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Under review as a conference paper at ICLR 2027

C-Δθ: Circuit-Restricted Weight Arithmetic for Selective Refusal

Abstract

Modern deployments require LLMs to enforce safety policies at scale, yet many controls rely on inference-time interventions that add recurring compute cost and serving complexity. Activation steering is widely used, but it requires runtime hooks and scales cost with the number of generations; conditional variants improve selectivity by gating when steering is applied but still retain an inference-time control path. We ask whether selective refusal can be moved entirely offline: can a mechanistic understanding of category-specific refusal be distilled into a circuit-restricted weight update that deploys as a standard checkpoint? We propose C-Δθ : Circuit Restricted Weight Arithmetic, which (i) localizes refusal-causal computation as a sparse circuit using EAP-IG and (ii) computes a constrained weight update Δθc supported only on that circuit (typically <5% of parameters). Applying Δθc yields a drop-in edited checkpoint with no inference-time hooks, shifting cost from per-request intervention to a one-time offline update. We evaluate category-targeted selectivity and capability retention on refusal and utility benchmarks.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM Safety, Deployment Efficiency, Weight Editing, Circuit Localization, Selective Refusal

Reviews

Among:
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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_fa2EOpenReview ↗
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2
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Paper summary

The paper addresses the problem of custom-domain policy refusal control in LLMs. They introduce “Circuit-restricted weight editing”, a method that uses Edge Attribution Patching (EAP-IG) to find refusal-causal circuits in a model, and then computes a masked weights update that works only on the parameters within these circuits to improve safety while maintaining model utility without the need for any inference-time steering. The method is evaluated across 6 models from 2 different families showing almost consistent gains against steering baselines. The paper also gives extensive experiments and ablations across safety, utility, and circuit selection.

Critical strengths
  1. The idea behind the proposed methodology is intuitive and interesting. If refusal in LLMs is propagated through specific circuits, identifying and updating these parameters makes a lot of sense. The method also avoids inference-time overhead.

  2. The paper provides extensive experimental evaluation across multiple models and harm categories, with several interesting ablations and evaluations of safety and utility preservation.

Critical weaknesses
  1. Limited evidence of category-specific refusal control. The method is proposed for models or systems that “may need to strengthen refusal for one policy domain”, but the results in Table 5 seem to contradict this. All models, regardless of the category of prompts used to identify updatable parameters, improve comparably across all categories. In the “Health” category, for example, other edit categories produce better safety results in that category compared to the “Health” edit. While this does not contradict the authors' definition of harmful-versus-benign selectivity, it raises questions about the value of category-conditioned circuit discovery.

  2. Limited generalization of the claimed refusal selectivity. Although Table 1 shows relatively low benign over-refusal, the method seems to induce significant over-refusal on challenging over-refusal benchmarks (XSTest) in the Gemma example in Table 15. The ‘optimal’ steering weight α\alpha in Table 1 leads to significant over-refusal (≈49\approx 49). Reducing the steering strength to lower over-refusal drops harm refusal from ≈90\approx 90 to only 45.645.6. This makes the usability of the method in real-world scenarios questionable.

Questions for authors
  1. Could you please provide additional over-refusal / harm refusal trade-offs across models and steering strengths?
  2. What is the impact of using categorical prompts during the first phase of your pipeline (circuit discovery)? How would the results in Table 5 look with a baseline where all categories were used together?
  3. In Section 3.1, the clean and corrupted runs change both the prompt harmfulness and the refusal/compliance continuations. This makes it difficult to isolate which part is responsible for refusal. Have the authors considered a counterfactual using the same harmful prompt with refusal and compliance continuations?
  4. How does your method compare to more recent safety weight-editing and steering baselines? See [1, 2]

[1] AlphaSteer: Learning Refusal Steering with Principled Null-Space Constraint (Sheng et al, ICLR 2026).

[2] Turning the Spell Around: Lightweight Alignment Amplification via Rank-One Safety Injection (Abu Shairah et al, EMNLP 2026).

3 comments

Thank you for the questions on pooled discovery, the same-prompt counterfactual, hard-benign trade-offs and newer baselines. New results are in Section 5.5 and Appendix L (orange).

W1/Q2. Category specificity and a pooled baseline. The category edits share much of their structure. One reason is that we use the contrastive dataset of CAST (Lee et al., 2025), in which all category datasets are designed around the same benign prompts, so the discovery sets are similar to each other. Our selectivity claim is about harmful versus benign prompts within a policy; we do not claim zero transfer across harm categories. We implemented the pooled baseline you suggested: one shared support discovered from 700 examples (about 140 per category), one pooled update, and a single α = 0.65 chosen on joint validation (mean harmful refusal, every benign rate ≤ 10%). One checkpoint serves every category, with no routing:

CategoryOne pooled edit for all categories: harmful / benignSeparate edit per category (paper): harmful / benign
Crime94.3 / 8.394.0 / 6.9
Hate92.9 / 8.395.1 / 6.6
Health60.6 / 8.353.4 / 11.4
Legal66.0 / 8.358.9 / 10.3
Sexual79.4 / 8.378.9 / 8.6

Pooling helps Health and Legal (+7.1 pp each, p ≈ 0.018 after correcting for five categories); the other differences are not significant. MMLU is 68.52% vs. 68.74% base. Pooled discovery works as an extension of the framework, and per-category discovery remains available when a single policy is targeted.

W2/Q1. Hard-benign trade-offs. The revision adds full α curves on XSTest-safe, OR-Bench-hard and MMLU for Llama Crime/Legal and Gemma Crime. Lower strengths give a different trade-off: Gemma Crime at α = 1 has 62.7% validation harmful and 16.4% XSTest-safe refusal with unchanged MMLU (59.7%); base is 24.7% and 6.4%. Training the contrastive update with hard-benign negatives on the standard support lowers OR-Bench-hard refusal from 78.0 to 55.7% and FalseReject-test from 47.5 to 24.9% at the same 62.7% validation harmful refusal (paired p ≈ 4.4e-12 and 1.4e-10; XSTest not significant), with MMLU 59.0% vs. 59.7% (exploratory; Appendix L includes a ratio-matched control).

Q3. Same-prompt counterfactual circuits. We ran this on Llama-3.1-8B and Gemma-3-4B, Crime and Legal: discovery holds each harmful prompt fixed and contrasts a refusal continuation with a compliance continuation, and training and calibration are unchanged (Appendix L). The paper's contrast (harmful prompt with refusal vs. harmless prompt with compliance) gives higher test harmful refusal in three of four settings: Llama Crime 94.0 vs. 90.0%, Gemma Crime 97.1 vs. 92.6%, Gemma Legal 38.9 vs. 34.3% (p ≤ 0.044), with no significant benign difference. The same-prompt contrast is better on Llama Legal (65.1/9.7 vs. 58.9/10.3, p = 0.012). It selects a largely different set of channels (Jaccard 0.13–0.20 with the standard mask) that still gives a usable edit. We keep the paper's construction and report the same-prompt variant in Appendix L.

Q4. Newer baselines (Appendix L, Table 42). Test refusal (%, n = 350) and MMLU (5-shot) on Llama-3.1-8B Crime:

MethodHarmfulBenignMMLU
Base model42.90.668.7
C-ΔΘ94.06.968.5
AlphaSteer, matched to C-ΔΘ's benign refusal79.16.642.3
AlphaSteer, intermediate strength (1.25)62.31.163.3
ROSI, best layer70.02.656.7

AlphaSteer steers activations at inference time, constrained to a null space meant to leave benign inputs unchanged; we used the official repository and steering matrix. At C-ΔΘ's benign refusal it reaches 79.1% harmful refusal, against 94.0% for C-ΔΘ, and no strength in its grid reaches 94.0%. At this strength its MMLU falls to 42.3% (base 68.7%).

ROSI adds a rank-one refusal direction to the attention and MLP output projections, with no training. We adapted it to each category and chose the layer on validation. On Llama Crime it reaches 70.0% harmful refusal only at a strength where MMLU falls to 56.7%. On Gemma Crime it reaches 45.1% with MMLU at 26.0%, and on Llama Legal 2.3%, against 97.1% and 58.9% for C-ΔΘ. Both baselines buy harmful refusal with general capability: MMLU drops by about 5 points for AlphaSteer at a much lower harmful refusal, and by 12 to 34 points for ROSI. C-ΔΘ reaches the highest harmful refusal while keeping MMLU within 0.3 points of the base model on Llama (68.5 vs. 68.7%) and within 0.1 points on Gemma, because it learns its update from contrastive data on the selected channels only.

I thank the authors for their response and for running many additional experiments, which I really appreciate.

Unfortunately, some of the new results further reinforce my original concerns. The pooled categories edit performs comparably to, and sometimes better than, the category-specific edits, further questioning the need for per-category circuit discovery. The authors suggest this may be due to the dataset, but this explanation needs actual evidence to support. Otherwise, the benefit of category-specific discovery remains unclear, especially with the paper's motivation of enabling targeted policy edits.

Additionally, the rebuttal mentions adding "full α curves on XSTest-safe, OR-Bench-hard and MMLU," but I could not find these plots in the revised paper or appendix. Could the authors please include them or point me to their location?

For these reasons, I will maintain my original score for now.

Thank you for the follow-up. We apologize for the missing figure, the α curves are now Figure 11 in Appendix L.

Pooled vs. per-category discovery. The pooled results follow from how the contrastive data of Lee et al. (2025) is built. In all 700 training rows, the five categories share the same benign prompt, and each category's harmful prompt is a rewrite of that prompt. Within a row, the harmful prompts of different categories share 0.20 of their words, against 0.03 across rows. Half of each category's discovery contrast is therefore identical, so the category masks overlap and a pooled edit loses little on harmful vs. ordinary benign refusal. Where per-category discovery does make a clear difference is on hard-benign prompts. At matched test harmful refusal on Crime (94.0% vs. 94.3%), the Crime-only edit refuses 54.4% of XSTest-safe and 86.0% of OR-Bench-hard prompts, against 69.6% and 95.7% for the pooled edit.

Reviewer_mGSmOpenReview ↗
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Paper summary

The paper proposes C-ΔΘ, an offline procedure for strengthening refusal behavior in a selected harm category without inference-time activation-steering hooks. It first applies EAP-IG to contrastive harmful/benign prompt pairs to select sparse MLP output-projection channels. Two models are then fine-tuned on refusal versus compliance suffixes with gradients restricted to that support, and their weight difference is added to the base checkpoint. Experiments cover six Llama/Gemma models and five harm categories, comparing refusal of harmful prompts against over-refusal on benign prompts, with additional out-of-distribution safety, capability, mask-selector, and composition analyses. The reported results often improve the harmful/benign refusal trade-off while retaining most measured capabilities.

Critical strengths
  • C-ΔΘ produces an edited checkpoint without inference-time steering hooks, offering a practical alternative to activation-based interventions.
  • Combining EAP-IG circuit localization with constrained weight arithmetic provides a structured approach to targeted behavioral modification.
  • Experiments span six models and five harm categories, with inverse-mask controls, capability benchmarks, and robustness analyses supporting the method's effectiveness.
Critical weaknesses
  • The Gemma Crime edit refuses 49.2% of safe XSTest prompts versus 12.0% for the base model, raising concerns about selectivity beyond the main benign benchmark.
  • Random and gradient-based masks achieve competitive or better results in some settings, making the distinct contribution of attribution-based localization uncertain.
Questions for authors
  • Is the calibration set used to select α disjoint from the held-out test set used in Table 1?
  • How does EAP-IG compare with random and gradient-based masks on hard-benign benchmarks at matched harmful-refusal rates across more models and categories?
2 comments

Thank you for the positive assessment and the concrete questions. New results are in the revised PDF, marked in orange (Section 5.5, Table 6, Appendix L).

Q1. Was α chosen on separate data? No. In the submission, α was selected on the same prompts we report. As an additional check, we re-selected α on 150 validation prompts per category and evaluated once on the remaining 350, with the same rule for C-ΔΘ and every control. The conclusions do not change: on the two main models all 10 settings stay within their benign cap on the held-out prompts, and across all 30 model/category settings the results are similar to the original operating points, each still raising harmful refusal over its base model (Section 5.5).

W2/Q2. Attribution versus simpler supports. At the original 15% budget, a random mask with the same per-layer counts as the EAP-IG mask performs about as well (Llama Crime: EAP-IG 94.0%, layer-matched random 94.9%), while a random mask spread evenly over depth drops to 84.9%. At this budget, EAP-IG's main contribution is choosing which layers to edit and how many channels each gets. To test whether the ranking of channels within a layer also matters, we trained every category on both main models at 1% and 5% of MLP-output rows, against three layer-matched random masks and a gradient-attribution mask per setting (Table 6):

  • At 1%, EAP-IG is ahead of layer-matched random in 5 of 10 settings (Llama Legal and Health; Gemma Crime, Legal, and Hate at higher benign refusal), tied in 3 (Llama Crime, Hate, Sexual) and behind in 2 (Gemma Health; Gemma Sexual nominally).
  • At 5%, random never significantly beats EAP-IG on harmful refusal. EAP-IG is higher on Legal in both models (+9.1 and +16.6 pp) and on Gemma Health (+12.2 pp), and statistically tied in the other seven.

EAP-IG reliably picks the right layers and channel counts. Its ranking of individual channels within a layer adds harmful refusal mainly at tight budgets and is not always the best choice. We have revised the claims in Section 5.5 to match.

Q2. Selectors on hard-benign prompts at matched harmful refusal. We ran this comparison on Llama-3.1-8B and Gemma-3-4B, Crime and Legal (κ = 15%). Each selector's strength is set so its validation harmful refusal matches EAP-IG's, and all are scored on the same 250 XSTest-safe prompts (Appendix L). XSTest-safe refusal, lower is better:

SettingEAP-IGLayer-matched random (mean of 3)Gradient
Llama Crime54.462.352.8
Llama Legal50.847.643.6
Gemma Crime68.471.283.2
Gemma Legal52.857.263.6

EAP-IG refuses fewer safe prompts than random in three of four settings (Llama Crime: against every draw, p ≤ 0.02) and fewer than gradient attribution on both Gemma settings (p ≤ 2e-4). No single selector is lowest in every setting.

W1. Hard-benign over-refusal. Over-refusal on hard-benign prompts depends on edit strength, and the revision adds full strength curves on XSTest-safe, OR-Bench-hard and MMLU. Llama Crime at α = 0.4 reaches 74.0% validation harmful refusal with 0.7% ordinary benign and 21.6% XSTest-safe refusal (base: 38.7%, 0.7%, 11.6%; MMLU 68.56% vs. 68.74%). The method also accepts hard-benign negatives: training the contrastive update with them on the standard support (Gemma Crime) lowers OR-Bench-hard refusal by 17–24 points at matched validation harmful refusal, with some increase in ordinary benign refusal at the highest strengths. C-ΔΘ edits refusal for a chosen policy category, and we report hard-benign refusal next to each operating point.

Thanks for the additional experiments and discussions. The held-out α\alpha selection and the selector comparisons answer my questions. I will keep my score.

Reviewer_qhAEOpenReview ↗
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Paper summary

This paper proposes Circuit Restricted Weight Arithmetic (C-ΔΘ\Delta\Theta) to strengthen refusal to harmful requests while retaining compliance with other requests. C-ΔΘ\Delta\Theta is a 2-stage algorithm: (1) first, by applying the attribution metric in EAP-IG, it identifies a circuit (subset of MLP output channels) that relates to refusal; (2) second, by using weight arithmetic to find a direction Δθ=θ+−θ−\Delta \theta = \theta_+ - \theta_- with the circuit masking (where θ+\theta_+ induces the desired behavior while θ−\theta_- induces the opposite behavior, and both are supported only on the circuit), it applies the direction to the model, θ′=θ+αΔθ\theta^\prime = \theta + \alpha \Delta\theta. Numerical results have shown tradeoffs between benign and harmful refusals, and comparisons to activation steering methods and weight arithmetic without circuit masking are provided.

Critical strengths
  • The proposed method produces an edited checkpoint without inference-time interventions, and the steering coefficient α\alpha provides an easy way to explore the harmful/benign tradeoff.
  • Experiments have been performed across various models and tasks, and harmful and benign refusals are both reported.
Critical weaknesses
  • While the method is called Circuit Restricted Weight Arithmetic, it is unclear whether the selected channels truly form a circuit. Unlike EAP-IG in Hanna et al. (2024) that uses greedy search to find the connected circuit, top-κ\kappa of MLP output channels applied in this work does not ensure the faithfulness of the circuit. Figure 7 shows that the selection concentrates on the first and last layers, while almost no parameters in layers 22-28 are selected. Also, Table 22 shows that the selected parameters do not overlap much with random subsets of prompts, which means the selection is unstable.
  • The ablation study in Table 3 does not show a Pareto improvement of C-ΔΘ\Delta\Theta with top-κ\kappa mask over WS-MLP2 or inverse mask. Specifically, in most experiments, C-ΔΘ\Delta\Theta does not simultaneously show lower benign refusal and higher harmful refusal.
Questions for authors
  • Could you test the faithfulness of the circuit selected by top-κ\kappa attribution score?
  • Instead of the global top-κ\kappa channels, could you compare against the circuit by EAP-IG in Hanna et al. (2024)?
  • In Table 3, could you control the steering strength α\alpha to match one of the benign/harmful refusals so that we can compare the improvement on the other axis?
5 comments

Thank you for the review. One clarification first, since it bears on W1, Q1 and Q2: C-ΔΘ does not claim to find a complete circuit. It uses EAP-IG attribution, the same scoring used for circuit discovery and exactly the original EAP-IG algorithm, to select a small set of MLP output channels within the circuit, and fine-tunes only the weight rows that write those channels. "Circuit-restricted" refers to that attribution-based restriction. We will state this in Section 3 and write "attribution-selected channels" where "circuit" overstates the claim. New results are in Section 5.5, Table 6 and Appendix L (orange).

W1/Q1. Faithfulness. We edit selected channels and never prune the model to them, so circuit faithfulness has no clear definition for C-ΔΘ and the method does not rely on it. We still tested how much the behavior depends on the edited rows, by restoring half of them to base weights (per-layer sizes and removed-update norm matched):

Top-attributed half of edited rows restoredHarmful refusal, intact → restoredMMLU, intact → restored
Llama Crime95.3 → 78.768.5 → 68.5
Llama Legal59.3 → 18.068.6 → 68.6
Gemma Crime94.7 → 72.759.6 → 59.6

(Validation, n = 150, α fixed.) Across 45 conditions, 37 of the harmful-refusal drops are statistically significant (Holm-corrected), while MMLU stays within 0.5 points of the intact edit. The refusal gain therefore depends on the update to the selected rows, and removing that update does not damage general ability.

W2/Q3. Top versus inverse mask at matched operating points. We have added this comparison to the paper (Section 5.5, Appendix L). Each mask now gets its own validation-selected α under the same benign cap, and both are scored on the same 350 test prompts. Results for all ten settings (refusal in %):

SettingTop-ranked mask: harmful / benignBottom-ranked mask: harmful / benignHarmful difference, p (paired test)Significant after Holm correction
Llama Crime94.0 / 6.987.4 / 7.12.9e-4yes (top)
Llama Hate95.1 / 6.682.6 / 7.13.9e-10yes (top)
Llama Sexual78.9 / 8.651.7 / 7.71.1e-17yes (top)
Llama Health53.4 / 11.452.9 / 14.90.92no
Llama Legal58.9 / 10.365.1 / 10.90.04no
Gemma Crime97.1 / 9.184.6 / 8.31.1e-13yes (top)
Gemma Hate94.0 / 3.194.0 / 5.71.0no
Gemma Sexual93.7 / 7.177.1 / 6.92.4e-13yes (top)
Gemma Health46.0 / 8.044.9 / 9.40.70no
Gemma Legal38.9 / 9.731.7 / 9.44.1e-3yes (top)

The top-ranked mask is ahead in 9 of 10 settings. In 6 it gives significantly higher harmful refusal. In Llama Health, Gemma Hate and Gemma Health harmful refusal is tied and the top-ranked mask has lower benign refusal (11.4 vs. 14.9, 3.1 vs. 5.7 and 8.0 vs. 9.4). The bottom-ranked mask is ahead only on Llama Legal, and not significantly once we correct for testing ten settings. Each mask has its own α, so the gap does not come from using one strength for both: the channels EAP-IG ranks highest are a better place for the edit than the channels it ranks lowest.

Q2. Hanna et al. We use the same EAP-IG scores as Hanna et al. (2024). The methods differ in what they do with them: Hanna et al. extract a connected edge circuit and measure how faithfully it reproduces the model, while C-ΔΘ takes the top-scoring MLP output channels and edits their weight rows. An edge circuit does not define weight rows to edit. To test the granularity question, we selected whole MLP blocks by node-level EAP-IG under the same 15% budget, with training and calibration unchanged (Appendix L). Row-level selection gives higher harmful refusal on Llama Crime (94.0 vs. 82.0%). On Legal the block-level edit reaches 64.0% but exceeds the 15% benign cap (16.3% vs. 10.3%). All differences are significant (p < 0.03).

Figure 7 and global top-κ. We separate depth allocation from ranking with per-layer attribution quotas, layer-matched random and uniform-depth random supports. On Llama Crime, global top-κ reaches 94.0% vs. 84.3% for the per-layer quota and 84.9 ± 0.9% for uniform-depth random, while layer-matched random reaches 94.9%. The depth profile chosen by global ranking, including the sparse middle layers, drives the result there. At tight budgets the ranking itself also helps (Table 6: Legal in both models at 1% and 5%, Gemma Health at 5%).

Table 22 (now Table 23), overlap. Low overlap between masks does not make the edits unstable. A mask discovered on all categories together gives category edits close to those from each category's own mask, and editing Crime with the Legal mask gives 94.3/8.3 test harmful/benign refusal against 94.0/6.9 with the Crime mask. The overlaps in Table 23 are low because those masks came from small discovery sets. Running discovery on three independent random subsets of 600 of the 700 Llama Legal pairs gives pairwise Jaccard 0.75–0.78 at κ = 15% (3.1–3.3× layer-matched chance), and each agrees with the full-data mask at 0.74–0.77 (Appendix L). With 250 pairs agreement is 0.38–0.47, and with the 50–100 pairs of our earlier runs about 0.26. Edits retrained from two resampled masks reach 60.6% and 59.7% test harmful refusal on Legal, against 58.9% for the full-data edit (benign 12.6% and 15.1% vs. 10.3%). With enough discovery data, EAP-IG finds largely the same channels each time, and masks from different samples give the same edit.

Dear Reviewer qhAE,

We sincerely appreciate your time and thoughtful feedback. We would like to kindly ask whether our rebuttal has addressed your concerns. We are happy to discuss any other concerns.

Reviewer_eWSaOpenReview ↗
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Paper summary

This paper proposes C-ΔΘ, a circuit-restricted weight editing method for selective refusal in LLMs. It first uses EAP-IG to identify refusal-related MLP output channels and then performs contrastive weight editing within the selected parameters. The resulting model is a standalone checkpoint that does not require additional inference-time interventions. The authors evaluate the method across six models and five harmful-content categories, showing improvements in harmful refusal while generally maintaining relatively low benign refusal.

Critical strengths
  1. The paper addresses an important practical problem: improving targeted refusal behavior without introducing additional inference-time overhead.

  2. The proposed framework is intuitive, combining mechanistic attribution with contrastive weight editing to constrain the parameters involved in behavioral changes.

  3. The experiments are relatively extensive, covering multiple model families, harm categories, and several ablation studies. The authors also investigate adaptive attacks and multi-category editing.

Critical weaknesses
  1. The methodological novelty is somewhat limited. The proposed approach mainly combines existing techniques, including EAP-IG for circuit attribution, contrastive weight steering, and sparse parameter updates. The main contribution is applying mechanistic circuit localization as a constraint on weight editing, rather than introducing a fundamentally new algorithm. While this combination is interesting, the paper could better distinguish its contribution from existing weight-steering and sparse editing approaches. In particular, it remains unclear how much of the observed improvement comes specifically from circuit localization rather than simply restricting the editable parameters.

  2. The contribution of EAP-IG is not fully established. The selector ablation results show that EAP-IG does not consistently outperform random or gradient-based selection. For example, gradient selection performs better on Llama Crime, and the authors acknowledge that no clear advantage over random selection is observed in this setting. Although EAP-IG performs better in some other settings, these mixed results make the necessity of mechanistic localization less convincing. Additional evidence showing when and why circuit-based selection is beneficial would strengthen the paper.

Questions for authors
  1. What is the main advantage of using EAP-IG for parameter selection compared with simpler sparse selection strategies?
  2. Can the authors provide further evidence that the selected channels are causally related to refusal behavior?
  3. Are the data used for selecting the steering coefficient α independent of the final evaluation data?

Minor Issues

  1. Some appendix pages contain considerable unused whitespace, and the overall formatting could be improved.
  2. The computational cost of the complete offline editing pipeline could be described more clearly.
2 comments

Thank you for the review. New results are in Section 5.5, Table 6 and Appendix L of the revision (orange).

W1, W2 and Q1. What EAP-IG adds beyond restricting the edit. EAP-IG decides two things: how many channels each layer may edit, and which channels within a layer. The first carries most of the gain at the original budget. The random masks in our selector ablation kept the same per-layer counts as the EAP-IG mask, so they inherited this depth profile, which is why they were competitive (Llama Crime: EAP-IG 94.0%, layer-matched random 94.9%). A random mask of the same size spread evenly over depth reaches only 84.9%, and the bottom-ranked mask gives significantly lower harmful refusal than the top-ranked mask in 6 of 10 settings (Appendix L). Restriction alone therefore does not explain the results. The choice of individual channels matters more as the budget shrinks: with only 1% of MLP-output rows editable, EAP-IG is ahead of layer-matched random in half of the ten settings, and at 5% random never significantly beats it (Table 6).

Q2. Causal evidence. Knocking out channels damages the model's general computation, so a knock-out test would not isolate refusal. C-ΔΘ acts through a learned update on the selected rows, so we test that update instead: we restore half of the edited rows to their base values (matched per-layer counts and removed-update norm, α fixed) and measure refusal. If those rows carry the refusal behavior, harmful refusal should drop while general ability stays intact. It does: validation harmful refusal falls from 95.3 to 78.7% on Llama Crime, 59.3 to 18.0% on Llama Legal and 94.7 to 72.7% on Gemma Crime, and MMLU stays within 0.5 points of the intact edit (Appendix L). The refusal gain therefore comes from the learned update on the selected rows. Which rows are selected matters most at small budgets, as the 1% results above show.

Q3. Is α independent of the evaluation data? No. In the submission, α was selected on the same prompts we report. As an additional check, we re-selected α on 150 validation prompts per category and evaluated once on the remaining 350. The conclusions do not change: on the two main models all 10 settings stay within their benign cap on the held-out prompts, and across all 30 model/category settings the results are similar to the original operating points, each still raising harmful refusal over its base model (Section 5.5).

Minor. We will fix the appendix layout. Appendix L gives the measured pipeline cost: EAP-IG discovery takes 20–26 minutes on Llama-3.1-8B and about 4 minutes on Gemma-3-4B on a shared GPU, and masked training takes a median of 23 and 16 minutes. The edited checkpoint keeps the original architecture and needs no runtime hooks.

Dear Reviewer eWSa,

We sincerely appreciate your time and thoughtful feedback. We would like to kindly ask whether our rebuttal has addressed your concerns. We are happy to discuss any other concerns.

Comments on the paper

1 comment
AuthorsOpenReview ↗

Summary of revisions and additional experiments

We thank all reviewers for their careful reading. We ran the following experiments in response. All are in the revised PDF (Section 5.5, Table 6 and Appendix L), with changed text in orange.

  1. Top-ranked vs. bottom-ranked channels at matched calibration (qhAE, eWSa). With each mask given its own α, the top-ranked mask is ahead in 9 of 10 settings, with significantly higher harmful refusal in 6.
  2. What attribution contributes (mGSm, eWSa, qhAE). EAP-IG sets how many channels each layer edits and which channels within a layer. At the original budget the depth profile carries most of the gain: a random mask spread uniformly over depth drops from 94.0% to 84.9% harmful refusal on Llama Crime. Even at matched depth (random masks with the same per-layer counts as EAP-IG), random never significantly beats EAP-IG at 5% of MLP-output rows, and EAP-IG leads in half of the settings at 1% (Table 6).
  3. Causal test of the learned update (eWSa, qhAE). Restoring half of the edited rows to their base weights cuts harmful refusal sharply (for example 59.3% to 18.0% on Llama Legal) while MMLU stays within 0.5 points of the intact edit.
  4. Newer baselines (fa2E). AlphaSteer (official repository and matrix) and a category-adapted ROSI. On Llama Crime, C-ΔΘ reaches 94.0% harmful refusal with MMLU at 68.5% (base 68.7%). AlphaSteer at the same benign refusal reaches 79.1% with MMLU at 42.3%, and ROSI's best layer reaches 70.0% with MMLU at 56.7%.
  5. Hard-benign prompts (mGSm, fa2E). Full strength curves on XSTest-safe, OR-Bench-hard and MMLU; a selector comparison on XSTest-safe at matched harmful refusal; and a variant trained with hard-benign negatives that lowers OR-Bench-hard refusal by 17–24 points on Gemma Crime.
  6. Pooled and same-prompt discovery (fa2E). One pooled edit with a single α covers all five categories and raises harmful refusal on Health and Legal by 7.1 points each. The same-prompt counterfactual contrast also gives a usable edit; the paper's contrast is higher in three of four settings.
  7. Granularity and stability (qhAE). Component-level (whole MLP block) selection, and discovery resampling: with 600 pairs, independent subsets give masks with Jaccard 0.75–0.78, and edits retrained from them match the full-data edit.
  8. Held-out strength selection (mGSm, eWSa). As an additional check, we re-selected α on 150 validation prompts per category and evaluated once on the remaining 350, for C-ΔΘ and every control. On the two main models all 10 settings stay within their benign cap, and across all 30 model/category settings the results are similar to the original operating points, each still raising harmful refusal over its base model.
  9. Cost and data audit (eWSa). Measured discovery and training times, and a duplicate audit of all data splits.

We also clarify that "circuit-restricted" means the edit is restricted to EAP-IG-selected channels, and we will state this in Section 3. The method and its central claim are unchanged.

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

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