Camera Disproportionality Tests for Unsupervised Re-Identification Pseudo-Labels

Unsupervised person re-identification tries to learn to match the same pedestrian across different cameras without anyone labeling who is who. The standard recipe clusters image features, treats each cluster as a pseudo-identity, and trains on those guesses. Its main failure is camera bias. Images from one camera share lighting, background and color balance, so the clusterer often groups by camera instead of by person. The model then trains on these bad clusters and makes the bias worse. Current fixes use blunt rules. The most effective of them deletes every cluster that contains only one camera. That rule works on benchmarks where nearly every person crosses several cameras. It throws away real people in camera networks where many pedestrians pass a single camera and leave, and it ignores clusters that are 90% one camera.

Drug-safety monitoring has faced the same statistical problem for decades. Spontaneous adverse-event databases have no exposure denominator, so analysts ask whether a drug–event pair appears disproportionately often relative to the database's background rates. They combine a sensitive frequentist ratio with a Bayesian estimate that shrinks unstable small counts toward baseline. We propose to treat each pseudo-cluster as a "drug" and each camera as an "event." A cluster's camera concentration is then tested against the camera traffic it would show if identity and camera were independent, with shrinkage for small clusters. Clusters flagged this way are not discarded outright. They go to an adjudication step borrowed from multi-algorithm consensus: a flagged cluster is kept only if it also survives clustering in a feature view that has had its camera-sensitive dimensions removed. The claim is that this pairing, a base-rate-corrected disproportionality flag plus a consensus check, tells camera artifacts apart from genuine single-camera identities. We expect it to match existing debiasing on standard benchmarks and to beat it clearly when camera traffic is sparse and uneven.

Core Claim

A cluster that is concentrated in one camera is ambiguous. It may be several different people merged by camera style, or one real person seen by only one camera. Camera counts alone cannot resolve this ambiguity. A true single-camera identity with eight images and an eight-image artifact cluster have the same camera contingency table. Our proposal therefore makes two separate claims, which the experiments test separately.

The first claim concerns detecting suspicious clusters. A disproportionality score that corrects for camera base rates and shrinks small counts flags suspicious clusters better than camera counts or camera-distribution entropy. The reason is that busy cameras naturally dominate clusters, and small clusters are dominated by chance.

The second claim concerns resolving the ambiguity among flagged clusters. A cluster that is one real person should persist when features are stripped of camera-sensitive dimensions. An artifact cluster held together by camera style should fragment. This applies the consensus principle that "genuine signals are invariant across different mathematical lenses." We deliberately build the second lens to be blind to camera bias rather than hoping two ordinary models happen to disagree.

Relation to Prior Work

The pharmacovigilance literature supplies the statistics. Studies of sapropterin (Safety assessment of sapropterin dihydrochloride) required a drug–event pair to pass the reporting odds ratio, the proportional reporting ratio, and the information component from a Bayesian confidence propagation network all at once. The multiple myeloma cardio-oncology study (Cardiovascular adverse events associated with targeted therapies for multiple myeloma) ran the reporting odds ratio and the information component in parallel, and the same pattern recurs in studies of eculizumab (ADE risk signal mining related to eculizumab), tiotropium (Adverse drug events associated with tiotropium) and dopamine agonists (Comparative safety signals of dopamine agonists). We reuse their dual frequentist-plus-Bayesian criterion and their fixed conventional thresholds. We move the criterion from drug–event tables to cluster–camera tables, which none of them consider.

The unsupervised re-identification literature motivates the problem and constrains the design. Cluster Contrast keeps one momentum-updated memory vector per cluster. Its authors concede it depends on clustering quality, and it is our base learner. Exploring the Camera Bias of Person Re-identification is the strongest prior result and the closest one. It shows that camera bias concentrates in a small set of feature dimensions. It shows that per-camera feature normalization combined with discarding single-camera clusters raises Cluster Contrast on MSMT17 from 29.8% to 49.1% mAP. It also notes that normalization needs roughly 25–50 images per camera. We keep its insight about camera-sensitive dimensions, which is what builds our second lens. We replace its binary discard rule with a graded test and an adjudication step.

Camera-aware methods take a different route. Camera-aware Proxies splits clusters into per-camera proxies. Intra-Inter Camera Similarity trains per-camera heads and then merges them. Pseudo Labels Refinement prunes cross-camera members with a centrality rule. All three change how clusters are formed or trained. None of them asks whether a cluster's camera makeup is statistically implausible.

On the consensus side, REPIC finds cryo-EM particles that all of several pickers agree on and cuts false positives on empty micrographs by 35% to 99%. Self-Similarity Grouping clusters whole-body and part features from one shared backbone. It shows that several views need not multiply training cost, and we follow it by computing both of our views from one network. The motif-discovery work of Fraenkel et al. supplies a warning we take seriously. Consensus helps only when the members make different errors. Two views of the same backbone make largely the same errors unless one is deliberately stripped of the shared bias.

Research Program

At each clustering round, after the usual clustering step (DBSCAN, a density-based clusterer), we build a two-by-two table for every cluster $k$ and camera $c$. The four cells are $A$, the images of $k$ in $c$; $B$, the images of $k$ in other cameras; $C$, the images of other clusters in $c$; and $D$, the rest. From this table we compute the reporting odds ratio $AD/BC$ with its 95% lower bound. We also compute a shrunk information component,

$$\mathrm{IC}_{kc} = \log_2 \frac{A + 0.5}{E_{kc} + 0.5}, \qquad E_{kc} = \frac{(A+B)(A+C)}{N},$$

where $N$ is the total number of training images. $E_{kc}$ is the count expected if cluster membership were independent of camera, given that camera's traffic. The additive half-counts pull small clusters toward no signal.

A cluster is flagged as camera-disproportionate if, for some camera, three conditions hold at once: $A \ge 3$, the odds-ratio lower bound exceeds 1, and the lower 95% limit of $\mathrm{IC}_{kc}$ exceeds 0. These are the conventions used in the sapropterin study, and we do not tune them.

Unflagged clusters train normally. Flagged clusters go to adjudication. We rank feature dimensions by the variance of their per-camera means, pooled over all cameras. Only a ranking is needed, which is more stable than full per-camera standardization when some cameras are sparse. We then zero out the top fraction of dimensions, set at 13% following Exploring Camera Bias, and re-cluster that debiased view.

A flagged cluster is kept if most of its members fall into a single cluster in the debiased view. The Jaccard overlap between the original cluster and its best-matching debiased cluster must exceed 0.5, a threshold we fix in advance. Otherwise the members are treated as unlabeled outliers for that round. Surviving flagged clusters can also be down-weighted in the contrastive loss by their shrunk score, which lets us test a soft variant against the hard keep-or-drop rule.

The added cost is one extra clustering pass per round on features that are already computed. No second backbone is trained.

The analysis has two parts. First, using the training identity labels that benchmarks contain but the method never sees, we label every cluster in every round. A cluster is a camera artifact if it contains two or more identities and is dominated by one camera. It is a true single-camera identity if it is pure and single-camera. It is a valid multi-camera cluster otherwise. We then measure how well each filtering rule separates these classes. Second, we measure downstream retrieval accuracy.

Baselines

The naive reference point is plain Cluster Contrast with no camera handling. It reports 83.0% mAP on Market-1501, 33.0% on MSMT17 and 40.8% on VeRi-776. We rerun it with our backbone and seeds, because the camera-bias paper reproduces it at 29.8% on MSMT17.

The strongest existing competitor is the debiased Cluster Contrast of Exploring the Camera Bias of Person Re-identification, which combines per-camera normalization with single-camera-cluster discarding. It reports 49.1% mAP on MSMT17. No reported result was found on Lacuna for this debiased variant's mAP on Market-1501 or in any sparse-traffic setting. It is the right opponent because it attacks exactly our failure mode with the cheapest possible rule. We run it in two ways: with the discard rule alone, and with normalization plus discard.

We also run Camera-aware Proxies and Pseudo Labels Refinement as representatives of camera-aware training. Pseudo Labels Refinement reports 83.2% mAP on Market-1501 and 43.3% on MSMT17.

Fairness rests on four controls. Every method uses the same ResNet-50 backbone, DBSCAN radius, epochs and data. Our thresholds are fixed conventions, while every heuristic baseline gets its cutoff tuned against ground truth. That tuning is an oracle advantage we grant deliberately. All results are reported as mean and spread over three seeds.

Four ablations isolate the ingredients. The first uses the frequentist ratio alone. The second uses the shrunk information component alone. The third runs the disproportionality flag with discarding, but without adjudication. The fourth runs adjudication on all single-camera clusters with no disproportionality flag. We also compare against two cheaper continuous scores: camera-distribution entropy, and dominant-camera fraction. The latter is tested both with and without division by that camera's traffic share.

Our bar is set in advance. On the standard benchmarks we must stay within about half a point of mAP of debiased Cluster Contrast. On the sparse splits we must exceed it by at least two points of mAP across seeds, and beat every heuristic on artifact-versus-true-identity separation. Failing the second bar while passing the first would mean the method is merely a restatement of the existing rule.

Why not just…?

Why not just discard single-camera clusters? On MSMT17 and Market-1501 almost every training identity crosses cameras, so this rule costs little there. We expect to only tie it on those benchmarks, and we say so plainly. Its weakness is structural. It deletes every true single-camera identity, and it cannot see a cluster that is 90% one camera with one stray image from another. The sparse-traffic splits described below are designed to expose exactly these cases. If the discard rule still matches us there, the proposal's practical case fails.

Why not just normalize features per camera? Normalization removes a global camera shift but says nothing about which individual cluster is wrong. Its own authors report that it needs roughly 25–50 images per camera (Exploring Camera Bias). Our thinned-camera splits push some cameras below that range. Normalization is complementary to our method, not a rival, so we also run normalization combined with our filter. It is a genuine threat on well-populated cameras, and the sparse-versus-dense comparison will show where each one breaks.

Why not just threshold camera entropy or the number of cameras per cluster? This is the most serious alternative, because it captures the graded concentration we care about with no statistics. It has two blind spots. It ignores camera base rates, since a cluster dominated by the busiest camera is expected rather than suspicious. It also treats a three-image cluster and a fifty-image cluster alike. We test entropy and traffic-normalized dominant fraction with oracle-tuned thresholds. If either one matches the shrunk disproportionality score on artifact detection, we will adopt it as the flag and keep only the adjudication step as the contribution.

Why not just ensemble several backbones and keep clusters they agree on? Different ImageNet-pretrained backbones carry correlated camera bias concentrated in similar dimensions (Exploring Camera Bias). The orthogonality that makes consensus work in REPIC is therefore unlikely to hold. Such an ensemble also multiplies training cost. We include a two-backbone agreement baseline at matched compute to check this directly.

Proposed Experiments and Decisive Checks

We train on Market-1501 (Scalable Person Re-identification), MSMT17 (Person Transfer GAN) and VeRi-776, using the standard query and gallery sets and reporting mAP and Rank-1.

We then build sparse-traffic training splits from each benchmark's training set. In these splits, a fraction of identities (20%, 40% or 60%) keep images from only one camera. In a harder variant, two or three cameras are thinned below 25 images. The test protocol stays unchanged, so gains reflect better pseudo-labels rather than an easier evaluation.

The first decisive check is diagnostic and needs no retrieval training. In the first clustering round and in later rounds, we compute the area under the ROC curve for separating camera-artifact clusters from true single-camera identities, for each flagging rule. If the full method does not beat entropy and camera count on this measure, the downstream story has no mechanism behind it.

The second check tracks the fraction of training images carrying correct pseudo-labels over rounds. The goal is to show that adjudication recovers true single-camera identities that the discard rule throws away.

The third check is retrieval accuracy against the bars stated in the Baselines section.

The fourth check tests whether adjudication really depends on removing camera-sensitive dimensions. We rerun adjudication with a random 13% of dimensions removed. If it works equally well, the benefit comes from re-clustering noise rather than from camera-blind invariance, and the consensus claim is false.