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Under review as a conference paper at ICLR 2027

Where Will It Fail? Detector-Native Concept Blindspots for Forecasting Errors

Abstract

Object detection underpins numerous safety-critical applications such as autonomous driving and embodied AI, yet even the best detectors still make perception errors that pose serious risks. Understanding detector failure modes is therefore important for diagnosing model vulnerabilities, assessing risk, and guiding improvements. A detector’s intrinsic concepts may play a fundamental and general role in determining its errors, but explicitly extracting and quantifying such concept-level vulnerabilities remains challenging. We introduce a framework to discover, validate, and leverage detector-native concept blindspots for failure diagnosis and risk screening. We develop DetSAE, our task-relevant sparse autoencoder, to extract sparse concepts from a fixed detector's object-level representations while preserving its classification and localization behavior. We then generate 20 style-transferred versions of the original dataset and track objects to identify blindspots associated with statistically supported excess detection degradation. Experiments demonstrate that suppressing excessive blindspot activations improves frozen-head classification across detector backbones, providing causal evidence of their contribution to errors. Using the same frozen blindspot representation, our separate false-negative and false-positive risk predictors achieve the best performance among compared methods across diverse benchmarks. These results show that seemingly isolated detection failures can share concept-level weaknesses that support both model interpretation and actionable risk assessment. Our code and generated datasets are publicly available on GitHub.

Primary area:
interpretability and explainable AI
Keywords:
Object Detection, Concept Blindspots, Sparse Autoencoders, Causal Intervention, Failure Prediction

Reviews

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1234this paper, Bottom 27%
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.
Reviewer_ohmpOpenReview ↗
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Paper summary

This paper proposes a framework for identifying detector-native concept blindspots using DetSAE and analyzing detection degradation across 20 style-transformed images through regression analysis to identify concept clusters associated with systematic detection failures. The identified blindspots are evaluated through activation restoration experiments and incorporated into separately trained FN/FP risk predictors. Experiments across multiple driving benchmarks report improved FN/FP risk prediction performance, while the intervention results demonstrate classification-level improvements rather than reductions in actual detection errors. However, the lack of controlled studies isolating potentially critical factors (e.g., style-transfer artifacts, SAE representation learning, and supervised predictor training) raises concerns about the validity and distinct contribution of the identified blindspots, and it remains unclear whether the reported improvements have any direct implications for reducing actual FN/FP errors or improving detection mAP.

Critical strengths
  1. Extensive Evaluation. The paper demonstrates consistent FN/FP risk prediction improvements across multiple benchmarks and domain shifts.

  2. Task-Aware Concept Extraction. DetSAE preserves detection-related information, while intervention experiments provide additional evidence of the relevance of the extracted features.

Critical weaknesses
  1. Insufficient Blindspot Validation. The paper does not sufficiently establish that the identified blindspots represent meaningful detector-native concepts, as it remains unclear what visual patterns these concepts capture and whether the observed detection failures are actually caused by them. Moreover, detection degradation under style transformations may be influenced by proposal localization shifts, RoI feature misalignment, or geometric artifacts, which are not adequately isolated through controlled experiments. Although the authors show that restoring blindspot activations to their original-image values improves classification accuracy, they do not demonstrate corresponding improvements in actual FN/FP errors or mAP. These limitations weaken the central claim that the identified blindspots explain systematic detection failures.

  2. Unclear Blindspot Contributions. The paper attributes FN/FP risk prediction performance to the proposed blindspot mechanism, but several methodological choices and experimental results leave its specific contribution insufficiently validated. For example, Table 5 shows that explicitly adding blindspot channels to all SAE-derived concepts yields only marginal gains in FN risk ranking performance. Since the all-concept representation already includes the identified blindspots, the benefit of explicitly emphasizing them remains unclear. Moreover, although the blindspot-only ablation outperforms randomly selected normal concepts, it is unclear whether the proposed blindspot identification procedure offers advantages over simpler feature selection methods. The use of a separately trained predictor further complicates this assessment, as its performance may reflect supervised learning from FN/FP error labels rather than the ability of the identified blindspots themselves to indicate detection failures. These limitations make it difficult to determine the specific contribution of the proposed blindspot mechanism to the reported results.

Questions for authors
  1. Specify the exact clustering procedure, including the similarity measures, merging criteria, and justification for the selected thresholds. Discuss the sensitivity of the identified blindspots to these design choices. More importantly, since the framework relies on both a learned DetSAE representation and a separately trained risk predictor, the reported gains could also be attributed to additional representation learning and supervised prediction rather than the discovery of blindspots. Address this alternative explanation and explain what distinguishes the proposed mechanism from simpler feature decomposition methods, such as PCA/SVD, followed by a trained predictor.

  2. Explain how the proposed method distinguishes detection degradation associated with blindspots from changes in proposal localization, RoI feature alignment, or geometric distortions introduced by style transfer. Since detection quality depends on both confidence and IoU, changes in bounding box predictions alone could affect blindspot identification. Specify how object layouts and annotations were verified across the 20 generated styles, and discuss whether these factors could influence the identified blindspots.

  3. The intervention experiments demonstrate improvements in frozen-head classification, but their relationship to actual FN/FP errors remains insufficiently established. Explain how these classification-level results support the claimed role of blindspots in detection failures, particularly false positives arising from background regions. Discuss whether the observed effects extend to final detection outputs, including FN/FP errors and mAP, rather than only classification accuracy.

  4. Distinguish the contribution of blindspot identification from that of general SAE representations and supervised predictor training. Table 5 shows that explicitly adding blindspot channels provides relatively small gains over using all concepts, although the blindspot-only representation outperforms randomly selected normal concepts. Explain whether the identified blindspots can directly indicate detection risks without a separately trained predictor. Also, discuss the effect of additional style-transformed training data in Ours (MS), given that competing trainable baselines do not use equivalent augmentation.

  5. Discuss the generalizability of the proposed framework beyond the evaluated Faster R-CNN architecture. Although the experiments cover multiple datasets and two CNN backbones, they primarily consider Car and Person detection within the same detector family. Explain how the proposed concept extraction and blindspot identification procedures would apply to different architectures, such as YOLO or DETR, and whether the framework depends on characteristics specific to RoI-based detectors.

6 comments
AuthorsOpenReview ↗

Response to Reviewer ohmp

Thank you for your review. References use the revised paper; quotes are excerpts.

Clustering and PCA (Q1)

Specify the exact clustering procedure

simpler feature decomposition methods, such as PCA/SVD

We report exact clustering, sensitivity tests and PCA predictors.

Similarity weights active-set/top-50/dictionary/prototype agreement 0.30/0.20/0.20/0.30. Complete linkage uses 1−s≤0.701-s\leq0.70; identity thresholds are 0.05 share and 0.50 mass. Merge thresholds 0.25/0.30/0.35 yield 12/17/19 blindspots from 158 atoms (Sec. 3.1; App. A.1/B.1).

PCA directions use variance or source-error association. At 84 inputs (16 outputs + 17 directions × four statistics), blindspots / the two PCA choices give FN AUROC 78.13/64.03/64.75 on RealDriveSim and 54.38/50.60/51.71 on SIM10K. Four differences pass Holm correction over 96 tests. Full PCA leads all concepts on 5/6 FN AUROC estimates at 420 inputs (App. D.4, Tables 20–23).

Geometry and difficulty (Q2)

geometric distortions introduced by style transfer.

The effects remain with proposals and box regression fixed.

Styles were checked for object count, shape, position and annotations; original concept identities are retained. Regression controls original quality, geometry, other concepts and class/style difficulty.

We also control original probability, margin, entropy, their squares and quality squared:

DetectorClusterExtra degradation95% CIJoint BH-FDR
R101C3-F030.0781[0.0646, 0.0921]0.0104
R101C3-F120.0808[0.0631, 0.0997]0.0348
R50C3-F280.0932[0.0724, 0.1133]0.0104

Three pass added controls under joint BH (209 clusters, 20,000 scene resamples); 17/16 use original controls. Head outputs can overlap concept information (App. B.1).

Final detection effects (Q3)

final detection outputs, including FN/FP errors and mAP

We diagnose and predict failures; restoring selected blindspot activations reduces misses and improves AP.

Diagnosis complements detector improvement by locating likely errors in unlabeled data. Here detector training is unchanged, with weights, proposals and box regression fixed. We compare with the frozen baseline and equal-norm controls, not retraining gains under different constraints. Table 3 (Sec. 4.6): 500 scenes × six non-generative changes, GT/paired originals, decoding/NMS.

DirectionAP50AP50:95Δ[email protected]Δ[email protected]
Frozen detector49.12126.13100
Opposite49.04026.093+23+11
Normal concept49.14726.137−50
Random49.12526.132−2+1
Other object49.46326.239−124+14
Blindspot restoration49.47926.245−134+13
Source-selected PCA49.55126.239−232+37
Class gradient (0.25)49.62126.260−269+33

AP50/AP50:95 gains (95% CI): 0.3578 [0.2878, 0.4243] / 0.1148 [0.0920, 0.1353] points. Both pass correction over 110 tests with 5,000 paired scene resamples. Direct intervention touches 5.50% of baseline misses, counted per view (App. C.1).

Direct indication and prediction (Q4)

without a separately trained predictor.

Yes, blindspot identities indicate FN without training a risk predictor.

Match same-image/class GT objects by size/position, independently of outcomes/confidence; threshold 0.5.

DomainPairs / imagesBlindspot-only retained%Blindspot-only FN%Normal-only FN%Difference [95% CI]
BDD100K386 / 31814.8477.9837.31+40.67 [34.63, 46.77]
KITTI157 / 15519.3858.607.01+51.59 [43.04, 60.00]
RealDriveSim931 / 7578.5088.1835.55+52.63 [48.88, 56.30]
SIM10K532 / 5034.6476.6920.49+56.20 [47.24, 64.47]

All four pass correction over 30 tests. Retained% is matched/eligible blindspot-only objects (App. B.3).

We retrain the 472-input model after linear transforms learned from source data remove blindspot activation information, copies included. Controls target matched normals or normals selected by source errors: 68 directions each. Five random controls match input-change magnitude.

FN AUROC (%); removal columns name the information targeted:

DomainFullBlindspotsNormalsError-selected normalsFull minus blindspots [95% CI]
KITTI75.30663.96568.94866.855+11.341 [10.194, 12.483]
RealDriveSim82.85975.04981.99476.986+7.810 [6.192, 9.436]

Both losses pass Holm correction over 576 tests. Losses exceed all controls on KITTI, but only normals on RealDriveSim. No C@5 loss passes (Sec. 5.4, Table 5; App. D.1). The 420-input control fixes 16 outputs (D.2, Table 17); shared-style training is in A.3, Tables 7–10.

Other architectures (Q5)

beyond the evaluated Faster R-CNN architecture.

Other detector architectures need further study.

Direct transfer of our method to YOLOv8x yielded no clusters meeting the existing blindspot criteria (App. B.1). Discovery must account for detector architecture; extensions require further study.

We hope this addresses your concerns.

Dear Reviewers,

The authors have addressed your comments in their rebuttal. Please review their responses and provide any further feedback or follow-up questions, if any. Thank you!

Best, AC

Q1. Classic ML alternatives such as PCA match or exceed the proposed approach. This supports the research direction of this work but weakens the motivation for DetSAE-based blindspots. The manuscript should justify in what respect the proposed approach is superior.

Q2. The criteria for verifying layouts and annotations are not specified. The validation thus lacks a grounded basis, which limits the proposed approach's technical soundness.

Q5. The manuscript's experiments can't distinguish whether the achievements stem from the proposed approach's effectiveness or good compatibility with a particular detector family.

Reviewer_TBw9OpenReview ↗
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Paper summary

This paper presents a framework for diagnosing object detection failures through detector-native concept blindspots. The paper proposes DetSAE, a sparse autoencoder that extracts object-level concepts while preserving the frozen detector’s classification and localization behavior. Using 20 paired style-transferred views, the framework identifies concept clusters associated with statistically significant excess detection degradation. Controlled activation interventions provide evidence that these blindspots contribute to frozen-head classification errors. Experiments across six driving benchmarks demonstrate consistent improvements in false-positive screening and generally competitive false-negative prediction.

Critical strengths
  1. Strong FP risk-screening performance. Both OG and MS outperform all external baselines in the reported FP dataset–metric comparisons, showing consistent improvements.
Critical weaknesses

1.The contribution of the blindspot-aware representation is not sufficiently separated from the benefits of synthetic data. The method uses 20 generated style variants per reference image, introducing a potential data advantage over baselines trained only on original images. MS additionally uses these variants for risk-predictor training, while both OG and MS rely on them for blindspot discovery.

2.The semantic interpretation of the learned “concepts” remains weakly supported. The paper provides limited evidence that the discovered clusters correspond to visual concepts. Since blindspot discovery relies on generated style variants, it is also unclear how generation fidelity and the choice of style prompts affect the identified blindspots and downstream performance.

Questions for authors

1.Do the performance gains remain when the baselines are trained with the same synthetic style variants?

2.How sensitive the results are to generation quality and style prompts?

2 comments
AuthorsOpenReview ↗

Response to Reviewer TBw9

Thank you for the careful review. References use the revised paper; quotes are excerpts.

Shared style data (Q1)

Do the performance gains remain when the baselines are trained with the same synthetic style variants?

The FP lead over the eleven external methods remains when trainable methods receive the same style data and training budget.

We retrained the trainable external methods on the same 62,463 source original and style images used by Ours (MS): 20K updates per candidate, effective batch 64, three training seeds, identical learning-rate opportunities, and original-source checkpoint selection. Reference-bank and statistical-fitting methods use the same pool.

Output-only is a supervised MLP predicting image-level FN/FP risk from 16 statistics of detector box counts and confidence scores, without concept or blindspot inputs. Its hidden layers and training settings match ours.

Table 4 summarizes FN AUROC and C@5; Appendix A.3, Tables 7–10 retain all FN/FP metrics and the output-only control. Full MS leads the eleven external methods on 24/24 FP and 7/24 FN point estimates. The output-only control is stronger on FP (Section 5.3).

Section 5.4, Table 5 uses linear transforms learned from source data to remove information about blindspot activations, then retrains the original predictor. FN AUROC falls by 11.34/7.81 points on KITTI/RealDriveSim, supported after Holm correction across 576 comparisons. Section 4.4 additionally tests external-object difficulty without a risk MLP.

Visual meaning and styles (Q2)

The semantic interpretation of the learned “concepts” remains weakly supported.

How sensitive the results are to generation quality and style prompts?

Visual examples show shared patterns, and discovery includes controls against any single style dominating the result.

First, what do the blindspots look like? For each of the 17 frozen blindspots, we collected sampled high-activation objects and compared them with class-matched random objects. Fifteen sets showed clearer shared properties, including reflective highlights, similar vehicle body shapes, occlusion, exposed rooflines, and boundary truncation. Figure 4 shows six clusters with five examples each; complete descriptions, example identifiers, and visualization code will accompany the GitHub materials.

For two of the 17 clusters, we could not identify clear shared visual properties in these samples. Their labels follow the same detector-based excess-degradation criterion as the other clusters.

Checks on generated images and individual styles. This is an important question. We manually checked each style image against its original for object count, shape, position, and annotation consistency. Discovery uses all 20 paired styles, removes the mean degradation for each class/style, and requires every accepted blindspot's estimated extra degradation to remain above 0.05 when any single style is omitted (Section 3.2). These checks reduce the risk of one generated style determining the result. Additional checks omitting groups of styles are reported in Appendix B.1.

Finally, does the evidence extend beyond generated images? On four external datasets, within-image matched cars still have FN gaps of 40.7–56.2 points without a risk MLP (Section 4.4). The final-detection intervention in Section 4.6 also uses six non-generative appearance changes. Thus the observed detection association and activation effects are not confined to generated images.

We hope this addresses your concerns.

Dear Reviewers,

The authors have addressed your comments in their rebuttal. Please review their responses and provide any further feedback or follow-up questions, if any. Thank you!

Best, AC

Reviewer_6w5eOpenReview ↗
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2(+1)
Confidence
3
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2
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2
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Paper summary

The paper works on predicting where an object detector fails based on its internal representations. It uses SAEs to get concept clusters, uses generated styles to identify concept clusters which could degrade the performance of the detector. The identified blindspot concepts along with all the concepts and prediction confidence form the input for the risk predictor which predicts detector failure rates. The method is evaluated w.r.t to its risk prediction with comparison to baselines, and blindspot identification through interventions.

Critical strengths

The idea to use concepts obtained through SAEs along with identifying problematic concepts by differences induced by style to predict the failure rates of object detector is interesting.

Critical weaknesses

1)Experiments and evaluations are not thorough and does not fully support the claims made:

a)The usefulness of blindspots in predicting the risk is modest as can be seen in table 5. Additionally, FP ablation is missing. These issues make the contribution of blindspots in risk prediction not well supported.

b) FN performance with OG which doesn't use extra training samples doesn't show improvement over the strongest baselines in most cases. In my understanding the number of training samples used by the baselines is not mentioned while MS uses 20 more samples for every image compared to OG. MS uses 21 times more data than baselines than it would be an unfair comparison.

c) The details on intervention controls are not clear. As suggested in line 232 if the magnitudes are matched to suppressed concepts instead of restoring then it is unfair comparison of baselines with effects of blindspots getting inflated.

d) With no ablation it is unclear about the contribution of detector confidence compared to the concepts (all or blindspots).

e)Uncertainty is missing in the paper results.

2)The paper claims DetSAE as one of the main contributions but task relevant SAEs have been used in prior work [1] (which the paper cites), while this paper adapts it to object detection, the utility of new objective term (localization) added is not established.

[1]Braun, Dan, et al. "Identifying functionally important features with end-to-end sparse dictionary learning." Advances in Neural Information Processing Systems 37 (2024): 107286-107325.

Questions for authors

1)Can you show ablation results (Table 5) with FP?

2)What visual properties or semantic features do the identified blindspot concepts represent? Are there any patterns among blindspot concepts?

5 comments
AuthorsOpenReview ↗

Response to Reviewer 6w5e

Thank you for your review. References use the revised paper; quotes are excerpts.

Blindspot value (1a; Q1)

The usefulness of blindspots in predicting the risk is modest

FP ablation is missing.

Blindspot information contributes to FN prediction, and the FP ablation is complete.

FP (%); random normals average five trained 15 Car/2 Person sets.

DomainFP inputC@5AUROCAUPRCNAURC
BDD100KRandom normal concepts9.6587.5698.8537.54
BDD100KBlindspots only9.8088.4198.9437.17
BDD100KAll concepts10.9989.5599.1134.21
BDD100KAll+blindspots10.9289.6499.1334.14
KITTIRandom normal concepts8.9887.8997.7030.98
KITTIBlindspots only8.9789.1698.0429.83
KITTIAll concepts10.3191.0898.3822.65
KITTIAll+blindspots10.1890.9698.3523.49

All concepts include blindspots; extra channels give mixed BDD100K changes and worsen all KITTI FP metrics (App. D.3, Table 18). FP performance is attributed to the complete predictor.

For FN, we learn linear transforms from source data to remove blindspot activation information, including copies, then retrain the original 472-input model. Controls target matched normals or normals selected by source errors. All remove 68 directions; five random controls also match input-change magnitude. A separate control keeps 16 output statistics fixed (App. D.2, Table 17).

FN AUROC (%); removal columns name the information targeted:

DomainFullBlindspotsNormalsError-selected normalsFull minus blindspots [95% CI]
KITTI75.30663.96568.94866.855+11.341 [10.194, 12.483]
RealDriveSim82.85975.04981.99476.986+7.810 [6.192, 9.436]

Both losses pass Holm correction over 576 tests. On KITTI, blindspot removal hurts more than normal/error-selected/random removal by 4.983/2.891/2.510 AUROC points (adjusted p=0.0288/0.0457/0.0288). RealDriveSim supports the normal comparison (+6.946, p=0.0288), not the other controls. Full leads all six AUROC estimates, significant on these two; no C@5 loss is significant (Sec. 5.4, Table 5; App. D.1).

Shared data (1b)

MS uses 21 times more data than baselines

We reran comparisons with identical source images and updates.

MS methods share 62,463 Cityscapes original/style views; trainable ones use 20K updates, batch 64, three seeds, three learning rates, and source-only selection. Ours leads eleven external methods on 7/24 FN point estimates (Table 4; App. A.3).

Intervention norm (1c)

matched to suppressed concepts instead of restoring

Controls match the RoI change from restoring activations, not deleting them.

We set selected activations to their paired-original values and scale control directions to the same L2 change in raw RoI space. Residuals and other activations stay fixed. If normal concepts produce no change, we use random directions (5,843/7,542 events). Where normal updates are nonzero, restoration still leads by AP50 +0.1403 [0.0996, 0.1944], Holm p=0.006 over 12 tests (Sec. 3.3; App. C.1).

Output-only control (1d)

contribution of detector confidence compared to the concepts

Full MS leads FN AUROC on five domains; output-only leads FP.

Output-only trains an MLP on 16 box-count and confidence statistics to predict image-level FN/FP risk, without concepts or blindspots. Hidden layers and training settings match ours. Cells: ours / output-only, AUROC (%); details: App. A.3, Table 10.

DomainFN AUROCFP AUROC
BDD100K64.79 / 67.8889.64 / 95.65
KITTI75.31 / 74.5590.96 / 93.69
RealDriveSim82.86 / 66.1090.50 / 93.61
SIM10K60.09 / 52.5786.60 / 90.70
Rainy85.92 / 61.2073.57 / 76.23
Foggy69.20 / 53.2282.29 / 87.82

Output-only leads 24/24 FP estimates (19 pass correction over 48 tests); Full MS leads 18/24 FN estimates, including C@5 on three domains. Input/parameter counts differ (App. A.2).

Uncertainty (1e)

Uncertainty is missing in the paper results.

Confidence intervals and training-seed variation are reported separately.

Screening intervals: App. A.2, Table 6; other tests use paired resampling with stated units and corrections.

Localization term (Weakness 2)

the utility of new objective term (localization) added is not established.

The box loss preserves the detector's own box predictions.

Building on Braun et al., our classification-only versus classification-plus-box ablation raises IoU with the detector's own boxes by 0.23–0.31 points; GT-box IoU does not improve (Sec. 4.2; App. C.2).

Visual meaning (Q2)

Are there any patterns among blindspot concepts?

Samples from 15 blindspots show recognizable shared patterns.

We compared high-activation and class-matched random samples for all 17 blindspots. Figure 4 shows six: reflections, shape, occlusion, rooflines and truncation. Two of the 17 had no clear shared visual property in these samples.

We hope this addresses your concerns.

Dear Reviewers,

The authors have addressed your comments in their rebuttal. Please review their responses and provide any further feedback or follow-up questions, if any. Thank you!

Best, AC

Thank you for the rebuttal. My concerns regarding the evaluation setup are addressed but the results show limited utility for blindspots and localization term. I am raising my score to 2.

Comments on the paper

1 comment

We thank all reviewers for their constructive suggestions. We added visual examples, final-detection interventions and predictor information-removal tests, and matched training data and budgets. Cascade replication, localization-loss ablations and fixed-budget review are now also in the manuscript. Three findings follow; references use the revised version.

Blindspots show recognizable visual properties and indicate external detection difficulty. We compared sampled high-activation objects with class-matched random objects for all 17 blindspots. Fifteen showed clearer shared properties: reflections, vehicle shapes, occlusion, exposed rooflines and boundary truncation; Figure 4 illustrates six (Section 4.3). With the concept model and list frozen, within-image, same-class geometric matching across BDD100K, KITTI, RealDriveSim and SIM10K reveals 40.7–56.2-point FN gaps between blindspot-only and normal-only cars, without a risk MLP. All four survive correction across 30 comparisons (Section 4.4). Separate mixed-identity comparisons, coverage and visibility checks are in B.3. These GT-object tests are distinct from GT-free screening.

Activation changes affect final detections with proposal geometry fixed. Paired-original restoration raises AP50/AP50:95 by 0.358/0.115 points, with 134 fewer FN and 13 more FP at confidence 0.5. Proposals and box regression stay fixed; classification changes reach decoding and NMS. GT-matched objects and paired originals are used, with equal-norm, PCA and classifier-gradient controls (Section 4.6).

Cascade R-CNN replication finds 24 blindspots; 18 pass frozen-head excessive-activation restoration tests against four equal-norm controls (C.3, Tables 15–17).

Adding localization preservation lowers box-output reconstruction error by 4.9–5.0%. In the separate 456-input downstream ablation, KITTI FN AUROC/C@5 increase by 1.62/0.48 points; BDD100K does not improve (C.2, Tables 13–14).

Blindspot-associated information contributes to FN prediction and budgeted review. Removing it from the original 472 inputs and retraining lowers FN AUROC by 11.34/7.81 points on KITTI/RealDriveSim. KITTI losses exceed matched-normal, source-error-selected normal and random removal by 4.98/2.89/2.51 points. Controls match lost directions; random controls also match input-change magnitude. These contrasts pass 576-test Holm correction (Section 5.4; D.1). D.2 keeps 16 output statistics fixed. A.3/D.3 retain mixed FP emphasis gains and the stronger output-only control. Output-only is a supervised MLP predicting image-level FN/FP risk from 16 statistics of detector box counts and confidence scores, without concept or blindspot inputs.

At the same 84-input and training budget, blindspots find 1,135 SIM10K misses versus 944 for source-error-selected PCA17 in 500 reviewed images: +191 (+20.2%). C@5 improves by 0.981 points [95% CI: 0.517, 1.412], passing 144-test Holm correction (D.4, Table 29). Full PCA and ViLU find 1,212/1,709; this is a matched compact-PCA gain.

Manuscript revisions relative to the submitted version. We have revised the paper to incorporate these findings and make the diagnostic and predictive contributions explicit:

Location in the revised paperChange
AbstractRetained the original motivation and method description; updated final-detection AP results, the prediction claim, and released-artifact availability.
Sections 1–2 and 6Revised the claims and contributions to distinguish concept diagnosis, functional evidence, and supervised prediction; clarified the relationship to prior task-preserving SAE work.
Section 3Specified the clustering and identity rules, statistical tests, and matched magnitude of restoration and control interventions.
Sections 4.3, 4.4 and 4.6Added images showing shared visual properties of blindspot-activating objects, within-image matched-object comparisons, and intervention effects on final AP and FN/FP.
Sections 5.2–5.4; Tables 4–5Added a compact six-domain FN comparison, including the output-only control, followed by removing information and retraining the original predictor. Explained how proposal-level concepts and emitted-box statistics provide different cues for FN/FP screening.
Appendices A–DImplementation/uncertainty: A.1–A.2; full FN/FP tables: A.3, Tables 7–10; discovery/layout checks: B.1; visual/matched objects: B.2–B.3; interventions and C3-F08 linking Figure 4(e), loss and both regimes (existing results, not a new experiment): C.1; localization fidelity/downstream ablation: C.2, Tables 13–14; Cascade replication: C.3, Tables 15–17; original/conditional removal: D.1–D.2, Tables 18–22; input emphasis: D.3, Tables 23–24; PCA controls/budgeted review: D.4, Tables 25–29.

We hope these revisions and responses address your concerns and clarify the evidence supporting our conclusions.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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