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Withdrawn from ICLR 2027

TrustReID: Learning Which Identity Evidence to Trust for Universal Person Re-Identification

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Person re-identification (ReID) requires matching identities across changes in viewpoint, clothing, sensing modality, and visibility. In unlabeled videos, strict association criteria fragment identities across views, whereas permissive criteria introduce incorrect identity merges, compromising supervision for pre-training. During matching, visual cues that distinguish identities in one setting may mislead retrieval in another, making fixed evidence fusion inadequate for a shared model. We introduce TrustReID, a two-stage framework that addresses these challenges through view-conditioned identity pre-training and counterfactual evidence routing. In Stage I, View-Conditioned Progressive Identity Discovery (VPID) preserves view-specific prototypes and progressively links observations within and across videos using relation-specific criteria. This process assigns high-purity pseudo-identity labels to over six million person images, supporting transferable identity learning with identity-supervised losses. Under matched data and computational budgets, this identity-supervised objective outperforms contrastive pre-training. In Stage II, Counterfactual Evidence Routing (CER) complements an always-on pretrained identity branch with four experts encoding color, texture, body structure, and visible parts. A shared, task-agnostic router weights these experts for each query–gallery pair. In addition to the final retrieval loss, we supervise expert weights using the change in the positive-negative ranking margin when each expert is masked, guiding the model to select evidence that improves identity ranking. Without downstream fine-tuning, the frozen pretrained model achieves Rank-1/mAP of 77.28%/51.18% on MSMT17, 70.58%/63.84% on AG-ReID v1 under ground-to-aerial retrieval, and 97.70%/96.25% on Occluded-ReID. After joint training, TrustReID outperforms several existing unified ReID models on multiple benchmarks, while supporting six ReID settings with a single checkpoint. We will publicly release the pre-training dataset and model weights to facilitate reproducibility and future research.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Person Re-Identification, Mixture of Experts, Counterfactual Evidence Routing

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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Paper summary

This paper proposes TrustReID, a two-stage framework for universal person re-identification. In Stage I, View-Conditioned Progressive Identity Discovery (VPID) maintains identity prototypes for different person orientations and applies association rules conditioned on recording scope and viewpoint relations. The resulting pseudo-identities are used for identity-supervised pre-training on unlabeled video data. In Stage II, four experts specializing in color, texture, body structure, and visible parts are combined through Counterfactual Evidence Routing (CER), which predicts expert weights for each query–gallery pair. CER constructs auxiliary supervision for the router from changes in the positive–negative ranking margin when an expert’s contribution is removed. The final matching score combines an always-on base identity branch with adaptively weighted expert scores, supporting multiple ReID settings.

Critical strengths
  1. The motivation is clear, and the framework reasonably addresses conflicting evidence requirements across tasks. Rather than assuming that all tasks should use the same feature-fusion strategy, the paper considers how the usefulness of color, texture, shape, and local correspondence varies across matching conditions. Modeling evidence extraction and evidence weighting separately is a reasonable and practically relevant direction.

  2. The experiments cover diverse settings and distinguish direct transfer from joint training. The paper separately evaluates frozen-model direct transfer and a single jointly trained checkpoint across standard, clothes-changing, occluded, visible–infrared, sketch-based, and aerial–ground retrieval. ENTIReID is explicitly excluded from training, hyperparameter tuning, and checkpoint selection. This held-out evaluation provides useful evidence of generalization beyond the jointly trained datasets. The controlled ablations in Table 3 also provide empirical support for the benefit of utility supervision over ranking-only routing.

Critical weaknesses
  1. The proposed “counterfactual utility” is mathematically equivalent to an expert-specific ranking margin, which weakens the novelty and interpretation of CER. The central idea of Counterfactual Evidence Routing (CER) is to estimate how useful each expert is by removing that expert from the reference score and measuring the resulting change in the positive–negative ranking margin. However, because the reference score is purely additive, the proposed utility simplifies exactly to
Δe=βe[se(q,g+)−se(q,g−)].\Delta_e = \beta_e \left[s_e(q,g^+) - s_e(q,g^-)\right].

Therefore, the utility does not actually depend on the base identity branch or on any of the other experts. In other words, masking an expert does not measure its conditional contribution to the full model; it simply measures whether that expert alone prefers the positive over the negative. This substantially weakens the “counterfactual” interpretation. A stronger formulation should capture interactions between experts or measure whether an expert provides additional information beyond what the remaining branches already explain. Comparisons against simpler targets based directly on the expert ranking margin are also necessary to determine whether the proposed counterfactual formulation provides any benefit beyond ordinary expert-quality supervision.

  1. The paper does not provide sufficient evidence that the four experts actually learn the intended distinct types of identity evidence. TrustReID assumes that the four experts correspond to color, texture, body structure, and visible-part evidence. However, the paper explicitly allows their representations to overlap, and the expert-specific losses do not guarantee semantic disentanglement. For example, grayscale and low-pass transformations encourage sensitivity to particular appearance properties, but they do not ensure that the resulting representations contain only texture or color information. Similarly, silhouette reconstruction and part prediction may still preserve substantial appearance and identity information inherited from the shared backbone. The current ablation only shows that different experts have different effects on retrieval performance across datasets. This does not establish that they encode the semantic factors claimed by the method. The paper should provide quantitative probing experiments, such as predicting color, texture, body shape, and part information from each expert representation, together with cross-expert leakage tests or invariance tests under controlled perturbations.

  2. The evaluation of VPID does not adequately validate the central trade-off between incorrect identity merging and identity fragmentation. VPID is motivated by the claim that conservative association fragments the same identity, while permissive association introduces false merges. However, the pseudo-identity audit primarily measures association precision. The final pseudo-identities achieve only about 88% sampled-pair precision, and the most difficult cross-video cross-view association stage has considerably lower precision than the easy same-view stage. More importantly, the paper does not report a corresponding recall or fragmentation measure. High association precision can always be obtained by linking fewer samples, but this does not demonstrate that VPID successfully reconnects the same person across views and videos. Since solving this precision–fragmentation trade-off is one of the main motivations of Stage I, the paper should report identity-level precision and recall, fragmentation statistics, cluster purity/completeness, or pairwise F1 on a manually annotated subset.

  3. The current VPID ablation conflates several algorithmic changes, making it difficult to identify which component is actually responsible for the gain. The “w/o VPID” baseline is not obtained by removing only view conditioning. It simultaneously changes the clustering threshold strategy, removes viewpoint-specific association, restricts positive relationships across cameras, and eliminates the progressive cross-view/cross-video association procedure. Therefore, the improvement of the full VPID model cannot be attributed specifically to view-specific prototypes or progressive association. A more informative ablation should separately evaluate: a single prototype versus view-specific prototypes, fixed versus relation-specific thresholds, progressive versus one-shot association, with/without camera-time constraints, with/without reciprocal-neighbor filtering, and with/without the final cross-video cross-view stage. Without these controls, VPID is currently validated as an entire heuristic pipeline rather than as a clearly justified algorithmic contribution.

  4. The contribution of CER to the final jointly trained model is not cleanly separated from the effect of multi-dataset supervised fine-tuning. The main Stage II model is obtained by jointly fine-tuning the shared backbone, identity branch, and router on multiple downstream datasets. This produces very large improvements on several benchmarks. However, the main routing ablation is performed with the identity branch and expert representations fixed. Therefore, the ablation does not directly establish how much of the final Stage II improvement comes from CER versus ordinary supervised multi-dataset adaptation of the backbone. There is also a consistency issue during joint fine-tuning: the expert modules remain frozen while the shared backbone is updated, and the expert-specific specialization losses are no longer applied. Since all experts consume features from the shared backbone, their input distributions can change during this stage, potentially altering the intended expert semantics. The paper should include matched joint-training baselines such as identity-only fine-tuning, fixed expert fusion, rank-only routing, and full CER under exactly the same backbone-update schedule. It would also be useful to evaluate whether expert specialization is preserved before and after joint fine-tuning.

  5. The evidence for “universal” generalization is limited because most Stage II evaluations are performed on datasets participating in joint training. The paper emphasizes a task-agnostic router and a single universal ReID checkpoint, but most of the strong Stage II results are obtained on datasets whose training splits participate in the multi-dataset joint-training procedure. ENTIReID is the main dataset explicitly held out from training, hyperparameter tuning, and checkpoint selection. This makes it difficult to distinguish genuine task-agnostic evidence routing from successful multi-task supervised adaptation to a known collection of retrieval conditions. A stronger evaluation would use leave-one-dataset-out or leave-one-setting-out training, where the router is trained without seeing one complete retrieval condition and is then evaluated on that unseen condition. Such experiments would provide much stronger evidence that the learned routing rule generalizes across ReID settings rather than primarily exploiting distributional patterns observed during joint training.

  6. The relationship between triplet-level utility and pair-specific routing supervision requires stronger justification. Equation (12) measures an expert’s contribution to a triplet-level ranking margin, whereas Eq. (13) aggregates this quantity into soft targets for pair-specific weights. For a single-triplet illustration, expert scores of 0.8 and 0.6 produce a target of approximately 0.55 for both pairs under the stated settings. Importantly, this is a soft target rather than an unconditional instruction to increase either weight, and aggregation over different triplet sets may produce different targets for the two pairs. Nevertheless, when the negative-pair weight is below this target, increasing that weight alone reduces the triplet’s ranking margin, holding the scores and other contributions fixed. This illustrates a potential local tension, not an invalidation of the overall objective: the utility loss may serve as a useful reliability regularizer alongside the ranking loss. Please clarify this interpretation and examine the compatibility of the two objectives. A comparison with targets derived from separate positive- and negative-pair interventions would be informative.

  7. Association thresholds and the scope of the pseudo-identity quality audit need clarification. Tables 5 and 10 report inconsistent thresholds for the same four association stages. In stage order, Table 5 gives 0.85, 0.80, 0.75, and 0.70, whereas Table 10 gives 0.88, 0.82, 0.75, and 0.68. Please clarify which configuration generated the pre-training data and whether the reported quality audit evaluates that configuration. Appendix B already describes an audit of 200 associations per regime and 500 within-cluster pairs, with precision calculated after excluding undetermined cases. The reported 88.1% precision provides useful evidence of sampled pair consistency. However, the sampling procedure does not clearly establish how clusters of different sizes are represented, and the audit does not characterize identity fragmentation. Please specify whether sampling is uniform over clusters or within-cluster pairs, clarify whether the audit subset is independent of threshold selection, and assess erroneous merges and fragmentation on a manageable annotated subset. A matched non-VPID comparison would further strengthen the evidence.

  8. Expert specialization and the preservation of intended cue-specific sensitivities need direct validation. The specialization objectives are reasonably motivated, but they do not directly establish that the final experts retain their intended sensitivities. In particular, how is the grayscale-negative objective for the color expert handled when infrared or sketch inputs are already approximately grayscale? In such cases, the transformation may provide little meaningful color-removal contrast. The stated sample-validity criterion mainly concerns clothing-mask coverage, so any additional modality or chromatic-content filtering should be clarified. Furthermore, final fine-tuning updates the shared backbone without expert-specialization losses. Freezing the expert heads therefore does not guarantee preservation of their intended cue-specific sensitivities, since their input representations continue to change. Please evaluate expert scores and routing weights under controlled color, texture, and occlusion perturbations before and after fine-tuning, preferably using transformations different from those used for training. These tests need not demonstrate strict disentanglement or unchanged outputs; they should establish that the intended evidence preferences remain present in the final model.

  9. Pairwise retrieval costs are not sufficiently reported. Caching image features does not eliminate the additional cost of pair-dependent routing. Please report per-query latency at increasing gallery sizes, peak GPU memory, feature-storage requirements, and routing overhead relative to the identity-only baseline under matched hardware, batch size, and caching conditions. Per-image feature extraction and pairwise scoring costs should be reported separately.

Minor Issues

  1. Table 5 lists association thresholds of 0.85, 0.80, 0.75, and 0.70, whereas Table 10 lists 0.88, 0.82, 0.75, and 0.68. Please clarify whether these correspond to different configurations or correct the inconsistency.
  2. Figure 3's caption mentions \emph{m}AP, but both Rank-1 and mAP are plotted. Please revise.
  3. The pseudo-identity audit paragraph (Appendix B) contains a typographical error: "Association precision ranges from 96.4" lacks proper formatting and separation from the following sentence.
  4. The paper should clarify the exact relationship between reference utility targets and learned router weights, and explicitly identify which components are frozen during each training phase.
Questions for authors

Please refer to Weaknesses.

2 comments

W = Critical Weaknesses, Q = Questions For Authors

W1: Equation (12) explicitly gives Δe=βe[se(q,g+)−se(q,g−)]\Delta_e=\beta_e[s_e(q,g^+)-s_e(q,g^-)]. This equivalence follows from the intentionally additive reference: removing an expert measures its contribution to that reference ranking margin, without additional forward passes. It does not estimate interactions or information beyond the remaining experts. CER’s contribution is to turn this expert-level ranking signal into explicit supervision for pair-dependent evidence routing. Equation (13) aggregates utilities into detached pair-level targets, which supervise the router alongside the final ranking loss. A direct-margin implementation using the same calibration, coefficients, aggregation, and target mapping would produce identical supervision; we do not claim an additional benefit from expressing it through masking. Table 3 evaluates the benefit of this supervision under fixed representations and matched routing settings. Adding utility supervision to rank-only routing improves mAP by 3.29, 3.38, and 3.13 points on PRCC, SYSU-MM01, and PKU-Sketch. These results support the contribution of explicitly supervising evidence selection within our specialized-expert framework.

W2+W9: TrustReID separates two complementary questions. The first is what evidence each expert expresses. The second is how that evidence should be used for the current query gallery pair. Specialization objectives guide the first question. Complementary grayscale and low pass objectives plus chromatic histogram supervision guide color and texture preferences. Silhouette reconstruction and human parsing supervision guide body structure and visible part information. Figure 4 shows these transformations and supervision targets. CER addresses the second question through ranking utility supervised pair fusion. Experts can therefore retain shared identity information, which does not conflict with intended cue preferences. Our goal is useful specialized representations, not mutually exclusive semantic representations. Table 3 supports both aspects. With the identity representation fixed, color and texture improve MSMT17 mAP from 51.18 to 53.19 and 54.09. The structure expert improves PRCC mAP from 35.78 to 47.29. Visible part evidence improves Occluded ReID mAP from 96.25 to 98.41. These results agree with the intended complementary retrieval roles. Compared with fixed fusion, CER further improves PRCC and SYSU MM01 mAP by 7.13 and 8.28 percentage points, supporting the value of learning how to use existing evidence rather than fixing its contribution. For grayscale negatives, this objective is used for color specialization training between original visible images and their grayscale transformations. The current pipeline uses paired samples including visible subsets of SYSU MM01 and LLCM. It does not uniformly apply color removal contrast to infrared and sketch inputs. Modality sample selection here differs from clothing region coverage conditions. The former determines training sample sources. The latter determines the validity of regional supervision. The implementation adds no additional chromaticity filtering threshold. Joint fine tuning keeps the learned expert modules and freezes their parameters while updating the shared representation, identity branch, and router so that evidence use adapts to the final retrieval objective. What is frozen is the expert parameters, not an assumption that their input representations remain completely unchanged. The core of TrustReID is to establish different evidence preferences through specialization objectives and then let CER learn fusion according to the discriminative value of evidence for the current identity match. We therefore state the original conclusion explicitly as cue guided expert design and the retrieval value of its adaptive fusion, corresponding to the above training mechanism and experimental evidence.

W3+W8: Pretraining and the audit both use the Table 10 thresholds: 0.88, 0.82, 0.75, and 0.68. Table 5 contains outdated values and will be corrected. These thresholds were fixed before audit sampling; audit results were not used to select or adjust them. We audited 200 associations per regime and 500 within-cluster pairs. For the latter, we uniformly sampled 500 eligible clusters without replacement, then randomly selected two images without replacement from each cluster. Thus, sampling is uniform over clusters, rather than over all within-cluster pairs. The audit contains 423 correct, 57 incorrect, and 20 undetermined pairs, giving 88.1% precision among determinate pairs, with 4.0% undetermined. The added comparison uses a uniform threshold of 0.8 as the control. Relation-specific thresholds improve sampled precision from 92.8→96.4%, 88.6→91.3%, 83.7→85.4%, and 75.8→77.7% in Table 10’s regime order. Final within-cluster precision increases from 84.4% to 88.1%.

W = Critical Weaknesses, Q = Questions For Authors

W4: We added ablations using approximately 500k images, as repeating pretraining on the SurvID-6M was not feasible within the rebuttal period. We added five controlled configurations: A full VPID, B single prototype, C one-shot association, D same-camera positives only, and E single prototype with same-camera positives; relation-specific thresholds are identical across all five. Rank-1/mAP (%) in ENTIReID / MSMT17 / Market1501 order: A 54.32/55.41; 62.15/33.24; 79.82/67.61. B 53.58/54.61; 61.55/33.04; 79.46/67.41. C 52.17/54.72; 61.26/32.52; 78.75/67.18. D 50.42/52.31; 61.45/33.14; 77.88/64.05. E 50.12/51.89; 59.95/32.09; 77.52/64.47. A−B isolates view-specific prototypes: +0.74/+0.80, +0.60/+0.20, +0.36/+0.20. A−C isolates progressive association: +2.15/+0.69, +0.89/+0.72, +1.07/+0.43. A−D isolates cross-camera positives under full VPID: +3.90/+3.10, +0.70/+0.10, +1.94/+3.56. B−E tests cross-camera positives under a single prototype: +3.46/+2.72, +1.60/+0.95, +1.94/+2.94. D−E tests view-specific prototypes with cross-camera positives disabled: +0.30/+0.42, +1.50/+1.05, and +0.36/−0.42. View-specific prototypes improve Rank-1 on all three datasets, showing that their benefits in these comparisons are not solely explained by cross-camera positive sampling.

W5: Table 3 deliberately freezes the backbone, identity branch, and expert representations to isolate the benefit of routing supervision from backbone adaptation. Under matched settings, adding utility supervision to rank-only routing improves mAP by 3.29, 3.38, and 3.13 points on PRCC, SYSU-MM01, and PKU-Sketch. These gains therefore demonstrate a contribution from CER without multi-dataset backbone fine-tuning. The final Stage II results evaluate the complete jointly trained system: the backbone, identity branch, and router are updated while expert parameters remain frozen. Table 3 establishes CER’s benefit under controlled representations, but does not quantify its separate contribution after joint fine-tuning. The matched joint-training comparison could not be completed during rebuttal. We will add an identity-only fine-tuning control using the same downstream data, initialization, backbone-update schedule, and training budget. The expert-specialization question is addressed in our response to W2/W9.

W6: ENTIReID is excluded from training, tuning, and checkpoint selection: Stage I (66.67/67.78), Stage II (70.0/71.1). Added LTCC cloth-changing evaluation, Stage I 33.93/18.95, Stage II 62.96/39.06. We distinguish unseen-dataset transfer from an entirely unseen retrieval condition.

W7: During router training, the backbone and experts are frozen; both losses update the router. Eq. (13) supplies an auxiliary reliability target aggregated over triplets, while the ranking loss optimizes the final fused margin. For a negative pair with a positive expert score, moving a weight toward a higher utility target can locally oppose the ranking loss, λutility\lambda_{\mathrm{utility}} controls their balance. Table 3 shows empirical compatibility on all six protocols. Adding utility supervision improves Rank-1 and mAP on all six protocols.

W10: Cached single-query retrieval takes about 0.557/0.565/3.445/31.960 ms at 1K/10K/100K/1M. Similarity and routing need about 22,400 MACs per pair; cost grows linearly with gallery size. We process 16,384 candidates at a time and store no gallery-by-gallery routing matrix; feature storage still grows with gallery size.

Reviewer_tjMMOpenReview ↗
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Paper summary

The information that can be used to determine identity is not the same under different conditions such as changing clothes, occlusion, and cross modality, and the model should not always fuse this information in the same way. This paper proposes TrustReID to address this issue. Specifically, by associating trajectories from unlabeled videos, a large-scale pseudo identity dataset SurvID-6M is constructed for pre training basic identity representation. The method trained experts who focus on different visual cues and supervised the router to learn fusion weights based on the ranking changes before and after removing a certain expert. The main contributions of the paper include the process of constructing large-scale pseudo identity data and the adaptive fusion method based on expert ranking contributions. The paper evaluated this framework in various ReID scenarios and provided pseudo identity quality auditing, data scale analysis, and specific implementation details.

Critical strengths
  1. Under different ReID conditions, information such as color, texture, body structure, and local visibility may change, and fixed fusion has limitations. The paper adopts expert routing using query–gallery pairs and provides a specific and feasible solution for conditional adaptive fusion by masking experts to generate additional counterfactual utility supervision.

  2. The paper validated multiple ReID conditions and presented the results of direct transfer with frozen pretrained representations and subsequent expert and routing training. The appendix provides detailed implementation details and evidence of data quality.

Critical weaknesses
  1. Table 3 has compared the results of using only ranking loss and adding utility supervision, but it is not clear whether the two experiments used exactly the same backbone, experts, score calibration, router structure, and training settings. If other settings also change, it is difficult to attribute performance improvement solely to utility supervision.

  2. The current supervision measures an expert’s contribution to the positive–negative ranking margin, but this does not necessarily mean that the visual cues relied upon by the expert are more reliable.

  3. The differences in performance of different experts on different datasets do not directly indicate that the router will reduce their reliance on relevant experts when color, texture, or body parts are disturbed or obstructed. More targeted experiments are needed to verify whether this weight adjustment is indeed effective.

  4. The training data and retrieval conditions used by experts and the router respectively need to be explained more clearly.

  5. It is not clear whether the quality audit of pseudo-identities is independent of threshold selection. If the audit samples also participate in the selection of association thresholds, the quality assessment may be optimistic.

  6. The selection of 500 within-cluster pairs, how many of them cannot be determined whether they are the same person, and how these uncertain pairs are included in the statistics will affect the results, and whether these results can represent the quality of the entire dataset.

Questions for authors
  1. What specifically does' Trust 'refer to in the paper? Is it said that a certain expert can help the model rank the current sample more accurately, or is it said that the visual cues relied upon by this expert are more reliable?
  2. Is there any experiment that can show that when color, texture, or local visibility is disturbed, the router will correspondingly reduce their dependence on relevant experts and improve retrieval performance?
  3. Which datasets were used to train the experts and the router, respectively, and what retrieval conditions were covered? What results truly involve types of conditions that have not been seen in training?
1 comment

W = Critical Weaknesses, Q = Questions For Authors

W1: The last two rows of Table 3 differ only in utility supervision: λutility=0\lambda_{\mathrm{utility}}=0 versus 11. Both use identical backbone/expert checkpoints, score calibration, router architecture and initialization protocol, training data, sampling, optimizer, learning-rate schedule, and training budget. Only the router is updated; the backbone, identity branch, and experts remain frozen.

W2 + Q1: “Trust” refers to how useful the evidence provided by an expert is for distinguishing identities under the relevant matching conditions. We operationalize this through ranking utility: Eq. (12) measures the expert’s contribution to the positive–negative reference margin, and Eq. (13) aggregates it into pair-level supervision for a router that does not require explicit task labels. Expert-specific objectives guide what evidence is represented, while utility supervision guides when to rely on it.Table 3 supports this interpretation. For example, fixed color-expert fusion increases mAP from 51.18 to 53.19 on MSMT17 but decreases it from 35.78 to 31.84 on PRCC, illustrating that the value of the same evidence depends on the retrieval condition. With representations fixed, adding utility supervision over rank-only routing further improves mAP by 3.29, 3.38, and 3.13 points on PRCC, SYSU-MM01, and PKU-Sketch. These results support ranking utility as a useful supervision signal for evidence selection. We will clarify that “Trust” concerns evidence usefulness for identity matching, rather than a guarantee of cue reliability under every visual perturbation.

W3 + Q2: Router weights are learned to reflect each expert’s usefulness for identifying a query–gallery pair, rather than the perceptual quality of its associated visual attribute. In visible-light retrieval, imperfect color information can still help distinguish identities. In visible–infrared retrieval, even clear color information in the visible image may have limited matching value because comparable color evidence is unavailable in the infrared image. Thus, weighting depends on the evidence’s relevance to the matching condition and the particular image pair, without explicit task labels. Table 3 evaluates the retrieval benefit of this learned fusion under frozen representations.

W4 + Q3: The experts and router use the same downstream training pool from the datasets listed in Table 6, excluding ENTIReID. Training covers standard, clothes-changing, occluded, visible–infrared, sketch–photo, and aerial–ground ReID, with balanced dataset sampling and identity labels kept distinct across datasets. Expert specialization updates only the experts using cue-specific objectives. Router training updates only the router, with the backbone, identity branch, and experts frozen. Ranking triplets are constructed within the same dataset and retrieval condition, following the corresponding protocol and excluding self-matches. Conditions guide sampling but are not supplied as router inputs. ENTIReID is excluded from training, hyperparameter tuning, and checkpoint selection, testing transfer to an unseen standard-ReID domain. Separately, Stage I uses only visible-light SurvID-6M images without downstream adaptation; its visible–infrared and sketch–photo results in Table 8 evaluate matching conditions unseen during pretraining. These provide distinct evidence from Stage II evaluation on the jointly trained retrieval settings.

W5 + W6: Association thresholds were fixed before audit sampling, and the audit results were not used to select or adjust them. The audit evaluates the pseudo-identities actually used for pretraining. We uniformly sampled 500 distinct clusters containing at least four images, without replacement, and randomly selected two images without replacement from each cluster. Of the resulting pairs, 423 were correct, 57 incorrect, and 20 undetermined. Excluding undetermined cases gives 423/(423+57) = 88.1% precision; their proportion is reported separately as 4.0%. Each eligible cluster has equal selection probability, rather than each within-cluster pair across the corpus. The reported precision therefore describes determinate-pair consistency under this cluster-uniform sampling scheme.

Reviewer_4xa1OpenReview ↗
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Paper summary

This paper presents TrustReID for universal person re-identification. It first builds a large-scale dataset, SurvID-6M, using view-conditioned progressive identity discovery, and pretrains an identity model with pseudo-identity classification and triplet losses. It then adds four experts that focus on color, texture, body structure, and visible parts. A router assigns expert weights to each image pair and combines their scores with those of the identity branch. The router is also trained by measuring how removing each expert affects the ranking margin between positive and negative pairs. The method is evaluated across six ReID settings, including direct transfer without fine-tuning and multi-dataset training using a single model.

Critical strengths
  1. The paper addresses a real conflict in universal ReID: clothing cues help standard retrieval but can hurt clothes-changing and cross-modal matching.
  2. The four experts have explicit training objectives, giving their color, texture, structure, and part roles a concrete basis.
  3. The frozen Stage I model transfers well without downstream training, reaching 77.28% Rank-1 and 51.18% mAP on MSMT17.
Critical weaknesses
  1. The exact pretraining data sources and downstream overlap checks are insufficiently documented.
  2. The VPID ablation confounds viewpoint conditioning with cross-camera positive sampling.
  3. Pair-dependent routing lacks a scalability analysis for large galleries.
  4. The impact of residual pseudo-label noise is not evaluated, despite the reported 88.1% pair precision.
Questions for authors
  1. Could you separately ablate viewpoint conditioning, progressive association, and cross-camera sampling?
  2. Does identity-supervised pretraining still outperform stronger contrastive baselines under matched budgets?
  3. What are the exact SurvID-6M sources, and how is overlap with downstream benchmarks checked?
  4. What are the query latency, gallery storage, and throughput at different gallery sizes?
  5. How sensitive is pretraining performance to pseudo-label noise and association thresholds?
1 comment

W = Critical Weaknesses, Q = Questions For Authors

W1 + Q3: SurvID-6M was constructed exclusively from RGB surveillance videos collected by our team using 49 campus cameras. No images or videos from any downstream benchmark were included in its construction.

W2 + Q1: We added ablations using approximately 500,000 images, as repeating pretraining on the SurvID-6M was not feasible within the rebuttal period. The same relation-specific thresholds were used across configurations. Relative to the full configuration A, B ablates viewpoint conditioning in the prototype representation by replacing view-specific prototypes with a single prototype, C replaces progressive association with one-shot association, and D disables cross-camera positive sampling by restricting positive pairs to the same camera. Thus, A−B, A−C, and A−D separately examine these three factors with the other components fixed. In ENTIReID/MSMT17/Market1501 order, the corresponding mAP gains are 0.80/0.20/0.20, 0.69/0.72/0.43, and 3.10/0.10/3.56 percentage points; Rank-1 also improves in all three comparisons on all three datasets. We additionally evaluated E, which combines a single prototype with same-camera-only positive sampling while retaining progressive association. Comparing D with E tests viewpoint-conditioned prototypes with cross-camera positive sampling disabled, yielding mAP changes of +0.42/+1.05/−0.42 points. The gains on ENTIReID and MSMT17 therefore remain present without cross-camera positive sampling. Together, these comparisons distinguish the effects of viewpoint conditioning and cross-camera sampling at the evaluated scale.

W3 + Q4: Caching image features avoids repeated encoding, but each query still requires scoring every gallery candidate. Similarity computation and routing together require approximately 22,400 MACs per pair, excluding auxiliary operations. The scoring work therefore grows linearly with gallery size—doubling the gallery roughly doubles the computation. We process 16,384 candidates at a time to limit temporary GPU memory, without storing a gallery-by-gallery routing matrix; feature storage still grows with gallery size. In our preliminary architecture benchmark, cached single-query retrieval takes 0.557, 0.565, 3.445, and 31.960 ms for galleries of 1K, 10K, 100K, and 1M images, respectively.

W4 + Q5: Pseudo-identities supervise both cross-entropy and triplet losses. Incorrect associations can introduce false positives or false negatives, weakening identity learning. We assessed threshold sensitivity by comparing uniform and relation-specific thresholds. Sampled association precision improves from 92.8% to 96.4% for intra-video/same-view associations, 88.6% to 91.3% for cross-video/same-view, 83.7% to 85.4% for intra-video/cross-view, and 75.8% to 77.7% for cross-video/cross-view. Final within-cluster pair precision increases from 84.4% to 88.1%, a gain of 3.7 percentage points. These results support relation-specific thresholds for improving association consistency in the audited samples. The uniform-threshold baseline uses a fixed threshold of 0.8 across all four association regimes.

Q2: The relative strength of a contrastive baseline depends on the task, training configuration, and available budget, so a stronger alternative needs to be specified through a concrete implementation. Table 2 compares identity-supervised and contrastive pretraining strategies under matched data and computational budgets. Our contrastive implementation adapts MoCo to use pseudo-identity associations, including cross-camera positive pairs. Identity-supervised pretraining with VPID outperforms this configuration on all three evaluated benchmarks, supporting its use in our pipeline. Whether this advantage extends to additional competitive contrastive configurations remains to be verified.

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