) into a log-wage model and comparing the magnitudes of their estimated experience gradients. Second, we allow coefficients for Z* and Z*-experience interactions to depend on skill importance (which we measure directly) to determine whether learning and screening depend on the skill’s importance to productivity.
We implement these extensions of the Altonji and Pierret (2001) model using data from the 1979 National Longitudinal Survey of Youth (NLSY79) combined with Occupational Information Network (O*NET) data. To proxy for premarket skills that are unobserved by employers, we use test scores for seven components of the Armed Services Vocational Aptitude Battery (ASVAB). The use of narrowly defined test scores distinguishes our approach from the existing literature, where most analysts rely on scores for the Armed Forces Qualifications Test (AFQT)—a composite score based on four ASVAB components that we use individually.1 By using skill-specific test scores, we can determine whether employer learning plays a different role for arithmetic ability, reading ability, coding speed, and so forth. We further extend the analysis by using O*NET data to measure the importance of each skill in the three-digit occupation associated with each job. These additional variables enable us to determine whether skill-specific screening and skill-specific employer learning are themselves functions of skill importance.
By allowing employer learning to vary with skill type and skill importance, we contribute to an emerging literature that explores heterogeneity in employer learning along various dimensions. Bauer and Haisken-DeNew (2001) find evidence of employer learning for men in low-wage, blue-collar jobs but not for other male workers; Arcidiacono, Bayer, and Hizmo (2010) find evidence of employer learning for men with 12 years of schooling but not for men with 16 years of schooling; Mansour (2012) finds that employer learning differs across workers’ initial, two-digit occupations. Our approach incorporates three innovations. First, we allow for a richer form of heterogeneity than is permitted with a high school/college or blue-collar/white-collar dichotomy and, in fact, we demonstrate that employer learning does not differ across categories used by Bauer and Haisken-DeNew (2001) and Arcidiacono, Bayer, and Hizmo (2010). Second, while we incorporate Mansour’s (2012) notion that detailed measures of “job type” are needed to capture true heterogeneity in employer learning, we define “job type” in terms of the skills needed to perform a specific task rather than occupational categories. We do so in light of existing evidence that jobs are better described in terms of tasks or skills than by orthodox occupational taxonomies (Poletaev and Robinson 2008; Lazear 2009; Bacolod and Blum 2010; Gathmann and Schönberg 2010; Phelan 2011; Yamaguchi 2012). Mansour (2012) allows employer learning to differ with the long-term wage dispersion associated with initial two-digit occupational groups. While this is an innovative measure of job-specific heterogeneity, it raises questions about why employer learning is identical for school teachers and truck drivers (who perform different types of work but fall into occupational categories with identical wage dispersion) and dramatically different for physicians and medical scientists (whose work is similar but whose occupational groups are at opposite ends of the wage dispersion distribution). Third, in contrast to the existing literature, we explicitly examine the tradeoff between employer learning and screening rather than simply infer that any absence of learning must be due to increased screening.
Prior to bringing importance scores into the analysis, we find evidence of employer learning for all seven skill types. We also find that differences across skill types in the degree of learning are uniformly insignificant, as are differences across “worker type” (12 versus 16 years of schooling, or blue-collar versus white-collar) for most skills; in contrast to Bauer and Haisken-DeNew (2001) and Arcidiacano, Bayer, and Hizmo (2010), this initial evidence points to little heterogeneity across skills or workers in the role of employer learning. Once we incorporate measures of skill importance, our findings change dramatically. We identify distinct tradeoffs between screening and employer learning, and we find that the effect of skill importance on screening and learning differs by skill type. For coding speed, mathematics knowledge, and mechanical comprehension, screening increases and learning decreases in skill importance; for word knowledge, paragraph comprehension, and numerical operations, screening decreases in skill importance. These patterns suggest that the role of employer screening in wage determination depends intrinsically on the type of skill being assessed and the nature of the job being performed.
II. Model
In this section, we review the test for public (symmetric) employer learning proposed by Altonji and Pierret (2001) (hereafter referred to as AP), and we demonstrate how it can be extended to assess the role of employer learning for a range of skills that differ across jobs in their productivity-enhancing “importance.” Our extension of the AP framework enables us to identify both screening and employer learning through sample covariances. As a result, we can assess tradeoffs between learning and screening for job types that are richly defined on the basis of skill type and skill importance. As we discuss, we rely on the AP model rather than Lange’s (2007) speed of learning model because the latter cannot distinguish between screening and learning. We also detail how we are able to identify employer learning and screening in the presence of initial occupational sorting as well as subsequent sorting and job mobility.
A. The Altonji and Pierret (AP) Employer Learning Model
1. Productivity
Following AP, we decompose yit, the true log-productivity of worker i at time t, into its components:
(1)
where Si represents time-constant factors such as schooling attainment that are observed at labor market entry by employers and are also observed by the econometrician; qi represents time-constant factors such as employment references that are observed ex ante by employers but are unobserved by the econometrician; Zi are time-constant factors such as test scores that the econometrician observes but employers do not; Ni are time-constant factors that neither party observes; and H(Xit) are time-varying factors such as work experience that both parties observe over time. In a departure from AP, we explicitly define λz as the importance of the unidimensional, premarket skill represented by Zi —that is, the weight placed on each test score in determining true log-productivity.2
Employers form prior expectations of factors they cannot observe (Zi and Ni) on the basis of factors they can observe (Si and qi):
(2)
(3)
where, following AP, qi can be excluded from one expectation. Over time, employers receive new information about productivity—which we refer to as Dit —that they use to update their expectations about Zi and Ni. With this new information in hand, employers’ beliefs about productivity at time t are:
(4)
where λzνi + ei is the initial error in the employers’ assessment of productivity. Following AP, we assume that new information is public and, as a result, learning across firms is symmetric.
2. Wages and omitted variable bias
Given AP’s assumption (used throughout the employer learning literature) that workers’ log-wages equal their expected log-productivity, we obtain the log-wage equation used by employers directly from Equation 4. In a departure from AP’s notation, we write the log-wage equation as:
(5)
where β1 = r + λzγ2 + α2, β2 = λzγ1 + α1, git = E(λzνi + ei|Dit), ζit represents factors used by the firm that are outside the model, and H(Xit) is omitted for simplicity. The econometrician cannot estimate Equation 5 because qi and git are unobserved. Instead, we use productivity components for which data are available to estimate
(6)
AP’s test of employer learning is based on an assessment of the expected values of estimators obtained with “misspecified” Equation 6. Ignoring work experience and other variables included in the econometrician’s log-wage model (which we revisit in IIC), these expected values are:
(7)
(8)
The δs in Equations 7–8 are defined by auxiliary regressions qi = δqsSi + δqzZi and vi = δvsSi + δvzZi, where vi is now “shorthand” for the initial error λzνi + ei, θt = (Szg / Szv), 
and 
; the remaining variance and covariance terms in Equations 7–8 are defined similarly.
The first term in Equation 7 represents the true effect of Si on log-wages, the second term represents the time-constant component of the omitted variable bias, and the third term (by virtue of its dependence on git) is the time-varying component of the omitted variable bias. Similarly, in Equation 8—where there is no true effect because employers do not use Zi to set wages—the first (second) component of the omitted variable bias is constant (varying) over time.
3. AP’s test of employer learning
AP’s primary test of employer learning amounts to assessing the sign of the time-varying components of the omitted variable biases in Equations 7–8. Given the relatively innocuous assumptions that Szv > 0, Szs > 0, and Zi and Si are scalars, it is apparent that the time-varying component of Equation 7 is negative and the time-varying component of Equation 8 is positive. Stated differently, the expected value of the estimated Si coefficient in the econometrician’s log-wage model declines over time while the expected value of the estimated Zi coefficient increases over time.
AP and subsequent contributors to the literature operationalize this test by modifying Specification 6 as follows:
(9)
where Si is “highest grade completed,” Zi is a test score, Xit is a measure of cumulative labor market experience, and ϵit represents all omitted or mismeasured factors. A positive estimator for b5 is evidence in support of employer learning; a negative estimator for b4 is evidence that employers use schooling to statistically discriminate regarding the unobserved skill, Zi.
B. Assessing Employer Learning for Different Skills and Skill Importance
1. Skill type
Our first goal is to estimate log-wage Model 9 with alternative, skill-specific test scores representing Zi, and to use the set of estimators for b3 and b5 to compare signaling and employer learning across skills. To do so, we must assess magnitudes of the time-varying components of the omitted variable biases in Equations 7–8. This constitutes a departure from AP, whose objective simply required that they sign each time-varying component.
Inspection of Equations 7–8 reveals that the time-varying components (that is, the right-most terms) depend on Szg, which represents the covariance between the test score used in estimation (Zi) and the employer’s updated information about productivity (git = E(λνi + ei|Dit)), as well as Szs, Szz, and Sss. While Szg is a direct measure of employer learning, two of the remaining three terms also vary across test scores and, therefore, can confound our ability to interpret 
for each test score as a skill-specific indication of employer learning.
To address this issue, we follow Farber and Gibbons (1996) by constructing skill-specific test scores that are orthogonal to schooling. We define 
as the residual from a regression of Zi on Si and a vector of other characteristics (Ri):
(10)
We normalize each 
to have unit-variance (Szz = 1) and replace Zi with this standardized residual in Specification 9. Because Szs = 0 by construction, the time-varying components of the omitted variable biases in Equations 7–8 reduce to:3
(11)
where B1t and B3t represent the right-most terms in Equations 7–8 (θtδυs and θtδυz). By using standardized, residual test scores, the Z–X slope in Specification 9 is determined entirely by employer learning.4 This suggests that if we use a 
about which the performance history is particularly revealing, we can expect the coefficient for 
identified by Specification 9 to be particularly large. To summarize our first extension of AP’s test: We use alternative measures of 
in Specification 9 and compare the magnitudes of 
to judge which skills employers learn more about.5
The time-constant components of the omitted variable biases in Equations 7–8 are also of interest, given that these terms represent the extent to which Zi is tied to initial wages via signaling. After replacing Zi by 
and standardizing, the time-constant components of the omitted variable biases (β2δqs and β2δqz in Equations 7–8) are given by:
(12)
The expression for B30 reveals that the time-invariant relationship between 
and log-wages increases in Szq, which represents the covariance between the skill and productivity signals observed ex ante by the employer but not the econometrician. All else equal, we expect the estimated coefficient for 
in Specification 9 to be larger for test scores that are relatively easy to assess ex ante via their correlation with signals other than Si; unsurprisingly, the skills measured by such test scores would contribute relatively more to initial wages under these circumstances.
However, we cannot apply this argument to our interpretation of 
because “all else” is not held constant as we substitute alternative test scores into the regression. In particular, B30 depends on β2, which in turn depends on structural parameters α1, γ1, and λz. If changes magnitude as we substitute alternative test scores into Specification 9, we cannot determine whether the change reflects cross-skill differences in signaling (Szq) or skill importance (λz). As explained below, in select circumstances we can make this distinction by using data on skill importance. More generally, we simply view the combined effect of Szq and λz (what employers learn via screening combined with how they weight that information) as the screening effect.
2. Skill importance
Building on the preceding discussion, we consider three avenues through which skill importance can affect the wage-generating process and, therefore, the omitted variable biases shown in Expressions 11–12. First, importance affects B30 directly through β2, which is a function of λz, so the estimated coefficient for 
in Specification 9 depends in part on the skill’s importance. Second, importance affects B30 indirectly if employers’ ability to screen for a particular skill is itself a function of importance (that is, if Szq depends on λz). This channel—which is consistent with Riley’s (1979) argument that screening is more important in some occupations than in others—might exist because employers screen more intensively (or efficiently) for those premarket skills that matter the most. For example, dancing skill is critical for a dancer while arithmetic skill is not, so dancers’ employers are likely to hold dance auditions (a component of q) prior to hiring but not administer an arithmetic test. Third, importance affects B3t directly because Szg (the covariance between skill and time-varying productivity signals that give rise to learning) depends on skill importance, and not just the skill itself. This latter channel implies that the estimated coefficient for 
in Specification 9 depends on skill importance.6
In light of these arguments, we augment Specification 9 to allow b3 and b5 to depend on skill importance:
(13)
where 
is an “importance score” representing the importance of skill 
for the occupation held by worker i at time t; we view 
as a direct measure of λz. While Specification 13 illustrates a parsimonious way to allow the coefficients for 
and 
to depend on 
, we also experiment with more flexible specifications that interact 
with additional variables and/or allow 
to have nonlinear effects on the parameters of interest.
Because the time-varying component of the relationship between 
and wit (per Equation 11) is a function only of Szg, we can interpret any 
-pattern in the 
slope as representing the effect of skill importance on employer learning. In contrast, the time-constant component of the relationship between 
and wit (per Equation 12) is a function of both Szq and λz, so estimates for a6 in Specification 13 are potentially more difficult to interpret. Given that λz tautologically increases in its empirical analog 
, a finding that the estimated 
coefficient declines in skill importance is unequivocal evidence that screening (Szq) declines in skill importance. If the estimated 
coefficient increases in skill importance, we cannot determine whether Szq increases or decreases in importance. We illustrate this ambiguity by considering the case where 
measures arithmetic ability and “increased importance” corresponds to contrasting a dance company to an accounting firm. The scenario where Szq increases in importance corresponds to accounting firms screening for arithmetic skill more effectively than dance companies; in addition, accounting firms necessarily put more weight on arithmetic skill in the initial wage-setting process so a given amount of arithmetic skill translates into higher initial log-wages for accountants than for dancers because both Szq and λz are larger. In the alternative scenario, accounting firms screen less effectively than dance companies for arithmetic skill but place a greater weight (λz) on whatever arithmetic skill they are able to identify ex ante; a given amount of skill continues to translate into a higher initial log-wage for accountants than for dancers because the smaller Szq is offset by a larger λz. We cannot distinguish empirically between the two scenarios but in interpreting our estimates we view the “total” effect of 
on the estimated 
coefficient as the screening effect of interest.
C. Additional Considerations
In this subsection, we consider several factors that potentially affect our ability to relate the magnitude of estimated Z ⋅ X coefficients in Specifications 9 and 13 to the extent of employer learning associated with skill Z. We consider the role of initial occupational sorting, subsequent job mobility, on-the-job training, and the simple fact that we include more regressors in Specifications 9 and 13 than were brought to bear in deriving expected parameter values. In addition, we clarify why we assess employer learning by directly identifying Szg, rather than by estimating Lange’s (2007) speed of employer learning model.
1. Omitted variable bias in the presence of additional regressors
Following AP, we derived the omitted variable biases in Equations 11–12 for Specification 6, which ignores regressors other than Si and Zi. When we estimate Specifications 9 and 13, however, we control for additional factors, including race and ethnicity, cumulative labor market experience (Xit), and skill importance 
. In order to draw inferences based on the notion that Szg is the sole determinant of estimated Z-X slopes, we must recognize that variances and covariances involving all remaining regressors not only affect those estimates but can contribute (along with Szg) to differences across test scores. We address this problem by replacing Zi in each log-wage model with a residual test score 
that is orthogonal by construction to Si, Xit, 
, and every other regressor such as race.7
2. Occupational sorting and job mobility
Initial occupational sorting can directly influence employers’ inferences about workers’ unobserved skills. As noted by Mansour (2012), a finding that Occupation A has more (or faster) employer learning than Occupation B can reflect the fact that workers are more homogenous with respect to skill in A than in B as a result of occupational sorting. More precisely, Mansour’s argument is that systematic occupational sorting on the basis of skill reduces the variance of employers’ initial expectation errors (λzνi + ei in Equation 4), thus reducing the amount to be learned. While we agree with Mansour’s argument, intensive screening (perhaps for “important” skills) will also reduce the variance of employers’ initial expectation errors, and hence the amount left to be learned. In principle, a finding that Occupation A has more employer learning than Occupation B can reflect occupational sorting or differences across occupations in screening intensity. As noted in IIC1, we eliminate the role played by initial occupational sorting in our analysis by using residual test scores 
that are orthogonal to initial (and final) occupation-specific importance scores.
Over the course of workers’ careers, additional occupational sorting can also influence employer learning. For example, an employer for whom mechanical comprehension is very important might infer that among workers with two years of experience, workers with insufficient mechanical comprehension have migrated to other occupations. We cannot distinguish empirically between learning due to (noninitial) sorting and learning due to performance histories: Employer learning in our model reflects Szg, which is the sample analog of cov(Zi, E(λzνi + ei|Dit)); the information contained in Dit includes how long the worker has been in the labor market as well as his performance history. We do not model the learning process per se and thus do not distinguish between changes in employers’ inferences resulting from awareness of sorting versus observing a worker’s performance history. The fact that employers’ inferences can change over time due to sorting is not problematic for identifying employer learning; in our application, it simply suggests another reason to expect employer learning to be related to skill importance insofar as importance might be systematically related to sorting patterns.
Log-productivity Equation 1 imbeds AP’s assumption that the marginal productivity of a given skill is constant over time and across occupations. As a result, when we derive the expected value of the estimated coefficient for Zi in Specification 6, the only source of time-variation in the omitted variable bias (per Equation 11) is Szg, which represents employer learning. In contrast to this simplified assumption, the marginal productivity of a given skill is expected to vary across jobs (Burdett 1978; Jovanovic 1979; Mortensen 1986). Therefore, lifecycle job mobility introduces an additional source of time variation in the relationship between Zi and log-wages that cannot be distinguished from employer learning within the AP framework. If workers tend to move to jobs that place more (less) importance on a given skill than did their previous jobs, then we will overestimate (underestimate) employer learning. However, if workers change jobs but the relative importance of skill does not change over time in the sample, then our estimates are less likely to be affected by mobility.
To assess the potential effect of mobility on our estimates, we reestimate Specification 9 using subsamples of workers who remain in the same occupation or, alternatively, who remain in occupations placing comparable importance on a given skill. In Section IV, we demonstrate that mobility does not substantially influence our estimates.8
3. On-the-job training
In Equations 1 and 4, H(Xit) represents the fact that wages evolve over time as workers augment their premarket skill via on-the-job training (Becker 1993; Mincer 1974). The omitted variable biases in Equation 11 are derived under the assumption that this additional human capital is orthogonal to Si and Zi, which ensures that its effect on log-wages is entirely captured by the experience profile when we estimate Specifications 9 and 13. As noted by Farber and Gibbons (1996), if instead complementarities exist between 
(the component of premarket skill that is orthogonal to schooling) and the subsequent acquisition of human capital, then we will be unable to separate employer learning from the effects of these complementarities.9 A likely scenario is that these skill investments are complementary with Si, which implies that E (b4) > 0 in Specification 9 (and E(a4) > 0 in Specification 13), in contrast to the prediction (per Equation 11) that the S-X slope is zero. In Section IV, we find evidence for such complementarities.
4. Speed of employer learning
Lange (2007), Arcidiacono, Bayer, and Hizmo (2010), and Mansour (2012) estimate a structural speed of learning parameter (k1) that depends on two factors: the variance of employers’ initial expectation errors (which reflects the “need” for employer learning once initial screening occurs) and the variance of subsequent productivity signals (which reflects the “ability” to learn on the basis of time-varying information).10 As discussed in IIB, we focus instead on (nonstructural) parameters that are directly related to Szq (which reflects employers’ ability to screen for skill Z) and Szg (which reflects employer learning); this strategy enables us to examine effects of skill importance on both screening and learning. It stands to reason that skill importance also affects the two variances that determine k1. If employers are relatively more effective at screening for important skills, then they should have relatively little to learn—that is, their initial expectation errors should have relatively little variance. Similarly, if productivity signals are relatively more informative for important skills, then those signals should have relatively low variance. We choose to focus on the sample covariances Szq and Szg rather than on k1 because estimation of the speed of learning parameter cannot readily distinguish between effects of skill importance on screening versus learning.11
III. Data
A. Sample Selection
We estimate the log-wage models described by Equations 9 and 13 using data from the 1979 National Longitudinal Survey of Youth (NLSY79). We also use data on workers’ attributes and job requirements from the Occupational Information Network (O*NET) to construct occupation-specific importance scores for select skills; background information on O*NET data is provided in Appendix 1. The NLSY79 began in 1979 with a sample of 12,686 individuals born in 1957–64. Sample members were interviewed annually from 1979–94 and biennially from 1996 to the present. Data are currently available for 1979 through 2010, but we use data through 2000 for conformity with prior studies, which demonstrate that employer learning is concentrated in the early-career.12
In selecting a sample for our analysis, we adhere as closely as possible to the criteria used by AP to facilitate comparison with its study. We begin by dropping the 6,283 female NLSY79 respondents who make up roughly half the original sample. Among the 6,403 male NLS79 respondents, we drop from our sample 428 men who did not take the 10-component ASVAB test in 1980, given that we rely on these test scores to represent productivity factors that employers learn over time. We then drop 2,075 men whose initial exit from school precedes January 1978 because Census three-digit occupation codes were not systematically identified for jobs held prior to then, and we require such codes to construct occupation-specific importance scores based on O*NET data. AP apply a similar selection rule for the purpose of constructing an actual experience measure based on weekly employment arrays that exist for January 1978 onward. However, AP relax the rule for a subset of respondents for whom weekly information can be “filled in” prior to January 1978. We delete an additional 30 men whose reported “highest grade completed” at the time of initial school exit is less than eight. Another 801 men are deleted from the sample because we lack at least one valid wage (an average hourly wage between $1/hour and $200/hour for which a 1970 Census three-digit occupation code is available) for the current or most recent job at the time of each interview. The relevant observation window for the selection of wages begins at initial school exit and ends at the earliest of three dates: (1) subsequent school reenrollment; (2) the respondent’s last NLSY79 interview through 2000; or (3) 15 years after initial school exit. Of these 801 deletions, only 51 men report an otherwise-valid wage for which an occupation code is missing; most of the remaining 750 men drop out of the survey relatively soon after school exit. These selection rules leave us with a sample of 22,907 post-school wage observations contributed by 3,069 men.
As discussed in IIC, we estimate select log-wage models using subsamples of nonmobile men to determine whether our estimates are influenced by job mobility. We select observations for a subsample of “occupation stayers” by allowing each man to contribute wage observations as long as his three-digit occupation remains unchanged relative to his initial observation. We select subsamples of “importance score stayers” by retaining each sample member as long as his raw skill-specific importance score does not change by more than 0.1 relative to his initial occupation’s score. Each subsample has the same number of men (3,069) as the full sample. The subsample of “occupation stayers” has 8,778 wage observations; sample sizes for “importance score stayers” are tied to the skill measure being used but range from 9,471 for mechanical comprehension to 10,273 for coding speed (see Table 8).
We also estimate select specifications for a subsample of men with exactly 12 or 16 years of schooling and for a subsample of observations corresponding to blue-collar or white-collar occupations.13 These subsamples are used for comparison with the findings of Bauer and Haisken-DeNew (2001) and Arcidiacono, Bayer, and Hizmo (2010) although, unlike those authors, we use pooled samples (S = 12 and S = 16; blue-collar and white-collar) and interactions to allow each parameter to vary by type. We also define each “type” to be time-constant for each respondent whereas Bauer and Haisken-DeNew (2001) and Arcidiacono, Bayer, and Hizmo (2010) allow respondents to appear in both subsamples. Our schooling sample consists of 14,979 observations for 1,677 men with 12 years of schooling and 4,516 observations for 560 men with 16 years of schooling; our occupation sample consists of 17,189 observations for 1,900 men in blue-collar occupations and 9,597 observations for 1,264 men in white-collar occupations.
B. Variables
Table 1 briefly defines the variables used to estimate our log-wage models and presents summary statistics for samples described in the preceding subsection. Our dependent variable is the natural logarithm of the CPI-deflated average hourly wage, which we construct from the NLSY79 “rate of pay” variables combined with data on annual weeks worked and usual weekly hours.
Means and Standard Deviations for Select Variables in Alternative Samples
For comparability across specifications, we always use a uniform set of baseline covariates. We follow convention in using highest grade completed (S) as a measure of productivity that employers observe ex ante.14 Our schooling measure is based on NLSY79 created variables identifying the highest grade completed in May of each calendar year and identifies the schooling level that prevails at each respondent’s date of school exit. Because we truncate the observation period at the date of school reentry for respondents seen returning to school, our schooling measure is fixed at its premarket level for all respondents, as required by the model; discontinuous schooling is a relatively common phenomenon among NLSY79 respondents (Light 1998, 2001). We also control for a cubic in potential experience (X), which we define as the number of months since school exit divided by 12. In addition, we control for two dummy variables indicating whether the individual is black or Hispanic (with non-black, non-Hispanics serving as the omitted group), interactions between S and these race/ethnicity dummies, the interaction between S and X, a dummy variable indicating whether the individual resides in an urban area, and individual calendar year dummies. This baseline specification mimics the one used by AP.
In a departure from prior research on employer learning, we control for productivity correlates that employers potentially learn over time (Z) with eight alternative measures of cognitive skills. Our first measure is the one relied on throughout the existing literature: an approximate Armed Forces Qualifications Test (AFQT) score constructed from scores on four of the ten tests that make up the Armed Services Vocational Aptitude Battery (ASVAB).15 Our remaining measures are scores from seven individual components of the ASVAB: arithmetic reasoning, word knowledge, paragraph comprehension, numerical operations, coding speed, mathematics knowledge, and mechanical comprehension. We use the first four ASVAB scores because they are used to compute the AFQT score; we include the remaining scores because, along with the first four, they can be mapped with minimal ambiguity to O*NET importance scores.16 We provide the formula for computing AFQT scores and a mapping between ASVAB skills and O*NET measures in Table A1 in Appendix 1.
As detailed in Section II, our use of alternative test scores presents us with a challenge not faced by analysts who rely exclusively on AFQT scores as a proxy for Z: In order to compare estimated coefficients for Z·X and Z across test scores and attribute those differences to skill-specific employer learning and screening, we have to contend with the fact that each Z is correlated with S, X, and other regressors and that these correlations differ across test scores. Table 2 shows correlations between each (raw) test score and S, black, Hispanic, X and IS; because X and IS are time-varying, we use each worker’s initial and final values. Unsurprisingly, each test score is highly correlated with S. These correlations range from a high of 0.645 for mathematics knowledge to a low of 0.426 for mechanical comprehension, which is arguably the most vocationally oriented of our skill measures. Each test score is negatively correlated with black and Hispanic, and with both initial and final values of X—and for each variable, the degree of correlation again varies considerably across test score.17 Scores for the more academic tests (including mathematics knowledge, arithmetic reasoning, and word knowledge) tend to be highly correlated with skill importance, while scores for vocationally oriented tests (coding speed, mechanical comprehension) are much less—and even negatively—correlated with importance.
Pearson Correlation Coefficients for Skill Measures and Select Covariates
To net out these correlations we regress each raw test score, using one observation per person, on each time-invariant regressor (S and the two race/ethnicity dummies) as well as initial and final values for urban status, X, S·X, black·X, Hispanic·X, and the importance score corresponding to the particular test. Because NLSY79 respondents ranged in age from 16–23 when the ASVAB was administered, we also include birth year dummies in these regressions. We then standardize score-specific residuals to have a zero mean and standard deviation equal to one for the “one observation per person” sample of 3,069 men; the standard deviations continue to be very close to one in the regression sample consisting of 22,907 person-year observations.
Our use of alternative test scores also compels us to consider whether the seven ASVAB components measure distinct skills or whether they simply provide alternative measures of a single, general skill. In the top panel of Table 3 we demonstrate that correlation coefficients among raw scores for the seven tests range from 0.54 to 0.84, with the largest correlations belonging to two pairs: word knowledge and paragraph comprehension, and arithmetic reasoning and mathematics knowledge. The bottom panel of Table 3 shows that most of these correlations fall to 0.30–0.50 when we use residual scores although they remain at about 0.7 for the two pairs just mentioned. Clearly, much of the correlation in the raw scores reflects the fact that sample members who are older and/or more highly schooled tend to perform better on all tests. Once those factors are netted out, the dramatically lower correlation coefficients in the bottom panel suggest that we are not simply measuring “general skill” with seven different tests—although the skills measured by word knowledge and paragraph comprehension are undeniably similar, as are those measured by arithmetic reasoning and mathematics knowledge. The evidence in Table 3 suggesting that we are, in fact, measuring five distinct skills (“verbal,” “math,” numerical operations, coding speed, and mechanical comprehension) is corroborated by several studies that use factor analysis or item response theory to analyze ASVAB scores (Stoloff 1983; Welsh, Kucinkas, and Curran 1990; Ing and Olsen 2012).
Pearson Correlation Coefficients for Skill Measures
As a result of correlations among our residual test scores, estimated effects of screening and employer learning for a given skill will potentially reflect screening and learning with respect to any other skill with a correlated test score. Suppose, for example, that employers learn about numerical operations over time but not about paragraph comprehension. Given the modest correlation between the test scores for these skills seen in Table 3, our estimates would identify employer learning with respect to paragraph comprehension—but would correctly identify more employer learning for numerical operations than for paragraph comprehension. In general, our estimates will correctly “rank” the degree of learning (and screening) across distinct skills, even if the test score correlations shown in Table 3 cause some estimates to be overstated.18
In another departure from the existing literature, our covariates include occupation-specific importance scores (ISZ) for each skill measure except AFQT scores. These scores, which we construct from O*NET data, represent the importance of each skill measured by the given ASVAB component in the three-digit occupation associated with the current job; we use the first-coded occupation for each job, so ISZ is time-invariant within job. For example, the score for arithmetic reasoning reflects the importance in one’s occupation of being able to choose the right mathematical method to solve a problem while the score for mathematics knowledge measures the importance of knowing arithmetic, algebra, geometry, etc. The importance scores range from one for “not important” to five for “extremely important” and reflect the average responses of workers surveyed in an occupation.19 Some skills are important in most jobs while others are important in only a few jobs, as the distributions in Table 4 indicate. For instance, paragraph comprehension and word knowledge are “important,” “very important,” or “extremely important” (scores 3–5) in more than half of all observations in our sample while arithmetic reasoning and numerical operations range from “important” to “extremely important” in only about 10 percent of the observations in our sample.
Importance Score Distributions (Full Sample)
Given that importance scores (ISZ) play such a critical role in our analysis, we conclude this section by addressing two questions: Do the scores appear to make sense? What do these scores measure that might be missed by conventional occupation categories? To address these questions, in Table 5 we present importance scores for several three-digit occupations, along with the mean growth in residual wage variance (GRV) reported in Mansour (2012) for the aggregate occupation group to which the three-digit occupation corresponds. Unsurprisingly, the importance scores for “word knowledge” and “paragraph comprehension” are highest for lawyers and lowest for dancers, truck drivers, and auto mechanics. Similarly, importance scores for “arithmetic reasoning” and “numerical operations” are highest for mathematicians and lowest for dancers. Coding speed, which is the ability to find patterns quickly and accurately, is more important for key punch operators than for other occupations in our selected group, while mechanical knowledge is most important for auto mechanics. If any surprise is revealed by Table 5, it is that basic reading, language, and mathematics skills are deemed to be fairly important in each of these disparate occupations.
Importance Scores and Growth in Variance of Log Wage Residuals (GRV) for Select Occupations
Table 5 also illustrates the type of heterogeneity that is captured by ISZ but potentially missed by Mansour’s (2012) occupation-based classification (GRV). A comparison of secondary school teachers and truck drivers reveals that, unsurprisingly, importance scores for most skills differ dramatically across these occupations. However, these highly dissimilar occupations fall into aggregate occupational groups with identical mean GRV. At the other extreme, physicians and biological scientists fall into aggregate occupations (health diagnosing and natural scientists) with GRV values at opposite ends of the distribution (0.291 versus –0.064), despite the fact that importance scores for these occupations tend to be similar. Auto mechanics and truck drivers make another interesting comparison: Importance scores for most skills are virtually identical for these two occupations and, in this case, they have fairly similar values for GRV. However, mechanical comprehension is extremely important for mechanics and much less so for truck drivers. We use these examples to suggest that a measure of “job type” based strictly on occupation codes (as proxied by GRV) lacks the substantive content embodied in a task-based or skill-based measure (ISZ). Importance scores suggest that employer learning with respect to word knowledge might be more pronounced for teachers but not for truck drivers because this particular skill is important for teaching. The use of GRV not only predicts identical employer learning for teachers and truck drivers but lacks the “content” to justify why this (or any) similarity might exist.
IV. Findings
Table 6 reports estimates for eight versions of log-wage Model 9, which is the standard log-wage model used by AP and others to test for employer learning. The first column of estimates uses AFQT scores to represent Z, the skill component that is unobserved by employers. The next seven columns replace AFQT scores with scores for individual components of the ASVAB. In the top panel, we transform each raw test score by regressing it on birth year dummies to account for age differences when the tests were taken, and then standardize the residual scores to have unit variance. In the bottom panel—as well as in all subsequent tables in this section—we switch to the construction method described in IIB1 and IIIB in which residuals are obtained from regressions that also include S, X, ISZ, and other covariates.
Estimates for Log-Wage Model 9 Using Alternative Skill Measures (Full Sample)
We begin by comparing our AFQT-based estimates reported in the top panel of Table 6 to those obtained by AP using a similar specification but data through 1992 only.20 Our estimated coefficient for Z ⋅ X/10 (0.067) is larger than the estimate reported by AP (0.052) while our estimated coefficient for S ⋅ X/10 (0.015) is precisely estimated and of the opposite sign compared to AP’s (imprecise) estimate of –0.019. Because our AFQT-based estimated coefficients for Z ⋅ X are positive, we join AP in finding support for employer learning—but not in finding support for statistical discrimination.
When we replace AFQT scores with individual ASVAB scores in the top panel of Table 6, the estimated coefficients for Z ⋅ X range from 0.046 for coding speed to 0.069 for word knowledge. It is difficult to interpret these differences because, as discussed in IIB, each estimated coefficient reflects covariances between Z and other regressors, including S; as indicated by Table 2, these covariances differ substantially across test scores. If we were to ignore these confounding covariances we would conclude that employer learning is most pronounced for word knowledge and least pronounced for coding speed and mechanical comprehension, which are the only two tests under consideration that measure vocational skill rather than general verbal and quantitative skills.21 This “straw man” result is surprising insofar as we might expect word knowledge to be a skill that workers can accurately signal to employers ex ante while vocational skills would be among the skills employers learn over time by observing performance.
However, such judgments should be based on the bottom panel of Table 6, where we use the portion of Z that is orthogonal to S, X, ISZ, and other regressors. We can now apply the expression for B3t in Equation 11, which tells us that a positive estimated coefficient for Z ⋅ X is consistent with employer learning and that the magnitude of each estimate is a direct measure of employer learning. While each estimated Z ⋅ X coefficient continues to be positive in the bottom panel, we cannot reject the null hypothesis that all eight estimates are identical (nor can we reject the null hypothesis that any pairwise difference is zero). Stated differently, we find evidence of employer learning for all eight skill measures but no evidence that the degree of employer learning is skill-specific. The (statistically significant) difference in the top panel between the smallest estimated Z ⋅ X coefficient and the largest is entirely attributable to the fact that coding speed has a relatively small correlation with S while word knowledge has a large correlation with S (Table 2).22
The estimates in the bottom panel of Table 6 are noteworthy for two additional reasons. First, the estimated coefficients for Z range from a statistically insignificant 0.007–0.012 for paragraph comprehension and word knowledge to a precisely estimated 0.035 for numerical operations. As shown by expression B30 in Equation 12, these estimates reflect the extent to which premarket information other than schooling is correlated with Z (Szq) and the importance of Z in determining productivity (z). We can conclude, therefore, that word knowledge and paragraph comprehension are less screenable and/or less important than other skills. Second, the estimated coefficients for S ⋅ X are small in magnitude but uniformly positive and statistically significant. This again contradicts the model’s prediction (per the expression for B1t in Equation 11) that the relationship between S and log-wages should not change with experience. As noted in IIC (following Farber and Gibbons 1996), a positive S-X slope is consistent with a feature of wage determination abstracted from in the model—namely, that highly schooled workers invest more intensively than their less-schooled counterparts in on-the-job training and/or receive a higher return to these skill investments.23
Before proceeding to a discussion of how skill importance affects our inferences, we discuss the robustness of the estimates reported in the bottom panel of Table 6. In results available from the authors, we experimented with nonlinear skill-experience gradients (Z ⋅ X2) for the model specifications shown in Table 6 given that Lange (2007) and Arcidiacono, Bayer, and Hizmo (2010) find that most employer learning occurs in the first few years of the labor market career. In no instance did this added flexibility affect our inferences.
Table 8 shows estimates for log-wage Model 9 based on subsamples of “occupation stayers” and “importance score stayers” described in IIIA. Given that job mobility—especially toward jobs that place greater importance on the skill measured by test score Z—can produce a positive estimated Z-X slope in the absence of employer learning, our goal is to assess the potential influence of mobility on our “full sample” estimates (Table 6) by comparing them to estimates based on subsamples of workers who do not change occupations, or who do not change occupations “enough” for the Z-specific importance score to change. Both sets of estimates in Table 8 reveal that job mobility has little effect on the full sample estimates. In particular, we fail to reject the null hypothesis that all seven estimated Z·X coefficients are equal in both the “occupation stayer” and “importance score stayer” samples. In a few instances the estimated coefficient for Z·X changes noticeably relative to the Table 6 estimates. For example, in the “importance score stayer” sample the estimated arithmetic reasoning parameter increases from 0.048 (Table 6) to 0.065 (Table 8) while the estimated math knowledge parameter falls from 0.047 to 0.030; only for these two skills do we fail to reject the pairwise equality of the estimated coefficients for Z·X. Overall, the finding that employer learning does not differ significantly across test scores continues to hold in samples of nonmobile workers, indicating that job mobility does not significantly affect our findings.
Additional Estimates Corresponding to the Bottom Panel of Table 6 (Full Sample)
Estimates for Log-Wage Model 9 Using Alternative Skill Measures (Subsamples of Occupation Stayers and Importance Score Stayers)
In Table 9, we present estimates for log-wage Model 9 based on a subsample of men with S = 12 or S = 16 and a subsample of observations associated with blue-collar or white-collar occupations; for each subsample, we allow every parameter in the model to differ by “type.” These estimates permit comparison with the findings of Arcidiacono, Bayer, and Hizmo (2010), which identifies S-specific parameters using the NLSY79, and Bauer and Haisken-DeNew (2001), which identifies parameters for blue-collar and white-collar workers using German Socioeconomic Panel Study data.
Estimates for Log-Wage Model 9 Using Alternative Skill Measures (Subsamples of Men with Schooling = 12 or 16, and Men in Blue- or White-Collar Occupations)
The top panel of Table 9 reveals that the estimated Z·X coefficients are statistically indistinguishable for men with 12 years of schooling and men with 16 years of schooling for each test score. This finding contrasts starkly to evidence in Arcidiacono, Bayer, and Hizmo (2010), who report an imprecisely estimated AFQT·X coefficient equal to 0.01–0.02 for the S = 16 sample, and a precisely estimated coefficient that is ten times larger for the S = 12 sample. While they conclude that employer learning occurs only for less-schooled men, we find no evidence that employer learning differs across the two schooling groups for any skill.24
When we compare the estimated Z·X coefficients for blue-collar and white-collar workers in the bottom panel of Table 9, we find that the point estimates are larger for white-collar workers than for blue-collar workers for all but word knowledge and mathematics knowledge, although only for numerical operations is the pairwise difference statistically significant. This contradicts the conclusions of Bauer and Haisken-DeNew (2001), who find evidence of employer learning for low-wage, blue-collar workers only. The two studies, however, are not strictly comparable given that Bauer and Haisken-DeNew uses German data and a measure of parental schooling in lieu of test scores to represent Z.
As a group, our estimates for log-wage Model 9 reveal that employer learning exists for each skill type, for both S = 12 and S = 16 workers and for both blue-collar and white-collar workers, but that the degree of learning does not vary across skills or worker types.
In Table 10 we report estimates for log-wage Model 13 in which coefficients for Z and Z·X are allowed to vary linearly with skill importance (ISZ). Our goal is to determine whether skill-specific employer learning and screening are themselves functions of the skill’s importance to productivity. Turning first to the right-most column in Table 10, we observe that for mechanical comprehension the predicted relationship between Z and log-wage increases from –0.013 (–0.032 + 0.019) on jobs for which mechanical comprehension is not important (ISZ = 1) to 0.063 (–0.032 + 5 ⋅ 0.019) on jobs for which it is extremely important (ISZ = 5), while the predicted relationship between Z ⋅ X/10 and log-wage decreases from 0.125 to –0.055 over the same range of ISZ scores. As discussed in IIB2, the positive effect of skill importance on the estimated Z coefficient represents an increase in Szq multiplied by skill importance; we interpret this total effect as increased screening. For mechanical comprehension, therefore, we find a distinct tradeoff between screening and learning: When this skill is unimportant, employers do not screen and instead rely on performance histories to reveal productivity over time, but when mechanical comprehension is important employers rely more on screening and less on learning. This suggests that signals of mechanical ability are available at the outset of the career but that these signals are impractical to obtain when employers are relatively unconcerned about the skill.25 We find qualitatively similar patterns for coding speed and mathematics knowledge although for the former skill the Z ⋅ ISZ and Z ⋅ X ⋅ ISZ coefficients are estimated very imprecisely.
Estimates for Log-Wage Model 13 Using Alternative Skill Measures (Full Sample)
Table 10 reveals the opposite pattern for word knowledge, paragraph comprehension, and numerical operations: The estimated Z coefficients decrease in ISZ (which, as discussed in IIB2, necessarily means Szq decreases in importance) while the estimated Z ⋅ X/10 coefficients increase, although most interaction terms are imprecisely estimated. This pattern suggests that signals (elements of q) available to employers at the outset of the labor market career are insufficiently informative for jobs for which the skill is highly important. For such jobs, employers rely on performance to learn about the worker’s skill over time in the absence of a more informative and easily obtained premarket signal.
The Z and Z ⋅ X/10 parameters will not vary linearly in skill importance if, for example, employers only engage in intensive screening when a particular skill is highly important to the worker’s job. To explore these nonlinearities, in Table 11 we report estimates from a specification in which the key parameters are allowed to differ when skill importance is high. As shown in Table 4, some skills are important (ISZ = 3–5) in relatively few occupations while others are important in most occupations. Given the inherent difficult of defining “high” importance uniformly for all seven skills, we use two alternative definitions. In the top panel of Table 11 we define “high” as any importance score in the top quartile of the Z-specific distribution; this requires the raw importance score to exceed 2.56 to 3.48, depending on the skill (Table 4). In the bottom panel of Table 11 we define “high” uniformly across skills as any importance score equal to 3.25 or higher; the percentage of observations meeting this absolute cutoff ranges from two percent for coding speed to 34 percent for paragraph comprehension.
Estimates for Modified Log-Wage Model 13 with Nonlinear IS Effects (Full Sample)
With few exceptions, the estimates in Table 11 reveal the same patterns seen in Table 10. Using quartile-based definitions of “high” skill importance, estimated Z ⋅ high ISz coefficients in Table 11 have the same sign as the corresponding Z ⋅ ISz estimates in Table 10 for all skills. Estimated coefficients for Z ⋅ X/10 ⋅ high ISz in Table 11 and Z ⋅ X ⋅ ISz in Table 10 have the same sign for all skills except work knowledge, where the estimates are effectively zero in both tables. Estimates in the bottom panel of Table 11 are qualitatively similar to those in Table 10 for all skills except arithmetic reasoning and numerical operations, where high importance is defined for a very small number of observations. The estimates in Table 11 suggest that the relationships between skill importance and screening and learning are adequately captured by the linear specification in Table 10, which has the advantage of using all of the variation in IS to identify the relationships between skill importance and screening and learning.26
V. Conclusions
In light of the potential centrality of employer learning to economists’ understanding of life-cycle wage paths, numerous analysts have looked for evidence of learning in broad samples of workers (Farber and Gibbons 1996; Altonji and Pierret 2001; Lange 2007; Schönberg 2007; Pinkston 2009) while others have explored heterogeneity in learning with respect to worker type (Bauer and Haisken-DeNew 2001; Arcidiacono, Bayer, and Hizmo 2010) or job type (Mansour 2012). However, existing studies have relied exclusively on a single cognitive test score (AFQT scores), which means they have identified employer learning with respect to the basic language and quantitative skills measured by this test. Moreover, existing studies of heterogeneous employer learning have relied on broad definitions of worker or job type that do not capture the skill-needs associated with each narrowly defined job.
In the current study, we use seven cognitive test scores—each measuring a well-defined skill such as mathematics knowledge or coding speed—to determine whether employers learn more about some skills than others. We also use direct measures of each skill’s occupation-specific importance to productivity to learn whether employer learning is more or less pronounced when a given skill is relatively important for the work being performed and to assess tradeoffs between employer learning and ex ante screening. We are able to accomplish these objectives by combining test score data from the NLSY79 with O*NET data on each skill’s importance on each three-digit occupation and by deriving conditions under which the magnitudes (and not simply the signs) of parameter estimates are directly tied to the extent of screening and employer learning.
We identify four key results. First, employer learning exists for each skill type and, within each skill type, for high school graduates, college graduates, blue-collar workers, and white-collar workers. Second, before the role of skill importance is brought to bear, we find little evidence that the degree of employer learning differs across skill types or worker types. Third, upon incorporating information on skill importance, we find distinct tradeoffs between employer learning and screening for several skills. Fourth, we find that the effect of skill importance on employer learning and screening differs across skills. When mathematics knowledge and mechanical comprehension are relatively important for a given occupation, employers screen for these skills rather than learn about them over time. In contrast, when word knowledge or paragraph comprehension is important to occupational productivity, employer learning occurs over time but screening is nonexistent. These findings suggest that the manner in which worker ability is revealed to their employers depends intrinsically on the interplay between skill type and skill importance. Studies that focus on a single, general skill and/or explore heterogeneity in employer learning across broad types of workers have masked much of this variation.
Having developed an approach (building on Farber and Gibbons 1996) that facilitates a comparison of how employer learning differs across skills, we conclude by suggesting two dimensions in which our analysis can be extended. First, an examination of employer learning with respect to noncognitive skills seems warranted. We have focused exclusively on cognitive skills that range from basic verbal and quantitative skills to vocationally oriented skills. Ignoring skill importance, we conclude that employer learning does not differ across these skill types; a different conclusion might be reached if measures of conscientiousness, agreeableness, and locus of control are considered—although, as noted in Section III, a lack of data on the occupation-specific importance of noncognitive skills is why we confine our attention to cognitive skills. Second, existing evidence (Schönberg 2007; Pinkston 2009) that employer learning is largely public rather than private might not hold up in an analysis that considers both alternative skill types and the role of occupation-specific skill importance.
Appendix 1 O*NET Data
We use O*NET data to associate seven skill-specific importance scores (ISZ) with each unique job (defined as a spell with a given employer) in our NLSY79 data. These importance scores are used as regressors in select specifications of the log-wage model. O*NET refers to the Occupational Information Network, which is a data collection and dissemination project (replacing the Dictionary of Occupational Titles) sponsored by the Employment and Training Administration of the U.S. Department of Labor and conducted by the North Carolina Employment Security Commission. Details on the project and the data used for our analysis are available at www.onetcenter.org.
The O*NET database has descriptive information for 1,102 distinct occupations defined by the O*NET-SOC occupational taxonomy, which is modeled after the Standard Occupational Classification (SOC) taxonomy. The descriptive variables (referred to in O*NET documentation as “descriptors”) consist of 277 distinct measures of the abilities, knowledge, skills, and experience needed in the workplace as well as the tasks and activities associated with various types of work. These descriptors comprise the O*NET content model, which decomposes the various dimensions of work into three worker-oriented domains (worker characteristics, worker requirements, and experience requirements) and three job-oriented domains (occupational requirements, workforce characteristics, and occupation-specific information). Each domain contains a large set of measurable characteristics (descriptors). For example, the worker characteristics domain contains numerous measures of abilities that influence performance on the job, ranging from written comprehension to selective attention to explosive physical strength; it also contains measures of preferences for different work environments and work styles that affect job performance. The worker requirements domain contains numerous types of knowledge ranging from economics to mathematics to telecommunications, while the experience requirements domain contains measures of the amount of experience in such areas as writing, mathematics, programming, and time management needed to enter each occupation. Some descriptors measure the importance of an ability or type of knowledge to each occupation and others measure the frequency with which a type of knowledge is used or a task is performed. We focus exclusively on descriptors that identify—using a scale of 1 to 5—the importance of select abilities and types of knowledge for each occupation.
O*NET data are updated on a “rolling” basis by conducting a survey approximately every six months that focuses on a subset of occupations in the O*NET database. Each data collection effort involves randomly sampling businesses that are likely to employ workers in the selected occupations, randomly sampling workers within those businesses, and then randomly assigning the sampled workers questionnaires designed to elicit occupation-specific information associated with a subset of O*NET descriptors. The data collected from surveyed workers are used to score descriptors for their occupations.
We face a number of challenges in combining O*NET data with NLSY79 data and constructing occupation-specific importance scores (IS). First, we require a clear-cut mapping between our chosen NLSY79 skill measures and the associated O*NET importance scores. Table A1 briefly describes the skill that is measured by each of the seven ASVAB scores along with the O*NET descriptor that we use to measure the skill’s importance on the job. Using word knowledge as an example, we are measuring sample members’ “ability to select the correct meaning of words presented in context,” and measuring the importance in their current job of knowing “the meaning of words” as well as other language-related components.27 In most cases, our NLSY79 skill measures map into a unique O*NET descriptor in a straightforward manner. In cases where two viable O*NET descriptors exist for a given skill measure, we use the O*NET descriptor that in our judgment best matches the ASVAB component under consideration. For example, “mathematics skill” (defined as the ability to use mathematics to solve problems well) is available in the O*NET skills module; this skill is very highly correlated with “mathematics reasoning” ability, which we use for the arithmetic reasoning IS score. Given the high correlations between such O*NET descriptors, our estimates are not sensitive to the choice of descriptor.
Description of NLSY79 Skill Measures and Corresponding O*NET Importance Scores
Second, we require uniform occupation codes in order to merge O*NET data with NLSY79 data. The O*NET database only contains O*NET-SOC codes while for our observation period the NLSY79 provides 1970 three-digit Census occupation codes. We use a cross-walk to convert O*NET-SOC codes to DOT codes, and then another cross-walk to convert from DOT codes to three-digit 1970 Census codes. In cases where multiple O*NET-SOC categories map into a given Census category, we compute the average O*NET importance score for that Census category.
Third, we need to associate each job reported in the NLSY79 with a single occupation code. Jobs that are reported by NLSY79 respondents in multiple interviews can have time-varying occupation codes. Temporal variation might reflect true changes in respondents’ work assignments, or it might reflect the fact that verbatim job descriptions recorded in each interview are coded differently across interview rounds.28 To skirt the within-job variation in occupation codes, we associate each job in the NLSY79 with the first-coded occupation; we also confirmed that using the modal or last-coded occupation does not affect our findings.
Footnotes
Audrey Light is a professor of economics at Ohio State University.
Andrew McGee is an assistant professor of economics at Simon Fraser University and a research fellow at IZA. The data used in this article can be obtained beginning June 2015 through May 2018 from Audrey Light, Department of Economics, Ohio State University, 410 Arps Hall, 1945 N. High Street, Columbus, OH 43210; email: light.20{at}osu.edu.
↵1. We also use AFQT scores in our log-wage models for comparison with existing studies. To our knowledge, no prior study reports estimates based on a cognitive test score other than the AFQT, although Pinkston (2006) notes (p. 279, Footnote 23) that he used two ASVAB test scores and obtained results that “resembled” his AFQT-based estimates. As alternatives to test scores, analysts have used parental schooling attainment (Altonji and Pierret 2001; Bauer and Haisken-DeNew 2001; Pinkston 2006; Arcidiacono, Bayer, and Hizmo 2010), sibling wages (Altonji and Pierret 2001; Pinkston 2006) or the presence of library cards in the household at age 14 (Farber and Gibbons 1996; Altonji and Pierret 2001).
↵2. Equation 1 imposes the restriction that λz (and all coefficients) is uniform across employers and occupations; we discuss the implications of relaxing this restriction in IIC.
↵3. We defer discussion of these characteristics (Ri) to IIC and IIIB.
↵4. Szg in Equation 11 now refers to the covariance between
(not Zi) and productivity signals. We use (standardized, residual test scores) throughout our empirical analysis, but in the remainder of this section we often leave implicit that Zi is, in practice, transformed into .↵5. The expression for B1t in Equation 11 indicates that once we replace Zi with
, we should expect in Specification 9 to be 0 because Si does not serve as a signal for the portion of Zi that is orthogonal to schooling. This testable hypothesis originates with Farber and Gibbons (1996) who, in contrast to AP, also used rather than Zi as a regressor.↵6. Altonji (2005) proposes a model in which the rate at which employers learn is related to the overall level of skill importance in an occupation. Altonji does not pursue this extension empirically.
↵7. In Equation 10 we use initial and final values of time-varying regressors and assume that this effectively reduces their covariances with Zi to 0. Letting X represent a single component of R for illustration, once we construct residual test scores in this fashion, Szx = 0 and the expected value of b5 is reduced to a function of Szg and sample moments Sz,z*x, Ss,z*x, Sz,s*x, Sz*x,x, etc., as well as other sample moments that do not involve Zi (and therefore do not vary across Z). We can use the law of iterated expectations to show that each population covariance involving Zi equals 0 or equals a value that does not vary with Zi; for example, Ss,z*x = 0 and Sz,z*x = E(X). The sample moments will not be exactly 0 because we have a finite and unbalanced sample, but we expect them to contribute little to cross-Z variation in estimated slope parameters.
↵8. Workers may also move between occupations to learn about their own skills (Antonovics and Golan 2012). Our estimates based on a subsample of (occupation or importance level) “stayers” allow us to assess empirically the effect of such experimentation on estimates of employer learning.
↵9. Kahn and Lange (2010) test a model of the evolution of wages nesting both employer learning and human capital models and find support for both.
↵10. Structural approaches that consider the role of multidimensional skills in determining earnings include James (2011) and Yamaguchi (2012).
↵11. In light of our discussion of endogenous mobility in C2, it is worth noting that if workers move systematically to jobs placing more or less importance on a skill, speed of learning models will conflate these systematic changes in λz with employer learning.
↵12. Farber and Gibbons (1996), Altonji and Pierret (2001), Lange (2007), and Arcidiacono, Bayer, and Hizmo (2010) use data through 1991, 1992, 1998, and 2004, respectively.
↵13. Following U.S. Census Bureau definitions, we define a wage observation as white collar if the worker’s initial occupation corresponds to professional, technical, and kindred workers; managers and administrators, except farm; sales workers; or clerical and kindred workers. A wage observation is classified as blue collar if the initial occupation corresponds to craftsmen and kindred workers; operatives, except transport; transport equipment operatives; or laborers, except farm.
↵14. Highest grade completed is used to represent S throughout the employer learning literature, but we suspect this measure is not directly observed by employers: resumes, job applications, and school transcripts typically report degree attainment, credit completion, and enrollment dates, but not highest grade completed. See Frazis, Ports, and Stewart (1995), Kane, Rouse, and Staiger (1999), and Flores-Lagunes and Light (2010) for discussions of why highest grade completed and highest degree might capture distinct information.
↵15. NLSY79 respondents were administered the ASVAB in 1980. All respondents were targeted for this testing—which was conducted outside the usual in-person interviews—and 94 percent completed the test.
↵16. Our seven skill measures are the only ones satisfying two requirements: (a) they must be measured for NLSY79 respondents prior to the start of the career, and (b) an O*NET measure of skill importance must be available for the skill. Other precareer NLSY79 skill measures (for example, the three remaining ASVAB components and noncognitive skill measures such as locus of control and self-esteem) do not map cleanly into O*NET importance scores. Other O*NET importance scores (for example, physical stamina) are not assessed by the NLSY79.
↵17. The pronounced, negative correlation between skill and Xf (final potential experience) reflects the fact that less-skilled individuals leave school earlier and are therefore more likely than their more-skilled counterparts to contribute an observation at (or near) the maximum experience level of 15 years.
↵18. In principle, we can eliminate correlations among test scores by including all other scores in the regressions used to compute skill-specific residual scores. We do not use this strategy due to concerns that “noise” dominates the remaining variation in each residual score. We do not include multiple test scores in a single regression because AP’s test for EL requires scalar measures of Z.
↵19. See Appendix 1 for additional details on how O*NET creates importance measures and how we construct our IS variables.
↵20. As reported in their Table 1, Column 4, AP’s estimates (robust standard errors) for Z, Z ⋅ X/10, S and S ⋅ X/10 are 0.022 (0.042), 0.052 (0.034), 0.079 (0.015) and −0.019 (0.012), respectively.
↵21. While we fail to reject the joint hypothesis of equality of the estimated Z ⋅ X coefficients in the top panel of Table 6, the pairwise difference between the estimated word knowledge and coding speed Z ⋅ X coefficients is statistically significant.
↵22. When we construct standardized, residual test scores from regressions of Z on birth year dummies and S but no additional regressors, we obtain estimates (not reported) that are virtually identical to those in the bottom panel of Table 6. Thus, we conclude that differences between the top-and bottom-panel estimates in Table 6 are due to Szs.
↵23. Farber and Gibbons (1996) include interactions between S and year dummies in their wage model to net out secular increases in the price of skill. When we add similar interactions terms, our estimated S ⋅ X coefficients fall to zero or, in some cases, become negative. Because we use a narrow birth cohort and measure experience as elapsed time since school exit, we believe that skill-price effects cannot be distinguished from the effects of post-school skill acquisition.
↵24. Using data and programs provided by the authors (available at http://www.aeaweb.org), we determined that the findings reported by Arcidiacono, Bayer, and Hizmo (2010) are driven by college-educated men whose potential experience is significantly overstated. See Light and McGee (2013) for details.
↵25. When hiring automobile mechanics, for example, employers care about mechanical comprehension and are likely to obtain signals provided by certification programs.
↵26. Additional (untabulated) experiments reveal that the patterns seen in Tables 10–11 are robust to allowing the effects of X, X2, X3, S, and S ⋅ X to vary with IS, adding Z ⋅ X2 effects interacted with IS, and allowing the Z and Z ⋅ X parameters to vary more flexibly with IS. We also estimate Specification 13 for pooled S = 12/S = 16 samples and pooled blue-collar/white-collar samples and continue to find that parameters do not vary across worker type; for each skill the p-value for the null hypothesis that parameters are equal across workers type is 0.40 or larger.
↵27. We do not use the three remaining ASVAB scores (general science, auto/shop knowledge, electronics information) or the noncognitive skill measures available in the NLSY79 (such as the Rotter Locus of Control) because it is much less obvious which O*NET descriptor would measure the importance of those skills on the job.
↵28. From 1994 onward, within-job variation in occupation is reduced because new job descriptions were only elicited from survey respondents who first stated that their job responsibilities had changed. We cannot exploit this regime change because most respondents are well into their careers by 1994, and employer learning has been shown to be concentrated in the first few years (Lange 2007). Moreover, given the difficulties inherent in coding verbatim job descriptions, one-time reports do not necessarily produce more accurate occupation codes than multiple reports.
- Received March 2013.
- Accepted January 2014.
