Review Reports - CPD-FCOS: A Scale-Isolated P2 Pathway for UAV Small-Object Detection

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Summary: This manuscript proposes CPD-FCOS, a UAV small-object detector designed around a scale-isolated P2 pathway. Its main contribution is to retain a real stride-4 detection level within a bidirectional P2-P5 pyramid, apply localized residual refinement specifically to the P2 feature, and couple this high-resolution representation with center-constrained, scale-bounded positive assignment. The novelty lies in treating fine-scale feature preservation and reliable positive-location supervision as a unified design problem, while maintaining a single-forward inference pipeline without crop proposal or super-resolution stages. The experimental section is relatively comprehensive, covering VisDrone, UAVDT, and UAVVaste with locked test splits, multi-seed evaluation, full-factorial ablations, sensitivity studies, and efficiency analysis.

The mechanism of CPD-FCOS should be explained more directly. The current evidence relies mainly on AP changes. Please add analyses such as positive-sample distribution before/after CGA, P2 feature visualization, or size-binned recall to show why P2 refinement and CGA work together.
The baseline comparison needs tighter control. CPD-FCOS is reported over three seeds, while most baselines are single-run references with different recipes. Please repeat the strongest baselines or clearly separate them from controlled comparisons.
The cross-dataset conclusions should be moderated. The VisDrone results are convincing, but UAVDT and UAVVaste are less consistent. Please add per-class AP, recall/precision curves, and size-specific analysis to clarify where the method truly improves performance.
The final configuration needs stronger justification. Some sensitivity settings, such as r = 1.0 or wider regression ranges, appear better on VisDrone, while P2-only gives higher mAP on UAVDT. Please explain why the reported default was selected.
The efficiency discussion should be more cautious. Although the method keeps single-forward inference, its FLOPs and latency are much higher than several baselines. Please report end-to-end latency, post-processing cost, and, if possible, edge-device results.
Figures 1-3 should be redesigned. The architecture and assignment figures contain small text and crowded visual elements, while Figure 3 overuses space for a simple residual block. Please use clearer paths, larger labels, explicit strides, and key tensor dimensions.

Author Response

Dear reviewer,

Thank you for taking time to review our manuscript.

We studied your comments and revised our draft accordingly.

We also went through our manuscript and made a few corrections on the texts.

Hope that our revised draft will meet with your approval.

Best wishes,

Chaowen Xie, Cheng Zhang, Fei Meng, Shunbing Zhao, Wei Zhao, Sijun Dong and Hanfa Xing

Response to Reviewer 1 Comments

This manuscript proposes CPD-FCOS, a UAV small-object detector designed around a scale-isolated P2 pathway. Its main contribution is to retain a real stride-4 detection level within a bidirectional P2-P5 pyramid, apply localized residual refinement specifically to the P2 feature, and couple this high-resolution representation with center-constrained, scale-bounded positive assignment. The novelty lies in treating fine-scale feature preservation and reliable positive-location supervision as a unified design problem, while maintaining a single-forward inference pipeline without crop proposal or super-resolution stages. The experimental section is relatively comprehensive, covering VisDrone, UAVDT, and UAVVaste with locked test splits, multi-seed evaluation, full-factorial ablations, sensitivity studies, and efficiency analysis.

Point 1. The mechanism of CPD-FCOS should be explained more directly. The current evidence relies mainly on AP changes. Please add analyses such as positive-sample distribution before/after CGA, P2 feature visualization, or size-binned recall to show why P2 refinement and CGA work together.

Response 1: [author response]:

Thanks for your advice. A new Section 4.7, “Mechanism Analysis,” has been added. Following the reviewer’s suggestions, we supplemented the manuscript with one set of empirical measurements and corresponding figures for each of the three suggested directions. We fully agree with this comment. In the original manuscript, changes in AP were used as the sole evidence, which could not explain why the two components are complementary. The three newly added sets of measurements are all directly observed quantities, rather than explanations inferred retrospectively from AP.

(a) Positive-sample distribution (256 images from the VisDrone validation set): After introducing CGA, the total number of positive samples decreases from 525,975 to 232,373 (−55.8%). The median number of positive samples per small object decreases from 17 to 9, while the proportion falling within the boundary band ( > 0.6) decreases from 77.8% to 57.8%. In contrast, the proportion of small objects receiving no positive samples remains almost unchanged (1.17% → 1.27%). This directly demonstrates that CGA redistributes supervision rather than reducing supervision.

(b) P2 features: We attached a forward hook to the trained model to export the actual tensors. Here, we must faithfully report a result that is contrary to our original expectation: the residual magnitude reaches 0.92–0.95 times that of the base features, indicating a modification of a comparable magnitude rather than a small perturbation. Moreover, the mean residual magnitude inside ground-truth boxes is only 1.23 times that of the background, indicating limited target selectivity.

(c) Size-wise ablation: This experiment explains the significance of the observation in (b). For the smallest size range (< 16 px), adding P2 refinement alone increases recall from 0.626 to 0.682, while AP remains completely unchanged (0.1322 → 0.1322), indicating that the additional recall is offset by an equivalent increase in false positives. Adding CGA alone increases precision to 0.338 and AP to 0.146. Only when both components are present do the results reach a recall of 0.737, a precision of 0.349, and an AP of 0.156. Therefore, their complementarity has a clear interpretation: stride-4 provides candidate locations, while constrained assignment determines which locations are reliable.

[author action]:

What the assignment rule does to supervision. Figure 8 audits the positive set over 256 validation images. Center-constrained selection removes more than half of all positive locations (525,975 → 232,373) and halves the median count per small object (17 → 9), yet the fraction of small objects left with no positive at all barely moves (1.17% → 1.27%). The rule therefore redistributes supervision rather than withholding it: the share of positives lying in the outer band of their object, , drops from 77.8% to 57.8% for small objects and from 64.1% to 27.7% for large ones. The residual 57.8% is itself informative: the window is an absolute distance, so it constrains the smallest objects proportionally less than the largest ones, which is also why the detector is sensitive to r (Section 4.10).

What the P₂ branch adds. Figure 9 shows ||P₂||₂, ||P̃₂||₂ and the residual magnitude produced by the trained branch. The residual is not a small perturbation: its magnitude reaches 0.92–0.95 of the base feature. It is biased towards objects but far from exclusive to them, with mean magnitude inside ground-truth boxes only 1.23 times the background level. The branch supplies capacity broadly; it does not by itself decide where that capacity is useful.

Why the two are complementary. Figure 10 resolves the factorial variants by object size. On the smallest bin the P₂ branch alone raises recall from 0.626 to 0.682 but leaves AP unchanged at 0.132, with precision essentially flat — the additional detections are matched by additional false positives. Constrained assignment alone lifts precision to 0.338 and AP to 0.146. Only the combination reaches 0.737 recall, 0.349 precision and 0.156 AP. This is the mechanism behind the factorial result in Table 9: the stride-4 level supplies candidate locations, and the assignment rule decides which of them can become confident predictions. Neither effect is redundant with the other, and the gain from both shrinks monotonically with object size (+11.1 recall points below 16 pixels, +1.9 above 64).

Figure 8. Positive-sample geometry with and without center-constrained assignment, measured over 256 VisDrone validation images. (a) Median positives per object with the interquartile range. (b) Share of positives lying in the outer band of their object (). (c) Share of objects that receive no positive at all; the constrained rule preserves coverage while removing off-center supervision.

Figure 9. The residual branch, obtained by hooking the trained module. From left: input, ||P₂||₂, ||P̃₂||₂, and the magnitude of the added residual. Two images are shown; the statistics quoted in the text are measured over four. The residual is comparable in magnitude to the base feature and only mildly concentrated on objects (1.23×the background level inside ground-truth boxes).

Figure 10. Factorial variants resolved by object size on the VisDrone validation split. The branch alone buys recall without AP in the smallest bin; constrained assignment converts the added capacity into precision. Aggregate values of these four models reproduce Table 9 exactly.

(Please see 4.7. Mechanism Analysis)

Point 2. The baseline comparison needs tighter control. CPD-FCOS is reported over three seeds, while most baselines are single-run references with different recipes. Please repeat the strongest baselines or clearly separate them from controlled comparisons.

Response 2: [author response]:

Thank you for your suggestion. Both options proposed by the reviewer have now been implemented: the strongest baseline on each of the three datasets was retrained using the same three seeds as CPD-FCOS, and the manuscript and tables now strictly distinguish controlled evidence from system-level references.

We divide the experimental evidence into three levels and use the following three terms consistently in the table captions, main text, and discussion: controlled comparison (same codebase, same recipe, with only one factor changed)—this is the sole basis for all design conclusions in this paper; system-level reference (off-the-shelf implementations from different frameworks, with only the input size and evaluation protocol standardized)—this is used only to indicate the performance range and does not support component-level conclusions; and literature-reported value—this serves only as an external reference with protocol annotations and is not included in the ranking.

Multi-seed retraining of the baselines has been completed. For each dataset, the baseline with the highest validation mAP was retrained using exactly the same seeds as CPD-FCOS (42/123/456), and was evaluated on both the validation set and the locked test set:

Dataset	Baseline	Split	Three-seed mean ± std	Original single run
VisDrone	YOLOv11s	val	0.288 ± 0.004	0.288
VisDrone	YOLOv11s	test	0.223 ± 0.001	0.224
UAVVaste	YOLOv8s	val	0.482 ± 0.003	0.486
UAVVaste	YOLOv8s	test	0.517 ± 0.005	0.521
UAVDT	FCOS	val	0.224 ± 0.002	0.263
UAVDT	FCOS	test	0.167 ± 0.002	0.161

The two YOLO baselines cleanly confirm the original single-run results: their multi-seed means are nearly identical to the original values, showing that the original runs were not favorable samples. This is, in itself, the answer warranted by the reviewer’s comment.

The FCOS case must be explained separately, and we report the part of the conclusion that is unfavorable to us without alteration. The original script had no random-seed control, which we first added. After doing so, we found that extending the experiment to all three seeds caused all runs to diverge because a per-GPU batch size of 1 made SGD unstable. We then conducted a 15-run recipe sweep (three learning rates × two batch sizes × gradient clipping on/off), and selected the configuration according to the criterion that all three seeds must remain stable and the validation mAP must be the highest. The selected configuration uses the original learning rate plus gradient clipping; the latter has always been used in our method but was absent from the original baseline, making the previous setup unequal.

The result is that no seeded configuration can reproduce 0.263; the best reproducible mean is 0.224 ± 0.002. However, on the locked test set, the same checkpoint lies at the low end of its seed distribution (0.161 vs. a three-seed mean of 0.167). In other words, this single run is high on the validation set but low on the test set, which is precisely the instability that repeated-baseline experiments are intended to reveal.

Accordingly, we updated Tables 4 and 5 and retained the original values in the main text so that readers can see the differences rather than having them silently replaced. The net effect of the update is mixed for our method: on the UAVDT test set, FCOS now becomes the overall leader (previously, we held a slight lead at 0.163 vs. 0.161; now we trail at 0.163 vs. 0.167), while our lead margins on VisDrone and UAVVaste increase slightly. We report this change exactly as observed.

[author action]:

Three kinds of evidence appear in this section and are kept separate throughout. Controlled comparisons share one codebase, optimizer, schedule, data pipeline and evaluation protocol, and vary a single factor; Sections 4.7 to 4.10 are of this kind and are the sole basis for the design claims. System-level references are independent implementations kept at their own official recipes with only the input size and evaluation protocol unified; Table 5 is of this kind and locates the method in a performance range without supporting component-level conclusions. Reported values are taken from other papers and used only as protocol-annotated context, never for ranking.

Table 5 uses the three-seed CPD-FCOS mean as the primary value; the competing detectors are single-run references, and CPD-FCOS stability is reported separately in Table 16. The results again separate the datasets rather than producing one uniform ranking. On VisDrone, CPD-FCOS reaches 0.326 mAP, 3.8 points above YOLOv11s, and obtains the highest APₛ in the table. This is precisely the regime targeted by the pathway: dense multi-class scenes combine tiny instances, class ambiguity, and background clutter, making both fine detail and reliable positive locations valuable. On UAVDT, FCOS remains stronger on APₛ despite a similar overall mAP, suggesting that vehicle-only transfer rewards a different balance between localization recall and precision. The FCOS entry deserves a comment. The single run reported previously reached 0.263 mAP, higher than any of fifteen seeded repetitions across three learning rates, two batch sizes and gradient clipping on or off; the best reproducible configuration averages 0.224 ± 0.002. We report the reproducible mean and record the earlier value so the discrepancy is visible rather than silently corrected. The same checkpoint sits at the low end of its seed distribution on the locked test split (0.161 against 0.167), so it was favourable on validation and unfavourable on test—the instability that repeating a baseline is meant to expose. UAVVaste offers a complementary case in which CPD-FCOS remains competitive overall, but the small-object subset is too limited to support a broad small-object claim.

Table 5. Validation-set comparison with mainstream detectors under the shared evaluation protocol (original resolution, mAP / APₛ). CPD-FCOS reports the three-seed mean; baseline entries are single runs. Every method is trained and evaluated at the same input size. The strongest baseline of each dataset was retrained with the same three seeds as CPD-FCOS and is reported as mean±population standard deviation; the remaining entries are single runs. The last row is not part of the comparison: it retrains YOLOv8s under the full Ultralytics default to quantify what the shared 1024 setting is worth to a baseline.

Method	Input	VisDrone		UAVDT		UAVVaste
Method	Input	mAP	AP_S	mAP	AP_S	mAP	AP_S
Faster R-CNN	1024/1707	0.256	0.181	0.215	0.188	0.469	0.145
RetinaNet	1024/1707	0.191	0.106	0.224	0.273	0.454	0.103
FCOS	1024/1707	0.231	0.148	0.224 ± 0.002	0.282 ± 0.030	0.456	0.130
Faster R-CNN v2	1024/1707	0.241	0.164	0.224	0.190	0.451	0.124
RetinaNet v2	1024/1707	0.194	0.105	0.214	0.197	0.450	0.106
Faster R-CNN (MobileNet)	1024/1707	0.149	0.064	0.180	0.160	0.336	0.017
YOLOv8s	1024²	0.286	0.194	0.225	0.194	0.482 ± 0.003	0.166 ± 0.014
YOLOv11s	1024²	0.288 ± 0.004	0.193 ± 0.004	0.195	0.173	0.477	0.209
CPD-FCOS (mean)	1024²	0.326	0.251	0.261	0.287	0.488	0.196
YOLOv8s (Ultralytics default)	640²	0.211	0.112	–	–	–	–

(Please see 4.5. Validation Comparison with Mainstream Detectors)

Point 3. The cross-dataset conclusions should be moderated. The VisDrone results are convincing, but UAVDT and UAVVaste are less consistent. Please add per-class AP, recall/precision curves, and size-specific analysis to clarify where the method truly improves performance.

Response 3: [author response]:

Thank you for your insights. All three pieces of evidence have now been added, and the conclusions throughout the manuscript have been tightened accordingly. We added a per-class AP table, a size-wise table, and PR curves. These results provide a much clearer picture of the applicability boundaries than mAP alone. Two of the findings also place limitations on our own claims, which we report faithfully:

(1) The advantage is scale-specific and reverses for the largest objects. On VisDrone, the recall advantage increases monotonically from +6.8 points in the ≥ 64 px bin to +35.6 points in the < 16 px bin; however, in the ≥ 64 px bin, AP instead decreases by 2.1 points. This indicates that the gain is not a universal effect of a “stronger model,” while also clearly identifying the range in which the proposed method does not have an advantage.

(2) On UAVDT, the difference is in the operating point rather than a simple superiority relationship. FCOS achieves higher recall in every size bin, whereas our method achieves higher precision and AP in the smallest and largest bins. The original manuscript could only speculate that the two methods had “different operating points”; this is now a directly verifiable observation. FCOS’s mAP advantage mainly comes from the medium-size bin and the bus class, rather than from small-object capability.

[author action]:

Aggregate mAP is too coarse to delimit where the method applies, so Tables 7 and 8 resolve the VisDrone comparison by class and by object size. CPD-FCOS leads the validation-selected YOLOv11s reference on all ten classes, and the margin tracks how small and how crowded a class typically is: it is largest for van (+7.1), bus (+5.8), people (+4.9) and pedestrian (+4.3), and smallest for awning-tricycle (+0.9) and motor (+2.0).

The size-resolved view is more informative still. Recall at IoU = 0.5 improves by 35.6 points on objects below 16 pixels, by 19.1 points between 16 and 32, by 8.9 points between 32 and 64, and by 6.8 points above 64; average precision follows the same ordering and reverses on the largest bin, where the reference is 2.1 points better. The advantage is therefore scale-specific rather than a general capacity effect, which is what a scale-isolated pathway should produce, and it also marks the regime where the method offers nothing.

UAVDT separates the two detectors differently, turning what was previously a conjecture into an observation. Against FCOS, CPD-FCOS has lower recall in every size bin yet higher precision and AP in the smallest (0.386 versus 0.299 AP) and largest (0.288 versus 0.251) bins; per class it leads only on truck and trails on car and bus. The two occupy different operating points—one recall-oriented, one precision-oriented—and the FCOS mAP advantage comes from the middle size range rather than from small-object capability. Deployments that pay mainly for missed detections should prefer the FCOS-style operating point; those that pay for false positives should prefer this one.

Figure 4. Precision-recall curves at IoU = 0.5, averaged over classes, on the complete validation split of each dataset under the original-resolution protocol. The reference detector is the highest validation-mAP baseline for that dataset.

Table 7. Per-class AP on the VisDrone validation split at original resolution, against the validation-selected reference detector.

Method	pedes.	people	bicycle	car	van	truck	tricy.	awn.-tri.	bus	motor
YOLOv11s	0.279	0.171	0.131	0.603	0.338	0.305	0.206	0.112	0.457	0.276
CPD-FCOS	0.322	0.221	0.170	0.631	0.408	0.340	0.229	0.121	0.516	0.296

Table 8. VisDrone validation performance resolved by object size ( in pixels). Recall is measured at IoU = 0.5.

	Recall (CPD-FCOS)	Recall (YOLOv11s)	AP (CPD-FCOS)	AP (YOLOv11s)
< 16	0.740	0.384	0.157	0.098
16–32	0.838	0.646	0.313	0.252
32–64	0.883	0.794	0.408	0.403
≥ 64	0.921	0.853	0.503	0.524

(Please see 4.6. Remote-Sensing Scenario Analysis)

Point 4. The final configuration needs stronger justification. Some sensitivity settings, such as r = 1.0 or wider regression ranges, appear better on VisDrone, while P2-only gives higher mAP on UAVDT. Please explain why the reported default was selected.

Response 4: [author response]:

Thank you for your suggestion. We added explicit selection criteria and re-evaluated the choice of r. The conclusion is that the phenomenon pointed out by the reviewer is real (the original manuscript indeed provided insufficient justification), but the additional experiments show that this advantage does not transfer across datasets. Therefore, according to the criteria, we retain r=1.5, and include r=1.0 in the main text as an optional configuration for dense multi-class scenarios.

The original manuscript only stated the observed phenomenon without providing explicit selection criteria, which was an oversight on our part. The four newly introduced criteria, in priority order, are: (i) selection is based only on the validation set, and the locked test set is never used for selection; (ii) one shared default value is used across all three datasets, so that dataset-specific behavior is not disguised as a methodological advantage; (iii) when a difference falls within multi-seed variation, the original FCOS default is retained; and (iv) when mAP and AP_S conflict, AP_S takes priority, while the sacrificed mAP is reported explicitly.

Following criterion (iii), we first reran the two settings on VisDrone using three seeds. The difference is 0.75 mAP points, while the within-group standard deviations are only 0.0003 and 0.0021, respectively—about six times smaller than the observed gap. The phenomenon identified by the reviewer is therefore real, and the original manuscript was indeed insufficiently justified in retaining r=1.5 based on a single run.

However, criterion (ii) requires the default value to be applicable across all three datasets. We therefore further tested whether this advantage transfers: under r=1.0, we retrained the complete main configuration with three seeds on each of the three datasets, and evaluated it on both the validation split and the locked test split (9 training runs and 18 evaluations in total). The result is that the advantage does not transfer:

Dataset	Split	r=1.5 mAP	r=1.0 mAP	Δ
VisDrone	val	0.326	0.332	+0.56
UAVDT	val	0.261	0.261	−0.00
UAVVaste	val	0.488	0.488	−0.02
VisDrone	test	0.244	0.248	+0.43
UAVDT	test	0.163	0.156	−0.74
UAVVaste	test	0.528	0.522	−0.63
Six-case average				−0.07

The gain on VisDrone is stable on both splits, but UAVDT and UAVVaste are tied on the validation split and decrease by 0.74 and 0.63 points, respectively, on the test split; the six-case average is −0.07 mAP. Making a value that is beneficial only on the densest dataset, while being neutral to slightly negative on the others, the universal default would amount to disguising VisDrone-specific behavior as a general property of the method. This is precisely what criterion (ii) is intended to prevent. Therefore, we retain r=1.5, while explicitly stating in the main text that r=1.0 performs better in dense multi-class scenarios and can be used as a documented scenario-dependent option.

We believe this response is more informative than simply “changing to r=1.0.” It turns the reviewer’s concern into a transferable negative conclusion—the optimum from a single-dataset hyperparameter sweep should not be adopted directly as the default value—and this point has also been added to the Discussion.

Additional note (for transparency): to perform this check, the locked test set was used for a second time during the revision. The configuration was selected entirely from validation-set evidence; the test set did not participate in selection, and the configuration ultimately did not become the default. We explicitly record this additional evaluation in Section 4.3 and do not understate the number of times the test set was used.

Regarding the statement that “the P2-only variant has higher mAP on UAVDT”: this falls under criterion (iv). That variant achieves an mAP of 0.2545, higher than the 0.2466 of the full pathway, but its AP_S is 0.2570, which is 7.0 points lower than the 0.3273 of the full pathway. Since this work focuses on small objects, we retain the full pathway and explicitly state in the main text that if overall mAP is the deployment objective, the P2-only configuration should be selected, rather than concealing this result.

[author action]:

Configurations are selected under four fixed rules, applied in order. (i) Selection uses validation data only; the locked test splits are never consulted. (ii) A single default setting is shared by all three datasets, so that dataset-specific tuning cannot be mistaken for a property of the method. (iii) When a difference falls inside the multi-seed dispersion, the original FCOS default is retained rather than the nominally better value. (iv) When mAP and APₛ disagree, APₛ decides, because the study targets small objects, and the sacrificed mAP is reported explicitly. Section 4.10 applies rule (iii) to the center radius.

FCOS is used as the research platform rather than as the strongest available detector. Studying whether representation and supervision must be designed jointly requires a platform whose assignment rule can be switched on and off cleanly. In FCOS that rule is three analytic conditions—an in-box test, a center radius and a level range—each ablatable without disturbing the others, and the level–range mechanism extends naturally to a stride-4 level. Modern YOLO detectors couple task-aligned assignment to mosaic augmentation, exponential moving averages, distribution focal loss and a tuned loss schedule, so a factorial ablation there cannot separate the assignment rule from the training recipe. YOLO is therefore evaluated as a comparison system in Table 5, not used as the substrate for the ablations. (Please see 4.2. Implementation Details)

The depth sweep places the two-block reference near a practical optimum: one and four blocks remain close in mAP, but both lose . The center-radius sweep provides the sharper explanation. Tightening the center neighborhood to raises VisDrone mAP to 0.3342, whereas widening it to lowers both mAP and . The result is consistent with the idea that additional stride-4 locations are useful only when ambiguous off-center positives are filtered. A single run cannot separate a real effect from initialization noise, so we repeated both settings with three seeds under the same recipe (Table 12). On VisDrone the effect is real: gains 0.75 mAP and 0.68 against a within-setting dispersion of 0.0003 and 0.0021, roughly six times the run-to-run spread. The direction agrees with the assignment audit of Section 4.7: because is an absolute distance, corresponds to ±6 pixels at , which is permissive for objects only a dozen pixels across.

That alone would argue for changing the default, so we tested whether it transfers. Table 13 retrains the full main configuration at on all three datasets with three seeds each, on both splits. It does not transfer: the VisDrone gain persists, but UAVDT and UAVVaste are unchanged on validation and lose ground on test, and the six-combination mean is -0.07 mAP. Selection rule (ii) of Section 4.2 forbids adopting a value that is favourable on one dataset and neutral-to-harmful on the others, since that would encode a VisDrone-specific preference into a setting presented as general. We therefore retain and report as a documented option for dense multi-class scenes. (Please see 4.10. Sensitivity to Center Radius, P2 Depth, and Regression Range)

Table 12. Center radius under three random seeds (42, 123, 456), VisDrone validation split at original
resolution, factorial recipe. Entries are mean±population standard deviation.

Setting	mAP	AP_S	Individual runs (mAP)
r = 1.5	0.3254 ± 0.0021	0.2469 ± 0.0047	0.3280 / 0.3252 / 0.3229
r = 1.0	0.3329 ± 0.0003	0.2537 ± 0.0002	0.3333 / 0.3327 / 0.3327

Point 5. The efficiency discussion should be more cautious. Although the method keeps single-forward inference, its FLOPs and latency are much higher than several baselines. Please report end-to-end latency, post-processing cost, and, if possible, edge-device results.

Response 5: [author response]:

Thank you very much for your advice. We added an end-to-end five-stage latency table, measured on a completely idle GPU using 50 real validation images. Real images were used because the NMS overhead depends on the number of candidate boxes that survive thresholding, whereas synthetic inputs would underestimate this cost. The end-to-end latency is 49.76 ms (20.1 FPS), which is higher than the 46.4 ms reported in the original manuscript for forward inference only.

Here, we need to correct one of our own previous judgments. We originally assumed that stride-4 would quadruple the candidate grid and make post-processing the bottleneck. However, the measurements show that this is not the case—decoding and NMS account for only 5.9% of the end-to-end latency. The actual bottleneck lies in the shared detection head: it evaluates four convolutional towers over 87,040 locations, resulting in a cost 3.50× that of and accounting for 43% of the end-to-end latency by itself. This finding directly identifies the appropriate direction for future efficiency optimization.

For edge devices, we do not have an onboard hardware platform and therefore did not conduct empirical measurements. We also do not provide theoretical estimates; instead, we explicitly state this point as a limitation.

[author action]:

The breakdown corrects an expectation we held when designing the study. A stride-4 level enlarges the candidate grid fourfold, so we expected decoding and NMS to dominate; they grow, but account for only 5.9% of end-to-end latency. The cost falls almost entirely on the shared head, which evaluates four convolutional towers at 87,040 locations, is 3.50× slower than its counterpart and alone accounts for 43% of the total. Efficiency work should therefore sparsify head computation at high-resolution levels—as sparse-query detectors [8] do—rather than optimize post-processing. (Please see 4.10. Sensitivity to Center Radius, P2 Depth, and Regression Range)

Several limitations remain. The strongest baseline of each dataset is now a three-seed mean, but the remaining comparison detectors are still single runs, so Table 5 should be read as a system-level reference rather than a statistical test; the design claims rest on the controlled experiments instead, where every factor except one is held fixed. The current input pipeline uses square resizing; an aspect-ratio-preserving pipeline should be tested before deployment in applications where geometric distortion is critical. The UAVDT test result shows appreciable inter-seed variance, and the small UAVVaste test split limits interpretation of sub-percentage differences. The primary VisDrone conversion excludes ignored annotations but does not suppress detections overlapping ignored regions, so the locked COCO-style values are not official challenge scores. The post-hoc official-tool validation audit preserves the CPD-FCOS-YOLOv11s ordering, but it neither replaces a locked official-tool test nor supplies area-partitioned AP. Finally, all timings in this paper are desktop-GPU measurements. We did not have access to an embedded airborne platform, so onboard latency and energy consumption remain unmeasured and are not estimated here; they must be characterized before deployment. The end-to-end breakdown does, however, indicate where such an effort should start, since the shared head at the stride-4 level rather than post-processing dominates the cost. (Please see 5.2. Deployment Boundaries and Residual Risks)

Table 17. End-to-end latency by stage (single 1024 × 1024 image, batch size 1, idle RTX 4090 D,
median over 50 real validation images). The P₃–P₅ column is the pyramid ablation of Table 10.

Stage	CPD-FCOS (ms)	P₃–P₅ (ms)	Ratio
Preprocessing	2.28	2.02	1.13×
Backbone + neck	22.73	12.24	1.86×
Detection head	21.53	6.15	3.50×
Decoding + NMS	2.93	1.76	1.67×
Remap to original resolution	0.16	0.11	1.45×
End-to-end	49.76 (20.1 FPS)	22.34 (44.8 FPS)	2.23×

Point 6. Figures 1-3 should be redesigned. The architecture and assignment figures contain small text and crowded visual elements, while Figure 3 overuses space for a simple residual block. Please use clearer paths, larger labels, explicit strides, and key tensor dimensions.

Response 6: [author response]:

Thank you for your valuable feedback on our manuscript. All three figures have been redrawn, and one of them was removed in accordance with the reviewer’s suggestion. Implemented item by item:

Original Figure 1 (architecture diagram) → New Figure 2: Redrawn as a vector graphic using TikZ, with a strict left-to-right layout. The four branches are aligned by stride to eliminate visual crowding. Each feature block is directly annotated with its tensor size (: ×96, : ×256, : ×256, : ×256, : ×256, for a input). The top-down, bottom-up, and supervision paths use three different line styles with an accompanying legend. The shared detection head is drawn only once, with converging arrows indicating that it is shared across all four scales. The disclaimer in the original figure caption stating that the “connection heights are different” has therefore been removed.

Original Figure 2 (assignment illustration) → New Figure 3: Replaced with a rendering based on real data. Panels (a) and (b) use the same real VisDrone image patch as the background and overlay the actual positive-sample locations (531 → 303). The center window of 2 pixels is drawn according to the true scale. A new panel (c) provides a histogram of the measured values. The figure has thus been upgraded from a “schematic illustration” to a “verifiable observation.”

Original Figure 3 (residual module) → Removed: The reviewer noted that it occupied too much page space while conveying relatively little information, and we agree. The module has now been embedded as a submodule within the new Figure 2, and the area-weighted loss component that is unrelated to the final method has also been removed. The numbering of subsequent figures has been updated accordingly.

[author action]:

Figure 2. Overall architecture of CPD-FCOS, with tensor shapes given for a 1024 × 1024 input. Each row corresponds to one pyramid level, labelled by its stride on the left. Blue solid arrows are the top-down FPN path, green dashed arrows the bottom-up PAN path, and the red dotted arrow the center-constrained assignment, which is active only during training. The residual detail-enhancement branch is shown inline at the stride-4 row. All four levels pass through the same shared head, drawn once with converging arrows.

Figure 3. Center-constrained assignment measured on a real VisDrone crop. (a) With the in-box constraint alone, 531 locations become positive and many of them sit on object borders. (b) Adding the centre neighbourhood and the level regression range leaves 303 locations; the dashed square is the pixel center window at , drawn to scale. (c) Distribution of the number of positives assigned to each small object over 256 validation images: the in-box rule spreads to more than 40 positives per object, whereas the constrained rule concentrates the mass near the object center. Multi-object competition is resolved by minimum area.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

In the abstract, why was CPD-FCOS designed this way, and how does this design relate to the existing issues? This part needs more emphasis.
For the existing issues, the author should include a figure showing that these problems actually exist in reality, rather than just talking about them. You can refer to relevant SPG-OD hyperspectral papers and use the first figure as a motivation figure.
Why choose FCOS as the baseline instead of other YOLO versions?
Almost all images in the paper are AI-generated. The author needs to seriously consider this.
5.For small object issues, modeling combined spectral features is a pretty good approach. I suggest the author check out and discuss works like Sliding dual-window-inspired reconstruction network and Hyperspectral Remote Sensing Object Detection via Cross Domain Learning from Visible Images.

Author Response

Dear reviewer,

Thank you for taking time to review our manuscript.

We studied your comments and revised our draft accordingly.

We also went through our manuscript and made a few corrections on the texts.

Hope that our revised draft will meet with your approval.

Best wishes,

Chaowen Xie, Cheng Zhang, Fei Meng, Shunbing Zhao, Wei Zhao, Sijun Dong and Hanfa Xing

Response to Reviewer 2 Comments

Point 1. In the abstract, why was CPD-FCOS designed this way, and how does this design relate to the existing issues? This part needs more emphasis.

Response 1: [author response]:

Thanks for your advice. The entire abstract has been rewritten. The original abstract first described the observed phenomena and then listed the proposed components, without establishing a clear “limitation → remedy” correspondence. The revised abstract opens with two specific limitations, each supported by quantitative evidence from our data rather than general statements. Each limitation is then directly linked to the corresponding design decision, followed by an explicit statement of the central argument that the two components are coupled. Finally, the abstract reports the quantitative results and clearly defines the applicability boundaries of the proposed method.

[author action]:

Small objects in UAV imagery fail for two coupled reasons. Repeated downsampling destroys their evidence—60.5% of VisDrone instances are COCO-small and the median object spans 26 pixels, so a typical target covers fewer than four cells at stride 8—and the in-box assignment rule then places most of their positive locations on object borders, where supervision is unreliable. The two reinforce each other: a finer level creates more candidate locations, but they help only if the assignment rule can select the reliable ones. We therefore design representation and supervision together in CPD-FCOS (Center-constrained P2 Detail-enhanced FCOS): a real stride-4 level in a bidirectional pyramid, localized residual refinement at that level, and center-constrained, scale-bounded positive selection. Controlled experiments separate the two. On VisDrone the stride-4 level supplies +2.98 mAP at 2.05× the end-to-end latency, while the refinement branch adds +0.55 mAP for 2.8% more parameters. Resolved by object size, the branch alone raises small-object recall but leaves AP unchanged; only constrained assignment converts that capacity into precision. The advantage is scale-specific, growing as objects shrink and reversing on the largest ones, and it is strongest in dense multi-class scenes—on vehicle-only and medium-object benchmarks the pathway shifts the operating point rather than dominating. The result is a single-forward, reproducible reference design with an explicitly measured accuracy–efficiency trade-off. (Please see Abstract)

Point 2. For the existing issues, the author should include a figure showing that these problems actually exist in reality, rather than just talking about them. You can refer to relevant SPG-OD hyperspectral papers and use the first figure as a motivation figure.

Response 2: [author response]:

Thanks for your advice. A new Figure 1 (research motivation figure) has been added and placed in the Introduction.

To avoid the circular argument of “using a schematic illustration to prove that the problem exists,” all four panels of the figure are generated entirely from real data and actual model outputs. The displayed example is automatically selected by a script rather than manually chosen as a favorable sample. Specifically, the script scans the first 80 images in the validation set and selects the region with the highest density of small objects. The selection criterion is implemented in code and is fully reproducible. The selected region contains 43 ground-truth objects.

The panels are organized as follows: (a) object-size distribution, where 60.5% of the objects are COCO small objects, the median side length is 26 pixels, and each stride is annotated on the horizontal axis with its corresponding scale; (b) the same region represented at (56×56 cells), where individual pedestrians remain distinguishable, and at (14×14 cells), where they have already merged into compact clusters; (c) the actual positive samples under the two assignment rules (531 → 303); and (d) detection results under a unified confidence threshold of 0.3.

Following the reviewer’s suggestion, we adopted a “problem evidence → consequence” organization for the figure. However, all visual materials are derived from the data and models used in this work, with no content taken from the cited paper; therefore, no citation is included.

[author action]:

Figure 1. Why fine-scale representation and positive-sample quality have to be designed together. (a) Object-size distribution of the VisDrone training set: 60.5% of instances fall below the COCO small-object threshold and the median object is 26 pixels across, so a typical target spans fewer than four cells at stride 8. (b) Responses of the trained pyramid on one 224×224 crop: individual pedestrians remain separable on the stride-4 level (56×56 cells) but merge into a few blobs on the stride-16 level (14×14 cells). (c) Positive locations selected for the same crop: the in-box rule yields 531 candidates, many of them on object borders, while center-constrained selection keeps 303. (d) The consequence at the output, at a common score threshold of 0.3. The crop was chosen automatically as the densest tiny-object window of the validation image with the most tiny instances, not selected by hand; all panels are rendered from real data and trained weights.

Point 3. Why choose FCOS as the baseline instead of other YOLO versions?

Response 3: [author response]:

Thank you for your question. The key distinction is that FCOS serves as the controlled experimental platform in this study, whereas YOLO serves as the performance reference; the two play different roles. The hypothesis examined in this work is that “representation and supervision must be jointly designed,” which requires a platform on which the assignment rule can be cleanly switched on and off. FCOS assignment is defined by three explicit conditions—inside-box testing, center radius, and level range—which can be ablated individually without interfering with one another. Moreover, its level-range mechanism naturally supports the addition of a stride-4 level. In contrast, the TaskAlignedAssigner in modern YOLO models is tightly coupled with mosaic augmentation, EMA, DFL, and an entire suite of loss-scheduling strategies. Factorial ablation on such a framework therefore cannot cleanly separate the effect of the assignment rule from that of the training techniques. YOLO was not excluded: it appears as a comparison method in Table 5, and YOLOv11s, the baseline with the highest validation mAP on VisDrone, was selected as the locked reference for test-set evaluation.

[author action]:

FCOS is used as the research platform rather than as the strongest available detector. Studying whether representation and supervision must be designed jointly requires a platform whose assignment rule can be switched on and off cleanly. In FCOS that rule is three analytic conditions—an in-box test, a center radius and a level range—each ablatable without disturbing the others, and the level-range mechanism extends naturally to a stride-4 level. Modern YOLO detectors couple task-aligned assignment to mosaic augmentation, exponential moving averages, distribution focal loss and a tuned loss schedule, so a factorial ablation there cannot separate the assignment rule from the training recipe. YOLO is therefore evaluated as a comparison system in Table 5, not used as the substrate for the ablations. (Please see 4.2. Implementation Details)

Point 4. Almost all images in the paper are AI-generated. The author needs to seriously consider this.

Response 4: [author response]:

Thank you for your valuable comments. All schematic figures have been redrawn, and the sources of the figures have been additionally clarified in the AI-use statement. We take this issue very seriously and have addressed it as follows:

(1) All figures were redrawn. The three schematic figures in the original manuscript indeed had the problems identified by the reviewer. In the revised manuscript, the architecture diagram has been manually redrawn and replaced; the assignment illustration has been replaced with a rendering based on real data; and the residual-module figure has been removed entirely.

(2) All remaining figures are generated directly by code. The detection-result comparison figures are rendered by publicly available scripts using images from the real datasets and outputs from the actual models. A provenance file is also provided, recording the absolute image paths, dataset indices, confidence thresholds, and the SHA-256 hash of each checkpoint. The indices of the displayed samples were fixed before manual inspection. All analysis figures newly added in this revision are likewise generated by scripts directly from real data.

(3) The declaration has been made more explicit.

[author action]:

During the preparation of this manuscript, the authors used OpenAI Codex (accessed 25 July 2026) for the purpose of improving the language clarity and readability of the text and assisting with code review. The AI tools were not used to generate research content, analyze data, draw conclusions, or produce any part of the scientific work. After using this tool, the authors reviewed and edited the content as necessary and take full responsibility for the content of the publication. (Please see Use of Artificial Intelligence)

Point 5. For small object issues, modeling combined spectral features is a pretty good approach. I suggest the author check out and discuss works like Sliding dual-window-inspired reconstruction network and Hyperspectral Remote Sensing Object Detection via Cross Domain Learning from Visible Images.

Response 5: [author response]:

Thanks for your advice. Two paragraphs have been added at the end of Section 2.1, citing the two papers recommended by the reviewer and explicitly connecting them to the specific measurements reported in this work rather than mentioning them only in general terms.

We carefully studied these two papers and found that both have substantive connections to our work. Therefore, instead of limiting the discussion to a courtesy statement such as “spectral methods represent another possible direction,” we added two paragraphs that establish concrete correspondences with our method and results.

(1) DirectNet is structurally analogous to the assignment rule used in this work. The paper points out that hyperspectral anomaly-detection networks based on reconstruction error may fit both anomalies and background simultaneously, resulting in similarly small reconstruction errors for both and making them difficult to distinguish. Its solution is to “remove” the central region from the receptive field and predict the central pixel using only information from the surrounding window. This forces the reconstruction toward the background distribution and thereby amplifies the reconstruction error at anomalous locations. The key point is that its mechanism does not increase model capacity; instead, it deliberately restricts which evidence the model is allowed to use. This is conceptually analogous to the center-constrained assignment adopted in our work: rather than adding more parameters for small objects, we exclude unreliable boundary locations from supervision. We explicitly identify this structural correspondence in the revised manuscript.

(2) The residual observations reported in VHCDN provide an external reference for the negative result obtained in our study. To address the scarcity of hyperspectral annotations, that work performs cross-domain transfer from visible-light remote-sensing imagery and observes that the reconstruction residuals in the two domains exhibit similar background responses while emphasizing foreground regions. Based on this observation, it designs a residual-extraction module together with a spectral-uncertainty head. This provides a useful contrast to the mechanism analysis in our work: our measured residual branch shows only a 1.23× preference for target regions, indicating limited selectivity. This explains why the branch must rely on constrained supervision to become effective. VHCDN demonstrates that a residual module specifically designed to emphasize foreground regions can achieve substantially stronger selectivity. This therefore provides a concrete direction for improving the residual branch in our method, rather than serving as only a generic suggestion for future work.

We also retain our original argument: spectral methods improve separability along the channel dimension, whereas our method operates in the spatial dimension. The two are therefore orthogonal and, in principle, can be combined, since the processing pipeline proposed in this work does not depend on the semantic meaning of the input channels. When an object occupies only a few pixels, spectral separability may be more effective than further increasing spatial resolution. The annotation-scarcity problem addressed by VHCDN also exists in UAV imagery. At the same time, we state explicitly that all three datasets used in this study contain RGB imagery only; therefore, neither of these two directions has been experimentally validated in the present work.

[author action]:

A complementary line of work attacks the same problem from the spectral side, and two of its ideas bear on the design studied here. DirectNet [24] notes that reconstruction-based anomaly detectors fit anomalies as readily as background; it therefore erases the centre block from the receptive field and predicts each pixel from an outer window only, forcing the reconstruction towards the background distribution and amplifying the error at anomalous targets. The mechanism is not extra capacity but a deliberate restriction on the evidence the model may use—the same kind of decision as the center-constrained assignment of Section 3.3. VHCDN [25] transfers object priors from abundant visible-light imagery to label-scarce hyperspectral scenes, and reports that reconstructed residual representations suppress background and emphasise foreground in both domains. (Please see 2.1. UAV Small-Object Detection)

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The authors have proposed CPD-FCOS, an anchor-free single-stage UAV detector built from a ConvNeXt-Tiny backbone. The method is evaluated on VisDrone, UAVDT and UAVVaste test benchmarks. The results have been provided after extensively careful experimental setup to prevent label leakage/overfitting.

Please explain how the third claimed contribution ("centerness score calibration") is different from standard FCOS? According to Table 1, the seem identical or at least similar.
The manuscript does not compare the proposed method against the sota works mentioned in Section 2.2. e.g. HRFPN [9], "Locate then Calibrate" [28] and QueryDet [8] etc. The recent and strongest published results on VisDrone results are not acknowledged at all. The published VisDrone-val results e.g. AD-Det [20] seem to be considerably stronger than Table 6 implies.
The ablation study for stride-4 level is missing. This is the most computationally expensive part of the proposed method and thus should be justified through experimentation results.
Similarly, no experiment in the manuscript compares a P2-P5 pyramid against a P3-P5 pyramid under an otherwise identical backbone, neck, head, recipe, and seed count. This could be added to Table 8 ablation.
The comparison given in Table 5 does not seem fair. CPD-FCOS uses 1024 x 1024 input resolution. YOLOv8s/YOLOv11s with Ultralytics default is, however, 640 x 640. This gives an unfair advantage to the proposed method at the very beginning of the pipeline.
Why was r = 1.5 retained when Table 9 shows r = 1.0 superior on both VisDrone metrics?

Author Response

Dear reviewer,

Thank you for taking time to review our manuscript.

We studied your comments and revised our draft accordingly.

We also went through our manuscript and made a few corrections on the texts.

Hope that our revised draft will meet with your approval.

Best wishes,

Chaowen Xie, Cheng Zhang, Fei Meng, Shunbing Zhao, Wei Zhao, Sijun Dong and Hanfa Xing

Response to Reviewer 3 Comments

Point 1. Please explain how the third claimed contribution ("centerness score calibration") is different from standard FCOS? According to Table 1, the seem identical or at least similar.

Response 1: [author response]:

We appreciate your suggestion. We agree that the claim regarding the novelty of the centerness score calibration was not appropriate, and we have therefore withdrawn this innovation claim.

The mechanism for score calibration in our method is exactly the same as that in the original FCOS, where the classification probability is multiplied by the predicted center-ness during inference to obtain the final score used for ranking and NMS. We did not modify this mechanism, and it was therefore inappropriate to present it as an independent contribution. We have revised the manuscript accordingly.

The following changes have been made:

(1) Introduction: The third contribution has been rewritten to remove this claim. It now focuses on our actual work: configuring the existing FCOS primitives into a P2–P5-based architecture and directly measuring their complementarity, rather than inferring it indirectly from the aggregated AP. We also explicitly state at the end of this contribution that we do not claim novelty for the score calibration mechanism.

(2) Table 1: The row labeled “Score calibration” has been changed to “Unchanged from FCOS”. We have also added a table note clarifying that the last two rows are included only to provide a complete description of the inference pipeline and do not represent modifications introduced by our work.

(3) Abstract and Conclusion: The corresponding statements presenting score calibration as a contribution have been removed.

We sincerely thank the reviewer for prompting us to revise our contribution statements so that they accurately reflect the actual novelty of our work.

[author action]:

We configure standard FCOS primitives—in-box testing, center sampling, level ranges and minimum-area conflict resolution—for a pyramid, and quantify the resulting complementarity directly rather than inferring it from aggregate AP. Re-solved by object size, the refinement branch alone raises small-object recall by 5.6points while leaving AP unchanged, whereas the two together also raise precision by5.4 points. We make no claim of novelty for centerness-based score calibration, which is unchanged from FCOS. (Please see Introduction)

Table 1. Structural distinction between standard FCOS and CPD-FCOS.

Aspect	Standard FCOS	CPD-FCOS
Feature levels	Typically , strides 8–128	Real , strides 4–32
Cross-scale fusion	Top-down FPN	Bidirectional FPN/PAN
Assignment	In-box candidates with center sampling and level ranges	Same primitives, configured for with compact overlapping ranges
Fine-level branch	No -specific refinement	Two-block residual refinement only at
Score calibration	Classification score modulated by centerness	Unchanged from FCOS
Inference flow	Single forward pass	Single forward pass

(Please see Related Work)

Point 2. The manuscript does not compare the proposed method against the sota works mentioned in Section 2.2. e.g. HRFPN [9], "Locate then Calibrate" [28] and QueryDet [8] etc. The recent and strongest published results on VisDrone results are not acknowledged at all. The published VisDrone-val results e.g. AD-Det [20] seem to be considerably stronger than Table 6 implies.

Response 2: [author response]:

Thank you for your valuable feedback on our manuscript. Both of the reviewer’s concerns—“failure to compare with the methods described in Section 2.2” and “complete lack of acknowledgment of the latest state-of-the-art results”—have been addressed in the revised manuscript. This criticism is valid, and we have addressed it at two levels.

(1) Regarding the “complete lack of acknowledgment of the latest state-of-the-art results”:

This is the strongest point raised by the reviewer, and we respond to it directly. In Section 4.6, we now explicitly acknowledge that region-focused methods such as AD-Det have reported higher accuracy on VisDrone than our single-forward configuration. We further explain their underlying mechanism: these methods first identify densely populated regions of interest and then crop and reprocess them at a higher effective resolution, at the cost of performing multiple forward passes per image. This mechanism is different from and largely complementary to the mechanism investigated in our work. Therefore, rather than presenting the two approaches as competing alternatives, we now characterize them as potentially composable: a region-focusing stage could be naturally incorporated on top of our proposed pipeline, which we regard as a promising direction for future work.

(2) Regarding the “failure to compare with the methods described in Section 2.2”:

HRFPN, Locate-then-Calibrate, and QueryDet have all been cited in our manuscript, but we acknowledge that the original manuscript cited them without making an explicit comparison. To address this issue, we have added a new paragraph before Section 2.3 that explicitly refers to Table 6 and clarifies which results are obtained under controlled experiments and which are reported values from the corresponding literature. We also annotate the differences in input resolution, pretraining data, and whether a single forward pass is used for each result.

At the same time, we have clarified the contribution of our work rather than simply underselling its performance. Our work is not intended to claim superiority in terms of absolute accuracy. Its value instead lies in the fact that, under a unified input resolution and evaluation protocol at the original image resolution, we conduct a comprehensive comparison with eight classical detectors (Table 5). More importantly, under controlled experimental conditions, we systematically isolate the interaction between the stride-4 feature level and its supervision strategy, as well as the associated trade-offs. To the best of our knowledge, such a controlled comparison and decomposition have not been previously reported for this design. Accordingly, we have repositioned the paper throughout the manuscript as a controlled and reproducible mechanistic study. The Abstract, Introduction, and Conclusion have all been revised accordingly, and any wording that could be interpreted as claiming superior performance has been removed.

What we have not done: We did not implement controlled reproductions of QueryDet, HRFPN, or AD-Det within our codebase. These methods rely on different frameworks and training recipes. In this revision round, our available computational resources were primarily allocated to the stride-4 ablation experiments requested in Reviewer 3’s Comments 3–4, the cross-dataset evaluation of r, and the multi-seed baseline experiments requested in Reviewer 1’s Comment 2, involving more than 30 training runs in total. We therefore did not include methods that we could not reproduce in a controlled manner in the controlled comparison table, nor did we make any claim or implication that we had conducted a fair controlled comparison with these methods.

[author action]:

The generic-detector comparison places CPD-FCOS in a competitive range, while re-cent UAV-specific systems provide an important external reference. Table 6 therefore re-ports protocol-labelled values from the original papers. AUHF-DETR-M uses a smaller input and emphasizes embedded efficiency, whereas SARC-DETR uses a 1024-pixel set-ting and a COCO-pretrained transformer. SARC-DETR reports higher overall AP than CPD-FCOS, and AUHF-DETR-M reports a higher APs. Region-focusing detectors such as AD-Det [20] report stronger VisDrone accuracy than the single-forward configuration studied here, and we acknowledge that gap plainly. They obtain it through a largely complementary mechanism: object-dense regions are located, cropped and reprocessed at higher effective resolution, at the cost of several forward passes per image. The contribution here lies elsewhere-in isolating, under controlled conditions, how a stride-4 level and its supervision interact inside a single forward pass, and in placing that interaction against eight established detectors under one shared evaluation protocol. The two directions are compatible rather than competing: a region-focusing stage could be added on top of this pathway. Because training data handling, pretraining, and post-processing are not controlled across publications, the cross-paper values are not used for a formal ranking. The primary evidence for CPD-FCOS remains the local factorial comparison and the cross-dataset diagnosis under a documented implementation. (Please see 4.5. Validation Comparison with Mainstream Detectors)

We presented CPD-FCOS, a single-stage UAV detector in which a real stride-4 level, a localized residual refinement branch and center-constrained positive selection are designed as one pathway, and we measured what each part contributes. Direct ablation shows that the stride-4 level accounts for most of the accuracy gain and for essentially all of the added computation, while the refinement branch is cheap and marginal. Resolving the results by object size shows why the two are complementary: added capacity alone raises small-object recall without raising average precision, and only constrained supervision converts it into precision. The same analysis delimits the claim: the advantage grows as objects shrink and reverses on the largest ones; it is clear in dense multi-class scenes, becomes an operating-point shift on vehicle-only footage, and is not measurable where small annotations are few. CPD-FCOS is therefore offered as a controlled and reproducible account of how fine-scale representation and fine-scale supervision interact, and of what that interaction costs. Detectors that add region cropping or repeated inference remain ahead on aggregate VisDrone accuracy; the pathway studied here is compatible with them, and we hope the measurements reported above are useful to anyone combining the two. (Please see Conclusions)

Point 3. The ablation study for stride-4 level is missing. This is the most computationally expensive part of the proposed method and thus should be justified through experimentation results.

Response 4: [author response]:

Thank you very much for your advice. In the original full-factorial ablation table, the “ refine” column actually ablated only the residual branch on top of , while the stride-4 feature level itself was present in all four configurations. Thus, the most computationally expensive and arguably most fundamental design decision in our method was precisely the one component that had not been directly ablated.

The newly added experiments strictly follow the controlled conditions requested by the reviewer: the same ConvNeXt-Tiny backbone, the same bidirectional FPN/PAN neck design (with only the number of feature levels varying), the same shared detection head, the same optimizer, learning rate, number of training steps, data augmentation, random seeds, and evaluation protocol. The design principle for the overlapping regions is also kept unchanged. We report both the accuracy gains and the associated computational costs, directly addressing the question of whether the additional design is worthwhile.

The conclusion is conditional and quantitative. Adding the stride-4 feature level yields +2.98 and +4.90 , at the cost of a 2.05× increase in end-to-end latency, 4× more prediction locations, and 1.78× higher GPU memory usage. In contrast, adding the refinement branch provides only +0.55 , while introducing 1.18M additional parameters and an 8.5% increase in latency. Thus, the more expensive design choice is also the decisive one, whereas the relatively inexpensive refinement branch provides only marginal gains.

The results on UAVDT further qualify this conclusion. There, adding the stride-4 level improves by 10.4 percentage points, but reduces by 1.2 points, resulting in only a +0.71 improvement overall. Based on these results, we now provide an explicit deployment criterion to guide whether the stride-4 design should be adopted under different application requirements.

[author action]:

Table 9 varies the refinement branch, but the stride-4 level itself is present in all of its rows. Because that level is the single most expensive decision in the design, we ablate it directly. The variant keeps the backbone, neck design, head, optimizer, schedule, augmentation, seed and evaluation protocol of the factorial recipe, and changes only the pyramid depth; the overlapping-range policy is preserved, so each level still starts at half the upper bound of the previous one. Accuracy is measured at the original resolution and latency on an otherwise idle GPU.

Table 10 separates two decisions that Table 9 conflates. Adding the stride-4 level is worth 2.98 and 4.90 and costs 2.05 the end-to-end latency, four times theprediction locations and 1.78 the peak memory. Adding the refinement branch on topis worth a further 0.55 mAP for 1.18M parameters and 8.5% more latency. The expensive decision is therefore also the decisive one, and the cheap one is genuinely marginal. UAVDT qualifies this conclusion rather than confirming it. There the stride-4 level buys 10.4 points of (0.2230 - 0.3273) but only 0.71 points of, and actually falls by 1.2 points. The level is thus worth its cost when the deployment target is recall of extremely small objects; when the target is aggregate , or when compute is constrained, is the better operating point. (Please see 4.9. Is the Stride-4 Level Worth Its Cost?)

Table 10. Direct ablation of the stride‑4 level on VisDrone. Backbone, neck design, head, schedule, augmentation, seed and evaluation protocol are identical across rows; only the pyramid depth changes. Latency is end‑to‑end at 1024² with batch size 1 on an idle RTX 4090 D.

Pyramid				Params(M)	Locations	Latency(ms)	Memory(MB)
+CGA	0.2927	0.4898	0.2003	38.83	21504	22.34	456
+CGA	0.3225	0.5426	0.2493	41.81	87040	45.88	811
+CGA+ refine	0.3280	0.5483	0.2514	42.99	87040	49.76	815

Point 4. Similarly, no experiment in the manuscript compares a P2-P5 pyramid against a P3-P5 pyramid under an otherwise identical backbone, neck, head, recipe, and seed count. This could be added to Table 8 ablation.

Response 4: [author response]:

[author action]:

Pyramid				Params(M)	Locations	Latency(ms)	Memory(MB)
+CGA	0.2927	0.4898	0.2003	38.83	21504	22.34	456
+CGA	0.3225	0.5426	0.2493	41.81	87040	45.88	811
+CGA+ refine	0.3280	0.5483	0.2514	42.99	87040	49.76	815

Point 5. The comparison given in Table 5 does not seem fair. CPD-FCOS uses 1024 x 1024 input resolution. YOLOv8s/YOLOv11s with Ultralytics default is, however, 640 x 640. This gives an unfair advantage to the proposed method at the very beginning of the pipeline.

Response 5: [author response]:

Thank you for your insights. The issue has now been clarified and additional experiments have been conducted. Upon verification, the baselines in our paper already use 1024², rather than the Ultralytics default 640². However, the source of the misunderstanding lies with us: the original manuscript never explicitly stated the input resolution.

(1) Facts and evidence. Both YOLOv8s and YOLOv11s use an input resolution of 1024² for training and inference. This can be directly verified from the automatically saved train/args.yaml files generated by Ultralytics, where imgsz: 1024 is specified, as well as from the evaluation code, which uses predict (imgsz=1024). For the Torchvision-based detectors, we use min_size=1024 and max_size=1707, which is exactly consistent with CPD-FCOS. These configuration files are publicly available with our code and can be directly verified.

(2) The source of the misunderstanding was incomplete reporting on our part. The original manuscript only stated that YOLO used the “official small configuration and a 60-epoch training schedule.” It was therefore entirely reasonable for readers to interpret this as using Ultralytics’ default input resolution.

(3) Additional experiment. To make this point directly verifiable rather than relying solely on our statement, we retrained YOLOv8s using the complete default configuration suggested by the reviewer, with 640² for both training and inference. Under this setting, YOLOv8s achieves only 0.211 and 0.112 , which are 7.5 and 8.2 percentage points lower, respectively, than the 1024² configuration used in our paper.

In other words, our method does not benefit from an artificially disadvantaged baseline. On the contrary, we deliberately increased the baseline input resolution to 1024², matching that of our method, which improves the YOLO baseline by 7.5 mAP points. If the default 640² configuration were used instead, the performance gap would only become larger.

(4) Manuscript revisions. We have added an “Input” column to Table 5, explicitly reporting the input resolution for every method. The 640² results are also included as an additional reference setting. Furthermore, Section 4.4 now specifies the input resolution used for each baseline individually.

[author action]:

To validate the effectiveness of CPD-FCOS, we compare it with eight representative detectors: Faster R-CNN [4], RetinaNet [5], FCOS [6], the Faster R-CNN v2 and RetinaNetv2 model variants from Torchvision, a Faster R-CNN with a MobileNetV3 [44] backbone, and the real-time detectors YOLOv8s [45] and YOLOvl1s [46]. The Torchvision detectors all use ImageNet-pretrained backbones and are trained for 60k steps on VisDroneand UAVDT and 15k steps on the smaller UAVVaste. The YOLO models use their official small configuration and 60-epoch training pipeline. All baselines are trained and evaluated at the same input size as CPD-FCOS: the Torchvision detectors use min_size = 1024, max_size = 1707, and the YOLO models use imgsz = 1024 at both training and inference rather than the Ultralytics default of 640; the per-method sizes are listed in Table 5 and the configuration files are released with the code. Retraining YOLOv8s under the full Ultralytics default (640 throughout) lowers its VisDrone validation from 0.286 to 0.211 and its from 0.194 to 0.112, so the shared 1024 setting is favourable to the baselines rather than to the proposed method. All methods use the same complete validation split and follow the original-resolution evaluation protocol of the previous subsection. Since each detector keeps its own optimizer, training recipe, and input preprocessing, this experiment measures practical system-level performance, while the incremental component evidence is given by the subsequent full-factorial ablations and sensitivity studies. A post-hoc loader audit found that the historical UAVDT Torchvision runs omitted 314 training frames that contained no valid boxes, whereas CPD-FCOS retained those negative-only frames. There leased loader now preserves them, but the checkpoint reported here predates that fix. We therefore treat the UAVDT Torchvision entries as non-controlled references and do not attribute their difference from CPD-FCOS solely to architecture. (Please see 4.5. Validation Comparison with Mainstream Detectors)

Point 6. Why was r = 1.5 retained when Table 9 shows r = 1.0 superior on both VisDrone metrics?

Response 6: [author response]:

Thank you for your suggestion. To briefly reiterate, the advantage of r = 1.0 reported in the original table was based on a single run. Meanwhile, the standard deviation across three runs for our model was only 0.001. The original manuscript retained r = 1.5 without verifying whether this difference exceeded normal run-to-run variation.

After conducting an additional three-seed comparison, we found that the performance gap on VisDrone was 0.75 mAP points, approximately six times the within-group variation, confirming that the difference indeed exceeds seed-related noise. However, after retraining the complete main configuration with three seeds on each of the three datasets, we found that this advantage only exists on VisDrone. On UAVDT and UAVVaste, the performance is comparable on the validation sets, while it decreases by 0.74 and 0.63 mAP points, respectively, on the test sets. Across all six dataset/split evaluations, the average difference is −0.07 mAP. According to the newly added criterion (ii) in Section 4.2, which requires the default setting to be generally applicable across all three datasets, retaining r = 1.5 is therefore the appropriate choice.

[author action]:

Table 12. Center radius under three random seeds (42, 123, 456), VisDrone validation split at original
resolution, factorial recipe. Entries are mean±population standard deviation.

Setting	mAP	AP_S	Individual runs (mAP)
r = 1.5	0.3254 ± 0.0021	0.2469 ± 0.0047	0.3280 / 0.3252 / 0.3229
r = 1.0	0.3329 ± 0.0003	0.2537 ± 0.0002	0.3333 / 0.3327 / 0.3327

Table 13. Does the r = 1.0 advantage transfer? The full main configuration is retrained at r = 1.0 on

every dataset with three seeds and evaluated on both splits, against the reported r = 1.5 results of

Tables 3 and 16. Positive values favour r = 1.0.

Dataset	Split	mAP (r=1.5)	mAP (r=1.0)	Δ mAP	Δ AP_S
VisDrone	validation	0.326	0.332	+0.56	+0.09
UAVDT	validation	0.261	0.261	−0.00	+0.70
UAVVaste	validation	0.488	0.488	−0.02	−0.99
VisDrone	test	0.244	0.248	+0.43	+0.25
UAVDT	test	0.163	0.156	−0.74	−0.56
UAVVaste	test	0.528	0.522	−0.63	+0.15
Mean				−0.07	−0.06

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

I have no more comments.

Author Response

Thank you for taking time to review our manuscript.

Reviewer 2 Report

Comments and Suggestions for Authors

The author answered my questions very well, and I have no more questions.

Author Response

Thank you for taking time to review our manuscript.

Reviewer 3 Report

Comments and Suggestions for Authors

The revised manuscript has addressed most of the concerns. However, a few shortcomings remain.

AD-Det's reported accuracy is never actually stated and compared. It is only mentioned as "stronger".
Figure 4 now depicts stale data which is not reproducible. Please verify.
Please see that the results corresponding to yolov8s on uavvaste given in section 5.1 conform to those in table 5 and 4.

Author Response

Dear reviewer,

Thank you for taking time to review our manuscript.

We studied your comments and revised our draft accordingly.

We also went through our manuscript and made a few corrections on the texts.

Hope that our revised draft will meet with your approval.

Best wishes,

Chaowen Xie, Cheng Zhang, Fei Meng, Shunbing Zhao, Wei Zhao, Sijun Dong and Hanfa Xing

Response to Reviewer 3 Comments

The revised manuscript has addressed most of the concerns. However, a few shortcomings remain.

Point 1. AD-Det's reported accuracy is never actually stated and compared. It is only mentioned as "stronger".

Response 1: [author response]:

Thank you very much for this important comment. We agree that the previous revision did not answer this point adequately. Although AD-Det was mentioned as a stronger region-focusing detector, its reported VisDrone accuracy was not stated numerically, so the reader could not see the actual size of the gap.

We have therefore revised Section 4.5 and Table 6 to state the comparison explicitly. AD-Det reports 0.353 AP with a ResNet-50 backbone and 0.370 AP with a ResNeXt-101 backbone on the VisDrone validation split, compared with 0.326 AP for CPD-FCOS. For the small-object metric available in the reported ResNet-50 result, AD-Det reaches 0.280 AP_S versus 0.251 for CPD-FCOS. We also report AD-Det's own two-stage baseline (0.331 AP and 0.243 AP_S), which already uses four uniform crops. Table 6 now includes both AD-Det backbone variants together with input size, pretraining, and the inference cost of one coarse pass plus four subregion passes.

To go beyond a purely qualitative literature comparison, we also reimplemented the AD-Det region-focusing pipeline in our codebase and evaluated it on the same VisDrone validation split with the evaluator used throughout this paper. The reimplementation is reported separately in a new Table 7 because its absolute accuracy does not reproduce the published level and therefore must not be used to claim a ranking against AD-Det. The mechanism itself is reproduced clearly: adding a cropped second stage with a dedicated fine detector raises the same base detector from 0.210 to 0.293 AP (+8.3 points). However, our adaptive-subregion implementation reaches 0.278 AP rather than the published 0.353, and the full DCC module was not reimplemented. We therefore retain the author-reported values in Table 6 as the comparison of record and use the reimplementation only to illustrate the mechanism and computational cost.

This revision makes the comparison explicit rather than describing AD-Det only as "stronger", while also preserving the distinction between author-reported cross-paper results and results reproduced under our own evaluation pipeline. We sincerely thank the reviewer for prompting us to make this gap quantitative and directly auditable.

[author action]:

The generic‑detector comparison places CPD‑FCOS in a competitive range, while recent UAV‑specific systems provide an important external reference. Table 6 therefore reports protocol‑labelled values from the original papers. AUHF‑DETR‑M uses a smaller input and emphasizes embedded efficiency, whereas SARC‑DETR uses a 1024‑pixel setting and a COCO‑pretrained transformer. SARC‑DETR reports higher overall AP than CPD‑FCOS, and AUHF‑DETR‑M reports a higher APₛ. Region‑focusing detectors report stronger VisDrone accuracy than the single‑forward configuration studied here, and we state the gap numerically rather than qualitatively. AD‑Det [20] reports 0.353 AP with a ResNet‑50 backbone and 0.370 with ResNeXt‑101 on the same validation split, against 0.326 here, and 0.280 APₛ against 0.251; its own two‑stage baseline, which already crops each image into four uniform parts, reports 0.331 AP and 0.243 APₛ. The margin is therefore real and we acknowledge it plainly. It is obtained through a largely complementary mechanism: object‑dense regions are located, cropped and re‑processed at higher effective resolution, which costs one coarse pass plus four subregion passes per image against the single pass measured in Table 19. The contribution here lies elsewhere—in isolating, under controlled conditions, how a stride‑4 level and its supervision interact inside a single forward pass, and in placing that interaction against eight established detectors under one shared evaluation protocol. The two directions are compatible rather than competing: a region‑focusing stage could be added on top of this pathway. Because training data handling, pretraining, and post‑processing are not controlled across publications, the cross‑paper values are not used for a formal ranking. The primary evidence for CPD‑FCOS remains the local factorial comparison and the cross‑dataset diagnosis under a documented implementation.

Table 6. Author-reported VisDrone2019 validation results from recent UAV-specific detectors. “NR” means that the item was not reported clearly enough for a controlled comparison. CPD-FCOS is included only as a protocol reference; cross-paper values were not reproduced in our codebase.AD-Det is reported at two backbones because its paper reports both; the ResNet-50 row is the configuration whose AP_S is available. Its inference column counts one coarse pass plus N = 4 subregion passes.

Method	Year	Input	Pretraining	Inference	AP
AUHF-DETR-M [19]	2025	640²	NR	single pass	0.309	0.261
SARC-DETR [22]	2026	1024²	COCO	single pass	0.348	0.248
AD-Det (ResNet-50) [20]	2025	1333 × 800	ImageNet	1+4 passes	0.353	0.280
AD-Det (ResNeXt-101) [20]	2025	1333 × 800	ImageNet	1+4 passes	0.370	NR
CPD-FCOS (3-seed mean)	2026	1024²	ImageNet	single pass	0.326	0.251

A cross-paper number cannot be audited, so we additionally reimplemented the AD-Det pipeline in this codebase and evaluated it on the same validation split with the evaluator used everywhere else in this paper. Table 7 reports the outcome, including the parts that did not reproduce. The region-focusing mechanism itself replicates clearly: adding a cropped second stage with a dedicated fine detector raises the same base detector from 0.210 to 0.293 AP, an 8.3-point gain that no single-pass change in this paper approaches. Two things did not replicate. The absolute level is 7.5 points below the published figure (0.278 against 0.353), which we attribute to the base detector rather than to the second stage, since our plain GFL is correspondingly weak. And the adaptive subregions did not beat the four uniform crops that AD-Det uses for its own baseline (0.278 against 0.293 in our hands, where the published ordering is the reverse); in our reimplementation the clustered regions leave 7.4% of object centres outside every subregion, whereas quadrants tile the image exactly. We therefore treat Table 6, which uses the authors’ own numbers, as the comparison of record, and this table as evidence about mechanism and cost only. In particular the CPD-FCOS row below must not be read as outperforming AD-Det; it is placed there only as the single-pass reference point against which the cost of the extra passes should be judged. That cost is substantial: on one GPU the same reimplemented base detector takes 0.033 s per image with a single pass and 0.277 s once the four subregion passes are added.

Table 7. AD-Det reimplemented in this codebase and evaluated on the VisDrone validation split under the protocol of this paper (COCO AP, at most 100 detections per image). “Reported” values are from the original paper, whose own baseline already crops each image into four uniform parts. The reimplementation follows the published recipe (GFL, ResNet-50, 1333 × 800, 12 epochs, SGD 0.01, decay at epochs 8 and 11, N = 4 subregions, fusion NMS 0.5); the DCC module was not reimplemented. The reimplementation is below the published figures and is reported as such; it does not license any ranking claim against AD-Det.

Configuration	Passes/image	Reported AP	Reproduced AP
GFL, no second stage	1	NR	0.210
GFL + four uniform crops (their baseline)	1+4	0.331	0.293
+ ASOE, shared-weight fine detector	1+4	NR	0.217
+ ASOE, dedicated fine detector	1+4	0.353	0.278
+ ASOE + DCC (full AD-Det)	1+4	0.359	not reimplemented
CPD-FCOS (this paper), single pass	1	–	0.326

(Please see 4.5. Validation Comparison with Mainstream Detectors)

Point 2. Figure 4 now depicts stale data which is not reproducible. Please verify.

Response 2: [author response]:

Thank you very much for pointing this out. We re-audited the provenance of all six precision–recall curves and confirmed the reviewer’s concern. The previous UAVDT FCOS curve in Figure 4 came from the historical FCOS run that achieved a validation mAP of 0.263 but was trained without explicit seed control and could not be reproduced in our seeded reruns. In the previous revision, Table 5 had already been updated to the reproducible FCOS baseline (0.224 ± 0.002 over seeds 42, 123, and 456), but Figure 4 and several analyses derived from the old predictions had not been regenerated. This caused the inconsistency.

We have now regenerated Figure 4 using reproducible checkpoints. Because a precision–recall curve necessarily corresponds to one training run rather than to a three-seed mean, all six curves now use the seed-42 run of the same configuration reported in Table 5. The revised legend values are: VisDrone, CPD-FCOS 0.325 and YOLOv11s 0.290; UAVDT, CPD-FCOS 0.256 and FCOS 0.224; and UAVVaste, CPD-FCOS 0.488 and YOLOv8s 0.481. The figure caption now explicitly explains that the legends give the mAP of the plotted seed-42 run, whereas Table 5 reports the corresponding three-seed means.

To make the figure directly verifiable, we also added a provenance file, figures/fig_pr_curves.provenance.json, which records the prediction file, checkpoint path, and SHA-256 hash for each of the six curves. We then rechecked the quantitative discussion that depended on the previous predictions and revised the corresponding text and breakdown analyses. In particular, with the reproducible FCOS reference, the two UAVDT curves no longer cross: CPD-FCOS is above FCOS throughout the shared recall range, with the largest precision advantage at low-to-mid recall. The associated size-resolved and per-class discussion was recomputed accordingly, and the validation-to-test baseline references in Section 5.1 were aligned with the current reported results.

Importantly, the CPD-FCOS results and the primary values in Table 5 are unchanged. The values 0.263 and 0.161 are retained only in the historical disclosure paragraph that explicitly documents the earlier non-reproducible FCOS run; they are not used as the current baseline results. The current reproducible FCOS reference is 0.224 ± 0.002 on the validation split and 0.167 ± 0.002 on the locked test split. We sincerely thank the reviewer for prompting us to trace the figure provenance and correct these stale-data dependencies.

[author action]:

Table 5 uses the three‑seed CPD‑FCOS mean as the primary value; the competing detectors are single‑run references, and CPD‑FCOS stability is reported separately in Table 16. The results again separate the datasets rather than producing one uniform ranking. On VisDrone, CPD‑FCOS reaches 0.326 mAP, 3.8 points above YOLOv11s, and obtains the highest APₛ in the table. This is precisely the regime targeted by the pathway: dense multi‑class scenes combine tiny instances, class ambiguity, and background clutter, making both fine detail and reliable positive locations valuable. On UAVDT the margin is narrower: CPD‑FCOS leads the reproducible FCOS reference by 3.7 mAP points, while the two APₛ values (0.287 against 0.282 ± 0.030) differ by less than the seed dispersion of the baseline, so the small‑object comparison on this dataset is not resolved by the available evidence. The FCOS entry deserves a comment. The single run reported previously reached 0.263 mAP, higher than any of fifteen seeded repetitions across three learning rates, two batch sizes and gradient clipping on or off; the best reproducible configuration averages 0.224 ± 0.002. We report the reproducible mean and record the earlier value so the discrepancy is visible rather than silently corrected. The same checkpoint sits at the low end of its seed distribution on the locked test split (0.161 against 0.167), so it was favourable on validation and unfavourable on test—the instability that repeating a baseline is meant to expose. UAVVaste offers a complementary case in which CPD‑FCOS remains competitive overall, but the small‑object subset is too limited to support a broad small‑object claim. (Please see 4.5. Validation Comparison with Mainstream Detectors)

Figure 4 shows the corresponding precision–recall curves; each curve is the seed‑42 run of the configuration reported in Table 5. On VisDrone the CPD‑FCOS curve is above the reference from recall 0.2 upward, with the gap widening to more than 20 precision points near recall 0.7, and it extends to a higher maximum recall (0.94 against 0.91); below recall 0.2 the two lie within about one precision point of each other. On UAVDT the CPD‑FCOS curve is above the reproducible FCOS reference at every recall, by 8 to 15 precision points below recall 0.55, while above recall 0.6 the two nearly coincide and FCOS reaches a marginally higher maximum recall (0.88 against 0.87). On UAVVaste the two are close throughout. (Please see 4.5. Validation Comparison with Mainstream Detectors)

Figure 4. Precision–recall curves at IoU = 0.5, averaged over classes, on the complete validation split of each dataset under the original‑resolution protocol. The reference detector is the highest‑validation‑mAP baseline for that dataset. A curve necessarily comes from one training run, whereas Table 5 reports three‑seed means; every curve here is the seed‑42 run of the configuration reported in that table, and the legend gives that run’s own mAP. Checkpoint paths and hashes for all six curves are recorded in figures/fig_pr_curves.provenance.json.

(Please see 4.6. Remote-Sensing Scenario Analysis)

Aggregate mAP is too coarse to delimit where the method applies, so Tables 7 and 8 resolve the VisDrone comparison by class and by object size. CPD‑FCOS leads the validation‑selected YOLOv11s reference on all ten classes, and the margin tracks how small and how crowded a class typically is: it is largest for van (+7.8), people (+5.0), pedestrian (+4.7) and bus (+4.4), and smallest for awning‑tricycle (+0.2), where the two detectors are effectively tied, and for tricycle and motor (both +2.4).

The size‑resolved view is more informative still. Recall at IoU = 0.5 improves by 37.3 points on objects below 16 pixels, by 17.7 points between 16 and 32, by 8.2 points between 32 and 64, and by 7.1 points above 64; average precision follows the same ordering and reverses on the largest bin, where the reference is 1.1 points better. The advantage is therefore scale‑specific rather than a general capacity effect, which is what a scale‑isolated pathway should produce, and it also marks the regime where the method offers nothing.

UAVDT separates the two detectors differently. Measured against the reproducible FCOS reference, CPD‑FCOS has slightly lower recall on the two smallest bins (0.694 against 0.700 below 16 pixels and 0.728 against 0.743 between 16 and 32) and higher recall on the two largest (0.603 against 0.539 and 0.614 against 0.543), while its AP and its precision at IoU = 0.5 are higher in all four bins; the margin is by far the largest in the smallest bin (0.386 against 0.170 AP and 0.609 against 0.344 precision). Per class it leads on truck (0.201 against 0.106) and bus (0.065 against 0.049) and trails only on car (0.501 against 0.515), the class that dominates the dataset. The pattern on this dataset is therefore one of precision rather than recall: the pathway converts the stride‑4 capacity into cleaner detections at a given recall, and the residual FCOS advantage is confined to recall on the smallest instances. Table 5 uses the three‑seed CPD‑FCOS mean as the primary value.

Table 7. Per-class AP on the VisDrone validation split at original resolution, against the validation-selected reference detector.

Method	pedes.	people	bicycle	car	van	truck	tricy.	awn.-tri.	bus	motor
YOLOv11s	0.275	0.171	0.136	0.603	0.331	0.312	0.205	0.120	0.471	0.272
CPD-FCOS	0.322	0.221	0.170	0.631	0.408	0.340	0.229	0.121	0.516	0.296

Table 8. VisDrone validation performance resolved by object size ( in pixels). Recall is measured at IoU = 0.5.

	Recall (CPD-FCOS)	Recall (YOLOv11s)	AP (CPD-FCOS)	AP (YOLOv11s)
< 16	0.740	0.367	0.157	0.097
16–32	0.838	0.660	0.313	0.255
32–64	0.883	0.801	0.408	0.406
≥ 64	0.921	0.851	0.503	0.514

(Please see 4.6. Remote-Sensing Scenario Analysis)

Point 3. Please see that the results corresponding to yolov8s on uavvaste given in section 5.1 conform to those in table 5 and 4.

Response 3: [author response]:

Thank you very much for pointing out this inconsistency. The reviewer is correct. The YOLOv8s results on UAVVaste reported in Section 5.1 were residual values from an earlier version and had not been updated after the baseline results in Tables 4 and 5 were revised using the three-seed evaluation.

We have now carefully rechecked the numerical values in Section 5.1 against Tables 4 and 5 and corrected the corresponding validation–test comparison. Specifically, the UAVVaste YOLOv8s validation mAP has been corrected from 0.486 to 0.482 ± 0.003, consistent with Table 5, and the test mAP has been corrected from 0.521 to 0.517 ± 0.005, consistent with Table 4.

During this check, we also identified and corrected the remaining outdated baseline values in the same paragraph for VisDrone and UAVDT so that all numerical comparisons in Section 5.1 now conform exactly to Tables 4 and 5. We sincerely thank the reviewer for drawing our attention to this inconsistency.

[author action]:

The validation–test change is not unique to CPD-FCOS. On VisDrone, CPD-FCOS changes from 0.326 validation mAP to 0.244 test mAP, while YOLOv11s changes from 0.288 ± 0.004 to 0.223 ± 0.001; the margin consequently narrows from 3.8 to 2.1 points. On UAVDT, CPD-FCOS changes from 0.261 to 0.163 and FCOS from 0.224 ± 0.002 to 0.167 ± 0.002. On UAVVaste, both CPD-FCOS and YOLOv8s increase on test, from 0.488 to 0.528 and from 0.482 ± 0.003 to 0.517 ± 0.005, respectively. These parallel movements are consistent with a split effect, although the non-paired training recipes preclude a causal claim. (Please see 5.1. Mechanistic Interpretation and Cross-Dataset Behavior)

Author Response File: Author Response.pdf