Long-term Unemployment and Intergenerational Earnings Mobility Scott Drewianka and Murat Mercan∗ University of Wisconsin-Milwaukee
Abstract We investigate the influence of long-term unemployment on intergenerational earnings mobility among men. We defend our definition of the long-term unemployed as those who have zero annual earnings despite labor force participation and emphasize that previous studies have routinely excluded these workers. When this relatively small group is included, estimates of intergenerational mobility drop substantially. Consistent with a simple model, the drop is more pronounced when earnings are studied over a longer period. Moreover, while both earnings when working and spells of long-term unemployment are correlated across generations, the large drop we identify is mainly driven by the latter. Keywords: Intergenerational earnings mobility, long-term unemployment, poverty JEL Codes: D31, I32, J13
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Introduction Economists and other social scientists have long been concerned about the correlation between the in-
comes of parents and their children. This concern is largely motivated in terms of fairness and “equality of opportunity.” Sometimes it is also taken as an indication of the efficiency of the labor market–if abilities are not too strongly hereditary, a high degree of intergenerational mobility might be interpreted as a sign ∗ Mercan is the corresponding author. Address (for both): Dept. of Economics, Bolton Hall 868, 3210 N. Maryland Ave., Milwaukee, WI 53211. E-mail:
[email protected],
[email protected]. Phone: (414)229-2730; fax: (414)229-3860. We are grateful for comments by Scott Adams, Keith Bender, Tristan Coughlin, John Heywood, and participants of seminars at Lake Forest College, UWM, and the Midwest Economics Association annual meetings. All remaining flaws are our responsibility.
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that there are few barriers to efficient employment matches. Over the last few decades, several empirical studies have attempted to quantify that intergenerational churning using a summary statistic called “intergenerational earnings (or income) elasticity.” Most recent estimates of that parameter in the U.S. fall within a relatively narrow range and imply a moderate pace of convergence across generations. Thus far, most work has focused on techniques to measure this elasticity more accurately. In many ways, this paper builds upon that work–the main analysis involves running the literature’s canonical regression and draws upon many of the associated empirical insights. However, it approaches intergenerational mobility from a modestly different, ultimately simpler perspective.1 It is less concerned than previous studies with measuring the intergenerational elasticity precisely, although our baseline results will be consistent with earlier estimates. Instead, we compare estimates of intergenerational elasticity from two different samples, one that uses classical sample selection rules and another that adds a group that is suspected of having a substantial impact on mobility. Our results confirm that suspicion: although the second sample contains only a few more observations than the first, it yields greatly reduced estimates of intergenerational mobility. Along with a body of supplementary evidence, this leads us to conclude that scholars and policy makers interested in promoting intergenerational mobility may wish to devote greater attention to these workers. The particular group that we emphasize is the long-term unemployed, defined here as prime-age men who report that they earned zero dollars in the previous year, that they were unemployed, and that they were not students or retirees. Such workers seem especially relevant for studies of poverty because they have suffered unusually large transitory earnings shocks that markedly affect their realized lifetime earnings, and that could plausibly have negative causal effects on their children’s future outcomes. Perhaps ironically, such men have typically been intentionally excluded from studies of intergenerational mobility. A few papers have considered the impact of including all men with no earnings, but they primarily emphasize voluntary labor force participation decisions and thus do not distinguish between unemployed workers and non-participants. Our suspicion is that the long-term unemployed have been ignored in part because researchers suspect that they actually withdrew from the labor force. Yet not only do these men explicitly report long spells of unemployment, but they also report positive earnings in the years before and 1 A similar strategy has recently been used in part of Dustmann’s (2008) study of difference in intergenerational mobility between native and immigrant families in Germany.
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after those spells, are more likely to have zero annual earnings during economic recessions, and when employed they tend to work in notably volatile industries and occupations, especially construction. Moreover, we find that these men have relatively low earnings even when they are employed, so the standard methodology of excluding this group would tend to make the sample less representative in a potentially important way. Even more significantly, their sons are unusually likely to have low average earnings and/or to suffer their own year with zero earnings. Together with the intergenerational earnings regressions we present, this evidence suggests that including these families in the analysis affects estimates of earnings persistence not only because the sample is more representative, but also because this group has greater earnings persistence than other groups. Notably, this last point is consistent with a subtle prediction from Becker and Tomes’ (1986, p. S34) theoretical model: that “earnings regress more rapidly to the mean in richer than in poorer families,” perhaps due to the latter group’s greater exposure to credit constraints. Having said that, it should be understood from the outset that we do not definitively identify the mechanisms underlying this group’s low mobility. Three possibilities were suggested above–hereditary or learned skills and attitudes, negative child outcomes caused by the parent’s lack of earnings in a particular year, and credit constraints that might apply to poorer families generally–and it is not difficult to think of alternate explanations involving, e.g., geographic labor markets, discrimination, or risk-taking.2 We do not believe it is possible to distinguish conclusively between these hypotheses using the data and methods employed here, and indeed this is a long-standing critique of this literature (Goldberger, 1989). Even so, an exercise presented near the end of the paper offers some insight. Recognizing that a worker’s average lifetime earnings reflects both his earnings when employed and his years of long-term unemployment, we re-estimate intergenerational mobility using workers’ earnings only in years when they have positive earnings. The modified estimate is unremarkable, similar to consensus estimates in previous work. It is thus only when we incorporate workers’ years with zero earnings that we find the sharp decrease in intergenerational mobility. Further investigation reveals that the result is driven entirely by the sons; estimates of intergenerational mobility are actually not very sensitive to the treatment of fathers’ years with zero earnings. These findings cast doubt on several mechanisms mentioned above, at least for this group. Yet they raise an 2 Many
of these hypotheses are discussed more extensively by Bowles and Gintis (2002) and Grawe and Mulligan (2002).
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interesting new question: why are children from poor families prone to work in occupations and industries where there is a relatively high risk of long-term unemployment? While we cannot answer that question, we hope our findings will motivate future studies that shed more light on the challenges facing these families. The exposition begins with a brief review of the empirical literature on intergenerational earnings mobility. Section 3 then discusses the statistical advantages and disadvantages of including the long-term unemployed in analyses of intergenerational mobility. Section 4 introduces our data, and Section 5 investigates the characteristics of the long-term unemployed. Among other things, that section argues that we have accurately identified workers who have suffered long-term unemployment, shows that they have low incomes in general, and presents initial evidence on the subsequent labor market experiences of their children. The analysis of intergenerational mobility is conducted in Section 6, and Section 6.2 investigates the mechanisms driving the results. Section 7 concludes with a brief discussion of the implications for public policy and future studies.
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Previous work Studies of intergenerational earnings mobility are typically limited by the availability of data. In principle,
the goal is to understand how the distribution of potential earnings outcomes for an individual varies with the incomes earned by his or her parents. Unfortunately, only a few data sets even allow researchers to link children to their parents, and the sample is often not large. Consequently, the inquiry is almost always reduced to an attempt to measure the correlation between the earnings of parents and children (as opposed to, e.g., a transition matrix), and in light of men’s greater labor force attachment, the question is usually posed in terms of fathers and sons. Ideally one might base the analysis on the present value of the individuals’ lifetime earnings, but virtually all studies instead simply compute an average of workers’ annual earnings over some subset of their careers and make some adjustments for inflation and the workers’ ages. Formally, if Yt is a worker’s earnings in year t, the desired measure of his earnings over a T year career ³P ´ T ∗ is Y ≡ t=1 Yt /T , and researchers seek to measure β in the regression Y s = α + β ∗ Y f + e,
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(1)
where f and s index fathers and their sons. β ∗ represents the persistence of earnings across generations. Although β ∗ could take on any value, we ordinarily expect that β ∗ > 0 (so parents with above average incomes tend to have children who also earn incomes above average), but also that β ∗ < 1 (regression to the mean). Intergenerational earnings mobility can thus be thought of as 1 − β ∗ . It is rarely possible to estimate (1) as shown above because few data sets track workers over their full careers. Instead, researchers usually must average incomes over a smaller number of years n < T , defining Zn ≡ (
Pn
t=1
Yt ) /n. A related complication is that workers are observed at different ages A, and the age-
earnings profile implies that E[Y |Zn , A] is not independent of A. Thus, instead of (1), researchers estimate f s s f = α + βZn(f Zn(s) ) + γ(A , A ) + ε,
(2)
where γ(As , Af ) is a polynomial in the son’s and father’s ages that adjusts for the fact that individuals are observed at different points along the age-earnings profile.
2.1
Estimates and Caveats
Although researchers have run regressions like (2) since at least the mid-1960s (Soltow, 1965), interest in intergenerational mobility accelerated with two seminal papers by Becker and Tomes (1979, 1986). Their 1986 paper surveyed ten empirical studies that could be used to estimate the intergenerational elasticity (β from regression (2) if Z is measured in logs) of earnings and/or income. The data for those studies came from several locations around the globe, yet the range of estimates was fairly narrow. Results in nine of the ten papers implied β < 0.3, and eight implied values less than 0.2. (The remaining study, by Atkinson (1981), estimated β ≈ 0.4 in Great Britain.) Such estimates imply a fairly high degree of mobility, and based on their theoretical model, Becker and Tomes (1986, p. S32) interpret this evidence as indicating that “both the inheritability of endowments and the capital constraints on investments in children are not large.” This sanguine conclusion was subsequently challenged on statistical grounds in two papers by Solon (1989, 1992). Solon’s critique emphasizes two issues that he shows to be interrelated: transitory earnings shocks and sample homogeneity. In the presence of transitory earnings shocks (or response error in the f data itself), the father’s observed average income Zn(f ) is a noisy estimator of his actual permanent income
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h i f f f f f f Y f –even if E[Zn(f 6= 0. Consequently, estimates of ) |A ] = Y , it is still true that V ar Y − Zn(f ) |A
β underestimate β ∗ due to the familiar attenuation bias associated with errors-in-variables. While previous researchers were clearly aware of this concern, Solon shows that the bias is particularly pronounced when the analysis uses a sample of relatively homogeneous individuals. This realization cast considerable doubt on the early estimates because matched data on fathers’ and sons’ earnings had only been available in a few unusual circumstances; for example, the fathers in an influential study by Behrman and Taubman (1985) are all white male twins who served in the military and lived until at least age 50.3 By the early 1990s, some nationally representative longitudinal data sets had been collected long enough
to contain earnings from both fathers and sons. Starting with Solon (1992), much of the recent research on the U.S. uses the Panel Study on Income Dynamics (PSID). That sample tracks members of families even after they leave and form new households, so data now exists on adult outcomes of children from the early waves. It is thus straightforward to identify matched pairs of fathers and sons. Besides overcoming the concern about sample homogeneity, the longitudinal survey design is also helpful for overcoming the concern about transitory earnings shocks because researchers can average fathers’ earnings over several years. However, Mazumder’s (2001) simulations suggest that estimates may still be attenuated until n(f ) approaches 20. In keeping with Solon’s critique, these methodological differences have a considerable effect on estimates b While the original wave of studies estimated β to be around 0.2, most studies since of β (call them β).
1990 have concluded that there is much less intergenerational mobility. Solon (1992) estimated that β is in the range of 0.4 to 0.5, and Zimmerman (1992) obtained similar results using different U.S. data set (the National Longitudinal Surveys) and several different methods. Several subsequent studies have corroborated this estimate, and the consensus seems to favor values in the range of 0.4-0.5 (see Solon (1999) for a survey).4 The largest estimate we are aware of is by Mazumder (2005), who found β ≈ 0.6. The quantitative difference may seem small, but estimates of this magnitude are substantively quite different from estimates of 0.2. Solon (1992, pp. 403-404) points out that if fathers’ and sons’ earnings are joint-normally distributed, the son of a father at the fifth percentile of the income distribution would have 3 Not surprisingly, the authors present evidence that neither the fathers nor the sons in this sample have earnings or education that are representative of the overall population. 4 Although we have exclusively discussed estimates for the U.S., intergenerational mobility has been studied in many other countries as well. See Solon (2002) for a survey.
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a 12 percent chance of earning a salary above the 80th percentile if β = 0.2, but only a 5 percent chance if β = 0.4, and only a 3 percent chance if β = 0.5. Mazumder (2005, p. 235) describes the difference in terms of time: raising β from 0.4 to 0.6 almost doubles the expected time (from 3 generations to 6) before descendants of a poverty-level family attain incomes within 5 percent of the median. One other complication of regression (2) warrants a note. Ordinarily, measurement error in the dependent variable is less troublesome than in the independent variables, so one might imagine that there is no harm in running (2) with only a single year of sons’ earnings (n(s) = 1). However, Grawe (2006) and Haider and s Solon (2006) have shown that the standard intuition does not apply because the measurement error in Zn(s) s is not classical: the correlation between Zn(s) and Y s is not constant over the life-cycle, but rather peaks
around age 40. Left-hand side measurement error is thus not harmless, and better estimates will generally be obtained by averaging the sons’ incomes over more years, i.e., increasing n(s) (Lee and Solon, 2006).
2.2
Observations with Zero Earnings
Another methodological issue that arises throughout this literature concerns respondents who report zero annual earnings. Most recent papers follow Solon (1992) and Zimmerman (1992) and drop all individuals who ever report a year of zero earnings. They offer only limited justification for this restriction, but the apparent motivation is a suspicion that many such people could have earned positive earnings but chose not to. In this view, the workers’ choice not to participate in the labor force reveals their preference for an alternate time use (e.g., retirement, full-time schooling, child-rearing), so their well-being would be badly misrepresented if the workers were treated simply as if they had been very unlucky. A handful of papers have investigated the consequences of this practice. Couch and Lillard (1998) b from the usual “restricted” sample (i.e., excluding the workers who ever reported zero earnings) compared β
to estimates from an “unrestricted” sample that also included workers who reported zero earnings, and they
b ≈ 0. Most subsequent papers have reached the opposite conclusion, found that the latter sample yielded β
however. Jäntti et al. (2006) deal with zero earners by retaining those observations, but replacing their
reported earnings with data from other years in which the workers had positive earnings, and their estimates are similar to Solon’s and Zimmerman’s, about 0.4. Minicozzi (2003), Francesconi and Nicoletti (2006),
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and Hendricks (2007) have used more complex methods in essence to predict the potential earnings of zero earners (and in some cases certain other workers), such as assumptions on earnings bounds, selection models, and simulations of the present value of lifetime income based on estimated earnings generating processes. All of them conclude that previous work has overestimated intergenerational mobility, although most estimates are still at least fairly close to 0.4 (e.g., Hendricks’ preferred estimate is 0.54).5 Unlike those studies, we focus exclusively on workers who report zero earnings despite claiming to participate in the labor force. They are not students, retirees, or prisoners, but men who claim to have experienced an extended spell of unemployment. While we appreciate the sample selection concerns raised in previous work, our impression is that the proposed adjustments are complex and controversial. Instead, we take as our baseline the original sample selection rule (i.e., dropping anyone who ever reported zero earnings), then we ask how the estimates change when we add our particular sample of zero earners. In doing so, we shall pay special attention to the number of years over which fathers’ and sons’ earnings are averaged. In short, the next section argues that it is much more sensible to include zero earners when n(f ) and n(s) are larger, so we can learn about the nature of the biases by varying the lengths of the panels.
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Zero Earnings: Shock or Signal? The merits of including zero earners depend on the relative importance of the two concerns raised by
Solon (1989), measurement error and sample selection. The former issue has been frequently noted: an observation in which a worker reports zero earnings represents the largest negative transitory earnings shock he could possibly receive. This would be problematic if workers’ incomes are averaged over only a few years. To see this formally, let us continue to use the notation from Section 2 above, and now define εt as the deviation between the worker’s current and lifetime earnings (εt ≡ Yt − Y ) and B(n) as the difference between the worker’s actual and observed average incomes: Ã n ! X B(n) ≡ Zn − Y = εt /n.
(3)
t=1
5 Mazumder (2005) and Haider and Solon (2006) also confront observations with zero earnings, but for a different reason. Both use administrative data in which some workers’ (positive) earnings are reported as zero due to censoring.
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Let us ignore the components of ε and B that are due to the age-earnings profile, since they are absorbed by the age-related polynomial γ in (2). Then when Yt = 0, the transitory earnings shock takes on its most negative feasible value, εt = −Y , and this has a large effect on the measurement error B(n) if n is small (as seen in (3)). For example, when n = 1, including the observations with zero earnings would amount to including the workers who have the most badly-measured permanent earnings (at least from below), potentially causing severe underestimation of β via (2). On the other hand, if we have the worker’s complete earnings history (n = T ), there is no problem at all: B(T ) = 0 in (3) by construction. Thus, when n is small, it seems more reasonable to drop workers with zero earnings on the grounds that their observed earnings do not closely represent their actual permanent incomes, but this concern becomes less important as n grows. In contrast to the concern about measurement error, sample selection concern is probably relatively unimportant for small n, but it becomes more troublesome as n increases. For example, suppose that an individual’s probability of earning zero dollars in a year is 1−p, where p varies across workers and is positively correlated with the worker’s permanent income: dp/dY > 0. If workers with zero earnings are excluded from the sample, the sample inclusion rule will disproportionately exclude workers with low permanent incomes. As long as dp/dY is relatively small, this sample selectivity problem would be relatively minor, but the issue becomes more relevant as panels grow longer because the standard practice is to exclude workers who have ever had a year with zero earnings. For example, if p is constant over a worker’s life, the probability that a worker remains in the sample when n years of earnings are averaged is pn . Since ∂(pn )/∂Y = npn−1 (dp/dY ) > 0, the resulting sample is non-representative. Further, as long as a reasonable share of the workers remain in the sample, ∂ 2 (pn )/∂Y ∂n = pn−1 (dp/dY )[1 + n log p] > 0.6 Thus, the sample becomes more non-representative when incomes are averaged over a larger number of years. To illustrate the potential magnitude of this concern, suppose that “rich” workers have p = 0.99 and “poor” workers have p = 0.98. If n = 1, the sample will still be nearly representative, containing 99 percent of the rich workers and 98 percent of the poor. However, for n = 10 the probability that a rich worker remains in the sample is (0.99)10 = 0.904, but the same probability for a poor worker is just 0.817. For n = 27 (as when we average fathers’ incomes over 20 years and their sons’ over 7), the probabilities become 6 Specifically, ∂ 2 pn /∂Y ∂n > 0 as long as pn > 1/e. This condition is likely to hold in almost any available sample. For example, if the probability of earning zero is no more than 2 percent (p ≥ 0.98), then the panel would have to contain at least 50 years of data to violate the condition. Even for p = 0.96, the condition holds for n ≤ 25.
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0.762 and 0.597, respectively. Thus, despite our assumption that the poor are twice as likely to experience zero earnings, both groups are almost equally likely to be included in the sample for n = 1, yet at n = 27 rich workers are 28 percent more likely than poor workers to remain. To summarize intuitively, the choice to include or exclude workers who ever report zero annual earnings involves a trade-off between measuring each worker’s earnings accurately and maintaining a representative sample. When we only observe workers’ earnings for a small number of years, the greater fear is that including observations with zero earnings will result in measurement error–the transitory shocks they receive in those years are not balanced against several more representative years, and the sample is still nearly representative because relatively few workers are dropped at any level of permanent income. However, when n is larger there is less to fear from measurement error because large transitory shocks are averaged over a larger number of years, but there is a much greater danger of creating a seriously non-representative sample because individuals with high permanent incomes are much more likely never to experience a year with zero earnings.
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Data Our main empirical analysis uses the PSID, the same data used by Solon (1992) and most subsequent work
on intergenerational mobility in the U.S. The PSID is a longitudinal survey that has tracked all members of the sample families since 1968, so many men from early waves can be matched to their adult sons in later waves. When we investigate intergenerational mobility in Section 6, those matched pairs of fathers’ and sons’ earnings histories are the unit of analysis. The unit of analysis is individual person-years in Section 5, when we examine the characteristics of men who report zero annual earnings. That exercise will also use data from the Current Population Survey (CPS), but we will wait to discuss that ancillary sample.
4.1
Sample Inclusion Criteria
As discussed in Section 3, some of our analysis requires us to compare estimates across specifications in which individuals’ earnings are averaged across different numbers of years. To ensure that the comparison is not affected by sample attrition in the intervening years, we shall always (except where otherwise stated) restrict our sample to only the father-son pairs in which the father has reported earnings data in all 20
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years from 1968-1987 and the son has reported earnings data in all applicable years between 1989-2002. It may appear that this gives us 14 years of data for sons, but only seven years are actually available because some waves of the PSID do not contain information on earnings and because the PSID became biennial after 1997.7 Since our emphasis is only on men who intend to participate in the labor force, we exclude any men who report that they were students, retired, keeping house, or disabled in any of the years, regardless of the earnings the individual reported receiving for those years. We also drop any men who did not report at least two years of positive earnings. This is not a stringent requirement; 99 percent of the fathers have at least 17 years with positive earnings, and 96 percent of the sons have at least five years (out of 7). Finally, we drop any respondents who were under age 21 or over age 65, as well as sons who were over age 16 in 1968. Previous work uses similar restrictions in order to ensure that the men within each group (fathers and sons) do not belong to extremely different cohorts, and here the restrictions also eliminate men who are at ages where it is common to be a student or retired, even if the men do not report those statuses. The resulting sample thus includes fathers born between 1923 and 1947 and their sons born between 1952 and 1968. We have created two samples using these specifications. The first includes only the 226 father-son pairs in which neither ever reports a year with zero earnings. This is the restriction common in the literature, and we call the resulting data the “restricted” sample. The other sample includes all 226 pairs from the restricted sample, plus 51 additional father-son pairs in which one or both report at least one year with zero earnings, for a total of 277 pairs. Note that the additional men still meet all of the conditions listed above, so their responses are consistent with our theme of long-term unemployment. We call this second set our “unrestricted” sample. Some fathers in these samples have multiple sons; the restricted sample includes only 142 unique fathers, and the unrestricted sample has 171. Depending on one’s perspective, this may cause some complications. If we are mainly interested in the opportunities available to sons, then the proper approach would be to regard the data as observations on sons. We would then weight the data using the sons’ sample weights and cluster the standard errors on the fathers in order to adjust for non-independence of observations from brothers. Alternatively, one might be interested in fathers’ abilities to help their sons move through the 7 Sons’
earnings data is available for 1989-1992, 1996, 1998, and 2002.
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earnings distribution. Some previous papers have at least implicitly adopted that perspective by considering only the oldest qualifying son for each father and using the fathers’ sample weights. We are somewhat more sympathetic to the former perspective, so we adopt that approach as our preferred specification. Nevertheless, we have also tried the latter approach, and as presented in Section 6, the results are similar. One reason may be that relatively few fathers have many sons. Fathers in both of our samples have an average of 1.6 sons, almost 60 percent of them (99 of 171) have just one son, and only 19 have more than two. One caveat to note is that the PSID only reports the total labor earnings of men who are heads of households, so men who are not heads throughout the sample period cannot be used in the analysis.8 This is somewhat disconcerting because some men may respond to long-term unemployment by giving up headship status–e.g., by moving in with friends or relatives. To the extent that such transitions occur, they would presumably cause us to lose some of the zero earners who are the focus of our analysis. Unfortunately, the concern is unavoidable because earnings information for non-heads is simply unavailable. We present some brief evidence on the consequences of this limitation at the end of the following section. A second concern relates to the employment status question used to create the sample. As noted above, we exclude men who ever report being students, retired, disabled, or keeping house. Most remaining men either report being employed or unemployed, but some list their status as “other.” We have retained those men because ”other” includes participation in job training programs, which is likely common among the longterm unemployed. Unfortunately, in some years that category also includes men who are in jail or prison. We were initially concerned that such men may account for some of our zero earners, but our fears were calmed when we investigated further. It is clear from the PSID’s question about “reasons for non-response” that families headed by prisoners usually do not participate in the study in those years. Further reassurance comes from a battery of questions on the 1995 PSID questionnaire that address individuals’ experiences with the criminal justice system. Although those questions were only asked of persons under age 50 (which excludes all of the fathers in our sample), they can be used to assess the sons. Almost 40 percent (21 of 57) of the sons’ zero earnings years occurred before that time, but only one of those years could possibly have been due to imprisonment. Moreover, only one son who first reported zero earnings after 1995 had been 8 The only years in which the PSID reports total earnings for men who are not household heads are 1990-1992. We have not used that data in order to maintain consistency across waves.
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incarcerated before 1995, and he was released in 1994. Of course, it is possible that some sons may have first entered jail after 1995, but it may not be likely, as they were already fairly old by then (aged 27-43). Finally, we ran several key regressions in two ways: (a) excluding the individual who had both been in jail and reported zero earnings before 1995, and (b) excluding all sons who had so much as been charged with breaking the law before 1995. In all cases the estimates differed from those reported in Section 6 by less than two percent. Thus, while we cannot be absolutely certain that none of our zero earners were in prison, the evidence indicates that the scope of the problem is quite limited and has little effect on our results. Another issue is sample selection caused by attrition. To some extent this is an unavoidable feature of the PSID, and it may or may not be a problem. Becketti et al. (1998) find that the PSID is fairly representative in spite of attrition, but Hertz (2008) argues that the poor are more likely to exit the sample. Under our sample selection rules, there is also quasi-attrition due to retirements, schooling, other transitions out of the labor force, and changes in headship status. It is not clear how this affects the sample composition. Wealthy families may be underrepresented if they are more likely to retire early and to send their children to graduate school, but attrition due to incarceration may have the opposite effect. Of course, such issues are pervasive in this literature, and they would be more troubling if our goal were to measure β precisely. They are less b increases substantially when we include problematic here, since we are more interested in showing that β people who have experienced long spells of unemployment.
4.2
Measures of Earnings
The main dependent and independent variables are the son’s and father’s average log real earnings (in 2003 dollars). To accommodate observations with zero earnings, we add one dollar to each person’s reported earnings. Thus, if yt is the person’s total labor earnings in year t and pt is the price level, we compute
Zn =
à n X
!
ln(1 + yt /pt ) /n.
t=1
(4)
Note that Zn is the log of the geometric average of real income (plus one). In principle, one might have instead P computed the log of average earnings (ln [ (yt /npt )]), but specification (4) follows the standard practice (e.g., Solon, 1992; Couch and Lillard, 1998).Call Zn the person’s “(unconditional) average log earnings.”
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It is also useful to decompose Zn into (a) the worker’s number of zero earnings years, and (b) his average earnings when his earnings are positive. Thus, define a worker’s “conditional average log earnings” as
fn ≡ Z
Pn Zn t=1 ln(1 + yt /pt ) P , = n Φn t=1 I(yt > 0)
(5)
Pn where I is an indicator function and Φn ≡ [ t=1 I(yt > 0)] /n is the worker’s zero earnings rate.
4.3
Summary Statistics
Table 1 reports some summary statistics for our sample. Only 277 father-son pairs have reported earnings for all 27 years. While this sample is small compared to those used in most microeconomic studies, it is only slightly smaller than many samples used in studies of intergenerational mobility. For example, Solon’s (1992) largest sample contained 326 father-son pairs, and only 290 remained when he averaged fathers’ incomes over five years. What is more notable here is that 51 of the available father-son histories contain at least one report of zero annual earnings, so the unrestricted sample is 23 percent larger than the restricted sample. [TABLE 1 ABOUT HERE] The table also shows that father-son pairs in which someone experiences a year with zero earnings are similar to other families in terms of age, race, and education. Nevertheless, there are rather large differences in average log earnings. The difference in Z20 between the fathers in the restricted sample and the remaining fathers is 0.80, and the difference in Z7 for sons is 1.95–respectively corresponding to 122 percent and 603 percent premiums in their (geometric) average earnings. Much of these differences are due to the zero-earnings years themselves, but even if we exclude those years from the computation, the difference in g f conditional log average earnings (Z 20 and Z7 , respectively) between the two groups is 0.23 for fathers and
0.36 for sons. In other words, the raw evidence strongly suggests that men who earn relatively low wages even when they are employed are also more likely to experience long-term unemployment.
5
Characteristics of Zero Earners Since our sample from the PSID is relatively small, it is helpful to consult a larger data set to gain further 14
insight into men who have years with zero earnings. We have thus constructed a second data set from the 1980-2005 waves of the CPS.9 For comparability to our PSID sample, we again include only men aged 21-65 who report either (a) that they had positive earnings in the previous year, or (b) that they earned zero dollars but had at least one week of unemployment. However, we were unable to restrict the sample to include only men who are fathers because children are identified only while they live in the same household. The resulting sample contains 690,146 male heads of household, 6,759 of whom report zero earnings–almost 60 times as many zero earnings years as in our PSID sample (113 person-years). We have also constructed a similar sample of non-heads, which is discussed separately at the end of this section. Table 2 presents some additional summary statistics. There is a modest difference in the rates of zero earnings between the overall PSID sample (all person-years from both fathers and sons) and the sample of heads from the CPS. About 1.5 percent of person-years in the PSID sample indicate zero earnings, but the rate in our CPS sample is 1.0 percent.10 Since our PSID sample is much smaller, this difference could plausibly reflect random sampling error, but another possible explanation relates to the samples’ demographic composition. For example, 12.2 percent of the person-years are for men aged 21-30 in the PSID (an age range with slightly lower rates of zero earnings), but in the CPS the corresponding share is 21.5 percent. The CPS men also have lower wages and somewhat more education, both of which are presumably related to the relatively higher proportion of young men. The two samples have similar racial composition, however. [TABLE 2 ABOUT HERE] Despite these differences, the two samples generally display similar variation in the zero earnings rate across demographic groups. The main exception is education–according to the PSID data, persons with education beyond high school are at greater risk of having zero earnings, but the opposite pattern prevails in the CPS. Apart from that, the two samples display similar patterns of covariation. For example, non-whites are about 30 percent more likely to experience a year of zero earnings in both the PSID and the CPS. Perhaps the most notable pattern is that the zero earnings rate seems to be fairly constant over the life-cycle, especially after age 30. In the CPS, the zero earnings rate is 0.9 percent for men aged 31-40, 1.0 9 We
obtained the CPS data from the Integrated Public Use Microsample (King et al., 2009). rates are similar to figures published by the Bureau of Labor Statistics. Over the last 35 years, the average monthly fraction of the labor force that has been unemployed more than 27 weeks is 1.0 percent (calculated from Tables A-1 and A-9 in monthly Employment Situation reports, available at www.bls.gov ). 1 0 These
15
percent for men aged 41-50, 1.2 percent for men aged 51-60, and 1.1 percent for men aged 61-65. There is somewhat more variation in the age-specific rates in the PSID, but the zero earnings rate does not change monotonically in age, and one of the highest rates is for men aged 31-40. Depending on one’s prior beliefs, this evidence may lend support to the claim that these men really are unemployed and not simply uninterested in working. One might have suspected that the youngest and oldest men (who have the highest rates of unemployment anyhow) would have been most apt to falsely report unemployment when they did not really intend to work, but that hypothesis is inconsistent with the evidence in Table 2. Several other features of the data suggesting that our zero earners are indeed long-term unemployed are presented in the next section. Before we turn to that evidence, a brief aside is warranted to discuss men who are not heads of household. Recall that such men are not included in our PSID sample because that survey does not contain information on their earnings. There are no such limitations in the CPS, so we have created a second extract that includes non-heads rather than heads, but which otherwise uses the same sample selection criteria as the original CPS sample. Summary statistics for the non-heads appear in the final column of Table 2. Non-heads account for 27 percent of the men we extracted from the CPS, and 33 percent of men who report zero earnings. The risk of zero earnings is especially high for non-heads who are non-white or who have no more than a high school education; for both groups, the zero earnings rate is about double that among all household heads. This is also significant because non-white and less-educated men are more likely to be non-heads. Non-heads are substantially younger than heads as well, with almost half being under age 30. Non-heads earn much less than heads, even when they are employed–the difference in unconditional (respectively, conditional) average log earnings is 0.57 (0.53), implying a 77 (70) percent premium. It is not entirely clear how these findings affect the interpretation of our estimates in Section 6 below. It is possible that we might estimate a higher degree of intergenerational mobility if it were possible to include non-heads in the analysis. For example, if many non-heads only remain in that status for a short period while they adjust to a large negative earnings shock, then they might move throughout the earnings distribution over their careers, and thus including them might raise the estimated earnings mobility both within and between generations. It is also possible that non-heads have fewer children than other men, and if so they may not be very relevant for intergenerational studies. On the other hand, non-heads both have
16
unusually low earnings and are unusually prone to long-term unemployment. Thus, they seem in some ways like a more extreme variation on the heads who have years with zero earnings, and that would suggest that our results likely understate the role of such men in maintaining the earnings distribution across generations.
5.1
Are Zero Earners Unemployed or Withdrawn?
Since we consider men who report zero earnings but also claim to be unemployed, it may be helpful to emphasize that these men really are unemployed. We are sympathetic to the concern that the difference between unemployment and non-participation is often less than clear-cut, and obviously we have no way to verify the individuals’ state of mind during their year of zero earnings. Nevertheless, we believe there is evidence to suggest that a high percentage of the men we have identified were indeed unemployed. Perhaps the most obvious evidence lies in the report of unemployment itself. The CPS asks respondents about the duration of their spells of unemployment, and people who claim to have zero earnings answer that question very differently from other workers. Heads of household with zero earnings report an average of 31 weeks of unemployment in the previous year, and non-heads report an average of 40 weeks. In contrast, other heads of household in our sample report an average of 2 weeks of unemployment, and other non-heads report an average of 4 weeks. For zero-earning heads, 56 percent report at least 26 weeks of unemployment, 40 percent report at least 40 weeks, and 36 percent report that their spell of unemployment lasted at least 52 weeks. The fractions are even higher for non-heads: 72 percent, 64 percent, and 39 percent, respectively. Only 3 percent of other heads and 5 percent of other non-heads report more than 26 weeks of unemployment in the previous year. Thus, while it appears that a few zero earners were not actively seeking employment for part of the year, a majority indicated that they had indeed experienced long-term unemployment. Moreover, the spells of unemployment that show up in the CPS are generally isolated in the worker’s employment history. Of the 48 men in our PSID sample who report zero earnings at least once, 23 report only one zero, and another 10 report exactly two non-consecutive years with zero earnings. All of the remaining men reported positive earnings before their first year of zero earnings, all but three reported positive earnings in some wave after their last report of zero earnings, and in a majority of the cases their work history involves two or more spells of unemployment separated by some years with positive earnings. Again, a handful of
17
these cases may seem somewhat suspicious, but most seem perfectly consistent with the description of a worker who intends to participate in the labor force but has trouble maintaining steady employment. In addition. workers are much more likely to report zero earnings in years marked by economic recessions. Figure 1 plots the time series of the U.S. unemployment rate and the “zero earnings rate,” which we have computed from the CPS by dividing the number of zero earners by the total number of observations that meet our sample inclusion criteria. Since the unemployment rate is much higher than the zero earnings rate in every year, for the sake of comparison we have standardized both series by dividing each observation by the average value of the series over the period. As the figure clearly shows, the zero earnings rate tracks the official unemployment rate quite closely. It is also fluctuates more severely than the unemployment rate, which makes sense if one thinks that zero earnings year are less likely to occur in times of relatively low unemployment because unemployed workers are more likely to receive job offers at any point in time. [FIGURE 1 ABOUT HERE] A final piece of evidence shows that the respondents who report zero earnings also report that their careers are in occupations and industries that are known to be especially volatile. Table 3 lists the occupations and industries commonly reported by zero earners, along with the share of other workers who report working in those same occupations and industries. The most important thing to note is the overrepresentation of zero earners in the construction industry. That sector employs less than 10 percent of other workers, but nearly half of the zero earners, and five of the ten most common occupations among zero earners are related to construction. Specifically, about one in three zero earners are carpenters, painters, masons, tilers, construction supervisors, carpet installers, roofers, or slaters, but among other men only one in 25 is employed in those occupations. Of course, construction is the classic textbook example of a highly procyclical industry, so it would not be surprising if workers in that sector frequently experience relatively long spells of unemployment during economic downturns. Similar arguments can be made about many of the other occupations and industries listed in Table 3, including trucking, gardening, and theaters and motion pictures. Agriculture is also a volatile industry, although the shocks in that sector are presumably less related to the business cycle than to atmospheric conditions. Regardless, the point is that these lists are probably what one would expect to see if zero earners really had suffered extended bouts of unemployment. 18
[TABLE 3 ABOUT HERE]
5.2
Intergenerational Persistence in the Risk of Zero Earnings
Thus far we have argued that the men we have identified as zero-earners are long-term unemployed, represent a meaningful share of the population, have relatively low earnings, and are not a random crosssection of the labor force. These points imply that a sample that excludes zero earners may be substantially non-representative, and consequently the exclusion may bias estimates of intergenerational mobility. We now extend that argument by showing that sons are more likely to experience a year of zero earnings if their father did as well, or even if their father simply had relatively low earnings. Table 4 addresses the first claim by presenting cross-tabulations of two dummy variables (one each for fathers and sons) that equal one if the person ever reported zero annual earnings. When we consider all father-son pairs, we find that 9 percent of sons whose fathers never had zero earnings reported a year with zero earnings, but the share for sons of zero-earner fathers was 29 percent. If we only consider oldest sons, the corresponding shares are 8 and 41 percent, respectively. Likewise, fathers are more likely to be zero earners if their sons are as well. Although these are small samples, in both cases the hypothesis that fathers’ and sons’ experiences are statistically independent can be rejected at the 1 percent level. This is consistent with previous evidence that British and Norwegian workers are also at greatly increased risk of unemployment if their parents had been unemployed at some point (O’Neill and Sweetman, 1998; Ekhaugen, 2009). [TABLE 4 ABOUT HERE] The other claim is addressed in Table 5. That table presents results from four probits in which the dependent variable equals one for individuals who ever report zero earnings and zero otherwise. The first two probits indicate that sons are less likely to meet that fate if their fathers have higher earnings. Whether we measure the father’s average log earnings with (first probit) or without (second probit) the father’s zero earnings years, the estimates imply that a one percent increase in the father’s earnings reduces the son’s propensity to experience zero earnings by 0.06 percentage points. When we add simple controls for the person’s race and education (a dummy for high school or less), the estimate increases to 0.07 percentage points or 0.12 percentage points, depending on whether we use the fathers’ unconditional or conditional 19
(respectively) average log earnings. For comparison, the last two lines show the effect of individuals’ own conditional average log earnings on their propensity to earn zero, and the estimated marginal effects are -0.13 for sons and -0.14 for fathers (and -0.15 and -0.19 respectively when we use the additional controls). Thus, it appears that the risk of earning zero is at least half, and possibly as much as 80 percent, as sensitive to one’s father’s typical level of earnings as it is to one’s own typical level of earnings. [TABLE 5 ABOUT HERE] These are strong associations. Even the most conservative estimate associates a one standard deviation increase in a father’s conditional average log earnings (0.52) with a 3.1 percentage point decrease in his son’s probability of having a year with zero earnings, or about 27 percent of the mean propensity (11.2 percent, as seen in Table 4). If we use the estimate from the probit with race and education controls, the same difference in the father’s conditional average log earnings is associated with a 55 percent decrease in the son’s risk of a zero earnings year. In the latter specification, a one standard deviation increase in the son’s own conditional average log earnings predicts that his probability of having a zero earnings year falls by 79 percent, so the risk is only modestly less sensitive to the father’s typical earnings than it is to the son’s own.
6
Zero Earnings and Estimated Earnings Mobility Taken together, the findings presented above form a circumstantial case that long-term unemployment
presents a substantial barrier to intergenerational mobility. Not only are zero-earners drawn from a relatively poor segment of the earnings distribution, but they also tend to have children who are poor and at risk of long-term unemployment themselves. Among other things, this suggests that most previous studies may have overestimated intergenerational earnings mobility because they excluded such men from the analysis. We now investigate these issues by estimating the intergenerational earnings elasticity directly. Each b from a specification of regression (2) that averages point in Figure 2 represents the estimated elasticity (β)
incomes of fathers and sons over a different number of years. The points along a given line are estimates
for each value of n(f ) (2 ≤ n(f ) ≤ 20), holding constant n(s). The left-hand side of the figure presents results from the restricted sample, and the right-hand side presents results from the unrestricted sample.
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All regressions in Figure 2 use all qualifying father-son pairs, use the sons’ sampling weights, and specify γ(As , Af ) as a sum of separate cubic polynomials in the father’s and son’s average ages. [FIGURE 2 ABOUT HERE] Several features of Figure 2 should be noted. First, the estimates from the restricted sample are fairly b grows somewhat when n(s) rises, but as explained at the end of Section 2.1, this is expected in stable. β light of the increasing correlation between young men’s current and lifetime earnings as they grow older. At
any rate, the rise is modest, and all 114 estimates for the restricted sample fall between 0.41 and 0.53. This range is not only relatively narrow, but also consistent with most recent estimates in the literature. The estimates from the unrestricted sample are much more varied. They range from 0.34 to 0.76, and they tend to rise not only with n(s), but also with n(f ). The latter finding is particularly instructive in light of the discussion in Section 3 of the statistical costs and benefits of excluding persons with zero earnings. In short, the argument was that the cost (error in measuring individuals’ lifetime earnings) fell as n(f ) rose, and the benefits (representativeness of the sample) rose with n(f ). In other words, estimates from the unrestricted sample become more reliable relative to estimates from the restricted sample when incomes are averaged over a larger number of years. It is thus not surprising that the estimates from the unrestricted sample are less than those from the restricted sample for low n(f ), yet that is exactly when we expect the restricted estimates to be more appropriate. In contrast, where the unrestricted estimates are expected to be superior (as n(f ) grows), those estimates are much greater than the restricted estimates. One possible objection is that some fathers appear in the sample multiple times. However, Figure 3 shows that the same pattern emerges when we consider only the oldest son for each father. If anything, the results are even more extreme. The estimates from the restricted sample are slightly larger in this case (ranging from 0.47 to 0.61), and those from the unrestricted sample grow more sharply in n(f ), from a minimum of 0.34 (equal to the minimum estimate from the sample of all father-son pairs) to a maximum of 1.05. [FIGURE 3 ABOUT HERE] As an aside, the fact that the estimates are smaller when we consider all father-son pairs argues against a simple genetic theory of intergenerational mobility. If one hypothesized that the correlation between fathers’
21
and sons’ earnings were simply a matter of biology, and the degree of hereditability is the same across the population, then one would expect that the two samples (all sons and oldest sons) would yield similar estimates, all else equal (same n(f ), same n(s), treatment of zero earners, etc.). Since that prediction is not supported by the data, we are left to conclude either that the degree of genetic hereditability differs across people and is correlated with fertility, or else that intergenerational mobility is also affected by nongenetic factors. Of course, many non-genetic mechanisms seem quite reasonable, as everything from parental investments in children’s human capital to fertility decisions is plausibly influenced by parental earnings. At any rate, the evidence in Figures 2 and 3 indicates that the best estimates of the intergenerational earnings elasticity increase markedly when the zero earners are included in the sample. For example, when we average incomes over the largest number of years (n(f ) = 20, n(s) = 7), the point estimates are 0.47 (s.e.=0.07) and 0.54 (0.08) in the restricted samples of all sons and oldest sons, respectively. In the respective unrestricted samples, the estimates grow to 0.68 (0.19) and 0.94 (0.25). To be fair, the standard errors are large enough here that we cannot reject the hypothesis that the unrestricted and restricted estimates are equal, but the same critique could be leveled against much of the intergenerational mobility literature. To take a prominent example, a key estimate in Solon’s (1992) seminal paper (with n(f ) = 5, n(s) = 1) has a 95 percent confidence interval of (0.23, 0.60)–in other words, ranging from a very high to a very low rate of intergenerational mobility. In any of these papers, the force of the argument comes not from the estimate’s precision, but from its robustness. In that sense, our strongest evidence may be the large number of estimates, from different samples and averaging incomes over different numbers of years, that indicate a substantial reduction in intergenerational mobility when zero earners are included. b is especially striking considering that the unrestricted samples are only The magnitude of the increase in β
about 20 percent larger than the restricted samples–that is, there are about five times as many father-son pairs in which both had positive earnings every year than pairs in which the father or son has a zero earnings year. To take an example from the preceding paragraph, the only difference between the restricted and
unrestricted samples is the treatment of 29 father-oldest son pairs (less than 17 percent of the unrestricted sample) in which there is a zero earnings year, yet that causes the point estimate of β to rise by 74%. Clearly, the families with zero earners must have an extremely high intergenerational earnings elasticity.
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6.1
Attrition Bias
Although it does not affect the conclusions above, readers interested in the level of β may suspect that these estimates suffer from attrition bias. After all, our analyses thus far have used only father-son pair in which both individuals appear in the data in all relevant periods, and it is possible that the pairs that leave the sample have unusually high rates of earnings mobility. For example, attrition may be more common among families that experience large earnings shocks. Most previous studies have not used such a strong sample retention criterion, so that difference might account for some of the gap between our estimates of β. This possibility is addressed in Figure 4. Like Figures 2 and 3, Figure 4 plots estimates of β when fathers’ and sons’ earnings are averaged over different numbers of years, but here each regression uses all father-son pairs that have sufficiently long earnings histories to compute the relevant average earnings. For example, some pairs that are included in the regressions using (n(f ) = 2, n(s) = 2) do not appear in those using (n(f ) = 5, n(s) = 3) because some individuals exit the sample in the intermediate years. Despite those differences, Figure 4 looks much like Figure 2. Not only are the patterns of estimates similar across figures, but so are the levels. That is not surprising when incomes are averaged over many years (e.g., the estimates for (n(f ) = 19, n(s) = 7) could only differ between the two figures if many fathers who had 19 years of earnings data did not report their earnings for the 20th year), but we see that the levels are even similar for small n(f ) and n(s). For example, the four estimates (restricted versus unrestricted, constant sample or not) of β using (n(f ) = 5, n(s) = 2) are all between 0.41 and 0.46. The only conclusion to be drawn is that our findings are not heavily influenced by sample attrition. [FIGURE 4 ABOUT HERE]
6.2
Do Zeros Matter Directly or Via Selection?
b increases when we include persons with zero earnings, a natural Now that we have established that β
question to ask is whether the increase is predominantly due to (a) the correlation between fathers’ and sons’ risks of long-term unemployment and the attendant large earnings shocks, or (b) the increased sample homogeneity caused by the disproportionate exclusion of workers who have relatively low earnings even when they are employed. Some of the evidence presented previously has lent support to both claims. Table
23
4 showed that sons are much more likely to have a year with zero earnings if their father does as well, and the comparison of unconditional and conditional average log earnings in Tables 1 and 2 indicated that those measure of average earnings are quite sensitive to the treatment of years with zero earnings. On the other hand, Table 5 demonstrated that individuals’ risk of zero earnings years is highly correlated with their conditional average log earnings, and Table 1 implies that a sample selection rule that excludes zero earners causes many fathers and sons with low Ze to be dropped from the sample.
In an effort to distinguish between the two channels, Table 6 presents estimates of the intergenerational
earnings elasticity from five regressions that average fathers’ incomes over 20 years and sons’ incomes over 7 years. The first four regressions use the unrestricted sample, and the only difference between them lies in the method used to compute average log earnings. The four regressions represent the complete set of possible combinations of unconditional and conditional log average earnings for the fathers and sons. The fifth regression presented in Table 6 is from the restricted sample. Note that there is no distinction between the unconditional and conditional averages in that sample because no individuals in that sample ever report zero earnings, and thus there is only one possible regression for that sample. [TABLE 6 ABOUT HERE] The first and last estimates are those plotted at the end of the top lines in the unrestricted and restricted b = 0.68 and β b = 0.47, respectively. The difference is what we attribute to the inclusion panels of Figure 2: β of father-son pairs that include zero earners. The second regression is identical to the first, except that the
explanatory variable is now fathers’ conditional average log earnings rather than the unconditional average. The resulting estimate is 0.63, only slightly smaller than the estimate using the fathers unconditional average. Based on that comparison alone, it may seem that the increased elasticity is mainly due to sample selection, rather than the influence of the large negative earnings shocks experienced by the zero earnings fathers. However, the situation appears much different if we use the conditional averages for both fathers and sons. This is the fourth regression in Table 6, and the resulting estimate of 0.44 is very close to (even slightly less than) the estimate from the restricted sample. The major difference between those two regressions is that the unrestricted sample adds father-son pairs for whom earnings cannot be averaged over quite as many years due to the zeros that are ignored in computing the conditional average. Thus, those zeros are evidently what 24
drove the sharp increase in the intergenerational elasticity when we used unconditional average earnings. An even more telling result emerges when we go back to using the father’s unconditional average log earnings, but continue to use the son’s conditional average (the third regression in Table 6). In that case, the b from the identical estimated intergenerational elasticity falls even further to 0.31–less than half the size of β regression in which the zeros were included in the son’s earnings. In other words, the father’s unconditional
average log earnings does not predict the son’s conditional average as well as the father’s conditional average does. This contrasts with our earlier finding that the fathers’ unconditional and conditional averages were almost equally correlated with the sons’ unconditional average. We interpret these results as follows. If we ignore years with zero earnings when computing average log earnings, it does not make much difference whether the sample includes or excludes people who report some zero earnings years. Either way, the estimate is around 0.45, which is quite consistent with previous results. Based on that, we conclude that sample selection is not really the issue. Moreover, using the zeros to compute the father’s average income seems to make it harder to predict the son’s conditional average log earnings. We suspect that the zeros do not provide much help in predicting the son’s conditional average beyond what was already offered by the father’s conditional average, but the introduction of the zeros into the father’s average (i.e., switching from the father’s conditional average to his unconditional average) acts like measurement error in weakening the relationship between the father’s income measure and the son’s conditional average. However, things are substantially different if the goal is to explain the son’s unconditional average. In that case, the estimated intergenerational elasticity is much larger, and not very sensitive to the choice between using fathers’ unconditional or conditional averages. The explanation for this difference lies in Table 5: sons’ risk of zero earnings is very sensitive to their fathers’ conditional average log earnings. In other words, it seems that the high intergenerational earnings elasticity estimated from our unrestricted sample is not mainly caused by the fathers’ years with zero earnings, nor does it reflect a fundamental difference in the earning power between the families that are included and excluded under the traditional sample selection rule, at least when they are employed. Rather, sons of fathers with low earnings (even conditional on working) are much more likely to experience long-term unemployment. When they are employed, such sons have earnings that are correlated with their fathers’ in much the same way as in other
25
families. Yet that relationship grossly understates the persistence of earnings differences across generations because it ignores the very bad outcomes that are much more likely for children from poor families. Stated yet another way, the main problem with the usual sample selection rule that excludes zero earners is not exactly that it disproportionately excludes poor families. Based on our results using conditional averages, it appears that the persistence of conditional earnings for such families is not so different from other families. Nor is the problem really that it excludes people who have experienced bad outcomes. That is a problem, but the direction of the bias is not clear ex ante–it could actually bias the estimates toward greater mobility if that bad outcome were equally likely for children from all points along the (fathers’) earnings distribution. Rather, the major problem really lies at the nexus of those concerns. The rule excludes people who have experienced bad outcomes, and those people are drawn heavily from families with b toward zero because it predominantly lower earnings, and consequently the rule effectively tends to bias β removes families where the bad outcome reinforced the family’s position in the earnings distribution.
7
Conclusion Considering that our unrestricted estimates of the intergenerational earnings elasticity are among the
largest in the literature, there may be some temptation to conclude that previous studies have underestimated that parameter, and thus overestimated intergenerational mobility, because they have ignored families that have experienced large negative earnings shocks. While we agree that it is disconcerting that the usual sample selection rules apparently have the unintended effect of dropping a group of relatively poor respondents from studies largely intended to investigate poverty, we are hesitant to draw a strong conclusion about the true level of mobility. It has become clear to us through the course of this project is that estimates of the intergenerational earnings elasticity can be quite sensitive to sample selection rules, and there is at least some disagreement in the literature about those rules. Furthermore, we suspect that people who face a greater risk of earnings shocks are more likely to be underrepresented in empirical samples, not only because of sample selection rules that exclude apparent outliers, but also simply because surveys have greater difficulty in finding and following such people. Of course, it is far from clear that the inclusion of those individuals would always raise the estimated elasticity, so the magnitude of the estimates should be interpreted cautiously.
26
Yet even if we are circumspect about the level of the intergenerational earnings elasticity, it strikes us as less controversial to compare estimates from two samples that differ only by the inclusion of the focal group. Using that methodology, we have found that estimates are very sensitive to the inclusion of families in which a father and/or his son have ever experienced a year with zero annual earnings despite attempting to work. In keeping with the motivation for considering that group, several facts suggested that those individuals had indeed experienced long-term unemployment, and their children have both relatively low earnings when employed and a heightened risk of long-term unemployment themselves. We thus conclude that such families have much less intergenerational mobility through the earnings distribution, and consequently that such families warrant greater attention from researchers and policy makers. One can easily imagine several reasons why this group would have unusually low intergenerational mobility. Not only are there the usual mechanisms of nature and nurture, but there are also a host of possibilities involving institutions like credit markets, welfare policies, labor laws, and geographic variation in labor demand. While the evidence presented here does not provide conclusive evidence on those potential mechanisms, several findings are suggestive. First, what seems to have the greatest influence on the estimated intergenerational elasticity is the inclusion of the sons’ years with zero earnings; the estimates are not especially high if we use the sons’ log average earnings conditional on working, even when we include the zero earner families. It thus appears that the result is driven by the correlation between fathers’ earnings and their sons’ risk of long-term unemployment. Having said that, the estimated intergenerational elasticity is quite similar whether the key regressor is the father’s unconditional average log earnings or his average log earnings conditional on having positive earnings. This suggests that the intergenerational effect has less to do with the father’s episode of unemployment than with the fact that his earnings are typically low, which would seem to argue against explanations involving credit market failures, inadequate social safety nets, or the son’s psychological trauma associated with his father’s unemployment. Similarly, the facts that zero earners are much more common in volatile industries, especially construction, and that they are most likely to have zero earnings during recessions cast some doubt on theories involving some hereditary factors like health problems or addictions, but instead they seem to indicate that the main mechanism must explain why children from less affluent families are often observed in volatile careers.
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[12] Grawe, Nathan D., and Casey B. Mulligan. 2002. “Economic interpretations of intergenerational interpretations.” Journal of Economic Perspectives 16(3), 45-58. [13] Haider, Steven, and Gary Solon. 2006. “Life-cycle variation in the association between current and lifetime income.” American Economic Review 96(4), 1308-1320. [14] Hendricks, Lutz. 2007. “The intergenerational persistence of lifetime earnings.” European Economic Review 51(1), 125-144. [15] Hertz, Tom. 2008. “A group-specific measure of intergenerational persistence.” Economics Letters 100(3), 415-417. [16] Jäntti, Markus, Bernt Bratsberg, Knut Røed, Oddbjørn Raaum, Robin Naylor, Eva Osterbacka, Anders Björklund, and Tor Eriksson. 2006. “American exceptionalism in a new light: A comparison of the intergenerational earnings mobility in the Nordic countries, the United Kingdom, and the United States.” IZA Discussion Papers Series, number 1938. [17] King, Miriam, Steven Ruggles, Trent Alexander, Donna Leicach, and Matthew Sobek. 2009. Integrated Public Use Microdata Series, Current Population Survey: Version 2.0. [Machine-readable database]. Minneapolis, MN: Minnesota Population Center. Available at http://cps.ipums.org. [18] Lee, Chul-In, and Gary Solon. 2006. “Trends in intergenerational income mobility.” NBER Working Paper Series, number 12007. [19] Mazumder, Bhashkar. 2001. “Earnings mobility in the U.S.: A new look at intergenerational inequality.” FRB Chicago Working Paper Series, number 2001-18. [20] Mazumder, Bhashkar. 2005. “Fortunate sons: New estimates of intergenerational mobility in the United States using Social Security earnings data.” Review of Economics and Statistics 87(2), 235-255. [21] Minicozzi, Alexandra L. 2003. “Estimation of sons’ intergenerational earnings mobility in the presence of censoring.” Journal of Applied Econometrics 18(3), 291-314. [22] Nicoletti, Cheti, and Marco Francesconi. 2006. “Intergenerational mobility and sample selection in short panels.” Journal of Applied Econometrics 21(8), 1265-1293. 29
[23] O’Neill, Donal, and Olive Sweetman. 1998. “Intergenerational Mobility in Britain: Evidence from Unemployment Patterns.” Oxford Bulletin of Economics and Statistics 60(4), 431-447. [24] Solon, Gary. 1989. “Biases in the estimation of intergenerational earnings correlations.” Review of Economics and Statistics 71(1), 172-174. [25] Solon, Gary. 1992. “Intergenerational income mobility in the United States.” American Economic Review 82(3), 393-408. [26] Solon, Gary. 1999. “Intergenerational mobility in the labor market.” In O. Ashenfelter and D. Card, eds., Handbook of Labor Economics, Vol. 3 (Amsterdam: Elsevier), 1761-1800. [27] Solon, Gary. 2002. “Cross-country differences in intergenerational earnings mobility.” Journal of Economic Perspectives 16(3), 59-66. [28] Soltow, Lee. 1965. Toward Income Equality in Norway. (Madison, WI: University of Wisconsin Press). [29] Zimmerman, David J. 1992. “Regression toward mediocrity in economic stature.” American Economic Review 82(3), 409-429.
30
1.9 1.7
Zero earnings rate
1.5
Unemployment rate
1.3 1.1 0.9 0.7 0.5
Year
2005
2004
2003
2002
2001
2000
1999
1998
1997
1996
1995
1994
1993
1992
1991
1990
1989
1988
1987
1986
1985
1984
1983
1982
1981
0.3 1980
Rate relative to its average over the period
2.1
Figure 1: Standardized unemployment and zero earnings rates in the U.S., 1980-2005
Estimated intergenerational earnings elasticity
0.9
Figure 2: Estimated intergenerational earnings elasticity when averaging earnings of fathers and sons over the specified number of years, for all father-son pairs in the restricted and unrestricted samples
0.8
0.7
0.6
0.5
0.4
0.3
Restricted sample
Unrestricted sample
0.2
Years used to compute sons' avg. log earnings 0.1
2 year avg
3 year avg
4 year avg
5 year avg
6 year avg
7 year avg
0 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20
2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20
Years used to compute fathers' average log earnings
1.1
Figure 3: Estimated intergenerational earnings elasticity using only pairs of fathers and their oldest sons
Estimated intergenerational earings elasticity
1 0.9 0.8 0.7 0.6 0.5 0.4 Unrestricted sample
Restricted sample
0.3
Years used to compute sons' avg. log earnings
0.2
2 year avg
3 year avg
4 year avg
5 year avg
6 year avg
7 year avg
0.1 0 2
4
6
8
10
12
14
16
18
20
2
4
6
8
10
Years used to compute fathers' average log earnings
12
14
16
18
20
Estimated intergenerational earnings elasticity
0.9
Figure 4: Estimated intergenerational earnings elasticity using all fatherson pairs, including pairs that exit the sample during the period
0.8
0.7
0.6
0.5
0.4
0.3
Restricted sample Unrestricted sample
0.2
Years used to compute sons' average log earnings 0.1
2 year avg
3 year avg
4 year avg
5 year avg
6 year avg
7 year avg
0 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20
2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 18 19 20
Years used to compute fathers' average log earnings
Table 1: Summary Statistics
Unrestricted sample Fathers
Average log earnings, 1968-1987 …Average log earnings, excluding zeros Age in 1968 White Years of schooling
Restricted sample (no zero earners)
Father-son pairs with at least one year of zero earnings
Mean 10.59 10.70 34.76 0.86 12.42
Std Dev 0.72 0.52 5.56 0.35 2.99
Mean 10.74 10.74 34.70 0.85 12.44
Std Dev 0.52 0.52 5.47 0.36 2.92
Mean 9.94 10.51 34.94 0.86 12.31
Std Dev 1.04 0.49 5.86 0.35 3.28
10.29 10.58 28.61 0.85 13.67
1.24 0.60 4.16 0.36 2.02
10.65 10.65 28.69 0.85 13.62
0.53 0.53 4.19 0.36 2.03
8.70 10.29 28.25 0.86 13.90
2.03 0.78 4.04 0.35 1.96
Sons
Average log earnings, 1989-2002 …Average log earnings, excluding zeros Age in 1989 White Years of schooling
Number of father-son pairs 277 226 51 Notes: The unrestricted sample includes all father-son pairs in the PSID in which the father appears in the survey as a head of household aged 21-65 in every wave from 1968-1987 and the son appears as a head aged 21-65 in every wave between 1989 and 2002 in which the survey asked about earnings. Individuals are considered to be missing if they report zero earnings and but not unemployment status (i.e., retirees, students, etc., are excluded). The restricted sample drops father-son pairs in which either individual ever reports zero earnings.
Table 2: Comparisons of Zero Earners in Our PSID and CPS Samples Our Sample (PSID) Variables Sample size (person-years) Years with zero earnings
Mean log real earnings Mean log real earnings, excluding zeros Percent who are White Educated beyond HS Age 21 to 30 Age 31 to 40 Age 41 to 50 Age 51 to 60 Age 61 to 65
Whites Non-whites
Overall 7,479 113
CPS, 1980-2005
Fathers 5,540 56
Sons 1,939 57
Sample means 10.44 10.59 10.69 10.70
10.29 10.58
10.32 10.42
9.75 9.89
84.8 53.1 34.0 51.9 14.0 0.0 0.0
87.8 52.6 21.5 30.5 25.5 17.7 4.8
81.1 47.5 46.7 25.5 16.5 9.0 2.2
0.9 1.2
1.2 2.3
84.7 44.0 12.2 34.0 36.5 16.5 0.8
84.5 35.0 4.6 27.7 44.4 22.3 1.0
Heads Non-heads 690,146 254,318 6,759 3,283
Percentage of observations in each group that report zero earnings 1.4 1.1 2.4 1.9 0.7 5.4
Education: HS or less Education: More than HS
1.1 2.1
0.9 1.2
1.9 3.9
1.3 0.6
1.9 0.8
Age 21 to 30 Age 31 to 40 Age 41 to 50 Age 51 to 60 Age 61 to 65
0.7 1.9 1.2 2.0 N/A
0.4 0.3 1.0 2.0 N/A
0.8 4.1 3.6 N/A N/A
0.7 0.9 1.0 1.2 1.1
1.2 1.6 1.4 1.4 1.1
85.2 14.8
68.8 31.2
64.9 35.1
71.2 28.8
Whites Non-whites
Percent of the observations with zero earnings who are: 84.7 85.7 83.9 15.3 14.3 16.1
Education: HS or less Education: More than HS
50.9 49.2
57.1 42.9
41.9 58.1
Age 21 to 30 5.3 1.8 8.8 16.7 42.3 Age 31 to 40 41.6 8.9 73.7 29.3 30.0 Age 41 to 50 30.1 42.9 17.5 27.5 16.8 Age 51 to 60 N/A 22.1 44.6 21.2 9.0 Age 61 to 65 N/A 0.9 1.8 5.4 1.9 Notes: All men in "our sample" are household heads aged 21-65 througout the duration of the sample. All samples exclude men who report zero earnings but did not report unemployment (e.g., students and retirees). Averages are weighted using sample weights. "N/A" indicates that there were fewer than 200 observations in the category; in some cases this is by construction (e.g., all sons in the PSID were born after 1951, so none are over age 50 in 2001).
Table 3: Most commonly reported occupations and industries of persons reporting zero earnings, U.S., 1980-2005 Heads of household
All men
Percentage of group in occ/ind Occupation Carpenters Managers and administrators, n.e.c. Painters, construction and maintenance Truck, delivery, and tractor drivers Masons, tilers, and carpet installers Supervisors of construction work Gardeners and groundskeepers Salespersons, n.e.c. Automobile mechanics Roofers and slaters Total in listed occupations Industries Construction Miscellaneous business services Agriculture Trucking service Theaters and motion pictures Auto repair services and garages Miscellaneous repair services Real estate Eating and drinking places Logging Total in listed industries
Zero earners Positive earners 16.44 1.75 10.55 8.15 7.12 0.61 5.31 4.41 4.28 0.48 3.25 0.94 2.25 0.64 2.12 3.50 2.10 1.15 2.07 0.21 55.49 21.84
48.41 6.08 5.37 4.96 3.15 3.05 2.30 1.72 1.60 1.24 77.88
9.68 3.70 2.91 2.26 0.36 1.47 0.75 1.47 2.18 0.19 24.97
Percentage of group in occ/ind Occupation Carpenters Managers and administrators, n.e.c. Painters, construction and maintenance Truck, delivery, and tractor drivers Masons, tilers, and carpet installers Supervisors of construction work Gardeners and groundskeepers Automobile mechanics Salespersons, n.e.c. Roofers and slaters Total in listed occupations Industries Construction Agriculture Miscellaneous business services Trucking service Auto repair services and garages Theaters and motion pictures Miscellaneous repair services Eating and drinking places Real estate Miscellaneous entertainment and recreation Total in listed industries
Zero earners Positive earners 15.33 1.83 9.02 6.96 7.58 0.69 5.11 4.46 3.92 0.51 3.02 0.86 2.94 0.84 2.18 1.19 2.15 3.39 1.98 0.26 53.23 20.99
46.18 6.06 6.01 4.59 3.38 3.30 2.23 1.95 1.48 1.14 76.32
Notes: Data is from the CPS, 1980-2005. The reported numbers are the fraction of men in our sample (see text for restrictions) who report careers in the listed occupations and industries. The shares of employed men (postive earners) in those occupations and industries is listed for comparison.
9.98 2.89 3.94 2.29 1.59 0.40 0.73 2.90 1.38 0.86 26.96
Table 4: Incidence of zero earnings years for fathers and sons A. All father-son pairs Sons with no zero Sons with at least one earnings years zero earnings year Fathers with no zero earnings years Fathers with at least one zero earnings year
226 20
23 8
Row Total 249 28
Column total Fraction with at least one year
246 0.08
31 0.26
277 0.10
0.11
Chi-squared 7.30
P-value 0.007
Fraction with at least one year 0.08 0.41 0.11
Hypothesis: fathers and sons are independent
Fraction with at least one year 0.09 0.29
B. Fathers and their oldest sons Sons with no zero Sons with at least one earnings years zero earnings year Fathers with no zero earnings years Fathers with at least one zero earnings year
142 10
12 7
Row Total 154 17
Column total Fraction with at least one year
152 0.07
19 0.37
171 0.10
Chi-squared 11.98
P-value 0.001
Hypothesis: fathers and sons are independent
Table 5: Estimated effects of fathers' (and sons') average log earnings on the probability of experiencing zero earnings Independent variable: Marginal Marginal average log earnings effect effect Dependent variable (dummy) SE P SE P Son ever reports zero earnings -0.059 0.019 0.00 -0.074 0.019 0.00 Father's, including zeros Son ever reports zero earnings
Father's, excluding zeros
-0.059
0.034
0.08
-0.119
0.043
0.00
Son ever reports zero earnings
Son's, excluding zeros
-0.126
0.032
0.00
-0.148
0.034
0.00
Father ever reports zero earnings
Father's, excluding zeros
-0.135
0.047
0.00
-0.185
0.054
0.00
age race (=1 if white) education (=1 if HS or less) Notes: The marginal effects are estimated using probits on the sample of all available father-son pairs. Sample size is 277 in all cases. Other control variables:
age
Table 6: Unrestricted estimates when average earnings includes or excludes zeros Dependent variable: son's avg. log earnings, 1989-2002 (7 years) Independent variable: father's avg. log earnings, 1968-1987 (20 years) Zeros included in avg. log earnings? Specification Son Father Estimate 1 Yes Yes 0.68 2 Yes No 0.63 3 No Yes 0.31 4 No No 0.44 5 (Restricted sample) 0.47
SE 0.19 0.16 0.05 0.08 0.07
Sample size 277 277 277 277 226
Note: All regressions are run using all father-son pairs that report earnings data in each year. The specification also includes a cubic polynomial in both fathers' and sons' ages. Data is weighted using sons' sample weights, and standard errors are clustered on families.
