- Rating
- 3
- Confidence
- 2
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
The paper introduces the Geometric-Prior Evaluation Protocol (GPEP) to quantify the extent to which training transformation coverage can be reduced by geometric priors. Experiments on ImageNet-100 and CIFAR-10 show that C4-equivariant networks achieve comparable accuracy with substantially narrower training rotation ranges. However, these advantages diminish when conventional models receive additional training time and test-time augmentation. Further experiments investigate learned geometric priors across flat and hierarchical architectures, finding that augmentation generally outperforms learned priors on hierarchical backbones.
Critical strengths
Some of the paper's major strengths are as follows.
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The paper presents several interesting empirical observations. For example, test-time augmentation using four rotated views (TTA4) yields substantial accuracy improvements under narrow training rotation coverage, whereas additional training yields comparatively smaller improvements in those settings. The analysis also demonstrates how the apparent advantage of equivariant architectures depends on the comparison budget and evaluation target.
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The authors have done a commendable job of documenting the experimental configurations, including hyperparameters, computational budgets, parameter counts, training times, and implementation details. The extensive supplementary results and reporting of per-seed variation are particularly helpful for understanding the comparisons.
Critical weaknesses
For me, there are two major weaknesses of the paper: (a) Motivation and (b) Novelty. The following is the detailed assessment of the paper.
- I find the overall practical motivation of the proposed transformation-coverage metric insufficiently convincing.
The authors report that exact C4 requires approximately four times the FLOPs and eight times the training time of the plain model on ImageNet-100. When the ordinary CNN receives additional training time and four-view test-time augmentation, the interpretation of the original 156° coverage-saving result changes considerably.
A similar observation appears in the CIFAR-10 results. At a training half-width of 90°, C4 achieves 92.00% accuracy, while the time-matched plain model with TTA4 achieves 91.94%. These results indicate that the benefits depend substantially on the computational budget and experimental configuration.
More fundamentally, the authors explicitly acknowledge that transformation-coverage savings do not imply fewer training examples (Section 3, line 186). Since full-range image rotation augmentation is relatively inexpensive and straightforward to implement, I am not entirely convinced of the practical significance of minimizing angular training coverage as a resource in its own right.
I would encourage the authors to explain what practical model-selection or deployment decisions can be informed by knowing that C4 saves 156° of training-band half-width, particularly when the corresponding architecture has substantially higher computational costs.
- I have some reservations about the novelty of the proposed evaluation and its findings. Group-equivariant and steerable CNNs have been studied extensively. The authors themselves refer to the ICLR 2017 paper on steerable CNNs. The underlying mathematical relationships between group invariance and transformations are well established, as the authors themselves acknowledge in Appendix F.
Section 3.4 empirically relates folded distance to transformation-coverage requirements. However, the observed relationship is largely consistent with what one would expect from established group-equivariance principles combined with rotation augmentation. The experiments do not establish a general relationship between folded distance and classification accuracy, and the empirical agreement is not exact.
Consequently, I am unsure how much new understanding this particular analysis contributes beyond existing equivariance theory.
- In continuation with the aforementioned point, Section 4 introduces GCLS as a learned geometric-prior probe involving orientation-constrained sampling and channel-wise alignment. Is GCLS a novel combination proposed by the authors, or an adaptation of established mechanisms? Since the main contributions stated in the Introduction do not emphasize a new architectural mechanism. I would suggest that the authors clarify this.
Some other comments.
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Although the authors provide detailed experimental configurations, the motivation for selecting 30 training epochs is unclear.
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The time-matched experiments partly address computational fairness, but they do not establish whether either architecture has saturated in training or validation performance. I would particularly appreciate it if the following experiments could be included. a. Validation accuracy versus training time for plain ResNet-18 and C4, preferably under the same computational budgets. b. Training-loss curves to understand convergence and optimization behavior.
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Sections 5 and 6 explicitly discuss robustness under rotation-induced distribution shifts. This raises an important question about the paper's positioning relative to established methods for handling distribution shifts. The experimental comparisons primarily consider conventional augmentation, additional training, and test-time prediction averaging. However, unsupervised domain adaptation and test-time adaptation are also established approaches for addressing changes between training and deployment distributions.
I acknowledge that these approaches operate under different assumptions, particularly regarding access to unlabeled target-domain data. Therefore, I am not suggesting that they must necessarily be included as additional baselines. Nevertheless, I would encourage the authors to discuss how these approaches relate to, or could complement, the geometric priors examined in this paper. Such a discussion would help readers understand the positioning and practical relevance of the proposed evaluation framework within the broader literature on distribution-shift robustness.
Questions for authors
Overall, the paper is well written, with most critical details included in the main draft or the appendix. However, I have some concerns about the paper's overall motivation and novelty and would like the authors to clarify them. Please refer to the critical weaknesses of the paper for the main questions.
2 comments
Response to the Authors' Rebuttal
Thank you to the authors for the response and for conducting the additional experiments. In particular, I appreciate the additional experiments and the authors' transparent reporting of their limitations, including the retrospective selection of the best-performing augmentation range. The revised empirical question is more concrete, and the contrasting results between CIFAR-10 and ImageNet-100 are informative.
I have considered the new results, and while they provide some useful additional evidence, I feel that my two principal concerns regarding motivation and novelty remain only partially addressed.
- The new cross-support comparisons, particularly the observation that broader augmentation allows the plain model to surpass C4@30 on CIFAR-10, are helpful. However, my original concern was questioning the practical significance of treating angular training coverage as a resource to be saved.
For example, if generating training images with rotations within ±90° is not more expensive than generating images within ±30°, then what practical advantage does the narrower training coverage offer? This is particularly important as the equivariant architecture itself incurs substantially higher computational costs. I would have appreciated a clearer explanation of what practical model-selection or deployment decisions this metric enables beyond the accuracy-versus-computation comparisons already available.
- I appreciate the clarification that the folded-distance identity is established mathematics and that the contribution lies in the fixed-image support intervention and the measured substitution boundaries. However, this does not fully address my original question regarding novelty.
My concern is not that the authors reuse established equivariance principles, but rather what fundamentally new understanding the proposed evaluation provides beyond existing research on equivariance, augmentation, and data efficiency.
The new substitution-boundary experiments are informative, but I would have appreciated a more explicit comparison with closely related prior work, explaining what existing evaluations could not establish and what additional insights the proposed framework enables.
- I appreciate that the authors have collected additional training-objective and held-out monitoring trajectories. However, the response still does not clearly explain the original choice of 30 training epochs. Furthermore, as the authors acknowledge, the monitoring trajectories do not establish convergence.
Response to Reviewer kPKz: practical significance and training-budget evidence
Thank you for asking what decision the support axis informs. We have completed additional experiments and prepared a revised manuscript. Its central question is: if broader augmentation is available, can it recover a measured prior working point after allowing additional training and orbit averaging?
The completed sweeps give different answers. For the original five angles with border padding on CIFAR-10, plain+TTA4 at T90 reaches 91.935%, above C4@30 at 90.697%, despite a 14.83-point deficit at the same T30 support. Under the same angle/operator choice on ImageNet-100, our new 30-run sweep shows that C4@30 reaches 78.933%, while the best observed plain+TTA4 band is T90 at 77.325%. The mean paired gap is 1.608 +/- 0.228 percentage points, with sample SD over three seed contrasts. Its direction remains positive for every seed under both operators and both angle cohorts. The best support is a retrospective test-score choice; this SD does not quantify selection uncertainty. C4@15 is replaceable on both datasets, so the finding concerns a measured substitution boundary rather than universal architectural superiority. It distinguishes which narrow-support gains survive an available broader-support alternative. Angular support is not interpreted as saved labels or compute.
We recorded training-objective and upright held-out monitoring trajectories for all 30 new ImageNet runs, and recovered training-objective trajectories for all 45 CIFAR runs. Plain receives approximately 172.57–173.40 epochs within its paired C4 training-region time. The models use their final-budget checkpoints; monitoring never selects them. The ImageNet monitoring reuses the existing evaluation split, so it does not supply independent validation or prove convergence. Training-time matching is within each support/seed pair, with actual cross-support times reported separately.
The folded-distance identity is standard and is used only to organize observed curves. The empirical contribution is the fixed-image support intervention and the different complete substitution boundaries under specified budgets. GCLS remains a specified task-dependent diagnostic probe. We also added the relation to domain adaptation and test-time adaptation, which alter access to target observations or model updates.