Do neighborhoods affect work behavior? Evidence from the NLSY79

Do Neighborhoods Affect Work Behavior? Evidence from the NLSY79 September 2000 Bruce A. Weinberg* **, Patricia B. Reagan*, Jeffrey J. Yankow*** * Department of Economics and Center for Human Resource Research Ohio State University 1945 North High Street Columbus, Ohio 43210 ** Hoover Institution Stanford University Stanford, California 94305-6010 ** Department of Economics and Business Administration Furman University 3300 Poinsett Hwy. Greenville, SC 29613-1130 [email protected] [email protected] [email protected] We wish to thank Steve Cosslett, Steve Durlauf, Eric Gould, Joe Hotz, Richard Green, Keith Ihlanfeldt, Saul Lach, Audrey Light, Don Haurin, Randy Olsen, Shlomo Yitzhaki and seminar participants at Emory University, the University of Georgia, Georgia State University, Hebrew University of Jerusalem, Ohio State University (Departments of Economics and Geography), SUNY Albany, an ARUEA session at the 2000 ASSA Meetings, and the MacArthur Foundation Network on Social Interactions and Inequality. Do Neighborhoods Affect Work Behavior? Evidence from the NLSY79 ABSTRACT Researchers have argued that neighborhoods are an important determinant of labor activity. Using confidential street address data from the NLSY79, respondents were linked to neighborhood social characteristics and measures of job proximity. A one standard deviation increase in the social characteristics of a neighborhood increases annual hours by 6%; a similar increase in job proximity raises hours by 4%. Labor market activity at the individual level is positively related to labor market activity of neighbors. But employment is not the only neighborhood characteristic that matters. Being in a disadvantaged neighborhood, as measured by a variety of characteristics, reduces market work. Social interactions have non-linear effects with the greatest impact in the worst neighborhoods. Social interactions are more important for less educated workers and Hispanics. Job locations are more important for blacks. Estimates that do not account for neighborhood selection on the basis of time-invariant and time-varying unobserved individual characteristics substantially overstate the social effects of neighborhoods but understate the effects of job access. Do Neighborhoods Affect Work Behavior? Evidence from the NLSY79 I. Introduction Economists and sociologists have argued that neighborhoods affect labor market activity along with a variety of other youth outcomes1. Two classes of models have been proposed. Social interaction models posit that individual work decisions are affected by the behavior or characteristics of neighbors. A recent line of inquiry focuses on information externalities as the primary form of social interaction (Granovetter 1995). If neighbors are an important source of information about jobs, individuals living in neighborhoods characterized by low socio-economic indicators will face greater difficulties in learning about job opportunities. Alternatively, spatial mismatch models focus on the effects of job proximity as a determinant of employment status (Kain 1968). If distance affects the cost of commuting to work or the availability of information about employment opportunities, individuals living in neighborhoods spatially isolated from jobs will have lower employment rates. Estimates of both sets of effects often indicate that neighborhoods are an important determinant of employment status but raise concerns with endogenous neighborhood choice. In the case of social interactions models, unobserved individual characteristics that raise participation may lead individuals to choose better neighborhoods. In the case of the spatial mismatch hypothesis, individuals with exogenously low labor force attachment have less incentive to locate in neighborhoods with good job access. But estimated effects of job access can also be biased downwards 1 since individuals with weak labor force attachment may be attracted to older neighborhoods around central business districts with the best job access (see Glaeser, Kahn, and Rappaport 2000). Thus, endogenous neighborhood choice is likely to bias estimates of social interactions upward, while estimates of the mismatch hypothesis may be biased in either direction. This paper exploits a unique data set to estimate the effect of neighborhoods on employment behavior. For administrative purposes, exact street addresses were recorded annually for respondents to the 1979 National Longitudinal Survey of Youth (NLSY79). Using geographic mapping software, respondents were matched to the latitude, longitude and 1990 census tract in which they resided at the time of each interview. Neighborhood characteristics, including employment rates and welfare recipiency, were obtained from the 1990 Census Summary Tape Files at the census tract level. Information on jobs came from the 1987 Censuses of Manufactures, Retail Trade, and Services that report employment at the zip code level. Jobs were matched to their zipcode centroid. The number of jobs within concentric circles over various distances around each respondent was then calculated. The NLSY79 data have a number of attractive features for our purposes. First, the longitudinal aspects of the data make it possible to track the same individuals over time as they move across neighborhoods. In addition, the data focus on individuals at the outset of their work careers for whom neighborhood influences are believed to be 1 Among sociologists, Wilson (1987, 1996), Massey and Denton (1993), and Kasarda (1996) have, perhaps, had the greatest effect on the economics literature. 2 strongest. Finally, these data oversample blacks and Hispanics making it possible to obtain precise estimates for these groups2. Our empirical work addresses four questions. First, we ask whether contemporaneous neighborhood social characteristics and proximity to jobs affect individual employment behavior in an effort to distinguish between competing models.3 Second, we consider whether neighborhoods have non-linear effects and whether the effects vary with individual characteristics. Third, we provide some evidence on the channels through which social effects operate. Finally, we address the various forms of heterogeneity that must be controlled to accurately estimate the effects of neighborhoods. Our major findings can be summarized as follows. We find that neighborhoods have a significant impact on individual employment outcomes. Interestingly, both social influences and job proximity are found to be important determinants of work. A one standard deviation increase in the social characteristics of a neighborhood increase annual hours by 6%; a similar increase in job proximity raises hours by 4%. In keeping with existing work, these effects are found to be non-linear: Social influences generally have the greatest effects in the worst neighborhoods (see for example Crane 1991). Their effects are greatest for less educated individuals and for Hispanics. Although social characteristics have similar effects on blacks and whites, job locations have a greater 2 The data also oversample low income whites. The present study focuses on urban residents so this group, which is predominantly rural, is largely excluded from the analysis. 3 Our focus is on the contemporaneous effect of neighborhoods (as opposed to the effects of the neighborhood in which a person was raised). 3 effect on blacks4. This finding is consistent with a model in which black residences are constrained by discrimination. Our results also shed light on the question of how social influences operate. Labor market activity at the individual level is positively related to labor market activity of neighbors, but employment is not the only neighborhood characteristic that matters. We find that the effects of high public assistance income recipiency are comparable to those of low neighborhood employment. This finding suggests that the labor activity of neighbors per se may not be the crucial factor. We examine a variety of statistical models to determine the robustness of the finding that neighborhoods influence labor market choices, starting with weak controls for individual differences and introducing more thorough heterogeneity controls. We exploit the panel aspects of our data to control for both time invariant individual differences and individual differences in life-cycle profiles. Our results suggest that estimates of neighborhood effects that do not control for individual fixed effects, even those with a rich set of controls, overstate the social effect of neighborhoods by a factor of two to five. Job access generally has a negative impact on hours worked with incomplete controls for unobserved heterogeneity but a significantly positive effect with appropriate controls. This finding indicates that job access is an important determinant of labor attachment but that the neighborhoods with the best job access (i.e., those that are close to central business districts) generally attract individuals with low labor attachment. Even with these controls, our estimates may overstate the effect of neighborhoods if exogenous innovations in employment status affect the choice of neighborhoods. After 4 There is some evidence for stronger effects among immigrants, who tend to live in more 4 presenting our estimates, we assess this possibility by studying the timing of changes in work behavior around moves. In the case of neighborhood employment, there is little evidence for reverse causality, but the estimates for job access are more ambiguous. It is worth noting that our focus is on obtaining estimates of neighborhood effects that control for neighborhood selection, not on structural inference to distinguish between endogenous and exogenous neighborhood effects. While structural estimation is clearly of interest, it is impossible until neighborhood selection has been addressed. The next section contains a brief review of the existing literature. Section III describes the data set and its construction. Section IV presents the empirical analysis. Section V concludes. II. Existing Literature Both social interaction and spatial mismatch models have received considerable attention. The early literature on social interactions investigates a wide range of outcomes using a variety of methods. Datcher (1982) is among the early work that finds social effects of neighborhoods on labor market outcomes. Case and Katz (1991) find evidence for neighborhood effects on a variety of outcomes. O’Reagan and Quigley (1996) find that social influences and job access affect youth employment controlling for observed individual characteristics. Jencks and Mayer (1990a) survey the literature on social influences on children’s outcomes (also see Deitz 2000); Brooks-Gunn, Duncan, and Aber (1997a,b) and Jargowsky (1997) provide comprehensive views of neighborhood homogenous neighborhoods. 5 poverty; Haveman and Wolfe (1995) discuss the determinants of outcomes more generally. Borjas (1995) and Bertrand, Luttmer, and Mullainathan (1999) show that ethnic capital is an important determinant of adult outcomes, and that these effects are greatest for those living in neighborhoods with people of the same background. Looking across metropolitan areas, Cutler and Glaeser (1997) find that racial isolation reduces a variety of black outcomes including employment. In contrast to these studies, Corcoran, Gordon, Laren, and Solon (1992) find at most weak effects of neighborhoods on subsequent earnings. Page and Solon (1999) reach a similar conclusion after controlling for local labor market conditions during adulthood. Evans, Oates, and Schwab (1992) find that neighborhoods affect teenage fertility and dropout behavior when neighborhood behavior is treated as exogenous but not when it is treated as endogenous. More recently, researchers have begun to confront econometric issues in the identification of social interactions. Although many methodological questions remain, the work of Manski (1993), Duncan, Connell, and Klebanov (1997), Brock and Durlauf (1999), and Moffitt (1999) begin to address simultaneity, correlated unobservables and endogenous choice of neighborhood in a systematic framework. As indicated, the focus of the present study is to control for neighborhood selection, which is a precondition for structural estimation. The literature on spatial mismatch dates back to Kain (1968), who finds that as employers’ distance from black neighborhoods declines so does the fraction of jobs held 6 by blacks5. Much of the work on spatial mismatch exploits inter-neighborhood variation within a metropolitan area. In an influential study using this type of cross-neighborhood variation, Ellwood (1986) found only weak effects of job proximity on employment. More recent studies exploiting cross-neighborhood variation by Ihlanfeldt and Sjoquist (1990) and Raphael (1998) have supported the mismatch hypothesis. However, Conley and Topa (1999) present strong evidence of endogenous neighborhood choice within cities. Another strand of the literature exploits variation across metropolitan areas. Intercity tests of the mismatch hypothesis have generally been more supportive than crossneighborhood studies within a single metropolitan area (examples include Mooney (1969), Farley (1987); Ihlanfeldt and Sjoquist (1989); Cutler and Glaeser (1997); and Weinberg (1999, Forthcoming)) 6. Two points from the existing literature deserve particular attention. First, as discussed in the introduction, virtually all approaches to estimating the effects of social influences and job proximity have raised concerns with endogeneity. The primary concern in intra-city estimates pertains to endogenous neighborhood choice. Inter-city studies, which typically focus on the spatial mismatch hypothesis, have raised concerns with endogeneity in employer locations. Unfortunately, relatively few studies explicitly control for endogeneity (Plotnick and Hoffman (1995), Aaronson (1998), Cutler and 5 Although Leonard (1987) presents more recent evidence in support of his original findings, Offner and Saks (1971) dispute his results. 6 Harrison (1974), Vrooman and Greenfield (1980), and Price and Mills (1985) compare the wages of blacks living in central cities to those living in suburbs. Straszheim (1980) and Hughes and Madden (1989) compare the wages of blacks who work in the central city to those who work in the suburbs. Zax and Kain (1991), Rogers (1997), and Ross (1998) have looked at employment and residential mobility. 7 Glaeser (1997), Bertrand, Luttmer, and Miullainathan (1999), and Weinberg (1999, Forthcoming) are exceptions). Indeed, a number of recent studies have turned to experimental designs to obtain exogenous variations in neighborhoods to address these concerns (Ladd and Ludwig 1997, Rosenbaum, DeLuca, and Miller 1999, Katz, Kling, and Liebman 1999). While these studies are valuable, especially for policy purposes, they are less well suited to assessing the impact of naturally-arising variations in neighborhoods or the effect of neighborhood selection on the estimated effect of neighborhoods7. Second, the existing literature has made little attempt to ascertain the channels through which neighborhoods affect employment. The few studies that explore the link generally find social influences to have stronger effects than job access (Cutler and Glaeser (1997); O’Regan and Quigley (1992); and Conley and Topa (1999)). Only Weinberg (Forthcoming) finds stronger effects of job access. III. Data Description Sample Construction The primary data source for this study is the National Longitudinal Survey of Youth 1979 (NLSY79). The NLSY79 provides a comprehensive data set ideally suited for study of the determinants of early career employment status. The survey began in 1979 with a sample of 12,686 men and women born between 1957 and 1964. Annual interviews were conducted from 1979 to 1994, and biennially thereafter. Present within the NLSY79 data files are detailed longitudinal records of the employment history of each respondent. 7 Move to Opportunity studies must, at the moment, focus on short-term effects. 8 In order to construct a sample suitable for empirical analysis we introduce several selection criteria. We limit the sample to a subset of the 6,403 young men in the survey. Because our interest lies in post-schooling labor market activity we follow individuals from the time they leave school. The longitudinal structure of the NLSY79 allows one to determine precisely when most workers make a permanent transition into the labor force. Conceptually, we define the working career to begin the first time a respondent leaves formal schooling. To avoid counting summer breaks or other inter-term vacations as leaving school, we adopt the convention of defining a schooling exit as the beginning of the first non-enrollment spell lasting at least 12 consecutive months. Accordingly, respondents are excluded from the sample if the date of schooling exit cannot be clearly ascertained from the data. This occurs if the respondent is continuously enrolled throughout the observation period or there is incomplete or inconsistent schooling information. Table 1 provides a detailed summary of sample deletions. The number of males in the NLSY79 is 6,403. We delete the 824 individuals in the military sub-sample and another 746 who indicate military service at some time between 1979 and 1996. Since we follow respondents from the date of schooling exit, we delete 77 individuals for whom the date of schooling exit cannot be determined and another 11 for whom the highest grade completed cannot be determined. Our analysis is restricted to individuals living in a metropolitan statistical area (MSA). We require respondents to contribute at least 10 years of interviews while living in an MSA after leaving formal schooling. We lose 909 respondents who were interviewed less than 10 times after leaving school for at least 12 months. We lose 9 another 1255 respondents who did not live in an MSA at the date of interview for at least ten interviews. We delete another 799 respondents, residing in MSAs for at least ten years, for whom we can make an exact address match to the respondent’s latitude, longitude, and Census tract in at least 10 years. Additionally, require valid data for all other variables used in the analysis (excluding AFQT and Mother’s Education). This accounts for the loss of 82 additional respondents. Our final sample consists of 1646 young men satisfying each of the selection criteria. Table 1 demonstrates how racial composition, age in 1979, educational attainment and performance on the Armed Forces Qualifying Test (AFQT) change as we delete respondents who fail to satisfy various sample selection criteria. Performance on the AFQT may be particularly relevant to job readiness as it is a measure of trainability found by a number of authors to be positively correlated with wages. Requiring respondents to be interviewed at least 10 times after leaving school causes some changes in the racial mix and other characteristics of the sample. These changes arise because we lose a substantial fraction of the poor white oversample (PWOS), who were not interviewed after 1990.8 This requirement causes the fraction of the sample comprised of the PWOS to fall from over 13 percent to 10 percent. The fraction of the sample that is white falls from 54.5 percent to slightly less than 49 percent, with commensurate increase in the fraction of the sample that are black and Hispanic. We seem also to be losing somewhat 8 The poor white oversample was interviewed at most 12 times, while the cross section and black and Hispanic oversamples were interviewed up to 17 times by 1996. This population is most at risk to fail to satisfy the requirement of at least 10 interviews after leaving formal schooling for at least 12 months. Furthermore, they are more likely than other sample strata to reside outside of an MSA. 10 better educated respondents. There is a decrease in the average highest grade completed of 0.4 years. The recognized differences in AFQT scores by education level and the changing education mix of our sample account for the 3.5 percentage point drop in average AFQT score. The restriction that each respondent must be interviewed at least 10 times while residing in an MSA (after leaving school) causes a large decline in the fraction of respondents who lived in a rural area in 1979. There is also a decline in the fraction of the sample represented by the PWOS from 10 percent to around 6 percent, with consequent decreases in the fraction of the sample that is white and increase in the fractions of the sample that are black and Hispanic. However, the MSA residence restriction leaves relatively unchanged the average education and AFQT score. There are three remaining sample restrictions: (1) Valid address data for at least 10 years (while residing in an MSA after leaving school for at least 12 months), which allows us to identify census tract of residence and calculate job counts by distance to the respondents’ residence; (2) Valid data for all other variables used in the analysis, except AFQT score and mother’s highest grade completed; (3) The respondent must live within five miles of the nearest job reported at the zipcode level by the Economic Census.9 These restrictions have negligible effects on the average highest grade completed and 9 There are two possible reasons why someone residing in an MSA lives more than five miles away from the nearest measured job in the manufacturing, retail or service sectors. First, they may live in a rural portion of a county covered by an MSA. Alternatively, they may live near jobs that were reported to the Economic Census with bad zipcode data. About 10 percent of the jobs reported by the Economic Census are missing a zipcode. Observations with no jobs within 5 miles have been dropped from our analysis as probable outliers. 11 AFQT score.10 On the whole, although we implement stringent sample selection criteria, we experience only modest declines in education and AFQT scores.11 We do not believe that we have introduced serious sample selection bias as a result of our sample selection criteria. Summary Statistics Table 2 presents sample statistics, based on the person/years, for the variables used in this study. The dependent variable in our analysis is the natural logarithm of annual hours plus one divided by full week, full year hours, i.e. 40*52=2080. To create a measure of annual hours, we utilize the work history hours array, which contains the usual hours worked per week at all jobs from Jan. 1, 1978 through the final interview week.12 We then sum over all weeks in each calendar year to obtain a measure of annual hours. The person/year average highest grade completed in 11.7. Since the average highest grade completed for the 1626 individuals in the study is 12.1, respondents with lower levels of schooling are contributing disproportionately to the person/years in the sample. In other words, individuals with higher levels of education are contributing fewer years that those with lower levels of education. 10 The fraction of the sample accounted for by the PWOS declines, as does the overall fraction of the sample that is white. There is a disproportionate loss of whites who were residing in rural areas in 1979. 11 We lose too many of the PWOS to treat poor whites as a separate group, as we do with blacks and Hispanics. However, the largely rural white-poverty population is outside the scope of this study, which looks at labor force attachment among residents of large metropolitan areas. 12 The NLSY79 allows one to construct a weekly timeline of each respondent’s employment history. 12 Potential experience, age minus education minus 6, is on average 9.8 years. Blacks contribute 30 percent of the person/year observations and Hispanics contribute 24 percent of the observations. Immigrants, individuals born outside the U.S. and its territories to parents who are not themselves U.S. citizens, contribute 8.9 percent of the observations. To capture individual differences in ability and skill acquisition, we include the score from the Armed Forces Qualifying test (AFQT). AFQT scores are constructed from a subset of scores from the Armed Services Vocational Aptitude Battery (ASVAB) which was administered to 94% of the original NLSY79 respondents in 1980. The AFQT are used by the armed services to assign workers to various jobs within the military and are considered to be a useful measure of skills valued in the work place (Neal and Johnson, 1996). The AFQT score that we use in our regression analyses is adjusted for the age at which the respondent took the test. The test in designed and normed for individuals age 17 and above. Respondents took the test in 1980, when the youngest were aged fifteen. Individuals who took the test at age 15 and 16 perform 10 percentage points below the older respondents. To control for this, we use the cross section sample within the NLSY79 to construct birth year mean scores. We then take each respondent’s individual score and subtract from the birth year mean. The respondents in our sample include the oversamples of blacks and Hispanics, along with a handful of poor whites, who perform less well on the AFQT than a representative sample, like the cross section. Therefore, it is not surprising that the mean deviation in AFQT from birth year means is –10. Mother’s Education, defined as the highest grade completed by the respondent’s mother, is on average 10.57 years of schooling. Maternal education is often found to have 13 a statistically significant effect on child outcomes. We use it in this study to control for family background characteristics. Married refers to the current marital status of the respondent at the time of the survey and indicates that the respondent is married with spouse present. In our sample, respondents are married with spouse present in 37 percent of the sample years. The average number of respondent’s own children residing in the household is 0.4. This number is low due to the age range of the respondents, lack of marital stability, and tendency for children of divorce to reside with the mother. In the regression analysis we account for nonlinearities in the labor market impact of children by transforming this variable into the natural log of 1 plus the number of own children. The transformed variable has a mean of 0.34. In the process of geocoding the NLSY79, we obtained information on the Census tract in which each geocoded respondent lives. Tracts generally contain between 2500 and 8000 people. Tracts, when first delineated, were designed to include people who were homogeneous with respect to socio-econoomic characteristics. We merge neighborhood characteristics at the tract level from the summary tape files of 1990 Census. We use tract level employment rates of adult males and adult females as measures of the labor force activity of neighbors. The employment rate for adult males is 67 percent. The employment rate of adult females is 52 percent. We also use the fraction of adults who have a college diploma and the fraction of adults who are high school dropouts as two additional measures of social capital in a neighborhood. Since adults are on average older than the respondents in our sample, we classify these variables as proxies for role model influences, both positive and negative. On average, 17 percent of adults in the tracts have a college diploma, and 31 percent of adults in the tracts do not have a high school 14 diploma. We use the average poverty rate for persons aged 25-34, roughly the same age as the respondents in our sample, to proxy for negative peer influences. The average poverty rate for persons aged 25 to 34 in the block groups is 16 percent. Finally, we use the fraction of households receiving public assistance as a general measure of neighborhood disadvantage. Twelve percent of households are receiving income from public assistance. We use these neighborhood measures to proxy for variation in the social capital embodied in the respondent at each interview date. We expect that labor force attachment, measured by annual hours, will decrease as indicators of neighborhood disadvantage increase. IV. Empirical Results Estimation Strategy This section estimates the effect of neighborhood characteristics on labor activity. We start with a discussion of our estimation strategy before turning to our estimates. As emphasized, a concern with existing studies of neighborhood effects is that the choice of neighborhood is affected by unobserved characteristics. There are two fundamental approaches to this problem – to start with contaminated data and introduce controls for heterogeneity; or to identify and exploit an exogenous source of variation in neighborhoods. We have chosen the first approach in the absence of attractive instruments for neighborhood choice. To gauge the impact of individual heterogeneity on estimates of neighborhood effects and to enable the reader to assess the appropriate controls, we start with specifications with weak controls for individual heterogeneity and introduce more thorough controls. We then investigate the effectiveness of our controls by investigating changes in labor market activity around moves. 15 We exploit the longitudinal aspects of these data by estimating panel regressions. Consider a general model, y it = α it + X it β + N it γ + U itθ + ε it . Here, y it is the natural logarithm of annual hours plus one. We use a measure of annual hours to capture variations in the intensity of work conditional on the number of days/weeks the respondent worked. The individual’s observable characteristics at time t are given by X it . The characteristics of the neighborhood in which he resides at time t are given by N it . These are measured at the census-tract level. Estimates based on bock group-level data are similar to those reported here but are generally somewhat weaker. While there are likely to be variations even within narrowly defined neighborhoods, this finding suggest that social interactions operate across a reasonably large portion of a neighborhood. The unemployment rate at time t in i’s county of residence is given by U it 13. We consider three main specifications: OLS estimates, in which the intercept is constrained to be equal for all individuals ( α it = α ∀i, t ); fixed effects models, in which the intercept is allowed to vary across individuals but not over time ( α it = α i ∀t ); and fixed effects models that allow the effects of experience to vary across individuals14. The latter estimates are based on individual deviations from the typical experience profile 13 A portion of the sample (1.3% of respondent-years) is missing unemployment rates. A dummy variable is included for these observations. Results are similar with a state-level unemployment rate, which is available for all respondent-years. 14 Unmeasured neighborhood characteristics generate a correlation in the residuals from observations drawn from the same neighborhood. Our standard errors correct for this 16 where the strength of the common experience profile is allowed to vary across individuals. These estimates were generated in a three-stage procedure. First, we construct a typical experience profile for each variable (dependent and independent) by regressing it on a quadratic in experience using all person/year observations in the sample. Letting zit denote an arbitrary variable used in the analysis and eit denote years of potential experience, we estimate z it = φ1z + eit φ 2z + eit φ 3z + υ itz . 2 Predicted values of each variable are then obtained 2 zˆit = φˆ1z + eitφˆ2z + eit φˆ3z . To allow the effect of experience to vary across individuals, in the second stage individual-specific regressions were run in which each variable was regressed on an intercept and the typical experience profile for that variable as follows: zit = µiz + zˆitψ iz + ζ itz . The residuals from this regression were obtained. In the third stage regression, the estimates of which are reported below, each variable (dependent and independent) was replaced by its ζ itz , the deviation of that variable from its typical experience profile. 15 correlation. Our OLS standard errors also correct for the correlation in errors within individuals, which are estimated explicitly in the other specifications. 15 An alternative procedure would have been to allow for linear or quadratic experience profiles that vary across individuals. The present procedure allows for a more plausible functional form than a linear experience profile. Under the hypothesis that it is the strength of experience that varies across individuals, but that the shape of the experience profile is similar for most people, estimates from the current procedure should be similar to those that allow for individual quadratic effects. The current procedure preserves more degrees of freedom and somewhat more variation in the independent variables than the latter. Consistent with this hypothesis, the present procedure generates point estimates 17 We also address the econometric issue raised by censoring in the data. Formally, the data have a tobit structure. A modest portion of the sample (7.4% of respondentyears) report zero hours worked. The appendix table reports OLS and tobit estimates with (non-logged) full-time equivalent weeks as the dependent variable with and without fixed effects (the latter were estimated using an estimator developed by Honore (1992)). As expected, the tobit estimates yield somewhat greater effects than OLS, but the two estimates are qualitatively similar. Given the modest difference and our interest in introducing as rich a set of heterogeneity controls as possible, the remaining analysis employs OLS. Baseline Estimates Our initial measures of neighborhood characteristics are the employment rate of adult men in the neighborhood and the log of the number of manufacturing, service, and retail jobs within a five mile radius of the respondent (weighted by the inverse of distance from the respondent’s residence)16. Adult employment is intended to capture social influences. To the extent that neighbors are an important source of information about job opportunities, neighborhood employment rates will also affect available information (as in Granovetter 1995). Most likely, adult employment will also reflect variations in job access that are orthagonal to the job proximity measure. that are quite close to those that allow for individual quadratics but standard errors that are substantially lower. 16 To control for differences in job densities across MA’s, the density is expressed as the log deviation from the mean in the MSA/CMSA. Non-differenced estimates are similar. To control for variations in the supply of labor to different parts of the MA’s, we have also estimated population densities for working age individuals. Including the population 18 Table 3 reports estimation results. Our first model suppresses the individual fixed effects ( α it = 0 ∀it ) and includes a limited set of controls (education, a quadratic in potential experience, and dummy variables for race and Hispanic background). The implied effects of a one standard deviation change in the neighborhood variables are reported in brackets beneath the estimates and standard errors. A one percentage point increase in adult male employment raises full time equivalent weeks by 2.7%. Contradicting the spatial mismatch hypothesis, individuals living in areas that are closer to jobs work less than those that are far from jobs. Education and experience both raise work. Blacks work substantially less than observationally equivalent whites. Individuals with a Hispanic background work slightly less than non-Hispanic whites. A 1 percentage point increase in county unemployment reduces full-time equivalent weeks by .043%. The second specification includes a richer set of time-invariant control variables (AFQT, mother’s education, and immigrant status). Including this richer set of controls reduces the estimated effect of both neighborhood variables somewhat. Higher AFQT scores are associated with more work; an increase in mother’s education is associated with a reduction in work (this result is weakened if AFQT is removed from the model). Immigrants work more than non-immigrants. The third specification returns to the more simple first specification but includes two time varying (and potentially endogenous) controls, marital status and the natural logarithm of (one plus) the number of own children present. The effects of adult male employment are comparable to those in the first specification. With these time-varying density as a separate regressor or measuring job density using the log difference between 19 controls, job proximity takes on the expected positive sign. As expected, married men and men with more own children present work more. The fourth specification includes the full set of time-invariant and time-varying controls. The coefficient on neighborhood employment in this specification is lower than in the previous specifications. The effects of job locations increase somewhat. The standard deviation across neighborhoods of the employment rate and the job proximity measure are .127 and 1.050 respectively. Given these estimates, a one standard deviation increase in neighborhood employment raise full time equivalent weeks by 27% while job proximity leads to an increase of 1.1%. Thus, estimates that control for individual heterogeneity using a rich set of control variables imply very large social effects of neighborhoods but a weak or even negative effect of job proximity. If neighborhood amenities are normal goods, one would expect individuals with higher labor attachment and hence higher incomes to choose to live in better neighborhoods. Similarly, individuals with strong labor attachment have the most to gain from living in neighborhoods with good job access. On the other hand, individuals with weak labor attachment may be attracted to the older neighborhoods near central business districts. To control for time-invariant individual differences in attachment that affect neighborhood choices, specifications 5 and 6 include individual fixed effects (these regressions are “within” regressions estimated by taking deviations from individual means). After eliminating individual fixed effects, the variance in the neighborhood variables is one quarter of the raw variance. job and population densities produces estimates that are similar to those presented here. 20 Controlling for fixed individual differences reduces the relationship between neighborhood employment rates and work by two-thirds compared to the corresponding OLS estimates. Thus, a correlation between unobserved fixed individual characteristics and neighborhood characteristics accounts for the majority of the social “effects” of neighborhoods estimated using OLS. On the other hand, including fixed effects makes the effect of job proximity positive and significant, economically and statistically. This finding indicates that OLS estimates of the effect of job locations are biased down because of a tendency for low attachment workers to cluster in neighborhoods that are close to jobs17. Thus, it appears that estimates of the mismatch hypothesis that use crossneighborhood variation in job access risk understating the true effects of neighborhoods. Based on these estimates, annual hours worked are increased by 10% by a one standard deviation increase in neighborhood employment and by 4% by a one standard deviation increase in job access. The between estimator (reported in column 7) is of interest in that it corresponds most closely to the estimator that would be obtained from pure cross-sectional data. The estimates for neighborhood employment exceeds the other estimates by a considerable margin, again indicating that naïve estimates of social interactions substantially overstate the true effects. Similarly, the between regressions shows markedly lower effects for job 17 Regressions of job density on distance from the central business district (measured using the location of the county courthouse of the central city or the central city of the main PMSA in a CMSA) show that job densities decline with distance from the business district. The same result holds true for manufacturing job densities. 21 access. The GLS estimates in column 8 are efficient under the hypothesis that unobserved individual characteristics are orthogonal to neighborhood characteristics18. Individuals may exhibit different growth rates in labor attachment as well as timeinvariant differences. Individuals experiencing the greatest increases in labor force attachment might be expected to upgrade their neighborhoods more rapidly than others. To control for this possibility, the estimates in columns 9 and 10 allow for differences in experience effects across respondents as well as time-invariant individual differences. The estimates of neighborhood employment are somewhat beneath the fixed effects estimates, however the effects of job locations are comparable to those that only include individual fixed effects. This reduction in social interactions is consistent with dynamic selection on the basis of unobserved time-varying characteristics. On the other hand, it is well known that the reduction in variance in the independent variables from fixed effects estimates biases such estimates downward (see, for example, Griliches and Hausman 1986). These estimates, which exclude 85% of the raw variance and 40% of the variance available in the fixed effects, are likely to suffer from attenuation bias. Most likely, the true effects, lie between these estimates and the fixed effects estimates. These estimates imply that a one standard deviation increases in neighborhood employment and job proximity raise annual hours by 6% and 4% respectively. 18 A Hausman test for the hypothesis that the individual fixed effects are uncorrelated with the explanatory variables yields a chi-square statistic of 175.95 with 5 degrees of freedom, yielding a p-value beneath .0001. 22 A Variety of Neighborhood Characteristics The preceding estimates indicate that neighborhoods exert a strong influence on individual work decisions. This section reports estimates based on other measures of neighborhood characteristics for three of the previous specifications (those in columns 4, 6, and 10 of table 3). The purpose of the analysis is to probe the sensitivity of the preceding resultsand provide some evidence on the channels through which social influences operate. We examine two additional variables. We use the employment rate of adult females as a second employment variable, to test the robustness of our finding for the adult male employment rate. If there are informational externalities to job holding, living in a neighborhood with higher employment rates of females, as well as males, should raise labor force attachment. We contrast the effects of employment with that of a measure of general social disadvantage. For this purpose, we use the fraction of households with public assistance income. Table 4 reports regression results including one neighborhood variable in each regression. For comparison purposes we also report results in which male labor force participation and proximity to jobs are separately included. OLS estimates with a rich set of controls (reported in column 1) show a strong relationship between neighborhood social characteristics and employment rates. The implied effects of a one standard deviation change in each variable (reported in brackets) are generally quite large. Column 2 reports fixed effects estimates (using deviations from individual means). As above, introducing fixed effects greatly reduces the implied social effect of neighborhoods. The implied effects are between one half and one quarter of the corresponding OLS estimates. Based on these estimates, there is little question that 23 estimates of the social effects of neighborhoods that fail to control for fixed individual differences risk overstating these effects. Column 3 reports estimates that allow for inter-personal differences in the strength of experience as well as individual fixed effects. These estimates are beneath the comparable fixed effects estimates. All social variables have the expected signs, but only the estimates for adult male employment are statistically significant. The implied effect of a one standard deviation change in each variable range from 3.7% for women’s employment to 5.2% for recipiency of public assistance income to 5.6% for men’s employment. The ordering of the implied effects for the various measures is fairly stable across specifications. The finding that female employment increases the labor force attachment of the men in our sample leads us to conclude that employment in general is one channel through which neighborhoods affect labor activity, as would be the case if job information from working neighbors was responsible for the effects. The finding that the “effect” of public assistance recipiency is comparable to that of adult male employment suggests that employment status, per se, may not be the only channel though which neighborhood effects operate. Non-Linearities and Interactions with Individual Characteristics The effects of neighborhoods are, most likely, not uniform. They may be greatest in the neighborhoods at the extreme low end of the distribution (Wilson 1987, 1991, Crane 1991, Galster, Quercia, and Cortes 1999, Krauth 2000). The effects of neighborhoods are also likely to be greatest for individuals who are closest to the margin to work. We examine these hypotheses by including higher order terms in the neighborhood 24 characteristics and interacting the neighborhood characteristics with individual characteristics. The estimates reported are based on models that control for individual fixed effects. Our estimates indicate that neighborhoods have the greatest effects in the worst neighborhoods, on Hispanics, and on those with less education. While the social interactions variables are comparable for blacks and whites, the effects of job locations are greater for blacks. Table 5 reports the results. The first two columns show the effect of including a second order term in the neighborhood measures19. For the social measures, the sign on the squared term indicates that neighborhoods have the greatest effects at the low end of the distribution. Thus, employment of men and women have positive effects at low levels and weaker effects at higher levels. Negative linear and higher order terms indicate that the effects of public assistance recipiency are greatest at high levels. There is no evidence that job access has a non-linear effect. While of interest in their own right, the presence of non-linearities may also assist in structural estimation. Table 6 reports interactions with individual characteristics. Interactions with education (reported in the first set of columns) uniformly indicate that the social effects of neighborhoods are greatest at low levels of education. Two additional years of school (beyond 12) eliminates all effects. Similarly, the effects for someone with only 10 years 19 Another way of seeing the non-linearity is by comparing the effect of adult education measured at different points in the distribution. Despite being highly correlated, results not reported here indicate that the implied effect of a one standard deviation change in the fraction of the adult population that are high school dropouts exceeds that for high school graduates, which exceeds that for college graduates. Thus, work is especially sensitive to the bottom end of the education distribution. 25 of completed school (less than a standard deviation beneath the mean) are between one third and five times greater than for someone with 12 years of school. There are no consistent differences in the social effect of neighborhoods on blacks relative to whites (in the second set of columns; see Duncan, Connell, and Klebanov 1997 on this point). While the point estimates do not differ systematically, social influences do contribute to black-white employment differentials because blacks tend to live in neighborhoods with worse characteristics than whites. The estimates indicate that the effects of job access among blacks are double the effects among non-blacks, although the difference is not statistically significant. This finding is consistent with a model in which residential segregation limits blacks’ residential choices20. The estimates for the social variables indicate that social influences have a larger effect on Hispanics, who may live in more homogeneous neighborhoods than on non-Hispanics. Job locations are less important for Hispanics. Similarly, immigrants often cluster in homogenous neighborhoods with tight communities, which might generate stronger social effects among immigrants (see Borjas 1995 and Bertrand, Luttmer, and Mullainathan 1999). Estimates (not reported here) do indicate somewhat greater social effects on immigrants, but these differences are not statistically significant because immigrants constitute only 9% of respondent-years. Reverse Causality An obvious concern with our estimates is that exogenous changes in employment status may lead to changes in neighborhoods rather than the reverse. This possibility is hard to 26 rule out. Nevertheless, it is possible to assess the importance of reverse causality by examining the timing of changes in employment status relative to changes in neighborhood characteristics. A finding that employment rates increase in the years leading up to moves into better neighborhoods would suggest that exogenous changes in employment status are an important determinant of neighborhood choice and that the preceding estimates may be biased upward. While not dispositive, a finding that employment rates are constant or declining prior to moves into better neighborhoods would undermine the reverse causality argument. For this analysis, we regress work behavior on leads and lags of changes in neighborhood characteristics. The specification controls for individual fixed effects and allows for individual-specific experience effects in the manner described above. Formally, [ ] y it = α it + X it β + ∑ s = −7 φ s Moved i (t + s ) + ψ s ∆ i (t + s ) + ε it ∆ i (t + s ) ≡ N i ( t + s ) − N i ( t + s −1) 7 Here Movedit denotes a set of dummy variables for whether the respondent moved between years t-1 and t, which control for the direct effect of moving, and ∆ it denotes the change in the respondent’s neighborhood characteristics between periods t and t-1 (this variable is, by construction, equal to zero if the respondent did not move)21. Only variables corresponding to the next and previous move are included.22 20 For example, Holzer and Ihlanfeldt (1998) document reluctance on the part of retailers to hire blacks to work in stores that primarily service non-black customers. 21 The timing of moves is not available from the survey. The preceding analysis was based on a sample that measured employment over the calendar year. This structure was chosen because most surveys occur during the summer, so that if moves occur midway 27 Figure 1a plots the effect of moving to a neighborhood with 1 standard deviation higher adult male employment (ψ s σ Neigh. Emp. ) along with 2-standard error confidence bands23. The figure also shows the estimates when the effects of moves are assumed to be piecewise linear with a break in the year of the move. For people who will move into a neighborhood with a higher employment rate, the estimates indicate that hours decline in the years leading up to the move. After a move into a high employment neighborhood, hours trend upward. Taking time in the neighborhood as an indicator of integration into neighborhood networks, the effect of being in a high employment neighborhood is greatest after people have become more integrated into their neighborhoods. These estimates provide no support for the hypothesis that people who are moving into better neighborhoods are increasing their hours prior to their moves. There is clear evidence, however, for a positive break in the trend in annual hours after moves to better neighborhoods24. Figure 1b, shows changes in hours around moves into neighborhoods with improved job access. For people who will move into high job density neighborhooods, annual hours exhibit a large decline between seven and four years prior to the move and between interviews on average, the calendar year will best reflect the place of residence. For this analysis, we estimate employment over the survey year to bracket moves. 22 If, for example, a person moves in two consecutive years the variables corresponding to the first move are set to zero until after the first move occurs. Once the second move occurs the variables for the first move are set to zero. This procedure ensures that the effects of changes in characteristics are not estimated from people who are no longer living in a neighborhood. 23 These estimates net out the direct effect of moving. More precisely, they give the effect of moving from one neighborhood to another with one standard deviation higher adult male employment relative to moving between neighborhoods with the same employment. 28 then show an increase between four years before and the year before the move, although they remain beneath their initial level. Hours continue to increase after the move. While the increase in employment in the year prior to the move suggest that endogenous neighborhood choice may bias our estimates upward, the prolonged decline in the preceding years indicates a long-term downward trend in labor activity for people who move into neighborhoods with better job access, which may indicate that our estimates are biased down25. To further probe these results, Figure 1c presents analogous estimates for a model with fixed effects, but without individual-specific experience profiles. These estimates indicate that the people who are moving into high job density neighborhoods are those for whom annual hours are trending downwards over a long horizon – hours decline between 7 and 4 years before the move and from 2 years after the move onward, with an increase in the intervening years. When the individual-specific experience profiles are included to control for the underlying downward trend, there is a tendency for hours to increase in the few years before and after the move. Thus studying the timing of changes in hours worked around moves provides little evidence that annual hours are increasing prior to moves into high employment neighborhoods, but clear evidence for a positive break in trend after the move. Estimates for job density indicate that annual hours are on a long-term downward trend for people who move into high job density neighborhoods, but that hours increase in the few preceding and following years. 24 The negative trend before the move and the positive trend after the move are not statistically significant, but the difference in trends is significant at the 5% level. 29 V. Conclusion Researchers have argued that neighborhoods affect labor attachment as well as other youth outcomes. Such effects may stem from social interactions or job proximity. Estimates generally suggest that such effects are present, but have raised concerns with endogenous neighborhood selection. Using confidential administrative data, respondents to the NLSY79 were linked to measures of neighborhood social characteristics at the census tract level from the 1990 Census and measures of job proximity estimated from the 1987 Censuses of Manufacturing, Retail Trade, and Services. Social influences and job proximity are both important determinants of employment status. A one standard deviation increase in the social characteristics of a neighborhood increases annual hours by 6%; a similar increase in job proximity raises hours by 4%. Social interactions have non-linear effects with the greatest impact in the worst neighborhoods. Neighborhoods also exert a greater influence on less educated workers and Hispanics. Consistent with a model in which black residential decisions are constrained by discrimination, job locations are more important for blacks than nonblacks. We find relationships between a variety of neighborhood social characteristics and work indicating that being in a disadvantaged neighborhood is important but that the labor activity of neighbors per se may not be the crucial factor. The analysis indicates that estimates that do not account for neighborhood selection on the basis of time-invariant unobserved individual characteristics substantially overstate the social effects of neighborhoods but understate the effects of job access. We study the direction of causality 25 Imposing linear trends before and after the move yield estimates that are essentially 30 by looking at the timing of employment changes around neighborhood moves. 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Chicago: University of Chicago Press, 1987. Wilson, William Julius. When Work Disappears: The World of the New Urban Poor. New York: Alfred A. Knopf, 1996. Zax, Jeffrey; and John F. Kain. “Commutes, Quits, and Moves.” Journal of Urban Economics 29 (1991), 153-165. 36 Figure 1. Annual Hours Around A Move to a High Employment Neighborhood, Fixed Effects with Individual-Specific Experience Profiles. Deviation of Log Annual Hours from Trend 0.2 0.15 0.1 0.05 0 -7 0 7 -0.05 -0.1 Time from Move (Move between -1 and 0) Note. Two standard error bounds shown. Figure shows the effect on log full time equivalent weeks of moving to a neighborhood with an adult male employment rate one standard deviation above the mean level from one with an employment rate equal to the mean between years –1 and 0. Estimates controls for marital status, the log of one plus the number of own children present, the unemployment rate in the county, years prior to / since move, individual fixed effects, and allow for individual differences in the strength of experience profiles. 37 Figure 2. Annual rs Around A Move to a Neighborhood with better Job Access, Fixed Effects with Individual-Specific Experience Profiles. Deviation of Log Annual Hours from Trend 0.08 0.06 0.04 0.02 0 -7 -0.02 0 7 -0.04 -0.06 -0.08 Time from Move (Move between -1 and 0) Note. Two standard error bounds shown. Figure shows the effect on log full time equivalent weeks of moving to a neighborhood with one standard deviation more jobs within a five mile radius (in logs) from one with the mean number of jobs within five miles between years –1 and 0. Estimates controls for marital status, the log of one plus the number of own children present, the unemployment rate in the county, years prior to / since move, individual fixed effects, and allow for individual differences in the strength of experience profiles. 38 Deviation of Log Annual Hours from Trend Figure 3. Annual Hours Around A Move to a Neighborhood with better Job Access, Fixed Effects Only. -7 0.12 0.1 0.08 0.06 0.04 0.02 0 -0.02 0 -0.04 -0.06 -0.08 -0.1 7 Time from Move (Move between -1 and 0) Note. Two standard error bounds shown. Figure shows the effect on log full time equivalent weeks of moving to a neighborhood with one standard deviation more jobs within a five mile radius (in logs) from one with the mean number of jobs within five miles between years –1 and 0. Estimates controls for marital status, the log of one plus the number of own children present, the unemployment rate in the county, years prior to / since move, and individual fixed effects. 39 TABLE 1 Sample Selection Criterion White Poor Rural White Residence Over – in 1979 Sample Male respondents in NLSY79 6043 0.191 0.115 0.592 0.252 0.156 18.4 After deletion because military subsample 5579 0.216 0.132 0.570 0.260 0.170 18.0 12.5b 39.3e After deletion because ever served in military 4833 0.217 0.136 0.577 0.246 0.177 18.1 12.5c 39.0f After deletion because no school exit date or no HGC data 4745 0.218 0.136 0.576 0.247 0.177 18.1 12.5 39.0g After deletion because interviewed less than 10 years after date if school exit After deletion because less than 10 years living in MSA, based on NLSY79 geocode limited public release data After deletion because less than 10 years valid lat-longs 3836 0.221 0.098 0.545 0.267 0.188 18.2 12.1 36.5h 2581 0.101 0.057 0.485 0.297 0.218 18.3 12.2 36.6i 1782 0.101 0.025 0.463 0.299 0.238 18.4 12.1 36.5j After deletion because less than 10 years with valid data for all other variable of analysis (except AFQT and Mother’s education) Final sample after deletion because less than 10 years with positive job counts within a 5 mile radius 1700 0.086 0.025 0.463 0.299 0.238 18.7 11.8 36.8k 1679 0.075 0.026 0.462 0.301 0.237 18.7 11.8 36.8l N Black Hispanic Age in 1979 AFQT Raw Percentile Score Highest Grade Completed At time of first leaving school for at least 12 months 12.5a Reason for deletion from sample a N = 6,390 b N = 5,567 c N = 4,822 d N = 5,951 e N = 5,212 f N = 4,524 g N = 4,470 h N = 3,650 i N = 2,457 j N = 1,709 k N = 1,632 l N = 1,612 40 40.9d Table 2 Summary Statistics of Final Sample of Person/Years Mean Individual Characteristics (NLSY79) Annual Hours/2080 Highest Grade Completed Experience Black Hispanic Immigrant AFQT (deviation from cross section birth year mean) Mother’s Education Married Spouse Present Log(1 + Own Children Present) Year .775 11.753 9.841 .306 .242 .089 -9.929 10.596 .372 .336 87.9 Std. Dev. .343 2.185 5.126 .461 .428 .285 23.179 3.334 .483 .504 4.66 Neighborhood Characteristics (1990 Census) Employment Rate of Adult Males .673 .127 Employment Rate of Adult Females .520 .116 Fraction of Households with Public Assistance Income .118 .114 Proximity to Jobs (1987 Economic Census) Log Number of Jobs Weighted by Inverse of Distance 9.636 1.050 Note: All variables have 21,584 observations except mother’s education, which has 19,976 observations, and AFQT, which has 20,841 observations. 41 Table 3. Effect of Adult Male Employment and Job Proximity on Log Annual Hours. (1) (2) (3) (4) (5) (6) (7) OLS OLS OLS OLS Within Within Between Employment Rate of Adult Men 2.689 2.215 2.551 2.098 .795 .775 3.685 (.306) (.297) (.298) (.289) (.200) (.196) (.384) [.342] [.281] [.324] [.266] [.101] [.098] [.468] -.011 Log Number of Jobs Weighted by -.021 .034 -.012 .039 -.001 -.017 (.029) Inverse of Distance (.030) (.014) (.029) (.014) (.029) (.040) [-.012] [.036] [-.022] [-.013] [.041] [-.001] [-.018] Education .116 .040 .098 .025 .125 (.015) (.021) (.015) (.021) (.018) Experience .080 .093 .035 .051 .093 .076 -.012 (.016) (.015) (.015) (.015) (.012) (.012) (.085) Experience2 -.005 -.005 -.003 -.004 -.006 -.005 .001 (.0007) (.0007) (.0007) (.0007) (.0005) (.0005) (.004) Black -.612 -.276 -.536 -.214 -.367 (.082) (.103) (.090) (.102) (.089) Hispanic -.074 -.063 -.129 -.101 -.150 (.077) (.095) (.076) (.092) (.084) AFQT .016 .015 (.003) (.002) Mother’s Education -.033 -.029 (.013) (.012) Immigrant .275 .246 (.119) (.114) Married .419 .370 .167 .570 (.055) (.057) (.035) (.141) Log(1+Own Children) .253 .262 .089 .377 (.057) (.059) (.040) (.132) County Unemployment Rate -.043 -.048 -.044 -.049 -.056 -.057 -.012 (.010) (.010) (.009) (.010) (.006) (.007) (.017) Missing Unemployment Rate -.252 -.333 -.225 -.303 -.390 -.395 .307 (.160) (.169) (.158) (.167) (.126) (.122) (.642) Individual Fixed Effects No No No No Yes Yes – Deviations from IndividualNo No No No No No No Specific Time Trends R2 .112 .125 .130 .142 .526 .527 .258 Number of Observations 21,584 18,920 21,584 19,356 21,584 21,584 21,584 42 (8) GLS 1.207 (.139) [.153] .027 (.015) [.028] .116 (.015) .067 (.008) -.005 (.000) -.755 (.076) -.152 (.081) (9) Deviat. .485 (.223) [.062] .034 (.016) [.036] (10) Deviat. .478 (.123) [.061] .035 (.016) [.037] 1st Stage 1st Stage 1st Stage 1st Stage .220 (.035) .124 (.035) -.056 (.005) -.384 (.103) Yes No -.044 (.006) -.384 (.108) Yes Yes .066 (.034) .049 (.045) -.044 (.006) -.382 (.108) Yes Yes .105 21,584 .606 21,584 .606 21,584 Note: Standard errors in parentheses. Standard errors correct for within-neighborhood correlation in residuals. OLS standard errors also correct for within-person correlation in residuals. Absolute value of the implied effect of a one standard deviation change in brackets. Independent and dependent variables in deviations from individual-specific time trend regressions use residuals from separate regressions on a quadratic in experience for each respondent. 43 Table 4. Estimates of Various Neighborhood Characteristics on Annual Hours. Employment Rate of Adult Men Employment Rate of Adult Females Fraction of Households with Public Assistance Income Log Number of Jobs Weighted by Inverse of Distance 2.077 (.189) [.265] 1.792 (0.280) [.208] -2.778 (.415) [-.316] -.033 (.029) [-.035] Yes Yes .761 (.195) [.097] .589 (.191) [.068] -.780 (.276) [-.089] .029 (.014) [.030] Yes - .443 (.223) [.056] .323 (.205) [.037] -.458 (.309) [-.052] .030 (.016) [.032] 1st Stage - Includes a Quadratic in Experience Includes Education, Race, Hispanic Background, AFQT, Mother’s Education, and Immigrant Status Includes Marital Status and Log(1+Own Yes Yes Yes Children) Includes Individual Fixed Effects No Yes Yes Includes Individual Specific Age Profiles No No Yes Observations 19,356 21,584 21,584 Note. Standard errors in parentheses. Standard errors correct for within-neighborhood correlation in residuals. OLS standard errors also correct for within-person correlation in residuals. Absolute value of the implied effect of a one standard deviation change in brackets. Estimates are from separate regressions for each independent variable. 44 Table 5. Non-Linearities in Neighborhood Characteristic Main Effect Squared Term 2.166 -1.174 Employment Rate of Adult Men (0.154) (0.849) Employment Rate of Adult Women 2.120 (.752) -1.543 (.724) Fraction of Households with Public Assistance Income -0.439 (0.491) -0.673 (1.181) Log Number of Jobs Weighted by Inverse of Distance 0.030 (0.018) 0.0009 (0.007) Note. Standard errors, which correct for within-neighborhood correlation in residuals, in parentheses. A separate regression was run for each neighborhood characteristic. Regressions also include individual fixed effects, education, a quadratic in potential experience, marital status, and log(1+number of own children present). Sample contains 21,584 observations. 45 Table 6. Neighborhood Characteristics Interacted with Individual Characteristics Model 1 Model 2 Neighborhood Characteristic Neighborhood Characteristic Interacted with Interacted with Education - 12 Black and Hispanic Background Main Effect Interaction Main Effect Interaction Interaction with Education with Black with Hispanic Employment Rate of Adult Men .594 -.359 .506 .102 .808 (.179) (.090) (.214) (.409) (.429) Employment Rate of Adult Women 0.487 (.178) -0.208 (.088) .376 (.187) .084 (.437) .571 (.381) Fraction of Households with Public Assistance Income -.529 (.273) .229 (.129) -.084 (.409) -.729 (.582) -.950 (.609) Log Number of Jobs Weighted by Inverse of Distance .028 (.015) .003 (.007) .036 (.015) .030 (.053) -.048 (.032) Note. Standard errors, which correct for within-neighborhood correlation in residuals, in parentheses. Separate regression were run for each neighborhood characteristic. Estimates for interactions with education from one regression. Interactions with black and Hispanic background from a second regression. Regressions also include individual fixed effects, education, a quadratic in potential experience, marital status, and log(1+number of own children present). Sample contains 21,584 observations. 46 Appendix Table. Linear and Tobit Models of Annual Hours. Estimation Strategy: Linear Model Tobit Employment Rate of Adult Men .422 .157 .469 .164 (.027) (.032) (.029) (.053) Log Number of Jobs Weighted by -.005 .009 -.005 .011 Inverse of Distance (.003) (.003) (.003) (.004) Education .011 .011 (.002) (.002) Experience .035 .044 .036 .049 (.002) (.002) (.002) (.003) Experience2 -.002 -.002 -.002 -.003 (.000) (.000) (.000) (.000) Black -.060 -.063 (.008) (.009) Hispanic -.036 -.037 (.009) (.009) AFQT .003 .003 (.000) (.000) Mother’s Education -.005 -.006 (.001) (.001) .054 Immigrant .048 (.011) (.012) Married .118 .045 .123 .044 (.008) (.008) (.008) (.010) County Unemployment Rate -.014 -.013 -.014 -.014 (.001) (.001) (.001) (.002) Missing Unemployment Rate -.071 -.098 -.077 -.101 (.026) (.022) (.027) (.027) Log(1+Own Children) .037 .006 .044 .013 (.008) (.008) (.008) (.011) Includes Fixed Effects No Yes No Yes R-squared .178 .063 2 Note: Standard errors in parentheses. Reported R for fixed effects regression excludes variance explained by fixed effects. 47