Fair Traffic Sensor Placement Under Sensor Corruption

Cities place traffic counters to estimate flow on every road from measurements on a few of them, and the standard way to choose the locations is to minimize average reconstruction error across the whole network. That choice hides a failure. When a counter sticks, drifts, or is spoofed, the estimator can only notice and discard the bad reading if other nearby measurements cross-check it. Utilitarian placements put their cross-checks where traffic is dense, so a single broken sensor in a thinly instrumented neighborhood silently corrupts that neighborhood's estimates while the network-wide average barely moves. We propose to choose sensor locations so that every geographic zone keeps its reconstruction error low even after the worst few of its sensors are corrupted, and to build the traffic model that guides placement from open census and map data instead of proprietary trajectory logs.

In two sentences: sensor corruption is not an evenly spread nuisance, because robustness to bad readings comes from measurement redundancy and utilitarian placement rations redundancy unequally. We make placement optimize the worst zone's error after corruption, measured by what the estimator can still recover once suspect readings are dropped, and we test whether that closes an equity gap that per-zone sensor quotas do not.

Core Claim

Our central claim is that under flow conservation (the rule that traffic entering a junction equals traffic leaving it), whether a zone's estimate survives a corrupted sensor depends on the redundancy structure of its measured links: which measured links are also implied by other measurements through conservation, acting like parity checks in an error-correcting code. It does not depend on the zone's sensor count. So a fair placement must allocate redundancy, not only coverage. We expect three things. Utilitarian placements that do well on clean data will show a much larger worst-zone error gap once sparse gross errors are injected. A minimum-sensors-per-zone quota will close only part of that gap. A placement that directly minimizes worst-zone post-corruption error will close most of it at a small cost in average error.

This builds most directly on Sensor Placement for Learning in Flow Networks, which places sensors greedily under flow conservation using fast Woodbury-identity updates, minimizes network-wide squared error, and tests robustness only to Gaussian noise in the initial flow guess. We reuse its machinery. What we change is the objective (worst zone rather than average) and the threat (sparse gross corruption of deployed sensors rather than a noisy prior). Sensing Resource Allocation Against Data-Poisoning Attacks in Traffic Routing does address corrupted data, placing monitors to tell poisoning attacks apart using the same 27 Anaheim zip-code subnetworks. Its goal is aggregate routing cost, though, and it never asks which zones stay exposed. The fairness motivation comes from Post-processing of Differentially Private Data: A Fairness Perspective, which proves that cleaning noisy counts separately from the downstream allocation systematically penalizes small groups. We conjecture a sensing analogue: data cleaning that runs downstream of a placement it cannot influence penalizes sparsely sensed zones. The design is constrained by Bujna et al., who find that learned models collapse below historical averages when corruption is structured. That finding steers us toward an explicit physics-constrained estimator rather than a neural imputer.

Research Program

Let $x \in \mathbb{R}^m$ be flows on the $m$ links, with a prior mean and covariance $\Sigma$. A placement $S$ of $k$ links yields readings $y_S = x_S + \epsilon + o$, where $\epsilon$ is small noise and $o$ is a sparse vector of gross errors on at most $s$ sensors. The estimator combines the prior, the conservation constraints, and an $\ell_1$ outlier term. It is a flow-network version of the low-rank-plus-sparse separation in Load Curve Data Cleansing and Imputation Via Sparsity and Low Rank, which isolates sparse bad data under the assumption that outliers are rare. A robust estimator can do no better than an oracle that knows which readings are bad and drops them. We therefore use the worst-case "leave-$s$-out" error as a computable surrogate for post-corruption error:

$$E_z(S; s) = \max_{T \subseteq S,\ |T| \le s} \ \mathrm{tr}\big(\Sigma^{\mathrm{post}}_{z}(S \setminus T)\big),$$

where $z$ indexes a geographic zone and $\Sigma^{\mathrm{post}}_z(S\setminus T)$ is the posterior covariance of the flows on zone $z$'s links given the surviving measurements and conservation. The placement problem is

$$\min_{|S| \le k} \ \max_z \ E_z(S; s) \quad \text{subject to} \quad \frac{1}{m}\sum_{\ell} \mathrm{Var}^{\mathrm{post}}_\ell(S) \le (1+\delta)\, \bar{E}_{\mathrm{util}},$$

where $\bar{E}_{\mathrm{util}}$ is the average error of the best utilitarian placement and $\delta$ caps the price of fairness.

For $s=1$, every leave-one-out posterior is a rank-one downdate, so the Woodbury trick from Burudgunte and Silva evaluates all of them cheaply. For $s>1$ we let a greedy adversary pick the readings to remove. We handle the max over zones with multiplicative weights: zones whose current error is highest get larger weights in a weighted greedy step. This is the same logic that Active Sampling for Min-Max Fairness uses to reduce the worst group's loss without degrading the others. Their convergence guarantees hold for convex losses and do not transfer to this combinatorial problem, so we report empirical convergence only. Fair Maximum Coverage warns that exact fair covering is NP-complete. We expect the same here and make no exactness claim. Instead, on the smallest instances, we compare the greedy result against an exact mixed-integer solution.

The prior $\Sigma$ is where mobility data accessibility enters. The prior needs plausible flow scenarios, and the flow-network paper assumes a known origin-destination (OD) demand matrix. We will build three priors: an oracle prior from the benchmark OD matrix, the perturbed prior that Burudgunte and Silva already test, and an open-data prior. The open-data prior samples OD matrices from WEDAN, the whole-city graph diffusion model trained on the LargeCommutingOD benchmark of 3,333 U.S. areas with census and point-of-interest features. We assign those OD samples to the road network and take the empirical covariance of the resulting link flows. This avoids the proxy bias that INSPIRE-GNN acknowledges when it trains on Strava fitness trips. It also avoids the proprietary seed data that SynMob needs. The generator is a supporting ingredient. The question for it is only whether a placement guided by an open-data prior loses little relative to the oracle prior on the fairness metrics.

The testbed is the Anaheim network, with 416 nodes, 914 directed links, and 27 zip-code subnetworks as defined by Yu et al. The zip codes serve as zones. We attach census income to each zip code so we can report error gaps between higher- and lower-income zones. Barcelona, Chicago, and Winnipeg from the flow-network paper serve as replication networks.

Baselines

The naive reference points are random placement and a betweenness-centrality placement. INSPIRE-GNN reports that centrality underperforms learned placement on Melbourne cycling, with a mean squared error of 1533.25 against 1020.48. We include centrality mainly to show where it leaves zones blind.

The strongest existing method is the flow-aware Woodbury greedy placement of Burudgunte and Silva, which reports a reconstruction correlation of 0.936 with ground truth on Anaheim, against 0.852 for the Max Flow heuristic. We rerun their algorithm on the same budgets, priors, and corruption draws as our method, and feed its placement to the identical robust estimator. Any difference therefore comes from placement alone. We found no reported result on Lacuna for per-zone or worst-zone error on Anaheim under any method, so we compute it for their placement ourselves.

The Yu et al. subnetwork-monitoring MIP is a second corruption-aware competitor. They report that monitoring 5 of the 27 subnetworks restored routing costs to near-perfect-information levels. We evaluate that placement at the matched budget.

Three ablations isolate our key ingredient. The first is utilitarian but corruption-robust: it minimizes average leave-$s$-out error. The second is fair but corruption-naive: it applies min-max over zones to clean-data error. The third is a quota variant that runs the Burudgunte greedy under a floor of at least $q$ sensors per zone, with $q$ tuned over the same search budget as our $\delta$.

Beating the field means two things at every budget between 5% and 15% of links. At the corruption levels tested, our worst-zone RMSE must be lower than that of the best baseline and the best ablation, with non-overlapping confidence intervals across corruption draws. Our average error must stay within the stated $\delta$ of the Burudgunte greedy placement.

Why not just…?

Why not just enforce a minimum number of sensors per zone on top of the utilitarian greedy? This is the most serious threat, and the quota ablation is built to settle it. Our mechanism predicts that quotas fail when a zone's sensors sit on links that no conservation relation ties together, since a corrupted reading there has no cross-check. We will measure, per zone, both sensor count and the number of independent redundancy relations among measured links, and regress post-corruption error on each. If count explains zone error as well as redundancy does, and the tuned quota matches our method, the parity story is wrong. In that case the honest recommendation is quotas, and we will report it that way.

Why not just place sensors for average accuracy and clean the data robustly afterwards? The PoS paper shows that decoupling cleaning from the downstream decision creates a provable small-group penalty. Its result concerns privacy noise on counts, however, not sensor networks. Our first ablation (utilitarian but corruption-robust, with the same robust estimator) is the direct test. If downstream cleaning were enough, that ablation would already equalize zones.

Why not just add spare sensors everywhere, or use a learned imputer to fill gaps? Uniform redundancy costs budget roughly in proportion to network size and spends it on zones that are already well cross-checked. We will show this by giving a uniform-duplication scheme the same total budget. Learned spatiotemporal imputers of the kind used for buoy data restoration are what Bujna et al. find to collapse under structured corruption. We include one as an estimator variant to check whether our placement gains persist when the estimator is learned.

Why not just use the real OD matrix instead of a generator? On Anaheim we can, and that is the oracle prior. The generator exists for cities that lack such a matrix. The comparison between the oracle prior and the open-data prior tells us whether that substitution is safe.

Proposed Experiments

The first experiment is the disparity diagnosis. We take the Burudgunte greedy placement, inject random sparse stuck-sensor errors at several corruption rates, and report the worst-zone to median-zone error ratio and the income-group error gap, with and without corruption. The project's premise holds only if this gap widens substantially under corruption. If it does not, we stop.

The second experiment compares the full method against all baselines and ablations on Anaheim at matched budgets. It uses two kinds of corruption: random corruption, and adversarial corruption modeled on the Yu et al. poisoning attacks, which target the most influential sensors. The main outcome is the worst-zone RMSE versus average-RMSE frontier as $\delta$ varies.

The third experiment is the redundancy-versus-count regression described above. It is the decisive test of the mechanism.

The fourth experiment is the prior swap. We compare placements built from the oracle prior, the perturbed prior, and the WEDAN open-data prior, and report how far fairness and accuracy degrade as the prior moves further from the true demand. WEDAN reports more than an 8% RMSE reduction and an 11.5% gain in common part of commuting (the overlap between predicted and real commuting flows) over prior OD generators. Those gains are measured on commuting flows, not link flows, so we treat link-flow fidelity as unknown until this experiment measures it.

The final experiment replicates the diagnosis and the main comparison on Barcelona, Chicago, and Winnipeg, to check that the effect is not an artifact of one network's topology.