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The Geometry of AP Degradation: A Closed-Form, Zero-Parameter Theory of Localization Sensitivity

Abstract

Average Precision (AP) is discontinuous in box coordinates because it thresholds a continuous quantity, IoU — but exactly where that discontinuity falls, and why it produces the empirical fragility practitioners observe (a single-pixel shift can drop mAP by double digits, hitting small objects hardest), has been missing. We derive closed-form IoU expressions under translation and corner-anchored scaling giving the exact shift at which a detection flips from correct to incorrect, , a zero-parameter formula in object size and IoU threshold . This single formula unifies four otherwise-disconnected phenomena as corollaries of one mechanism: why small objects degrade fastest, why diagonal shifts hurt more than axis-aligned ones, why enlarging and shrinking have near-identical effect, and why averaged mAP degrades faster than . We validate against official COCOeval on real COCO annotations (MAE , correlation , transferring with no refitting to LVIS), and show the same closed form predicts real detectors' (Faster R-CNN, YOLOv11) relative degradation shape, once rescaled by their own baseline. The theory is prescriptive as well as explanatory: inverting the formula yields a size-adaptive threshold that cuts the size bias of AP degradation roughly twentyfold on the idealized protocol ( on five real detectors), and a smoothed variant removes the discontinuity while leaving detector rankings unchanged.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
average precision, object detection, IoU, evaluation metrics, mAP, COCO, localization error, small objects, threshold effects, metric robustness, detection benchmarking, AP fragility, size bias, COCOeval.

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.00 over 3 reviews, above 85% of the others.
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Paper summary

This paper investigates the sensitivity of Average Precision (AP) to small bounding-box localization errors in object detection. The authors derive closed-form expressions for IoU under translation and corner-anchored scaling and use them to characterize the displacement at which a detection crosses a specified IoU threshold. They further relate dataset-level degradation to the distribution of object sizes.

The theoretical results are validated using controlled perturbations on COCO and LVIS annotations, together with experiments involving pretrained detectors, including Faster R-CNN and YOLOv11. The authors propose size-adaptive IoU thresholds and smoothed AP as potential approaches to reducing size-dependent sensitivity and discontinuities in conventional evaluation.

The central contribution is an analytical characterization of known AP sensitivity phenomena, together with theory-guided modifications to object detection evaluation.

Critical strengths
  1. Clear and interpretable theoretical characterization. The paper provides a unified analytical explanation of several localization-sensitivity phenomena, including object-size dependence, directional sensitivity, and differences between IoU thresholds. The connection between individual threshold-crossing distances and dataset-level size distributions is particularly useful because it relates aggregate degradation behavior to measurable dataset properties.

  2. Extensive validation of the geometric predictions. The authors evaluate their theoretical predictions using controlled perturbations on COCO and LVIS, as well as real detector outputs. The inclusion of different perturbation types, detector architectures, and Gaussian localization noise strengthens the evidence that the geometric effects are not specific to a single model or dataset. The experiments distinguish idealized absolute prediction accuracy from relative degradation estimates for real detectors.

Critical weaknesses
  1. Novelty Relative to Prior Work. The novelty is not sufficiently established relative to existing research. Borji, “Sensitivity of Average Precision to Bounding Box Perturbations,” investigates AP sensitivity using nearly identical experimental protocols, including eight translation directions, 0–10 pixel perturbations, ground-truth boxes as predictions, real detectors, and enlarging/shrinking transformations. Le Jeune and Mokraoui, “Rethinking Intersection Over Union for Small Object Detection in Few-Shot Regime,” study scale-adaptive evaluation and derive a mathematically equivalent horizontal IoU inversion in Appendix C.3, for a different purpose. This submission adds general-direction analysis, dataset-level characterization, and additional validation.

  2. Insufficient Validation of the Proposed Metric. The proposed size-normalized metric reduces size-dependent AP degradation. This does not necessarily establish better evaluation quality. The paper provides no validation against human localization judgments or downstream task performance and lacks comparisons with relevant alternatives. The proposed metric's detector rankings depend on the chosen localization tolerance. Paper does not establish a principled method for selecting this parameter.

Questions for authors
  1. Novelty Relative to Prior Work. What are the main theoretical contributions beyond Borji and Le Jeune and Mokraoui, given the mathematically equivalent horizontal IoU inversion in Appendix C.3 of Le Jeune and Mokraoui?

  2. Validity of the Adaptive Threshold. How does Equation (7) handle s <= c, which produces nonpositive thresholds and may accept zero-overlap predictions? Does Corollary 7's direction-uniform guarantee extend to rectangular boxes?

  3. Practical Significance. How does the proposed metric compare with alternatives such? Is there evidence that it better reflects human judgments or downstream task performance, beyond reducing size-dependent AP degradation?

3 comments

PART 1 of 3 — Novelty relative to Borji (2022) and Le Jeune & Mokraoui (2023)

Thank you for the careful and knowledgeable review. Both prior works are real, closely related, and we should have cited them; we have revised the paper accordingly.

Borji (2022), "Sensitivity of Average Precision to Bounding Box Perturbations" (arXiv 2206.10107). This is the closest prior work, and omitting it from the submission was our error, now corrected: it is cited in the Introduction and Related Work and credited as the first measurement of this sensitivity. We deliberately reuse its protocol (ground-truth boxes as predictions, eight translation directions, 0–10 px, one-sided enlarge/shrink) so that results are directly comparable. That work is empirical: it measures AP's sensitivity but has no closed-form analysis, no size-dependence derivation, no dataset-level characterization, no size-adaptive criterion and no implemented remedy. What this submission adds is the explanation and what follows from it:

Borji (2022)This submission
Analysisempirical measurement onlyclosed-form IoU under general-direction translation and scaling; threshold-crossing distances
Dependence on object sizeobservedderived; dataset-level curve is a rescaled survival function of the size distribution
ValidationMask R-CNN, COCO, GT boxes as predictionsofficial COCOeval (MAE <= 0.032, correlation >= 0.997 under the idealized protocol); transfer to LVIS; 16 real detectors incl. DETR-family and vision-language models
Detector rankingnot studiedranking-stability analysis (a 1 px shift costs strong detectors 1.0–2.6 mAP points yet reorders no detector pair)
Remedynonesize-adaptive pixel-tolerance criterion, with its limits tested (Parts 2 and 3)

"We have also sent a confidential note to the AC regarding this reference."

Le Jeune & Mokraoui, "Rethinking IoU for Small Object Detection in Few-Shot Regime" (arXiv 2307.09562). You are right, and we verified it: Appendix C.3 inverts the horizontal IoU of identical squares, C(x) = (w - |x|)/(w + |x|), via g(z) = w(1-z)/(1+z) to derive the distribution of IoU/GIoU under Gaussian shift. That is exactly our axis-aligned Corollary 2, t*(tau, W) = W(1-tau)/(1+tau). We now say so in the paper (Sec. 4 and Related Work) and describe the corollary as elementary algebra, no longer "the central quantitative result". Their purpose differs: a distribution of the criterion under random noise, versus our tolerance (crossing distance) used to explain AP behaviour and to define a pixel-tolerance threshold.

What remains as contribution beyond these two:

  1. General-direction and anisotropic crossing distances (the diagonal/axis asymmetry, Lemma 1 and the general-direction corollary) and the closed forms for corner-anchored enlarge/shrink, which neither work derives.
  2. The dataset-level characterization: the aggregate degradation curve is a rescaled survival function of the object-size distribution (Corollary 4), so its shape is predictable from dataset statistics.
  3. The AP-level validation of those predictions (COCOeval, LVIS, 16 detectors) and the ranking analysis (a systematic 1 px shift costs strong detectors 1.0–2.6 mAP points yet reorders no detector pair).
  4. A threshold-based, pixel-tolerance remedy with its limits measured (Parts 2 and 3). Note that SIoU is a different design (IoU^p, a power transform of the similarity, with a human study), and they themselves remark that scale-adaptive thresholds are not equivalent to it.

We are also happy to scope the paper's claim explicitly: it is primarily an explanation and validation of known AP sensitivity, plus theory-guided diagnostics, not a new theory of IoU.

PART 2 of 3 — Validity of the adaptive threshold: Eq. (7) when s <= c, and rectangular boxes (Corollary 7)

Eq. (7) and s <= c. You are right: for s <= c the threshold (s-c)/(s+c) is non-positive, and since IoU >= 0 such an object accepts any same-class detection, even a disjoint one. Our code clipped tau at 0, so it did exactly this: 1.7% of val2017 boxes on average over c = 1..10 (5.1% at c = 10; 12% of the small ones) and 19% of LVIS boxes. We now floor it at COCO's loosest threshold, tau(s,c) = max{(s-c)/(s+c), 1/2} (tolerance saturates at s/3), and report the effect: the idealized large-small gap reduction, measured with a real AP evaluator, is 9x (not the previously reported ~20x, which was also a pass-rate statistic); LVIS 8.9x -> 5.2x; on real detectors it changes little (five CNN detectors 5.4x -> 5.9x; ranking agreement with standard mAP over 16 detectors Spearman 0.971 -> 0.974). The un-floored version over-corrected (small objects scored above large ones); the floored version slightly under-corrects them. Appendix B reports tau_min in {0, 0.3, 0.5}.

Corollary 7 (direction-uniform guarantee) does not extend to rectangular boxes. Thank you for catching this: the proof is for squares (W = H = s), but we then applied it with s = sqrt(WH) to all boxes and stated the guarantee without that restriction. We tested it numerically:

  • For s = 50 px, c = 5 px, the guaranteed tolerance falls with aspect ratio r: 0.96c at r = 1.5, 0.88c at 2, 0.76c at 3, 0.67c at 4, 0.48c at 8 (the worst direction is no longer 45 degrees).
  • On the 36,334 val2017 boxes (median r = 1.67; 36% have r > 2) at c = 10: median guaranteed tolerance 0.94c; 38% of boxes get < 0.9c and 12% get < 0.75c.
  • The exact rule for any rectangle is the smallest IoU over all displacements of length c: tau_rect(W,H,c) = min over theta of IoU(c cos theta, c sin theta), a one-dimensional minimization (Lemma 1 plus monotonicity of IoU in |dx|,|dy|). Wherever its floor of 1/2 is inactive (57–90% of boxes for c = 10..3) it guarantees exactly c pixels in every direction (verified numerically: guaranteed tolerance / c = 1.0000).

The corollary is now restated for squares, with a new remark giving these numbers and the exact rectangular rule (Appendix B; a summary is also in Sec. 6 of the main text). We have not used the direction-uniform variant in any experiment (the experiments use the axis-aligned form), and the paper says so.

PART 3 of 3 — Practical significance: human judgments, downstream performance, alternatives, and the choice of the tolerance

We have no validation against human judgments or downstream performance of our own, and we agree this limits what can be claimed. Rather than leave it at that, we added what can be tested, and one of the results goes against our proposed metric; we report it plainly.

External human evidence (premise only). Le Jeune & Mokraoui's 75-participant study (>3,000 ratings, DOTA images) finds people are more lenient than IoU toward small objects. That supports the premise behind a size-adaptive tolerance. It does not validate our metric (different data and criterion), and their SIoU-vs-IoU correlation gap (Kendall tau 0.701 vs 0.674) is small.

A validity criterion needing no human labels: ranking stability under annotation noise. A metric should not reorder detectors because of irreducible annotation noise. COCO and LVIS annotated the same images independently, so we measured the disagreement on 13,393 matched objects: median 1.1 px per coordinate (90th percentile 7.2 px), growing sub-proportionally with object size (log-log slope 0.62; lower bounds, since matching requires IoU >= 0.5). We then perturbed the ground truth of a 500-image subset with this empirical disagreement (10 draws) and rescored our 16 detectors (Appendix H):

metricKendall tau vs. unperturbed rankingpairs swapped (of 120)
standard mAP0.9930.4
SIoU-AP (their defaults)0.9950.3
AP750.9731.6
NWD-AP (C = 32)0.9701.8
AP500.9373.8
size-normalized AP (ours)0.9234.6

The size-normalized metric is the least rank-stable. Starting its tolerance range above the noise floor did not help (c = 5..10: tau = 0.89). So we have no evidence that it evaluates better than standard AP by this criterion, and we now claim it only as a diagnostic of size-dependent localization quality, not a better metric (abstract, Sec. 6 with the ranking-stability table now in the main text as Table 4, Limitations and Conclusion revised accordingly). A by-product that supports the paper's main message: annotation noise moves standard mAP's absolute value by ~11 points (24% relative) while barely touching the ordering.

Choosing the tolerance C. The measured noise gives no principled single C. Annotator disagreement is neither constant in pixels nor proportional to size, so neither a fixed pixel tolerance nor a fixed IoU matches it. Our default C = 10 lies between the 90th and 95th percentile of disagreement, which is a rationale, not a derivation. We continue to recommend reporting rankings at more than one C.

Alternatives. We compared against AP50, AP75, NWD-AP and SIoU-AP (table above), but not against LRP, PDQ or Optimal Correction Cost, which we cite but did not reimplement; a comparison with them, a downstream-task study, and a human study of our own are listed in the Limitations as open.

Reviewer_scaHOpenReview ↗
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Paper summary

This paper studies how localization errors affect AP in object detection. It derives IoU expressions under translation and scaling. It further relates threshold-crossing distances to the object-size distribution. Besides, it proposes size-adaptive thresholds and smoothed thresholding to address size dependence and threshold discontinuities. Experiments evaluate perturbed ground-truth boxes and real detector predictions on COCO, with additional validation on LVIS.

Critical strengths
  1. The paper addresses an important issue in detector evaluation. Small localization errors can substantially change AP, especially for small objects. Studying this sensitivity helps explain how object size and perturbation direction affect evaluation scores.
  2. Geometric analysis is interpretable. Eqs. (1)–(4) relate IoU changes and threshold-crossing distances to box size and displacement.
  3. The validation includes full COCO val2017 and an LVIS subset. Further experiments examine real detector predictions and Gaussian localization noise, extending the analysis beyond perturbed ground-truth boxes.
Critical weaknesses
  1. Fig. 1 reports pass rates as mAP. Appendix H states that it measures the fraction of boxes passing the IoU threshold. This does not include the ranking and precision-recall calculation required for AP. Therefore, the reported 20-fold reduction concerns the pass-rate gap, not the AP gap. The labels and claims should be corrected.
  2. Eq. (7) can accept predictions far from the target. For a 5-by-5 target and c=10, the threshold is -1/3. A prediction shifted by 100 pixels has IoU=0, but still passes this threshold. This contradicts the intended 10-pixel tolerance. Please specify how cases with s≤c are handled.
  3. The margin model does not preserve the measured IoU. Appendix D converts the initial IoU into a displacement and then randomizes its direction. For a 40-by-40 box with IoU 0.8, rotating the displacement to 45 degrees gives IoU approximately 0.738, even before adding the tested perturbation. The model starts with a different localization error. Its lower MAE alone does not establish that the measured initial margin explains the residual error.
  4. The paper does not discuss several closely related works. [1] study how bounding-box annotation noise affects AP, especially for small objects and high IoU thresholds. [2] introduce SAFit for size-adaptive detection evaluation. [3] uses weighted true and false positives to avoid a fixed IoU threshold. It would be better to discuss these works and distinguish the proposed evaluation methods from these earlier contributions.

[1] Murrugarra-Llerena and Jung, Noise-Aware Evaluation of Object Detectors. WACV, 2025.

[2] Ying et al., Visible-Thermal Tiny Object Detection: A Benchmark Dataset and Baselines. IEEE TPAMI, 2025.

[3] Zhang et al., Area in Circle: A Novel Evaluation Metric for Object Detection. Knowledge-Based Systems, 2024.

Questions for authors

Please refer to the weaknesses above.

6 comments

PART 1 of 4 — Overview; Weakness 1 (Fig. 1 reports pass rate as "mAP")

Thank you for a careful and technically precise review. We checked each of your three technical points against our code, and fixed them in the revised PDF, and in two cases the correction changes a headline number. We report the corrected numbers below, not just the fixes.

Weakness 1: Fig. 1 plots a pass rate under the label "mAP", so the "20-fold reduction" is a pass-rate gap, not an AP gap. You are right. Our code computes, per box, the fraction of boxes with IoU >= tau; no ranking or precision-recall integration is involved. (The LVIS appendix said so, but Fig. 1 and the main text did not.) The same applies to the soft-credit figures.

What we did:

  1. Re-scored the idealized protocol with a real AP evaluator (ranking + 101-point precision-recall integration, as in COCOeval). We validated it against official COCOeval on the same ground-truth-as-prediction data (mAP 0.6616 vs 0.6614 at 3 px, 0.3697 vs 0.3694 at 10 px).
  2. The submitted pass-rate statistic reproduces (mean |large-small| gap 0.622 -> 0.029, 21x), but the AP gap is what matters. Fig. 1 (now Fig. 2) is regenerated from the AP evaluator and labelled "AP".
  3. The AP numbers differ from the pass-rate headline, mainly because of your Weakness 2 (Part 2): with the corrected threshold, the standard-AP gap 0.625 shrinks to 0.069, a 9x reduction, not 20x. This replaces "twentyfold" everywhere (abstract, intro, Sec. 5, conclusion, tables).
  4. Soft credit: the claim that the soft variant "tracks standard mAP (0.002)" compared per-box credits (pass rates), not AP, and "preserves ranking" was never tested on AP. The text, captions and figure labels now say "per-box soft credit / pass rate", state explicitly that we have not built or evaluated a full soft AP, and drop the ranking claim for it. This is listed in the Limitations.
  5. LVIS is labelled a pass-rate statistic in the main text too.
  6. On real detectors the gap was measured with a real AP evaluator on each detector's own outputs (5 CNN detectors: 0.369 -> 0.062, 5.9x), so that claim only needed its numbers refreshed.

PART 2 of 4 — Weakness 2 (Eq. 7 and s <= c)

You are right, and your example is exact: for a 5x5 target and c = 10, (s-c)/(s+c) = -1/3. Because IoU >= 0 always, such an object accepts any same-class detection, including a disjoint one, contradicting the intended 10-pixel tolerance. Our implementation clipped tau at 0, so it did exactly this: the matcher compares IoU < tau, and IoU = 0 is not < 0.

How much it matters. Fraction of boxes with s <= c: 1.7% of val2017 boxes on average over c = 1..10, 5.1% at c = 10 (12% of the small boxes), and 19% of LVIS boxes (32% of its small ones). In total 29% of val2017 boxes at c = 10 (this includes those 5.1%) received a threshold below AP50's 0.5. It also visibly over-corrected: in the idealized AP evaluation at 10 px, small objects scored above large ones (0.093 vs 0.052 size-normalized AP).

Fix (Eq. 7 in the revision): tau(s,c) = max{ (s-c)/(s+c), 1/2 }, i.e. never more lenient than COCO's loosest threshold, so tolerance saturates at s/3 for objects with s < 3c. The cost is stated plainly: objects below the tolerance cannot be granted c pixels, so small objects are slightly under-corrected (0.021 vs 0.052).

Effect on every result that uses it (large-small gap, standard -> size-normalized; the floor is a design choice, so the appendix on the size-normalized threshold shows tau_min in {0, 0.3, 0.5}):

settingsubmitted (tau_min = 0)corrected (0.5)
idealized, real AP evaluator0.625 -> 0.018 (35x)0.069 (9x)
idealized, pass rate0.622 -> 0.029 (21x)0.072 (9x)
LVIS, pass rate0.605 -> 0.068 (8.9x)0.115 (5.2x)
5 CNN detectors, own outputs, AP5.4x5.9x
16 detectors, own outputs, AP7.7x8.4x

On real detectors the floor changes little: the five-detector ranking is unchanged, and across 16 detectors agreement with standard mAP is Spearman 0.971 -> 0.974 (7 -> 6 reordered pairs of 120). The idealized and LVIS headline numbers change by 2-4x, which is why they are restated. The 0.5 floor is principled (never looser than AP50) but not unique, and the residual limitation is now in the paper.

PART 3 of 4 — Weakness 3 (the margin model does not preserve the measured IoU)

You are right, and we reproduced your number: a 40x40 box with IoU 0.8 has t0 = s(1-m)/(1+m) = 4.44; rotated to 45 degrees that displacement has IoU 0.738, not 0.8. The submitted model therefore started from a different localization error than the one measured, and, as you say, a lower MAE alone does not show the margin explains the residual.

Fix. For each direction phi we now solve for the magnitude t0(phi) at which IoU(t0 cos phi, t0 sin phi) = m exactly (a quadratic; the general-direction threshold-crossing corollary with tau = m), so each detection starts at its measured IoU in every direction (verified: max |IoU - m| < 2e-9). The pass rate is computed per direction, then averaged. It still models the pre-existing error as a pure translation, which is stated.

Does the corrected model help? Mean relative-mAP-curve MAE over our 16 detectors: naive 0.160, submitted margin model 0.066, corrected 0.052 (subset); 0.143 / 0.085 / 0.071 on full val2017, where the corrected model improves 13 of 14 detectors (the submitted one 9 of 14).

But your deeper point stands, and a control confirms it. We reran the corrected model with the margins (i) shuffled across true positives, which keeps their distribution but breaks the link to each detection, and (ii) all set to their mean. Both fit as well or better: 0.027 and 0.034 (subset), 0.040 and 0.051 (full), against 0.052 and 0.071 for the measured margins; the shuffled control is at least as good for 14/16 and 13/14 detectors. So the improvement comes from detections starting below IoU = 1 as a population, and the per-detection margin adds nothing detectable. We have withdrawn the claim that a detector's own margin "explains" its residual (abstract, Sec. 5, Appendix D, Limitations); the paper now says what the control shows, and that the residual is reduced, not explained, by this model.

Reviewer_LCeHOpenReview ↗
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Paper summary

This paper explains why COCO-style AP metric is sensitive to some tiny shift of some result bboxes. A box only counts as correct if its overlap with the ground truth clears a fixed bar. The authors figure out from the box’s width and height alone, how far you can nudge it before it drops under that bar. The slack grows with the object, so small boxes fall off first. The same picture also covers the other patterns they measure: a diagonal nudge hurts more than a sideways one, growing a box and shrinking it start out about equally bad, and the averaged score falls faster than the looser fifty-percent score. Overall, this topic is interesting.

Critical strengths
  1. The topic is interesting: why some difference of the bbox raise critical difference in the AP metric.
  2. The overall analysis is informative and insightful.
Critical weaknesses
  1. There is a lack of experiment result. Most of the paper is analysis.
  2. Old detector is used, like Faster RCNN. The main-stream detector was DETR-based model after the RCNN era, and now the main-stream detector is vision-language model. The main analysis should on the morden VLM model.
Questions for authors
  1. Although small difference in bbox will cause big difference in AP metric in some numerical range, it can still reflect the good or bad bbox trend. So is it still need to modify the AP metric?
3 comments
AuthorsOpenReview ↗

Response to comments (Part I)

part 1 of 3 — Overview and Weakness 1

Thank you for the careful review. Your two weaknesses (too little experimental evidence; no modern detectors) and your question are all fair, and we addressed each with new experiments rather than argument. Everything below is in the revised PDF (new paragraphs "Real detectors across architecture generations" and "Does AP still rank detectors correctly?" in Sec. 5, plus Appendix G) and in the supplementary code.

What changed.

  • Real-detector evidence went from one detector on 128 images (plus a YOLO check) to 16 detectors in four families: 7 CNN detectors; 5 DETR-family detectors (DETR R50/R101, Deformable DETR, RT-DETRv2, D-FINE-X); 2 open-vocabulary vision-language detectors (Grounding DINO, OWLv2); 2 generative vision-language models (Qwen2.5-VL-7B, Qwen3-VL-8B). Fourteen run on the full COCO val2017 (5,000 images, 36,334 boxes); all 16 are compared on a fixed 500-image subset (the VLMs are slow). Same perturbations, official COCOeval, no parameter fitted anywhere.
  • A new analysis answers your question about whether AP still ranks detectors correctly (part 3).
  • In re-running everything at this scale (and following another reviewer's checks) we found some claims in our original submission that did not hold up, and corrected them in the paper (part 2).

Weakness 1: "Lack of experiment results; most of the paper is analysis." This is mainly a theory paper, but you are right that the real-detector support was thin: it rested on 128 images. The new evidence:

  1. The three qualitative findings (small objects collapse fastest; mAP falls faster than AP50; enlarge and shrink behave alike) hold for all 16 detectors.
  2. The zero-parameter closed form is a conservative bound: at every shift, every detector retains more of its mAP than the theory predicts, never less. On full val2017 the median mean-absolute error of the relative mAP curve is 0.115 under translation, and 0.106–0.113 under enlarging, shrinking and random Gaussian jitter. Correlation with the theory is >= 0.95 for every detector except the two weakest (SSD300, SSDlite: 0.89–0.90).
  3. For AP_small the theory is nearly exact: no detector falls more than 0.01 below it.
  4. A one-pixel systematic shift costs every detector above 39 AP between 1.0 and 2.6 mAP points (D-FINE-X and Grounding DINO 2.6, Faster R-CNN 2.1, DETR-R50 1.0).
family (n), 500-image subset, medianAP(0) %loss at 1 px (pts)mAP kept at 10 pxAP_small kept at 10 pxMAE vs. theory
CNN (7)44.61.70.470.050.135
DETR-family (5)47.11.60.460.070.126
open-vocab. VL detector (2)53.82.00.450.070.118
generative VLM (2), all images23.40.40.550.100.197
closed-form theory0.340.050

Where the theory is weaker, we say so: it over-predicts fragility for the weak SSD detectors (MAE 0.27–0.33) and for the generative VLMs on all images (0.197); part 2 explains why.

Presentation. We take the score of 1 seriously. We condensed the introduction's contribution list into four numbered items, removed the roadmap paragraph, and tightened the abstract so it separates what is proved, what is measured, and what is not claimed. If particular passages were hard to follow, we would be grateful to know which.

part 2 of 3 — Weakness 2: modern detectors and VLMs

You are right, and our original submission said as much: its limitations listed transformer set-prediction detectors as untested. We have now tested them, and the VLMs.

Why the theory is architecture-independent, and why we still tested. The closed form depends only on the geometry of an axis-aligned box and a fixed IoU threshold, so it makes no assumption about what produced the box. That is why the paper is organised as theory plus validation. But whether it describes DETR-family and VLM outputs is an empirical question, and you are right that it must be answered on them. They are in the main text (Table 3, Fig. 1), not an appendix.

Results. The DETR-family and open-vocabulary detectors are indistinguishable from the CNNs under the theory: relative-curve MAE 0.126 (DETR-family), 0.118 (open-vocabulary VL detectors), 0.135 (CNN). Modern detectors are, if anything, more exposed in absolute terms: D-FINE-X (59.1 AP) and Grounding DINO (55.5 AP) lose 2.6 points to one pixel, the largest of any detector, and the loss tracks baseline AP (Spearman 0.93), because a stronger localizer's mAP rests on high-IoU true positives, which a shift removes first. DETR-family models are NMS-free, so the interaction between perturbation and NMS that we studied for CNNs cannot arise for them.

Generative VLMs: what we did and what to trust. Qwen2.5-VL-7B and Qwen3-VL-8B were prompted once per image with the 80 class names and asked for a JSON list of boxes. Their boxes are text tokens with no confidence score, so we score each box by the geometric-mean token probability of its JSON object, and also report a constant-score variant; the two differ by <= 0.015 in MAE and <= 2.0 points in AP(0), so the conclusions do not depend on the score. Important caveats:

  • Our 1,536-token cap truncates generation on 19% of images (crowded scenes). On all 500 images the naive theory's error is 0.197; restricted to images whose generation completed (~405 images) it falls to 0.095–0.150, within the CNN range, and Qwen3-VL reaches 43.8 mAP. We report both.
  • Their absolute AP here (18.5 and 28.4 on all images) reflects a single-prompt protocol on 500 images, not the models' best attainable accuracy. Their small absolute one-pixel loss (0.3–0.4 points) is just a consequence of that low AP. The object of study is relative degradation, not these models' ranking.
  • We did not test diffusion-based or SAM-based detectors, and a larger-scale, differently-prompted VLM evaluation would be valuable. These are in the Limitations.

Claims we had to correct. (i) The original submission said a detector's matched-IoU margin explains the residual gap (error 0.136 -> 0.031, on 128 images). Re-examining it (another reviewer found a flaw in the model, which did not preserve the measured IoU), we fixed the model so every detection starts at exactly its measured IoU. It still lowers the error (mean 0.160 -> 0.052 on the subset, 0.143 -> 0.071 on full val2017; 13 of 14 detectors improve). But a control that shuffles the margins across detections, or sets them all to the mean, fits as well or better (0.027, 0.034 on the subset), so the gain comes from detections starting below IoU = 1 as a population, not from each detection's own margin. We withdrew the "explains" claim. (ii) We claimed the size-normalized remedy "preserves ranking exactly"; that holds for the five CNN detectors we had, but across all 16 it reorders 6 of 120 pairs (Spearman 0.97). The paper now says so.

part 3 of 3 — Question: "AP still reflects the good/bad trend, so must it be modified?"

This is the most important question, and the data support half of the premise.

What we agree with: AP is a sound coarse ranker. We applied the same systematic shift to every detector and re-ranked (Appendix G):

  • At 1 px, 0 of 120 pairs (0 of 91 on full val2017) change order, under translation, enlarging, shrinking or Gaussian jitter.
  • At <= 3 px only near-ties swap: under translation, only pairs <= 1.2 mAP points apart (<= 3.6 under any perturbation); Kendall tau = 0.98 at 3 px.
  • Among pairs >= 5 points apart, only 1 of 93 swaps even under a 10 px translation.

So a uniform localization error does not scramble a leaderboard, and we do not argue that AP should be discarded.

What AP is not: a precise ruler. Three things the trend argument does not cover:

  1. Absolute numbers move more than gaps. The one-pixel loss for strong detectors (1.0–2.6 points) is as large as the median gap between adjacent-ranked detectors (1.4 points on the subset, 2.3 on full val2017). A coordinate-convention or resize-rounding difference between two evaluation codebases, with no change to any detector, can therefore move a reported number by roughly a generation of progress, even though it leaves the order intact. Comparing numbers across codebases or papers is where this bites.
  2. Better localizers are penalised most (Spearman 0.93 between baseline AP and loss), so the sensitivity is largest exactly where progress is being claimed.
  3. Size dependence. By the paper's central formula, the tolerated shift scales with object width (t* = W(1-tau)/(1+tau)), so the same pixel error costs a small object several times more IoU than a large one. A trend that is correct on average therefore weights small and large objects very unequally, which matters when datasets differ in object size (e.g. aerial or small-object benchmarks vs. COCO).

Our recommendation, stated more carefully in the revision. Not "replace AP", but report AP together with its sensitivity: e.g. the mAP change under a 1–2 px shift, particularly when comparing detectors within a few points or across datasets with different size distributions. The size-normalized and smoothed variants in Sec. 6 are offered as proofs of concept, not replacements. We also tested whether the size-normalized metric is a safe drop-in on the 16 detectors: it is not rank-preserving (6 of 120 pairs reordered, including some pairs 5–10 points apart), which is a reason to report it alongside AP rather than instead of it. We have not evaluated either remedy against human judgment or downstream performance (stated in the Limitations).

Thank you again; the question sharpened the paper, and the revised conclusion now makes exactly the distinction above.

Comments on the paper

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Summary of responses

We thank all reviewers for their constructive feedback. We have posted individual responses and uploaded a revised PDF. The main updates:

Broader evidence (LCeH). We extended the evaluation to 16 modern detectors, including DETR-family and open-vocabulary/VLM detectors. The AP discontinuity and its small-object bias hold across all of them. The paper now reports this.

Tighter analysis (scaH, 23BG). Following the reviewers' points, we re-audited our pipeline and strengthened the paper:

  • Fig. 1 now uses a full AP evaluator. It shows a ~9× reduction in size bias, a more conservative figure than our earlier per-box estimate.
  • Eq. 7 now has a floor of τ ≥ 1/2, so small objects no longer accept arbitrary same-class boxes. This is verified on COCO and LVIS.
  • We give the exact tolerance rule for rectangular boxes. The earlier direction-uniform result is now stated for squares.
  • We replaced the margin-model explanation of the residual with a control-tested analysis.
  • The ranking-preservation claim is now qualified by results across all 16 detectors: it is exact for 5 CNN detectors and 114 of 120 pairs hold overall.

Positioning (23BG). We added Borji 2022 and Le Jeune & Mokraoui 2023 to related work and clarified what is new here: the size-normalized formulation, the theory, and the large-scale empirical validation.

Metric validity. A new noise-robustness test against COCO-vs-LVIS annotator disagreement characterizes how size-normalized AP behaves. We present it as a complementary diagnostic alongside standard AP.

The main text remains within the 10-page limit. Details are in the per-reviewer responses.

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

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