Assessing the IQ-earnings link in environmental lead impacts on children: Have hazard effects been overstated?

Environmental Research 131 (2014) 219–230

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Environmental Research journal homepage: www.elsevier.com/locate/envres

Assessing the IQ-earnings link in environmental lead impacts on children: Have hazard effects been overstated? David S. Salkever a,b,n a b

Department of Public Policy, University of Maryland-Baltimore County (UMBC), USA Department of Health Policy and Management, Bloomberg School of Public Health, The Johns Hopkins University, USA

art ic l e i nf o

a b s t r a c t

Article history: Received 13 August 2013 Received in revised form 2 January 2014 Accepted 18 March 2014

Studies in the 1990s by Schwartz and by Salkever provided the bases for measuring the earnings impacts of IQ decrements due to lead exposure for children, and many subsequent regulatory, policy guidance, and academic analyses adopted the estimates from these studies. Results by Salkever implied somewhat greater impacts of IQ decrements, but have been contested, in a series of more recent critical review articles, as overestimates of the negative impacts on children's future earnings caused by IQ decrements due to lead exposure. This paper examines the contentions of proponents of this overstatement hypothesis, the applicability of the evidence they offer, and the results from an additional important study from 1998 heretofore overlooked in the literature. Results of this examination indicate that the evidence for the overstatement hypothesis is seriously flawed. Studies cited to support this hypothesis (1) often report only evidence on wage impacts and thus ignore IQ impacts on hours of work and work participation rates, (2) give lesser weight to or completely exclude population groups that show relatively higher IQ impacts (e.g., women), and (3) give substantial weight to pre-1980 wage and earning data, thereby omitting the influence of recent upward trends in skill differentials in earnings and increasing returns to education. Because of these and other deficiencies, available evidence does not substantiate the overstatement hypothesis. In contrast, recent evidence overlooked by the proponents of this hypothesis suggests that the results reported by Salkever understate the actual strength of the negative IQ impacts from lead exposure. & 2014 Elsevier Inc. All rights reserved.

1. Introduction Following seminal work by Needleman et al. (1979, 1990), Needleman and Gatsonis (1990), Needleman (2004), Bellinger et al. (1991), and Bellinger (2008) that reported damaging neurocognitive effects on young children of even low levels of lead exposure, federal policy analysts at the Environmental Protection Agency (EPA) and the U.S. Centers for Disease Control (CDC) began to carefully examine the economic importance of these effects. One of the most salient dimensions of economic impact was the projected loss of earnings for each successive cohort of exposed children. Early studies by Schwartz (U.S. CDC, 1991, Appendix II; Schwartz, 1994), using U.S. Bureau of the Census age-earnings profiles for 1987, suggested that lead exposure sufficient to cause a 1-point decrement in IQ per child would result in reductions in earnings (for each annual cohort of U.S. children) in excess of $5 billion, equivalent to more than $11.4 billion in current (September

n Correspondence address: Department of Public Policy, University of Maryland-Baltimore County (UMBC), Baltimore MD, USA. E-mail address: [email protected]

http://dx.doi.org/10.1016/j.envres.2014.03.018 0013-9351/& 2014 Elsevier Inc. All rights reserved.

2013) dollars. (The adjustment to 2013 was based on the increase in the level of the BLS Employment Cost Index.) An updated analysis published one year later (Salkever, 1995) suggested that the Schwartz loss figures were approximately 40% too low; this result implied that the earnings reductions per cohort for a 1-point IQ decrement were actually in excess of $7 billion (in 1987) or more than $15 billion in current dollars (September 2013). Adjustment for 14 per cent growth in the under-15 population from 1990 to 2010 would increase the latter figure to more than $17 billion per annual cohort. Findings from these early studies fueled expectations that the vigorous policies of the 1970s and early 1980s, aimed at lowering lead exposure from gasoline, residential paint and other sources, promised substantial benefits from reducing these earnings losses. As a result, in the 1990s and beyond, evaluative studies by Federal agencies that assessed policies to control lead exposures gave the estimation of such benefits a prominent place in their reports (U.S. CDC, 1997; U.S. EPA, 1997, 2000, 2005, 2006, 2008a, 2008b). A series of recent literature reviews (Grosse et al., 2002; Grosse, 2007; Robinson, 2007, 2013), however, have critically re-assessed the evidence from the earlier studies, and advanced the overstatement hypothesis that the earnings impact of IQ decrements

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due to harmful exposures has been substantially exaggerated. The lesson they draw, either explicitly or implicitly, is that expected beneficial effects of controls on environmental exposures are in fact far less than some earlier studies would imply. In this paper, we examine more carefully the available evidence for and against these critical re-assessments. We begin in Section 2 by describing the conceptual approaches used in statistical models of the impact of IQ decrements on earnings. Sections 3 and 4 then present a detailed review and discussion of the methods and results from the only four studies that have developed estimates of such impacts on average annual earnings. We highlight important empirical findings relating to the different components of IQ impacts, consistent differences in impacts across demographic groups defined by gender and race, and possible explanations for differences in estimates across these four studies. Section 5 briefly reviews other empirical studies from the labor economics literature, with reported estimated IQ impacts on average hourly wages, which have been cited as evidence in the case for the overstatement hypothesis. We note that the empirical findings from these empirical studies (1) confirm our expectation that IQ impacts on average hourly wages are substantially smaller than estimated impacts on annual earnings and (2) corroborate the pattern of demographic differences in IQ impacts noted in Section 3. Section 6 critically re-examines an important metaanalysis that has also been cited by the overstatement hypothesis proponents, and explains the reasons why the evidence in this meta-analysis does not in fact support that hypothesis. With the careful evidentiary review of Sections 3–6 as background, Section 7 re-examines the literature reviews that have argued in support of the overstatement hypothesis. This section considers several interesting measurement and statistical issues, and then documents a pattern in these reviews of conceptual confusions and inappropriate generalizations from particular population groups to the general population. These difficulties, and others detailed in Section 7, led the proponents of the overstatement hypothesis to misread the actual empirical evidence that does not in fact support their arguments. Section 8 briefly explains a plausible argument for understatement of IQ impacts, and Section 9 provides a summary and concluding comments.

2. Conceptual considerations 2.1. Overview of conceptual models of toxic environmental exposure impacts on IQ and earnings Empirical studies that relate measures of IQ to earnings can generally be classified into one of two categories. The first is studies that use recursive models that develop separate estimates of (a) “direct” IQ impacts on earnings statistically controlling for levels of education and (b) the “indirect” impacts of IQ on earnings that are the combined result of the influence of IQ on levels of education and the direct influence of education on earnings. A schematic representation of this recursive model is shown in Fig. 1. The impact of toxic exposure on measured IQ is arrow 1. Arrow 5 represents the direct impact of IQ on earnings, while the indirect impact of IQ on earnings, working through the influence of IQ on education, is the product of arrows 2 and 6. Thus, the total impact of IQ on earnings is the sum of the direct impact and the indirect impact. The role of “other factors” in the analysis (arrows 3 and 4) is discussed below.1 1 Note that arrow 1, the direct epidemiologic link between exposure and IQ, is portrayed as a dashed line to signify that it is an input to the studies we discuss but is not directly estimated in these studies.

Fig. 1. Recursive model of exposure impacts on IQ and earnings showing direct IQ impacts controlling for education (5), and indirect IQ impacts via education (2)  (6). Arrow 1, in Figs. 1–5 or this paper, is dashed to indicate that in the studies reviewed here, the corresponding impact magnitude is not directly estimated, but is obtained from prior published epidemiologic studies.

The second category is studies that used more parsimonious reduced-form models. These models do not explicitly include education in the analysis, and estimate a single total IQ impact on earnings that combines the “direct” and “indirect” IQ effects noted above. A schematic representation of a reduced-form model is shown in Fig. 2. In this case, the impact of IQ on earnings (arrow (5)) represents the total impact (directþindirect) of IQ, since the model does not statistically control for education. 2.2. Decomposition of earnings impacts The estimated impact of a 1-point IQ change on annual earnings per person for any group of persons is simply the change in the expected value of annual earnings per person (controlling for other factors, as in Figs. 1 and 2). Note that annual earnings per person is just equal to W  H  P, where W is the earnings per hour for persons who do any work in a year, H is the average hours of work for these persons, and P is the work participation rate (i.e., the fraction of persons in the group who do any work in the year). Thus, we can express the total impact of the 1-point IQ change on expected earnings per person, in percentage terms, as the sum of (1) the percent impact on wages per hour (ΔW/W) plus (2) the percent impact on hours (ΔH/H) plus (3) the percent impact on the work participation rate (ΔP/P).2 Assuming that each of these 3 terms is negative for a 1-point decrement of IQ, omission of any one of these terms will lead to an under-estimate of the negative impact of the IQ decrement on earnings. A simpler decomposition applies for studies that examine annual earnings for those who work (rather than wages and work hours separately). In this case, the total earnings impact in percentage terms, of a 1-point change in IQ is just the sum of the percent impact on earnings (ΔE/E), where E is the annual earnings for those with any work, plus the impact on work participation (ΔP/P). (As above, if both percent impacts are negative for a 1-point IQ decrement, omission of the work participation impact leads to an under-estimate of the negative impact of the IQ decrement on earnings.) 2.3. Other factors that influence earnings Figs. 1 and 2 indicate that studies that estimate IQ impacts on earnings also usually control for other factors, such as demographic characteristics and family background, by including them as covariates in the statistical models. For purposes of this discussion, our main concern is the extent to which inclusion or 2 See the online supplement (https://umbc.academia.edu/DavidSalkever) for the details of the algebra that lead to this result.

D.S. Salkever / Environmental Research 131 (2014) 219–230

Fig. 2. Reduced-form model of exposure-related total IQ impacts on earnings (5).

omission of some of these covariates will result in a bias that either attenuates or increases the size of the estimated IQ impact on earnings. A particular concern is inclusion in the models of covariates that may themselves be influenced by IQ (e.g., occupational status or work experience measured when the individual is an adult). When such covariates are included, the resulting estimates of IQ impacts capture only a portion of the total causal influence of IQ on earnings. VanderWeele (2009 and n.d.) has stated the relevant general concern about using “intermediate” outcomes in causal models: “Controlling for a variable occurring after the treatment that is a consequence of treatment can bias our estimates. Effectively, by controlling for such “post-treatment” variables, one blocks part of the effect of treatment…” In the current context, these intermediate outcome variables become blocking variables that attenuate estimated impacts of IQ on earnings.

3. Recent estimates of IQ impacts on annual earnings We now discuss models, data, and results from the three recent empirical studies (Salkever, 1995; Johnson and Neal, 1998; Zax and Rees, 2002) that used recursive and/or reduced form models identical or similar to the models sketched in Figs. 1 and 2. We also provide a detailed review of the original approach used by Schwartz (U.S. CDC, 1991, Appendix II; and Schwartz, 1994) and point out interesting differences between his approach and these 3 recent studies. Table 1 provides a convenient summary that compares the major empirical results among all 4 of these studies; thumbnail descriptions of the major characteristics of these studies are given in Appendix Table A1.3 Salkever (1995) analyzed education and earnings data for a national sample of young adults from the 1979 National Longitudinal Survey of Youth (NLSY79). The education and income data he utilized were reported in the 1990 follow-up of the survey (when NLSY79 respondents ranged in age from 25 to 33). The conceptual framework employed in this study is depicted in Fig. 3; note that it is identical to the recursive model of Fig. 1 except that in Fig. 3 the direct and indirect IQ effects on earnings are each decomposed into two parts: effects on annual earnings of workers (arrows 5a, 2 and 6a) and effects on participation in work (arrows 5b, 2 and 6b).4 3 Further explanatory details relating to these tables are provided in in the online supplement (https://umbc.academia.edu/DavidSalkever). 4 The two arrows at the bottom of the figure are shown as dotted lines since annual hours equals annual hours of workers multiplied by the work participation

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An important feature of the NLSY79 was that it included an administration of the Armed Forces Qualifying Test (AFQT) in 1980 to all ongoing study participants. (Test results were obtained for approximately 11,500 respondents out of a 1980 total of slightly over 12,100 respondents.) Results from this test, rescaled to a mean of 100 and a standard deviation of 15, were used as the indicator of cognitive ability. (We follow the practice in the literature reviewed here of defining “IQ” as cognitive skills measured by a standardized test. Further discussion of concerns about using the AFQT or other cognitive ability tests (used in other papers discussed here) is presented in Section 7.) The IQ impact estimates from Salkever (1995) are summarized in Table 1, rows 1–3. Separate estimates were obtained for males and for females; note that the percentage impact estimates for females were considerably larger. A single set of impact estimates, based on combining data from males and females, are shown in row 3 of the table. The combined estimate for the total impact of a 1-point IQ decrement is  2.563%. Approximately one-fifth of this impact is due to the effect on work participation (  0.498%), with remainder due to the impact on annual earnings for those with any work. A second set of impact estimates from the NLSY79 was obtained by Johnson and Neal (1998), using the reduced-form model depicted in Fig. 4. This study differs from Salkever (1995) in a number of details pertaining to: age-standardization of the AFQT scores, inclusion of only the major random samples and subsamples of NLSY79 respondents, exclusion of older respondents, and exclusion of family background covariates. (See Appendix Table A1.) The only dependent variable was annual average earnings, however, and thus a participation effect was excluded from the study.5 Key results from Johnson and Neal (1998) are in rows 4–6 of Table 1. The estimated directþindirect impacts in column (b) for both males and females are approximately one-third larger than the analogous results from Salkever (1995). Note, however, that Johnson and Neal confirm the finding from Salkever that impacts for females are about 50 percent larger than those for males. Rows 7–10 show comparative results by race and gender from Johnson and Neal, which indicate much larger impacts for black males vs. white males, and much larger impacts for white females vs. black females. Column (a) of rows 7 and 8 also report the only estimates provided by Johnson and Neal of direct IQ impacts on annual earnings, controlling for schooling by including 0-1 indicators for high school graduates and college graduates. We note that these estimates for males are very similar to the direct IQ impact estimate for males from Salkever (1995) in row 1. This indicates that the somewhat larger impact estimates in Column (b) for Johnson and Neal arise from larger estimates of indirect IQ impacts working through the influence of IQ on education levels. Zax and Rees (2002) reported IQ impact estimates from reduced-form models using the same general methods as Johnson and Neal, but with some very important specific differences in their data and methods. First, their study population was restricted to males from the Wisconsin Longitudinal Study, all of whom were high school seniors when first surveyed in 1957, all of whom graduated from high school, and almost all (about 98%) of whom were white. Zax and Rees used earnings at age 35 (i.e., in 1974) and

(footnote continued) rate, so no statistical estimation is needed to estimate the magnitudes of these two arrows. 5 We provide an approximation to these missing participation effects in note b to Table 1. Because annual earnings for workers were averaged for each respondent over the years 1990–1992, those who reported zero earnings in only one or two of these years were included in this average; thus the rate of non-participation (i.e., zero earnings in all three years) was about 40% below the rate for a single year of earnings. See the online supplement for further details on this.

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Table 1 Earnings impact estimates. Study

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15

Salkever (1995)

Johnson and Neal (1998)

Zax and Rees (2002)c Zax and Rees (2002)d Zax and Rees (2002)e Schwartz (1994)

Population group to whom the estimate applies

Males age 25–33 Females age 25–33 Overalla age 25–33 Males age 25–28 Females age 25–28 Overalla age 25–28 Black males age 25–28 White males age 25–28 Black females age 25–28 White females age 25–28 White males age 35 White males age 53 White males age 35 White males age 35 Malesf

Impacts on annual earnings of workers

Participation effect

Total

Col. a Earnings direct

Col. b Earnings directþ indirect

Col. c Work participation

Col. d Total

 1.240  1.400  1.318 NA NA NA  1.484  1.252 NA NA NA NA NA NA  0.500

 1.731  2.415  2.065  2.271  3.389  2.817  2.987  2.134  2.885  3.618  0.752  1.390  0.577  0.390  1.286

 0.200  0.810  0.498 NAb NAb NA NA NA NA NA NA NA NA NA  0.473

 1.931  3.225  2.563 NAb NAb NA NA NA NA NA NA NA NA NA  1.759

a The weights used to combine estimates for males and females were based on the male and female populations under the age of 15 in the US in 2010: 31,757,000 males and 30,355,000 female. http://www.census.gov/population/age/data/2010comp.html, Table 1, accessed 11.23.13. b Using an approximation to the Johnson and Neal data sample, we developed work participation impact estimates of  0.077% for males and  0.367% for females. Combining these with results in the table, we get total impact estimates in rows 4 and 5 of  2.348% and  3.756% respectively. See the on-line supplement for further details. c Model 1; see Appendix Table A1, row D. d Model 2; see Appendix Table A1, row E. e Model 3; see Appendix Table A1, row F. f Some information for females is included. See the text and online supplement for explanation.

Fig. 3. Recursive model from Salkever (1995) with annual earnings factored into two components (annual earnings of workers and work participation rate).

Fig. 4. Reduced-form model of exposure-related total IQ impacts on earnings of workers.

earnings at age 53 (i.e., in 1992) as their dependent variables. As in Johnson and Neal, persons with zero earnings were excluded from the regressions so participation effects of IQ were not captured. Since the Zax and Rees study population was confined to white males, the demographic group showing the smallest impacts in the Johnson and Neal study, one would expect relatively small estimated IQ impacts for that reason alone. Another very important factor leading to this expectation is the exclusion of persons

who did not graduate from high school; since this exclusion attenuated the variance in their sample in schooling level, in effect the Zax and Rees IQ impact estimates are intermediate between direct estimates (with statistical controls for level of education) and total (directþindirect) estimates (as in Johnson and Neal). The fact that Zax and Rees use much earlier dependent variable data (from 1974) than the data used by Salkever and by Johnson and Neal may also tend to produce lower impact estimates if in fact IQ impacts have been increasing over time. We return to this issue in Section 4.6 Results from Zax and Rees reported in Table 1 confirm these expectations of lower IQ impact estimates. For example, their estimate in row 11 (  0.752%) is only roughly one-third the size of the corresponding estimate for white males from Johnson and Neal (  2.134%) or the latter's estimate for all males (  2.271%); it is also well below both the direct and total impact estimates for males from Salkever. The Zax and Rees estimates for their study sample at age 53 (row 12) increased substantially, to  1.39%, though still well below the directþindirect impact estimates from Salkever and from Johnson and Neal. In rows 13 and 14 of Table 1, we report two additional estimates from Zax and Rees. The estimate in row 13 is obtained from a regression that includes a number of covariates describing household and parental characteristics at baseline. Note that inclusion of these additional covariates reduces the magnitude of the estimate of IQ impact. The estimate in row 14 adds a number of additional parental, community and school characteristics as covariates, and a 0-1 indicator of whether or not the respondent was planning to attend college. As Grosse (2007) has noted, this latter covariate is presumably an intermediate outcome affected by the respondent's IQ, and its inclusion therefore can be presumed to be a blocking variable as described by VanderWeele (2009).

6 Note also that the IQ measure Zax and Rees used (respondents' scores on the Henmon–Nelson administered in eleventh-grade) appears to show lower correlations with future earnings and earnings-related outcomes than other comparable tests (Jencks et al., 1979, Chap. 4; personal communication from Jencks cited in Zax and Ress, 2002).

D.S. Salkever / Environmental Research 131 (2014) 219–230

Fig. 5. Model for Schwartz' synthesis estimates. All arrows in this figure are dashed to indicate impacts magnitudes not directly estimated obtained from prior published studies.

Inclusion of this blocking variable (as well as additional covariates) leads to a further reduction in the estimated IQ impact to 0.39%.7 A fourth recent study from the literature that has presented earnings impact estimates is from Schwartz (U.S. CDC, 1991, Appendix II; Schwartz, 1994). Rather than estimating impacts directly from a data analysis, Schwartz assembled and synthesized a set of estimates from reviews of prior studies. Fig. 5 depicts the conceptual approach employed, which differs somewhat from the studies discussed above in several respects. First, Schwartz includes two direct links (arrows 7a and 7b) from exposure to education rather than a single direct link from IQ to education (arrow 2 in Figs. 1 and 3). Magnitudes of the exposure-education links were based on findings from and interpretation of the epidemiology literature. It is important to note that these magnitudes result from overall effects of lead exposures on young children, which include both cognitive impacts and behavioral impacts (Needleman, 2004). Arrow 7a represents the lead exposure effect on years of education completed, while Arrow 7b represents the exposure effect on probability of high school completion. The magnitude estimates for each of these arrows pertains to elevated blood lead levels rather than IQ decrements; each is converted by Schwartz to a perIQ-point basis by dividing them by 0.25 (the estimated IQ points lost for each 1 μg/dL increase in blood lead levels). Schwartz combined the magnitude estimate for Arrow 7a with a magnitude estimate for Arrow 6a based on his review of multiple studies (see the online supplement for details) relating education to wages, to estimate the lead exposure effect via reduced education on annual earnings of workers. He used the magnitude estimate for Arrow 7b and an estimate from Cropper and Krupnick (1989) of male high school graduate vs. non-graduate differences in labor force participation, in estimating the lead exposure effect, via reduced graduation probability, on the work participation rate. To arrive at an estimate of the direct effect of a 1-point IQ loss on annual earnings of workers (Arrow 5a), Schwartz used results from a literature survey of estimated direct IQ effects on earnings (Barth et al., 1984), and an analysis by Grilliches (1977) of estimated direct IQ effects on 1959 median earnings for the preferred occupation at age 30 of young men (as indicated in 1969 by respondents to the National Longitudinal Survey of Young Men, who were in the age range 17–27 at that time and had a mean age of 21). His estimate of the overall percentage effect on annual earnings of lead exposure per IQ point loss was computed as: [Arrow 1  Arrow 5a]þ[Arrow 7a  Arrow 6a]þ[Arrow 7b  Arrow 6b]. The estimates from Schwartz are shown in Row 15 of Table 1. The table indicates that the population group covered is limited to males. While Schwartz presents his estimates as applying to both genders combined, we present them in Table 1 as pertaining only to males because the three magnitudes in his analysis that are

7 Robinson (2012) noted that another covariate included in this model that may block IQ impacts was a categorical indicator of parents' encouragement or discouragement of college attendance.

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arguably most important (represented by arrows 5a, 6a, and 6b) are actually based only or primarily on data for males. One (Arrow 5a) is the direct IQ effect on earnings from Barth et al. (1984) and Grilliches (1977); the former reviews 19 different estimates from empirical studies, 18 of which are based only on males, while the latter also uses data only for males. Shackett (1981), cited in Barth, notes a direct effect of IQ (controlling for experience) that is 60% larger for women than for men. Grosse (2007) also suggests that for women “the estimated associations between earnings and observed test scores are 30–40% larger than for men.” A second magnitude based solely on males is Arrow 6a, the effect on earnings of an additional year of school (see the on-line supplement for details). The third magnitude, represented by Arrow 6b, is the work participation effect of high school graduation, drawn partly from Cropper and Krupnick's regression analysis of data for males, aged 18–65 in 1977. Several other factors may have contributed to Schwartz presenting a smaller direct effect estimate ( 0.5) compared with the estimate for males in Salkever (1.24). First, of the 19 reported direct estimates in Barth, 5 included blocking covariates (work experience and/or occupation), 5 used hourly earnings as a dependent variable, and one used weekly earnings. Inclusion of blocking variables and using hourly or weekly earnings variables (which assume zero IQ effects on annual hours or weeks of work) will tend to attenuate estimated IQ impacts. Second, the vintages of the earnings data in the 19 studies surveyed by Barth were relatively old, with 10 studies using earnings data from the 1950s and 1960s, while the remaining 9 studies used data from the 1970s. This tends to produce lower impact estimates if IQ effects on earnings and/or schooling effects on earnings, have been increasing over time. Third, sample selection factors in a number of the studies reviewed by Barth could have attenuated variation in IQ and reduced estimated IQ effects (Barth et al., 1984). Use of test results from high school in most of the studies excluded or substantially under-represented high-school drop-outs, and restriction of samples to veterans or persons in the armed forces screened out persons not qualified to serve. Finally, the estimate from Grilliches (1977), which is given particular weight in Schwartz (1994), used 1959 median earnings in future occupations expected (preferred) by respondents, as the dependent variable; Grilliches noted that using this dependent variable had several disadvantages, including: (1) it involved respondents' expectations (preferences) for future occupations rather than actual realized earnings, and (2) it ignored expected returns to ability within occupations because it used median earnings. A broader comparison of the Schwartz estimates shows a total earnings effect, excluding participation, of  1.286%. This is clearly below the corresponding estimates of this effect for males by Salkever and by Johnson and Neal, even though (as noted above) Schwartz' estimate of the link between exposure and schooling includes behavioral as well as cognitive impacts of exposure. In contrast, Schwartz' estimate of the participation effect ( 0.473%) is very close to the overall estimate from Salkever (  0.498%). This is consistent with the finding from Salkever that IQ impacts on educational attainment are similar for both genders.

4. Summary and further consideration of variations in IQ impact estimates on earnings Our review of the only 4 recent studies that developed estimates of the impact of a 1-point IQ decrement on annual earnings of workers shows a substantial range among the estimates. The two studies based on NLSY79 national survey data using earnings figures from the early 1990s (Salkever, 1995; Johnson and Neal, 1998) show impact estimates of  1.731% and

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2.271% for all males; the corresponding impact estimates for females are  2.415% and  3.389%. In view of the similarities in databases and methods between these two studies, it is surprising that the Johnson and Neal estimates are 31% and 40% higher for males and females respectively. One factor leading to this result is that Johnson and Neal used a 3-year period rather than a single year to compute average annual earnings. Persons with zero earnings in only one or two years were included in the analysis of average annual earnings for workers and this reduced the number of persons classified as non-workers, A consequence of this use of 3-year averages was to shift some of the overall IQ impact on participation to the overall IQ impact on annual earnings of workers (from column (c) to column (b) in Table 1). Thus, compared with the Salkever estimates, our approximate estimates of participation effects for the Johnson and Neal population (Table 1, note b) are only about 35% as large for men and 45% as large for women. Adding these to the estimates in column (b) of Table 1 would increase the Johnson and Neal impacts to  2.348% and 3.756% for males and females respectively, total impact estimates that are respectively 16% and 22% above the total IQ impact estimates from Salkever. Another possible explanation for the lower impact estimates in Salkever (1995) is that the regressions in Salkever included a detailed set of parental characteristics covariates. This accords with comparisons of results from Zax and Rees (Table 1, row 11 vs. row 13) that show a reduction in IQ impacts when these covariates are added to a reduced form model. Similarly, Grosse (2007) argues that “(t)he inclusion of family characteristics…is likely to understate the effect of cognitive ability because of shared genetic determinants of ability between parents and biological children.8 The two remaining works in this group of four studies, Schwartz (1994) and Zax and Rees (2002) reported IQ impacts on earnings for all workers that were substantially lower. We have already noted several reasons for this difference in results, including (1) the primary reliance on data from males by Schwartz and the exclusion of data on females by Zax and Rees; (2) the exclusion of persons who did not graduate from high school and the under-representation of blacks in the survey data used by Zax and Rees; and (3) the fact that the earnings data used in both studies were drawn from the early 1970s and before, rather than the early 1990s (as in the case of Salkever and of Johnson and Neal). The connection between the vintage of the earnings data and the estimated IQ impacts warrants further comment. As early as 1984, Barth et al. noted the possibility that “… the relationship between schooling, ability and earnings may have changed” since the time periods (the 1930s through the 1960s) when the sample populations in their literature review entered school. In their recent meta-analysis, Bowles et al. (2001) cited a variety of studies reporting upward trends for a variety of periods over the years 1964–1991 in the relationship of cognitive skills to earnings or wages. The strongest evidence of an increasing IQ impact appears to be due either to an increasing impact of schooling or to an increasing impact over time of the interaction between schooling and measures of cognitive skills. Salkever (1995) and Zax and Rees (2002) also cited several of these same studies, with Zax and Rees noting them as a possible partial explanation for the increase in their IQ impact estimates from 1974 (when respondents were age 35) to 1992 (when respondents were age 53). 8 He cites as support for this view a number of studies that reported much weaker associations between parental characteristics and educational attainments of adopted offspring compared with analogous associations for biological children.

Bowles et al. do report variability across the cited studies in terms of attributing the trend of increasing IQ impact entirely to increased returns to schooling, to increased returns to cognitive skills per se, or to an interaction between the two. For the present analysis, however, any of these results combined with the strong positive impact of IQ on schooling implies a strong upward trend in total IQ impacts in either reduced form or recursive models. Accordingly, this evidence suggests that the Zax and Rees (2002) and Schwartz (1994) estimates based on earlier data will understate the IQ impact on earnings in more recent years.

5. Estimates of IQ impacts on hourly wages We expect that estimated total IQ impacts on hourly wages should be substantially less than analogous IQ total impacts on earnings, because they exclude both (direct and indirect) IQ impacts on annual hours of work and (direct and indirect) IQ impacts on work participation rates. Nevertheless, we briefly review results from several hourly wage impact studies both to gauge the magnitude of the difference between hourly wage impacts and total annual earnings impacts, and because the wage impact results have been prominent in recent arguments in favor of the overstatement hypothesis. Results from 3 recent studies noted in the over-statement literature are shown in Table 2. All 3 studies use the reduced form approach to modeling the IQ hourly wage impact.9 One study also reports direct IQ impact estimates on hourly wages from a regression in which education covariates are also included. Rows 1 and 2 of Table 2 show Johnson and Neal's (1998) estimates of 1.167% for men and 1.66% for women. Since their corresponding impact estimates on earnings in Table 1, rows 4 and 5, were  2.271% for men and  3.389% for women, their results in Table 2 imply that total IQ impacts on hourly wages are only about one-half as large as total IQ impacts on annual earnings of workers, implying that IQ impacts on hours of work are similar in magnitude to the reported wage impacts. Furthermore, the reported wage impacts will be even less than one-half of total IQ annual earnings impacts that include participation effects. Rows 3–6 of Table 2 show the Johnson and Neal estimates for black and white respondents, by gender. While the patterns of racial differences (impacts for black men greater than for white men, impacts for black women slightly smaller than impacts for white women) are similar to those reported in Table 1, the relative magnitudes of these differences in Table 1 are larger. This suggests that racial differences in earnings impacts, by gender, are mainly due to differences in IQ impacts on hours worked rather than on hourly wages. Results for Neal and Johnson (1996) are included in Table 2 since these results are cited prominently in the papers arguing for the overstatement hypothesis (Grosse, 2007; Robinson, 2007, 2013). For both men and women, results are very close to those reported by Johnson and Neal; this is expected since both studies used the same IQ measures, data sources, and regression specifications, and very similar survey data. Results on hourly wage impacts for males from Heckman et al. (2006) reported in Table 2 are similar to those from Johnson and Neal, and from Neal and Johnson. Here again the similarity is not surprising given the use of the same data source, similar study samples, similar years of earnings data, and similar measures of cognitive skills. Several other aspects of the Heckman et al. results are of particular interest. One is that Heckman et al. included both measures of cognitive skills and non-cognitive skills as regressors 9 This is analogous to the model in Fig. 2 except that the outcome is average hourly earnings rather than annual earnings.

D.S. Salkever / Environmental Research 131 (2014) 219–230

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Table 2 Hourly wage impact estimates from the recent literature.

1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17

Study

Pop. group

Johnson and Neal (1998)

Men age 25–28 Women age 25–28 White men age 25–28 Black men age 25–28 White women age 25–28 Black women age 25–28 Men age 25–28 Women age 25–28 White men Age 25–28 Black men age 25–28 White women age 25–28 Black women age 25–28 Men age 30 Women age 30 Men age 30 Men age 30 Men age 30

Neal and Johnson (1996)

Heckman et al., 2006 (Table 1) Heckman et al., 2006 (Table 5, measured scores) Heckman et al., 2006 (Table 5, corrected tests, simulated wages) Heckman et al., 2006 (Table 5, latent factors, simulated wages)

in their models. A second is that Heckman et al. reported results (in rows 16 and 17) using estimation strategies designed to cope with problems of measurement error and endogeneity in key variables in their analyses. Use of these estimation strategies yielded moderate reductions (19.3–24.3%) in the directþindirect IQ wage impact estimates.

6. Comments on additional evidence of IQ impacts in a recent meta-analysis In the most widely-cited brief for the overstatement hypothesis, Grosse (2007) reports that “(a) meta-analysis of 24 studies by Bowles et al. (2001) found that the mean estimate of the direct effect of cognitive ability on earnings is…0.5%”. Comparing this estimate with the results in Table 1, we see this estimate equals the estimate in Schwartz, but is substantially below the corresponding estimates in Salkever ( 1.320% for both genders combined). A careful review of the appendix to the Bowles et al. study (available from the authors) reveals, however, a number of reasons why the range of IQ impact estimates that they report is so low. First, in 12 of the 24 studies reviewed, the dependent variable is not annual earnings, but rather hourly wage (8 studies), weekly wage (2 studies), monthly wage (1 study), or both hourly and weekly wages (1 study). As noted in Section 5, studies of IQ impacts on hourly wages take no account of IQ impacts on annual hours of work, and consequently yield lower impact estimates. Analogous comments apply to studies that estimated impacts on average weekly wage or monthly wage. Second, of the 85 regression models for which results were reviewed by Bowles et al., more than two-thirds (58) provided estimates for males only. Given the persistent empirical finding that IQ impacts are larger for females, one would expect the range of results reported in this meta-analysis to be skewed toward lower estimated impacts. Third, the direct impact estimates previously reported in Tables 1 and 2 were derived from regressions with education covariates included, but other “intermediate outcome” measures that are themselves affected by IQ were excluded (since they would block some of the impact of IQ and result in attenuated impact estimates). In the literature reviewed by Bowles et al., however, most of the studies included additional covariates (besides schooling) that are themselves the consequences of differences in IQ. In 14 of these 24 studies, years of work experience and/or

Direct estimate

Total reduced-form estimate

 0.807  1.127  0.713  0.440  0.647

 1.167  1.660  1.173  1.287  1.747  1.680  1.152  1.514  1.157  1.379  1.400  1.358  1.267  1.673  1.180  0.953  0.893

job tenure were used as explanatory variables. In one additional study, weeks worked and an indicator of full-time vs. part-time status were included as covariates. Since results reviewed above suggest that IQ affects probability of working as well as hours worked, measures such as work experience, job tenure and hours of work presumably increase as IQ increases. The result in these studies is obviously to attenuate the measured impact of IQ on earnings. A variety of other special features of particular studies in the Bowles et al. review suggest that these studies tended to underrepresent those population groups that appear to experience the largest IQ impacts on earnings. Examples are specific studies reviewed by Bowles et al. (a) that restricted analysis to a sample of 2400 Wisconsin students enrolled in college in 1958, (b) that restricted analysis to above-average-IQ veterans, (c) that restricted analysis to persons who graduated from high schools in Wisconsin in 1957, (d) that restricted analysis to Minnesota high school graduates of 1936, or (e) that only analyzed data on veterans. It is probable that these studies under-represented precisely those groups that were found in Salkever and/or in Johnson and Neal to have the largest IQ impacts: persons with lower IQ levels, females, and Blacks. Thus, it seems reasonable to expect that the studies reviewed by Bowles et al. (2001) would report relatively lower levels of IQ impacts on earnings that should not be generalized to the entire population. Finally, in a number of the studies reviewed by Bowles et al., earnings and wage data used for the analyses were drawn from the late 1950s, the 1960s and the early 1970s. Of the 85 sets of regression results reviewed, 25 did not use any data newer than 1979 and 8 more were based primarily on pre-1980 data. We have previously noted the possibility that increases in IQ impacts over time may explain a tendency to find weaker IQ effects with earlier data. In summary, the methods used in the studies reviewed by Bowles et al. would be expected to provide IQ effect estimates that substantially understated nationally-representative and recent estimates of the direct IQ effects on earnings, holding constant the level of schooling.10

10 Note that Grosse (2007) also cited one other study (Gayer and Hahn), that briefly cites Neal and Johnson (1996) and Zax and Rees (2002), as support for his case for the overstatement hypothesis. He indicates that Gayer and Hahn “argued that the economic value of IQ has been overstated in regulatory impact analyses” and “reported that estimates in the relevant labor economics literature range 0– 1.1% reduction in earnings per IQ point.” Given that Gayer and Hahn's conclusions appear to be based on a very small sampling of the “relevant labor economics literature” that appears in their reference list, and that they seem unaware of the issues mentioned in Sections 4–6 of the current paper (e.g., the difference between

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7. Reviewing the case for the overstatement hypothesis Having reviewed in some detail the relevant features and results of the only four studies that develop total IQ impact estimates on earnings (either with or without participation effects), and the additional wage impact and meta analysis studies cited by the proponents of the over-statement hypothesis, we can finally turn specifically to a discussion of the case for that hypothesis. We consider two sets of concerns raised by the proponents: (1) measurement and statistical issues and (2) comparability of earnings impact results with recent findings in the labor economics literature.

7.1. Measurement and statistical Issues The principal measurement issue noted in the arguments for over-statement, and in a number of other studies reviewed above, concerns use of results from tests of cognitive skills (such as the AFQT) obtained from teen-agers or young adults as measures of “cognitive ability”. As a practical necessity, virtually all empirical studies relating IQ to adult earnings (or wages, hours, or work participation), including those cited earlier in this paper, have relied on IQ measurements from cognitive skills tests administered to individuals during their teen-age or early adult years. (Data from tests administered at much earlier ages to large survey samples of children are almost never used in analyses of adult earnings because longitudinal surveys with such tests very rarely extend into adulthood.) Evidence that cognitive test scores taken by teen-agers or young adults are influenced by their prior learning in school raises concerns that these tests are measuring learned skills a much as innate ability. The relevant question in the current context, however, is not whether tests such as the AFQT are “pure” IQ tests of innate ability, but rather the extent to which this problem with the available test data translates into either positive or negative biases on estimates of how IQ decrements due to lead exposure impact individuals' schooling and earning. Arguing for the overstatement hypothesis, Robinson (2013) suggested that using test data from later ages biases estimates of IQ impacts upward. She wrote that “Neal and Johnson … restrict their NLSY sample to those who were age 18 or younger when they took the AFQT, so that their estimates of the relationship between ability and earnings are less inflated by the effects of further education and experience than the estimates used by Salkever.” In fact, as noted above, Neal and Johnson used virtually the same data, the same AFQT measure, and the same regression model specifications as Johnson and Neal, except that the latter used both annual earnings and hourly wages as dependent variables. The fact that Johnson and Neal found larger IQ impacts than Salkever contradicts Robinson's suggestion, implying that Salkever's inclusion of data on persons older than 18 when they took the AFQT may actually have reduced the estimate of IQ impact rather than it being “inflated”.11 (footnote continued) hourly wage impacts and annual earnings impacts), it is not clear that invoking Gayer and Hahn adds much credence to the case for the overstatement hypothesis. 11 The foregoing comments also applied to the inaccuracy of a related contention by Grosse (2007); he erroneously suggested that one reason for the over-estimation of IQ impacts by Salkever relative to Neal and Johnson was the fact that the latter standardized their AFQT variable for differences in age while Salkever did not. Moreover, he states that Salkever in fact provided estimates of “direct effects on hourly wages”, which was also incorrect, since Salkever did not analyze IQ impacts on hourly wages at all.

The best resolution to this issue would, of course, be to analyze data that used the same IQ measures as the epidemiologic data (e.g., WISC scores for young children) in studies of their adult earnings from long-term follow-up surveys. Assuming that substantial bodies of longitudinal survey data with early childhood IQ scores and adult earnings figures are not likely to emerge in the near future, efforts to asses the bias from use of the currently available data (based on teen-age and/or young adult test scores) seem to be called for. Two other statistical concerns offered by Grosse (2007) and Robinson (2013) as possible causes of over-estimation are: (1) the omission of any variable measuring behavioral (“non-cognitive”) skills as a covariate in the regression models, and (2) measurement error and endogeneity concerns relating to the IQ variable and the education variable. The possibility of an upward bias in IQ impacts due to omission of behavioral measures was suggested by Grosse (2007) in his observation that “… the effect of behavioral factors may be captured at least in part by estimates of the returns to cognitive ability.” One study of IQ impacts on hourly wages, cited by the overestimation proponents, addresses several of these concerns. The results from Heckman et al. (2006) in rows 15–17 of Table 2, allow comparison of estimated direct and total IQ impacts on hourly wages for males using observed data on earnings, cognitive test scores (based on the AFQT) and non-cognitive test scores (row 15), vs. simulated earnings as well as simulated, standardized cognitive and non-cognitive test scores (row 16), vs. simulated earnings and estimates of latent cognitive and non-cognitive skill levels (row 17). Comparing the reduced-form IQ impacts on male hourly wages, using observed data, between Heckman et al. (row 15), Johnson and Neal (row 1), and Neal and Johnson (row 7), we see that all 3 estimates are very close, suggesting that addition of a covariate measuring non-cognitive skills has little effect on the observed coefficient for cognitive skills. Comparing results in rows 15 vs. 16 vs. 17, we see a small diminution of about 19% (from  1.18% to  0.953%) in the magnitude of the estimated IQ impact when simulated wages and test scores replace observed data, and a smaller additional diminution of about 5% (from  0.953% to  0.893%) when latent skill variables replace test scores. This evidence provides at least a bit of support for the argument that using measured test scores leads to a slight over-estimate in the IQ impact on hourly wages. Of course, this result may not generalize either to the IQ impact on annual earnings of workers (i.e., including an hours effect), or to the IQ impact on annual earnings of all persons (i.e., including both hours and participation effects). Moreover, the remaining inaccuracies in the simulated wage and test score measures (due to attenuated variance of the “true” measures) may themselves introduce a downward measurement error bias into the magnitudes of the estimated IQ impacts. In summary, the concerns about measurement and statistical problems causing over-estimation bias of IQ impacts are logically valid, but there is essentially no evidence at this point to show either (1) that this bias is important or (2) that whatever bias exists points to over-estimates rather than under-estimates. 7.2. Comparability of earnings impact results with other findings in the labor economics literature A second major theme in the arguments for the overstatement hypothesis is the contention that the results in Salkever (1995), and even the slightly lower estimates in Schwartz (1994), are not consistent with the findings from comparable recent studies in the recent labor economics literature. In particular, following her discussions of the Zax and Rees (2002) study, and the wage impact

D.S. Salkever / Environmental Research 131 (2014) 219–230

estimates from Neal and Johnson (1996) and Heckman et al. (2006), Robinson (2013) asserts that … newer research suggests that both the Salkever estimate of a 2.4% change in earnings per one-point change in IQ and the older Schwartz estimate of 1.76% are overstated. Grosse (2007) also goes into great detail in comparing results from these studies with the Salkever (1995) results to document that the latter are clearly above the norm implied by the wage impact estimates. The major problem with this argument is the non-equivalence of earnings impacts vs. wage impacts that has been stressed by both Barth et al. (1984) and Johnson and Neal (1998). Barth et al. offer the following observations: “A … factor which should be considered is that some studies use hourly wage as the dependent variable. Theoretically … variables that determine hourly wage may also influence … hours worked. The question arises whether it is appropriate simply to multiply the hourly wage results by a constant number of hours of work per year in order to compare them with other estimates based on annual earnings…Hence, the hourly wage equation estimates are assumed to translate simply into annual earnings estimates, with no account made for any endogenous hours-worked response. Johnson and Neal introduce their analysis with a justification for their focus on earnings rather than wages: “Since earnings are the product of hourly wages … and hours of paid work, earnings differences can arise from wage differences, differences in employment, or both. … Differences in earnings may provide a different and more complete picture than do wage differences of the economic consequences of… differences in pre-market skills. If, as an empirical matter, IQ wage impact estimates and IQ earnings impact estimates were almost equal, because hours of work did not vary systematically with IQ, it would not be problematic to treat wage impact estimates from one study and earnings impact estimates from a different study as equivalent results. Unfortunately for the proponents of the overstatement hypothesis, data from the study by Johnson and Neal show that this is clearly not the case. As shown in Tables 1 and 2, the Johnson and Neal estimates of earnings impacts are roughly twice as large as their wage impact estimates, suggesting the IQ impacts on hours of work are roughly the same size as IQ impacts on wages. They also present descriptive data documenting a clear positive gradient for males between education and annual hours of work; compared with males who did not graduate high school, mean annual hours are 12.6% higher for those who graduated from high school (but not college) and 17.7% higher for college graduates. A similar gradient was found for weeks worked (analogous figures were þ11.8% and þ15.1%). Since schooling varies positively with IQ, the IQ gradients for annual hours and weeks worked should also be positive. We tested this hypothesis in the case of weeks worked for both males and females using an approximation to the methods of Johnson and Neal; results (available in the online supplement) showed very significant positive impacts of IQ for both males (0.388%) and females (1.255%). In view of this evidence that positive IQ impacts on hours and weeks worked are non-negligible, we conclude that the observed differences between the wage impact estimates cited by Grosse (2007) and Robinson (2007, 2013) and the somewhat higher earnings impact estimates reported by Salkever (1995) can not be interpreted as supporting the overstatement hypothesis. Other problems with the Grosse and Robinson assertions of non-comparability, between the Salkever results and the results

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from Zax and Rees (2002) have already been noted above, including exclusion of non-high-school graduates by Zax and Rees, the atypical racial make-up of the Zax and Rees study sample, and the exclusion of females.

8. Do the “overestimates” of IQ impacts underestimate impacts at older ages? As indicated by the Zax and Rees' finding of greater IQ impacts at age 53 than at age 35, there is reason to suspect that IQ impacts on earnings depend upon the age when the earnings measure is observed. The general expectation, based in part on the observed rise in skill differentials in earnings with age, is that IQ impacts on earnings of young adults (e.g., age 30 or less) will be smaller than impacts on older adults approaching their peak earnings years (Barth et al., 1984; Grosse, 2007). Since almost all of the evidence reviewed here, as well as in Grosse (2007), pertains to IQ impacts on wages or earnings for relatively young adults (excepting the age 53 results from Zax and Rees), it is reasonable to expect that applying the impact measures reviewed here to estimate earnings losses for adults at older ages will tend to understate the actual IQ impacts. (Of course, discounting and a possible reversal of the age-IQ impact relationship at much older ages will presumably diminish this understatement somewhat.)

9. Summary and concluding comments In summary, since 2002 a number of recent review articles and reports dealing with projected earnings losses due to IQ decrements caused by lead exposure (Grosse et al., 2002; Grosse, 2007; Robinson, 2007, 2013) have asserted that the percentage earnings loss estimates per IQ point have been overstated by Schwartz (1994) and particularly by Salkever (1995). The principal argument offered in support of this hypothesis is that results from a number of other studies from the labor economics literature, and particularly more recent labor economics studies, are not comparable with the Salkever results and consistently indicate lower IQ impacts on earnings. The current paper has reviewed in detail these other labor economics studies, as well as the review articles and reports, and finds that the evidence they present offers little support for the overstatement hypothesis mainly due to the following limitations: 1. The great bulk of the evidence from these studies relates to impacts of IQ on wage rates (usually hourly) for workers rather than annual earnings, thereby omitting about half of the annual earnings impacts for workers which take the form of IQ impacts on annual hours of work. 2. Much of the evidence from these studies is based on pre-1980 data on wages and earnings, thereby omitting the influence of recent upward trends in skill differentials in earnings and increasing returns to education. 3. None of these studies offer any evidence about IQ impacts on work participation rates. 4. The preponderance of the evidence in these studies is based on data for men, thereby under-weighting the greater IQ impacts on women's earnings consistently reported in those few studies that do present gender comparisons. 5. Many of the studies rely on selected samples such as highschool graduates, veterans, smaller geographic regions (e.g., Wisconsin) or men whose high school records provide data on IQ tests of cognitive skills taken during high school. This underrepresents some groups, such as black males and persons with lower cognitive skill levels, for whom available evidence suggests that IQ impacts on earnings are relatively larger.

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(In contrast, the relatively few studies based on the national NLSY79 data do not suffer from this deficiency.) 6. None of the review articles that make the case for the overstatement hypothesis (Grosse et al., 2002; Grosse, 2007; Robinson, 2007, 2013) take any account of the recent study (Johnson and Neal, 1998), based on national NLSY79 data, that undermines their overstatement hypothesis and in fact suggests that the estimates from Salkever (1995) (as well as from Schwartz, 1994) are probably roughly 20% too low, rather than too high.

The overstatement hypothesis proponents have raised some interesting issues, some of which could actually argue for even larger rather than smaller IQ impact estimates on earnings of leadexposed children (e.g., the bias from omitting behavioral variables, the inclusion of detailed family background covariates). The empirical evidence that they presented in favor of overstatement, however, is clearly inadequate to support their claims. Perhaps the most important and surprising conceptual problem with their arguments is the failure to clearly and consistently differentiate between IQ impacts on wage rates and IQ impacts on annual earnings. Of course, this confusion is also a problem that has occurred in the general economics literature on the importance of IQ and cognitive skills (e.g., Zax and Rees, 2002; Bowles et al., 2001; Gayer and Hahn, 2006). As a profession, we need to be more precise in our usage of these terms. Given the importance of analyses based on the NLSY79 data, it is also surprising that the overstatement proponents neglected the work of Johnson and Neal (1998) which is one of the few studies that is most directly relevant for assessing impacts on earnings (rather than just wages). This neglect also may have diminished

the attention paid by Grosse and Robinson to the importance of heterogeneity of IQ effects and the attendant danger of overgeneralizing from bodies of evidence largely based on the experience of non-minority males. The omission of the Johnson and Neal results, combined with other conceptual and minor factual errors, points to a need for a much more thorough, rigorous and balanced examination of the relevant literature, rather than a detailed argument in support of a particular hypothesis. Hopefully, the current paper will stimulate interest in pursuing such an examination in the near future.

Conflicts of interest None.

Acknowledgments Thanks are due to Melissa Groves and to Lisa Robinson for providing relevant pieces of literature that are not routinely available, and to the anonymous referees for helpful suggestions. All errors of omission or commission are the sole responsibility of the author.

Appendix A See Table A1.

Table A1 Relevant Empirical Studies of IQ Effect on Earnings or Wages. Empirical Studies Reporting Estimates of IQ Effects on Annual Earnings Reference/ Data Source/ IQ Measure/ Dep. Vble. Definition and Year A. Schwartz(CDC, 1991; Schwartz, 1994)/Synthesis of results from various prior studies

Population Studied

Regression Model Type/ IQ Effects Estimated Other Study Methods

Synthesis of studies from Non-statistical synthesis various populations. Key of results in the literature. estimates based almost entirely on males. See text for details

Direct effect for workers Earnings effect for workers ——————————————— Work participation ——————————————— Total Effect Direct þ indirect effects All NLSY79 respondents 3 Regression models: B. Salkever(1995)/ (via schooling yrs) on schooling yrs¼ f(IQ, NLSY79/AFQT/ covariates); Participation (a) participation and Annual Earnings (b) annual earnings (0-1) ¼f(IQ,schoolings 1990 yrs, covariates); earnings ¼ f(IQ, schooling yrs, covariates) NLSY79 national random Reduced form regression Total earnings effects C. Johnson and Neal sample & Hispanic and (1998)/ NLSY79/ black supplement Age-Adjusted samples; persons born AFQT/Ave. Annual after 1960 w. ave. Earnings 1990-92 earnings 40 in at least 1 yr. (1990-1992) Reduced form regression Total earnings effects Male high-school D. Zax and Rees (Model 1) (2002)/ Wisconsin graduates in Wisconsin Longitudinal Study/ who were seniors in 1957 Henmon-Nelson IQ test (11th grade)/ Annual Earnings 1974 & 1992

Covariates presumably not impacted by IQ

Omitted IQ Effects

NA

None

"Blocking" covariates (i.e.,included covariates presumably impacted by IQ) None

Age in years, black and Hispanic 0-1 indicators, parents' education and income, region (urban vs. rural non-farm, vs. farm; south vs. non-south) 0-1 indicators

None

None

Age in years, black and Hispanic 0-1 indicators

Participation

None

None

Participation

Education (partial -nonhigh school graduates excluded from study) .

D.S. Salkever / Environmental Research 131 (2014) 219–230

229

Table A1 (continued ) Empirical Studies Reporting Estimates of IQ Effects on Annual Earnings E. Zax and Rees (2002)/ Wisconsin Longitudinal Study/ Henmon-Nelson IQ test (11th grade)/ Annual Earnings 1974 F. Zax and Rees (2002)/ Wisconsin Longitudinal Study/ Henmon-Nelson IQ test (11th grade)/ Annual Earnings 1974 & 1992

H. Heckman, Stixrud, and Urzua(2006)/ NLSY79/ ASVABa/ Ave. Hourly Wage at age 30 I. Johnson and Neal (1998)/ NLSY79/ Age-Adjusted AFQT/Ave. Hourly Wages 1990-93

Same as Row D.

Parents' education and occupation, household income, family structure

Reduced form regression Total earnings effects Male high-school (Model 3) graduates in Wisconsin who were seniors in 1957

Same as Row 6 plus town Participation pop., school class size, 0-1 indicators for public vs. private vs. catholic schools, peer characteristics, peers' household characteristics

Same as Row D plus: 0-1 indicators for plans to go to college, and parents encouraged or discouraged college.

Covariates presumably not impacted by IQ

Omitted IQ Effects

Age in years, black and Hispanic 0-1 indicators

Participation Hours

"Blocking" covariates (i.e., included covariates presumably impacted by IQ) None

Noncognitive skills, local unemployment rate, 0-1 indicators for race, year, region of residence.

Participation Hours

None

Age in years, black and Hispanic 0-1 indicators

Participation Hours

None

Empirical Studies Reporting Estimates of IQ Effects on Hourly Wages Reference/ Data Population Studied Regression Model Type/ IQ Effects Estimated Source/ IQ Other Study Methods Measure/ Dep. Vble. Definition and Year G. Neal and Johnson (1996)/NLSY79/ Age-Adjusted AFQT/Ave. Hourly Wages 1990-91

Participation

Reduced form regression Total earnings effects Male high-school (Model 2) graduates in Wisconsin who were seniors in 1957

NLSY79 national random sample and Hispanic and black supplemental samples, only persons born after 1960 with ave. wage40 in 1990 and/or 1991 NLSY79 national random sample with ave. wage40 at age 30

Reduced form regression Total wage effect

Reduced form regressions; also regressions with education covariates.

Total wage effect; direct effect controlling for 0-1 schooling indicators.

NLSY79 national random Reduced form regression Total wage effects sample & Hispanic and black supplement samples; persons born after 1960 w. ave. wage40 in at least 1 yr. (1990-1993)

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