Planners and public-health agencies routinely turn smartphone location data into estimates of how many people travel between neighborhoods and places. They then split those estimates by race, age, or income. The standard correction multiplies each neighborhood's observed device visits by the ratio of census population to devices, then divides the scaled visitors among demographic groups in proportion to the neighborhood's census makeup. This assumes that every group inside a neighborhood carries tracked phones at the same rate and travels the same way. We know that is false. Children, the elderly, and low-income residents are underrepresented in these data, and people from the same neighborhood sort into very different destinations. The error is worst for intersectional groups, such as low-income elderly Black residents, which are the groups these interventions most want to reach.
We propose to estimate group-specific device coverage and trip rates without any individual demographic labels. The approach uses a classic statistical trick: comparing many neighborhoods whose demographic mixes differ. If device counts rise and fall with the share of elderly residents across hundreds of block groups, that variation reveals how much the elderly are undercounted. The core difficulty is that the number of intersectional groups grows as $2^q$ in the number of attributes $q$, so an unstructured version of this comparison has far more unknowns than data. Our contribution is to constrain the intersectional rates with a structure borrowed from intersectional-fairness theory, to attach honest uncertainty to every group, and to say explicitly which intersections the data cannot resolve. We then check what this changes in a real downstream decision: where mobile vaccine clinics go.
Core Claim
Neighborhood-level population scaling hides a measurable, intersection-specific bias. This bias can be partly recovered by treating device counts and visits as mixtures of unknown group-specific rates, weighted by known census composition, and fitting those rates across many neighborhoods at once. Three things make the method both feasible and honest. First, intersectional rates are modeled as marginal effects plus interactions, and interactions are allowed only within blocks of attributes that are strongly correlated. Second, estimates are partially pooled across related groups. Third, the method reports a per-intersection verdict of "identifiable" or "not identifiable" instead of a point estimate that looks precise. The claim is falsifiable. On data where the truth is known, the method should beat uniform scaling on group-level flow error and should reach nominal interval coverage. Where the truth is only partly known, it should recover volumes that the biased sample does not see.
Where This Sits in Prior Work
Two papers define the practice we audit. Kang et al.'s multiscale mobility flow dataset scales SafeGraph visitor flows by census population over devices at the origin, and it validates the result against American Community Survey commuting flows at the county level. It acknowledges that the elderly and children are undercounted but applies a single factor per origin. Mehrab et al.'s vaccine-site placement system adds a second step: it apportions visitors to single demographic axes by block-group proportions. It showed that the top 25 sites for Black and Latinx residents overlapped in only 2 areas. That finding motivates us, because it shows the demographic split changes decisions. It also exposes the gap, because the split rests on the homogeneity assumption we test. Our work differs from both in the same way: we estimate within-neighborhood differences in coverage and travel rather than assuming them away, and we do so for intersections rather than single axes.
Two further papers show why the homogeneity assumption should fail. Nilforoshan et al. find exposure segregation ranging from 0.16 at performing arts centers to 0.42 at country clubs, so residents do not spread uniformly across destinations. They correct for sparsity with a mixed-effects model but do not reweight for missing populations. Shuman et al. find 10–15% tilts toward women at transit stops near care-related places. They also document that registered fare cards over-represent formal full-time workers. That second observation is the basis of one of our validation tests.
The method draws on the intersectional-fairness literature in three ways. Molina and Loiseau show that intersectional unfairness decomposes into marginal terms when attributes are conditionally independent. When attributes are correlated, they group them into blocks using total correlation, a multi-attribute generalization of mutual information. We reuse this idea as a structural prior on rates rather than as a bound on unfairness. Ji et al.'s hierarchical Beta calibration and Rudolph et al.'s structured embeddings supply the partial-pooling machinery. Both papers borrow strength from data-rich groups to stabilize estimates for sparse ones. Ferrara et al.'s size-adaptive testing (SAFT) supplies the reporting rule: switch from asymptotic to Bayesian intervals for small groups. The same paper also warns of a "no-power zone" in which small samples cannot separate signal from noise.
Two papers constrain the design. Paes et al. prove that auditing gains across many binary attributes becomes statistically impossible past about 19 attributes, even with Earth-scale data. Kim et al. (DRAF) show that enforcing constraints on micro-subgroups overfits noise. Together they rule out the naive goal of estimating every intersection. We accept these limits, and we build abstention into the method instead of promising full resolution.
Research Program
The model treats each block group $b$ as a mixture of intersectional groups $g$ with known census counts $N_{bg}$. Observed devices follow $$D_b \sim \text{Poisson}\Big(\sum_g N_{bg}\, \pi_{g}\, e^{u_b}\Big),$$ where $\pi_g$ is the probability that a member of group $g$ is tracked and $u_b$ is a neighborhood effect absorbing provider market share. Observed visits from $b$ to venue type $v$ follow the same form, with rate $N_{bg}\pi_g \lambda_{gv}$, where $\lambda_{gv}$ is the group's trip rate to that venue type.
The intersectional structure enters through the rates themselves. The log of $\pi_g$ is a sum of marginal attribute effects. Interaction terms are admitted only within the correlated blocks found by the Molina–Loiseau greedy partition applied to census joint tables. All terms get hierarchical shrinkage priors, and the model is fit in a standard probabilistic-programming tool.
Identifiability is diagnosed per group. We compare the posterior spread of each group's rate to its prior spread. Groups whose data contract the posterior by less than a set fraction are flagged as unresolved, and their scaled flows are reported as intervals only. This carries SAFT's size-adaptive logic from a single sample to the ecological setting.
The program has three components. The first is a semi-synthetic benchmark with known truth. The second is a real-data test with partial ground truth. The third is a downstream decision study that reruns Mehrab et al.'s siting pipeline with uniform scaling and with our estimates.
Baselines
The naive reference is uniform scaling, which is Kang et al.'s origin-level expansion ratio followed by proportional demographic apportioning as in Mehrab et al. It is the method actually deployed, and every other method must beat it. The strongest reported number for it is a Pearson correlation of 0.915 to 0.985 with ACS county commuting flows, reported by Kang et al.. That number concerns total flows, not group-level flows. For group-disaggregated accuracy, no reported result was found on Lacuna. We therefore expect near-parity with uniform scaling on totals, and the real test is group-level error.
The second baseline is marginal raking: separate scaling adjustments per attribute (age, income, race), iterated until the scaled sample matches each census marginal. This is the strongest simple survey-style competitor, and it tests whether intersections add anything beyond single axes.
The third baseline is unstructured ecological regression. It is our own model with every intersection given its own free rate and weak priors. This ablation isolates the key ingredient, the block-structured interaction prior.
A second ablation removes partial pooling, and a third removes the abstention rule so that point estimates are forced for every group.
For fairness of comparison, all methods receive identical inputs: the same device and visit counts and the same census tables. All methods get the same held-out validation split for choosing hyperparameters. Every Bayesian variant receives the same number of posterior samples.
Beating the baselines means two things. First, lower group-level flow error than uniform scaling and raking on the synthetic benchmark, with the largest gains on small intersections. Second, credible intervals whose empirical coverage is within a few points of nominal. A method with lower error but badly miscalibrated intervals does not count as a win.
Why not just…?
Why not just reweight with post-stratification or inverse-probability weights? Those weights require knowing each record's demographic group. Aggregated device traces carry no individual labels, so the only available stratification is by neighborhood, which is exactly the homogeneity assumption under test. Where an intersection has near-zero observed support, the weights explode or become undefined; FairGrad and Ma et al. on fair few-shot learning document the analogous instability in training. The uniform-scaling and raking baselines are precisely this family, so the comparison settles the question directly.
Why not just correct each attribute separately? Correcting single axes is marginal raking. Molina and Loiseau show that marginal quantities determine intersectional ones only under independence, and race, age, and income are strongly correlated through residential segregation. The raking-versus-structured comparison tests whether this matters in practice. If raking matches our method on intersectional error, we will report that intersections add nothing here. This is a real possibility wherever attribute correlations are weak.
Why not just run multilevel regression with post-stratification or plain Beta smoothing? This is the most serious alternative, because our model is essentially partial pooling plus post-stratification. The difference is the likelihood. Standard multilevel regression needs individual outcomes tagged by group, whereas ours must disentangle groups from neighborhood mixtures. Plain smoothing of per-neighborhood rates never separates groups at all. The Molina–Loiseau comparison of their estimator against Bayesian estimators shows that prior sensitivity in sparse cells is a real concern. The no-pooling and unstructured ablations measure how much of the gain comes from pooling alone and how much from the block structure. If pooling alone captures it, the structural contribution is not needed, and we will say so.
Proposed Experiments
The first experiment is the semi-synthetic benchmark, built from the 1990 US Census microdata subsets used by Molina and Loiseau. Individuals are assigned to synthetic block groups with realistic segregation. We then plant tracking and trip rates that differ by intersection and depend on venue type. Destination sorting is tuned so that venue segregation spans roughly the 0.16–0.42 range Nilforoshan et al. report. Finally, we generate device and visit counts. Metrics are error in group-level flows, interval coverage, and the precision of the "unresolved" flag against the groups that are truly unrecoverable. We vary the number of attributes from 2 to 8 to trace where resolution collapses, and we compare that collapse point with the shape Paes et al.'s bounds predict.
The second experiment uses the WMATA SmarTrip data. The 215,000 registered cards act as the biased sample, and the full 3.01 million cards give true stop-level volumes. We fit coverage rates on the registered subset against the demographic makeup of each stop's surrounding area. We then ask whether the corrected volumes predict the full volumes better than uniform scaling, especially at stops in low-income areas. No reported result was found on Lacuna for this task. External validation against group-disaggregated commuting flows, where available outside the file, would be an additional check.
The third experiment reruns the Mehrab et al. siting pipeline on SafeGraph patterns for Virginia. We measure how many of the top-ranked cells change, and how much estimated coverage of intersectional groups such as low-income elderly residents shifts, when uniform apportioning is replaced by our estimates. Unresolved groups enter the optimization as ranges, not points.
The decisive check comes from the first two experiments. On synthetic data, the structured model must cut small-intersection error relative to uniform scaling while holding interval coverage near nominal. On the fare-card data, it must predict the unobserved card volumes better than uniform scaling. If both hold, the homogeneity assumption behind current practice is shown to be both wrong and correctable. If the fare-card test fails, the method recovers structure only in simulation and should not guide real siting decisions.
References
- Multiscale dynamic human mobility flow dataset in the U.S. during the COVID-19 epidemic
- Data-Driven Real-Time Strategic Placement of Mobile Vaccine Distribution Sites
- Human mobility networks reveal increased segregation in large cities
- Can Mobility of Care be Identified from Transit Fare Card Data? A Case Study in Washington D.C.
- Bounding and Approximating Intersectional Fairness through Marginal Fairness
- Can I Trust My Fairness Metric? Assessing Fairness with Unlabeled Data and Bayesian Inference
- Structured Embedding Models for Grouped Data
- Size-adaptive Hypothesis Testing for Fairness
- On the Epistemic Limits of Personalized Prediction
- Doubly-Regressing Approach for Subgroup Fairness
- FairGrad: Fairness Aware Gradient Descent
- Fair Few-Shot Learning with Auxiliary Sets