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Federal Reserve Bank of Chicago Estimating the Intergenerational Elasticity and Rank Association in the US: Overcoming the Current Limitations of Tax Data Bhashkar Mazumder REVISED September 2015 WP 2015-04 Estimating the Intergenerational Elasticity and Rank Association in the US: Overcoming the Current Limitations of Tax Data Bhashkar Mazumder* Federal Reserve Bank of Chicago September, 2015 Abstract: Ideal estimates of the intergenerational elasticity (IGE) in income require a large panel of income data covering the entire working lifetimes for two generations. Previous studies have demonstrated that using short panels and covering only certain portions of the lifecycle can lead to considerable bias. I address these biases by using the PSID and constructing long time averages centered at age 40 in both generations. I find that the IGE in family income in the U.S. is likely greater than 0.6 suggesting a relatively low rate of intergenerational mobility in the U.S. I find similar sized estimates for the IGE in labor income. These estimates support the prior findings of Mazumder (2005a, b) and are also similar to comparable estimates reported by Mitnik et al (2015). In contrast, a recent influential study by Chetty et al (2014) using tax data that begins in 1996, estimates the IGE in family income for the U.S. to be just 0.344 implying a much higher rate of intergenerational mobility. I demonstrate that despite the seeming advantages of extremely large samples of administrative tax data, the age structure, and limited panel dimension of the data used by Chetty et al leads to considerable downward bias in estimating the IGE. I further demonstrate that the sensitivity checks in Chetty et al regarding the age at which children’s income is measured, and the length of the time average of parent income used to estimate the IGE, are also flawed due to these data limitations. There are also concerns that tax data, unlike survey data, may not adequately reflect all sources of family income. Estimates of the rank-rank slope, Chetty et al’s preferred estimator, are more robust to the limitations of the tax data but are also downward biased and modestly overstate mobility. However, Chetty et al’s main findings of sizable geographic differences within the US in rank mobility, are unlikely to be affected by these biases. I conclude that researchers should continue to use both the IGE and rank based measures depending on their preferred concept of mobility. It also important for researchers to have adequate coverage of key portions of the lifecycle and to consider the possible drawbacks of using administrative data. *I thank Andy Jordan and Karl Schulze for outstanding research assistance. I thank participants at seminars at IZA, the New York Fed, the Chicago Fed, the University of Bergen and the University of Tennessee as well as Nathaniel Hendren for helpful comments. I also thank a referee for valuable comments and guidance. The views expressed here do not reflect those of the Federal Reserve Bank of Chicago or the Federal Reserve system. I. Introduction Inequality of opportunity has become a tremendously salient issue for policy makers across many countries in recent years. The sharp rise in inequality has given rise to fears that economic disparities will persist into future generations. This has led to a heightened focus on the literature on intergenerational economic mobility. This body of research, which is now several decades old, seeks to understand the degree to which economic status is transmitted across generations. A critical first step in understanding this literature and correctly interpreting its findings is having a sound understanding of the measures that are being used and what they do and do not measure. This paper focuses on two prominent measures of intergenerational mobility, the intergenerational elasticity (IGE), and the rank-rank slope, and discusses several key conceptual and measurement issues related to these estimators. The IGE has a fairly long history of use in economics dating back to papers from the 1980s. It is generally viewed as a useful and transparent summary statistic capturing the rate of “regression to the mean”. It can, for example, tell us how many generations (on average) it would take the descendants of a low income family to rise to the mean level of log income. In recent years many notable advances have been made in terms of measurement and issues concerning life-cycle bias (e.g. Jenkins, 1987; Solon, 1992; Mazumder, 2005a; Grawe, 2006; Böhlmark and Lindquist, 2006; Haider and Solon, 2006). 1 As a result of these contributions, most recent US estimates of the IGE in family income are generally around 0.5 or higher. 2 1 Reviews of this literature can be found in Solon (1999) and Black and Devereaux (2011). Solon’s (1992) estimate is 0.483. Hertz (2005) reports an IGE of 0.538. Hertz (2006) finds the IGE to be 0.58. Bratsberg et al (2007) estimate the IGE of family income on earnings to be 0.54. Jäntti et al’s (2006) estimate of the same measure is 0.517. Mitnik et al’s (2015) estimate of the standard IGE is between 0.55 and 0.74. Note that all of these studies (like Chetty et al, 2014) report some variant of the IGE with respect to family income. Of course, many other studies have used a different income concept such as labor market earnings. 2 2 Thus far, no study of intergenerational mobility in the US has yet been conducted that has used very long time averages of family income of parents and has also utilized averages of family income in both generations centered at age 40, where lifecycle bias is minimized.3 This paper fills this void in the literature by using PSID data that meet these requirements. Using up to 15 year averages of income in the parent generation yields estimates of the IGE with respect to family income of sons that are greater than 0.6. I also find that the IGE with respect to the labor income of male household heads is greater than 0.6 and very similar to the estimate found by Mazumder (2005a) using social security earnings data. 4 These results stand in stark contrast with the results in a recent highly influential study by Chetty et al (2014), who use large samples drawn from IRS tax records and produce estimates of the IGE in family income of just 0.344 suggesting significantly greater intergenerational mobility. Furthermore, Chetty et al argue that none of the previous biases identified in the literature on IGE estimation apply to their data. Given the importance of the IGE as one of the key conceptual measures of intergenerational mobility, it is worth revisiting the measurement issues in the context of their sample. This exercise is not only useful for revisiting the specific results of Chetty et al, but also holds more general lessons for other research seeking to exploit administrative data to measure intergenerational mobility. The IRS-based intergenerational sample used by Chetty et al is fundamentally limited in a few key respects that ultimately stems from the fact that the data only begins in 1996. First, children’s income is only measured in 2011 and 2012. This is at a relatively early point in the 3 The closest is Mitnik et al (2015) who use 9-years of parent income and children between the ages of 35 and 38. Chetty et al (2014) suggest that the high estimates in Mazumder (2005a) are solely due to data imputations of fathers’ SSA earnings that are topcoded in some years and are not the result of using longer-time averages of father earnings. Below, I reiterate arguments against that claim that were originally discussed in Mazumder (2005a) but subsequently ignored by Chetty et al 2014 in their Appendix E discussion. I also point to other studies in the literature that are supportive of the findings in Mazumder (2005a). It is notable that this study yields similar estimates to Mazumder (2005a) while requiring no imputations of income. 4 3 life cycle for cohorts born between 1980 and 1982 (ages 29 to 32) and during a period when unemployment was quite high in the US. This age range is one in which we would expect substantial life cycle bias in producing IGE estimates (Haider and Solon, 2006). Moreover, relative to a more ideal data structure, where cohorts of children could be chosen such that they were observed over the 31 years spanning the ages of 25 to 55, Chetty et al are limited to using only 6 percent of the lifecycle. Second, parents’ income is also measured for only a short period (5 years) covering just 16 percent of the lifecycle and at a relatively late period in life. Roughly 25% of observations of fathers’ income in their sample are measured at age 50 or higher. The literature has shown that starting around the age of 50 a substantial share of the variance in income is due to transitory fluctuations. This leads to substantial attenuation of the IGE relative to what would be found if one used lifetime income for the parents (Haider and Solon, 2006; Mazumder, 2005a). Third, recent research has established that administrative data can sometimes lead to worse measurement error than survey data, particularly at the bottom end of the income distribution (e.g. Abowd and Stinson, 2013 and Hokayem et al., 2012, 2015). It is important to make it very clear that the main focus of Chetty et al is not their national estimates of the IGE. Instead, the authors make an important contribution to the literature by producing the first estimates of a different measure of mobility, rank mobility, at a very detailed level of U.S. geography. Notably, they provide evidence of substantial heterogeneity across the U.S. As I discuss below, the biases that affect their national estimates of the IGE likely have little effect on their main conclusions regarding geographic differences. The limitations of the tax data for intergenerational analysis can be sharply contrasted with the PSID sample used in this paper. In the PSID sample, family income is observed in both generations over a vastly larger portion of the lifecycle and the time averages are centered over 4 the prime working years in both generations. I estimate the IGE using this closer to “ideal” sample and then show how the estimates change if I impose the same kinds of data limitations that exist in the IRS data. The results show that the data limitations lead to IGE estimates that are roughly half the size of the estimates with the complete data and similar in magnitude to the estimates of Chetty et al. A very similar pattern of results is also found by Mitnik et al (2015). 5 Chetty et al also find the IGE to be very sensitive to how they choose to impute the income of children who report no family income during 2011 and 2012. However, it is the limited panel dimension of their data and their reliance on administrative data which makes their analysis susceptible to this problem. Had they been able to observe the income of children during later periods of the lifecycle and other sources of income, then such imputation becomes unnecessary. 6 This is important because it is their concern about the robustness of the IGE that led Chetty et al to using rank-based estimators. 7 This contrasts with other studies that have also used rank-based measures to study intergenerational mobility but for conceptual reasons. 8 Given the recent shift in the literature to using rank-based measures, it is useful to distinguish the measurement concerns with the IGE from the conceptual differences between the two estimators. In short, both measures can provide useful insights about different mobility concepts. Since certain questions are best answered by the IGE, researchers should continue to use that estimator as at least one tool in their arsenal. Nevertheless, rank-based estimators are also valuable. In addition to providing information on a different concept of mobility, positional 5 Mitnik et al (2015) use IRS data that begins in 1987 enabling children to be observed into their late 30s and for parent income to be measured over 9 years. Not only do Mitnik et al also produce similar sized estimates to the PSID results when using a comparable methodology (0.55 to 0.74), but they also show that they can match the Chetty et al estimates if they restrict their analysis to 29-32 year olds and use five year averages of parent income. 6 Mitnik et al (2015) introduce a new approach to estimating the IGE that enables them to overcome this sensitivity to years of missing income when using a small window to measure child income. I discuss this in section 3. 7 Dahl and Deliere (2008) also shift to rank based measures based on concerns regarding the robustness of the IGE but their concerns revolve around a different measurement issue than Chetty et al which I discuss in section 3. 8 See Bhattacharya and Mazumder (2011), Corak et al (2014), Mazumder (2014), Davis and Mazumder (2015) and Bratberg et al, 2015. 5 mobility, rank-based measures are also useful for distinguishing upward versus downward movements, making subgroup comparisons, and for identifying nonlinearities. I would argue that even if Chetty et al had found the IGE to be perfectly robust in their tax data, it would still be preferable to use rank-mobility measures to understand geographic differences. This is because an IGE estimated in, say, Charlotte, North Carolina would only be informative about the rate of regression to the mean income in Charlotte. If ranks are fixed to the national distribution, then rank mobility measures enable a more meaningful comparison across cities. Finally, I use the PSID to estimate the rank-rank slope. The estimates (0.4 or higher) are only moderately larger than what is found with the IRS data (0.341) or what is found with the PSID data when imposing the tax data limitations. Although the rank-rank slope may be more robust to the data limitations of the IRS sample than the IGE, it is still not perfect and suggests that the rate of intergenerational mobility even by rank-based measures may be overstated by the tax data. This is broadly in line with findings for Sweden (Nybom and Stuhler, 2015). In the future as the panel length of US tax data increases, these biases will recede in importance. However, it is uncertain whether researchers will be able to obtain tax data in future decades. I conclude that researchers should continue to use the IGE if that is the conceptual parameter of interest. Even when the ideal data is not available, researchers can still attempt to assess the extent of the bias based on prior research. The rest of the paper proceeds as follows. Section 2 describes conceptual differences between the IGE and the rank-rank slope. Section 3 discusses measurement issues with the IGE and outlines an “ideal” dataset. It then compares this ideal dataset with Chetty et al’s IRS-based sample and samples that can be constructed with publicly available PSID data. Section 4 describes the PSID data. Section 5 presents the main results and Section 6 concludes. 6 II. Conceptual Issues The concept of regression to the mean over generations has a long and notable tradition going back to the Victorian era social scientist Sir Francis Galton who studied, among other things, the rate of regression to the mean in height between parents and children. Modern social scientists have continued to find this concept insightful as a way of describing the rate of intergenerational persistence in a particular outcome and to infer the rate of mobility as the flip side of persistence. In particular, economists have focused on the intergenerational elasticity (IGE). The IGE is the estimate of β obtained from the following regression: (1) y1i = α + βy0i + εi where y1i is the log income of the child’s generation and y0i is the log of income in the parents’ generation. 9 The estimate of β provides a measure of intergenerational persistence and 1 - β can be used as a measure of mobility. For simplicity, if we assume that the intergenerational relationship actually follows a simple autoregressive process then one can use β to extrapolate how long it would take for gaps in log income between families to recede. 10 For example, consider a family whose log annual income is around 9.8 ($18,000). We might be interested in knowing roughly how many generations it would take (on average) for the descendants of this family’s log income to be within 0.05 of the national average log income of 11.2 ($73,000). If for example, the IGE is around 0.60 as claimed by Mazumder (2005a) then it would take 7 generations (175 years). On the other hand if the IGE is around 0.34 as claimed by Chetty et al Often the regression will include age controls but few other covariates since β is not given a causal interpretation but rather reflects all factors correlated with parent income 10 Recent research has cast doubt on the simple AR(1) model arguing that there may be independent effects emanating from prior generations such as grandparents and great-grandparents (Lindahl et al; 2014). Nevertheless, the AR(1) assumption provides a useful first approximation and conveys the general point about why the magnitude of the estimates might matter. 9 7 (2014) then it would take just 4 generations. Clearly, the two estimates have profoundly different implications on the rate of intergenerational mobility by this metric. If the rate of regression to the mean is, in fact, what we are interested in knowing, then the IGE is what we ought to estimate. For example, some papers find that the IGE is particularly useful for calibrating structural models of interest (e.g. DeNardi and Yang, 2015, Lee and Seshadri, 2005) The concept of regression to the mean is also widely used in other aspects of economics such as the macroeconomic literature on differences in per-capita income across countries (e.g. Barro and Sala-i-Martin, 1992). The rank–rank slope on the other hand is about a different concept of mobility, namely positional mobility. For example, a rank-rank slope of 0.4 suggests that the expected difference in ranks between the adult children of two different families would be about 4 percentiles if the difference in ranks among their parents was 10 percentiles. How are the two measures related? Chetty et al (2014) point out that that the rank-rank slope is very closely related to the intergenerational correlation (IGC) in log income. They and many others have also shown that the IGE is equal to the IGC times the ratio of the standard deviation of log income in the child’s generation to the standard deviation of log income in the parents’ generation: 𝜎𝜎 𝐼𝐼𝐼𝐼𝐼𝐼 = 𝐼𝐼𝐼𝐼𝐼𝐼 𝜎𝜎𝑦𝑦1 (2) 𝑦𝑦0 This relationship is sometimes taken to imply that a rise in inequality would lead the IGE to rise but not affect the IGC and that therefore, the IGC may be a preferred measure that avoids a “mechanical” effect of inequality. By extension one might also prefer the rank-rank slope if one accepts this argument. Several comments are worth making here. First, in reality the parameters are all jointly determined by various economic forces. In the absence of a structural model one cannot meaningfully talk about holding “inequality” fixed. For example, a change in 8 β might cause inequality to rise, rather than the reverse, or both might be altered by some third force such as rising returns to skill. The mathematical relationship shown in (2) does not substitute for a behavioral relationship and so we cannot truly isolate forces driving inequality from the IGE. Second, even if it was the case that the IGC or rank-rank slope was a measure that was “independent of inequality”, that doesn’t mean that society shouldn’t continue to be interested in the rate of regression to the mean. It may well be the case that it is precisely because of the rise in inequality that societies are increasingly concerned about intergenerational persistence and so incorporating the effects of inequality may actually be critical to understanding the rates of mobility that policy makers want to address. Mitnik et al (2015) for example, argue in favor of the IGE precisely because it incorporates distributional changes. In addition to providing useful information about positional mobility, the rank-rank slope has other attractive features. Perhaps its’ most useful advantage over the IGE is that it can be used to measure mobility differences across subgroups of the population with respect to the national distribution. This is because the IGE estimated within groups is only informative about persistence or mobility with respect to the group specific mean whereas the rank-rank slope can be estimated based on ranks calculated based on the national distribution. Chetty et al (2014) were able to use this to characterize mobility for the first time at an incredibly fine geographic level. Mazumder (2014) used other “directional” rank mobility measures to compare differences in intergenerational mobility between blacks and whites in the U.S. However, for characterizing intergenerational mobility at the national level both the IGE and the rank-rank slope are suitable depending on which concept of mobility a researcher is interested in studying. III. Measurement Issues and the Ideal Intergenerational Sample Measurement Issues 9 The literature on intergenerational mobility has highlighted two key measurement concerns that I briefly review. The first issue is attenuation bias that arises from measurement error or transitory fluctuations in parent income. In an ideal setting the measures of y1 and y0 in equation (1) would be measures of lifetime or permanent income, but in most datasets we only have short snapshots of income that can contain noise and attenuate estimates of the IGE. Solon (1992) showed that using a single year of income as a proxy for lifetime income of fathers can lead to considerable bias relative to using a 5 year average of income. Using the PSID, Solon concluded that the IGE in annual labor market earnings was 0.4 “or higher”. Mazumder (2005a) used the SIPP matched to social security earnings records and showed that using even a 5-year average can lead to considerable bias and estimated the IGE in labor market earnings to be around 0.6 when using longer time averages of fathers earnings (up to 16 years). Mazumder argues that the key reason that a 5-year average is insufficient is that the transitory variance in earnings tends to be highly persistent and appeals to the findings of U.S. studies of earnings dynamics that support this point. Using simulations based on parameters from these other studies, Mazumder shows that the attenuation bias from using a 5-year average in the data is close to what one would expect to find based on the simulations. In a separate paper that is less well known, Mazumder (2005b) showed that if one uses short term averages in the PSID and uses a Hetereoscedastic Errors in Variables (HEIV) estimator that adjusts for the amount of measurement error or transitory variance contained in each observation, then that the PSID adjusted estimate of the IGE is also around 0.6. This latter paper is a useful complement because unlike the social security earnings data used by Mazumder (2005a) the PSID data is not topcoded and doesn’t require imputations. Chetty et al (2014) has contended that the larger estimates of the IGE in Mazumder (2005a) were 10 due to the nature of the imputation process rather than due to larger time averages of fathers’ earnings. Specifically, in cases where earnings were above the social security taxable maximum they were imputed by using the mean earnings level by race and education level from other data sources. Mazumder acknowledges that this moves a step in the direction towards “instrumenting” for fathers earnings based on demographic characteristics but argues that it is not obvious that this imparts an upward bias and may well lead to a downward bias. 11 Mazumder also shows that when using up to 7 year averages and dropping fathers who are ever topcoded, which is about half of the sample, that the resulting IGE of 0.439 (N=1144) is not very different from the IGE of 0.472 (N=2240) for the full sample. Mazumder further argues that this robustness check of dropping fathers who are ever topcoded, may impart a downward bias due to a potential selection effect of eliminating father son-pairs whose IGE may be higher because they are selected from the top of the income distribution. 12 In any event, a number of other studies in addition to Mazumder (2005b), that also do not require imputed data, and in some cases use administrative tax data, demonstrate that longer time averages lead to substantially higher IGE estimates. These studies include: Nilsen et al (2012); Gregg et al (2013); Mazumder and Acosta, 2014; and Mitnick et al, 2015. 11 See footnote 13 in Mazumder (2005a). That footnote explains why in the presence of lifecycle bias, an IV estimate of the IGE for sons who are younger than 40 and fathers who are older than 40 leads to downward bias. The mean age of sons in Mazumder (2005a) is 32 and the mean age of fathers in 1984 is 47. Chetty et al (2014) ignore this point when they discuss Mazumder (2005a) in their Appendix E. 12 Mitnik et al (2015), for example, find that the IGE is higher at the upper half of the income distribution. Chetty et al (2014) in their Appendix E do not address this selection argument in their discussion of Mazumder’s Table 6 and imply that the results of the robustness check are explained by an upward bias due to IV. Mazumder (2005a) points out that if he uses longer time averages than 7 years and also drops fathers who are ever topcoded that this results in dramatically smaller samples that are likely to be highly selected and are likely to be uninformative about the effects of topcoding. One possible way to gauge the potential upward or downward bias of using imputing topcoded values would be to run simulations with fake data where one can use a range of parameter values to assess the magnitude of the bias. 11 The second critical measurement concern in the literature concerns lifecycle bias best encapsulated by Haider and Solon (2006). One aspect of this critique concerns the effects of measuring children’s income when they are too young. Children who end up having high lifetime income often have steeper income trajectories than children who have lower lifetime income. Therefore if income is measured at too young an age it can lead to an attenuated estimate of the IGE in lifetime income. Haider and Solon show that this bias can be considerable and is minimized when income is measured at around age 40. A related issue is that transitory fluctuations are not constant over the lifecycle but instead follow a u-shaped pattern over the lifecycle (Baker and Solon, 2003; Mazumder, 2005a). This implies that measuring parents’ income when they are either too young or (especially) when they are too old can also attenuate estimates of the IGE. While there are econometric approaches one can use to correct for lifecycle bias, one simple approach is to simply center the time averages of both children’s and parents’ income around the age of 40. Using this approach with the PSID, Mazumder and Acosta estimate the IGE to be around 0.6. Mitnik et al (2015) also use this approach with IRS data covering older cohorts who are observed as late as age 38 and find that both sources of bias are quantitatively important. Further, Nilsen et al (2012), Gregg et al (2014) and Nybom and Stuhler, (2015) using data from other countries, show that both time averaging and life-cycle bias play a role in attenuating IGE coefficients. Importantly, these studies find that these biases matter even when using administrative data. 13 Comparisons of Intergenerational Samples To better understand the limitations with currently available intergenerational samples in the US with respect to these measurement issues, it is useful to think about what an ideal sample 13 Chetty et al speculate that perhaps they find that time averaging and life cycle bias don’t matter because of their use of administrative data which they suspect to be less error prone than survey data. 12 would look like. In an ideal setting we would want to construct an intergenerational sample where income is measured for both generations throughout the entire working life cycle, say between the ages of 25 and 55. 14 For example, suppose our data ends in 2012 (as in Chetty et al); then for full lifecycle coverage for the children’s generation we would want cohorts of children who were born in 1957 or earlier. For the 1957 cohort we would measure their income between 1982 and 2012. For the 1956 cohort we would measure income between 1981 and 2011 and so on. Suppose that for the parents’ generation, the mean age at the time the child is born is 25. Then for the 1957 cohort we would collect income data from 1957 to 1987, from 1956 to 1986 for the parents of the 1956 birth cohort and so on. With such a dataset in hand we would be confident that we would have measures of lifetime income that are largely error-free and would also be free of lifecycle bias. Unfortunately, for most countries, including the US, it is difficult to construct an intergenerational dataset with income data going back to the 1950s. 15 Still, we can come somewhat close to this ideal sample with publicly available survey data in the Panel Study of Income Dynamics (PSID). 16 The PSID began in 1968 and started collecting income data beginning in 1967 for a nationally representative sample of about 5000 families. The 1957 cohort would have been 11 years old at the time the PSID began so this cohort along with those born as early as 1951 would have been under the age of 18 at the beginning of the survey. The approach I take in this paper is to construct time averages of both parent and child income 14 The precise end points are debatable but for measurement purposes one might want to ensure that most sample members have finished schooling and that most sample members have not yet retired. In theory, however, it may be better to consider earnings even at young ages when adolescents may have chosen to forego earnings for human capital accumulation that pays off later in life. In any case, the main point of the argument in this section would still hold if one used a much broader age range. 15 The SIPP-SER data used by Mazumder (2005) and Dahl and Deliere (2008) meets some but not all of these requirements. 16 The code used to construct the main estimates in this paper will be made available to researchers either through the author’s website or through personal communication. 13 centered around the age of 40 in order to minimize life-cycle bias. For parents, these time averages include income obtained between the ages of 25 and 55 and for children these averages include income obtained between the ages of 35 and 45. Relative to the ideal sample, the PSID sample is close in several regards. Since it covers the 1967 to 2010 period it is able to utilize large windows of the lifecycle for both generations. For example, for the 16 cohorts born between 1951 and 1965, in principle, income can be measured in all years that cover the age range between 35 and 45. For the cohorts born between 1967 and 1975, their parents’ income can also be measured through the ages of 25 and 55. Of course, attrition from the survey diminishes the size of the actual samples with observations in all of these years but at least the potential for such coverage is there. 17 Now let us contrast this with the limitations faced by Chetty et al (2014) in their analysis of currently available IRS data. First the tax data is currently only digitized going back to 1996, which is far from what the ideal dataset would require (1957), or even what is available in the PSID (1967). Therefore, there is no birth cohort for whom the income of parents can be measured for the entire 31 year time span between the ages of 25 and 55. Furthermore, the authors chose to limit the analysis to just a 5-year average between 1996 and 2000. A possible explanation for this choice is that lengthening their time averages further would have necessitated measuring income when parents were at an older than ideal age. I will return to this point later when I explain why their sensitivity analysis is flawed. The mean age of fathers in their sample in 1996 is reported to be 43.5 with a standard deviation of 6.3 years. This implies that over the 5 years from 1996 through 2000, roughly 24 percent of the father-year observations 17 As discussed later, I use survey weights to address concerns about attrition. 14 used in constructing the average would be when fathers are over the age of 50. 18 This is an age at which the transitory variance in income is quite high (Mazumder, 2005a). They also report that prior to 1999 they record the income of non-filers to be zero. Therefore for about 3 percent of observations in three of the five years used in their average they impute zeroes to the missing observations. 19 For the children in the sample, the data limitations are even more severe. Chetty et al use cohorts born between 1980 and 1982 and measure their income in 2011 and 2012 when they are between the ages of 29 and 32. For this age range, simulations from Haider and Solon (2006) suggest that there would be around a 20 percent bias in the estimated IGE compared to having the full lifecycle. A further complication is that their measures are taken in 2011 and 2012 when unemployment was relatively high and labor force participation quite low. They report that they drop about 17 percent of observations from the poorest families due to their having zero income over those 2 years. If their sample had covered 29 to 32 year olds in other time periods spanning other periods of the business cycle, then using such a short window would have been somewhat less of a concern. Finally, there is a concern about whether administrative income data adequately captures true income, particularly at the low and the high ends of the income distribution. For example, at the lower end of the distribution, tax data could miss forms of income that go unreported to the IRS. At the higher end, tax avoidance behavior could lead to an under-reporting of income. Hokayem et al (2015) find that administrative tax data can do a worse job than survey data in 18 This example assumes the data is normally distributed. In 2000, more than a third of the observations would be when fathers are over the age of 50. 19 See footnote 14 of Chetty et al. (2014). They show that measuring income over 1999 to 2003 has no effect on their rank mobility estimates but they do not show how the IGE estimates change. Measuring income from 1999 to 2003 potentially worsens the attenuation bias in the IGE resulting from measuring fathers at late ages. 15 measuring poverty. Abowd and Stinson (2013) argue that it is preferable to treat both survey data and administrative data as containing error. I also discuss below how a preferred concept of family income that includes all resources available for consumption, including transfers and income of other family members, would render tax data inadequate. It is useful to visualize just how different the data structure of the Chetty et al sample is from an ideal intergenerational sample. This is shown in Figure 1. For each of three samples there are two columns of 31 cells representing the ages from 25 to 55 in each generation and we assume that just one parent’s income can be measured. The degree of coverage over the life course is represented by the extent to which the cells are colored. Panel A shows that if we measured income in both generations using data spanning the entire life course for two generations then all the cells in both generations would be colored in. Panel B contrasts this with a typical parent-child observation in the Chetty et al sample. 20 This makes it clear just how small a portion of the ideal lifecycle is covered. Just 6 percent of the child’s lifecycle and just 16 percent of the parent’s lifecycle would be covered. Panel C contrasts this with an example of a result that will be produced with the PSID in the current study. There are many cohorts for whom both child and parent income can be measured over several years centered around the age of 40 when lifecycle bias is minimized. The figure presents an example of a 7-year average of child income and a 15-year average of parent income. Such a sample would cover 23 percent of the child’s lifecycle and 48 percent of the parent’s lifecycle. To their credit, Chetty et al (2014) attempt to conduct some sensitivity checks to assess these issues but their data, which only begins in 1996, are not well suited to doing effective 20 This example takes a child born in 1981 whose income is observed at age 30 and 31 during the years 2011 and 2012. I assume that the father was 29 years old when the child was born so that the father’s income is measured between the ages of 44 and 48 during the years 1996 to 2000. This example closely tracks the mean ages of the sample as reported by Chetty et al (2014). 16 robustness checks for the IGE measure. Below I will replicate their sensitivity checks with the PSID data and show how the current IRS data limitations lead them to reach incorrect conclusions regarding the sensitivity of their IGE estimates to these measurement problems. Estimating the IGE when children have zero income Chetty et al (2014) also argue that the IGE estimator is not robust to imputing years of zero family income observed for individuals in the child generation. 21 They obtain an estimate of 0.344 when they restrict the sample to those children with positive income in 2011 and 2012. If they impute $1000 of income to these individuals then their IGE estimate rises to 0.413. If they assign $1 then their IGE estimate rises to 0.618. There are three points worth making here. First, the issue of having to deal with missing values is largely a consequence of the poor lifecycle coverage of their sample. To see why this is the case, imagine a hypothetical researcher in the year 2035 that attempts an intergenerational analysis for the 1980 birth cohort using the tax data. In 2035 one would have complete information on family income throughout the ages of 25 to 55 and would not have to worry that some of these individuals reported no income in 2 of the 31 years of the lifecycle, during a period when unemployment was relatively high. There would be as many as 29 other years of income data available to calculate lifetime income. In fact, based on the prior literature, a researcher could probably obtain a fairly unbiased estimate of the IGE for the 1980 birth cohort by the early 2020s if they could obtain even a few years of income around the age of 40. In the PSID one can track cohorts born as far back as the 1950s who may be observed over many years, at many ages, and at different stages of the business cycle. Second, recent work by Mitnik et al (2015) point to an alternative approach for estimating the IGE that is not sensitive to situations in which researchers may have only a short 21 17 span of data on children’s income and encounter cases of zero income. Specifically, they estimate the elasticity of the expected income of children rather than the elasticity of the geometric mean of income, which the literature has traditionally focused on. They argue that this is the estimand that researchers should actually be interested in estimating. 22 They present striking evidence that unlike the traditional IGE estimator, their alternative estimator of the IGE is relatively immune to the treatment of missing income of children when income is measured over only a short window of the lifecycle. However, it is unclear, and ultimately an empirical question as to whether the Mitnik et al approach to estimating the IGE would yield substantially different results from the traditional approach if one had access to the entire lifetime income stream of children. In such a situation there would likely be very few cases of zeroes. This would be a fruitful avenue for future research to explore. A third remark relates to the concept of family income one wants to use. Economists (e.g. Mulligan, 1997) have sometimes argued that an ideal measure of intergenerational mobility would seek to measure lifetime consumption in both generations since consumption is perhaps the measure closest to utility which is what economists like to focus on. In this case ideally we would like to measure total family resources which includes income obtained from transfers and from other family members. This is an example where survey data that has access to transfer income would be preferable to tax data that may not. Including transfers may not only be a preferred measure but may also help alleviate the problem of observing zero earnings or zero income as is common in administrative data. It is also not obvious why the preferred measure of family income would be one that only includes labor market earnings, transfers and capital 22 Chetty et al (2014) argue that the preferred estimator of Mitnik et al (2015) can be interpreted as a “dollarweighted” estimator of the IGE and the traditional IGE can be viewed as a “person-weighted” estimator and suggest that each answers a different question. 18 income that happen to be reported on tax forms. This may help explain why Chetty et al estimate an IGE of 0.452 when they limit their sample to individuals between the 10th and 90th percentiles. The lack of coverage of all forms of transfer income may be less problematic for this range since it excludes the bottom of the income distribution. Estimating the IGE when parents have zero income It is worth pointing out that the prior discussion is in many ways very distinct from the problem of having a measure of zero income for parents. Chetty et al (2014) and Mitnik et al both cite Dahl and Deliere (2008) in their discussions of the robustness of the IGE but Dahl and Deliere actually confront an entirely different issue. Dahl and Deliere utilize social security earnings data. For the years 1951 through 1983, they cannot distinguish between years of zero earnings due to non-coverage in the SSA sector from “true” zeroes due to non-employment. When they construct measures of parent average earnings over the ages of 20 to 55 and include all years of earnings they obtain estimates of the intergenerational elasticity of only around 0.3 for men. However, their estimates may be including many years when actual earnings are positive but are erroneously treated as zero because fathers were working in the non-covered sector. Since this measurement error is on the right hand side it can severely attenuate the estimate of the IGE. They attempt to correct for this in some specifications by restricting the sample to parents who were not in the armed forces or self-employed and who therefore would likely be in the covered sector. But, importantly, the class of worker variable is only observed in one year, 1984, which is at a relatively late point in the lifecycle for most of their sample of fathers. Therefore, their long-term averages still include many years of zero earnings for workers who were actually in the non-covered sector in the 1950s, 1960s or 1970s but who had shifted to the covered sector 19 by 1984. Not surprisingly, using the class of worker status observed in 1984 to restrict the sample still yields very low estimates of the IGE. However, when they restrict the number of years of zero earnings in other very sensible ways to more directly address the issue, they obtain estimates of around 0.5 to 0.6. For example, when they use the log of average earnings beginning with the first 5 consecutive years of positive earnings up to age 55 they obtain an estimate of 0.498. A clear advantage of the IRS tax data compared to the SSA data is that there is no requirement of working in sectors covered by SSA. However, there may be concerns related to whether individuals file their taxes and whether the IRS samples contain those who don’t file. As mentioned earlier, Chetty et al assign zero income to parents who are in their sample but did not file taxes in years prior to 1999. This can also lead to attenuation bias in estimating the IGE. IV. PSID Data I restrict the analysis to father-son pairs as identified by the PSID’s Family Identification Mapping System (FIMS) and use all years of available family income between the ages of 25 and 55 between the years of 1967 and 2010. 23 For the main analysis I consider a measure of family income that excludes transfers and excludes income from household members that are not the head of household or the spouse. This provides a measure of family income that is probably most comparable to the concept used by Chetty et al (2014). In addition, I also constructed a measure of family income that also includes transfers received by the household head or spouse, but these results are not presented. 24 Finally, I construct a measure that uses only the labor income of the father and son to be more comparable to papers that emphasize the IGE in labor 23 The focus on sons contrasts with Chetty et al (2014) who pool sons and daughters and Mitnik et al (2015) who mainly produce separate estimates by gender. 24 These results were broadly similar to the baseline findings using the narrower measure of family income. 20 market income (e.g. Solon, 1992; Mazumder, 2005). Labor income is not simply earnings from an employer but also incorporates self-employment. Observations marked as being generated by a ‘major’ imputation are set to missing. Yearly income observations are deflated to real terms using the CPI. In the PSID the household head is recorded as having zero labor income if their income was actually zero or if their labor income is missing, so one cannot cleanly distinguish true zeroes with labor income. All of the main analysis only uses years of non-zero income when constructing time averages of income. When using family income, instances of reports of zero income are relatively rare so the results are virtually immune to the inclusion of zeroes. Therefore the concerns about the sensitivity of results around how to handle years of zero income is effectively a non-issue when using family income. The main analysis only uses the nationally representative portion of the PSID and includes survey weights to account for attrition. All of the analysis was also done including the SEO oversample of poorer households and includes survey weights. While the samples with the SEO are larger and offer more precise estimates, there is some concern about the sampling methodology (Lee and Solon, 2009). Finally all estimates are clustered on fathers. The approach to estimation in this study is slightly different than in most previous PSID studies of intergenerational mobility. Rather than relying on any one fixed length time average for each generation and relying on parametric assumptions to deal with lifecycle bias (e.g. Lee and Solon, 2009), instead I estimate an entire matrix of IGE’s for many combinations of lengths of time averages that are all centered around age 40. I will present the full matrix of estimates along with weighted averages across entire rows and columns representing the effects of a particular length of the time average for a given generation. For example, rather than simply comparing the IGE from using a ten-year average of fathers’ income to using a five year average 21 of fathers’ income for one particular time average of sons’ income, I can show how the estimates are affected for every time average of sons’ income. V. Results IGE Estimates Table 1 shows the estimates of the IGE in family income that is conceptually similar to that used by Chetty et al (2014). The first entry of the table at the upper left shows the estimate if we use just one year of family income in the parent generation and one year of family income for the sons when they are closest to age 40 and also are within the age-range constraints described earlier. This estimate of the IGE is 0.414 with a standard error of 0.075 and utilizes a sample of 1358. One point immediately worth noting is that this estimate which uses just a single year of family income around the age 40 is higher than the 0.344 found by Chetty et al (2014). Moving across the row, the estimates gradually include more years of income between the ages of 35 and 45 for the sons. At the same time the sample size gradually diminishes as an increasingly fewer number of sons have will income available for a higher length of required years. For the most part the estimates don’t change much and most are in the range of 0.35 and 0.42. At the end of the row I display the weighted average across the columns, where the estimates are weighted by the sample size. For the first row the weighted average is 0.381. Moving down the rows for a given column, the estimates gradually increase the time average used to measure family income in the parent generation and as a consequence also reduces the sample size. For example, if we move down the first column and continue to just use the sons’ income in one year measured closet to age 40 and now increase the time average of parent income to 2 years, the estimate rises to 0.439 as the sample falls to 1317. Using a five year average raises the estimate to 0.530 (N=1175). Increasing the time average to 10 years 22 increases the estimate to 0.580 (N=895). Using a 15 year average raises the estimate further to 0.680 (N=533). The weighted average for each row is displayed in the last column and the weighted average for each column is displayed in the bottom row. A few points are worth making. Since expanding the time average in either dimension reduces the sample size it risks making the sample less representative. The implications on the estimates, however, are quite different for whether we increase the time average for the sons’ generation or for the fathers’. For the parent generation, increasing the time average tends to raise estimates. This is consistent with a story in which larger time averages reduce attenuation bias stemming from mis-measurement of parent income (Solon, 1992; Mazumder, 2005). This also accords with standard econometric theory concerning mis-measurement of the right hand side variable. On the other hand, econometric theory posits that mis-measurement in the dependent variable typically should not cause attenuation bias. Indeed, increasing the time average of sons’ family income has little effect. But crucially, this is because we have centered the time average of family income in each generation so that the lifecycle bias which induces “non-classical” measurement error in the dependent variable (Haider and Solon, 2006) may already be accounted for. By this reasoning one might consider the estimates in the first column to be the most useful since they allow one to see how a reduction in measurement error in parent income affects the estimates while simultaneously minimizing life cycle bias and keeping the sample as large as possible. A more conservative view would be to use the weighted average in the final column that takes into account the possible effects of incorporating more years of data on sons’ income while also giving greater weight to estimates with larger samples. Figure 2 shows the pattern of estimates from the two approaches as I gradually use longer time averages. 23 With either approach, time averages of 10 to 15 years yield estimates of the IGE in family income that are consistently greater than 0.6. Appendix Table 1 and Appendix Figure 1 show the analogous set of estimates using larger samples that include the SEO oversample. The key idea of the study is to see how these IGE estimates would compare to what one would obtain by imposing the current data limitations of the IRS sample. To do this, one can use the second column and fifth row of Table 1 as a baseline estimate. That estimate of 0.493 uses a two year average of family income of sons centered around age 40 and a five year average of parent income centered around age 40. If I now impose a sample restriction such that I use a two year average of sons taken over the ages of 29-32 and use a five year average of parent income centered around the age of 46 then the estimate I obtain is 0.282 (s.e. = 0.099). This is only 57 percent of the value when using similar time averages centered at age 40. Furthermore, if the true IGE is actually 0.7, then it is only 40 percent of the true parameter. If I include the SEO subsample then the estimate rises a bit to 0.325 (s.e. = 0.081). For that sample, the data limitations yield estimates that are 62 percent of the comparable estimates when using time averages centered at age 40. Neither of the two estimates are statistically different from the Chetty et al estimate of 0.344. This suggests that it is the data limitations in the tax data that lead Chetty et al to produce estimates that are vastly lower than what has been reported in most of the previous literature. Interestingly, Mitnik et al (2015) report a strikingly similar pattern of results. Their baseline estimates use children’s income measured between the ages of 35 and 38 and 9 year averages of parent income. Using a non-parametric approach on a sample that includes all children, their estimates of the traditional IGE range from 0.55 to 0.74 depending on how they 24 impute the income of children who report no income. 25 When they move from this baseline sample to one that mimics the sample used by Chetty et al (children between the ages of 29 and 32 and using a 5 year average of parent income), their estimate falls to 0.28. If they instead use their preferred IGE estimator, then their main estimate is 0.50 and their estimate when mimicking the sample used by Chetty et al is 0.37. Table 2 shows a set of IGE estimates that only use the labor income of fathers and sons. On the whole, the estimates in Table 2 are fairly similar to those in Table 1 as is shown in Figure 3 which plots the weighted average across the columns. For example, when using a 12-year average of fathers’ income, the IGE when using labor income is 0.611 and when using family income the estimate is 0.612. These estimates are broadly similar and slightly higher than those found by Mazumder (2005a) who used the labor market earnings of fathers and sons from social security earnings data. Mazumder (2005a) relied on several data imputation approaches to deal with issues related to social security coverage and topcoding. However, with the PSID, none of these kinds of imputations are necessary. These findings, along with similar results in Mazumder (2005b), Mazumder and Acosta (2014) and Mitnik et al (2015) which also do not require imputations, suggest that the results of Mazumder (2005a) are likely not due to the use of imputations as argued by Chetty et al (2014) but instead are due to the longer time averages available in the SSA data and the PSID. This also suggests that Mazumder (2005a) may have been correct in arguing that the use of imputations may not have imparted an upward bias. 26 Robustness Checks 25 26 See their Table 11. Sees section 3 for a more detailed discussion of this issue. 25 A drawback of the PSID data is that there can be substantial attrition. One may be concerned that the samples that use longer time averages of parent income could be very different from the ones that use shorter time averages. Perhaps, it is the case that the higher estimates that I attribute to using longer time averages in Table 1 are instead due to a change in the composition of families. To address this I conduct two robustness exercises. First, I use a set of fixed samples to show how IGE estimates change as I increase the time average of parent income while holding the composition of families constant. To narrow the focus of the exercise, I consider the case of using 1 available year of income for sons when they are closest to the age of 40. 27 I then consider, for example, the 1063 families where I have 7 years of available family income of fathers and see how the estimates as I gradually increase the time average of parent income from 1 to 7 years. This is shown in column 3 of Table 3. If I use 1 year of parent income the IGE is estimated to be 0.358. If I use a 3-year average the estimate rises to 0.446. If I use a 5-year average the IGE rises further to 0.504 and rises to 0.529 when averaging all 7 years. In column 4, I show how the estimates change for the 895 families with 10 years of income and in column 5 I present the pattern of estimates for the 533 families with 15 years of income. Columns 1 and 2 consider the effects of time averaging for smaller time averages of 3 and 5 years where the samples are even larger. In nearly all cases, the estimates rise monotonically as more years are used to increase the time average. Mitnik et al (2015) present a similar set of exercises using their IRS samples in their Appendix and show a similar pattern when they increase time averages of parent income up to 9 years. This is comforting because one clear advantage of administrative tax data is that attrition from a survey is not a concern. 27 These are the samples that are in column 1 of Table 1. 26 A second exercise directly examines the characteristics of families in which longer time averages of parent income are available. I consider 7 characteristics of fathers: income, age; education; percent black, percent white; percent married and percent ever divorced. 28 As before I consider how these characteristics differ for the samples presented in column 1 of Table 1. The results are shown in Appendix Table 2. The table shows for example, that the mean education level of fathers in the sample of 533 families with 15 years of parent income is 13.0. This compares to a mean of 12.9 years for fathers with 5 years of income. The lower panel of the table shows that the difference is not statistically significant (p-value = 0.50). While the families with longer time averages may be slightly more educated they are also more likely to be black and more likely to be divorced, suggesting some evidence of negative selection. Overall, there is no clear pattern of selection with respect to socioeconomic status. If one compares the samples with 10 year averages to those with 1 or 5 years, there are no statistically significant or economically meaningful differences in father characteristics. The fact that the estimates of the IGE are already well above 0.5 even when using 10-year averages suggests that the main points of the paper likely hold. In summary, there are no especially striking patterns that suggest that the longer time averages are due to changing characteristics of parents. Despite these checks I would still be somewhat cautious in arguing that the considerably smaller samples, with say 11 to 15 years of parent income, do not suffer from any concerns related to selection. One concern is that if the attenuation bias with using short-term averages is truly due to measurement error and serial correlation in transitory fluctuations as argued by Mazumder (2005a), then one would not expect the IGE to increase nearly linearly with the length 28 I also consider mother’s education. 27 of the time average as Figure 1 shows, but instead, would exhibit a more concave pattern as the simulation results in Mazumder (2005a) depict. This is one argument in favor of using administrative data where attrition is typically not an issue. Although the currently available US tax data does not yet have a long enough panel length to resolve this issue, future studies using administrative data in the US and other countries should continue to shed light on the nature of the earnings process and what it might imply for IGE estimates using longer-time averages. Sensitivity Checks in Chetty et al (2014) Chetty et al (2014) argue that their national estimates of the IGE are unaffected by the age at which children’s income is measured. They also argue that their estimates are unaffected by the length of the time average used to measure parent income. They perform sensitivity checks to demonstrate this empirically and present the results visually in figures. In this section I describe why those sensitivity checks are flawed and show how one can demonstrate this using the PSID. In short, their sensitivity checks introduce new attenuation bias from using parent income at older ages. This bias appears to fully offset the reductions in attenuation bias that would otherwise have been apparent when using older children or when extending the time average of parent income. They first discuss the sensitivity of the IGE to the age at which child income is measured, Chetty et al claim that while there is some lifecycle bias early in the career that this stabilizes once children have reached the age of around 30. They conduct an empirical exercise that is shown in their Appendix Figure IIA. They implement this sensitivity check by using an additional tax dataset that includes much smaller intergenerational samples from the Statistics of Income (SOI). With the SOI data they can examine the IGE between parents and children for earlier birth cohorts going back to 1971. However, they continue to use family income in 2011 28 and 2012 for children and in 1996 to 2000 for the parents. This implies, for example, that when they examine the 1971 cohort to measure the IGE for 41 year olds they are actually using parent income that is measured when the child was between the ages of 25 to 29 and unlikely to be living at home. Perhaps more importantly, this also requires that they use the income of fathers when they are likely to be especially old. For example, the income of a father who was 28 when his child was born in 1971 would be 53 to 57 years old when his income was measured in 1996 to 2000. Using parent income at such late ages when transitory fluctuations are a substantial part of earnings variation can lead to substantial attenuation bias that could offset the reduction in lifecycle bias from measuring child income at age 40 (Mazumder 2005a). Overall it could make it appear as though there is no lifecycle bias when in fact it may actually be substantial. With a long-running panel dataset like the PSID one can replicate this sensitivity check but can also show how the results differ if one simultaneously keeps the age at which father’s income is measured, constant. To implement this exercise, I first replicate the findings in Chetty et al by gradually increasing the age at which sons’ income is measured from 22 to 41 while simultaneously increasing the parent age range at which the five year average of parent income is measured to match the analogous age range implied by the tax data. 29 I then fix this problem by using a 5 year time average of parent income that is always centered at the age of 40 while simultaneously raising the age of sons when their income is measured from 22 to 41. Figure 4 shows the results of this exercise. The red line replicates the flawed sensitivity check. Lifecycle bias appears to level off around the age of 30 and may even appear to decline slightly in the late 30s. The green line demonstrates that this sensitivity check is flawed once 29 To fix ideas, for those sons who are aged 32, one would use the income of fathers when the child is between the ages of 15 and 19 as in Chetty et al. For those who are 33 one would use the income of fathers when the child is between 16 and 20 and so on. 29 you hold parent age constant around the age of 40. While both lines track each other reasonably well before the age of 30, they start to diverge after the age of 32. This is precisely around the time when the red line utilizes data on parents when the child is no longer in the home, when the parents are entering their 50s and when their income becomes noisy. With the green line, however, we continue to use centered time averages of parents around the age of 40 to eliminate this downward bias. The bottom line is that there is in fact substantial lifecycle bias that cannot be uncovered by the sensitivity checks in the Chetty et al version of the tax data because of inherent data limitations. There is also a second pertinent sensitivity analysis that Chetty et al present in their Figure 3B. Here they consider how their results change when they increase the time average of parent income. They do this by adding additional years beyond the 1996-2000 time frame and showing that their rank-rank slope estimates do not increase, though they never show the results of this exercise for the IGE. The key problem with this approach is that can only extend the length of the time averages forward in time. This necessarily results in increasing the attenuation bias from using later ages in the lifecycle of parents. This can again have an offsetting effect due to attenuation bias. For example, the mean age of fathers in their sample in 2003 exceeds 50 so once they start lengthening time averages to include data in 2003 and beyond, they are actually including income observations containing a large transitory component. As before, this also implies that they are actually utilizing many years of income when the child is likely no longer living at home. With the PSID, one can avoid this pitfall. Specifically, one can increase the length of the time average while still holding constant the mean age of fathers by using centered time averages. 30 As before, I first use the PSID to replicate the results of the sensitivity check in Chetty at al and then show that time averaging does in fact reduce the attenuation bias once one removes the mechanical effect of increasing parent age. 30 The results are shown in Figure 5. First, I am able to replicate the spirit of the finding in Chetty et al’s Figure 3B. The red line shows that as I extend the time average of fathers’ income by using years when the fathers are getting older, I find that the time averages appear to have no effect on increasing estimates of the IGE. The IGE stays flat at first and then actually starts to decline when the time averages get very large. However, when I use a centered time average of fathers’ income around the age of 40, a lengthening of the time average generally leads to greater IGE estimates suggesting that larger time averages of parent income do tend to reduce attenuation bias. It is worth noting here that Mazumder (2005a) was able to use SSA data to extend his time averages of fathers earnings backwards in time and also use centered time averages. Finally, Mitnik et al (2015) also show that in their tax data that longer time averages of parent income and measuring child income at later ages lead to higher IGE estimates. Rank-Rank Slope Estimates In this section, I present an analogous set of results for the rank-rank slope. For this analysis I use the same measure of family income that is used to generate Table 1. The results are shown in Table 4. With the rank-rank slope some new patterns emerge. First, it appears that increasing the length of the time averages centered at the age of 40 for sons does appear to increase the slope estimates. For example, looking over the first 10 rows, it appears that in 30 Specifically, I use just a 2 year average of sons’ income over the ages of 29 to 32 and then start with a single year of fathers’ income that is measured when the son is 15 and then gradually add years of fathers’ income from subsequent years. For a five year average, this uses the income of fathers when the son is between the ages of 15 and 19. This mimics the 1981 birth cohort in Chetty et al whose parent income is measured between 1996 and 2000. A ten year average then utilizes the income of fathers when the son is between the ages of 15 and 24. 31 nearly every case the slope estimates are higher when sons’ income is averaged over 8, 9 or 10 years rather than just 1 or 2 years. This was not the case with the IGE. In Table 1 it was typically the reverse pattern. It is not obvious why this is the case but perhaps there is some aspect of lifecycle bias that is more pronounced when using ranks than when using the IGE. This may be a fruitful issue for future research to investigate. Second, the effect of using longer time averages of parent income is much more muted with the rank-rank slope than with the IGE. In table 1, the weighted average of the IGE across all the rows goes from around 0.38 when using a single year of family income to about 0.66 when using 15 year averages of family income –a 72 percent increase. The analogous increase in the rank-rank slope is a rise from 0.31 to 0.40 or just a 29 percent increase. A takeaway from Table 3 is that the rank-rank slope may be around 0.4 or higher rather than the 0.34 reported by Chetty et al. If we do the same exercise of imposing the limitations of the tax data on our PSID sample, the estimate drops from 0.33 when using centered time averages (two years of sons and five years for fathers) to 0.28 when using sons between the ages of 29 and 32 and fathers between the ages of 44 and 48. Again, these results suggest that even the rank-rank slope estimates using the tax data are likely attenuated, albeit to a lesser degree than the substantial attenuation with the IGE estimates. These results are also very similar if one includes the SEO oversample of poorer households or just uses labor income of fathers and sons (results available upon request). In Figures 6 and 7 I return to sensitivity analysis exercises from Chetty et al (2014) in the context of the rank-rank slope and replicate those exercises with the PSID, first allowing father’s age to shift higher mechanically but then correcting for this by holding father’s age constant using centered time averages around the age of 40. Figure 6 doesn’t point to a very clean story. 32 In this case the red line is often larger than the green line suggesting that estimates are often slightly lower when using the centered time averages. On the other hand both lines, but especially the green one, appear to trend higher over the course of the 30s suggesting that perhaps life-cycle bias does not taper off around age 30. Figure 7 is also interesting. The red line is flat to declining and very similar to what Chetty et al find but has the problem of conflating two different biases. The green line, which fixes the mechanical increase in fathers’ age when taking longer time averages does show evidence of larger estimates but only when the time averages are very long. Overall, estimates of the rank-rank slope are also likely biased down due the limitations of the tax data but to a much lesser extent than the IGE. VI. Conclusion The literature on intergenerational mobility over the past few decades has shown how attenuation bias and lifecycle bias can substantially affect estimates of the intergenerational elasticity (IGE). Most previous estimates of the IGE in family income in the U.S. are around 0.5. Utilizing PSID data I generate the first estimates of the IGE in the US using long time averages of parent income and using income centered at age 40 in both generations. I find that the IGE for sons is likely greater than 0.6 with respect to both family income and labor market earnings suggesting less mobility than most previous estimates and similar to estimates in Mazumder (2005a). In contrast, using very large samples of tax records that begin in 1996, Chetty et al (2014) estimate that the IGE is actually much lower at 0.344. Further they claim that these estimates are not subject to attenuation bias or lifecycle bias. If accurate, this finding is important because it implies that income gaps between families in America will dissipate relatively quickly over time. It is important to understand whether the evidence of greater mobility from their tax data sample 33 is accurate or spurious. Revisiting the results from this study may also hold more general lessons for researchers who use administrative data to estimate intergenerational mobility. I first describe the fundamental data limitations of using intergenerational samples based on US tax data that only begin in 1996. The key point is that the panel length is currently too short to do a good job overcoming the issues concerning attenuation bias and lifecycle bias. I demonstrate that a long-lived survey panel such as the PSID that may only have a few thousand families is actually more useful for estimating the national IGE than having millions of tax records if the data are limited in their ability to cover long stretches of the life course. Specifically, I show that when I use the PSID but impose the same age structure and use the shorter time averages of parent income to mimic Chetty et al, that I obtain similar IGE estimates of around 0.3. I also demonstrate that the sensitivity checks used by Chetty et al to address concerns about 1) the age at which sons’ income is measured, and 2) the length of time averages of parent income, are flawed because they impose an offsetting attenuation bias by increasing the age at which parent income is measured. Correcting for this confounding, I show that the lifecycle bias and attenuation bias almost surely exist in the tax data when estimating the IGE. Further confirmation of this is provided by Mitnik et al (2015) who find evidence of these biases in a different IRS sample that extends further back in time and enables an analysis of older children and the use of longer time averages of parent income. The fact that several other papers that also use administrative data in other countries (Nilsen et al, 2012; Gregg et al, 2013 and Nybom and Stuhler, 2015) also show that these biases matter, suggest that Chetty et al’s findings are more the exception than the rule. On the other hand, the results with the PSID with respect to the rank-rank slope suggest that these biases are much smaller and that the rank-rank slope is relatively more robust (though 34 not entirely immune) from these measurement concerns. It is important, however, to remember that the IGE is conceptually different from the rank-rank slope and may continue to be of substantial value to researchers and policy-makers especially in an era of rising inequality when income gaps in society may be expanding. In that context, focusing only on positional mobility solely because measurement is easier, may not be appropriate. Another point worth emphasizing is that survey data may be advantageous for measuring certain sources of income that simply may not be tracked in tax records. These sources of income may provide better measures of the true resources available to families, especially for those at the low end of the income distribution. Given the growing use of administrative data and the excitement over new sources of such data, this characteristic of survey data may start to become overlooked. This is an argument for continuing to produce estimates of intergenerational mobility using survey data despite their smaller sample sizes, at least as a complement to using administrative data. Finally, it is important to make clear that Chetty et al (2014) makes a notable contribution to the literature by demonstrating that there may be large geographic differences in intergenerational mobility across the U.S. It is likely that these large geographic differences will remain even after correcting for the biases in the tax data. 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Card, eds., Handbook of Labor Economics, Vol. 3, Elsevier, pp. 1761–1800. 38 Table 1: Estimates of the father-son IGE in family income Time Average of Sons' Income (years) Time Avg. Fath. Inc. 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 wgt avg. 1 0.414 2 0.372 3 0.405 4 0.375 5 0.397 6 0.361 7 0.317 8 0.315 9 0.354 10 0.415 Wgt. Avg. 0.381 (0.075) (0.067) (0.069) (0.068) (0.064) (0.070) (0.063) (0.068) (0.080) (0.091) 1358 0.439 1184 0.420 1050 0.434 932 0.402 786 0.429 595 0.443 440 0.391 351 0.379 267 0.419 183 0.453 0.423 (0.066) (0.059) (0.062) (0.062) (0.068) (0.088) (0.067) (0.069) (0.082) (0.089) 1317 0.478 1145 0.445 1015 0.450 901 0.414 758 0.440 572 0.440 419 0.401 331 0.380 251 0.416 170 0.449 0.441 (0.067) (0.060) (0.064) (0.064) (0.071) (0.088) (0.062) (0.066) (0.078) (0.088) 1268 0.478 1099 0.455 970 0.467 862 0.435 719 0.453 537 0.463 389 0.419 306 0.388 230 0.431 154 0.422 0.453 (0.068) (0.061) (0.069) (0.069) (0.079) (0.105) (0.063) (0.067) (0.085) (0.091) 1216 0.530 1051 0.493 926 0.500 819 0.468 678 0.479 497 0.477 354 0.428 273 0.398 203 0.441 133 0.454 0.485 (0.071) (0.065) (0.075) (0.076) (0.088) (0.113) (0.065) (0.069) (0.090) (0.098) 1175 0.517 1015 0.482 892 0.492 788 0.458 649 0.473 471 0.476 332 0.420 255 0.389 188 0.434 123 0.452 0.477 (0.071) (0.066) (0.077) (0.078) (0.091) (0.120) (0.064) (0.067) (0.091) (0.092) 1120 0.529 966 0.485 843 0.492 741 0.459 606 0.464 431 0.462 299 0.379 228 0.369 165 0.399 105 0.402 0.474 (0.077) (0.073) (0.086) (0.089) (0.105) (0.144) (0.065) (0.078) (0.109) (0.104) 1063 0.552 915 0.518 795 0.546 696 0.521 564 0.545 396 0.595 271 0.368 202 0.345 143 0.430 87 0.468 0.523 (0.086) (0.082) (0.091) (0.096) (0.110) (0.166) (0.092) (0.114) (0.166) (0.156) 1005 0.573 863 0.537 747 0.558 648 0.536 520 0.560 354 0.629 232 0.435 168 0.391 114 0.494 67 0.624 0.548 (0.090) (0.087) (0.096) (0.101) (0.115) (0.179) (0.090) (0.117) (0.183) (0.159) 956 0.580 818 0.529 710 0.545 614 0.521 488 0.550 326 0.633 208 0.421 147 0.388 97 0.502 54 0.698 0.544 (0.095) (0.092) (0.101) (0.106) (0.124) (0.197) (0.092) (0.124) (0.201) (0.192) 895 0.630 766 0.567 660 0.590 569 0.576 449 0.602 298 0.691 185 0.460 129 0.380 83 0.461 45 0.650 0.588 (0.099) (0.099) (0.107) (0.113) (0.134) (0.220) (0.093) (0.140) (0.234) (0.245) 818 0.648 696 0.592 595 0.623 510 0.589 399 0.624 255 0.747 149 0.474 98 0.386 59 0.400 31 0.604 0.612 (0.109) (0.108) (0.117) (0.123) (0.151) (0.258) (0.119) (0.164) (0.247) (0.271) 743 0.667 633 0.612 541 0.649 465 0.625 358 0.605 224 0.533 121 0.462 78 0.287 46 0.395 24 0.363 0.612 (0.122) (0.107) (0.110) (0.113) (0.114) (0.117) (0.155) (0.215) (0.301) (0.164) 656 0.714 554 0.692 470 0.714 399 0.681 307 0.659 184 0.629 96 0.511 57 0.457 31 0.986 13 0.761 0.685 0.656 (0.129) (0.104) (0.116) (0.120) (0.122) (0.115) (0.182) (0.311) (0.411) (0.368) 590 0.680 495 0.664 415 0.662 349 0.616 263 0.651 146 0.597 70 0.532 36 0.576 15 1.527 7 0.954 (0.134) (0.099) (0.109) (0.108) (0.123) (0.129) (0.216) (0.393) (0.258) (0.700) 533 448 374 309 228 120 54 24 11 6 0.539 0.501 0.517 0.485 0.501 0.510 0.405 0.374 0.432 0.469 39 Table 2: Estimates of the father-son IGE in labor income Time Average of Sons' Income (years) Time Avg. Fath. Inc. 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 wgt avg. 1 0.299 2 0.308 3 0.308 4 0.335 5 0.358 6 0.333 7 0.373 8 0.395 9 0.384 10 0.359 Wgt. Avg. 0.359 (0.072) (0.069) (0.063) (0.064) (0.065) (0.066) (0.069) (0.070) (0.085) (0.084) 955 0.412 824 0.412 696 0.407 581 0.405 466 0.407 360 0.369 264 0.439 202 0.422 156 0.427 104 0.412 0.383 (0.063) (0.061) (0.061) (0.065) (0.074) (0.075) (0.059) (0.059) (0.077) (0.081) 928 0.436 799 0.422 674 0.401 562 0.395 450 0.393 345 0.368 250 0.440 191 0.430 147 0.441 96 0.421 0.473 (0.061) (0.061) (0.059) (0.064) (0.073) (0.076) (0.056) (0.055) (0.072) (0.080) 900 0.420 773 0.412 649 0.408 539 0.392 431 0.387 329 0.359 236 0.435 180 0.404 137 0.409 88 0.395 0.491 (0.064) (0.063) (0.062) (0.067) (0.076) (0.077) (0.058) (0.058) (0.073) (0.082) 864 0.472 741 0.462 622 0.440 514 0.416 411 0.397 310 0.367 218 0.445 163 0.416 123 0.437 80 0.437 0.516 (0.069) (0.066) (0.067) (0.071) (0.080) (0.082) (0.059) (0.059) (0.077) (0.091) 841 0.485 720 0.473 609 0.450 502 0.432 401 0.402 300 0.360 209 0.455 155 0.434 116 0.471 76 0.488 0.490 (0.071) (0.068) (0.068) (0.074) (0.083) (0.082) (0.059) (0.061) (0.084) (0.102) 797 0.486 683 0.468 574 0.440 469 0.420 371 0.385 274 0.332 190 0.441 139 0.401 101 0.432 63 0.430 0.497 (0.077) (0.074) (0.075) (0.082) (0.091) (0.087) (0.073) (0.080) (0.104) (0.106) 760 0.510 652 0.487 546 0.473 445 0.459 349 0.451 255 0.407 174 0.414 123 0.352 88 0.382 52 0.409 0.559 (0.085) (0.081) (0.079) (0.087) (0.094) (0.080) (0.092) (0.108) (0.135) (0.117) 725 0.511 622 0.476 518 0.461 419 0.445 327 0.452 235 0.408 158 0.427 110 0.356 80 0.392 45 0.406 0.583 (0.086) (0.081) (0.079) (0.088) (0.094) (0.080) (0.092) (0.109) (0.136) (0.122) 699 0.513 597 0.474 500 0.468 404 0.461 314 0.475 225 0.426 149 0.446 103 0.413 73 0.443 41 0.516 0.593 (0.088) (0.084) (0.081) (0.092) (0.102) (0.085) (0.101) (0.122) (0.161) (0.144) 657 0.578 561 0.503 470 0.491 377 0.494 290 0.528 203 0.429 130 0.461 89 0.437 62 0.483 34 0.526 0.616 (0.093) (0.091) (0.087) (0.096) (0.106) (0.092) (0.116) (0.143) (0.203) (0.186) 597 0.596 512 0.506 425 0.526 340 0.496 255 0.565 176 0.413 107 0.427 69 0.376 48 0.346 24 0.391 0.611 (0.102) (0.108) (0.105) (0.113) (0.131) (0.118) (0.158) (0.158) (0.233) (0.157) 539 0.690 461 0.589 380 0.628 302 0.636 226 0.701 151 0.551 85 0.494 53 0.556 34 0.790 15 0.323 0.615 (0.111) (0.114) (0.112) (0.127) (0.153) (0.143) (0.176) (0.208) (0.316) (0.323) 477 0.744 401 0.651 327 0.676 254 0.715 185 0.793 118 0.699 66 0.638 38 0.695 22 1.526 7 5.971 0.702 0.713 (0.116) (0.122) (0.119) (0.138) (0.161) (0.158) (0.216) (0.266) (0.259) (0.916) 427 0.751 356 0.623 285 0.649 218 0.652 161 0.719 96 0.641 48 0.547 25 0.659 10 1.335 4 4.240 (0.122) (0.127) (0.125) (0.138) (0.163) (0.179) (0.266) (0.282) (0.253) (0.000) 386 319 251 189 135 78 35 18 7 3 0.574 0.517 0.458 0.469 0.504 0.471 0.519 0.535 0.564 0.592 40 Table 3: Estimates of the father-son IGE in family income using fixed samples Time Avg. Father Inc. 1 2 3 4 5 6 7 8 9 10 13 15 N Samples use sons with 1 year of income and fathers with the following available years of income 3 5 7 10 15 0.397 0.393 0.358 0.388 0.291 (0.070) (0.074) (0.078) (0.100) (0.131) 0.438 0.430 0.401 0.429 0.366 (0.068) (0.071) (0.076) (0.097) (0.122) 0.478 0.473 0.446 0.497 0.453 (0.067) (0.070) (0.075) (0.095) (0.124) 0.484 0.460 0.522 0.479 (0.069) (0.072) (0.091) (0.114) 0.530 0.504 0.579 0.568 (0.071) (0.075) (0.094) (0.121) 0.515 0.581 0.580 (0.075) (0.092) (0.118) 0.529 0.595 0.622 (0.077) (0.094) (0.120) 0.583 0.619 (0.094) (0.119) 0.584 0.635 (0.095) (0.123) 0.580 0.643 (0.095) (0.122) 0.662 (0.132) 0.680 (0.134) 1268 1175 1063 895 533 41 Table 4: Estimates of the father-son rank-rank slope in family income Time Average of Sons' Income (years) Time Avg. Fath. Inc. 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 wgt avg. 1 0.282 2 0.304 3 0.326 4 0.309 5 0.333 6 0.322 7 0.295 8 0.290 9 0.307 10 0.423 Wgt. Avg. 0.310 (0.032) (0.036) (0.039) (0.040) (0.043) (0.050) (0.059) (0.065) (0.071) (0.080) 1358 0.290 1184 0.312 1050 0.341 932 0.329 786 0.362 595 0.376 440 0.352 351 0.339 267 0.356 183 0.448 0.334 (0.032) (0.035) (0.038) (0.040) (0.043) (0.050) (0.059) (0.065) (0.073) (0.083) 1317 0.296 1145 0.317 1015 0.341 901 0.328 758 0.362 572 0.379 419 0.373 331 0.352 251 0.375 170 0.451 0.338 (0.032) (0.035) (0.039) (0.041) (0.043) (0.049) (0.055) (0.065) (0.072) (0.086) 1268 0.296 1099 0.320 970 0.347 862 0.333 719 0.366 537 0.391 389 0.396 306 0.363 230 0.389 154 0.435 0.343 (0.032) (0.036) (0.039) (0.041) (0.044) (0.050) (0.055) (0.067) (0.078) (0.096) 1216 0.309 1051 0.333 926 0.362 819 0.348 678 0.378 497 0.399 354 0.413 273 0.374 203 0.402 133 0.482 0.357 (0.032) (0.036) (0.040) (0.042) (0.045) (0.052) (0.058) (0.069) (0.083) (0.097) 1175 0.299 1015 0.319 892 0.348 788 0.333 649 0.362 471 0.385 332 0.404 255 0.365 188 0.399 123 0.504 0.344 (0.034) (0.037) (0.042) (0.044) (0.047) (0.054) (0.063) (0.072) (0.088) (0.095) 1120 0.283 966 0.302 843 0.328 741 0.311 606 0.336 431 0.350 299 0.370 228 0.316 165 0.339 105 0.436 0.318 (0.035) (0.039) (0.044) (0.046) (0.049) (0.057) (0.067) (0.076) (0.095) (0.104) 1063 0.282 915 0.303 795 0.336 696 0.321 564 0.348 396 0.362 271 0.332 202 0.279 143 0.280 87 0.396 0.317 (0.037) (0.042) (0.046) (0.049) (0.052) (0.062) (0.075) (0.088) (0.112) (0.123) 1005 0.292 863 0.309 747 0.342 648 0.333 520 0.365 354 0.394 232 0.403 168 0.327 114 0.318 67 0.493 0.334 (0.038) (0.043) (0.048) (0.050) (0.053) (0.062) (0.071) (0.091) (0.125) (0.113) 956 0.287 818 0.304 710 0.330 614 0.319 488 0.352 326 0.379 208 0.397 147 0.330 97 0.314 54 0.539 0.325 (0.039) (0.044) (0.049) (0.051) (0.054) (0.064) (0.074) (0.098) (0.138) (0.134) 895 0.299 766 0.315 660 0.345 569 0.338 449 0.364 298 0.394 185 0.413 129 0.315 83 0.267 45 0.518 0.336 (0.040) (0.046) (0.051) (0.054) (0.057) (0.069) (0.080) (0.112) (0.162) (0.169) 818 0.310 696 0.326 595 0.354 510 0.336 399 0.363 255 0.386 149 0.390 98 0.303 59 0.236 31 0.587 0.339 (0.042) (0.049) (0.054) (0.057) (0.062) (0.077) (0.093) (0.125) (0.179) (0.196) 743 0.335 633 0.355 541 0.392 465 0.384 358 0.385 224 0.357 121 0.311 78 0.133 46 0.076 24 0.264 0.354 (0.046) (0.051) (0.055) (0.057) (0.065) (0.088) (0.118) (0.162) (0.232) (0.295) 656 0.356 554 0.391 470 0.433 399 0.428 307 0.432 184 0.445 96 0.400 57 0.322 31 0.446 13 0.618 0.403 0.401 (0.048) (0.050) (0.055) (0.057) (0.066) (0.088) (0.127) (0.191) (0.285) (0.244) 590 0.350 495 0.382 415 0.428 349 0.426 263 0.447 146 0.436 70 0.418 36 0.399 15 0.635 7 0.423 (0.050) (0.051) (0.057) (0.057) (0.068) (0.095) (0.137) (0.242) (0.231) (0.382) 533 448 374 309 228 120 54 24 11 6 0.300 0.321 0.350 0.337 0.364 0.377 0.371 0.329 0.346 0.457 42 Figure 1: Comparison of life cycle coverage across intergenerational Samples A. Ideal Parent 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 Child 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 B. Chetty et al (2014) Parent Child 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 43 C. PSID Parent 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 Child 55 54 53 52 51 50 49 48 47 46 45 44 43 42 41 40 39 38 37 36 35 34 33 32 31 30 29 28 27 26 25 Figure 2: Effects of time averaging on father-son IGE in family income 0.8 0.7 0.6 IGE 0.5 0.4 0.3 0.2 0.1 0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 13 14 15 Length of Time Average of Father's Income Weighted Average One year of Sons' Income Figure 3: Father-son IGE in labor income vs family income 0.8 0.7 0.6 IGE 0.5 0.4 0.3 0.2 0.1 0 1 2 3 4 5 6 7 8 9 10 11 Length of Time Average of Father's Income Family Income Labor Income 44 12 Figure 4: Re-examining the Sensitivity of the IGE to Son's Age 1 0.9 0.8 0.7 IGE 0.6 0.5 0.4 0.3 0.2 0.1 0 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36 37 38 39 40 41 Age of Son Replicating the Chetty et al Approach Fixing the Sensitivity Check Figure 5: Re-examining the Sensitivity of the IGE to longer time averages of parent income 0.7 0.6 0.5 IGE 0.4 0.3 0.2 0.1 0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 Length of Time Average of Father's Income Replicating the Chetty et al Approach Fixing the Sensitivity Check 45 Figure 6: Re-examining the Sensitivity of the Rank-rank Slope to Son's Age 0.45 0.4 0.35 IGE 0.3 0.25 0.2 0.15 0.1 0.05 0 22 23 24 25 26 27 28 29 30 31 32 33 34 35 36 37 38 39 40 41 Age of Son Replicating the Chetty et al Approach Fixing the Sensitivity Check Figure 7: Re-examining the Sensitivity of the rank-rank Slope to longer time averages of parent income 0.45 0.4 0.35 IGE 0.3 0.25 0.2 0.15 0.1 0.05 0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17 Length of Time Average of Father's Income Replicating the Chetty et al Approach Fixing the Sensitivity Check 46 Appendix Table 1: Estimates of the father-son IGE in family income using SEO subsample Time Average of Sons' Income (years) Time Avg. Fath. Inc. 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 wgt avg. 1 0.451 2 0.403 3 0.434 4 0.414 5 0.426 6 0.393 7 0.357 8 0.363 9 0.383 10 0.401 Wgt. Avg. 0.415 (0.054) (0.048) (0.049) (0.051) (0.047) (0.050) (0.047) (0.054) (0.066) (0.077) 2133 0.485 1842 0.450 1611 0.468 1400 0.438 1158 0.457 867 0.451 623 0.406 490 0.402 364 0.418 251 0.430 0.453 (0.053) (0.045) (0.047) (0.049) (0.052) (0.061) (0.048) (0.053) (0.063) (0.069) 2062 0.526 1774 0.476 1550 0.491 1345 0.457 1109 0.476 828 0.473 590 0.439 460 0.428 340 0.446 234 0.461 0.480 (0.056) (0.049) (0.054) (0.053) (0.059) (0.068) (0.051) (0.054) (0.065) (0.074) 1989 0.531 1706 0.487 1483 0.508 1287 0.476 1054 0.487 780 0.493 548 0.449 427 0.435 313 0.464 213 0.443 0.492 (0.058) (0.051) (0.058) (0.059) (0.066) (0.080) (0.052) (0.056) (0.072) (0.079) 1865 0.586 1594 0.526 1389 0.544 1200 0.510 975 0.514 709 0.508 491 0.457 379 0.446 278 0.482 186 0.483 0.527 (0.062) (0.056) (0.066) (0.067) (0.076) (0.092) (0.058) (0.062) (0.082) (0.093) 1780 0.575 1519 0.515 1320 0.535 1137 0.499 917 0.506 661 0.503 452 0.437 346 0.425 253 0.476 167 0.481 0.518 (0.063) (0.056) (0.068) (0.069) (0.079) (0.097) (0.057) (0.062) (0.086) (0.094) 1677 0.593 1429 0.528 1235 0.548 1057 0.514 848 0.516 597 0.513 398 0.420 300 0.418 215 0.446 137 0.428 0.528 (0.067) (0.063) (0.076) (0.079) (0.093) (0.119) (0.060) (0.071) (0.099) (0.102) 1579 0.595 1343 0.544 1155 0.576 984 0.546 783 0.554 543 0.587 357 0.422 263 0.411 186 0.480 115 0.514 0.553 (0.073) (0.069) (0.077) (0.081) (0.090) (0.125) (0.079) (0.097) (0.137) (0.136) 1490 0.616 1266 0.560 1087 0.588 918 0.560 724 0.571 490 0.622 313 0.479 225 0.461 154 0.546 95 0.660 0.577 (0.077) (0.073) (0.081) (0.085) (0.094) (0.135) (0.077) (0.102) (0.153) (0.140) 1405 0.633 1190 0.558 1025 0.587 862 0.555 674 0.575 447 0.645 276 0.476 195 0.451 129 0.547 74 0.691 0.582 (0.082) (0.079) (0.087) (0.092) (0.105) (0.157) (0.086) (0.109) (0.170) (0.155) 1321 0.674 1123 0.584 961 0.618 803 0.587 623 0.599 410 0.669 245 0.471 172 0.385 112 0.470 63 0.606 0.608 (0.087) (0.086) (0.093) (0.099) (0.114) (0.179) (0.084) (0.119) (0.195) (0.183) 1182 0.700 1003 0.610 849 0.650 703 0.601 540 0.620 342 0.720 194 0.482 130 0.381 81 0.415 44 0.617 0.633 (0.097) (0.095) (0.103) (0.110) (0.131) (0.214) (0.108) (0.143) (0.215) (0.226) 1068 0.714 903 0.619 764 0.656 632 0.621 478 0.598 297 0.526 158 0.454 103 0.291 63 0.392 34 0.389 0.625 (0.111) (0.097) (0.099) (0.104) (0.104) (0.106) (0.144) (0.187) (0.251) (0.161) 942 0.769 794 0.698 667 0.721 546 0.678 414 0.651 248 0.616 126 0.507 78 0.436 45 0.909 21 0.859 0.700 0.682 (0.118) (0.094) (0.106) (0.112) (0.112) (0.104) (0.170) (0.274) (0.354) (0.353) 831 0.752 694 0.675 581 0.677 471 0.626 350 0.653 193 0.598 88 0.546 48 0.569 21 1.318 8 1.094 (0.123) (0.090) (0.099) (0.100) (0.112) (0.114) (0.200) (0.335) (0.334) (0.642) 745 624 521 419 304 163 70 34 16 7 0.587 0.526 0.549 0.515 0.522 0.524 0.435 0.415 0.461 0.479 47 Appendix Table 2: Summary statistics of fathers by available years of income 1 N 1358 2 1317 3 1268 4 1216 5 1175 6 1120 7 1063 8 1005 9 956 10 895 11 818 12 743 13 656 14 590 15 533 5 v. 10 T-Stat P-Val 5 v. 15 T-Stat P-Val Father Mother Income ($) Age Education Education Black 41.6 12.9 12.2 5.1% (0.1) (0.1) (0.1) (0.01) 41.9 12.9 12.2 5.1% (0.1) (0.1) (0.1) (0.01) 79233 41.5 12.9 12.2 5.1% (1601) (0.1) (0.1) (0.1) (0.01) 79805 41.7 12.9 12.3 5.3% (1565) (0.1) (0.1) (0.1) (0.01) 79477 41.4 12.9 12.3 5.2% (1520) (0.1) (0.1) (0.1) (0.01) 80877 41.6 12.9 12.3 5.3% (1630) (0.1) (0.1) (0.1) (0.01) 80962 41.3 12.9 12.3 5.2% (1659) (0.1) (0.1) (0.1) (0.01) 81612 41.5 12.9 12.3 5.5% (1675) (0.1) (0.1) (0.1) (0.01) 81175 41.2 12.9 12.3 5.4% (1682) (0.1) (0.1) (0.1) (0.01) 82609 41.4 12.9 12.4 5.1% (1744) (0.1) (0.1) (0.1) (0.01) 82650 40.9 12.9 12.5 5.3% (1780) (0.1) (0.1) (0.1) (0.01) 82005 41.0 13.0 12.5 5.2% (1823) (0.1) (0.1) (0.1) (0.01) 81503 40.6 13.0 12.5 5.2% (1909) (0.1) (0.1) (0.1) (0.01) 81444 40.7 13.0 12.5 5.7% (2012) (0.0) (0.1) (0.1) (0.01) 82272 40.3 13.0 12.5 5.9% (2131) (0.0) (0.1) (0.1) (0.01) Two-Sample Test in Difference of Means -1.35 0.38 -0.32 -0.45 0.10 0.18 0.71 0.75 0.65 0.92 -1.07 13.49 -0.68 -1.64 -0.56 0.29 0.00 0.50 0.10 0.58 48 White 94.1% (0.01) 94.1% (0.01) 94.2% (0.01) 94.0% (0.01) 94.0% (0.01) 94.0% (0.01) 94.0% (0.01) 93.7% (0.01) 93.8% (0.01) 94.0% (0.01) 93.7% (0.01) 93.8% (0.01) 93.7% (0.01) 93.1% (0.01) 92.7% (0.01) Married 97.2% (0.01) 97.2% (0.01) 97.2% (0.01) 97.2% (0.01) 97.2% (0.01) 97.2% (0.01) 97.2% (0.01) 97.3% (0.01) 97.4% (0.01) 97.3% (0.01) 97.1% (0.01) 96.8% (0.01) 96.4% (0.01) 96.1% (0.01) 95.9% (0.01) Ever Divorced 24.0% (0.01) 24.5% (0.01) 25.1% (0.01) 25.9% (0.01) 26.3% (0.01) 26.5% (0.01) 26.9% (0.01) 27.5% (0.01) 27.5% (0.01) 27.9% (0.02) 29.1% (0.02) 29.0% (0.02) 30.0% (0.02) 31.4% (0.02) 32.5% (0.02) 0.03 0.98 0.98 0.33 -0.12 0.91 1.34 0.18 -0.80 0.42 -2.57 0.01 Appendix Figure 1: Effects of time averaging on father-son IGE in family income including SEO sample 0.9 0.8 0.7 IGE 0.6 0.5 0.4 0.3 0.2 0.1 0 1 2 3 4 5 6 7 8 9 10 11 Length of Time Average of Father's Income Weighted Average One year of Sons' Income 49 12 13 14 15 Working Paper Series A series of research studies on regional economic issues relating to the Seventh Federal Reserve District, and on financial and economic topics. Examining Macroeconomic Models through the Lens of Asset Pricing Jaroslav Borovička and Lars Peter Hansen WP-12-01 The Chicago Fed DSGE Model Scott A. Brave, Jeffrey R. Campbell, Jonas D.M. Fisher, and Alejandro Justiniano WP-12-02 Macroeconomic Effects of Federal Reserve Forward Guidance Jeffrey R. Campbell, Charles L. Evans, Jonas D.M. Fisher, and Alejandro Justiniano WP-12-03 Modeling Credit Contagion via the Updating of Fragile Beliefs Luca Benzoni, Pierre Collin-Dufresne, Robert S. Goldstein, and Jean Helwege WP-12-04 Signaling Effects of Monetary Policy Leonardo Melosi WP-12-05 Empirical Research on Sovereign Debt and Default Michael Tomz and Mark L. J. Wright WP-12-06 Credit Risk and Disaster Risk François Gourio WP-12-07 From the Horse’s Mouth: How do Investor Expectations of Risk and Return Vary with Economic Conditions? Gene Amromin and Steven A. Sharpe WP-12-08 Using Vehicle Taxes To Reduce Carbon Dioxide Emissions Rates of New Passenger Vehicles: Evidence from France, Germany, and Sweden Thomas Klier and Joshua Linn WP-12-09 Spending Responses to State Sales Tax Holidays Sumit Agarwal and Leslie McGranahan WP-12-10 Micro Data and Macro Technology Ezra Oberfield and Devesh Raval WP-12-11 The Effect of Disability Insurance Receipt on Labor Supply: A Dynamic Analysis Eric French and Jae Song WP-12-12 Medicaid Insurance in Old Age Mariacristina De Nardi, Eric French, and John Bailey Jones WP-12-13 Fetal Origins and Parental Responses Douglas Almond and Bhashkar Mazumder WP-12-14 1 Working Paper Series (continued) Repos, Fire Sales, and Bankruptcy Policy Gaetano Antinolfi, Francesca Carapella, Charles Kahn, Antoine Martin, David Mills, and Ed Nosal WP-12-15 Speculative Runs on Interest Rate Pegs The Frictionless Case Marco Bassetto and Christopher Phelan WP-12-16 Institutions, the Cost of Capital, and Long-Run Economic Growth: Evidence from the 19th Century Capital Market Ron Alquist and Ben Chabot WP-12-17 Emerging Economies, Trade Policy, and Macroeconomic Shocks Chad P. Bown and Meredith A. Crowley WP-12-18 The Urban Density Premium across Establishments R. Jason Faberman and Matthew Freedman WP-13-01 Why Do Borrowers Make Mortgage Refinancing Mistakes? Sumit Agarwal, Richard J. Rosen, and Vincent Yao WP-13-02 Bank Panics, Government Guarantees, and the Long-Run Size of the Financial Sector: Evidence from Free-Banking America Benjamin Chabot and Charles C. Moul WP-13-03 Fiscal Consequences of Paying Interest on Reserves Marco Bassetto and Todd Messer WP-13-04 Properties of the Vacancy Statistic in the Discrete Circle Covering Problem Gadi Barlevy and H. N. Nagaraja WP-13-05 Credit Crunches and Credit Allocation in a Model of Entrepreneurship Marco Bassetto, Marco Cagetti, and Mariacristina De Nardi WP-13-06 Financial Incentives and Educational Investment: The Impact of Performance-Based Scholarships on Student Time Use Lisa Barrow and Cecilia Elena Rouse WP-13-07 The Global Welfare Impact of China: Trade Integration and Technological Change Julian di Giovanni, Andrei A. Levchenko, and Jing Zhang WP-13-08 Structural Change in an Open Economy Timothy Uy, Kei-Mu Yi, and Jing Zhang WP-13-09 The Global Labor Market Impact of Emerging Giants: a Quantitative Assessment Andrei A. Levchenko and Jing Zhang WP-13-10 2 Working Paper Series (continued) Size-Dependent Regulations, Firm Size Distribution, and Reallocation François Gourio and Nicolas Roys WP-13-11 Modeling the Evolution of Expectations and Uncertainty in General Equilibrium Francesco Bianchi and Leonardo Melosi WP-13-12 Rushing into the American Dream? House Prices, the Timing of Homeownership, and the Adjustment of Consumer Credit Sumit Agarwal, Luojia Hu, and Xing Huang WP-13-13 The Earned Income Tax Credit and Food Consumption Patterns Leslie McGranahan and Diane W. Schanzenbach WP-13-14 Agglomeration in the European automobile supplier industry Thomas Klier and Dan McMillen WP-13-15 Human Capital and Long-Run Labor Income Risk Luca Benzoni and Olena Chyruk WP-13-16 The Effects of the Saving and Banking Glut on the U.S. Economy Alejandro Justiniano, Giorgio E. Primiceri, and Andrea Tambalotti WP-13-17 A Portfolio-Balance Approach to the Nominal Term Structure Thomas B. King WP-13-18 Gross Migration, Housing and Urban Population Dynamics Morris A. Davis, Jonas D.M. Fisher, and Marcelo Veracierto WP-13-19 Very Simple Markov-Perfect Industry Dynamics Jaap H. Abbring, Jeffrey R. Campbell, Jan Tilly, and Nan Yang WP-13-20 Bubbles and Leverage: A Simple and Unified Approach Robert Barsky and Theodore Bogusz WP-13-21 The scarcity value of Treasury collateral: Repo market effects of security-specific supply and demand factors Stefania D'Amico, Roger Fan, and Yuriy Kitsul Gambling for Dollars: Strategic Hedge Fund Manager Investment Dan Bernhardt and Ed Nosal Cash-in-the-Market Pricing in a Model with Money and Over-the-Counter Financial Markets Fabrizio Mattesini and Ed Nosal An Interview with Neil Wallace David Altig and Ed Nosal WP-13-22 WP-13-23 WP-13-24 WP-13-25 3 Working Paper Series (continued) Firm Dynamics and the Minimum Wage: A Putty-Clay Approach Daniel Aaronson, Eric French, and Isaac Sorkin Policy Intervention in Debt Renegotiation: Evidence from the Home Affordable Modification Program Sumit Agarwal, Gene Amromin, Itzhak Ben-David, Souphala Chomsisengphet, Tomasz Piskorski, and Amit Seru WP-13-26 WP-13-27 The Effects of the Massachusetts Health Reform on Financial Distress Bhashkar Mazumder and Sarah Miller WP-14-01 Can Intangible Capital Explain Cyclical Movements in the Labor Wedge? François Gourio and Leena Rudanko WP-14-02 Early Public Banks William Roberds and François R. Velde WP-14-03 Mandatory Disclosure and Financial Contagion Fernando Alvarez and Gadi Barlevy WP-14-04 The Stock of External Sovereign Debt: Can We Take the Data at ‘Face Value’? Daniel A. Dias, Christine Richmond, and Mark L. J. Wright WP-14-05 Interpreting the Pari Passu Clause in Sovereign Bond Contracts: It’s All Hebrew (and Aramaic) to Me Mark L. J. Wright WP-14-06 AIG in Hindsight Robert McDonald and Anna Paulson WP-14-07 On the Structural Interpretation of the Smets-Wouters “Risk Premium” Shock Jonas D.M. Fisher WP-14-08 Human Capital Risk, Contract Enforcement, and the Macroeconomy Tom Krebs, Moritz Kuhn, and Mark L. J. Wright WP-14-09 Adverse Selection, Risk Sharing and Business Cycles Marcelo Veracierto WP-14-10 Core and ‘Crust’: Consumer Prices and the Term Structure of Interest Rates Andrea Ajello, Luca Benzoni, and Olena Chyruk WP-14-11 The Evolution of Comparative Advantage: Measurement and Implications Andrei A. Levchenko and Jing Zhang WP-14-12 4 Working Paper Series (continued) Saving Europe?: The Unpleasant Arithmetic of Fiscal Austerity in Integrated Economies Enrique G. Mendoza, Linda L. Tesar, and Jing Zhang WP-14-13 Liquidity Traps and Monetary Policy: Managing a Credit Crunch Francisco Buera and Juan Pablo Nicolini WP-14-14 Quantitative Easing in Joseph’s Egypt with Keynesian Producers Jeffrey R. Campbell WP-14-15 Constrained Discretion and Central Bank Transparency Francesco Bianchi and Leonardo Melosi WP-14-16 Escaping the Great Recession Francesco Bianchi and Leonardo Melosi WP-14-17 More on Middlemen: Equilibrium Entry and Efficiency in Intermediated Markets Ed Nosal, Yuet-Yee Wong, and Randall Wright WP-14-18 Preventing Bank Runs David Andolfatto, Ed Nosal, and Bruno Sultanum WP-14-19 The Impact of Chicago’s Small High School Initiative Lisa Barrow, Diane Whitmore Schanzenbach, and Amy Claessens WP-14-20 Credit Supply and the Housing Boom Alejandro Justiniano, Giorgio E. Primiceri, and Andrea Tambalotti WP-14-21 The Effect of Vehicle Fuel Economy Standards on Technology Adoption Thomas Klier and Joshua Linn WP-14-22 What Drives Bank Funding Spreads? Thomas B. King and Kurt F. Lewis WP-14-23 Inflation Uncertainty and Disagreement in Bond Risk Premia Stefania D’Amico and Athanasios Orphanides WP-14-24 Access to Refinancing and Mortgage Interest Rates: HARPing on the Importance of Competition Gene Amromin and Caitlin Kearns WP-14-25 Private Takings Alessandro Marchesiani and Ed Nosal WP-14-26 Momentum Trading, Return Chasing, and Predictable Crashes Benjamin Chabot, Eric Ghysels, and Ravi Jagannathan WP-14-27 Early Life Environment and Racial Inequality in Education and Earnings in the United States Kenneth Y. Chay, Jonathan Guryan, and Bhashkar Mazumder WP-14-28 5 Working Paper Series (continued) Poor (Wo)man’s Bootstrap Bo E. Honoré and Luojia Hu WP-15-01 Revisiting the Role of Home Production in Life-Cycle Labor Supply R. Jason Faberman WP-15-02 Risk Management for Monetary Policy Near the Zero Lower Bound Charles Evans, Jonas Fisher, François Gourio, and Spencer Krane WP-15-03 Estimating the Intergenerational Elasticity and Rank Association in the US: Overcoming the Current Limitations of Tax Data Bhashkar Mazumder WP-15-04 6