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Under review as a conference paper at ICLR 2027

Measuring Transformation-Coverage Savings from Geometric Priors: A Fixed-Data Evaluation of Equivariance, Augmentation, and Capacity

Abstract

Geometric priors can reduce the range of transformations needed during training, but measured savings depend on the baseline's training and inference budgets. We evaluate this dependence by fixing image count and test transformations, varying training rotation coverage, and recording the smallest sampled training half-width that reaches a shared accuracy target. A 60-run ImageNet-100 grid and a separate 45-run CIFAR-10 replication both show that exact saves an average of 156 degrees of training-band half-width on five test angles at a fixed epoch budget. Stronger baselines change the interpretation. On ImageNet-100, a plain model trained for the measured time and evaluated with four-view averaging reaches 10 of 11 fixed-epoch targets from the augmentation cohort at a half-width of 30 degrees, while retains accuracy advantages of 4.03 percentage points at that width and 2.97 percentage points at full coverage. On CIFAR-10, the corresponding advantage falls from 14.83 percentage points at 30 degrees to 0.07 percentage points at 90 degrees. Against the stronger full-band target, the primary operator gives 42 degrees of mean per-angle saving but zero saving for the macro-average target; crossings under the alternative operator and at the seed level are partly censored. These results expose sensitivity to the target and sampled grid. Separate learned-prior controls find smaller gains on hierarchical backbones than on flat networks and matched tasks. Coverage savings at fixed epochs therefore need not imply persistent accuracy gains under stronger baselines; transformation support, computation, uncertainty, and implementation fidelity must be reported together.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Equivariance, geometric priors, transformation coverage, data augmentation, distribution shift, computer vision

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_kPKzOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
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.

  1. 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.

  2. 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.

  1. 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.

  1. 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.

  1. 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.

  1. Although the authors provide detailed experimental configurations, the motivation for selecting 30 training epochs is unclear.

  2. 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.

  3. 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
AuthorsOpenReview ↗

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.

Reviewer_kPKzOpenReview ↗

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.

  1. 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.

  1. 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.

  1. 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.
Reviewer_t9wrOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper holds the number of training images and the test rotation angles fixed while varying the training rotation range to measure the transformation coverage saved by geometric priors in reaching a shared accuracy target. Results on ImageNet-100 and CIFAR-10 show that these savings depend on the training budget, test-time augmentation, and target accuracy. The paper also compares the benefits of learned geometric priors across different networks and tasks.

Critical strengths
  1. I appreciate the separate treatment of training transformation coverage and the number of training images, as well as the authors’ decision to retain results that reduce the previously observed advantages after stronger baselines are introduced.
  2. The controlled comparisons are fairly extensive. In addition to fixing the number of training epochs, the authors compare wider standard networks, matched training time, and four-view prediction averaging. The full CIFAR-10 sweeps separately report the effects of additional training and test-time augmentation (Tables 11 and 12), making the changes across budget configurations clear.
  3. The results establish clear limits to the benefits. With matched training time and four-view averaging, C4 retains an advantage of 4.03 percentage points on ImageNet-100 at a training half-width of 30 degrees and 2.97 percentage points at full coverage (Table 2). On CIFAR-10, the gap approaches zero as coverage increases (Table 3). The authors also explicitly distinguish similar accuracy from statistical equivalence.
Critical weaknesses
  1. Uncertainty in coverage savings under the stringent accuracy target is insufficiently quantified. In Section 3.3, under border padding, averaging the angle-wise savings for the same CIFAR-10 results yields 42 degrees, whereas averaging accuracy first and then computing the savings yields zero. These are different statistics, not a computational contradiction. However, at 90 degrees, C4’s macro-averaged accuracy is only 0.014 percentage points below the target, indicating that the threshold-crossing location can be sensitive to very small changes in accuracy. The authors report this issue. Nevertheless, Appendix D of the supplied PDF does not list the per-seed threshold crossings and failures to reach this stringent target. Table 23 concerns the ImageNet fixed-budget experiments and does not address this uncertainty. I would like to see results under reasonable accuracy tolerances and an account of how variability in the estimated target itself affects the coverage savings.
  2. The learned-prior experiments lack sufficient methodological detail. Section 4 only outlines GCLS’s local orientation sampling and low-rank channel alignment, without adequately specifying the orientation predictor, low-rank dimensionality, computation of the alignment operator, or insertion points and training configurations across tasks. The list of script names in Appendix B cannot substitute for these definitions. The capacity sweeps and data-scarcity controls are helpful, but it remains difficult to determine how much of the variation in gains across networks comes from the prior itself and how much comes from implementation or optimization settings. This limits the verifiability of the learned-prior contribution.
  3. Generalizations in the appendix figures go beyond what the main text supports. Figure 8 (p. 25) states that “wherever augmentation helps, the prior is redundant,” although its caption explicitly acknowledges that the separate experimental branches do not measure their combined effect. The title within Figure 11 (p. 27) attributes soft-prior gains to capacity and robustness to equivariance by construction, whereas Section 6 explicitly states that this decomposition cannot identify causal mechanisms. The figures and main text therefore offer different practical guidance. The statements within the figures should be restricted to the measured conditions. Retaining the redundancy claim would require a prior-plus-augmentation comparison on the corresponding elastic-deformation task; the rotated-MNIST combination experiment does not directly answer this question.
Questions for authors
  1. For the stringent CIFAR-10 target, could the authors report each seed’s target value, threshold-crossing location, and whether the target was reached, and show how the results change under pre-specified accuracy tolerances?
  2. The ImageNet-100 comparison with matched training time currently covers only training half-widths of 30 and 180 degrees. Are results available at narrower and intermediate coverage levels to determine how much coverage is still saved under the strong-baseline conditions? I recognize the reported accuracy advantage, but it does not replace a measurement of coverage savings.
  3. Could the authors fully specify the GCLS operator and experimental configurations, and explicitly withdraw or qualify the generalizations in Figures 8 and 11 that go beyond the measured results?
Reviewer_ZfwpOpenReview ↗
Rating
2(+1)
Confidence
4
Informativeness
1
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies how geometric priors reduce the range of training transformations needed to reach a shared accuracy target, while keeping the number of original images and the test transformations fixed. It defines coverage savings through the first sampled training rotation half-width that reaches the target. Experiments on ImageNet-100 and CIFAR-10 compare conventional and equivariant networks, with additional controls for augmentation, matched training time, four-view averaging, and rotation operators. At a fixed epoch budget, C4C_4 substantially reduces the required coverage. Under stronger conventional baselines, the advantage depends on the dataset, accuracy target, and transformation implementation. A separate suite examines GCLS and other geometric mechanisms across backbones and tasks.

Critical strengths
  1. The paper includes augmentation, matched training time, and four-view inference controls, with training and inference costs reported separately. These comparisons help identify how the observed benefits depend on the available resources.
  2. Per-seed results and negative findings are reported transparently. The authors distinguish exploratory analyses from fixed protocols and avoid treating nonsignificant differences as evidence of equivalence.
Critical weaknesses
  1. The background and reference coverage are limited, particularly for recent work on geometric priors and equivariant visual backbones. This weakens the positioning of the research gap and the claimed contribution.
  2. The study mainly compares existing architectures and training strategies, with GCLS serving primarily as a probe. It does not clearly establish a methodological improvement or sufficiently new insight beyond the known dependence of equivariance benefits on comparison budgets.
  3. The main text relies heavily on tables, making the central comparisons difficult to follow despite the plots in Figure 1 and the appendix. Clearer visual summaries and a stronger explanation of how the experimental components connect would improve readability.
  4. Under the stronger CIFAR-10 reference, mean per-angle savings are 42 degrees, whereas crossing the macro-average target yields zero savings. The sparse grid, strict threshold, and incomplete ImageNet-100 matched-time sweep limit robust quantification of the remaining coverage advantage.
Questions for authors
  1. What specific gap remains after recent work on equivariance, canonicalization, and augmentation-compute comparisons? How does the fixed-data coverage protocol address that gap?
  2. What is the main new insight, and what practical decisions does it support? Is GCLS a methodological contribution or mainly a diagnostic probe?
  3. How are the rotation-coverage and learned-prior experiments intended to inform each other? Could a concise visual summary clarify their main trends and motivating relationship?
1 comment
AuthorsOpenReview ↗

Response to Reviewer Zfwp: contribution, related work, and complete evidence

Thank you for asking us to identify the insight beyond the known role of training and inference budgets. We have completed additional experiments and prepared a revised manuscript with stronger evidence and clearer positioning.

Brehmer et al. already study equivariance/data/compute trade-offs, and Adly studies target crossings, sensitivity, and orbit averaging. We now discuss these explicitly, alongside learned canonicalization and recent equivariant visual backbones. Our controlled axis varies training transformation support while keeping original image identities and test transformations fixed. The new complete comparison asks which measured prior working points broader augmentation can replace, after specifying training and inference alternatives.

The added evidence establishes different substitution boundaries despite the same historical 156-degree fixed-epoch headline. On CIFAR-10, plain+TTA4 recovers C4@15 and C4@30 using T45 and T90 on the original angles, under both operators and every paired seed. In a fresh complete 30-run ImageNet-100 sweep, all five bands and three seeds have new paired C4/plain runs; plain receives its paired C4 training time and TTA4. Plain recovers C4@15 using T30, but no tested plain support recovers C4@30. On the original five angles with border padding, C4@30 exceeds the best observed plain band, T90, by 1.608 +/- 0.228 percentage points (sample SD of three paired contrasts). The direction remains positive for every seed under both operators and both angle cohorts. Thus neither the fixed-epoch headline nor a large same-support gap determines whether the available broader-support alternative can recover the prior's accuracy.

We enumerate all measured working-point substitutions and complete target regions, retaining operator differences, nonmonotonic curves, seed variation, and unattained targets. These are empirical diagnostics over the measured candidates; standard generalized-inverse mathematics supplies their interpretation. The best-over-support score is a retrospective test oracle, with independent selection uncertainty left outside the reported seed SD.

The opening figure in the revision we have prepared directly contrasts the two complete accuracy curves. An evidence map connects this primary support comparison with the supporting orientation-module and generator audits. We moved the descriptive OOD decomposition to the appendix and retain nine main-content pages. GCLS and the generator audits serve as supporting diagnostics. The contribution is a complete, fixed-data characterization of which prior working points broader augmentation recovers under the measured training and inference alternatives, including contrasting replacement boundaries across the two datasets.

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

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