Because of biases, commonly estimated associations between neighborhood characteristics and health/behavioral outcomes do not reflect causal neighborhood effects. Classic residential neighborhood studies use regression models to correlate residential exposures with overall health/behavioral outcomes (e.g., cumulating behavior inside and outside the residential neighborhood)1–4 to quantify residential intervention effects. Among the assumptions that need to be met for such associations to represent the target causal effects (see the first section of eAppendix 1; http://links.lww.com/EDE/B243 for a tentative overview of these conditions), the counterfactual framework requires the absence of confounding. With confounding, unmeasured factors causally influence both the exposure and the outcome or determinants of the exposure and outcome, threatening the exchangeability between exposure groups required to validly estimate causal effects.5 To improve the quality of causal inference, the present study aims to describe, diagnose, and correct a major confounding bias applicable to a large fraction of neighborhood and health studies. Surprisingly, this bias has received almost no attention in the literature (eAppendix 2; http://links.lww.com/EDE/B243). This source of bias has the major implication that residential neighborhood–outcome associations as commonly estimated may substantially overestimate the effects that residential interventions would have on the health of residents.
Recently, scholars have suggested that environmental exposures in the multiple places visited by people may influence health beyond residential neighborhood exposures.6–10 The source of the “residential” effect fallacy described here is that for many exposures, residential characteristics may be correlated with those of the multiple contexts visited during the daily activities (within-individual correlation) because of a common causal antecedent (see Figure 1).11,12 Consequently, associations between residential neighborhood and health outcomes as classically estimated may capture some of the effect that nonresidential environments visited may have on behaviors and health (confounding of residential neighborhood–health associations, used for quantifying residential intervention impacts, by nonresidential effects). The “residential” effect fallacy implies that because of the correlation between residential and nonresidential characteristics and resulting confounding, intervening on the residential neighborhood may not have the effect expected from classically estimated residential neighborhood–health associations.
As an empirical illustration, the present study relied on global positioning systems (GPS) tracking and on a mobility survey to precisely assess places visited over 7 days.8,13,14 The resulting ability to disentangle truly residential from nonresidential effects allowed us to demonstrate the existence of a major generator of confounding that we refer to as the “residential” effect fallacy (we use quotes to put into question the residential nature of the underlying effect), quantify its magnitude, and correct for it. As an illustration, we focus on the well-known hypothesis that the residential accessibility to services fosters walking for transport..1,15–17
Data Collection and Processing
The RECORD (Residential Environment and CORonary heart Disease) Study participants, recruited during preventive health checkups, were born in 1928–1978 and were residing at baseline in 112 municipalities of the Paris Ile-de-France region.18–23 During the second study wave, 410 participants were invited to enter the RECORD GPS Study (approved by the French Data Protection Authority) in 2012–2013.13 Of these, 247 accepted to participate and signed an informed consent form. Nine participants withdrew from the study, and data were incomplete for four participants, resulting in a final completion rate of 57% (N = 234). Seven participants who either lived or spent the 7-day follow-up outside the Île-de-France region were discarded. Overall, 227 participants were included.
GPS-based Mobility Survey
Participants wore a QStarz BT-Q1000XT GPS receiver24 on the right hip for the recruitment day and 7 additional days and filled a travel diary. GPS data (one point every 5 seconds) were processed by an ArcInfo 10 Python script (http://www.spherelab.org/tools).25 It identified the places visited by participants (stationary locations) over the data collection period. The algorithm calculates a kernel density surface from the set of GPS points for each participant, extracts peaks as potentially visited locations, derives a timetable of all visits (of at least 10 minutes) over the period to each detected location with their start and end times and uploads this information into the Mobility Web Mapping application.
The telephone-prompted recall mobility survey13,17 was based on this web mapping application.13 With the participant, using the travel diary, the survey operator confirmed each of the detected visits to places (where participants fulfill functions) and corresponding trips, geolocated visits to places undetected by the GPS receiver or algorithm (e.g., very short visits), and modified/removed inaccurate/incorrect visits to places. For each visited place, participants reported the type of activity practiced at the location and the transport modes to reach the place. A SAS program (version 9.3, SAS Institute, Cary, NC) generated the succession of visited places and trips between places with their start/end times.13 Over 7 days, the 227 participants made 7440 (potentially multimodal) trips between places.
Based on the survey, a trip-level binary outcome was set to 1 (vs. 0) if only walking was used in the trip (partly walked trips also using, e.g., public transport coded as nonwalking trips).
Age (three categories: 35–49; 50–64; ≥65 years) and gender were considered. Marital status was coded as living alone or in a couple. Education was coded in four categories: no education, primary education, or lower secondary education; higher secondary education and lower tertiary education; intermediate tertiary education; and upper tertiary education. Household income per consumption unit was coded in three categories using the tertiles. Employment status was categorized in four classes: stable job; unstable/precarious job; unemployed; and other.
As neighborhood selection factors,6,26 participants were asked whether, before moving to their current residence, when they were looking for a neighborhood to live, they found it important to live in a neighborhood (1) with good access to public transport and (2) with enough services and facilities.17 Each item was coded in three categories.
Modes in Previous Trips
Modes used in previous trips are a major confounder for the association between trip-level service accessibility and walking.17 Relying on a car in the previous trip influences both the environment visited and the mode in the next trip. For each trip, we counted the number of trips done since the last visit at home or in an alternative residence. A binary variable indicated whether a bike was used in one of these previous trips. A three-category variable indicated whether a personal motorized vehicle was used in none, some, or all of these previous trips.
The spatial accessibility to services was computed within street network buffers (radius = 1 km, corresponding to a 10- to 15-minute walk27–29) centered on the departure and arrival of each trip and on the residence (ArcInfo 10.0, Network Analyst). Using the Permanent Database of Facilities (Insee, 2011), we calculated the number of services of all types (public services, shops, entertainment facilities, etc.; see detail in eAppendix 3; http://links.lww.com/EDE/B243) in each buffer.
As illustrated in Figure 2, we calculated the percentage of each trip origin buffer and of each trip destination buffer that overlapped the residential buffer. When the percentage of overlap was 0 < X < 100, we calculated separately the number of services in the part of the trip origin/destination buffer that overlapped and in the part that did not overlap the residential buffer.
Statistical Analysis and Calculations
We excluded episodes at activity places, yielding a sample of trips. Regression analyses excluded the following trips from the full sample (n = 7440): trips >4 km of length as noneasily walkable (n = 2597); atypical trips (professional tours, etc.; n = 3); and trips starting and/or ending outside the Ile-de-France region (n = 207). The analytic sample comprised 4633 trips.
Correlation in Service Accessibility Between Residential and Nonresidential Neighborhoods
This correlation is a consequence of the causal structure in Figure 1 and the potential vector of the “residential” effect fallacy. We estimated a multilevel linear regression model with a random effect at the individual level to investigate the relationship between the density of services per km2 in the residential buffer (explanatory variable) and the density of services in the trip origin buffer (outcome). Trips starting at the residence were removed from this regression database. Moreover, for trips whose origin buffer partly overlapped the residential buffer, we used as the outcome the density of services per km2 in the portion of the trip origin buffer that did not overlap the residential buffer (we used densities per km2 in this analysis rather than counts of services as in the main analyses to deal with these portions of buffers). We specified interactions between the residential density of services and, on the one hand, the street network distance between the residence and the trip origin and, on the other hand, the square of this distance (quadratic term).
General Description of the Approach
To mimic an intervention focused on poorly served neighborhoods, the hypothetical interventions examined are to raise the number of services accessible in the residential buffer to 200, 500, or 1000 if below that number.
We estimated regression models at the trip level (one observation per trip).13,17 Variations in the probability of exclusively walking during a trip were modeled with linear probability models (binary variable, identity link). This model quantifies associations on the risk-difference scale,30 that is, on the probability scale, which is particularly relevant to decision-making.31 We used multilevel models, with a random effect at the individual level, to account for the within-individual correlation in modal choice. Individual sociodemographic covariates and neighborhood selection factors were forced into the models.
Naïve Estimate of the Residential Intervention Effect
The model based on trip-level data to calculate the naïve (biased) estimate of the intervention effect included sociodemographic variables, neighborhood selection factors, and the residential number of services (two continuous variables: linear and quadratic terms). Based on model coefficients, we calculated for each trip the predicted probability that it is entirely walked from all model covariates (including the number of services). This calculation was performed for the preintervention state and for each of the postintervention scenarios (residential services raised to 200, 500, or 1000 if below that number). For each of these four cases, we calculated the average probability that a trip is walked across all individuals and trips. The intervention effect estimate was computed for each intervention level as the postintervention average probability of entirely walking in a trip minus the preintervention probability, only among participants who received the hypothetical intervention (i.e., with less than 200, 500, or 1000 services).
Corrected Estimate of the Residential Intervention Effect
The corrected (unbiased) estimate (true intervention effect conditional on a number of conditions listed in eAppendix 1; http://links.lww.com/EDE/B243) was calculated from a model including sociodemographic variables, neighborhood selection factors, modes used in previous trips from home (confounder of the momentary environmental effect), the number of services at the departure and arrival of the trip (linear and quadratic terms), and the residential number of services (linear and quadratic terms). It is also useful to include the association between residential services and walking to capture (after adjustment for neighborhood selection factors) the influence of the residential accessibility to services on preferences and overall choice of mode (e.g., buying a car or relying on public transport) that may influence mode choice in all trips (even far from home). Associations with both the residential and trip origin/destination numbers of services are required to calculate the corrected intervention effect estimate.
The number of services in each trip origin or trip destination buffer was affected by the intervention only if the residential number of services was increased by the intervention and if the trip origin/destination buffer overlapped the residential buffer. If services in the residential buffer were increased by N and if X% of the residential buffer was in the trip origin/destination buffer, then the number of services in the trip origin/destination buffer was increased by X% of N.
We used the regression equation and values of covariates (including for the pre- and postinterventional number of services in the residential, trip origin, and trip destination buffers) to calculate the probabilities that each trip is walked. The same approach as for the naïve estimate was used to calculate the corrected estimate for the different intervention levels for participants in the intervention group.
Assumptions made by this approach are discussed in the second section of eAppendix 1; http://links.lww.com/EDE/B243. All regression models were estimated with a Markov chain Monte Carlo approach using Winbugs.32
Overall, 64% of the 4633 trips of 4 km or less were entirely walked. At the individual level (N = 227), the percentage of trips that were entirely walked varied from 0% to 100% (10th percentile: 18%; median: 67%; 90th percentile: 96%). The median number of services was of 613 in the residential neighborhood (10th percentile: 109; 90th percentile: 2992) and of 769 in the trip origin and trip destination buffers (10th percentile: 117; 90th percentile: 3389).
Figure 3 reports the magnitude of the association between the residential number of services and the trip origin number of services according to the street network distance between the residence and each trip origin. The association operated on a long range: even when the trip origin was 5 km away from the residence, an increase by 1000 in the residential number of services was associated with an increase of 656 services (95% credible interval [CrI] = 487, 825) in the trip origin buffer. The association vanished when the street network distance was >25 km.
Hypothetical Scenarios of Intervention
The three hypothetical scenarios of intervention are described in Table 1. For example, the intervention to raise the residential number of services to 200 would affect 58 participants (26%), corresponding to an increase in the number of services by 101 or more in 50% of the cases and implying a reduction of the distance between services along streets from a median of 315 m to a median of 165 m in the intervention neighborhoods.
Naïve Estimates of Intervention Effects
Based on the regression model reported in eAppendix 4; http://links.lww.com/EDE/B243, the probability to walk in a trip increased with the number of services in the residential neighborhood. As also shown in Figure 4A, there was a quadratic effect: increases in the number of services beyond 2000 were not associated with further gains in the probability that a trip is walked.
Based on this model, the hypothetical interventions to raise the residential number of services to 200, 500, and 1000 were associated with an increase by 0.020, 0.055, and 0.109 of the probability that a trip is walked for participants in the intervention groups (Table 2).
Corrected Estimates of Intervention Effects
To derive the corrected intervention effect estimates, we ran the model reported in eAppendix 4; http://links.lww.com/EDE/B243 (adjusted for modes used in previous trips and for the trip origin/destination numbers of services). As also shown in Figure 4, the residential number of services was no longer associated with walking (Figure 4B). While the trip origin number of services showed no relationship with walking (Figure 4C), the probability that a trip is walked increased with the number of services around the trip destination (Figure 4D). Again, a quadratic effect indicated that the increase in walking associated with an increment of services at the trip destination tended to be lower when the base number of services was high.
Based on the corrected model, the hypothetical interventions to raise the residential number of services to 200, 500, and 1000 led to an increase by 0.007, 0.019, and 0.039 of the probability that a trip is walked for participants in the intervention groups (Table 2). Thus, the naïve estimates overestimated the corrected ones by multiplicative factors of 3.0, 2.9, and 2.8.
Contributing to the causal neighborhood effect literature, the present study empirically demonstrates that the “residential” effect fallacy, an overlooked and potentially widespread generator of confounding, was of considerable magnitude for the association between a residential pseudointervention on the number of services and walking. This study estimated an association corrected from the spurious contamination by correlated nonresidential effects.
Strengths and Limitations
The primary strength of the present study is that it formally defined a bias, the “residential” effect fallacy, that, despite its general relevance for estimating causal neighborhood health effects, has to our knowledge received no formal consideration in the literature (eAppendix 2; http://links.lww.com/EDE/B243 reviews two studies10,33 connected to the present topic but that did not explicitly investigate the bias). Second, this paper could rely on accurate trip-level data obtained through a complex protocol combining GPS tracking, algorithm processing, and related prompted recall survey.8,13,17 The availability of data disaggregating the behavioral outcome at the level of the multiple places visited by the participants (in this study, the different trips) allowed the empirical identification and correction of the bias, which would have otherwise been impossible. A third strength is our policy-relevant specification of the target causal effect of services that was conceptualized in an interventional perspective (i.e., raising the access to services not by a constant value even in well-served neighborhoods but to a certain level if below that level). However, it should be kept in mind that this pseudointervention was not meant to mimic a completely plausible real-world intervention (whose area would not exactly match the precise home-centered buffers of specific individuals) but was seen as an intervention-like formulation of an observational effect estimate, an approach that we recommend for future observational neighborhood studies. As a fourth strength, eAppendix 5; http://links.lww.com/EDE/B243 shows that we were able not only to quantify the magnitude of the “residential” effect fallacy bias but also to recalculate the naïve estimate of the residential intervention effect based on an analytical understanding of the mechanism of bias (we could mimic the spurious transfer of nonresidential effects to the “residential characteristic”–walking association attributable to the confounding structure and correlation in the number of services).
Regarding limitations, as detailed in the second section of eAppendix 1; http://links.lww.com/EDE/B243, the present work did not consider that an increase in the number of services may also (1) increase the number of trips and that a similar “residential” effect fallacy may bias this association; and (2) affect the destinations and length of trips.
Interpretation of the Empirical Findings
Our data showed correlation in the local number of services between residential and nonresidential places over a long range of more than 20 km, supporting the causal structure in Figure 1 and creating a substantial potential for the “residential” effect fallacy.
In the adjusted model that was used to derive a corrected estimate of the residential intervention effect on walking (accounting for the residential, trip origin, and trip destination numbers of services), only the trip destination number of services was associated with walking. This finding that trip destination characteristics are more influential than trip origin characteristics has already been reported.34 A potential interpretation is that when constraints in mode choice at the beginning of the trip are taken into account (by controlling for the modes used in previous trips), the environmental conditions at the beginning of the trip lose their predictive importance, and only the spatial accessibility to services at the destination of the trip matters in the adoption or not of walking.
The major finding of our study is that the naïve effect estimates of the residential interventions of interest overestimated the true effects (true effects conditional on a number of assumptions listed in eAppendix 1; http://links.lww.com/EDE/B243) by a multiplicative factor of 3. Put the other way around, the correct estimates corresponded to only 35% of the naïve estimates. Clearly, the magnitude of this bias is very substantial compared to biases often documented in studies. The estimated intervention effect on transport walking was relatively modest, especially after applying the correction. Because of this carefully controlled correction and because we could recalculate the naïve intervention effect estimate based on the analytic understanding of the bias (eAppendix 5; http://links.lww.com/EDE/B243), we can confidently conclude that the bias of considerable magnitude that was documented was attributable to the “residential” effect fallacy People travel to various places in their daily activities,35 and the influence of the service environment in these various nonresidential places on mode choice is spuriously incorporated in the residential effect estimate because of the intraindividual correlation in the exposure to services between residential and nonresidential places.
The severity of the “residential” effect fallacy, a phenomenon of nonresidential to residential association contamination, depends on the magnitude of confounding and resulting correlation between residential and nonresidential places in the exposure of interest (as influenced to a large extent by the spatial autocorrelation of the exposure over the territory). Because of the urbanization structure of territories and of the socioeconomic distribution of populations, the spatial accessibility to services exhibits a considerable spatial autocorrelation,36 contributing to a correlation in services between residential and nonresidential neighborhoods visited. For the same reasons and others, many exposures of interest in neighborhood and health studies are likely spatially autocorrelated, such as neighborhood social stressors, fast-food restaurants, alcohol outlets, green spaces, or outdoor noise and air pollution.11,12 Thus, a considerable number of neighborhood or environmental studies exploring associations between residential characteristics and health/behavioral outcomes (cumulating outcome components inside and outside the neighborhood)1–4 likely yielded substantially overestimated residential effects estimates (although the bias may be weaker for exposures showing a lower correlation between residential and nonresidential places). Regarding generalization, there is no particular reason why this bias would be of particular importance in France (the marked distinction between urban centers, suburbs, and the countryside and the socioeconomic stratification of territories is widespread across countries).
When studies view their residential exposure variable as an imperfect proxy of environmental exposures in the multiple activity places visited, they are not subject to the “residential” effect fallacy bias described in the present study; however, they are then subject to a severe measurement error because residential exposures are inaccurate proxies of exposures associated with the activity space.7,37 As a consequence, classic residential neighborhood studies, depending on the interpretation of the estimated parameter, are either subject to the “residential” effect fallacy when the association is interpreted as a truly residential effect (because of the similarity between residential and nonresidential neighborhoods) or to measurement error when the association is interpreted as a total environmental effect (because of the dissimilarity between residential and nonresidential neighborhoods, i.e., to the fact that residential neighborhood characteristics are poor proxies of nonresidential characteristics). These two sources of error are likely to be substantial. Readers are referred to eAppendix 6; http://links.lww.com/EDE/B243 for advanced interpretations of the “residential” effect fallacy and sensitivity analyses (e.g., for an estimation of the intervention effect under the assumption that participants are also affected by the intervention in the other participants’ residential areas).
A critical implication of the “residential” effect fallacy is that interventions developed in a residential neighborhood will have a much lower impact on the behavior or health status of residents than would be expected based on the naïve association. To reach the impact expected from the estimated association, it would be necessary to intervene not only in the residential neighborhood but also in various visited locations of the persons (whose impact is spuriously incorporated in the residential effect estimate), which is far more challenging and costly.
For studies without access to individual mobility data, calculation approaches could be developed to speculate on the magnitude of the “residential” effect fallacy based on knowledge of the spatial distribution of the exposure of interest around participants’ residences and aggregated knowledge of local mobility patterns. However, the recommended strategy is obviously to collect detailed mobility data for each study participant to address both measurement error in environmental exposures and the “residential” effect fallacy. We suggest relying on the design proposed here, that is, to follow participants over time and space, to accurately identify life segments that make up their daily life schedules, to identify momentary exposures in these life segments, and to disaggregate the behavioral outcomes (e.g., physical activity, smoking, alcohol consumption, or food consumption) usually assessed at the individual level at the level of these multiple space–time segments of the days.17 This methodology will allow investigators to disentangle true residential influences from nonresidential effects that otherwise confound the residential intervention effect estimates of interest. Overall, our key, somewhat paradoxical, message is that to properly investigate residential effects, investigators critically need data on the nonresidential places visited.
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