By randomizing receipt of a housing voucher that could be used to move into a lower poverty neighborhood, the Moving To Opportunity (MTO) experiment essentially randomized neighborhood context for families in public housing in five US cities: Baltimore, Boston, Chicago, Los Angeles, and New York.1 As such, it provides strong evidence on the potential for housing policy to affect economic, education, and health outcomes by improving neighborhood and housing environments. Because MTO is the only study with this experimental design, it has received extensive research attention. However, despite the large number of MTO publications, effects have rarely been compared across cities, and site differences in effects have largely been ignored. Evaluating whether MTO had similar effects in all five cities, and if not, understanding drivers of those site differences, are important for understanding the generalizability of responses to housing policy.
Site differences in MTO effects could be due to (1) differences in the distribution of individual-level compositional factors across sites that modify intervention effectiveness, such as participants’ race/ethnicity or motivations for enrolling in the study (henceforth, referred to as “compositional”); or (2) differences in site-level contextual factors that modify intervention effectiveness, such as local economic or housing market conditions (henceforth, referred to as “contextual”). Focusing on the latter explanation, MTO researchers concluded: “With only five sites, which differ in innumerable potentially relevant ways, it was simply not possible to disentangle the underlying factors that cause impacts to vary across sites” (Orr et al2, p. B11), although qualitative research, including an examination of intervention implementation differences, has explored city-level underlying factors contributing to differences in MTO effects.3–5 Because five sites is too small a number to use traditional multilevel methods to quantitatively examine contextual drivers of site differences, and because other statistical tools to examine compositional drivers of site differences were not available, nearly all MTO analyses have reported results pooled across cities, controlling for city as a fixed effect in a regression model.6–8 This strategy implicitly assumes that the MTO intervention effect in one city is the same as in another city because the city fixed effect changes the intercept of the regression model but not the treatment effect coefficient.
However, the status quo of assuming a constant treatment effect across sites (and considering few if any compositional effect modifiers) may not be appropriate for the two reasons given above and may even result in wasted resources if policies or programs are implemented in populations unlikely to benefit. Recent statistical advances in the subfield of transportability (which is related to generalizability or external validity) offer the opportunity to improve upon this status quo by evaluating the contribution of differences in population composition to site differences.9–15 Instead of predicting that an intervention will have the same effect in a new setting, we can flexibly incorporate numerous compositional effect modifiers into the prediction, resulting in potentially more accurate predictions that are “personalized” for place. While this will not allow us to fully disentangle the underlying compositional and contextual factors that cause impacts to vary across sites, it will allow us to assess the extent to which these site differences are due to specific sets of individual compositional characteristics.
Our objective is to use a recently developed flexible and robust transport estimator10 to better understand site differences in MTO’s effects. We focus on MTO’s mental health and risk behavior effects among adolescent boys because previous research unexpectedly found harmful effects on these outcomes among this subgroup (though effects for diagnostic mental health disorders were nonsignificant).2 , 7 , 8 , 16–18 We first test for site differences for each outcome. Focusing on outcomes with qualitative site differences—marijuana use, behavioral problems, major depressive disorder, and generalized anxiety disorder—we identify sites that differ in terms of whether receipt of a housing voucher was beneficial or harmful. Then, we employ the transport estimator to assess the extent to which those site differences could be explained by differences in the distribution of compositional factors. Differences that cannot be explained suggest that macro-level, contextual factors (or unmeasured compositional factors) may be critical to determining whether the intervention was harmful.
We used data on male youth who were enrolled in MTO at the baseline and interim visits. The baseline visit occurred in 1994–1998, and we use outcomes measured at the follow-up visit, which occurred 4–7 years later when the youth were 12–19 years. MTO has been described previously.2 , 6 , 16 Briefly, it was a randomized control trial conducted by the US Department of Housing and Urban Development enrolling 4600 families living in public housing with children aged under 18 years. Weights accounted for changing random assignment ratios, sampling of children within households, and loss to follow up.16 We excluded the Baltimore site from all analyses because voucher receipt was not associated with a subsequent move to a low-poverty neighborhood ( < 25% of persons in poverty; results available upon request). We restricted to black and Hispanic/Latino youth as there were too few participants of other racial/ethnic groups to control for race/ethnicity without extrapolation concerns. Finally, we limited our analysis to those individuals with at least one nonmissing outcome. These exclusions resulted in a sample size of N = 1,094–1,095 (depending on imputed data set).This study was determined to be nonhuman subjects research by the University of California, Berkeley.
MTO randomly assigned families into one of three groups: (1) receipt of a Section 8 housing voucher to be used to move to a low-poverty neighborhood and assistance finding housing, (2) receipt of a Section 8 housing voucher without assistance finding housing, and (3) no intervention. Effect estimates comparing the two intervention groups to the control were similar, as has been shown previously2 and as supported by a partial F test (P values: 0.61, 0.21, 0.49, and 0.81 for marijuana use, behavioral problems, major depressive disorder, and generalized anxiety disorder, respectively). Therefore, we combined the two intervention groups and defined our instrument as randomization to receive a housing voucher versus not, as has been done previously.8 To allow for differences in intervention “take-up” across sites, we incorporated moving to a 2000 Census tract with less than 25% of persons in poverty as a causal intermediate. This poverty level was chosen as it represented a natural breakpoint in the distributions of residential poverty at follow-up for each site. The distribution of Census tract poverty levels by site is shown in eFigure 1; http://links.lww.com/EDE/B289. We tested several binary adolescent self-reported mental health and risk behavior outcomes. Major depressive disorder and generalized anxiety disorder correspond to Diagnostic and Statistical Manual of Mental Disorders (4th Edition) diagnoses, which have been shown to align with clinical diagnoses.2 , 19 Factor scores from an abbreviated Behavioral Problems Index20 were estimated using item response theory after previous work8 and then dichotomized at the 90th percentile.21 Marijuana use was defined as any lifetime use.
Because use of marijuana and diagnoses of generalized anxiety disorder and major depressive disorder are lifetime measures, we cannot definitively establish temporality for these outcomes. However, we believe temporality is likely because the ages at baseline—5–16 years old—are younger than the typical ages at onset for major depressive disorder and generalized anxiety disorder (median ages at onset are 31 and 32 years, respectively22) and also before most try marijuana (median age of 16 years).23 Moreover, although these outcomes were not measured at baseline, we would expect them to be balanced between treatment groups by virtue of the random assignment. Baseline covariates included sociodemographic characteristics of the adolescent and family members, behavior and learning characteristics of the adolescent, neighborhood characteristics at baseline, and reasons for participation in MTO. A full list of covariates is provided in the eAppendix; http://links.lww.com/EDE/B289.
We estimate the intent-to-treat average treatment effect, which is the average effect of being randomized to receive a housing voucher versus control on each health outcome considered. These measures are risk differences; for example, for major depressive disorder, the intent-to-treat average treatment effect would be the difference in risk of major depressive disorder at follow-up comparing those randomized to the housing voucher group versus the control group. We restricted our analysis to those observations with nonmissing outcomes. This resulted in a sample size of 1,018–1,019 for generalized anxiety disorder, 1,077–1,078 for marijuana, and 1,094–1,095 for major depressive disorder and behavioral problems. We used multiple imputation by chained equations to impute covariate values (race/ethnicity and ever repeating a grade, missing for < 1% and 6%, respectively), making 30 imputed data sets.24 For each outcome, the analysis proceeded as follows. We estimated site-specific intent-to-treat average treatment effects and identified sites with qualitatively different estimates (i.e., one site had an increase in risk while another had a decrease) that also demonstrated quantitative differences using a partial F test and an alpha level of 0.15. We aimed to transport the treatment effect estimate from the group of site(s) with the more extreme estimate, S = 1, to the site(s) with the less extreme estimate, S = 0. (Note that we could transport in either direction; we chose to transport from the site with the more extreme estimate to facilitate the inclusion of treatment in the outcome model when using data-adaptive methods in model fitting.) The transport estimator is premised on the assumption of a shared outcome model across sites. We tested this using a nonparametric omnibus test of equality of two functions in distribution,25 which uses the same flexible machine learning approach26 , 27 as is used in the transport estimator. Specifically, we test the null hypothesis, H 0 that E(Y | S = 0, W, A, Z) = E(Y | S = 1, W, A, Z), where Y is the outcome, W is the vector of covariates, A is housing voucher randomization, and Z is intervention take-up of moving to a lower poverty neighborhood. (Note that we would not need to incorporate Z to estimate a site-specific intent-to-treat average treatment effect. Z is incorporated into estimation of the transported treatment effect to account for compositional differences in take-up.9 , 10) If we did not have evidence to reject H 0 then we proceeded with estimating the transported treatment effect. Scenarios that result in the inequality E(Y | S = 0, W, A, Z) ≠ E(Y | S = 1, W, A, Z) would include contextual differences or differences in unmeasured individual-level confounders. Using Pearl and Bareinboim’s transport notation, this would be depicted by an S node pointing into Y node9 and could include scenarios such as differences in intervention implementation across sites or differences in other sources of bias in modeling Y across sites, such as measurement error.
We used a semiparametric transport estimator10 to predict the intent-to-treat average treatment effect for S = 0, accounting for differences in population composition and intervention uptake across sites. Practically, this means flexibly modeling several relationships: (1) how S = 1 and S = 0 differ in the distribution of covariates, (2) the S-specific model of moving to a low-poverty neighborhood (Z) as a function of covariates and randomization, and (3) the model of the outcome as a function of covariates and the take up in the S = 1 group. Using the outcome model for S = 1, we predict outcome values for those in the S = 0 group, using their covariate and take-up values and take-up model. For example, in the case of marijuana use, we predict the intent-to-treat average treatment effect for Los Angeles (S = 0) using covariate, randomization, take-up, and outcome data from Boston (S = 1) but no outcome data from Los Angeles. This is similar to re-weighting the intent-to-treat average treatment effect for S = 1 using the composition and intervention take-up of S = 0. We call the predicted treatment effect for S = 0 the “transported intent-to-treat average treatment effect”. The transport estimator uses targeted maximum likelihood estimation, which is a multiply robust approach (meaning that it is consistent even if some of the relationships described above are misspecified) compatible with flexible, machine learning approaches for modeling the relationships. The ensemble machine learning algorithm we used allowed for a very flexible model, including complex interactions between covariates, treatment, and take-up and incorporated cross-validation to avoid overfitting. Targeted maximum likelihood estimation differs from other estimation frameworks in that it targets the specific effect of interest and optimizes its estimation in terms of bias and variance.28 Finally, we compare the predicted intent-to-treat average treatment effect for S = 0 to the observed estimate for S = 0. The amount by which the predicted effect reduces the difference between the site-specific treatment effects represents the degree to which the site differences may be due to population composition. The portion unexplained represents the extent to which the site difference may be due to context or unmeasured individual characteristics. We used R version 3.3.1 for all analyses.
Table describes the analytic sample by site, which included black and Hispanic/Latino male adolescents at follow-up. Boston, Los Angeles, and New York City sites had roughly equal proportions of black and Hispanic/Latino male teens, while Chicago had very few Hispanic/Latino participants (1.36%). Ages of the participants at follow-up were similar across sites with a mean of 15 years.
There is substantial variation across the sites at baseline in terms of family sociodemographics, neighborhood perceptions, and school-related experiences. These individual-level compositional differences could be interacting with the MTO intervention to produce different effects across sites. Rates of moving to a low-poverty neighborhood after randomization were highest for Chicago (32%), followed by Los Angeles (30%), Boston (24%), and New York City (18%). At follow-up, teens in Chicago reported slightly higher rates of marijuana use (30%) and lower rates of behavioral problems (7%). Those in Boston reported the highest rates of behavioral problems (18%). The proportion of teens with generalized anxiety disorder was lowest in New York City (3%). The rates of major depressive disorder were similar across the sites.
Each outcome showed evidence of qualitative and quantitative site differences. The site-specific estimates and 95% confidence intervals (CIs) are shown in Figure. Receipt of a housing voucher increased marijuana use among boys in Boston but slightly decreased the use in New York City (P value for site difference = 0.03). Housing voucher receipt decreased behavioral problems among boys in Los Angeles but increased problems in New York City (P value for site difference = 0.12). Housing voucher receipt increased risk of major depressive disorder among boys in New York City but decreased risk in Chicago (P value for site difference = 0.10). Finally, voucher receipt increased risk of generalized anxiety disorder among boys in Boston and New York City but decreased risk in Los Angeles (P value for site difference = 0.04).
We tested whether we had evidence of a common outcome model across sites, an assumption required to identify the intent-to-treat average treatment effect for S = 0.10 For marijuana use, behavioral problems, and major depressive disorder, we found no evidence against the shared outcome model assumption (P values: 0.72, 0.44, and 0.74, respectively). However, we rejected the shared outcome model assumption for generalized anxiety disorder (P value = 0.04). This indicates that the intent-to-treat average treatment effect for generalized anxiety disorder could not be transported based on measured individual-level covariates, but we proceeded with transporting the treatment effect estimates for the remaining outcomes.
Figure shows the estimates for the effect of being randomized to the housing voucher group on risk of marijuana use (Figure A), behavioral problems (Figure B), major depressive disorder (Figure C), and generalized anxiety disorder (Figure D) among black and Hispanic/Latino male youth. Comparing the transported estimates (dashed lines) to observed estimates (solid lines) for site S = 0 allows us to assess the extent to which site differences could be attributed to differences in the distribution of compositional characteristics between the sites. If the site effects are transportable using measured individual-level characteristics, then the transported effect for S = 0 will coincide with the observed effect for S = 0. This would suggest that differences in the site effects are entirely due to differences in compositional factors between the sites. If, on the other hand, the transported effect is no closer to the observed estimate for S = 0 than the observed estimate for S = 1, then it suggests that the MTO’s effect on that outcome is not transportable based on these characteristics. If the transported estimate is between the two observed estimates, it suggests a partially transportable effect—that the site differences in effects are partially but not entirely attributable to measured compositional differences.
Figure A shows that the effect of housing voucher receipt on risk of using marijuana is partially transportable between Boston and Los Angeles using measured individual-level characteristics. The transported effect estimate for Los Angeles is 0.04 (95% CI = −0.11, 0.19). So, if Boston, counter to fact, had the population distribution of covariates shown in Los Angeles, we would predict that being randomized to the housing voucher group would increase risk of marijuana use at follow-up by 0.04. The transported estimate is closer to the observed Los Angeles estimate (−0.05; 95% CI = −0.19, 0.09) than is the observed Boston estimate (0.15; 95% CI = 0.04, 0.25); differences in measured compositional factors explained 52% of the difference between sites. The t statistic of the difference between the observed and transported Los Angeles estimates is −0.92 (95% CI = −2.89, 1.04). There is also evidence for partial transportability in the case of behavioral problems (Figure B). The transported effect estimate for Los Angeles (0.00; 95% CI = −0.11, 0.19) is closer to the observed Los Angeles estimate (−0.04; 95% CI = −0.14, 0.04) than is the observed New York City estimate (0.05; 95% CI = −0.00, 0.11), explaining 57% of the site difference. The t statistic of the difference between the observed and transported Los Angeles estimates is −1.02 (95% CI = −2.98, 0.95). In contrast, the wide CI for the transported major depressive disorder estimate in Figure C precludes any clear conclusion about transportability. The transported point estimate for Chicago (0.02; 95% CI = −0.11, 0.15) is essentially no closer to the observed estimate (−0.02; 95% CI = −0.07, 0.03) than was the observed New York City estimate (0.02; 95% CI = 0.01, 0.04)—the transported estimate only explained 9% of the site difference. The t statistic of the difference between the observed and transported Chicago estimates is −0.62 (95% CI = −2.59, 1.34).
As previously noted, we found evidence against the common outcome model assumption for generalized anxiety disorder, which precluded estimating the transported effect (Figure D). This is quantitative evidence suggesting that differences in measured aspects of population composition across sites did not contribute to the differences in site effects for generalized anxiety disorder and potentially also for major depressive disorder; instead, differences in context or in unmeasured individual-level compositional factors may play an important role.
We found evidence of site differences in MTO’s effects on marijuana use, behavioral problems, major depressive disorder, and generalized anxiety disorder among black and Hispanic/Latino adolescent boys. These site differences were qualitative—receiving a housing voucher appeared to be harmful for the health of adolescent males in some sites but beneficial in other sites. Since population composition also varied by site and such compositional factors could act as effect modifiers, we assessed the extent to which the site differences could be explained by differences in population composition. Differences in composition partially explained site differences in marijuana use and behavioral problems but did not appear to explain site differences for major depressive disorder and generalized anxiety disorder. Thus, the effects of housing vouchers on mental health and risk behaviors in adolescent males do not appear to be fully transportable across sites even after flexibly accounting for numerous baseline characteristics, thereby, providing quantitative evidence for the importance of context (or unmeasured individual-level compositional factors) in modifying MTO’s effects.
To our knowledge, this is the first time that quantitative evidence has been brought to bear in the “composition vs. context” debate in settings where there are too few sites to use multilevel methods to estimate contextual effects (see Macintyre et al29 and Oakes30 for an introduction to this debate). When there was evidence of differences in effects between sites, we used a transport estimator10 to predict the effect of the MTO intervention in one of the sites based on differences in individual-level characteristics between sites and the outcome model from the other site. The transport estimator is flexible, data-adaptive, and multiply robust; it can simultaneously account for numerous compositional factors that may modify the treatment effect without concerns about cherry-picking or misspecifying possibly complex relationships in parametric models. In addition, it results in accurate inference when incorporating machine learning algorithms, which is a challenge of other estimation strategies. The transported point estimates did not equal the observed point estimates in the target site for any of the outcomes, suggesting unmeasured factors at the contextual- or individual-level partially contributed to site differences. However, with only five cities (four of which were used for this analysis), we do not have the sample size necessary at the site level to empirically identify which contextual-level variables contribute to these site differences. Such identification would require a larger number of sites as part of a multilevel experimental design.31 A limitation of our analysis is small sample size in terms of the number of adolescents. Given the high-dimensional vector of baseline characteristics coupled with the small number of cases for the mental health outcomes, a larger sample size of adolescents would likely improve the precision of our transport estimates. In addition, small sample size coupled with a rare outcome could also negatively affect estimator performance in terms of bias and coverage.32 Another limitation further compounded by the small sample size limitation is the presence of practical violations of the positivity assumption.32 In this application, practical positivity violations mean that there are certain combinations of covariate values that nearly determine site membership or intervention take up. This is a problem because our estimator must then rely on extrapolation over areas where there are little or no data. Positivity violations can adversely affect estimator performance in terms of bias, variance, and confidence interval coverage.32–34 Although the transport estimator we use here is not very sensitive to practical violations of the positivity assumption, it nonetheless demonstrated slight increases in bias and variance and loss of confidence interval coverage under such violations.10 Coupled with small sample size, practical positivity violations could pose an additional problem if the site that we are transporting to has participants with combinations of baseline characteristics not observed in the site that we are transporting from. If those baseline characteristics are also important for modifying the effect of moving to a low-poverty neighborhood on the outcome, then the transported estimate may be biased because of its inability to account for those modifiers.
Finally, MTO’s effects on marijuana use and behavioral problems were partially transportable, and it might be of interest to know which aspects of population composition were most important in explaining these site differences. Unfortunately, no appealing method exists for identifying the most relevant modifiers. It is an area of future work to develop a variable importance algorithm for the machine learning approach used in our analysis, similar to other variable importance metrics.35
In summary, we found that a large number of baseline characteristics—including individual and family sociodemographics, experiences at school and in the neighborhood, and motivations to move—partially explained site differences in MTO effects for risk behavior outcomes but could not explain site differences in mental health outcomes among adolescent boys. This suggests that context or unmeasured compositional variables are important in modifying MTO’s effects. For example, qualitative evidence suggests that city-level differences in aspects of the economy, housing market, racial mixing, and school choice policies may have modified MTO’s effectiveness.3–5 Thus, even if great care is taken to implement an intervention the same way across cities2 and all relevant individual-level variables are accounted for, an intervention may still not be transportable due to differences in context. Given that social experiments like MTO are embedded within complex social settings, the potential for nontransportable effects due to differences in context may not be surprising and is aligned with sociological research demonstrating the importance of considering multiple levels of contextual influence.36–39
Our findings have two implications that are marked departures from the current understanding of MTO results. First, our finding suggests that the current practice of analyzing MTO data by pooling across sites and including a dummy variable for site in a regression equation may be inappropriate. Ideally, one would first check for site differences in treatment effects and, if site differences are found, whether they could be explained by measured baseline covariates. If not, as in our examples, then a site-specific analysis should be conducted (e.g., using interaction terms between site and treatment) or an analysis that only pools sites with similar effect estimates. The second, more general implication is that interventions should be considered in the context of where they are implemented and developed or modified with potentially relevant macro-level factors in mind. Previous MTO research demonstrated the importance of the neighborhood context on health outcomes; this study suggests widening the contextual lens to encompass city-level factors.
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