acceptodds
Under review as a conference paper at ICLR 2027

Stranded Capacity: Deep Pyramid Levels Earn No Return on Small Objects

Abstract

In UAV imagery, remote sensing, and traffic surveillance, small instances account for more than 70% of all objects, against about one third on COCO. Existing work appends modules to a general-purpose detector but inherits the allocation of capacity across pyramid depth, channel width, and input resolution, with the computational budget fixed for a different scale distribution and left largely unexamined. We vary each axis in turn and measure its marginal return per unit of compute. The optimum departs from convention on all three axes, and on two of them the sign reverses: removing deep heads or compressing deep channels raises AP50. We call this condition stranded capacity and trace it to a single geometric quantity, the effective feature area a target occupies on the grid from which the target is predicted. This area scales inversely with the squared pyramid stride and quadratically with input scale. These two dependencies predict the sign of the return on every axis. Reading the configuration from the measured returns yields a three-step transformation that adds no modules. Extensive experiments show that the configuration holds across both detection paradigms. On VisDrone, R-YOLOv11-L matches an identically resolved baseline (41.5 versus 40.8 AP50) with 96% fewer parameters and 76% less compute, and runs 2.3× faster. R-D-FINE-L gains 5.1 AP50 over the corresponding baseline with 87% fewer parameters. The same configuration transfers to five further datasets without retuning, gaining 20.2 and 18.0 AP50 on TinyPerson and SODA-D. The code is included in the supplementary material.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
small object detection, efficient inference, feature pyramid, compute allocation, neural architecture design

Reviews

Among:
Shape:
1234this paper, Top 4%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 3.33 over 3 reviews, above 96% of the others.
Reviewer_hN9tOpenReview ↗
Rating
4
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
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Paper summary

This paper investigates the allocation of computational resources in small-object detection. It introduces the concept of stranded capacity and analyzes the contributions of pyramid depth, channel width, and input resolution. Based on these observations, the authors propose a three-step reallocation strategy that reduces unnecessary capacity and improves detection efficiency without adding new modules.

Critical strengths
  1. The paper offers an interesting perspective on small-object detection by focusing on resource reallocation rather than introducing additional modules.
  2. The method achieves impressive improvements in model efficiency while maintaining or improving detection accuracy.
  3. The experiments are comprehensive, covering multiple datasets, different detection architectures, detailed ablations, and real-world deployment.
Critical weaknesses
  1. The final configuration is obtained from experiments on VisDrone. Although it transfers well to other datasets, it remains unclear how the proposed allocation rule can be applied to datasets with different object-scale distributions.
  2. The paper suggests that deep features may introduce background interference into shallow detection layers, but the evidence is mainly qualitative. Further analysis would help support this explanation.
Questions for authors

Please focus on the concerns raised in Weakness.

5 comments
AuthorsOpenReview ↗

Response 1

Thank you for the time you put into this review and for your support. We appreciate your positive remarks on reallocating capacity instead of adding modules (S1), on the efficiency gained while accuracy is maintained (S2), and on the experiments across datasets, detector families and deployment (S3).

Weakness 1 The final configuration is obtained from experiments on VisDrone. Although it transfers well to other datasets, it remains unclear how the proposed allocation rule can be applied to datasets with different object-scale distributions.

Thank you very much for raising this point. It is a very good one, and we fully agree. We also believe that misallocated capacity is not unique to data extremely skewed towards small objects and must exist in other settings as well, and this is exactly the direction we most want to pursue. Here is what we have explored so far.

(a) We repeated the same measurement on COCO. COCO has the opposite scale distribution: 47.9% of its instances are at least 64 px, against only 1.3% on VisDrone. We trained the same four-head architecture on COCO and closed its heads one at a time (Table k). The result is the opposite of VisDrone: closing the deep heads changes nothing on VisDrone but costs the most on COCO, and the shallowest head goes from the most important to the least important. We take this as first evidence that which capacity earns no return depends on the scale distribution of the data, so that in principle each dataset has its own better allocation.

Table k: Share of instances ≥64 px and change in AP when one head is closed, for the same architecture trained on each dataset (Table 1; Table e, response to Reviewer 79cX).

DatasetInstances ≥64 pxClose H2H_2Close H3H_3Close H4H_4Close H5H_5
VisDrone1.3%−13.27−3.540.000.00
COCO47.9%−1.58−10.12−12.45−13.45

(b) We compared the scale statistics of seven datasets with the state of their deep heads. On the six small-object datasets, instances of at least 64 px are below 1.5% of the annotations; the deep heads were never trained on five of them (their weights only decayed from initialisation) and only in part on CODrone. On COCO the share is 47.9%, and all heads are trained (Table e in our response to Reviewer 79cX). This agrees with what closing the heads shows on COCO.

In sum, the two measurements above give different results on data with different scale distributions: on small-object datasets the deep heads earn no return and can be removed, while on COCO they are the most valuable and have to be kept. We therefore think that the rule can be applied according to the scale distribution of each dataset, and that it is not tied to the configuration obtained on VisDrone. On a new dataset, the configuration is found again in the same three steps: (1) measure the return of each head and remove the heads that earn none; (2) narrow the deep channel groups one at a time, as far as the measured return allows; (3) spend the released compute on a larger input, until its return falls off. The steps can also be run in the opposite direction if the measured returns point that way, for example lowering the input resolution while widening the deep channels.

In the revised paper, a new appendix (App. F.3) will state how the rule is applied to a new dataset and the scope of the present configuration, with a pointer in §4.2 (changes in blue).

AuthorsOpenReview ↗

Response 2

Weakness 2 The paper suggests that deep features may introduce background interference into shallow detection layers, but the evidence is mainly qualitative. Further analysis would help support this explanation.

Thank you very much for this suggestion. We fully agree that a single feature map is not enough, so we made the following measurements on the full VisDrone test set (1,610 images).

(a) We quantified what Figure 4 shows. We compared how strongly the cells on targets and the cells on background are activated. For small objects, the signal sent down from the deep levels ranks a target cell above a background cell with probability 0.58–0.63 (0.5 means no separation), against 0.83 for the backbone P2. What Figure 4 shows in one scene therefore holds on the whole test set.

(b) We quantified its effect on the detections. We cut or narrowed the deep context reaching H2H_2, retrained, and counted the false positives that fall on background (Table j). With P4 at full width, small objects have slightly more background false positives than with P4 at 12.5% of its width (3.9 against 3.7 per image), and APs is slightly lower (11.6 against 11.9). The deep context cannot be removed altogether, however: without it, APs falls to 9.0 and the false positives rise to 10.7 per image.

Table j: APs and background false positives on small objects on the VisDrone test set, with each model thresholded at a small-object recall of 0.40 (mean of one to three seeds).

Context reaching H2H_2GFLOPsAPsBackground false positives on small objects at matched recall (per image)
none27.09.010.7
P351.311.14.8
P4 (12.5% width) + P352.711.93.7
P4 + P3 (Step 1)74.411.63.9

In sum, these measurements support the observation of Figure 4 and show that the extra width of P4 does not help small objects, while the deep context itself remains useful. This is why our method keeps P4 at 12.5% of its width instead of removing it.

In the revised paper, this quantification will be added as App. F.6 (Table j), and App. B.3 will point to it (changes in blue).


Thank you again for the encouraging and constructive review. We are glad to answer any further questions.

AuthorsOpenReview ↗

To Reviewer hN9t

Dear Reviewer hN9t,

We sincerely thank you for the time and care you have devoted to our paper, and for your support. Your two suggestions made the scope of the rule clearer and its explanation more accurate.

We hope the two responses above address your concerns. If any point remains unclear, or if further evidence would help, we would be glad to provide it during the discussion.

Thank you again for your careful evaluation. We look forward to your further comments.

Best regards,

The Authors

Reviewer_rBJwOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper reallocates capacity for small object detection by removing deep heads, compressing channels, and increasing input resolution. Experiments across several datasets show promising efficiency gains.

Critical strengths
  1. The same-resolution comparison on VisDrone shows substantial efficiency gains with comparable accuracy.
  2. The evaluation covers multiple datasets and includes measurements on deployment hardware.
Critical weaknesses
  1. I am not fully convinced by the explanation. An unused deep head does not mean its features are unhelpful. The feature maps alone are not enough to support this claim.

  2. The negative-return gains are small, and results from multiple seeds are missing. Also, Step 1 moves prediction to P2, so the improvement cannot be attributed only to removing capacity.

  3. For D-FINE and the transfer datasets, the comparisons use different input resolution. It is hard to tell how much improvement comes from the architecture itself.

Questions for authors
  1. Could the authors add baseline results at 960 for D-FINE, TinyPerson and SODA-D?
  2. Are the negative returns consistent across random seeds? It would also be good to see what happens when deep-to-shallow fusion is removed.
4 comments
AuthorsOpenReview ↗

Response 1

Thank you for the time and care you put into this review. We appreciate your positive remarks on the efficiency gains at comparable accuracy in the same-resolution comparison (S1) and on the evaluation across several datasets and deployment hardware (S2). Each of your three requests led to a control the paper needed, and all three are done: several seeds, removal of deep-to-shallow fusion, and 960-px baselines.

Weakness 1 and Question 2 (second part) I am not fully convinced by the explanation. An unused deep head does not mean its features are unhelpful. The feature maps alone are not enough to support this claim. It would also be good to see what happens when deep-to-shallow fusion is removed.

Thank you for drawing this distinction. Prediction and features have different answers, each with a measured reason.

(a) For prediction, P3–P5 are of little use. In the three-head baseline, H4H_4, H5H_5 and the bottom-up path (35% of the parameters) were never trained: their weights show weight decay only. At strides 16 and 32, a linear probe, i.e. a linear model fitted on the frozen features, cannot recover the in-cell position of a small object (Table a, last row). And over three seeds, removing all three heads with the bottom-up path, which carries fine-grained information from P2 up to P5, costs only 0.3 AP50 for 26% less compute (Table c).

Table a: Linear probing: logistic or ridge regression is fitted on the frozen neck feature of the cell containing a 6–8 px object and evaluated on held-out objects (AI-TOD baseline; 4,103 objects). Object presence and class remain linearly decodable at every stride, whereas the in-cell position is not decodable at strides 16 and 32.

Probed attributeStride 8Stride 16Stride 32
Object presence (AUROC; chance 0.5)1.000.980.97
Object class (balanced accuracy; chance 0.17)0.810.590.48
In-cell position (R², floored at 0)0.730.060.00

(b) The paper does not say that deep features are unhelpful; they are partly useful. At every stride the same probe still decodes the presence and the class of a small object (Table a, first two rows). The reallocated model keeps these features as context for H2H_2, at 50% of P3 and 12.5% of P4 (§4.2), and the experiment you asked for in Q2 measures their worth: with only H2H_2 predicting, we cut or narrow one level and retrain (Table b).

Table b: AP by object size when the context reaching H2H_2 is cut or narrowed and the model retrained (VisDrone test; mean of one to three seeds; the last two rows are new). Removing the context lowers AP at every size, while P4 at 12.5% of its width loses nothing.

Context reaching H2H_2GFLOPsAP50APsAPmAPl
P5 + P4 + P3 (H2H_2 only)80.837.611.731.838.1
P4 + P3 (Step 1)74.437.511.632.038.4
P4 (12.5% width) + P352.737.811.932.340.4
P4 (1.5% width) + P351.536.611.631.736.2
P351.335.411.130.435.8
none27.028.29.024.322.5

In sum, deep features no longer encode the position of a small object but still encode its presence and class: of little use for prediction, partly useful as context, and 12.5% of the P4 width is enough; the other 87.5% (21.7 GFLOPs) earns no return. What is stranded is capacity, not features.

Figure 4 alone is indeed not enough: in the revised paper, these measurements will be added as App. F.1 (Tables a and b), with a pointer in §4.1 (changes in blue).

AuthorsOpenReview ↗

Response 2

Weakness 2 and Question 2 (first part) The negative-return gains are small, and results from multiple seeds are missing. Also, Step 1 moves prediction to P2, so the improvement cannot be attributed only to removing capacity. Are the negative returns consistent across random seeds?

Thank you for these two points. We added three seeds per configuration (Table c), and the returns hold.

Across seeds, the negative return of P4 width holds, and the return of the deep heads is near zero. Narrowing P4 to 12.5% beats Step 1 in every seed (+0.1 to +0.5 AP50, mean +0.3) with 29% less compute. Removing H4H_4 leaves AP50 unchanged, removing H3H_3 lowers it by 0.2, and removing all three together with the bottom-up path lowers it by 0.3 for 26% less compute. The margins are small, as you note: for the heads they are within seed variation, i.e. the deep heads earn no return, and the return that is negative in every seed is that of the P4 width.

These returns are measured with prediction at P2 fixed. The reference of §4.1 is the four-head model, which already predicts at P2. Against it, Step 1 is 0.4 AP50 lower for 32% less compute, and P4 at 12.5% is 0.1 lower, within seed variation, for 52% less. The +2.3 of Step 1 over the official three heads in Table 5 includes the move of prediction to P2 (35.1 → 37.9 once H2H_2 is added); the returns we attribute to capacity are those measured against the four-head reference.

Table c: AP50 on VisDrone test for seeds 0 / 1 / 2 (mean and std from unrounded values; percentages relative to the four-head reference).

ConfigurationGFLOPsSeeds 0 / 1 / 2Mean ± std
Official three heads86.635.1–
Four-head reference109.437.7 / 37.9 / 38.237.9 ± 0.2
−H3H_3106.3 (−3%)37.9 / 37.5 / 37.637.7 ± 0.2
−H4H_4108.0 (−1%)38.1 / 38.1 / 37.637.9 ± 0.3
−H5H_5105.2 (−4%)38.0 / 38.1 / 37.537.9 ± 0.3
H2H_2 only80.8 (−26%)37.8 / 37.4 / 37.637.6 ± 0.2
Step 1 (H2H_2 only, Stage 5 removed)74.4 (−32%)37.4 / 37.5 / 37.537.5 ± 0.1
P4 at 12.5%52.7 (−52%)37.8 / 37.9 / 37.637.8 ± 0.2

In sum, over three seeds and with prediction at P2 fixed, P4 at 12.5% stays within 0.1 AP50 of the four-head reference for 52% less compute.

In the revised paper, a new table will report all seeds with mean ± std (App. F.2), §4.1 will state the result, and Tables 9 and 11 will point to it (changes in blue).

AuthorsOpenReview ↗

Response 3

Weakness 3 and Question 1 For D-FINE and the transfer datasets, the comparisons use different input resolution. It is hard to tell how much improvement comes from the architecture itself. Could the authors add baseline results at 960 for D-FINE, TinyPerson and SODA-D?

Thank you for suggesting the 960-px baselines: they separate what the resolution contributes from what the architecture contributes. Each uses the recipe of its 640-px baseline, with only the input size changed (Table d).

On the YOLO side, the architecture keeps its lead at equal resolution. On TinyPerson / SODA-D, R-YOLOv11-L is 8.6 / 2.3 AP50 above the 960-px baseline at about a quarter of the compute. The reported +20.2 / +18.0 thus split into 11.6 / 15.7 from resolution and 8.6 / 2.3 from the architecture.

On D-FINE, the reallocation buys compute, not accuracy. With the same recipe (random initialisation, 500 epochs), R-D-FINE-L is 0.9 AP50 below the 960-px baseline and 0.6 APs above it, with 41% of the compute and 87% fewer parameters. This is what the paper states: "Reallocation does not buy new accuracy; it makes that accuracy affordable."

Table d: Baselines retrained at 960 px (TinyPerson and SODA-D on their validation splits, as in Table 3).

DatasetModelInputGFLOPsAPAP50APs
TinyPersonYOLOv11-L64086.67.122.05.0
YOLOv11-L960196.511.733.69.2
R-YOLOv11-L96046.615.142.213.5
SODA-DYOLOv11-L64086.65.112.93.4
YOLOv11-L960196.512.528.69.5
R-YOLOv11-L96046.613.330.910.9
VisDroneD-FINE-L64096.124.342.215.1
D-FINE-L960202.928.548.218.0
R-D-FINE-L96084.128.047.318.6

In sum, at equal resolution the architecture still leads on the YOLO side and comes within 0.9 AP50 of D-FINE-L at 41% of the compute.

In the revised paper, the 960-px baselines will be added to Tables 2 and 3, and the abstract, §5.2 and §5.3 will state the same-resolution results (changes in blue).


Thank you again for your careful review. These results extend the VisDrone comparison you found convincing to more datasets and a second detector family; if they resolve your concerns, we would be grateful if you would reconsider your rating.

AuthorsOpenReview ↗

To Reviewer rBJw

Dear Reviewer rBJw,

We sincerely thank you for the time and care you have devoted to our paper. Your comments led us to test its claims more strictly and to state them more precisely, and the paper is better for it.

We hope the three responses above address your concerns. If any point remains unclear, or if further evidence would help, we would be glad to provide it during the discussion.

Thank you again for your careful evaluation. We look forward to your further comments.

Best regards,

The Authors

Reviewer_79cXOpenReview ↗
Rating
3
Confidence
2
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

In this paper, they assume that there 70% small object in the environments. for efficiency, deep pyramid levels should be designed for small objects. This paper proposes a three-step reallocation strategy: removing deep detection heads, compressing channels in deeper layers, and reinvesting the saved budget into higher input resolution. The core theoretical concept, "Make an Effective Feature Area" is shown to be inversely proportional to the square of the pyramid stride and directly proportional to the square of the input resolution. The proposed method achieves equivalent accuracy while reducing parameter count by 96% and computational load by 76%, without requiring any additional modules. Furthermore, the configuration derived from the VisDrone dataset generalizes to five other datasets without the need for further tuning.

Critical strengths

The use of a single geometric quantity, A_eff, to explain the performance trends across three distinct axes (depth, channels, and resolution) is highly effective. The study also demonstrates falsifiability through a counter-experiment on the COCO dataset, where the relative importance of detection heads is shown to be reversed. Additionally, the configuration proves effective across five other datasets, yielding significant gains (e.g., +20.2 AP50 on TinyPerson and +18.0 AP50 on SODA-D). The authors also validate improvements in both energy efficiency and latency on edge hardware (Jetson Orin Nano). Finally, the approach is shown to be model-agnostic, as it can be applied to both YOLO-based and DETR-based architectures.

Critical weaknesses

All operating points (P3 at 50%, P4 at 12.5%, and an input resolution of 960) are determined solely through an axis-wise sweep performed on a single dataset: VisDrone. As the authors themselves acknowledge, the extent to which these values ​​are representative has not been systematically analyzed. Furthermore, the selection of operating points in Step 2 involves sweeping each channel group independently and then combining them based on an "additivity" assumption; however, the computational cost (in terms of GPU time) of this search process is not reported, making it difficult to gauge the actual burden this imposes on the design procedure. Additionally, the logical progression lacks sufficient verification and analysis to establish both causality (via intervention experiments) and generalizability.

Questions for authors
  1. Why was the selection of operating points in Step 2 performed by sweeping each channel group independently and then combining them using an "additivity" assumption?
  2. Was the computational cost of the search process itself not taken into account in the analysis?
  3. Regarding the conclusion that the findings "support the causal role of A_eff," is it possible that the sample size is too small, and that the effects of changes in context have not been adequately isolated?
9 comments
AuthorsOpenReview ↗

Response 1

Thank you for the time and care you put into this review, and for recognising the explanatory role of AeffA_{\rm eff} and the reverse experiment on COCO. Your questions pointed to where our evidence was thinnest, and each of the three concerns now has added evidence.

Weakness (first part) All operating points (P3 at 50%, P4 at 12.5%, and an input resolution of 960) are determined solely through an axis-wise sweep performed on a single dataset: VisDrone. As the authors themselves acknowledge, the extent to which these values are representative has not been systematically analyzed.

Thank you for this point. The values were set on VisDrone and then frozen, and their representativeness is tested out of sample: used unchanged, the two ratios hold on five other datasets.

(a) Used unchanged, the two ratios hold on five other datasets, also at equal resolution. On all five transfer datasets, R-YOLOv11-L keeps P3 at 50% and P4 at 12.5% and improves on its baseline (Table 3). Against the new 960-px baselines, it leads at the same input on TinyPerson and SODA-D (AP50 42.2 vs. 33.6 and 30.9 vs. 28.6) at about a quarter of the compute (Table d in our response to Reviewer rBJw).

(b) The ratios carry over because their cause is shared: the scale distribution. The deep levels serve large objects, and on all six small-object datasets instances of at least 64 px, the band served by H4H_4 and H5H_5, are below 1.5% of the annotations. The trained baselines show it directly: the deep heads were never trained on five of the six and only in part on CODrone (Table e). On COCO the share is 47.9% and all heads are trained, so the values represent the small-object regime, not every dataset.

Table e: Share of instances ≥64 px in the training annotations (wh\sqrt{wh} after resizing to 640; COCO: val2017, Table 10) and state of the deep heads and bottom-up path in the trained baseline. "Untrained": weight norms at one common ratio to initialisation, i.e. weight decay only, no task gradient.

DatasetInstances ≥64 px (the band served by H4H_4/H5H_5)Deep heads and bottom-up path in the trained baseline
AI-TOD0.0%untrained
SODA-D0.0%untrained
TinyPerson0.1%untrained
TT100K0.2%untrained
CODrone0.3%H4H_4 box branch trained, H5H_5 not
VisDrone1.3%untrained
COCO47.9%all trained; head ordering reversed (Table 1)

(c) The result does not hinge on the exact ratios; the input size is the one value that differs by dataset, and the paper says so. On VisDrone, P4 gives ΔAP50 between +0.4 and +0.6 at every width from 75% down to 12.5%, and P3 declines gradually (−0.2, −0.7 and −1.4 at 75%, 50% and 25%; 50% trades 0.7 AP50 for 14.4 GFLOPs), so a neighbouring ratio moves AP50 by at most 0.7; only P4 below 12.5% costs accuracy (−0.8 at 1.5%; Table 11). The best input does differ: accuracy on TinyPerson peaks at 1600 px (§3), which is why the paper fixes 960 as a rule to test transfer without search, not as the optimum of each dataset (§4.2).

In sum, the values were set on one dataset but are not specific to it: used unchanged, they hold on five datasets of the same scale regime, and this regime is what they represent. One limitation remains: the sweep was run on VisDrone only, so the values are not shown to be optimal for other datasets. Future work will study how the operating points vary with the scale distribution and whether they can be read from it without a sweep, the next step named in our conclusion.

In the revised paper, Table e will be added to the main text (§4.1), and a new appendix (App. F.3) will state the status of each value (flat region for P4, trade-off for P3, budget rule for the input size) and this limitation, with a pointer in §4.2 (changes in blue).

AuthorsOpenReview ↗

Response 2

Questions 1 and 2 Why was the selection of operating points in Step 2 performed by sweeping each channel group independently and then combining them using an "additivity" assumption? Was the computational cost of the search process itself not taken into account in the analysis?

Thank you for these two questions. Additivity is measured, not assumed, and it is what keeps the search cheap; we now report the cost.

(a) Additivity is measured. The last four rows of Table 11 test it (Table f): each combined change differs from the sum of the single changes by at most 0.3 AP50, the size of the standard deviation across seeds (0.1–0.3). The chosen point also lies in a flat region (P4 from 75% to 12.5%: ΔAP50 between +0.4 and +0.6), so small interactions cannot change the choice.

Table f: Additivity test on VisDrone: ΔAP50 relative to Step 1 for combined compressions, against the sum of the single changes.

CombinationSum of single changesMeasuredDifference
P3 50% + P4 12.5%−0.30.0+0.3
P3 50% + Neck-P3 50%−0.8−0.9−0.1
P4 12.5% + Neck-P3 50%+0.3+0.2−0.1
All three−0.4−0.6−0.2

(b) The search is cheap because each step has a direction. Sweeping the three groups one at a time needs 12 runs; the full grid needs 108 (6 × 6 × 3), about 780 GPU-hours. Steps 2 and 3 together took 29 runs and about 265 GPU-hours (Table g), run once on VisDrone; the five transfer datasets reuse the two ratios (Table 3). Unlike NAS, the procedure searches no architecture space: it calibrates a few ratios and the resolution along fixed axes, each step guided by a measured return.

Table g: Cost of the sweeps from the training logs (single RTX 4090; 23 runs measured, 16 estimated from runs of the same kind; one Step-2 run takes about 7 hours, as one baseline training).

SweepRunsGPU-hours
Step 2: per-group sweep and combination checks (Table 11)22about 160
Step 3: resolution and channels (Table 11)7about 105
Head-removal analysis (Table 9; not part of the procedure)10about 90
Total39about 350

In sum, the per-group sweep rests on a measured additivity and replaces a full grid of 108 runs by 12.

In the revised paper, §4.2 will read "at most 0.3" instead of "less than 0.3" and point to these four rows, and Table g will be added to the appendix (changes in blue).

AuthorsOpenReview ↗

Response 3

Weakness (last part) and Question 3 Additionally, the logical progression—specifically regarding the causal role of A_eff—lacks sufficient verification and analysis to establish both causality (via intervention experiments) and generalizability. Regarding the conclusion that the findings "support the causal role of A_eff," is it possible that the sample size is too small, and that the effects of changes in context have not been adequately isolated?

Thank you for naming these two limits: the original experiment covered 29 targets, and cropping changed their context (hence "supports" in the paper). Two new interventions leave the context untouched: one on 10,248 targets from two datasets, one on the full VisDrone test set.

(a) What we did: shift the whole image by a few pixels and compare each target with itself. A stride-8 head predicts at one point per 8 × 8-px cell, the cell centre (a grid point). A small target sometimes covers a grid point (its annotated box contains one) and sometimes falls between two, depending only on where it sits in the image. We shift each image in 16 ways (0–6 px horizontally and vertically): the same target covers a grid point under some shifts and none under others, while the target and everything around it stay exactly the same.

(b) What we found: the same target is recalled 25–29 points more often when it covers a grid point. Under the shifts where it covers one, recall is 63.2% on VisDrone, against 34.7% under the shifts where it does not; on AI-TOD, 82.2% against 56.9% (10,248 targets, Table h). The target and its context are unchanged, so the difference comes only from covering a grid point.

(c) The gain comes from the grid point, not from the shift. A model with a finer grid (P2 head) is barely affected by the same shifts (+2.0 / +0.3). The gain appears in every 2-px size bin from 4 to 12 px (+11 to +45). The step is at the first grid point: covering a second adds nothing (+0.4 / −1.7), in line with the threshold of about one cell in the paper (θmin⁡=0.94\theta_{\min} = 0.94).

Table h: Recall of the same target under image shifts (10,248 targets of 4–12 px, 150 validation images per dataset; three-head baseline unless noted, and the P2-head model is P2–P5 on VisDrone and P2 only on AI-TOD; 95% bootstrap intervals in brackets). The gain comes with the first grid point.

VisDroneAI-TOD
Recall when the target covers no grid point34.7%56.9%
Recall when it covers one63.2%82.2%
Gain (points)+28.5 [27.0, 30.0]+25.3 [16.6, 32.7]
Control: gain for a model with a finer grid (P2 head)+2.0+0.3
Gain from covering a second grid point+0.4−1.7

(d) AeffA_{\rm eff} is the average number of grid points a target covers; raising it directly recovers about half of the gain of a P2 head. One more head reads the neck P3 output upsampled to stride 4 by parameter-free nearest-neighbour interpolation: no P2 feature enters, the image is unchanged, and every target covers 4 times as many grid points (Table i).

Table i: Grid densification on the full VisDrone test set (first two rows single-seed; the four-head AP50 is the mean of three seeds). The densified head recovers about half of the AP50 gain and about two thirds of the APs gain of a P2 head.

ModelAP50APs
Three heads35.110.0
+ densified head36.411.2
Four heads37.911.8

In sum, with the image content unchanged, a small target is detected far more often when it covers a grid point; AeffA_{\rm eff} is the average number of grid points a target covers and acts on detection through this number, which also explains why adding a P2 head helps.

In the revised paper, §3 will report the translation experiment with Table h, and App. F.5 will give both interventions in full (changes in blue).


Thank you again for these questions; the causal evidence in the paper is stronger because of them. We are glad to clarify anything further.

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

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