acceptodds
Under review as a conference paper at ICLR 2027

Weeding Out Bad Seeds: Initial-Noise-Robust Unlearning for Text-to-Image Diffusion Models

Abstract

Machine unlearning has emerged as a critical post-hoc safety measure to erase sensitive concepts from Text-to-Image (T2I) models without prohibitive retraining. However, we reveal that current state-of-the-art (SOTA) approaches are brittle due to a severe lack of robustness to noise initialization. We call this phenomenon “probabilistic forgetting”: suppressed concepts re-emerge under specific random initial noise conditions, despite appearing unlearned on other initializations. We trace this failure to the misalignment between standard Gaussian sampling during unlearning and the unlearning objective. Since the target concept manifests only in specific initial noise regions throughout the unlearning phase, uniform random sampling yields sparse, uninformative gradient updates that fail to drive robust erasure. To overcome this issue, we propose an adaptive, concept-conditioned sampling strategy that dynamically concentrates gradient updates on regions where the target concept manifests, down-weighting uninformative areas. We integrate our framework with six distinct SOTA unlearning methods across four diffusion backbones and evaluate it across safety, object, and artistic-style unlearning, as well as under black-box and white-box adversarial attacks. Our method reduces the conditional nudity re-emergence rate across random initializations by 67.2% on average over four baselines and lowers attack success rates across both adversarial evaluations. Across concept domains, Adaptive Noise Sampling strengthens adversarial robustness and non-target retention while preserving competitive generative quality and target-erasure performance.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
unlearning, text to image diffusion models, noise intialization

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_KTQcOpenReview ↗
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Paper summary
  • This paper investigates the problem of machine unlearning in terms of noise initialization. The paper argues that the existing unlearning method can mitigate performance in the fixed seed, while still generating harmful content in other seeds. The authors call this phenomenon as “probabilistic forgetting” and propose an adaptive and concept-conditioned strategy for sampling.
Critical strengths
  • The paper investigates an interesting question of machine unlearning regarding the initial seeds and their performance differences.

  • This paper developed an adaptive method to give more importance to the seed that the model does not unlearn.

  • The proposed method can be utilized in previous unlearning strategies.

Critical weaknesses
  • Please refer to the Questions below.
Questions for authors
  • The term “probabilistic forgetting” should be reconsidered. In machine unlearning, “probabilistic” stands for the probabilistic leakage or guarantee on generated data [1] or a certified guarantee using a similar framework of differential privacy. Please refer to the existing attack papers, such as adversarial attack or membership attack, to find a better notion.
  • As stated in Table 12, the proposed method requires additional (about 50%) computations. Can the authors compare the method within the same wall-clock time, not for the same epochs? Also, can the authors compare the additional memory consumption of the proposed method?
  • The method relies on importance sampling on the seeds; the method does not erase the concept. However, how can this method generalize to the other seeds (not only for 20) that the model does not observe? I believe that it can improve the performance on seen seeds, but not sure about other seeds not seen in the training.
  • The citation should be in parentheses if it does not stand for the authors, e.g., Text-to-Image (T2I) diffusion models have revolutionized content creation (Song et al., 2020; ~~~).

[1] A PROBABILISTIC PERSPECTIVE ON UNLEARNING AND ALIGNMENT FOR LARGE LANGUAGE MODELS, ICLR 25.

4 comments

We thank Reviewer KTQc for the thoughtful review and constructive suggestions. We appreciate your recognition of the importance of initial-noise sensitivity and the applicability of our method across existing unlearning strategies. Below, we clarify the terminology and evaluation protocol, provide an equal-runtime comparison, and address memory consumption and citation formatting.

Q1: Terminology. Thank you for highlighting this ambiguity and pointing us to Scholten et al. (2025). Their work develops probabilistic evaluations of LLM outputs with high-probability bounds on information leakage. Our term describes an empirical failure mode: a concept suppressed under one noise initialization re-emerges under another. Both studies examine risks missed by limited evaluations, but we claim no statistical guarantee of concept removal or certified unlearning guarantee. To avoid confusion, we will replace “probabilistic forgetting” with “illusory forgetting” throughout the manuscript, emphasizing that apparent erasure can conceal residual concept accessibility.

We will also cite and discuss Scholten et al. (2025) in the revised related-work section, acknowledging the shared concern that limited evaluations can conceal residual knowledge while distinguishing their probabilistic evaluation framework for LLMs from our study of seed-dependent concept re-emergence in diffusion models.

Q2: Comparison under equal runtime and memory consumption.

To account for candidate-scanning overhead, we compared two representative baselines, ACE and EAP, with thier adaptive counterparts under matched wall-clock budgets: 4 h 40 min for ACE and 3 h 22 min for EAP. Failure counts use the same 20-seed evaluation over 4,000 images as the main paper.

MethodTraining timeOptimization stepsFailure count ↓CLIP score ↑
ACE baseline4 h 40 min2,0004910.2357
ACE + Ours (equal runtime)4 h 40 min3042100.2432
ACE + Ours (full training)7 h 20 min500600.2428
EAP baseline3 h 22 min2,0001,1420.2358
EAP + Ours (equal runtime)3 h 22 min2357350.2345
EAP + Ours (full training)4 h 15 min3006380.2341

Under equal wall-clock budgets, our method reduces failures by 57.2% for ACE and 35.6% for EAP. These results show that the reduction in multi-seed failure counts persists when candidate-scanning overhead is included in the computational budget.

Memory consumption. Appendix K.1, Table 13 already reports our method’s peak GPU memory consumption under the default N = 20, M = 4 configuration on a single NVIDIA A100 GPU. We will supplement these measurements with the corresponding baseline values to explicitly quantify additional memory consumption.

MethodBaseline peak memory (GB)Ours peak memory (GB)Additional memory (GB)
ACE21243
EAP19245
ESD19223
RECELER20244

Q3: Generalization to unseen noise initializations.

The N = 20 candidates are freshly and randomly sampled in each training batch, rather than forming a fixed set of 20 training seeds.

For evaluation, we independently sample 20 random initializations per prompt, producing 4,000 images over the 200-prompt benchmark. The main results are additionally averaged over 10 independent unlearning runs, with means and standard deviations reported in Table 1. Thus, the evaluation measures performance under newly sampled initializations rather than performance on a fixed training candidate set.

Fresh random initializations during training and evaluation, combined with 10 independent runs, provide strong empirical evidence that the improvements generalize beyond the sampled training seeds and are not an artifact of a favorable seed selection.

Q4: Citation formatting. We will revise the manuscript to use parenthetical citations when references support a statement, reserving narrative citations for cases where the authors’ names form part of the sentence.

Dear Reviewer KTQc, thank you again for your helpful feedback.

As the discussion period draws to a close, we would appreciate your thoughts on the equal-runtime comparisons and additional memory measurements provided in our rebuttal, as well as our clarification that noise candidates are freshly sampled during training and evaluation uses independently sampled initializations. We have also proposed revised terminology to avoid implying certified unlearning guarantees.

Could you let us know whether any concerns remain, or whether a specific additional experiment or clarification would help resolve them? We would be happy to follow up within the remaining discussion period.

Thank you for the detailed responses regarding computation and memory. These results help clarify the empirical strengths of the paper.

However, I remain concerned about the methodological novelty, particularly the reliance on importance sampling over initial noise seeds, as I mentioned in my earlier comment. My concern is about the method itself, not just the experimental setup. I think applying importance sampling to initial noise seeds represents a relatively incremental methodological contribution, although identifying and characterizing this failure mode is interesting.

Therefore, I will maintain my current score. I share Reviewer W3RM’s concern regarding the methodological contribution beyond conventional hard-example mining and reweighting.

Thank you for recognizing that this failure mode is important and its characterization interesting. Our starting point was the observation that changing only the initial Gaussian noise can cause an apparently erased concept to reappear under the same prompt. A plausible explanation is that, under a limited unlearning budget, random sampling can miss regions of the noise space where the concept persists. This led us to formulate unlearning as risk minimization over a concept-conditioned distribution of initial noise. We derive the corresponding importance-weighted objective and establish a high-probability bound on the error in estimating its normalizing constant from a finite batch of seeds (Section 4 and Appendix D).

A distinction from unweighted hard-example mining becomes important late in training. Every batch has a highest-scoring seed, even when all concept scores are negligible. Unweighted Top-4 mining still gives the four selected seeds equal weight, so the ranking provides no signal to ease forgetting pressure. Continued updates can then lead to over-unlearning and degrade generation quality. In our method, once the mean concept score falls well below the regularization constant, the importance weights shrink and the forgetting update can approach zero while retention remains active (Eq. 10). This limits the risk of over-unlearning without a separate stopping rule.

To measure what weighting adds beyond selection, we compared three strategies in our response to Reviewer W3RM. All used four of 20 candidate seeds per update, with matched optimization-step budgets within each method. Across 4,000 generated images, random selection yielded 965 failures for ACE and 2,244 for EAP. Unweighted Top-4 mining reduced those counts to 360 and 913. Applying our importance weights under the same Top-4 rule reduced them further to 60 for ACE and 638 for EAP. That is 83.3% and 30.1% fewer failures than unweighted mining, respectively, and 93.8% and 71.6% fewer than random selection.

We also observed gains without any hard-example selection. When all eight randomly sampled seeds contributed to every weighted update, including those with low concept scores, failures fell from 491 to 80 for ACE and from 1,142 to 705 for EAP relative to their original baselines (Appendix L, Table 14). Top-4 selection makes backpropagation more computationally efficient, but the formulation also improves erasure when every seed is retained. Across the broader evaluation, we tested six unlearning methods on four diffusion backbones across three tasks. In the 20-seed nudity evaluation, failures decreased for every method–backbone pairing we tested.

Reviewer_W3RMOpenReview ↗
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Paper summary

This paper investigates the problem of target concepts re-emerging under different random seeds after concept erasure in text-to-image models. The authors propose adaptive noise sampling: a frozen classifier is used to identify high-risk initial noise, reweight the original unlearning loss, and update the model using only the Top-M candidates. Experiments show that this method reduces concept re-emergence but increases the total training time.

Critical strengths
  1. The paper focuses on the scenario where erased concepts can re-emerge simply by changing random seeds, without adversarial prompts, and conducts multi-seed evaluations on prompts that appear safe under a fixed seed. This reveals that single-seed evaluation may overestimate the reliability of concept erasure, complements existing evaluations based on prompt attacks and latent inversion, and is meaningful for practical deployment safety.

  2. The method is scalable and can be integrated with different concept erasure algorithms. The experiments cover multiple generative backbones, concept types, and independent evaluators

Critical weaknesses
  1. My biggest concern is that this paper mainly improves the training effectiveness of existing concept erasure objectives through classifier-guided hard initialization selection and weighting. The current evidence supports a reduction in the probability of concept re-emergence, but it is insufficient to establish that "insufficient noise coverage" is the key mechanism behind residual concepts. The paper also does not sufficiently demonstrate its independent contribution compared with conventional hard example mining. Therefore, this work is closer to a practical improvement in training strategy, and its mechanistic understanding of robust concept unlearning still needs to be strengthened.

  2. Table 14 compares different numbers of candidates and updates, but lacks comparisons between random selection, unweighted Top-M, and weighted Top-M under the same candidate pool. The training steps and time costs also differ across different settings. Therefore, it is currently difficult to determine whether the improvements come from the proposed weighting mechanism, hard example selection, changes in gradient scale, or training budget configurations.

  3. The change-of-measure derivation explains the weighted objective, but the actual updates also involve stop-gradient on parameter-dependent weights and Top-M truncation. Appendix D mainly analyzes the estimation error of the normalization constant, but does not sufficiently explain the gradient bias introduced by truncation or the relationship between the updates and concept suppression.

Questions for authors
  1. Beyond reducing the empirical failure rate, what independent technical contributions and new insights into concept unlearning does this paper offer compared with conventional hard example mining? Can the authors provide controlled experiments to support the mechanistic explanation that "insufficient noise coverage leads to residual concepts"?

  2. Can the authors compare random selection of M samples, unweighted Top-M, weighted Top-M, and full-batch weighting without truncation under the same candidate pool, number of update samples, and training settings? Please control for or explain the differences in gradient scale.

  3. Can the authors report the per-prompt failure rate distribution and the probability of recovering an erased concept at least once within K random attempts on a shared set of prompts across all methods? Further comparisons between model checkpoints with similar average failure rates would help determine whether the method specifically improves seed-related robustness.

8 comments

We thank Reviewer W3RM for the thoughtful review and recognition of the practical importance of seed-dependent re-emergence. Below, we clarify our contributions, provide controlled comparisons, and address the theoretical interpretation.

W1 / Q1: Contribution beyond hard example mining and evidence for the noise-coverage explanation.

Thank you for this important question. We agree that Top-M selection is related to conventional hard example mining, as acknowledged in Appendix C. Our contribution combines the characterization of initial-noise sensitivity with a concept-conditioned noise distribution and its importance-weighted forgetting objective. Top-M selection is an optional efficiency approximation, rather than our main contribution. Appendix L also reports improvements without truncation, where all candidates contribute to the weighted update. The controlled experiments below quantify the additional benefit of importance weighting and targeted allocation of a limited unlearning budget.

Broader noise exploration alone does not account for the full improvement. We compared uniformly selecting four noise samples with unweighted and importance-weighted Top-4 selection from the same pool of 20 candidates. The uniform control selects four candidates randomly without classifier-based selection. All three configurations use the same optimization-step budget within each method. Failure counts are measured over 4,000 images.

MethodSampling strategyOptimization stepsFailure count ↓CLIP score ↑
ACEUniform selection, M = 45009650.2396
ACEUnweighted Top-4, N = 20 (hard example mining)5003600.2411
ACEImportance-weighted Top-4, N = 20 (Ours)500600.2428
EAPUniform selection, M = 43002,2440.2332
EAPUnweighted Top-4, N = 20 (hard example mining)3009130.2391
EAPImportance-weighted Top-4, N = 20 (Ours)3006380.2341

Uniform sampling uses four random noise realizations per update, providing broader noise exploration relative to the original one-sample-per-update baseline. Unweighted Top-M represents the classifier-guided hard example mining control, while our method combines Top-M selection with importance-sampling (IS) weights.

These results show that uniformly incorporating multiple noise realizations does not match targeted selection. Unweighted hard example mining substantially improves erasure, but does not fully account for our method’s gains: importance weighting further reduces failures by 83.3% for ACE and 30.1% for EAP.

Second, our method uses the available computational budget more effectively. To account for candidate-scanning overhead, we compared each baseline with its adaptive counterpart under matched wall-clock budgets: 4 h 40 min for ACE and 3 h 22 min for EAP.

MethodTraining timeOptimization stepsFailure count ↓CLIP score ↑
ACE baseline4 h 40 min2,0004910.2357
ACE + Ours (equal runtime)4 h 40 min3042100.2432
ACE + Ours (full training)7 h 20 min500600.2428
EAP baseline3 h 22 min2,0001,1420.2358
EAP + Ours (equal runtime)3 h 22 min2357350.2345
EAP + Ours (full training)4 h 15 min3006380.2341

Within the same runtime, our method reduces failures by 57.2% for ACE and 35.6% for EAP.

Our results are consistent with inefficient coverage of concept-triggering initializations contributing to residual generation under limited unlearning budgets. Uniformly processing more noise samples does not reproduce the full improvement, and our method also achieves stronger erasure within the same wall-clock budget. Together, these findings support targeted budget allocation through sample prioritization and weighting.

Finally, holding the training configuration and update budget fixed, we change only the sampling rule governing sample selection and weighting and observe substantially reduced re-emergence. This controlled intervention provides evidence for a causal contribution of the sampling strategy to improved erasure. However, it does not uniquely attribute this benefit to noise coverage, since selection and weighting also change gradient direction and magnitude.

W2 / Q2: Separating selection, weighting, gradient scaling, and training budget.

The first table in W1/Q1 provides the requested comparison between random selection, unweighted Top-M selection, and importance-weighted Top-M selection. These controls share N = 20 candidates, M = 4 update samples, optimizer settings, and optimization-step budgets within each underlying method.

The second table in W1/Q1 additionally compares ACE and EAP under matched wall-clock budgets, including candidate-scanning overhead.

Loss normalization and gradient scale. Following Algorithm 1, all sampling-based forgetting updates use the same explicit 1/N1/N aggregation factor, including the unweighted controls. Importance weights are computed using the full candidate pool, with no additional renormalization after Top-M selection. The retention loss and its coefficient remain those of the underlying baseline.

Identical aggregation factors do not guarantee identical gradient magnitudes: importance weighting can change the overall forgetting-gradient magnitude relative to retention. These ablations measure the combined effect of weighting rather than isolating its directional effect alone.

Weighting without truncation. Appendix L, Table 14 additionally reports configurations where all candidates contribute to the importance-weighted update:

MethodOriginal baseline (2,000 steps)Weighting without truncation, N=M=4N=M=4Weighting without truncation, N=M=8N=M=8
ACE4919580
EAP1,142762705

These results show that Top-M truncation is not necessary for the observed improvement over the original baselines. However, they use smaller candidate pools and different update batch sizes, so they provide complementary evidence rather than the exact full-batch comparison at N=M=20N=M=20.

W3: Interpretation of the practical update and its approximations.

Stop-gradient and the parameter-dependent sampling process. As discussed in the preliminaries, the model generates forget samples by repeatedly applying its denoising network to an initial noise vector. Because every denoising step depends on the model parameters, differentiating through the generated samples requires backpropagation through the entire trajectory, storing or recomputing intermediate network activations at each step. This entails substantial memory and computation [1]. Full-trajectory differentiation can also suffer from exploding gradients [1].

We therefore follow the baseline convention of generating samples with the current model and treating them as constants during the update.

Accordingly, we will explicitly present Eq. (11) as a step-wise surrogate update, rather than the exact gradient of the complete parameter-dependent objective. The detachment bias remains unquantified. Our gradient diagnostics address the separate approximation introduced by Top-M truncation, comparing it against the full detached forgetting update.

Measuring Top-M truncation error. Truncation introduces a separate approximation, which we evaluate directly using N = 20, M = 4. For the same candidate pool and per-sample gradients, we compute:

gfull=120∑i=120wi∇Li,gtop=120∑i∈Iwi∇Li,g_{\mathrm{full}}=\frac{1}{20}\sum_{i=1}^{20}w_{i}\nabla L_{i},\qquad g_{\mathrm{top}}=\frac{1}{20}\sum_{i\in I}w_{i}\nabla L_{i},

where I contains the selected four candidates. Both use weights normalized over the full candidate pool, without renormalization after selection. These measurements concern only the forgetting-loss gradient and exclude the retention-loss gradient.

We report cosine similarity, relative error ∥gfull−gtop∥2∥gfull∥2+ε\frac{\lVert g_{\mathrm{full}}-g_{\mathrm{top}}\rVert_{2}}{\lVert g_{\mathrm{full}}\rVert_{2}+\varepsilon}, and the norm ratio ∥gtop∥2∥gfull∥2\frac{\lVert g_{\mathrm{top}}\rVert_{2}}{\lVert g_{\mathrm{full}}\rVert_{2}}, and the discarded norm fraction:

∑i∉Iwi∥∇Li∥2∑i=120wi∥∇Li∥2.\frac{\sum_{i\notin I}w_{i}\lVert\nabla L_{i}\rVert_{2}}{\sum_{i=1}^{20}w_{i}\lVert\nabla L_{i}\rVert_{2}}.

The discarded norm fraction measures the discarded share of summed individual weighted gradient norms, rather than the relative error of their aggregate. The unweighted diagnostic sets wi=1w_i=1.

ACE

WeightingStepsCosine similarity ↑Relative error ↓Top/full norm ratioDiscarded norm fraction ↓
Unweighted1–1500.66900.82890.29330.8035
Importance weighted1–1500.87860.42830.66530.4017
Unweighted151–3000.59750.83850.32450.7995
Importance weighted151–3000.99990.00150.99990.0009
Unweighted301–4500.61900.83470.32460.7975
Importance weighted301–4501.00000.00001.00000.0000

EAP

WeightingStepsCosine similarity ↑Relative error ↓Top/full norm ratioDiscarded norm fraction ↓
Unweighted1–1000.51590.85100.33430.7980
Importance weighted1–1000.97740.06560.96110.0561
Unweighted101–2000.50410.86900.31120.8103
Importance weighted101–2001.00000.00001.00000.0000
Unweighted201–3000.55400.84380.30380.8031
Importance weighted201–3001.00000.00001.00000.0000

These results support a stage-dependent truncation approximation. For ACE, early truncation error is substantial: relative error is 0.4283, with a discarded norm fraction of 0.4017. In the middle stage, relative error decreases to 0.0015 and cosine similarity reaches 0.9999. EAP shows close agreement on early valid steps and agreement to the reported precision on later valid steps.

References

[1] Clark et al. (2024). Directly Fine-Tuning Diffusion Models on Differentiable Rewards. ICLR 2024.

Reviewer_cBXZOpenReview ↗
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Paper summary

This paper investigates the sensitivity of text-to-image diffusion models to initial noise after concept deletion. When the same prompt fails to generate the target content under a particular random seed, the content may still reappear when a different seed is used. Based on this observation, the authors propose Adaptive Noise Sampling: a method that uses a frozen classifier to evaluate images generated by the current model from different initial noises, weights the forgetting loss according to concept confidence, and updates only the high-scoring candidates; by default, M=4 candidates are selected from N=20 candidates for backpropagation (Sec. 4, Eqs. 3–11; Algorithm 1). The primary experiments are based on SD1.4 and cover the forgetting of uncensored content, artistic styles, and objects; the appendix further evaluates SD2.1, SD3, and FLUX.1 [dev], involving six different forgetting methods. The authors report the number of failures for single seeds and multiple seeds, conditional recurrence rate, non-target retention, CLIP/FID, as well as black-box and white-box attack results; they also use independent detectors and human evaluation to validate the primary gains (Tables 1–3, 15–20).

Critical strengths
  • The evaluation questions have practical significance, and the primary improvements are substantial. In multi-subject testing across 4,000 images, the number of ESD failures decreased from 510 to 201, ACE decreased from 491 to 60, and EAP and RECELER also showed improvement (Table 1). These results demonstrate that relying solely on a single generation to determine whether deletion was successful is insufficient.
  • Validation does not depend exclusively on the classifier used during training. The evaluation was guided by NudeNet and assessed with Open-NSFW2, supplemented by CLIP-guided evaluation, damaged-guided evaluation, and human assessment; this supports the finding that the observed improvements are not unique to any single detector (Appendices J, R).
  • The three average metrics for style tasks improved; in object tasks, the non-target accuracy of RECELER increased from 72.5% to 79.9%, demonstrating the value of reducing collateral damage (Tables 2–3).
Critical weaknesses
  • The contributions of the individual components and of the training schedule could be separated more clearly. Standard ACE and EAP use 2000 steps, whereas the adaptive variants use 500 and 300 steps respectively, so early stopping may account for part of the retained gains; the total runtime of the proposed method is also longer (Appendix K). Table 14 already includes untruncated settings with N = M = 4 and 8, all of which outperform the baselines, so the gains cannot be attributed simply to Top-M selection. Adding an unweighted Top-M ablation and a uniform-sampling control under the same stopping rule would make clearer the respective value of the weighting and of the candidate selection.

  • The theoretical analysis needs to match the scope of the approximations in the implementation. Appendix C assumes that the weighted gradients of discarded samples are negligible, but no direct measurement is provided; Appendix D analyzes mainly the normalization constant rather than the full update. We suggest stating Eq. (11) as a surrogate update under a step-wise frozen sampling distribution, and restricting the stability- and convergence-related claims accordingly. This concern targets the precision of the theoretical interpretation; it does not imply that the stop-gradient engineering choice is itself wrong.

  • The conditional reproduction rate needs to be interpreted cautiously across models. This metric is conditioned on the prompts that each model passes under a fixed seed, so the conditioning sets may differ (Sec. 5.1; Table 1). Per-prompt failure rates on a common prompt set would help explain the residual seed risk. At the same time, Table 1 already reports multi-seed failure counts on the full prompt set, so the above definitional issue does not affect the overall evidence of improvement.

  • Ethics and image provenance. The authors state that annotators were informed of the risk of nude content and consented to participate. Please further confirm whether all human figures in Figures 1, 5, 7, and 8 are model-generated, and whether any real-person reference images or specific individuals' identities were used. If real persons or third-party images are involved, please state their sources and the corresponding permissions and basis for consent. In addition, please clarify whether the human evaluation underwent ethics review, received an exemption, or was assessed as not requiring approval.

Questions for authors

Q1. How were the training stopping points for ACE and EAP selected in Appendix K? If the uniform-sampling baseline is given the same checkpoint-selection rule and update budget, how does the gap between removing and retaining the component change?

Q2. On a representative baseline, what are the results for unweighted Top-M, weighting-only without truncation, and the full method, respectively? Is the 1/N scaling in Algorithm 1 used directly in the implementation, or are the selected weights re-normalized afterwards?

Q3. Can Eq. (11) be written explicitly as a surrogate objective update after fixing the current sampling distribution and the generated samples, and can you explain how the retained loss is handled within this update?

Q4. With the default settings N = 20 and M = 4, how much weighted gradient do the discarded samples contribute? Is there a comparison with the full-batch update in terms of direction or effect that would support the approximation in Appendix C?

Q5. If a common prompt set were used, how would the per-prompt failure rates be distributed across seeds for each method? Beyond the reduction in the overall average failure rate, what evidence further supports an improvement in residual seed risk?

5 comments

We thank Reviewer cBXZ for the careful review and constructive suggestions. We appreciate your recognition of the practical significance of initial-noise robustness, the substantial reductions in failures, and the validation using independent detectors and human evaluation.

W1a: Could the gains be explained by early stopping?

Thank you for highlighting this potential confound. For the standard baselines, we used the training-step counts reported in their respective papers. For our adaptive variants, we selected training durations during preliminary hyperparameter tuning, evaluating checkpoints every 100 steps on a validation subset disjoint from the reported benchmark samples. We observed declining importance-weighted forgetting gradients and a plateau in validation performance, motivating the selection of 500 steps for ACE and 300 steps for EAP.

To document this behavior, we report the average L2 norm of the forgetting-loss gradient over the indicated optimization-step intervals. We compute each gradient’s norm before averaging. Adaptive gradients include importance weighting; all measurements exclude the retention-loss gradient. We continued the diagnostic runs beyond the selected checkpoints to examine subsequent gradient behavior.

Optimization stepsACE baselineACE + OursEAP baselineEAP + Ours
1–1000.1583950.1100500.2295610.104138
101–2000.1249880.0343140.1829470.023200
201–3000.1062150.0173820.1536740.003707
301–4000.0884260.0046500.1269120.000012
401–5000.0711560.0009400.1018440.000002
501–6000.0569470.0000110.080475—
601–7000.0448010.0000020.062775—
901–1,0000.020596—0.028467—
1,401–1,5000.003612—0.005063—
1,901–2,0000.000226—0.000322—

The adaptive variants exhibit much earlier gradient decay. Baseline gradients also decrease substantially, but reach similarly small magnitudes at later stages.

Also, we evaluated checkpoints every 100 steps on a held-out validation subset disjoint from the benchmark prompts (40 prompts with 4 different seeds). The table reports validation failure rates (%), documenting performance around the selected stopping points: 500 steps for ACE and 300 steps for EAP.

Optimization stepACE baseline ↓ACE + Ours ↓EAP baseline ↓EAP + Ours ↓
10057.424.778.339.6
20044.610.972.622.5
30036.75.767.416.4
40032.12.861.716.4
50029.41.956.216.4
60026.31.951.1—
70023.81.947.2—
1,00018.7—38.1—
1,50014.5—31.6—
2,00012.7—29.1—

To test whether stopping earlier alone reproduces our gains, we additionally evaluated the original baselines at the same fixed optimization-step budgets as their adaptive counterparts. All failure counts use the same 20-seed evaluation over 4,000 images.

MethodOptimization stepsFailure count ↓CLIP score ↑
ACE baseline5001,1540.2420
ACE + Ours500600.2428
EAP baseline3002,6740.2431
EAP + Ours3006380.2341

At these matched update budgets, Adaptive Noise Sampling reduces failures by 94.8% for ACE and 76.1% for EAP. Thus, the reduction in failures cannot be explained by the shorter training schedule alone.

W1b: Computational overhead and comparison under equal runtime.

We agree that fewer optimization steps do not necessarily imply lower wall-clock cost. To assess whether the additional candidate-scanning cost is justified, we compared standard unlearning and Adaptive Noise Sampling under the same wall-clock training budget.

MethodTraining timeOptimization stepsFailure count ↓CLIP score ↑
ACE baseline4 h 40 min2,0004910.2357
ACE + Ours (equal runtime)4 h 40 min3042100.2432
ACE + Ours (full training)7 h 20 min500600.2428
EAP baseline3 h 22 min2,0001,1420.2358
EAP + Ours (equal runtime)3 h 22 min2357350.2345
EAP + Ours (full training)4 h 15 min3006380.2341

Under equal wall-clock budgets, our method reduces failures by 57.2% for ACE and 35.6% for EAP. Although candidate scanning increases the cost per optimization step, our method achieves better erasure.


W1c: Separating the contributions of candidate selection and importance weighting.

To isolate the contributions of the two components, we compare uniform sampling of four candidates, unweighted Top-4 selection from 20 candidates, and our full method with importance-weighted Top-4 selection from 20 candidates. All three configurations use the same optimization-step budget within each baseline. We also include the original 2,000-step baselines for reference.

MethodSampling strategyOptimization stepsFailure count ↓CLIP score ↑
ACE baselineStandard uniform sampling2,0004910.2357
ACEUniform sampling, M = 45009650.2396
ACEUnweighted Top-4, N = 205003600.2411
ACEImportance-weighted Top-4, N = 20 (Ours)500600.2428
EAP baselineStandard uniform sampling2,0001,1420.2358
EAPUniform sampling, M = 43002,2440.2332
EAPUnweighted Top-4, N = 203009130.2391
EAPImportance-weighted Top-4, N = 20 (Ours)3006380.2341

Note: The standard baseline effectively uses N = 1, M = 1, contributing one noise sample per update. The uniform-sampling control uses N = 20, M = 4, but selects four candidates randomly without scoring or weighting.

Both candidate selection and importance weighting contribute. Unweighted Top-4 selection reduces failures from 965 to 360 for ACE and 2,244 to 913 for EAP. Importance weighting further reduces failures by 83.3% and 30.1%, respectively. Table 14 complements these controls with weighting-only configurations at N = M = 4 and N = M = 8, without truncation.

Together, these controls show that the reduction in failures persists under matched update budgets matched wall-clock runtime. Both candidate selection and importance weighting contribute.

W2a: Measuring the contribution of discarded gradients.

Thank you for pointing out that Appendix C lacked a direct measurement of the truncation approximation. We conducted a gradient diagnostic for ACE and EAP using the default N = 20, M = 4 configuration. For the same candidate pool, we computed:

$ g_{\mathrm{full}}=\frac{1}{20}\sum_{i=1}^{20}w_i\nabla L_i, \qquad g_{\mathrm{top}}=\frac{1}{20}\sum_{i\in\mathrm{Top}\text{-}4}w_i\nabla L_i. $

Both gradients use importance weights normalized using the same full candidate pool, preserving the same 1/201/20 scaling without renormalization after selection. These measurements concern only the forgetting-loss gradient and exclude the retention-loss gradient.

We measure cosine similarity, relative error ∥gfull−gtop∥2∥gfull∥2+ε\frac{\lVert g_{\mathrm{full}}-g_{\mathrm{top}}\rVert_{2}}{\lVert g_{\mathrm{full}}\rVert_{2}+\varepsilon}, and the norm ratio ∥gtop∥2∥gfull∥2\frac{\lVert g_{\mathrm{top}}\rVert_{2}}{\lVert g_{\mathrm{full}}\rVert_{2}}. We also report the discarded norm fraction:

{\sum_{i=1}^{20}w_{i}\lVert\nabla L_{i}\rVert_{2}}.$$ This last metric measures the discarded share of the summed individual weighted gradient norms; it differs from the relative error of the aggregate gradient. For reference, we also report the corresponding unweighted diagnostic, setting $w_i=1$. **ACE** | Weighting | Steps | Cosine similarity ↑ | Relative error ↓ | Top/full norm ratio | Discarded norm fraction ↓ | |---|---|---:|---:|---:|---:| | Unweighted | 1–150 | 0.6690 | 0.8289 | 0.2933 | 0.8035 | | Importance weighted | 1–150 | 0.8786 | 0.4283 | 0.6653 | 0.4017 | | Unweighted | 151–300 | 0.5975 | 0.8385 | 0.3245 | 0.7995 | | Importance weighted | 151–300 | 0.9999 | 0.0015 | 0.9999 | 0.0009 | | Unweighted | 301–450 | 0.6190 | 0.8347 | 0.3246 | 0.7975 | | Importance weighted | 301–450 | 1.0000 | 0.0000 | 1.0000 | 0.0000 | **EAP** | Weighting | Steps | Cosine similarity ↑ | Relative error ↓ | Top/full norm ratio | Discarded norm fraction ↓ | |---|---|---:|---:|---:|---:| | Unweighted | 1–100 | 0.5159 | 0.8510 | 0.3343 | 0.7980 | | Importance weighted | 1–100 | 0.9774 | 0.0656 | 0.9611 | 0.0561 | | Unweighted | 101–200 | 0.5041 | 0.8690 | 0.3112 | 0.8103 | | Importance weighted | 101–200 | 1.0000 | 0.0000 | 1.0000 | 0.0000 | | Unweighted | 201–300 | 0.5540 | 0.8438 | 0.3038 | 0.8031 | | Importance weighted | 201–300 | 1.0000 | 0.0000 | 1.0000 | 0.0000 | Top-4 increasingly preserves the full importance-weighted forgetting gradient: ACE’s relative error falls from **0.4283** early in training to **0.0015** in the middle stage, with later agreement to the reported precision.This is consistent with initially similar classifier scores allowing substantial discarded contributions; as unlearning progresses, most scores become low, leaving a few high-confidence, concept-triggering samples that dominate the weighted gradient. We thank the reviewer for suggesting this informative diagnostic. We found the results interesting and helpful: they strengthen the empirical justification for Top-M truncation while clarifying that the approximation is more accurate later in training and need not be negligible at the outset. --- **W2b: Interpreting Eq. (11) as a surrogate update.** We agree that Eq. (11) is more precisely interpreted as an update to a **step-wise surrogate objective**, rather than the exact gradient of the parameter-dependent objective. We will reframe Eq. (11) and the accompanying discussion accordingly.

Comments on the paper

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AuthorsOpenReview ↗

We have updated the manuscript

We thank cBXZ and W3RM for recognizing the practical significance of seed-dependent concept re-emergence and the empirical gains of our approach. We also thank KTQc for highlighting the value of characterizing this failure mode and adaptively weighting seeds where the concept persists.

We have incorporated the following revisions into the manuscript.

  • For cBXZ, we made the retention loss and its coefficient explicit in Eq. 11 and Algorithm 1. Tables 17–19 now report forgetting-gradient norms during training, validation failure rates across checkpoints, and comparisons at matched optimization steps. Section 5.1 and Table 1 clarify that each model’s conditional re-emergence rate uses the prompts that passed its fixed-seed test. We also clarified image provenance and institutional ethics approval.
  • For cBXZ and W3RM, we added a comparison of random sampling, unweighted hard-example mining, and importance weighting (Table 20), along with per-prompt failure distributions and Failure@K on shared seeds (Tables 25–26). Appendix C.1 explains how weights retain their full-pool normalization after selection and measures how closely the Top-4 gradient approximates the full gradient at different training stages (Tables 4–5).
  • Table 15 adds the equal-runtime comparison requested by KTQc, also addressing training-cost concerns raised by cBXZ and W3RM. For KTQc, we expanded Table 16 to quantify peak GPU memory overhead, adopted the term illusory forgetting, and discussed Scholten et al. (2025) in Section 2.2. We also corrected the citation issue KTQc.

We thank all three reviewers for helping us strengthen the manuscript.

Best regards,

Authors

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