acceptodds
Under review as a conference paper at ICLR 2027

Adaptive Withdrawal of Refusal Steering

Abstract

Refusal steering can improve the safety of large language models (LLMs) by shifting internal activations in a refusal direction. Existing refusal steering methods keep steering active for a fixed number of output tokens or throughout generation, yet the number of steered tokens substantially affects both safety and utility. Withdrawing steering too early can allow harmful generation to resume, while keeping it active longer than necessary can increase over-refusal and degrade performance on benign prompts. These opposing risks motivate adaptive termination of inference-time safety interventions. We introduce adaptive withdrawal, a method that predicts the earliest time to end refusal steering for each request while maintaining response safety comparable to persistent steering. The prediction is based only on the model's internal refusal state and its change over the first two output tokens. It does not require observing the rest of the response, allowing earlier withdrawal with less impact on model performance. Across multiple LLMs, adaptive withdrawal achieves safety comparable to persistent steering, including when sampled generation continues long after withdrawal. Compared with state-of-the-art activation-steering methods, adaptive withdrawal achieves competitive safety and benign performance while adding substantially less inference overhead.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM safety, activation steering, refusal steering, inference-time intervention

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_CJSmOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
1
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Paper summary

The paper proposes an adaptive approach to refusal vector application, utilizing a simple, discrete-time survival analysis model to decide when to stop applying the refusal vector. Authors report similar safety gains compared to persistent application of the refusal vector, while reducing over-intervention, over-refusal, capability degradation. and inference overhead on four different LLMs.

Critical strengths
  1. The problem is interesting and the use of survival analysis is well motivated.
  2. The actual inference time mechanism is simple and efficient. I particularly like the interpretability of the parameters.
  3. Extensive evaluation using different models, attacks, judges, etc.
  4. Over refusal improvements are promising.
Critical weaknesses
  1. Survival target is ill-defined and the intervention may induce informative censoring (Section 3.3)

Setting a response as evaluable only if it reaches the designated width makes it so that the longest evaluable width depends on the response length, which steering itself affects. For example, a refusal ending after 10 tokens makes 16, 32, and 64 inadmissible.This induces informative censoring and makes the distribution estimated be different than "the shortest steering duration that produces a safe response". Utilizing a single noisy output per width considered and defining the survival time as a monotone closure so these times, which is sensitive to width grid coarseness, both compound the murkiness of this regression target.

Additionally, authors should consider reporting more recent survival evaluation metrics, accounting for for Inverse Probability Censoring Weights.

  1. Questionable practical significance of latency gains (Table 2)

Persistent steering already incurs less than 0.2% runtime overhead. Adaptive withdrawal saves less than 0.1% runtime in all settings. These savings are negligible and should not be considered a significant result, especially considering that multiple efficient activation vector inference engines exist and may cause relative gains to appear even smaller. Gains relative to other methods largely reflect architecture differences.

  1. MMLU evaluation in Table 1 of Appendix A could be the most significant piece of evidence for the method, but it's confounded

The MMLU results show that the adaptive approach might almost completely recover the accuracy lost under persistent steering, but the evaluation is very non-standard, employing steering during an analysis stage of the eval. The authors should score identical analyses without steering so that results are comparable. The unusually low Gemma and Llama MMLU accuracies also warrant investigation and explanation.

Questions for authors

Reproducibility: not all code needed for reproducing the paper results is present in the submission. Can this be amended?

4 comments
AuthorsOpenReview ↗

Official Comment Part 1

Thank you for recognising the practical motivation, the interpretable predictor, and the over-refusal results. We tested each concern you raised. The main complete-response result is supported by an experiment that does not use the duration target at all, and the revised manuscript states the remaining limitations of that target. All modifications are marked in red.

W1. Withdrawal targets and incomplete observations

On censoring, we re-analysed every tested duration for the 120 calibration prompts per model. The 37 cases with no identified safe withdrawal time all remained evaluable at 64 tokens, so none was censored by an early ending. Counting responses that end safely before the withdrawal point as safe changes none of the calibration targets or fitted policies. Steering still affects response length, so censoring may not be random, and the revised Section 3.3 says so.

On target noise, our new analysis supports your concern. Across five sampled runs, 35–42 of the 120 calibration prompts per model change their target, and the revised manuscript describes the target as one realisation of a noisy quantity. The policies fitted on these targets still meet the complete-response criterion in the primary held-out validation for every model (Table 7).

On the grid and the monotone closure, a finer duration grid does not consistently improve performance. The closure does matter. Replacing it with a first-safe target changes the selected policies and can reduce safety, for example to 94.00% on Gemma against 99.75% for persistent steering, which fails our criterion. The closure is therefore the conservative choice, and we report this sensitivity.

As independent evidence that does not use the duration target at all, we trained a binary classifier that chooses between withdrawal at two tokens and persistent steering. On the 400 held-out prompts per model it passes the multiplicity-adjusted complete-response criterion on all four models and removes 37.7–62.4% of the intervention. Its continuation comparisons pass on Gemma and Qwen3-8B only. Useful early withdrawal on complete responses therefore does not depend on the survival formulation.

Following your suggestion, we recalculated the prediction metrics with inverse-probability-of-censoring weights. Original values are from Table 12.

ModelC-index (original → weighted) ↑Brier (original → weighted) ↓
Gemma-1.1-7B-IT0.919 → 0.9180.056 → 0.058
Llama-3.1-8B-Instruct0.947 → 0.9410.067 → 0.069
Qwen3-4B0.669 → 0.6690.066 → 0.070
Qwen3-8B0.920 → 0.9180.053 → 0.056

The weighted values stay close to the originals. The revised manuscript specifies the weighting assumptions and makes clear that we predict the tested withdrawal targets, not safety probabilities across repeated generations.

(continued in Part 2)

AuthorsOpenReview ↗

Official Comment Part 2

W2. Practical significance of runtime

Persistent steering already adds less than 0.2% runtime (Table 2), so the runtime saving is negligible, and the revised manuscript no longer presents it as a result. The contribution is less unnecessary intervention and less over-refusal. On the primary evaluation, adaptive withdrawal removes 38.5–72.5% of the intervention while retaining 97.2–100.0% of persistent-steering safety on complete responses, and it raises the XSTest answer rate over persistent steering by 5.8–17.6% on Gemma, Llama and Qwen3-4B (Table 1).

W3. MMLU evaluation and implementation

We take your comment on "Table 1 of Appendix A" to refer to the MMLU results in Table 1 under the protocol of Appendix A.4.2. Thank you for identifying the confound in that evaluation. We re-ran MMLU on the same 1,026 questions with two protocol changes. The model generates its full analysis with no cut-off at 96 tokens, and, as you suggested, the answer is scored without steering for every method.

ModelUnsteeredPersistent steeringAdaptive withdrawal
Gemma-1.1-7B-IT46.2%44.2%45.1%
Llama-3.1-8B-Instruct57.2%54.7%56.1%
Qwen3-4B68.4%65.9%68.2%
Qwen3-8B69.4%67.1%68.2%

Under the matched protocol the differences are small. Adaptive withdrawal is 0.9–2.3% above persistent steering on every model and within 1.2% of unsteered accuracy. These differences are modest. On 1,026 questions each accuracy has a standard error of about 1.5%, so a single-model difference of 0.9–2.3% is comparable to the sampling error of the estimates. The revised manuscript therefore presents MMLU as evidence that withdrawal does not reduce accuracy relative to persistent steering, and no longer presents it as a gain. The low Gemma and Llama accuracies came largely from the 96-token limit. With full analyses, unsteered accuracy rises to 46.2% and 57.2%.

Reproducibility

We have updated the supplementary code package to include the implementation and evaluation code. We will publicly release the complete code and experimental configurations upon acceptance.

Based on the target-robustness analyses, the weighted metrics, the binary-classifier experiment and the matched MMLU evaluation, we hope we have addressed your concerns, and we hope you will consider raising your score.

Thank you for the thorough response and the additional experiments. I appreciate the candour with which the new analyses are reported, and the revised claims are better supported than the original ones.

I am keeping my score, since the revisions narrows contributions, and the method itself needs more work.

AuthorsOpenReview ↗

Response to Reviewer CJSm's follow-up comment

Thank you for the follow-up, and for noting that the revised claims are better supported. We believe the strengths of the revised paper outweigh its remaining limitations, which the paper states openly. We summarise them below and hope you will consider them in your final assessment.

The core result is unchanged. Adaptive withdrawal removes 38.5–72.5% of the intervention while retaining 97.2–100.0% of persistent-steering safety on complete responses, and all four models pass this comparison under both HarmBench and Qwen2.5 (Table 7). It also raises the XSTest answer rate over persistent steering by 5.8–17.6% on Gemma, Llama and Qwen3-4B (Table 1), which is the over-refusal improvement you described as promising.

Your comments also made the paper more rigorous. The binary-classifier experiment passes the complete-response criterion on all four models without using the duration target, so the finding does not depend on the survival formulation. The weighted metrics stay close to the originals (Table 28).

The strengths in your review remain after revision, namely a simple and interpretable inference-time rule and an extensive evaluation across models, attacks and judges. We believe these results outweigh the remaining limitations, and we hope you will weigh them in your final assessment.

Reviewer_Z1CyOpenReview ↗
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Paper summary

This paper asks an interesting question: can a model predict when to stop a safety intervention while retaining its benefit? The experimental effort is substantial. My main concern is that the strongest safety-preservation wording is broader than the evidence supports.

Critical strengths
  • Determining how long an intervention should remain active is a meaningful addition to work on whether and how strongly to steer.
  • Comparing two continuations from the same steered prefix and decoding state is a particularly good design. It helps isolate the effect of withdrawing the intervention.
Critical weaknesses
  1. In Table 9, looking at Qwen3-4B on HarmBench with up to 512 output tokens, safety drops off sharply once steering is removed:
DecodingContinued SteeringSteering Withdrawn
Greedy91.20%70.93%
Sampled93.33%74.00%

A roughly 20-point drop under both decoding strategies calls into question whether safety actually holds up after withdrawal. Because of this, the authors either need to dial back their main conclusion or adopt a more conservative withdrawal policy that holds up over longer generations.

  1. In Table 19, none of the models actually pass the target threshold when evaluated with MD-Judge. Similarly, Granite Guardian scores Qwen3-4B at 73.50% safety for adaptive steering compared to 91.75% for persistent steering. While this doesn't automatically mean the harsher evaluators are right, the discrepancy is too large to ignore and needs to be sorted out before making broad claims about safety.

  2. Looking at Table 7, three out of the four models fail the HarmBench noninferiority test after steering is withdrawn. While failing to clear that statistical bar doesn't strictly prove the method is worse, it does mean the paper hasn't met its own standard for showing comparable safety. On top of that, the authors should better justify why a 5% drop is an acceptable margin in the first place.

  3. Table 25 highlights 14 new safety failures overall, which sounds small until you notice that 11 of them happen across just 80 attacks on Llama (a 13.8% failure rate). In all of these instances, the model stays safe when steering continues, but breaks as soon as steering is pulled back. That points to a concrete weakness in how the withdrawal rule currently works for specific models.

Questions for authors

see above

3 comments
AuthorsOpenReview ↗

Official Comment Part 1

Thank you for recognising the importance of predicting intervention duration and the value of matched-prefix comparisons. We agree that our strongest safety wording was broader than the evidence supports. The core finding on complete responses is unchanged, and new results on direct requests at 128 tokens show comparable continuation safety as well. We have narrowed the main conclusion as you proposed. All modifications are marked in red.

1. Longer-generation safety

We confirm that most of the 20% drop on Qwen3-4B at 512 tokens is a real effect. In a blinded audit, five human raters confirmed on average 23.2 of 40 (58%) of the pairs in which HarmBench judged the withdrawn continuation unsafe and the maintained one safe. The revised manuscript no longer claims that safety persists long after steering ends.

Within the 128-token setting the evidence is stronger. On 159 official HarmBench direct requests (142–158 usable same-prefix pairs per model), the original frozen policies reach post-withdrawal continuation safety of 92.26–100.00%, against 90.32–100.00% for persistent steering, with 72.9–93.7% less intervention. All four models pass the multiplicity-adjusted criterion. These results show useful withdrawal operating points at this length, not robustness for arbitrarily long generation.

2. Evaluator disagreement and human evaluation

The disagreement is partly a judge artifact and partly unresolved. When MD-Judge is given the original harmful request as context, Gemma and Llama pass the multiplicity-adjusted criterion (97.50% vs. 99.00% and 82.00% vs. 81.00%). Neither Qwen model passes, so context explains only part of the MD-Judge result.

For Granite Guardian on Qwen3-4B, we conducted a blinded human audit. Five undergraduate raters, blind to the method and to every judge label, rated 40 randomly sampled pairs in which Granite Guardian judged the adaptive response unsafe and the persistent one safe. They confirmed on average 5.2 of the 40 pairs (13%), with Fleiss' κ of 0.58 across the audit. In a separate blinded study on 100 randomly sampled prompts, the same raters gave 92.2% safety for adaptive withdrawal and 94.6% for persistent steering. The 95% confidence interval on this 2.4% gap is −2.1% to 6.9%. It contains the HarmBench gap on the same model, which is 0.0% on the primary evaluation (95.5% vs. 95.5%, Table 10) and 2.3% in the same-prefix validation (94.08% vs. 96.42%, Table 7), and it excludes the 18.25% gap reported by Granite Guardian (Table 19). Human judgement is therefore consistent with our calibration evaluator, and we report this study as supporting evidence, not as a formal non-inferiority test.

(continued in Part 2)

AuthorsOpenReview ↗

Official Comment Part 2

3. Primary continuation safety and the 5% margin

All four models pass on complete responses, but only Gemma passes on the post-withdrawal continuation under HarmBench (Table 7). The revised manuscript states this distinction prominently and no longer describes the continuation result as meeting our standard.

Our 5% margin is an experimental tolerance, not a deployment threshold, and it follows closely related work. Tamsal and Rusert (2026) test equivalence with a prespecified ±5% margin on attack success rate, which is the complement of our safety rate. Wynn et al. (2026) study adaptive early exiting and control the prediction gap relative to the baseline at a tolerance of 0.05 in their in-context learning experiments. Our criterion is stricter than a 5% observed gap, since it requires the one-sided 95% lower confidence bound to stay above −5% (Appendix A.4.3). We also repeated threshold selection under stricter margins. At 2%, complete-response policies pass pointwise comparisons for Gemma, Llama and Qwen3-4B, and none passes at 1%. The revised manuscript reports this sensitivity analysis together with absolute harmful-response rates.

4. Llama-3.1-8B-Instruct under adaptive attack

The Llama result is a failure case of the withdrawal rule under this attack. No finite minimum duration qualifies for this model (Appendix G.4.3), so the safeguarded policy keeps steering on and gives no saving there. On the other three models the attack causes three new failures in 238 withdrawals (Table 25). A 32-token minimum on Qwen3-4B removes both of its failures while still reducing exposure by 58.7%, and an additional safeguard test on Qwen3-8B shows zero new unsafe continuations in 69 withdrawals with 59.2% less exposure. Outside this white-box attack, the Llama policy stays within 0.2% of persistent steering under GCG and PAIR while reducing exposure by 40.2–93.1% (Table 24). The safeguards were selected against one white-box attack, and we do not claim general robustness. The revised manuscript reports each attack family separately and lists Llama under this attack as a failure case.

Based on the narrower claims, the new continuation results, the human audit and the margin analysis, we hope we have addressed your concerns, and we hope you will consider raising your score.

References

Wynn, A., Jazbec, M., Peris, C., Khaziev, R., Liu, A., Khashabi, D., and Nalisnick, E. "Controlling the Risk of Corrupted Contexts for Language Models via Early-Exiting." ICML 2026, PMLR 306, pp. 137902–137925.

Tamsal, T., and Rusert, J. "Adaptation, Not Algorithm: LoRA and Full Fine-Tuning Show Comparable Black-Box Jailbreak Degradation in Five Open-Weight LLMs." Findings of IJCNLP-AACL 2026, pp. 4432–4458.

Thank you for the detailed rebuttal and additional experiments.

The overall readability of the manuscript needs improvement. I suggest revising the introduction to better motivate the key challenges and clarify the novelty relative to existing experimental design methods.

Overall, I will maintain my original rating with low confidence, given my limited expertise in area.

Reviewer_AombOpenReview ↗
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Paper summary

The paper describes an approach to modulate refusal steering of LLM output as a function of the prompt. A model estimates when steering ca be discontinued without rendering the remaining output of the model unsafe. The goal is to minimize steering overall so as not to impact the overall capabilities of the generating model more than absolutely required. The concept is intuitive and evaluations seems to indicate that it is effective in comparison to other steering methods, including persistent steering.

Critical strengths

The idea seems valid and worthwhile in terms of practical application to safety steering of LLMs.

Evaluation compared to several other steering approaches (but i don't know how comprehensive it is).

Critical weaknesses

The intuition behind velocity and veracity as the basis for estimating the withdrawal width is a bit nebulous. Also, it is not clear whether these two quantities are computed before or after applying steering to the first two tokens. Shouldn't more tokens be used to get a more stable estimate for the "safety" of the direction of the response (two tokens give very little information) ? If you're going to run a classifier for h_i(w) on the output, why not directly estimate the safety of the generated prefix?

Questions for authors

See questions under weaknesses.

1 comment

Thank you for your thoughtful review. Below we clarify what the two features mean, when they are measured, and what the predictor estimates. We have updated the manuscript accordingly, and all modifications are marked in red.

1. Feature intuition and observation timing

Both features are measured after steering is applied to the first two output tokens. As defined in Section 3.3, Equation (2) (lines 219–231), both features use the projection of the model's activation onto the refusal direction. Refusal veracity is the projection at the second output step and measures how strongly the model is currently oriented toward refusal. Refusal velocity is the absolute change in that projection between the first and second steps and measures how quickly the refusal signal is changing under steering. The steering edit is applied before these activations are read, and the revised Section 3.3 states this order explicitly. Each activation also reflects the entire input context, so these are not two isolated token embeddings. Velocity is a model-dependent refinement. It raises the C-index from 0.800 to 0.920 on Qwen3-8B and changes little on the other three models (Section 4.3, lines 402–406; Appendix E.2.1, Table 12).

2. Why observe only two decoding steps?

We tested four and eight steps, and they did not predict better. Two steps is the earliest point at which change can be measured. Velocity needs two readings, so withdrawal cannot happen before step two (Section 3.3, lines 243–248). Observing longer only delays withdrawal. As reported in Section 4.3, lines 407–410, and Appendix E.2.2, Table 13, we also tested whether observing four or eight steps improves prediction. C-index, higher is better:

Model2 steps4 steps8 steps
Gemma-1.1-7B-IT0.9190.8840.500
Llama-3.1-8B-Instruct0.9470.9240.790
Qwen3-4B0.6690.5740.642
Qwen3-8B0.9200.8220.843

The two-step predictor gives the best ranking for every model. We present this as an empirical finding, not an assumption that two steps are always enough.

3. Why not directly classify prefix safety?

The two questions differ. A safe-looking prefix does not show that the response will stay safe after steering stops. To clarify, hi(w)h_i(w) is not a classifier over the generated text. It is a small logistic model that takes only the two numbers above (veracity and velocity) and estimates how much longer steering is needed for that prompt. The prompt-level duration target is defined in Section 3.3, lines 208–213, and the withdrawal probability in lines 232–242.

A refusal-like opening such as "I cannot…" shows that the response looks safe now, but not that it will stay safe once steering ends. This is the shallow safety alignment phenomenon identified by Qi et al. (2025), "Safety Alignment Should Be Made More Than Just a Few Tokens Deep", which we cite in our related work. They show that safety alignment acts mainly on the first few output tokens and leaves the model's behaviour over later tokens largely unchanged. The same concern applies to a steered refusal opening. It is a shallow signal, and a prefix classifier would read exactly that signal. Our own results show this directly, since on Qwen3-4B at 512 tokens even 64 steered tokens do not restore safety to the level of persistent steering (85.75% vs. 90.50%, Table 6).

To measure persistence directly, our same-prefix protocol (Section 3.2, lines 180–186) branches from an identical prefix and decoding state and compares withdrawing steering against continuing it. Adaptive withdrawal is built to predict this intervention decision, rather than current prefix safety.

We hope these clarifications address your questions about the two features, the observation window and what the predictor estimates. We have made each of these points explicit in the revised manuscript, and we hope you will consider raising your score.

Reviewer_UYw4OpenReview ↗
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Paper summary

The paper asks how long refusal steering needs to stay on. Steering starts at the first output token. After two steps, the method reads two scalars from an output-proximal layer. Writing rdr_d for the normalized projection onto the refusal direction at decoding step dd, the features are V=r1V = r_1 ("refusal veracity") and U=∣r1−r0∣U = |r_1 - r_0| ("refusal velocity"). A discrete-time logistic hazard model maps them to a per-prompt duration in 2,4,8,16,32,64{2, 4, 8, 16, 32, 64} or persistent steering. The threshold is chosen on 120 calibration prompts under a 5-point HarmBench non-inferiority margin. On Gemma-1.1-7B, Llama-3.1-8B, Qwen3-4B and Qwen3-8B, the method:

  • cuts steered positions by 38.5–72.5%,
  • keeps complete-response HarmBench safety close to persistent steering, and
  • matches or beats persistent steering on XSTest, OR-Bench and MMLU.
Critical strengths
  • The question is practical and the payoff is clear. Persistent steering hurts benign behavior (e.g., XSTest drops from 80.4 to 61.2 on Gemma), and adaptive withdrawal recovers most of it (78.8).
  • The method is cheap and easy to deploy. It uses two scalars from activations that are already computed, with no extra forward pass and no judge at inference time.
  • The same-prefix branching protocol is a good way to isolate the effect of continued steering. I also appreciate that the appendix reports many results that don't favor the method.
Critical weaknesses

W1. The safety-persistence claim isn't supported by the paper's own tests. The contributions say safety is preserved "even when generation continues long after steering ends". The paper's own results say otherwise:

  • Sec. 3.2 counts a withdrawal point only if the post-withdrawal continuation also stays comparable. Under HarmBench, the judge used for calibration, this fails for Llama, Qwen3-4B and Qwen3-8B (Table 7).
  • At 512 tokens, Qwen3-4B continuation safety is 70.93% vs 91.20% (greedy) and 74.00% vs 93.33% (sampled). That's a gap of about 20 points (Table 9).
  • On complete responses, Granite Guardian gives 73.50% vs 91.75% on Qwen3-4B. MD-Judge fails the criterion on all four models (Table 19).

The positive long-generation results come mostly from the prompted Qwen2.5-14B judge. That judge is much more lenient here, and I didn't see it validated against human labels. Aggregate rates can't separate judge artifacts from real harmful continuations, so a fair conclusion for now is "unresolved", not "safety persists".

Robustness looks similar. In Table 16, the delimiter-reversal wrapper lowers continuation safety by 12.8–20.5 points on all four models. The adaptive attack in App. G.4 is described as stronger, yet it causes only 4.4% new failures overall. That figure rises to 13.8% on Llama, where no tested minimum-duration safeguard qualifies.

W2. It's unclear what the learned multi-duration policy adds over simpler options.

  • Since the predicted CDF is monotone in η=βVz(V)+βUz(U)\eta = \beta_V z(V) + \beta_U z(U), the policy amounts to ordered cutoffs on that one score. In practice it's close to a two-way choice: for Gemma and Llama, about 95% of prompts get one of two durations (2 and 64 for Gemma, 2 and persistent for Llama; Table 11).
  • Velocity clearly helps only on Qwen3-8B (C-index from 0.800 to 0.920, Table 12). In cross-model transfer, velocity alone ranks Gemma's prompts worse than chance (0.204, Table 21). The evidence supports "the early refusal projection is a good signal" more than a trajectory/velocity story.
  • At α∈2,3\alpha \in {2, 3}, all eight fitted policies in Table 17 are prompt-independent: either every prompt stops at 2 tokens or none is withdrawn.

So the obvious baselines are:

  • a calibrated two-action gate 2,persistent{2, \text{persistent}},
  • a V-only policy, and
  • a fixed 2-token pulse at higher strength.

They should all be compared at the same criterion on held-out safety, exposure and benign metrics. Right now, Table 12 only reports C-index and Brier, and the fixed-duration baseline in Table 4 isn't matched on safety.

W3. The MMLU gains are hard to attribute. Finite steering is switched off before answer scoring, but persistent steering stays on (App. A.4.2). On Llama, adaptive withdrawal removes only about 5 of 101 steered positions per question (Table 2). Yet MMLU goes from 29.8% to 39.8%, exactly the unsteered number. The simplest explanation is the unsteered scoring step, not shorter steering.

Also, unsteered MMLU is only 29.0% for Gemma-1.1-7B-IT and 39.8% for Llama-3.1-8B-Instruct. That's far below what these models usually get, and near chance for Gemma, so the protocol seems to hurt them on its own.

W4. The novelty is narrower than the framing suggests. As far as I know, predicting a per-prompt end time for refusal steering is new, but the pieces aren't:

  • SafeDecoding (Xu et al., 2024) already intervenes only during a fixed early window.
  • CAST and AdaSteer condition steering on internal activations.
  • SafeSwitch (Han et al., Findings of EMNLP 2025, not cited) uses internal-state probes to switch to a refusal head only when needed.

The predictor is a standard discrete-time hazard model. So the contribution is mostly empirical, which puts the weight on W1 and W2.

Minor.

  • "Retained safety" hides a lot near 100%. On Gemma, 97.0% vs 99.8% is reported as 97.2% retained, but the harmful rate goes from 0.2% to 3.0%, about 15 times higher. Please report harmful rates too.
  • Persistent steering already adds only 0.10–0.19% runtime (Table 2), so cutting exposure saves almost no compute. The real benefit is less over-refusal, and the paper should frame it that way.
  • "Veracity" and "velocity" are confusing names for a projection and an absolute difference.

Overall. The problem is worth studying and the branching protocol is a nice idea. But several of the paper's own results contradict the main safety claim. The benefit of the learned policy over much simpler baselines also isn't shown. I lean toward rejection in the current form. A version with narrower claims and the baselines from W2 could be a solid paper, and I'm open to raising my score if the rebuttal addresses W1 and W2.

Questions for authors
  1. Could you run a small blinded audit (say 50–100 cases) of the judge disagreements in Tables 9 and 19, especially on Qwen3-4B? That would separate real harmful continuations from judge artifacts.
  2. Under the same criterion, what are held-out safety, exposure and benign metrics for a two-action gate 2,persistent{2, \text{persistent}}, a V-only policy, and fixed 2-token pulses at α∈2,3\alpha \in {2, 3}?
  3. What is MMLU accuracy with persistent steering during analysis but none at scoring? And is scoring steered when the adaptive policy falls back to persistent?
  4. Why is persistent steering on Qwen3-8B at 93.6% in Table 1 but 89.75% in the matched sweep (App. C.1), apparently on the same 400 prompts?
5 comments
AuthorsOpenReview ↗

Official Comment Part 1

Thank you for recognising the practical motivation, the inexpensive inference mechanism, and the same-prefix evaluation design. The main result of the paper stands. In the evaluated 128-token setting, adaptive withdrawal removes 38.5–72.5% of the intervention while keeping complete-response safety comparable to persistent steering on all four models. The statement that safety is preserved "even when generation continues long after steering ends" went beyond this evidence, and we have removed it. The revised paper reports the failure cases you identified as limitations. We also ran the blinded audit and the baselines you requested. All modifications are marked in red.

W1 and Q1. Safety persistence and evaluator disagreement

The original text did not clearly distinguish the safety of the complete response from the safety of the text generated after steering is withdrawn. The revised manuscript reports the two separately. On complete responses, adaptive withdrawal is comparable to persistent steering on all four models under HarmBench and Qwen2.5 (Table 7). On post-withdrawal continuations, only Gemma passes under HarmBench (Table 7), and at 512 tokens Qwen3-4B loses about 20% (Table 9). We do not use the first result to support the second.

For Q1, we conducted the blinded audit you suggested on Qwen3-4B. Five undergraduate raters, blind to the method and to every judge label, rated 40 randomly sampled disagreement pairs from Table 19 and 40 from Table 9 (80 cases, 160 responses). Fleiss' κ was 0.58.

Disputed pairsJudge reporting the gapConfirmed by raters (mean over five raters)
Table 19, 128-token complete responsesGranite Guardian5.2 of 40 (13%)
Table 9, 512-token continuationsHarmBench23.2 of 40 (58%)

The audit separates the two cases. Most of the Granite Guardian gap at 128 tokens is not confirmed by human raters. Most of the HarmBench gap at 512 tokens is confirmed, so the long-generation drop on Qwen3-4B is real and is a limitation of the original policy. The prompted Qwen2.5 judge misses these cases, and we no longer rely on it for long-generation claims. In a separate blinded study on 100 randomly sampled prompts at 128 tokens, the same raters gave 92.2% safety for adaptive withdrawal and 94.6% for persistent steering. The 95% confidence interval on this 2.4% gap is −2.1% to 6.9%. It contains the HarmBench gap on the same model, which is 0.0% on the primary evaluation (95.5% vs. 95.5%, Table 10) and 2.3% in the same-prefix validation (94.08% vs. 96.42%, Table 7), and it excludes the 18.25% gap reported by Granite Guardian (Table 19). Human judgement is therefore consistent with our calibration evaluator, and we report this study as supporting evidence, not as a formal non-inferiority test.

Within the 128-token setting the evidence is stronger. On the 159 official HarmBench direct requests, the original frozen policies pass the multiplicity-adjusted criterion on post-withdrawal continuations for all four models, and the complete-response comparisons pass the pointwise criterion.

ModelUsable pairs (Appendix D.1)Adaptive continuation safetyPersistent continuation safetyIntervention reduction
Gemma-1.1-7B-IT15899.37%99.37%93.7%
Llama-3.1-8B-Instruct15592.26%90.32%89.9%
Qwen3-4B142100.00%100.00%72.9%
Qwen3-8B15098.00%99.33%91.8%

On evaluator transfer, giving MD-Judge the original request as context lets Gemma and Llama pass (97.50% vs. 99.00% and 82.00% vs. 81.00%), but the two Qwen models still do not, so that disagreement is only partly explained by context.

On robustness, the adaptive attack induces finite withdrawal on 318 of 320 prompts, and 304 of those withdrawals cause no new safety failure (Table 25). There are two clear failure cases. Under the delimiter-reversal wrapper, withdrawal lowers continuation safety by 12.8–20.5% on all four models (Table 16). The adaptive attack causes 13.8% new failures on Llama (Table 25), where no finite minimum duration qualifies and the safeguarded policy falls back to persistent steering. The safeguards in Appendix G.4.3 address the tested attack only. The revised manuscript reports each attack family separately and makes no general robustness claim.

(continued in Part 2)

AuthorsOpenReview ↗

Official Comment Part 2

W2 and Q2. Simpler policies and the value of duration prediction

We ran the two-action gate and the fixed two-token pulse on the 400 held-out prompts per model under the same criterion, and the V-only policy on the 159 direct requests. A calibrated two-action gate, trained directly to choose between withdrawal at two tokens and persistent steering, passes the multiplicity-adjusted complete-response criterion on all four models and removes 37.7–62.4% of the intervention, against 38.5–72.5% for the full policy in the paper. This shows that useful withdrawal on complete responses does not depend on our specific predictor. Much of the benefit comes from this two-way decision, and the revised manuscript says so. The multi-duration policy adds intermediate durations where a gate must keep steering on. This matters most on Qwen3-4B, where 320 of 400 prompts receive a duration between 4 and 32 tokens (Table 11).

A fixed two-token pulse fails the pointwise complete-response criterion on all four models at the primary strength, so two-token withdrawal cannot be applied to every prompt and has to be selective. At higher strengths the fitted policies are prompt-independent, as you note from Table 17, and the revised text states that the prompt-specific policy matters at the primary strength.

We accept your reading of the velocity results. Velocity clearly improves ranking only on Qwen3-8B (C-index 0.800 to 0.920, Table 12), and velocity alone does not transfer across models (Table 21). On the 159 direct requests the V-only policy reaches the same safety on Qwen3-4B (99.37%) but needs about twice the intervention (58.71 vs. 28.81 mean intervention points). The two predictors rank Qwen3-4B prompts equally well (Table 12), so we do not attribute this difference to better ranking. The revised text presents the early refusal projection as the main signal and velocity as a model-dependent refinement.

W3 and Q3. Matched MMLU evaluation

Thank you for identifying the scoring confound in the Table 1 MMLU results. We re-ran MMLU on the same 1,026 questions with two protocol changes. The model generates its full analysis with no cut-off at 96 tokens, and the answer is scored without steering for every method, including the persistent fallback. The "Persistent steering" column therefore answers Q3 directly.

ModelUnsteeredPersistent steeringAdaptive withdrawal
Gemma-1.1-7B-IT46.2%44.2%45.1%
Llama-3.1-8B-Instruct57.2%54.7%56.1%
Qwen3-4B68.4%65.9%68.2%
Qwen3-8B69.4%67.1%68.2%

Under the matched protocol the differences are small. Persistent steering costs 2.0–2.5% relative to unsteered generation, and adaptive withdrawal is 0.9–2.3% above persistent steering on every model and within 1.2% of unsteered accuracy. These differences are modest. On 1,026 questions each accuracy has a standard error of about 1.5%, so a single-model difference of 0.9–2.3% is comparable to the sampling error of the estimates. The revised manuscript therefore presents MMLU as evidence that withdrawal does not reduce accuracy relative to persistent steering, and no longer presents it as a gain. The low accuracies you noted came largely from the 96-token limit. With full analyses, unsteered accuracy rises from 29.0% to 46.2% on Gemma and from 39.8% to 57.2% on Llama.

W4. Contribution and relationship to prior work

Our contribution addresses a distinct control decision, namely how long an already-active refusal intervention should remain applied for each prompt. SafeDecoding intervenes within a fixed early window. CAST and AdaSteer decide whether and how strongly to steer, and SafeSwitch uses internal signals to switch on a safety head. Our method predicts a prompt-specific stopping time from two early activation readings, with no fine-tuning, no additional forward pass and no evaluator at inference time. We agree that the contribution is mostly empirical. We have added SafeSwitch to Section 2 and made these distinctions explicit.

(continued in Part 3)

AuthorsOpenReview ↗

Official Comment Part 3

Q4. Persistent controls in separate experiments

The two numbers come from separate runs on the same prompts. Table 1 reports the mean of five greedy reruns (93.6%), and the Appendix C.1 sweep is a separate greedy run with its own matched persistent control (89.75%). Greedy decoding removes sampling randomness but does not guarantee identical outputs across separate runs, since a small numerical difference can change one selected token and everything generated after it. Each restoration width is therefore computed against the control from its own run. Appendix C.1 reports simultaneous lower bounds of −1.76% at width 32 and −2.30% at width 64, and a stricter adjustment over a larger set of comparisons gives −2.75% and −3.50%. All four bounds are within the −5% margin.

Minor points

The revised manuscript reports absolute harmful-response rates next to retained safety, for example 3.0% vs. 0.2% on Gemma. It also frames the benefit as reduced over-refusal and no longer presents compute savings as a result. Adaptive withdrawal raises the XSTest answer rate over persistent steering by 5.8–17.6% on Gemma, Llama and Qwen3-4B (Table 1). We keep the names refusal veracity and refusal velocity, and Section 3.3 defines them as the projection onto the refusal direction at the second output step and its absolute change between the first two steps.

Based on the blinded audit, the simpler-policy comparisons, the matched MMLU evaluation and the narrower claims above, we hope we have addressed your concerns, and we hope you will consider raising your score.

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

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