Employment of Low-Income African American and Latino Teens: Does Neighborhood Social Mix Matter?

Abstract

We quantify how teen employment outcomes for low-income African Americans and Latinos relate to their neighborhood conditions during ages 14–17. Data come from surveys of Denver Housing Authority (DHA) households who have lived in public housing scattered throughout Denver County. Because DHA household allocation mimics random assignment to neighborhood, this program represents a natural experiment for overcoming geographic selection bias. Our logistic and Tobit regression analyses found overall greater odds of teen employment and more hours worked for those who lived in neighborhoods with higher percentages of pre-1940 vintage housing, property crime rates and child abuse rates, though the strength of relationships was highly contingent on gender and ethnicity. Teen employment prospects of African Americans were especially diminished by residence in more socially vulnerable, violent neighborhoods, implying selective potential gains from social mixing alternatives.

Keywords::

• neighborhood effects
• teen employment
• social mix
• logistic regression
• natural experiments

Acknowledgements

This research was supported by grants from the National Institute of Child and Human Development [5R01 HD47786-2], the U.S. Department of Housing and Urban Development, MacArthur Foundation, Annie E. Casey Foundation, and W.K. Kellogg Foundation. The opinions expressed herein do not necessarily reflect those of our funders. Profs. Tama Leventhal and Xiaoming Li served as expert advisors to this project. Stefanie DeLuca, Lisa Gennetian, David Harding, Jens Ludwig, Jeff Morenoff, and seminar participants at the University of Michigan and Glasgow University contributed helpful conversations related to our analytical strategy. The authors also gratefully acknowledge the programming assistance of Dr. Albert Anderson and the research assistance of Andy Linn, Kim Kostaroff, Georgios Kypriotakis, Rob Mehregan, Ana Sanroman, and Lisa Stack.

Notes

¹ We acknowledge that working as a teen is a double-edged sword. It appears that to hold a job is good but working more than 20 hours weekly is not, given the longstanding evidence on the deleterious effects on high school academic performance of working excessive hours (Mortimer, 2010; Steinberg and Dornbusch, 1991; Steinberg et al., 1993; Sum et al., 2006; Warren et al., 2000).

² The direction of the bias has been the subject of debate, with Jencks & Mayer (1990) and Tienda (1991) arguing that neighborhood impacts are biased upwards, and Brooks-Gunn et al. (1997) arguing the opposite. Gennetian et al. (2011) show that these biases can be substantial enough to seriously distort conclusions about the magnitude and direction of neighborhood effects.

³ For a review of this literature, see DeLuca & Dayton (2009).

⁴ Non-experimental analysis focusing on MTO families who resided for a majority of the study period in low-poverty and/or higher education neighborhoods revealed their substantially better adult employment and earnings than in the control group (Turner et al., 2012).

⁵ Of the post-1986 vintage tenants residing in conventional public housing developments at the time of the Denver Child Study interviews, 99 per cent were originally placed in such; only one per cent moved in from dispersed housing. Of the post-1986 vintage tenants residing in dispersed housing at that time, 94 per cent were originally placed in such; six per cent moved in from the conventional developments. Moreover, an unknown number of these transfers were involuntary, required by regulations after changes in family size or composition.

⁶ Slightly more than one-third of all caregivers interviewed in the study were former DHA residents.

⁷ Or, if the teen was younger than 18 at time of survey, a majority of years between age 14 and time of survey.

⁸ These criteria yielded an initial sample of 4323 current and former DHA residents. Respondent data obtained from the DHA database were updated using several DHA internal databases to verify current contact information. These data were cross-verified using an array of automated search engines (Anchor, Intellius, and Lexis-Nexis) as well as several Internet-based people search and telephone directories (e.g., Anywho). These additional search engines identified deceased residents (N = 80 or 1.9 per cent). Telephone screening and on-site canvassing by study interviewers identified households that did not meet study eligibility criteria (N = 51 or 1.2 per cent), households whose primary language was neither English nor Spanish (N = 15 or 0.3 per cent), and households that did not have working telephones (406 or 9.4 per cent). Return mail from the Post Office accounted for 1534 or 35.5 per cent of the initial sample households, primarily comprising former DHA residents. Another 804 households or 18.6 per cent of the initial sample households had both return mail and non-working telephones. This reduced the number of “reachable” households in the final sample to 1433.

⁹ This criterion was imposed to insure that even the youngest children analyzed in this paper had at least a year of exposure to the quasi-randomly assigned neighborhood, the characteristics of which were used as predictors of teen employment outcomes.

¹⁰ We also assessed caregiver gender; virtually, all were female so it is not included as a covariate. The average interval between interview date age 18 for focal teens was 3 years (ranging from 0 to 12 years). While subject to recall bias, we would posit that caregivers would be able to remember if a child was working during high school years and generally how long; they would be more likely to have problems remembering teens' income, which we did not request.

¹¹ We use a dummy variable indicating whether the parent exhibited sub-clinical or clinical depressive symptomatology (score at least 16 on the CES-D scale); Radloff (1977).

¹² The depression scales was the exception, measured at time of survey. All other variables are measured annually, so values are averaged over the four years corresponding to focal teens' ages 14–17.

¹³ These statistics apply to the “ever in DHA” sample but are comparable in the “majority of high school in DHA sample” as well.

¹⁴ We note that although a teen may legally obtain a work permit at age 14, a few caregivers reported that their children began working (presumably informally) at an earlier age.

¹⁵ Unfortunately, 2010 Census information was not yet available when these indicators were devised.

¹⁶ Recent research has shown that such subjective information based on residents' perceptions of neighborhoods provide important additional explanatory power in modeling a variety of economic outcomes (Furtado, 2011).

¹⁷ This is similar to the oft-used approach to obtain subjective neighborhood indicators; see Muhajarine et al. (2008)

¹⁸ This was operationalized in our model as the proportion of years during ages 14–17 when the youth was residing in a neighborhood where the parent had identified the presence of “many children or teens getting into trouble.”

¹⁹ All respondent-assessed neighborhood characteristics relate to a single residential address and thus do not vary unless the household moves. If the household moves while the focal teen is aged 14–17 there will be two or more subjective evaluations of these places constituting each indicator. Our summary indicator computes a weighted average of these assessments based on the number of years the teen lived there during the 14–17 age period.

²⁰ We remind the reader that we have neighborhood variables measured at three distinct geographic scales: (presumably) small, respondent-defined neighborhoods, census tracts, and Piton neighborhoods (approximately two tracts in size). This means that there is little nesting of households in a classic multi-level data structure even at the largest scales. Neighborhoods are always changing, so even if two households were occupying the same neighborhood simultaneously there would be no duplication of neighborhood indicator values unless their children were of identical ages in the 14–17 age period.

²¹ It also would have been interesting to explore measures of cumulative context since birth. Unfortunately, inadequate sample sizes for child-years subsequent to random assignment to DHA precluded this exploration.

²² For the two logistic models we used Stata's LOGIT and XTMELOGIT algorithms. We do not need to worry about clustering at the neighborhood level here because children who live in the same neighborhood are experiencing a different value of the neighborhood indicator because they are experiencing such for different years of their lives and different calendar years.

²³ The coefficient of a covariate in a Tobit model should be interpreted as the net effect of: (1) the change in the dependent variable for those with positive values, weighted by the probability of having such values and (2) the change in the probability of having positive values, weighted by the expected value of the dependent variable when it is positive (McDonald & Moffit, 1980).

²⁴ We admit that causation may run in the opposite way; low-income households in which teens do not work may be more likely to experience economic stress.

²⁵ In the full sample, the Ns for these strata were as follows: 166 African Americans, 258 Latinos, 222 males, and 222 females.

²⁶ The mixed-effects logits did not converge for several samples and thus are not reported.

²⁷ Although we note that the prior literature has a range of results on similarly-conceived “neighborhood disadvantage” variables, we stress that our results are not strictly comparable for two reasons. First, our score sums neighborhood percentages of: unemployment, poverty, female-headed households, and renters; it does not include ethnic, racial, or nativity measures, as do most others. Second, our models control for a host of other neighborhood characteristics that are often associated with “disadvantaged neighborhoods” but for which other studies have no direct measures: notably crime, child abuse, institutional resources, bad peer influences, social problems, social capital, and occupational prestige. Thus, other studies' “neighborhood disadvantage” variables serve as ambiguous proxies for a wide range of other attributes besides social status, and should not be used as precedents for results using our social vulnerability score.

²⁸ There may also be a spurious relationship: fewer teen job opportunities within or nearby violent neighborhoods (which we cannot measure in our models).

²⁹ In the case of our dichotomous outcome, estimates produced by two forms of logit estimators provide still another robustness check.