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Under review as a conference paper at ICLR 2027

Reading Decoder Trajectories: Training-Free Counterfactual Query-Trajectory Reliability for Small-Object Detection

Abstract

Small-object detection remains challenging because limited pixels cause information loss and suppress the scale knowledge encoded in pretrained detectors. Existing approaches mainly improve representations through multiscale training, architecture redesign, or parameter adaptation, implicitly assuming that frozen models lack the required capability. We challenge this assumption and hypothesize that small-object knowledge already exists in frozen detectors but remains underactivated and unstable during query evolution. To test this hypothesis, we propose Counterfactual Query-Trajectory Reliability (CQTR), a training-free framework that elicits latent responses through counterfactual scale interventions and interprets candidate reliability from decoder-internal spatial convergence, semantic persistence, and cross-scale conflicts. A small unlabeled training subset selects the appropriate correction mechanism for each model–data stream, without parameter updates or target-domain annotations. Across 27 combinations of nine frozen detectors and three datasets, CQTR consistently improves average precision (AP) and average precision for small objects (APs). Closed-loop analyses further show that scale intervention activates latent responses, trajectory evidence predicts ground-truth support, and unlabeled routing selects the more effective branch. CQTR therefore reframes small-object detection from external scale augmentation to the activation and reliability assessment of latent scale knowledge.

Primary area:
unsupervised, self-supervised, semi-supervised, and supervised representation learning
Keywords:
Small-object detection, training-free inference, counterfactual scale intervention, query trajectory interpretation, mechanistic interpretability, frozen object detectors

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_Ex94OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes Counterfactual Query-Trajectory Reliability (CQTR), a training-free framework for improving small-object detection with frozen DETR-based detectors. It combines counterfactual scale inference, decoder-trajectory reliability estimation, cross-scale semantic conflict correction, and unlabeled stream routing. Experiments across nine detectors and three datasets show consistent improvements in AP and APs without parameter updates.

Critical strengths

1.The paper explores an interesting training-free perspective on small-object detection by investigating latent capabilities in frozen detectors.

2.The framework is applicable to nine detectors with different query mechanisms, demonstrating broad architectural compatibility.

3.The decoder-trajectory analysis provides useful insights into spatial convergence and semantic persistence.

4.The experiments cover multiple datasets and include component ablations and interpretability analyses.

Critical weaknesses

1.Limited contribution beyond scale augmentation. Table 1 shows that counterfactual scaling accounts for nearly all performance gains. The complete framework improves over scale-only inference by just 0.03, 0.05, and 0.10 AP on COCO, TinyPerson, and VisDrone, respectively. This weakens the claimed methodological contribution.

2.Insufficient justification for trajectory reliability. Spatial convergence and semantic persistence are heuristic indicators. Incorrect predictions may also remain stable across decoder layers. Comparisons with simpler confidence- or uncertainty-based reliability measures are missing.

3.Limited validation of the routing strategy. The routing mechanism relies on manually chosen thresholds and selects a fixed correction branch for each model-dataset combination. Its robustness to threshold choices and calibration subsets remains unclear.

4.Insufficient efficiency analysis and baseline comparisons. CQTR requires additional high-resolution inference, potentially increasing computational costs. Comparisons with standard multiscale inference, high-resolution testing, and slicing-based approaches under matched computational budgets are needed.

Questions for authors

1.What evidence demonstrates that trajectory-based correction provides substantial benefits beyond counterfactual scaling?

2.How does trajectory reliability compare with confidence- or entropy-based alternatives?

3.How sensitive is stream routing to its thresholds and calibration subsets?

4.What are the inference costs compared with conventional multiscale approaches?

6 comments
AuthorsOpenReview ↗

Response to Weakness 1 and Question 1

We thank the reviewer for highlighting this distinction. We agree that counterfactual scaling accounts for most of the detection gains. On RT-DETR-R50, the selected reliability correction adds only 0.03, 0.05, and 0.10 AP over scale-only inference on COCO, TinyPerson, and VisDrone, respectively. These results do not establish a substantial AP contribution from trajectory correction, and we have revised our claims accordingly. To clarify whether trajectory evidence nevertheless provides information beyond final confidence, we added two complementary analyses on all 5,000 COCO val2017 images. First, we evaluated 273,920 eligible small-object candidates using score-ordered, one-to-one, same-class matching at IoU ≥ 0.5, counting duplicate predictions as false positives. Across trajectory-evidence quintiles, matched-positive rates increase monotonically from 0.58% to 12.32%. After controlling for final confidence, predicted box area, class, and local crowding using image-grouped five-fold cross-validation, adding trajectory evidence increases AUROC by 0.000691, with a 95% image-bootstrap confidence interval of [0.000278, 0.001045]. This indicates a positive but small incremental predictive contribution. Second, among the 10,523 matched predictions, mean IoU increases from 0.692 to 0.843 across evidence quintiles, and the proportion achieving IoU ≥ 0.75 rises from 34.49% to 84.27%. The partial rank correlation remains positive after controlling for the same variables, at 0.158 [0.137, 0.179]. This supports trajectory evidence as a complementary indicator of localization quality among matched predictions. However, our current correction adjusts confidence scores rather than box coordinates, and its realized AP benefit remains modest. We therefore distinguish the primary performance gains from scaling, the diagnostic information supplied by decoder trajectories, and the limited additional gains achieved by the current correction rule. We have revised the abstract, introduction, contributions, and conclusion to reflect this distinction, and report the additional analyses in Section 4.5 and Appendices A.4–A.5.

AuthorsOpenReview ↗

Response to Weakness 2 and Question 2

We thank the reviewer for suggesting these comparisons. We have added an appendix subsection, “Comparison with Confidence and Entropy-Based Reliability Measures,” reporting controlled experiments with frozen RT-DETR-R50 on all 5,000 COCO val2017 images. We compare final confidence, binary-entropy certainty computed from all 80 sigmoid class responses, and trajectory evidence. All methods use identical native and counterfactual predictions, candidate budgets, fusion procedures, and postprocessing. Each reliability measure is inserted into the same score-recalibration rule with a fixed strength of β=0.05\beta=0.05. Stream-level branch selection is disabled. We also verified the correspondence of all 273,920 eligible candidates with the original diagnostic cache, including matching labels, confidence scores, and trajectory evidence. Ground truth is used exclusively for evaluation and post hoc analysis. As reported in Table 13, scale-only inference achieves 54.1826 AP and 38.5090 APs. Confidence recalibration achieves 54.2305 AP and 38.6005 APs, while trajectory evidence achieves 54.2314 AP and 38.6475 APs. Binary-entropy certainty yields 54.1759 AP and 38.5088 APs. Thus, trajectory evidence performs comparably to confidence recalibration in overall AP and yields slightly higher small-object AP. We do not interpret the 0.0009-point AP difference as a meaningful performance advantage. We additionally examine localization-quality discrimination among 10,523 one-to-one matched small-object predictions, defining high-quality localization as IoU ≥ 0.90. Table 14 reports an AUROC of 0.7340 for trajectory evidence, compared with 0.7215 for confidence and 0.4631 for binary-entropy certainty. These results support trajectory evidence as a localization-quality indicator within the matched subset. Overall, the added comparisons support a qualified conclusion: trajectory evidence provides useful localization-quality information, but its realized detection benefit under the current recalibration rule is modest and broadly comparable to confidence recalibration. We have clarified this distinction in the appendix. We also specify that these results concern a shared recalibration rule with fixed β, rather than separately optimized settings for each measure.

AuthorsOpenReview ↗

Response to Weakness 3 and Question 3

We thank the reviewer for requesting a broader evaluation of routing sensitivity. We have added the appendix subsection “Sensitivity and Selection Accuracy of Unlabeled Routing,” covering all 27 model–dataset combinations. We vary the calibration subset size over M in {25,50,100,200}, use five random seeds, and independently perturb each of the two routing thresholds by −10%, 0%, and +10%. This produces 180 configurations per model–dataset combination and 4,860 configurations in total. For each seed, smaller calibration subsets are nested within the corresponding 200-image subset. All calibration images come from the training split and are used without annotations. Detector parameters and correction rules remain fixed. Across these configurations, 4,444 of 4,860 routing decisions (91.44%) agree with the default decision obtained using 100 images, seed 31415, and the original thresholds. This indicates that routing decisions are usually stable under the tested variations in subset size, sampling seed, and thresholds. This agreement measures stability relative to the default route, rather than selection accuracy. To assess selection accuracy separately, we evaluate both correction branches on each complete evaluation split. The default router selects the higher-AP branch in 19 of 27 combinations (70.37%). We also report AP regret, defined as the AP difference between the better branch and the selected branch. Mean regret is 0.0342 AP points, and maximum regret is 0.2897 points. The largest discrepancy occurs for DAB-DETR on COCO, where the selected conflict branch achieves 37.9431 AP, compared with 38.2328 AP for trajectory recalibration. Evaluation annotations are used only for this retrospective assessment and do not influence calibration or routing. These results show that the router is usually stable within the tested perturbation range, while incurring a small average AP regret. However, it does not consistently select the optimal branch. We therefore clarify that the router is a heuristic supported by these experiments, rather than a guarantee of optimal branch selection, and distinguish routing stability from selection accuracy throughout the revised discussion.

Reviewer_tcrKOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper proposes Counterfactual Query-Trajectory Reliability (CQTR), a training-free framework for improving small-object detection with frozen pretrained detectors. The paper investigates whether pretrained detectors already possess small-object detection capabilities that remain underutilized during standard inference, rather than fundamentally lacking the required representations. To investigate this hypothesis, CQTR introduces a counterfactual scale intervention to elicit additional object responses from frozen detectors. It then estimates prediction reliability using spatial convergence and semantic persistence across decoder layers, together with cross-scale semantic conflicts. An unlabeled stream-level routing mechanism selects between trajectory-based score recalibration and conflict-based suppression without requiring parameter updates or target-domain training annotations. The authors evaluate CQTR on nine detection architectures across three datasets (COCO, TinyPerson, and VisDrone2019), covering 27 model-dataset combinations. The results consistently demonstrate improvements in overall AP and small-object AP.

Critical strengths
  1. The research question and motivation is interesting. Instead of approaching small-object detection solely through representation enhancement, architectural modifications, or additional training, the paper investigates whether frozen detectors already encode useful small-object knowledge that remains insufficiently activated or utilized during standard inference. This perspective is conceptually appealing and provides a meaningful alternative way to understand small-object detection failures. In particular, examining the spatial and semantic evolution of decoder queries to assess prediction reliability is an interesting direction beyond conventional confidence-based prediction analysis. The combination of counterfactual scale interventions and decoder-internal reliability assessment offers a potentially useful perspective on the inference behavior of pretrained detectors. I consider this problem formulation and the associated investigation to be an important strength of the paper.

  2. The paper provides relatively comprehensive experimental validation across nine detection architectures and three datasets, covering 27 model-dataset combinations. CQTR consistently improves both overall AP and small-object AP across all evaluated settings. For example, on COCO, the reported AP improvements range from 0.75 to 1.65 points, while APs improves by 1.95 to 3.81 points. The improvements on TinyPerson and VisDrone further suggest that the framework can generalize across different data distributions without target-domain fine-tuning. Beyond the quantitative results, the authors provide ablation studies and additional analyses relating trajectory evidence to ground-truth support. These experiments offer preliminary evidence that intermediate decoder states contain useful information for assessing detection reliability. The consistency of the improvements across diverse detector architectures, together with the training-free setting, supports the practical relevance of the proposed approach.

Critical weaknesses
  1. Although the overall improvements are encouraging, the ablation results suggest that most of the performance gains originate from counterfactual scaling rather than the proposed trajectory-based reliability interpretation. For instance, Table 1 shows that counterfactual scaling alone improves RT-DETR-R50 from 53.09 to 54.18 AP on COCO, whereas the complete CQTR framework achieves 54.21 AP. Similarly, the additional improvements beyond scale-only inference are only 0.05 AP on TinyPerson and 0.10 AP on VisDrone. These results raise questions about the incremental contribution of trajectory recalibration and reliability routing.

  2. The central hypothesis is that counterfactual scale interventions activate latent small-object knowledge already encoded in frozen detectors. However, the observed improvements under higher-resolution inference do not necessarily establish this interpretation, since they may also result from improved spatial resolution and feature preservation. Similarly, although Figure 7 demonstrates a positive correlation between trajectory evidence and ground-truth support, it remains unclear whether trajectory-based reliability offers substantial information beyond final prediction confidence or other straightforward uncertainty measures. Additional controlled analyses would make the mechanistic interpretation more convincing. Moreover, CQTR requires additional forward inference at a counterfactual scale and access to intermediate decoder predictions. The paper does not sufficiently quantify the resulting computational overhead in terms of latency, memory consumption, and throughput.

Questions for authors
  1. Table 1 indicates that most of the performance improvement comes from counterfactual scaling, while the additional gains from trajectory recalibration and routing are relatively small. Could the authors further clarify the distinctive contribution of the reliability interpretation components and compare them with simpler inference-time score-calibration methods?

  2. How does CQTR compare with conventional high-resolution inference or multiscale testing under matched computational budgets? Such comparisons would help establish whether the proposed approach offers advantages beyond increasing input resolution.

  3. How sensitive is the unlabeled routing mechanism to the calibration subset size, random seed, and routing thresholds? Additionally, how often does the selected route match the better-performing correction branch across all 27 model-dataset combinations?

  4. Could the authors provide inference latency, FPS, and GPU memory comparisons among native inference, counterfactual scale-only inference, and complete CQTR? These measurements would help clarify the efficiency trade-offs of the proposed framework.

4 comments
AuthorsOpenReview ↗

Response to Question 1 and Weakness 1

We thank the reviewer for highlighting the distinction between the gains from counterfactual scaling and those from reliability correction. We agree that scaling accounts for most of the improvement. On RT-DETR-R50, the selected correction adds 0.03, 0.05, and 0.10 AP over scale-only inference on COCO, TinyPerson, and VisDrone, respectively. We have revised the abstract, introduction, contributions, and conclusion to distinguish the main gains from scaling from the modest additional benefits of reliability correction. To examine whether trajectory evidence provides information beyond final confidence, we added two complementary analyses. First, we compared a statistical model using final confidence, predicted box area, class, and local crowding with an otherwise identical model that additionally includes trajectory evidence. The analysis covers 273920 candidates on COCO, 84825 on TinyPerson, and 111278 on VisDrone, using image-grouped five-fold cross-validation and 1,000 image-level bootstrap replicates. On COCO, adding trajectory evidence increases AUROC from 0.943698 to 0.944389, with a paired gain of 0.000691 (95% CI: [0.000278, 0.001045]). The corresponding gain on TinyPerson is 0.000187 [0.000142, 0.000243]. Complete results and protocols, including the VisDrone estimates, are reported in Appendix A.4. These results support small incremental predictive information beyond the examined variables. We also clarified the distinction between overlap support and detection correctness. Figure 7 measures same-class ground-truth overlap, which permits multiple candidates to receive support from the same object. We have corrected the corresponding text and caption accordingly. To assess correctness under a stricter criterion, we additionally performed score-ordered, one-to-one, same-class matching at IoU ≥ 0.5 on all 5000 COCO val2017 images. Among 273920 eligible counterfactual candidates with predicted area ≤32^2 square pixels and original confidence ≥ 0.05, 10523 receive a one-to-one match. Duplicate predictions are counted as false positives. Across trajectory-evidence quintiles, matched-positive rates increase monotonically from 0.58% to 12.32%. The controlled COCO analysis above uses these one-to-one labels. Full matching details are provided in Appendix A.5. Second, among the 10523 matched predictions, mean IoU increases monotonically from 0.692 to 0.843 across trajectory-evidence quintiles, while the proportion achieving IoU ≥ 0.75 rises from 34.49% to 84.27%. After controlling for final confidence, predicted box area, class, and local crowding, the partial rank correlation remains positive at 0.158 (95% CI: [0.137, 0.179], estimated using 1000 image-cluster bootstrap replicates). This analysis, added in Section 4.5, supports trajectory evidence as an additional localization-quality indicator among matched small-object predictions. The current correction changes confidence scores rather than box coordinates, and its realized AP benefit is modest. We acknowledge this remaining limitation. Throughout the revised manuscript and figure captions, we now distinguish observed scale-dependent evidence, diagnostic reliability information, and actual detection gains, without claiming a causal activation mechanism.

AuthorsOpenReview ↗

Response to Question 2 and the mechanistic concerns in Weakness 2

We thank the reviewer for suggesting comparisons with conventional high-resolution and multiscale inference under matched computational budgets. We have added the appendix subsection “Comparison with Latency-Matched High-Resolution and Multiscale Inference,” which reports the complete protocol and results using frozen RT-DETR-R50 on all 5,000 COCO val2017 images. Both control configurations were selected solely by latency on unlabeled COCO training images, without using validation accuracy. The single-pass control uses a 1568×1568 input. Conventional two-scale testing combines 640×640 and 1344×1344 predictions using their original confidence scores and class-aware NMS at 0.8, retaining at most 300 candidates. Neither control uses trajectory recalibration or conflict suppression. All methods share the same checkpoint, evaluator, and candidate budget. All timing measurements were obtained in the same randomized interleaved run on an NVIDIA GeForce RTX 3060 Laptop GPU with batch size one, using 30 training images and three repetitions per image after warm-up. Timing includes preprocessing, forward inference, decoding, and method-specific postprocessing, but excludes disk access, evaluation, and one-time routing calibration. The single-pass control achieves 39.58 AP and 30.83 APₛ at 253.58 ms/image, compared with 54.21 AP and 38.55 APₛ at 249.81 ms/image for CQTR. Conventional two-scale testing provides a stronger comparison, achieving 54.15 AP and 37.76 APₛ at 257.82 ms/image. CQTR therefore improves over this control by 0.06 AP and 0.79 APₛ, while the control is approximately 3.2% slower. Peak allocated GPU memory is also lower for CQTR: 402.2 MiB versus 802.3 MiB for two-scale testing. We explicitly qualify these findings in the appendix. The controls are approximately latency-matched rather than FLOPs-matched or accuracy-optimized. The single-pass degradation may reflect sensitivity to excessive enlargement, and the multiscale result concerns the evaluated scale pair rather than all possible configurations. Because the resolutions differ, these comparisons do not isolate the contribution of trajectory correction. Our existing ablation remains the evidence for that contribution: scaling accounts for most of the improvement, while reliability correction provides modest additional gains.

AuthorsOpenReview ↗

Response to Question 3

We thank the reviewer for requesting a broader evaluation of routing sensitivity and selection accuracy. We have added an appendix subsection, “Sensitivity and Selection Accuracy of Unlabeled Routing,” covering all 27 model–dataset combinations. For sensitivity analysis, we vary the calibration size over Min{25,50,100,200}, use five random seeds, and independently perturb each routing threshold by −10%, 0%, and +10%. This produces 180 configurations per combination and 4,860 configurations in total. For each seed, smaller calibration subsets are nested within the 200-image subset. All configurations use unlabeled training images, with detector parameters and correction rules fixed. Across these configurations, 4444 of 4860 decisions (91.44%) agree with the default route obtained using 100 images, seed 31415, and the original thresholds. This measures stability relative to the default decision, rather than agreement with the better-performing branch. To evaluate selection accuracy, we separately assess trajectory recalibration and conflict suppression on each complete evaluation split. The default router selects the higher-AP branch in 19 of 27 combinations (70.37%). We additionally report AP regret, defined as the AP difference between the better of the two branches and the branch selected by the router. Mean regret is 0.0342 AP points, and maximum regret is 0.2897 points. The largest discrepancy occurs for DAB-DETR on COCO, where the selected conflict branch achieves 37.9431 AP, compared with 38.2328 AP for the trajectory branch. Evaluation annotations are used exclusively for this retrospective comparison and do not influence calibration or route selection. These results indicate that routing is usually stable under the tested changes in calibration size, seed, and thresholds, while incurring a small average AP loss relative to the better branch. However, it does not consistently identify the optimal branch. We have therefore revised the discussion to distinguish routing stability from selection accuracy and to describe the router as a heuristic supported by the evaluated settings, rather than a guarantee of optimal branch selection. The complete protocol, aggregate results, and a representative selection failure are provided in the added appendix “Sensitivity and Selection Accuracy of Unlabeled Routing” subsection.

AuthorsOpenReview ↗

Response to Question 4 and the efficiency concerns in Weakness 2

We thank the reviewer for requesting explicit efficiency measurements. We have added an appendix subsection, “Inference Efficiency and Computational Cost,” comparing native inference, counterfactual scale-only inference, and full CQTR. We benchmark frozen RT-DETR-R50 on an NVIDIA GeForce RTX 3060 Laptop GPU using FP32 precision and batch size 1. For each dataset, we use 100 fixed evaluation images, perform 10 warm-up iterations per configuration, and measure each image three times with CUDA synchronization. Timing includes preprocessing, host-to-device transfer, forward passes, and postprocessing, but excludes disk loading and CPU prediction export. We report peak PyTorch-allocated GPU memory. On COCO, native inference, scale-only inference, and full CQTR require 62.58, 150.61, and 234.43 ms per image, corresponding to 15.98, 6.64, and 4.27 FPS. Their peak allocated memory is 0.315, 0.393, and 0.393 GiB, respectively. Across the three datasets, full CQTR adds 37.9%–55.7% latency over scale-only inference, while increasing peak allocated memory only slightly. One-time calibration using 100 unlabeled training images takes 27.45–27.66 seconds, including image loading, and is excluded from per-image latency. Complete results and measurement details are provided in the added appendix subsection. These measurements show that the current implementation incurs substantial runtime overhead. We have explicitly acknowledged this accuracy–latency trade-off, particularly given the modest AP gains over scale-only inference, and clarified that training-free operation does not imply low inference cost.

Reviewer_UCESOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper introduced CQTR which is a training-free framework for improving small-object detection with frozen detectors.

Critical strengths

The CQTR method retains the detector’s parameters and uses its correction process based on a tiny subset that is not labeled. It could be useful when there are already some pre-trained detectors, yet lack annotated targets or means for their re-training.

Critical weaknesses

Please check Questions For Authors

Questions for authors

Scaling increases COCO AP from 53.09 to 54.18 on RT-DETR-R50 with scale-only inference, while full CQTR achieves 54.21. Therefore, scaling provides for about 95-99% of total AP gain, while other components account only for 0.03-0.10 AP. Also, VisDrone APs drops from 7.88 on scale-only inference to 7.85 on full CQTR. Thus, the importance stressed in the title is not sufficiently justified.

In Section 3.3, four decoder layers and three box transitions are needed. However, both the D-FINE-S and the D-FINE-S backbone configuration in DEIM implementations have only three decoder layers. Does the approach employ an encoder prediction or a prediction before the decoder as an additional state? Is the trajectory window shortened and normalization factors adjusted?

In Section 4, a common S0=640 is specified for all nine detectors. It is different from the standard validation preprocessing in the original DETR implementation that resizes the shorter side to 800 pixels with the maximal size of 1333.

Higher resolution inference does not verify the proposed mechanism of “latent scale knowledge activation.” What is the observable difference between “latent knowledge activation” and scale sensitivity?

Figure 7 demonstrates the relationship between trajectory evidence and ground-truth support, but no control is taken into account over final confidence, predicted object size, class, or crowd level.

Also, “ground-truth support” means only overlapping with some same-class object, rather than detection-ground-truth matching. Visual evidence is not sufficient either.

Cross-domain evaluation lacks important label-mapping and annotation handling details.

9 comments
AuthorsOpenReview ↗

Response to Comment 1

We thank the reviewer for this valuable observation. We agree that counterfactual scaling accounts for most of the AP improvement, whereas the subsequent reliability corrections provide only modest additional gains. To clarify the role of query-trajectory analysis, we conducted an additional localization-quality study using frozen RT-DETR-R50 on all 5000 images of COCO val2017. We analyzed 10523 small-object predictions obtained through score-ordered, one-to-one, same-class matching at IoU ≥ 0.5. From the lowest to the highest trajectory-evidence quintile, mean IoU increases monotonically from 0.692 to 0.843, while the proportion of matched predictions achieving IoU ≥ 0.75 rises from 34.49% to 84.27%. After controlling for final confidence, predicted box area, class, and local crowd level, the partial rank correlation remains positive at 0.158, with a 95% confidence interval of [0.137, 0.179] estimated using 1000 image-cluster bootstrap replicates. These results support trajectory evidence as an additional indicator of localization quality among matched small-object predictions. However, this association does not establish that trajectory recalibration improves box localization. The current recalibration rule adjusts candidate confidence without refining box coordinates, which limits how this diagnostic information can affect detection performance. We acknowledge that its diagnostic value has translated into only modest AP gains under the current rule. We have added this analysis in Section 4.5 and revised the abstract, introduction, contribution statements, and conclusion to distinguish the main gains from counterfactual scaling from the modest additional benefits of reliability correction. We now describe trajectory evidence as a complementary diagnostic signal with limited incremental predictive value, rather than as the primary source of the detection improvements.

AuthorsOpenReview ↗

Response to Comment 2

Thank you for identifying this ambiguity. D-FINE-S and DEIM-D-FINE-S indeed have three decoder layers. Our implementation already adapts the trajectory window to the available decoder depth: for a detector with L decoder layers, it uses the last K=min(4, L) decoder states and the corresponding K-1 box transitions. Thus, these two models use three layer-wise class-response observations and two box transitions. Neither encoder predictions nor pre-decoder predictions are included. Both quantities are aggregated using geometric means over the actual observations, with normalization factors of 1/K for semantic persistence and 1/(K-1) for spatial convergence. We have revised the title and description of Section 3.3, generalized Eqs. (2)–(3), and clarified the three-layer cases in the implementation details and Fig. 2. These revisions align the manuscript with the existing implementation and do not change the reported experimental results.

AuthorsOpenReview ↗

Response to Comment 3

Thank you for highlighting this ambiguity. Resizing the shorter side to 800 pixels while limiting the longer side to 1333 pixels corresponds to the original DETR evaluation protocol, whereas RT-DETR uses a fixed 640X640 input. Nevertheless, your concern about preprocessing fairness is valid for our DETR experiments. The original manuscript did not clearly distinguish our shared scale setting from each detector’s official evaluation protocol. To address this concern, we additionally evaluated DETR-R50 and DETR-R50 + CQTR on all 5000 COCO val2017 images using DETR’s official native preprocessing. We directly use the original repository’s validation transform, which preserves the aspect ratio, targets a shorter side of 800 pixels, and limits the longer side to 1333 pixels. Both methods use the same pretrained checkpoint and COCO evaluator. Under the official preprocessing, CQTR improves AP by 0.78 points and APₛ by 0.55 points. These results demonstrate that CQTR still improves DETR-R50 without reducing the baseline’s native evaluation resolution. We have added this supplementary experiment and the corresponding comparison table in Section 4.6.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary for the Area Chair

Dear Area Chair,

Thank you for overseeing the review of our submission. We summarize the evidence added during rebuttal and clarify the contribution that we respectfully ask you to consider.

1.Contribution and scope. CQTR studies whether small objects recovered through larger-scale inference already exhibit observable evidence in frozen detectors, and whether decoder trajectories provide reliability information beyond final confidence. Across nine detectors and three datasets, the complete framework consistently improves AP and small-object AP without parameter updates. We agree with the reviewers that scaling accounts for most of these gains. Our revised claims distinguish this performance improvement from the complementary diagnostic contribution of trajectory analysis.

2.Additional evidence. We added the following analyses in response to the reviews: Native-scale evidence for recovered objects. On all 5,000 COCO validation images, 857 of 966 small objects recovered at confidence threshold 0.30 already exhibit qualifying intermediate-layer or low-confidence final predictions at the native scale. This supports observable existing evidence, without establishing a causal activation mechanism. Reliability beyond final confidence. Using one-to-one matching, image-grouped cross-validation, and image-level bootstrap analysis, trajectory evidence provides small positive incremental predictive information after controlling for confidence, box area, class, and crowding across all three datasets. Among 10,523 matched COCO predictions, its partial rank correlation with localization quality is 0.158, with a 95% confidence interval of [0.137, 0.179]. Evaluation and routing checks. We added validation under official DETR preprocessing, clarified the shared-label cross-domain protocols, and tested 4,860 routing configurations across all 27 model–dataset combinations. Routing consistency is 91.44%, while selection of the higher-AP branch is 70.37%, with mean AP regret of 0.0342 points. We explicitly distinguish stability from optimal selection.

3.Request for assessment. We respectfully ask that the paper be assessed for its combined empirical contribution: a broad evaluation of frozen-detector scale interventions and controlled evidence about the diagnostic information in decoder trajectories. The remaining disagreement concerns whether this contribution is sufficient given the limited effectiveness of the current correction. We acknowledge that limitation and hope the additional evidence enables an informed assessment of the revised paper.

Thank you for your time and consideration.

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