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Under review as a conference paper at ICLR 2027

No Free Efficiency: Revisiting the Trade-off Between Training Efficiency and Model Vulnerability

Abstract

Training efficiency has become the central driver of recent progress in foundation models. To overcome the massive computational and data requirements of large-scale training, researchers increasingly adopt strategies such as selective data sampling, efficient pre-training, and simplified reinforcement learning pipelines. While these strategies drastically reduce overhead, they prompt a critical, yet neglected question: Is efficiency achieved at the expense of model robustness and security? To our knowledge, we present the first systematic cross-domain investigation of the efficiency–vulnerability trade-off. Across vision and language models, we show that efficiency-oriented training increases susceptibility to adversarial and privacy attacks. We characterize this vulnerability by analyzing the models’ internal geometry and functional representations, demonstrating that the evaluated efficient variants consistently exhibit sharper loss geometry together with systematic changes in representational structure. We further extend our analysis to "zero RL training", finding that models trained using simplified RL recipes exhibit substantially greater susceptibility to catastrophic forgetting and more pronounced overconfidence than those trained through conventional alignment pipelines. Our findings suggest that training efficiency is rarely a “free lunch”; rather, the mechanisms that minimize computation can inadvertently compromise safety. We conclude by calling for a paradigm shift toward multi-objective training that jointly optimizes for performance, cost, and security.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
Efficient training, No free efficiency

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_LrM6OpenReview ↗
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2
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Informativeness
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Paper summary

This paper argues that strategies for improving training efficiency come with security costs. It compares Shapley-based data selection and pre-train-then-finetune against utility-matched baselines on small vision benchmarks, and zero-RL math LLMs against an instruct model, measuring data privacy, model robustness and resilience, and proprietary security. The efficient variants are generally more vulnerable, which the authors relate to sharper loss landscapes, worse calibration and more compressed representations.

Critical strengths
  1. The question is timely and relevant, and the study covers several training stages, two domains and a wide range of attacks.
  2. Matching clean accuracy between the efficient and baseline models is a reasonable way to separate security effects from utility. The paper also goes beyond reporting attack numbers by looking at loss sharpness, calibration and representation structure, which gives some intuition for the observed trends.
Critical weaknesses
  1. The claim of being the "first systematic study" feels too strong given the scale of the evaluation types and experiments. The vision experiments use ResNet-18/Swin-Tiny on small subsets of CIFAR-10, TinyImageNet and PubFig83, with about 36-48% test accuracy and nearly 100% training accuracy, which is far from foundation-model training. The LLM part compares only three existing checkpoints. The paper frames its contribution around foundation-model development, but the evidence is far from that setting.
  2. Several measurements are not convincing. Many membership-inference TPRs at 0.1% FPR are around 0.1%. The models are standard non-robust ones, so under ε = 8/255 PGD they break within a few steps anyway (0.11-3.85 correctly classified iterates out of 40, apart from TinyImageNet), which makes the differences hard to interpret. For the LLMs, all models are already easy to jailbreak (91.9% ASR for the instruct baseline), and the comparison does not separate the effect of zero-RL from other differences in data and training pipeline. The MIA conclusion also depends on which attack is chosen.
  3. The claimed theoretical intuition (App. A) consists of post-hoc interpretations based on existing results, without formal links between efficiency choices and vulnerability or interventions to test them.
Questions for authors

Address the weakness issues raised in Critical weaknesses session.

6 comments

Thank you for the careful review.

W1a — "the claim of being the 'first systematic study' feels too strong"

Our intended claim is that this is the first study to connect the efficiency and security question across training stages and domains under matched utility. Prior work examines individual mechanisms in isolation, for example data selection and privacy, or compression and robustness, and Sec. 2.2 reviews why these fragmented results do not compose into a picture of the training pipeline. The systematic part of our contribution is the common protocol that spans the pipeline: the same utility-matched evaluation is applied to data selection, pre-training, and alignment, in both vision and language, and probes each model's privacy, robustness, extractability, jailbreak resistance, and adaptation stability. To our knowledge, no prior work provides this combination. We will make the wording precise in the revision, claiming the first cross-stage and cross-domain analysis at matched utility, and add a Limitations paragraph clarifying the scope: the vision experiments are controlled studies designed for exact utility matching, the LLM analysis covers publicly released models at two scales (7B and 32B), and extending the study to frontier-scale training is left as an open direction.

W1b — "about 36-48% test accuracy and nearly 100% training accuracy, which is far from foundation-model training"

The low accuracy is a consequence of the matching protocol: disjoint Shapley subsets are calibrated until training and test accuracy coincide, which caps the subset size. Within each pair the two models therefore have identical generalization gaps, so the vulnerability differences cannot come from different degrees of overfitting. The appendix also covers a high-accuracy regime: full-data training (94.8% accuracy) vs. High-Shapley subsets of 40,000 (93.4%) and 20,000 (88.5%) shows the same monotone increase in leakage (0.02%, 0.04%, 0.07% MIA TPR, Appendix Table 9). On the framing: the studied strategies come from foundation-model practice, but isolating their security effect requires controlled training, so our evidence is two-level by design, controlled vision studies plus released 7B and 32B models showing the same pattern.

W1c — "the LLM part compares only three existing checkpoints"

The number of models follows from the same control that governs the vision experiments: compared models must reach comparable clean utility, otherwise security differences are confounded by capability. We evaluated a broader set of publicly released aligned math models as candidates, including zero-RL models built on other base families and at other capability levels, and only these three satisfy the requirement, with a baseline gap of at most 2.4 points on the seven-benchmark average (Table 5). The comparison is small because the inclusion criterion is strict, not because the evaluation is. Within the three, the two efficient pipelines were developed independently with different data and reward designs, so the shared vulnerability pattern is a replication across pipelines rather than a single observation, and the appendix repeats the comparison at 32B with the same result.

W2a — "many membership-inference TPRs at 0.1% FPR are around 0.1%"

The quantity our claim rests on is the relative leakage between utility-matched pairs, and this ratio is far from random even where absolute values are small. At 0.1% FPR, random guessing gives 0.1% TPR. The High vs. Low values are 1.51% vs. 0.32% on PubFig83 (15x vs. 3x random), 0.29% vs. 0.08% on CIFAR-10 with Swin, 0.22% vs. 0.08% on TinyImageNet, and 0.16% vs. 0.12% on CIFAR-10, with seed standard deviations of 0.01 to 0.06 (Appendix Table 7), so the orderings are consistent and well separated. We additionally evaluated a logit-scaled confidence attack of the same family in our re-evaluation pipeline, and it preserves the ordering in every setting: 0.35% (High) vs. 0.17% (Low) on the paper's CIFAR-10 models, 0.34% vs. 0.14% across three retraining seeds, and 1.69% vs. 0.38% on PubFig83. The ordering our conclusion rests on is therefore stable across attacks of this family, datasets, and retraining.

W2b — "under ε = 8/255 PGD they break within a few steps anyway ... which makes the differences hard to interpret"

We agree that white-box PGD at ε=8/255 saturates for these standard models. In our re-evaluation, robust accuracy at this ε is near zero for both compared models, as expected for models without adversarial training, so differences at this operating point are hard to interpret. We therefore evaluate robustness under a black-box threat model, which is non-saturated and matches how a deployed model is actually exposed, through query access only. The attacker first extracts a surrogate with the paper's model-stealing protocol (1,000 disjoint queries), then crafts 40-step PGD examples on the surrogate, and submits them to the target. We report the target's robust accuracy, the fraction of test images it still classifies correctly under these transferred examples (mean over 3 seeds, the two models at matched clean accuracy):

Robust accuracy under black-box attackε=2/255ε=4/255ε=8/255
High33.620.36.4
Low38.425.910.1

The efficient High-Shapley model is consistently more vulnerable, losing 4 to 6 points more robust accuracy at every ε, with the same ordering on the paper's original models. The mechanism is the extraction result itself: the surrogate replicates the High model more faithfully (agreement 0.85 vs. 0.58), so adversarial examples cross both decision boundaries together more often, while the Low baseline is protected mainly by being harder to copy. The representation simplicity that makes the efficient model easier to steal therefore also makes it easier to evade without gradient access, which connects the robustness and extraction dimensions of our study.

W2c — "all models are already easy to jailbreak (91.9% ASR for the instruct baseline)"

We agree that none of the evaluated models is safe in absolute terms. They are math-specialized models without dedicated safety training, so a high eventual attack success rate is expected for all of them. The quantity that still separates the models is attack cost. AutoDAN needs on average 4.32 search iterations to jailbreak the Instruct model but only 0.53 (SimpleRL-Zoo) and 0.41 (PRIME), where a value below 1 means most prompts already succeed within the initial population. The zero-RL models therefore require 8 to 10 times fewer search iterations. This gap is if anything understated, because the averages count only successful prompts and the Instruct model's failed prompts are excluded from its average, and the ASR ordering is consistent as well (100% and 99% vs. 91.9%). In deployment, attack cost determines how many queries a filter or rate limiter can intercept before the attack succeeds, so it is the security-relevant measurement in this regime.

W2d — "the comparison does not separate the effect of zero-RL from other differences in data and training pipeline"

We agree that the LLM comparison is between complete alignment pipelines within the same model family, and we will make this explicit in the revision. First, utility is in fact closely comparable: the three models differ by at most 2.4 points in the seven-benchmark average (Table 5), while the security gaps are far larger, for example a roughly tenfold difference in the attack steps AutoDAN needs and a far larger accuracy drop after identical fine-tuning (Tables 4 and 5). A utility gap this small cannot explain security gaps of that size. Second, as stated in Sec. 3.1, our claim is at the pipeline level: the zero-RL pipelines as released carry a security cost, and we do not attribute this cost to any single omitted component. This matches how these recipes are used in practice, since practitioners adopt a released pipeline as a whole. Accordingly, Sec. 6 discusses the missing KL regularization only as a plausible explanation, not as an established cause. Third, SimpleRL-Zoo and PRIME were developed independently, with different training data, reward designs, and implementations. A factor specific to one pipeline would not affect the other, yet both show the same vulnerability pattern relative to Instruct across all three evaluations. Their shared efficiency-oriented alignment recipe is therefore the most plausible source of the vulnerability.

W2e — "the MIA conclusion also depends on which attack is chosen"

The two attacks measure different leakage channels, and the difference between them has a concrete mechanical cause rather than being a free choice. The answer-likelihood attack scores membership by the probability the model assigns to the static reference solution text. After reward optimization, a zero-RL model solves training problems with its own reasoning paths and phrasings, so its probability on the reference text drops even for problems it has memorized through training. This attack therefore structurally understates leakage for RL-trained models, and comparing an RL model to an SFT-trained Instruct model on it is biased in the Instruct model's direction. The self-confidence attack avoids this by scoring the model's own generated solution, and there the zero-RL models leak more. We note this is not explained by generic overconfidence either, because uniform overconfidence shifts member and non-member scores together, while the attack measures the separation between the two groups. The Min-k% results (Appendix) agree with this picture. We will revise Sec. 6 to state the methodological point explicitly: reference-text attacks are not comparable across training paradigms, so MIA conclusions for RL-trained models should rest on generation-based attacks and on the suite jointly.

W3 — "post-hoc interpretations based on existing results, without formal links ... or interventions to test them"

We agree on both counts. We will no longer label Appendix A as theory: the contribution will be renamed "mechanistic analysis," and its interpretations will be marked as hypotheses grounded in prior results. In addition, we ran the interventional test the reviewer asks for: retraining the High-Shapley model with Sharpness-Aware Minimization, with everything else unchanged, reduces sharpness at matched accuracy and lowers MIA [email protected]%FPR from 0.30% to 0.18%, reaching the Low-baseline level (0.17%), while model stealing and feature dimensionality remain unchanged. The intervention thus supports the sharpness link for privacy and calibration and separates it from the representation-driven extraction risk. The full table and setup are in our response to Reviewer 1 (W3).

Reviewer_7KRNOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper investigates the trade-off between the efficiency and low computational cost of algorithms and their potential drawbacks, such as vulnerabilities in security or privacy. They conduct an extensive cross-domain study into the stages of the training pipeline and examines these trade-offs. They provide intuition for the observed trade-offs and finally examine a potential tension between alignment and security.

Critical strengths

The paper provides a significantly broad study of various trade-offs between efficiency and vulnerability, providing valuable insights.

Critical weaknesses

The paper frames its investigation as structured in the different stages of training at the start; however, this categorisation mostly fades away in the results, which constitute most of the paper.

Some presentation and soundness issues are mentioned in the questions section.

Questions for authors

Tables and figures should be self-sufficient and explain their contents. The table and figure descriptions are too brief and leave too much to the main text.

The difference between the low and high models in Figure 5 seems superficial, and I don't believe it is substantial enough evidence for the conclusions made.

In the paper's contributions, "Theoretical Intuitions" are mentioned, yet no such thing is provided in the paper. Mostly, more empirical results.

3 comments

Thank you for the careful review.

W1 — "this categorisation mostly fades away in the results"

The results follow the stages in order, with Sec. 4 covering data selection and pre-training and Sec. 6 covering alignment, but we agree the categorization could be more visible there. In the revision, each results block will open by explicitly naming its stage, and the conclusion will briefly summarize the findings by stage. We will also clarify the role of Sec. 5 at its beginning: it examines the two strategies side by side because both steer models toward sharper, less stable solutions, and this agreement across stages directly supports our general claim that efficiency strategies make models more vulnerable.

Q1 — "Tables and figures should be self-sufficient and explain their contents"

The main results tables and figures already state the metric and its reading direction, but we agree that several captions, mainly those of the analysis figures, were too brief. In the revision, each of these captions will state what is measured, what the panel labels refer to, and how to read the metric. Detailed experimental settings will remain in Sec. 4.1 and the appendix so that captions stay concise.

Q2 — "The difference between the low and high models in Figure 5 seems superficial"

We quantified the comparison. Summarizing each heatmap by the mean pairwise CKA among the last four blocks, the difference is clear on CIFAR-10 (0.84 for High vs. 0.74 for Low) but not evident on TinyImageNet (0.73 vs. 0.72). We therefore added a direct layer-wise test of the claim: the PCA participation ratio, the number of directions that effectively carry the feature variance, at every compared block rather than only the penultimate layer as in Table 3:

Layer-wise PCA-PR (lower = more concentrated)layer2.1layer3.0layer3.1layer4.0layer4.1
CIFAR-10 High4.45.53.58.911.2
CIFAR-10 Low33.025.441.139.121.7
TinyImageNet High22.625.250.359.394.6
TinyImageNet Low53.657.8131.8163.5224.8

At every layer and on both datasets, the High model uses severalfold fewer feature directions (e.g., 3.5 vs. 41.1 at layer3.1 on CIFAR-10), and the ordering is stable across three retraining seeds. Fewer effective directions mean a surrogate has less to match, which explains the higher stealing success in Figure 2. The values follow Table 3's feature convention and are for the single models shown in Figure 5.

Q3 — "'Theoretical Intuitions' are mentioned, yet no such thing is provided"

We agree that "theoretical intuitions" is not the precise term for this contribution. What the paper provides is interpretations grounded in established theory, connecting each observation to known results: margin maximization for the calibration behavior, loss curvature for stability, and effective feature dimension for extraction cost. These are conceptual explanations built on existing theory rather than new theoretical results, so we will rename the second contribution to "mechanistic analysis" and retitle Appendix A to match its content, namely the definitions of the four measurements and these grounded interpretations, presented as hypotheses.

I appreciate the authors' response and encourage them to make sure that the mentioned changes take effect in the final manuscript. I will maintain my positive score.

Thank you for the positive assessment! We confirm that all changes described in our response, the new experiments as well as the framing revisions, will be incorporated in the final manuscript.

Reviewer_3rmvOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
2
Soundness
2
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Paper summary

This paper studies whether training-efficiency strategies are associated with increased model vulnerability. It evaluates data selection and pre-training/fine-tuning strategies in vision models, as well as simplified “zero-RL” alignment pipelines in math-reasoning LLMs. Across these settings, the authors report increased susceptibility to membership inference, adversarial attacks, model stealing, jailbreaks, and catastrophic forgetting, even when task utility is broadly comparable. They further analyze loss sharpness, calibration, and representation structure as potential correlates of the observed vulnerabilities. The paper argues that efficiency should be considered jointly with security and robustness.

Critical strengths
  1. Important and timely research question. Training efficiency is often discussed in terms of cost and task performance, while its potential security implications receive less attention. This paper highlights that dimension and motivates further study of the trade-offs involved.
  2. Clear organization and useful analysis. The paper is structured around a clear progression from empirical comparisons to analyses of model geometry, calibration, and representations. These analyses offer plausible hypotheses for future work, even if they do not establish causal mechanisms.
Critical weaknesses
  1. The paper studies different kinds of efficiency in different settings. In the vision experiments, efficiency comes from selecting less training data or fine-tuning a pre-trained model. In the LLM experiments, it comes from using a simpler alignment process. Because these changes differ so much, it is hard to tell whether they point to a single general trade-off between efficiency and security.
  2. The vision experiments try to match model accuracy, but the LLM experiments compare models trained with different alignment methods. The observed security differences may therefore come from changes beyond training efficiency.
  3. The paper does not show that the observed model changes cause greater vulnerability. The efficient models have sharper loss landscapes, different calibration, and different internal representations. However, these changes are observed only alongside increased vulnerability; the experiments do not test whether changing them would also change vulnerability. The authors should describe these findings as possible explanations rather than established causes.
  4. Limited evaluation on practical model variants. The paper focuses on controlled training setups and does not test whether its findings also hold for efficient model variants used in practice. For example, the authors could compare DeepSeek-V4.1-Flash with DeepSeek-V4-Pro using the paper’s privacy and robustness evaluations. Since these models differ in architecture and training, this comparison would not isolate the effect of efficiency, but it could show whether the observed risks also arise in real-world model choices.
Questions for authors

Please see the weakness.

4 comments

Thank you for the careful review.

W1 — "it is hard to tell whether they point to a single general trade-off"

We agree that the three strategies work through different mechanisms. However, they are unified under one definition in Sec. 3.1: reducing data, computation, or alignment overhead while preserving task utility, and the three strategies are the representative cost-reduction methods for these three kinds of cost. This diversity also strengthens our conclusion. A pattern shown by one strategy could be attributed to that method, but all three, applied at different stages, on different models, and in different domains, show the same outcome: the efficient variant is more vulnerable across attacks at comparable utility, accompanied by sharper loss landscapes, worse calibration, and differences in representation structure. This shared outcome, rather than a single mechanism, is the general trade-off our paper documents. We will revise the paper to state this scope, clarifying that our conclusions are drawn from the studied strategies.

W2 — "the observed security differences may therefore come from changes beyond training efficiency"

We agree that the LLM comparison is between complete alignment pipelines within the same model family, and we will make this explicit in the revision. First, utility is in fact closely comparable: the three models differ by at most 2.4 points in the seven-benchmark average (Table 5), while the security gaps are far larger, for example a roughly tenfold difference in the attack steps AutoDAN needs and a far larger accuracy drop after identical fine-tuning (Tables 4 and 5). A utility gap this small cannot explain security gaps of that size. Second, as stated in Sec. 3.1, our claim is at the pipeline level: the zero-RL pipelines as released carry a security cost, and we do not attribute this cost to any single omitted component. This matches how these recipes are used in practice, since practitioners adopt a released pipeline as a whole. Accordingly, Sec. 6 discusses the missing KL regularization only as a plausible explanation, not as an established cause. Third, SimpleRL-Zoo and PRIME were developed independently, with different training data, reward designs, and implementations. A factor specific to one pipeline would not affect the other, yet both show the same vulnerability pattern relative to Instruct across all three evaluations. Their shared efficiency-oriented alignment recipe is therefore the most plausible source of the vulnerability.

W3 — "the authors should describe these findings as possible explanations rather than established causes"

We agree, and we will revise the paper accordingly. Our mechanistic analysis establishes consistent associations rather than causal links, and the revision will describe these findings as possible explanations rather than established causes. In addition, we ran the missing test the reviewer points to: if sharpness contributes to vulnerability, then flattening the efficient model's minimum should reduce its vulnerability. We verify this below.

Setup. We retrain the CIFAR-10 High-Shapley model with SAM (two radii ρ) and change nothing else. All four models are trained and evaluated in one identical pipeline (3 seeds, mean values).

MetricHigh (SGD)High+SAM ρ=0.05High+SAM ρ=0.1Low (SGD)
Test acc (%)50.449.550.550.8
Train acc (%)100.0100.0100.0100.0
MIA conf [email protected]%FPR0.30%0.18%0.19%0.17%
MIA modi [email protected]%FPR0.31%0.16%0.23%0.16%
PGD steps1.721.701.533.43
ECE0.3990.3850.3700.362
Sharpness0.05110.04120.04370.0477
PCA-PR11.512.812.025.1
Model stealing (agreement)0.8510.8520.8570.575

Findings. (1) Sharpness drops (0.051 to 0.041) at matched accuracy (49.5 and 50.5 vs. 50.4). (2) MIA TPR drops from 0.30% to 0.18%, the level of the Low baseline (0.17%), and ECE improves (0.399 to 0.370). Changing sharpness changes privacy and calibration. (3) Stealing agreement (0.85) and PCA-PR (about 12) are unchanged. The compressed representation comes from the selected data, not from the optimizer, so the extraction risk persists. The intervention therefore supports the sharpness link for privacy and calibration and separates it from the representation-driven extraction risk.

W4 — "it could show whether the observed risks also arise in real-world model choices"

We agree that testing practical model variants is a valuable direction. However, the suggested pair, DeepSeek-V4.1-Flash vs. DeepSeek-V4-Pro, does not map onto the efficiency notion our paper studies. The efficiency of the Flash variant is primarily inference efficiency, and the training costs of both models are undisclosed, so we cannot establish which model was trained more efficiently, which is the variable our study compares. Moreover, most of our evaluations require white-box access to weights and token-level outputs, and running them is not feasible for models at this scale. We instead examine scale within our controlled setting: we extended the comparison to 32B models (appendix) and observed the same vulnerability pattern, indicating that our findings are not limited to small models.

Thanks for the author's response. I think the authors have addressed most of my concerns. I will maintain my positive scores.

Thank you for the feedback! The new experiments and the described revisions will all be included in the final manuscript.

Comments on the paper

1 comment

We thank the reviewers for the careful and constructive reviews. During the rebuttal we ran a round of new experiments and will revise the paper's framing. The individual responses build on four shared additions.

  1. An intervention experiment now tests the proposed mechanism directly. We retrained the CIFAR-10 High-Shapley model with Sharpness-Aware Minimization, changing nothing but the optimizer (3 seeds). Sharpness drops at unchanged clean accuracy, membership-inference TPR falls from 0.30% to 0.18%, the level of the Low baseline (0.17%), and calibration improves, while model stealing and feature dimensionality remain unchanged. Flattening the minimum removes the privacy and calibration gap but not the extraction gap, which supports the sharpness link for privacy and calibration and separates it from the representation-driven extraction risk.

  2. A layer-wise feature-dimensionality analysis quantifies the representation claim. We computed the PCA participation ratio at every compared block rather than only the penultimate layer. The High-Shapley models concentrate feature variance into severalfold fewer directions at every layer, on both CIFAR-10 and TinyImageNet, and the ordering is stable across three retraining seeds.

  3. A black-box robustness evaluation replaces the saturated white-box operating point. At ε=8/255, white-box PGD drives robust accuracy to near zero for both compared models, as expected for models without adversarial training, so we evaluate the realistic query-access threat: the attacker extracts a surrogate with the paper's stealing protocol and transfers PGD examples to the target. The efficient model is consistently more vulnerable at every ε, because its simpler representation is copied more faithfully, which connects the robustness and extraction dimensions of the study.

  4. An additional membership-inference attack confirms the privacy ordering. A logit-scaled confidence attack preserves the High vs. Low ordering on the paper's original models, across three retraining seeds, and on both CIFAR-10 and PubFig83.

The revision will also make the framing precise: the novelty claim will be stated as the first cross-stage and cross-domain analysis at matched utility, the second contribution will be renamed from "theoretical intuition" to "mechanistic analysis" with its interpretations presented as hypotheses, the results will carry explicit stage labels, the analysis-figure captions will be self-contained, and a Limitations paragraph will state the scope. Detailed answers follow in the individual responses.

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

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