- Rating
- 2
- Confidence
- 3
- Informativeness
- 2
- Presentation
- 2
- Soundness
- 2
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Paper summary
This paper proposes Fast Learning via Adaptive Rank Estimation (FLARE), which is an adaptive data-budget estimation method for conditional GANs. FLARE estimates the required sample count for each condition using the effective rank of centered per-sample critic gradients rather than selecting which samples to retain under a predefined budget. In addition, FLARE reallocates the total budget toward poorly modeled conditions based on global sliced-Wasserstein similarity. On optiGAN, FLARE uses about 1% of the optical photon simulation data and achieves a 19x training speedup while maintaining comparable generation quality. On CaloShowerGAN, χ²/NDF increasing from 1.56 to 5.39. On CTGAN, macro F1 improves from 0.518 to 0.570.
Critical strengths
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The paper addresses the practically relevant question of automatically determining data budgets for conditional generative models. It is interesting about the observation that uniform random sampling can match or outperform several sophisticated membership-selection methods.
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The paper provides multiple random-seed experiments, statistical comparisons, and detailed computational cost analyses.
Critical weaknesses
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Most components of FLARE are based on established methods.
(1) automatic coreset sizing has been investigated by Xia et al. [1]
(2) the spectral energy criterion (Eq. 2) follows standard PCA explained-variance selection, while the entropy-based effective rank (Eq. 3) is directly from Roy and Vetterli [2];
(3) performance-aware, class-wise data allocation and random sampling have been explored by DRoP [3] and RCAP [4].
Therefore, FLARE appears primarily to combine existing techniques rather than introduce fundamentally new mechanisms. -
The main novel component is mapping the effective rank of critic gradients directly to the required number of training samples. However, the paper provides no convincing mathematical justification for why the number of dominant gradient directions should determine the sample complexity of learning a conditional distribution.
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On optiGAN, FLARE uses smaller batch sizes than full-data training, but a full-data baseline with matched small batches is missing. Fixed random sampling across different budget fractions is also insufficiently explored. Furthermore, CaloShowerGAN shows substantial quality degradation (chi-squared/NDF: 1.56 to 5.39), while CTGAN's macro-F1 improvement may primarily result from class rebalancing, with worse sliced-Wasserstein distance.
References
[1] Xia et al., Refined Coreset Selection, ICML 2024.
[2] Roy and Vetterli, The Effective Rank: A Measure of Effective Dimensionality, EUSIPCO 2007.
[3] Vysogorets et al., DRoP: Distributionally Robust Data Pruning, ICLR 2025.
[4] Hassan et al., RCAP: Robust, Class-Aware, Probabilistic Dynamic Dataset Pruning, UAI 2025.
Questions for authors
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Could the authors clarify how FLARE differs fundamentally from existing coreset sizing methods [1] and performance-aware class-wise allocation methods [4, 5], beyond combining these techniques with spectral rank estimation?
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What theoretical or empirical evidence supports using the effective rank of critic gradients as the required number of training samples?
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Could the authors compare FLARE against full-data training with matched small batch sizes and fixed random sampling at different budget fractions?
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Could the authors clarify whether the CTGAN improvements come from spectral sizing rather than simple class rebalancing, and explain the substantial quality degradation on CaloShowerGAN?
3 comments
Thank you for the detailed rebuttal and additional experiments. I appreciate the authors' efforts to address the concerns regarding novelty, mathematical justification, and experimental fairness.
First, the clarification of FLARE's relationship to prior work is helpful. The authors acknowledge that the spectral estimators and performance-aware allocation strategies are established techniques, and appropriately narrow their novelty claims. The new comparisons with matched small-batch training and fixed-budget random sampling also address important experimental concerns.
However, my main concerns remain unresolved. The new experiments show that a fixed 1% budget with the same allocation strategy can match FLARE on optiGAN, while DRoP- and RCAP-style allocation achieves comparable or better results. This suggests that the benefits of the proposed spectral sizing mechanism remain insufficiently isolated from existing allocation strategies. Moreover, preserving 99.6% of gradient spectral energy does not establish why effective rank should determine the training sample budget. The reported sensitivity to critic width further raises concerns about the robustness of this heuristic.
Finally, the cross-domain evidence remains limited. CaloShowerGAN still exhibits substantial quality degradation, while the authors acknowledge that CTGAN's improvements mainly result from class rebalancing rather than spectral sizing.
Overall, the central methodological contribution and its advantages over simpler alternatives are still not sufficiently established. Therefore, I maintain my original rating of 2 (Weak Rejection).
Thank you for reading the new results. You noted that a fixed 1% budget with the same allocation matches FLARE on optiGAN. It does, but only within one pool. The same 1% fell short of full data on a quarter of the pool and beat it on five times the pool. FLARE's row count stayed within about 5% of its value on the original pool (general follow-up).
The DRoP- and RCAP-style splits did about as well as our tilt. We no longer claim the split, and the revision credits it to DRoP and RCAP. With FLARE setting the total in the same run, both matched what they did at a fixed total.
We agree that keeping 99.6% of the gradient energy does not explain why the effective rank should set the budget. The revision presents the rank as a size rule backed by experiments, not a derived count. Its sensitivity to critic width, the CaloShowerGAN gap, and CTGAN's rebalancing stay as stated limitations.
Our first reply kept the closed-form per-sample gradient as a second claim while a comparison with automatic per-sample differentiation was in progress. That comparison went against it. We withdraw the claim (general follow-up). We also called the paper's baseline a per-sample loop, but it looped over micro-batches of 8 rows.
Thank you. We agree with most of the component list and have narrowed our claims to match.
The energy rule is PCA's explained variance and the entropy rank is Roy and Vetterli's, and we credit both as standard. RCS (Xia et al.) makes the size an output, so that idea is theirs. It refines a size the user provides, by a search that retrains for each candidate. FLARE needs no starting size and no search. It reads the total training budget from the critic's gradient spectrum during one training run. That is our main claim. The closed-form per-sample gradient with the penalty term, which makes the sizing cheap, is our second. Classifier pruning already uses last-layer per-sample gradients, but its losses have no gradient penalty, so the penalty term's closed form is the new part. The paper times it only against a per-sample loop, and a comparison with automatic per-sample differentiation is in progress.
DRoP and RCAP take the pruning rate as given and split it across classes. Our reallocation toward poorly fit conditions (the tilt) was a version of the same idea, so the split is not our contribution. We ran their allocation rules with each condition's sliced-Wasserstein error in place of class accuracy, and they do as well or better. Given FLARE's total on optiGAN, the DRoP-style split is equivalent to FLARE on the worst quartile, and the RCAP-style comparison is inconclusive. Both cost less recall than our tilt. On CTGAN the RCAP-style split of random rows sits 0.04 to 0.06 macro F1 above FLARE's own split. The revision therefore pairs FLARE's total with these splits (general response). FLARE supplies the rate they take as given. Two experiments in progress test that directly. One runs these splits at totals below and above FLARE's on optiGAN. We expect them to need a total as our own rule did, but that is untested. The other runs FLARE's sizer and the splits together, since the runs above used a fixed total equal to FLARE's average budget. If there is a comparison with these methods that you would like to see in the revision, we are open to running it.
Not citing RCAP was our oversight. This project began as an attempt to adapt GradMatch, a subset-selection method built for classifiers, to optiGAN. It did no better than random subsets, and the other classifier-derived selection rules we tried skewed each condition's distribution. We then assumed that class-wise pruning rules such as DRoP and RCAP would not carry over to generators either, and we never tested them. The runs above show that assumption was wrong.
We have no bound linking the rank to a sample count, and we drop "the required number". The GAN sample-complexity bounds we know of hold over a whole critic class and do not use a measured rank. So the revision presents the rank as a size rule with evidence. A uniform subset of FLARE's size keeps 0.996 of the spectral energy of the pool's per-sample gradients, against 0.999 at best. FLARE's budget is also the smallest multiple we tested that is equivalent to full data on the worst quartile. An experiment in progress changes the pool size. If the size that works is a row count read from the model, it should stay put while a fixed ratio moves with the pool.
We ran both baselines you asked for. Full-pool training at FLARE's batch and step count is as fast as FLARE and about 0.016 lower on the worst quartile. Random subsets from 0.25% to 4% never reach full data on that endpoint. FLARE beats random at 1, 1.47, and 2%, and its budget never goes above 2%. A guessed 1% that keeps FLARE's tilt ties FLARE, and we report that. Run at six sizes, that guess falls short of full data at 0.5% and below and reaches it from 1% up. It still needs a total, and FLARE's lands in that range.
On CTGAN the gain is class rebalancing, as you suspected. Random rows at FLARE's total in the pool's proportions show no detectable difference from full data, and halving or doubling that total made none either. Runs at smaller totals are in progress. Random rows at the same total under a DRoP- or RCAP-style split keep the sliced-Wasserstein distance at full data's level, so the worse distance comes from our split and not from the small budget. On CaloShowerGAN, FLARE's subset at full data's batch did not close the gap, so the batch alone is not the cause. It stays a stated limitation.