- Rating
- 3
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 3
- Soundness
- 2
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Paper summary
Representing data as equivalence classes is effective in reducing redundancy; however, existing group-based works are restricted by the definition of group actions. Thus, such previous works cannot be applied to tasks where defining a group action is difficult, such as natural language. The authors propose a novel approach to identify equivalence classes and construct a quotient space directly from observations rather than relying on predefined transformations. Then, a conditional flow matching model generates realizations along the horizontal and vertical directions of the fiber.
Critical strengths
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I think that constructing a quotient space without explicitly defining a group is, ironically, a promising way to implement the effects of group actions. In many cases, we do not require the explicit group representation itself. Thus, I think this work provides a solid starting point for such a research direction.
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The theoretical setup and results, as well as the implementation with flow matching, are solid.
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The empirical evidence is sufficiently broad and shows clear improvements.
Critical weaknesses
- In the second paragraph of Section 3.3, the existence of a "constant rank " is not guaranteed. The authors commented on this in the Appendix; however, this issue should be treated more carefully because the proposed method relies on the constant-rank theorem. I think that stating an explicit assumption would alleviate this issue.
- In Table 3 and Table 4, the SR is noticeably low except for the 3 Joint + obs case.
Questions for authors
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Regarding W1: Can you show the rank stability and the singular value distribution on actual data, even in a simple case?
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How do approximation errors in the learned quotient map affect the topology and geometry of the resulting fibers?
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Regarding W2: Is there a trade-off between SR and SW?
3 comments
Thank you for the detailed rebuttal and additional experiments. My main concerns have been addressed.
One additional question came to mind regarding computational cost. Have you measured the computational overhead of the proposed method compared to the baselines, particularly in terms of training and inference time? If so, a brief explanation would be helpful.
Response to Official Comment by Reviewer 3G6G
Thank you for this question, and we are glad that all the main concerns have been addressed.
We measured both the additional geometry/preparation cost and complete sampling cost of the heaviest experiment, which is the spatial arm experiment, using RTX 5090, Xeon Silver 4510, CUDA-synchronized timing. Our generator is small and cheap to train, but the method adds offline preparation and a one-time local decoder construction per new target pose (~239 s). The extra computation buys fiber preservation and control.
Inference vs native baselines (2048 output)
| Method | Per-target setup (s) | Sampling (s) | SR (%) |
|---|---|---|---|
| IKFlow + native refinement | – | 0.32 | 93.87 |
| GGIK | – | 0.13 | 0.03 |
| Ours | 238.56 | 0.80 | 97.95 |
Setup is performed once per target and reused across batches. The native baselines are run without our terminal projection, which explains GGIK's low success (with projection (Tab. 12), GGIK reaches 99.35%).
Training vs native baselines
| Component | Ours | IKFlow | GGIK |
|---|---|---|---|
| Outcome-map training | 20.2 min | – | – |
| Training-bank preparation | 48.4 h (summed over parallel jobs) | released data | released data |
| Generator training | 7.0 min | not measured | not measured |
| Forward/backward, batch 512 | 2.19 ms | 21.75 ms | 152.77 ms |
The outcome map and banks are shared with the learned geometry baselines in Tab. 4, but are additional cost relative to IKFlow and GGIK. Bank preparation constructs the cost weighted training configurations on each fiber and is run as parallel jobs, and the 48.4h is the total duration of the bank preparation (12.1h on 4 GPUs).
Methods sharing our local geometry
| Method | Generator training (min) | Sampling (s) |
|---|---|---|
| RFM (adapted) | 175.96 | 3.99 |
| PCFM (adapted) | 24.13 | 7.06 |
| Ours | 7.01 | 0.80 |
RFM and PCFM here uses our local geometry and decoder, so preparation costs are shared. Ours learns a scalar local coordinate and decodes once, while RFM builds numerical geodesic training paths and PCFM repeatedly corrects configurations during sampling.
Response to Reviewer 3G6G
Thank you for your insightful review and encouraging assessment. We appreciate your recognition of our theoretical contributions, flow-matching implementation, and broad empirical validation. Your questions regarding rank stability, quotient-map approximation errors, and the trade-off between success rate and distributional fidelity are particularly valuable. Below, we address each point in detail.
We agree that the constant-rank assumption should be explicit and have revised Sec. 3.3 to explicitly restrict each local decoder to a C2, constant-rank region Ui, without crossing rank-changing boundaries. Rank may vary across regions, including ri=k (zero-dimensional fibers). To empirically assess this assumption, we evaluated 6,000 held-out Panda configurations across three seeds. All exhibited learned rank 6 at threshold 10−7, with minimum σ6=3.60×10−4 (Sec. 4.3). The learned singular-value distributions closely match analytical kinematics.
We further tested local rank stability using 16 directional perturbations per center at varying normalized joint-space radii.
These results support local rank stability within the tested neighborhoods, without claiming globally constant rank or guaranteeing regularity at untested points.
Approximation errors in the learned quotient map can shift fibers and misalign their tangent spaces. Near singularities, they may also alter fiber connectivity or dimension, so global topology preservation is not guaranteed. Empirically, the learned Panda nullspace closely matches analytical geometry, with a median angular error of 0.61°, mean of 1.61°, and 95th percentile of 5.83°. We further evaluate physical position error under finite displacement using identical learned geometry.
At 70% of the chart radius, implicit decoding reduces physical error from 4.430 mm to 0.638 mm, remaining close to the initial 0.627 mm error (Fig. 7, App. C.4). This demonstrates that the nonlinear correction limits additional drift despite approximation errors, supporting local geometric fidelity without claiming global topological guarantees.
We clarify that our method achieves 99.99% SR on 3J, 97.09% on 3J with obstacles, and 95.18% on Panda, with a lower 75.13% on 4J. Where ours is not the highest, the SR gap is at most 0.85 points, while our SW₁ is the lowest in all settings. Notably, all projection-based baselines exhibit similarly reduced 4J success rates (75.55–75.98%), suggesting a shared experimental difficulty rather than a limitation specific to our method. This is associated with the learned outcome map, whose mean endpoint error of 0.754 mm is close to the strict 1 mm tolerance, and exact geometry restores 100% success for both ours and FM with final projection.
Regarding the trade-off, SR measures task feasibility and target satisfaction, whereas SW₁ measures distribution accuracy. There is no inherent trade-off between them. In the matched exact-geometry ablation (Tab. 14), all variants achieve 100% validity, while SW₁ and component TV improve substantially. Similarly, in Tab. 13, all local-geometry baselines achieve 100% validity, while ours achieves the lowest SW₁ and component TV. Tab. 14 is attached below for reference:
These results demonstrate that distribution fidelity can improve without sacrificing feasibility, rather than implying an unavoidable trade-off between SR and SW₁.