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REVIEW 4 major objections 6 minor 52 references

Rethinking Annotation for Object Detection: Is Annotating Small-size Instances Worth Its Cost?

T0 review · 4 major / 6 minor · reviewed 2026-08-11 · deepseek-v4-flash

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Pith's one-line read The paper argues that detectors can match fully annotated baselines on small objects using only test-time upscaling and resolution-matching augmentation.

desk verdict Genuinely new cost-benefit question, clean COCO experiment, honest appendix — but the aggregate parity hides per-class losses on small-only classes like traffic lights, so the 'small annotation isn't worth it' headline overreaches the evidence. read the letter →

arxiv 2412.05611 v1 pith:VWFA2BCT submitted 2024-12-07 cs.CV

Yusuke Hosoya , Masanori Suganuma , Takayuki Okatani This is my paper · ORCID
classification cs.CV
keywords smallobjectdetectionannotationcosttest-timeupscalingdomaingapknowledgedistillationCOCO
verification ladder T0 review T1 audit T2 compute T3 formal

The pith

A machine-rendered reading of the paper's core claim, the machinery that carries it, and where it could break.

The reading

This paper asks whether the expensive, error-prone work of annotating small object instances is necessary for training an object detector. It restates the question as a testable one: can a detector trained with no small-instance annotations still detect small objects? On COCO, using Faster R-CNN and FCOS, the authors show that upscaling the test image and feeding it through the same detector, together with a training-time augmentation that makes medium-sized training instances look as blurry as upscaled small ones, reaches at least the accuracy of a baseline trained with all annotations. Downscaling training images to create synthetic small instances does not work as well, which the authors attribute to a context and perspective gap. The result suggests that skipping or coarsening small-instance annotation could cut annotation cost without sacrificing comparable detection accuracy.

What carries the argument

The mechanism is test-time upscaling: the detector is applied twice to the same image, once at native resolution to catch medium and large objects and once enlarged by a factor α (around 2.0–2.2) to make small objects appear medium-sized, with detected boxes rescaled back and merged. Because upscaled small objects are blurrier than native medium objects, the training set is augmented by downscaling training images by 1/γ and upscaling them back by γ (γ = 3) — or by Gaussian blurring — so that the detector learns to map blurry, medium-sized appearances to the correct classes. A contrastive method, downscaling training images so medium objects become small synthetic instances, fails, isolating the domain gap in context and perspective as the limiting factor. Finally, knowledge distillation turns the two-pass teacher into a single-path student trained on pseudo labels for small instances plus the original medium and large annotations, restoring the practical computational cost of the baseline.

What would settle it

Compute per-class average precision for small instances on the COCO validation split for context-dependent classes whose training instances are predominantly small (for example, traffic light and remote); if the upscaling method falls clearly below the fully annotated baseline on those classes, the claimed parity does not hold for all objects.

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Extended reading notes

Core claim

The central claim is that detectors can learn to detect small-size instances without any real small-size annotation, provided the input is upscaled at test time and the resolution gap is narrowed during training. In the COCO validation evaluation, the two-pass Up@Test-scale method reaches an average precision for small instances of 13.7 for Faster R-CNN against a baseline of 11.9, and 23.6 for FCOS against 22.3. Distilling the two-pass model into a single-path detector preserves the result, giving 11.0 for Faster R-CNN and 22.4 for FCOS, both comparable to their full-data baselines. The same experiments show that synthesizing small instances by downscaling training images does not match this performance, supporting the authors' conclusion that test-time upscaling, not small-instance annotation, is the effective ingredient.

Load-bearing premise

The load-bearing premise is that an upscaled small object, after the resolution-matching augmentation, looks enough like a native medium-sized object to the detector, so the remaining differences in context and perspective do not matter for the classes being detected.

Editorial extensions

If this is right

  • If the claim holds, an annotation pipeline can omit or roughly label small instances and still obtain a detector whose small-object accuracy is comparable to one trained on complete data.
  • The annotation budget saved on tiny objects could be redirected to harder medium and large annotations or to rare, context-dependent classes.
  • Because the method is detector-agnostic, the same upscaling-plus-augmentation recipe may transfer to other anchor-based and anchor-free detectors.
  • The failure of Down@Train predicts that synthetic small instances made by resizing will not substitute for real small annotations, so annotation decisions should account for context and perspective, not resolution alone.

Reading between the lines

Editorial extensions of the paper, not claims the author makes directly.

  • Editorial inference: the result raises the possibility of revising annotation guidelines so that crowd-like clusters of small instances are labeled with a single coarse box or an iscrowd flag, with test-time upscaling recovering the lost individual detections.
  • Editorial inference: a testable extension is to apply the same recipe to datasets captured with different camera focal lengths or to video frames; if the context and perspective gap widens, parity with fully annotated baselines should degrade.
  • Editorial inference: combining test-time upscaling with a super-resolution step could push small-object accuracy beyond the baseline, since the remaining gap the authors document for very small instances is partly a resolution effect.
  • Editorial inference: the per-class analysis in the appendix suggests that classes whose training examples are mostly small, such as traffic lights and remotes, may still need annotations; a per-class cost-benefit rule could identify exactly which classes justify small-instance labeling.
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Editorial analysis

A structured set of objections, weighed in public.

Desk editor's note, referee report, and a circularity audit.

Referee Report

4 major / 6 minor

Summary. The paper poses the cost-benefit question of whether annotating small-size object instances is worth its cost, and reformulates it as a falsifiable question: can a detector trained on data free of small-size instance annotations still detect small instances? The authors propose two methods: Up@Test, which upscales the input image at test time while training only on medium/large instances, optionally with blur or downscale-upscale augmentation to narrow the domain gap; and Down@Train, which downscales training images to create synthetic small instances. Experiments on COCO show that Up@Test with scale augmentation (γ=3) reaches small-instance AP slightly above the baseline trained on all annotations (Faster RCNN 13.7 vs 11.9; FCOS 23.6 vs 22.3), while Down@Train performs much worse. A distillation step yields a single-path student model with AP-small 11.0 vs 11.9 (Faster RCNN) and 22.4 vs 22.3 (FCOS), which the paper describes as comparable to the full-annotation baseline. The paper concludes that small-instance annotation may be unnecessary, and that this result should prompt rethinking of annotation practices.

Significance. The paper addresses a practically important and underexplored question: whether the high cost of annotating small objects is justified. The central claim, if it holds, would have direct implications for dataset construction and annotation cost reduction. The study is framed as a clear, testable hypothesis, and the proposed methods are simple, detector-agnostic, and include a distillation step that addresses the computational cost of running the detector twice. The paper is honest about the residual domain gap and shows failure cases. However, the evidence is limited to two detectors on a single dataset, and the headline conclusion relies on aggregate AP-small values that may conceal systematic per-class degradation, particularly for classes that only appear at small sizes in the training data. A per-class breakdown and a measure of variance across runs are needed to make the central claim robust.

major comments (4)
  1. [Sec. 5.4, observation (i) and Appendix A] The central claim that Up@Test achieves 'at least comparable performance' to Baseline is supported only at the aggregate AP-small level (Table 2: 13.7 vs 11.9 for Faster RCNN; 23.6 vs 22.3 for FCOS). Appendix A explicitly states that 'for objects that have only small-size instances in the training data (e.g., traffic light and remote), Baseline performs better.' This is not an edge case: traffic lights and remotes are exactly the kinds of small, context-dependent objects whose annotation the paper argues could be skipped. Without a per-class AP breakdown, the aggregate surplus could be driven by classes that have ample medium/large supervision while classes that predominantly appear small lose detection accuracy. Since the cost-benefit question is fundamentally per-class, the paper should report AP-small per class, or at least for classes with a high fraction of small instances, to support the headline conclusion.
  2. [Sec. 5.5, Table 3] The distilled single-path model for Faster RCNN achieves APS 11.0 vs Baseline 11.9, a deficit of 0.9, while for FCOS the values are 22.4 vs 22.3. The paper calls these 'comparable' but provides no error bars or multiple-seed results, so it is impossible to tell whether the Faster RCNN gap is within noise or a real degradation. The same issue applies to Table 2 (13.7 vs 11.9; 23.6 vs 22.3). The claim of 'at least comparable' would be much stronger with standard deviations over at least three runs.
  3. [Sec. 4.3 and Appendix A] The method rests on the assumption that the downscale-upscale augmentation (γ=3) or Gaussian blur closes the resolution part of the domain gap, and that the remaining context/perspective gap is small enough. Appendix A shows concrete failures on context-dependent cases (e.g., 'sports ball' on a cupcake, 'clock' in an eye) and on small-predominant classes. The paper acknowledges these failures but does not quantify how often they occur or how much they contribute to the aggregate result. A quantitative analysis of the residual domain gap, for instance by reporting AP-small separately for classes with a majority of small instances versus those with substantial medium/large supervision, would clarify the scope of the claim and the conditions under which the method can be expected to transfer to new datasets.
  4. [Sec. 5.1] All hyperparameters (α, γ, β, blur kernel and σ, confidence thresholds, mixing ratio) are selected based on COCO validation, and the final results are reported on that same validation split. This is effectively tuning on the test set, which can inflate the reported numbers and make the 'at least comparable' claim less reliable. The authors should either evaluate on a held-out test split (e.g., COCO test-dev) or, failing that, explicitly discuss the risk of overfitting to the validation set and report the sensitivity of the main results to the chosen hyperparameters.
minor comments (6)
  1. [Appendix A] The abbreviation 'DAT' is used in the opening paragraph of the appendix without ever being defined; it should be defined or replaced with 'Down@Train' for consistency.
  2. [Sec. 5.1] The sentence 'We do not employ any kind of multi-scale test or multi-scale training other than ours' is confusing because Up@Test itself is a form of multi-scale testing; please rephrase to clarify that no standard multi-scale augmentation or test-time augmentation is used beyond the proposed methods.
  3. [Sec. 5.1] The mixing ratio of 0.414 : 0.586 for blur/downscale augmentations is motivated only by the instance count ratio in COCO; the rationale for using this ratio for mixing training samples should be explained, since a ratio based on instance counts does not obviously translate to a ratio for image-level mixing.
  4. [Figure 3] The caption should state more explicitly that the 'human subject' is one of the authors and that the 500 images were chosen randomly, to avoid any impression of a formal human-study methodology.
  5. [Abstract and Sec. 5.5] The phrase 'at least comparable' is too strong given that the distilled Faster RCNN result (11.0 APS) is 0.9 below the baseline (11.9); consider softening to 'comparable within uncertainty' or reporting a confidence interval.
  6. [Figures 5-7] The legends and axis labels in Figures 5-7 are very small and hard to read; also, the figure captions should explicitly note that the broken lines are the Baseline values for each AP metric, not a single reference line.

Circularity Check

0 steps flagged · score 0.0 of 10

No circularity: the central claim is an empirical comparison against the external COCO validation benchmark, not a derivation from fitted inputs or self-citations.

full rationale

The paper makes no derived claim that is defined in terms of its own conclusion. The central observation (Sec. 5.4, observation i) is an empirical comparison against the external COCO validation set: Up@Test-scale is trained without small-instance annotations and evaluated on original small instances, with APS reported in Table 2 (13.7 vs 11.9 for Faster R-CNN; 23.6 vs 22.3 for FCOS). The domain-gap remedy (Gaussian blur or downscale-upscale by gamma) is a data augmentation applied to medium/large instances during training, not a fit to the small-instance APS being predicted. Hyperparameters (alpha, gamma, beta, confidence thresholds) are selected by validation performance, which is standard model selection rather than a fitted input renamed as a prediction. There are no self-citations, no uniqueness theorem imported from prior author work, and no ansatz smuggled in via citation. Appendix A's admission that classes appearing predominantly as small instances (e.g., traffic light and remote) are detected better by Baseline is a limitation of the central claim's scope, but it is an empirical boundary and does not make the derivation circular. The claim is directly falsifiable and self-contained against the COCO benchmark, so the circularity score is 0.

Assumptions & free parameters 6 free parameters · 5 assumptions · 0 invented entities

The empirical claim rests on a handful of hyperparameters (alpha, gamma, beta, blur kernel, confidence threshold) tuned on the validation set, plus standard assumptions about COCO ground truth and ImageNet pretraining. The most fragile assumption, that resolution matching closes the size-domain gap, is partially contradicted by the paper's own failure analysis in Appendix A. No invented entities are postulated.

free parameters (6)
  • test-time upscaling factor alpha = 2.0 (Faster R-CNN), 2.2 (FCOS)
    Selected as the peak of small-object AP on the COCO validation set (Figs. 5 to 7); the headline comparable result depends on this selection.
  • training scale augmentation factor gamma = 3
    Best of gamma in {2, 3} for Up@Test-scale; it maps medium-size instances into the small-size range and is used for both the reported teacher and the distilled student.
  • downscale factor beta for Down@Train = 1/3
    Chosen so that medium-size instances fall into the small-instance area range; Down@Train underperforms and is used only to supply extra pseudo small instances during distillation.
  • Gaussian blur kernel (k, sigma) = (11, 2.0)
    Best of the two blur settings tried for Up@Test-blur; the blur variant is secondary to the scale variant in the paper's conclusions.
  • distillation confidence threshold = 0.9 (Faster R-CNN), 0.7 (FCOS)
    Best small-object AP among the thresholds {0.3, 0.7, 0.9} in Table 3; reporting the best threshold per detector is a favorable selection.
  • augmentation mixing ratio = 0.414 : 0.586
    Fixed to the COCO instance-count ratio of small to medium-plus-large instances, not tuned to optimize AP.
assumptions (5)
  • domain assumption COCO ground-truth annotations are correct
    COCO annotations are used as supervision and as evaluation targets throughout; any annotation noise would affect baseline and proposed methods similarly but is not quantified.
  • domain assumption ImageNet pretraining transfers to COCO detection
    Both backbones are ImageNet-pretrained PyTorch models (Sec. 5.1); the paper does not test training from scratch or with other pretraining.
  • domain assumption Size scaling plus resolution matching suffices to bridge the train/test appearance gap for small instances
    Central to Up@Test: after downscale-upscale augmentation with gamma equal to 3, upscaled test small instances are assumed to match native medium instances in appearance distribution. Appendix A shows this fails for context-dependent classes, so the assumption is only partially validated.
  • domain assumption COCO small/medium/large area cutoffs define the problem
    The entire study is conditioned on COCO's area thresholds; the conclusion may not transfer to other definitions of small size or to other datasets.
  • domain assumption Validation-set hyperparameter selection gives unbiased performance estimates
    Peak alpha, gamma, and confidence thresholds are read off the same COCO validation split used for the reported numbers; no held-out test set or repeated evaluation corrects for this selection.

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Cite this review

Pith. "Pith review of Rethinking Annotation for Object Detection: Is Annotating Small-size Instances Worth Its Cost?." pith.science (2026). https://pith.science/paper/VWFA2BCT

@misc{pith2026241205611,
  author       = {Pith},
  title        = {Pith review of: Rethinking Annotation for Object Detection: Is Annotating Small-size Instances Worth Its Cost?},
  year         = {2026},
  howpublished = {\url{https://pith.science/paper/VWFA2BCT}},
  note         = {Machine review of arXiv:2412.05611}
}
read the original abstract

Detecting objects occupying only small areas in an image is difficult, even for humans. Therefore, annotating small-size object instances is hard and thus costly. This study questions common sense by asking the following: is annotating small-size instances worth its cost? We restate it as the following verifiable question: can we detect small-size instances with a detector trained using training data free of small-size instances? We evaluate a method that upscales input images at test time and a method that downscales images at training time. The experiments conducted using the COCO dataset show the following. The first method, together with a remedy to narrow the domain gap between training and test inputs, achieves at least comparable performance to the baseline detector trained using complete training data. Although the method needs to apply the same detector twice to an input image with different scaling, we show that its distillation yields a single-path detector that performs equally well to the same baseline detector. These results point to the necessity of rethinking the annotation of training data for object detection.

Figures

Figures reproduced from arXiv: 2412.05611 by the authors.

Figure 1
Figure 1. Compared with mid- and large-size object instances [PITH_FULL_IMAGE:figures/full_fig_p001_1.png] view at source ↗
Figure 2
Figure 2. Examples showing difficulties with annotating small-size object instances. (a) Images that are hard to annotate; while careful [PITH_FULL_IMAGE:figures/full_fig_p004_2.png] view at source ↗
Figure 3
Figure 3. “Accuracy” of a human subject’s annotation on se [PITH_FULL_IMAGE:figures/full_fig_p004_3.png] view at source ↗
Figures from the paper (6 more)
Figure 4
Figure 4. Figure 4: Three methods compared in the experiments. (a) The ordinary method. A model is trained with and applied to images with the [PITH_FULL_IMAGE:figures/full_fig_p005_4.png]
Figure 5
Figure 5. Figure 5: Results of Up@Test-vanilla, i.e., trained with the orig￾inal images and with only medium- and large-size instances. The left and right show Faster RCNN and FCOS, respectively. The horizontal axis indicates the factor of the test-time upscaling. The broken lines indicat…
Figure 6
Figure 6. Figure 6: Results of Up@Test-scale. The training images are scaled (×1/γ) and rescaled (×γ). (a) γ = 2 and (b) γ = 3. The rest is the same as [PITH_FULL_IMAGE:figures/full_fig_p007_6.png]
Figure 7
Figure 7. Figure 7: Results of Up@Test-blur. The training images are blurred with a Gaussian kernel with (a) kernel size k = 7 and (b) k = 11. The rest is the same as [PITH_FULL_IMAGE:figures/full_fig_p007_7.png]
Figure 8
Figure 8. Figure 8: The number of instances that are detected for all the [PITH_FULL_IMAGE:figures/full_fig_p008_8.png]
Figure 9
Figure 9. Figure 9: Success and failure cases of small-size instance detection evaluated by original test small-size instances by [PITH_FULL_IMAGE:figures/full_fig_p012_9.png]

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Pith tools

Reviewed August 11, 2026 · model on record in the stance chip above.