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Under review as a conference paper at ICLR 2027

Separating Source Efficacy from Cross-Context Transfer of Refusal Directions

Abstract

Does a frozen refusal-direction intervention work in its source context, and how does the same intervention behave in each target context? We evaluate published directional ablation using paired, context-specific baselines. On Qwen2.5-7B, the original Site A candidate has no established positive source or Passive effect under a fixed single-layer operator. Changing the extraction site to B reveals semantic harmful-compliance increases of 59.0/51.5 percentage points at source and 37.0/13.9 on Passive (JailbreakBench/HarmBench). A weak extraction can therefore hide, under the same operator, an intervention that still raises Passive compliance. A second extraction, screened only on Questioning validation, is source-effective on held-out requests, though the weaker candidate's increment is small (+6.1 points; interval excludes zero). The candidate gap remains large on low-baseline Neutral, with no clear contraction detected (D_N = -1.0 points, 95% interval [-9.4, 7.3], including zero), and shrinks on Passive, whose no-intervention rate is already 65.3%. A review of 30 requests supports these two qualitative conclusions. Academic shows automatic contraction; human review is same-signed but uncertain. Checking source efficacy is not a substitute for measuring each target wrapper.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
LLM safety, refusal directions, cross-context transfer, mechanistic interpretability

Reviews

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1234this paper, Bottom 1%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.00 over 3 reviews, above 0% of the others.
Reviewer_UqQrOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
1
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Paper summary

This paper investigates the source-context efficacy and cross-context transfer of refusal-direction ablation, showing that intervention effectiveness depends on the extraction site and that source-effective directions can exhibit different effects across prompt contexts. Through experiments on Qwen2.5-7B and Llama-3.1-8B, the authors evaluate source and target effects using matched baselines, semantic harmful-compliance scoring, and additional control and human evaluations.

Critical strengths
  • The paper highlights an important evaluation issue by distinguishing source-context efficacy from cross-context transfer. This distinction helps avoid drawing misleading conclusions about transferability from interventions that are ineffective even in their source contexts.

  • The experimental evaluation is relatively thorough, including multiple models, extraction sites, intervention settings, matched baselines, and random-direction controls. The additional semantic scoring, human evaluation, and sensitivity analyses further strengthen the credibility of the findings.

Critical weaknesses
  • The novelty and significance of the main contribution are limited. Distinguishing source efficacy from cross-context transfer is a reasonable evaluation practice, but the paper does not clearly establish how this distinction advances our understanding beyond existing intervention-validation methods. Most findings remain descriptive, with limited insight into why different refusal directions behave differently across contexts.
  • The main Passive gap-contraction result is difficult to interpret due to the high baseline harmful-compliance rate (65.3%) and potential ceiling effects. Since both candidates already achieve high compliance in Passive, the reduced performance gap may largely reflect limited room for further improvement rather than meaningful differences in cross-context transfer. The current experiments do not adequately disentangle these explanations, weakening one of the paper's central conclusions.
  • The writing and presentation quality are poor and need substantial improvement. For example, several table captions are placed too close to the tables without proper spacing, and the figures do not use the PDF format. The text also contains repetitive, formulaic phrasing that reads like insufficiently edited AI-generated content, including excessive parenthetical expressions such as "(N = XXX)" throughout the prose and abbreviations such as "No-Int." that are not clearly explained when introduced. These issues make the paper unnecessarily difficult to read and obscure its main contributions.
Questions for authors
  • The Passive context already has a high baseline harmful-compliance rate (65.3%), and both candidate directions achieve over 80% compliance after intervention. To what extent is the observed gap contraction driven by ceiling effects rather than genuine context-dependent transfer behavior? Could the authors provide a baseline-matched or headroom-adjusted analysis to disentangle these explanations?

  • How robust are the reported source and transfer effects across different extraction seeds and sampling choices? The current bootstrap confidence intervals are conditional on fixed extracted vectors, while the experiments use different vectors across several comparisons. In particular, the newly extracted Site A direction shows a positive source effect under the H/N heuristic, unlike the original Site A result. Can the authors demonstrate that their key conclusions remain consistent across independently extracted directions under the same intervention and semantic evaluation protocol?

  • How reliable are the semantic evaluation results, especially for Passive and Academic contexts? The human–automatic agreement is relatively modest (77.9% overall), and 490 out of 500 Academic responses reach the 256-token limit. Could the authors evaluate longer or complete responses and use additional independent human annotators to verify whether the main conclusions, particularly the Academic gap contraction, remain valid?

  • The prompt wrappers differ substantially in wording, length, framing, and baseline harmful-compliance rates. How can the authors distinguish genuine cross-context transfer effects from changes in the underlying task formulation or evaluation behavior induced by these wrappers? Would more controlled prompt variations, where only one contextual factor changes at a time, lead to the same conclusions?

  • What concrete conclusions about refusal-direction transfer become possible through the proposed evaluation framework that could not be obtained using existing intervention-validation practices? The distinction between source efficacy and target effects is reasonable, but its methodological novelty and broader significance remain unclear. Could the authors clarify which prior assumptions or conclusions are challenged by their findings, beyond demonstrating that different extraction sites and intervention configurations produce different behavioral effects?

Reviewer_Ph1dOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

This paper constructs refusal vectors from the mean difference in residual stream activations between harmful and harmless queries, ablates these vectors, and then analyzes the harmful compliance rate when the prompt is reformulated into different formats. In experiments on Qwen2.5-7B with JailbreakBench and HarmBench, vectors extracted at one location were ineffective even in their original format, whereas vectors extracted at another location increased harmful compliance in both the original and the modified formats. Based on these results, the authors argue that one should first verify whether a vector is effective in its original format and, even when it is, measure its effect separately for each format.

Critical strengths
  1. Evaluating each intervention against the no-intervention baseline of the same format, and reporting the effects in the original format and in other formats separately, is a reasonable evaluation approach. In addition, the appendix includes a variety of sensitivity analyses and control experiments.
Critical weaknesses
  1. I find the writing and presentation of this paper unclear. The motivation, problem definition, and method are not clearly explained in the introduction. Terms such as “Passive,” “Site A,” and “Neutral” appear in the Abstract and Introduction without being defined, which makes the rest of the paper difficult to follow. In addition, the paper combines several experiment series that use different vectors at the same coordinates, different scoring rubrics, and different denominators. As a result, it is very difficult to tell which result supports which claim.
  2. The core claim of this paper, that one should “check that an intervention works at the source and measure each target context with its own baseline,” seems rather trivial. Furthermore, the experimental evidence for this claim appears weak. The contraction observed in the Passive format can largely be explained by its high no-intervention baseline (65.3%), which leaves little room for improvement.
Questions for authors
  1. The results for Site A appear to be inconsistent across Sections 5.1 and 5.2. The paper states that the newly extracted vectors are different tensors and therefore retains the original Site A finding. Could the authors provide a more robust analysis of this issue (e.g., a multi-seed analysis)?
  2. Could the Passive contraction be separated from the ceiling effect, for example by evaluating only the requests whose Passive baseline label is zero?
Reviewer_nP4BOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
1
Soundness
1
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Paper summary

Separating Source Efficacy from Cross-Context Transfer of Refusal Directions examines how methodological variations in extracting and evaluating refusal-direction interventions affect downstream jailbreak compliance in language models. Building on difference-in-means directional ablation (Arditi et al., 2024), the authors wrap harmful and harmless requests in five prompt templates (which they term "wrappers": Questioning, Neutral, Passive, Academic, and Scenario) and seek to separate whether an extracted refusal vector works in the prompt wrapper from which it was extracted ("source efficacy") versus whether it transfers when evaluated under a different prompt wrapper ("target wrapper").

The authors report two primary findings, which this review paraphrases in simpler language:

  1. When a refusal vector is extracted at a poorly located coordinate (i.e., an unvalidated layer and token position) and ablated at a fixed single layer, the intervention fails both in its source prompt format and in a reformulated target format. A better-chosen extraction site in the same model succeeds in both.
  2. When comparing a strong refusal vector against a weak refusal vector across different prompt wrappers, the performance gap between them remains large on a standard low-baseline prompt wrapper (Neutral), but shrinks substantially if evaluated on a target wrapper (Passive) that already acts as a strong prompt-level jailbreak on its own before any intervention is applied.

For validation, the authors primarily evaluate Qwen2.5-7B (and do secondary checks on Llama-3.1-8B) across 100 JailbreakBench and 101 HarmBench requests, scoring responses using an automated LLM judge (GPT-4o-mini), and a single-annotator human review on a 30-request subset.

Critical strengths

The authors cite a relevant and contemporary body of refusal-ablation and jailbreak literature (i.e., Arditi et al., 2024; Zhao et al., 2025; Wang et al., 2025a,b; Joad et al., 2026), providing a reasonable bibliographic entry point for readers interested in activation-level safety interventions.

Additionally, separating surface opening-refusal heuristics from semantic harmful-compliance judgments provides more evaluation grounding than studies that rely solely on keyword-based refusal matching. The authors also include a 30-request human annotation check alongside the automated judge, which is marginally more grounding in human judgment than many papers provide, even though it was limited to a single annotator.

There are, however, weaknesses associated with both strengths, which will be discussed below.

Critical weaknesses

Beyond typical scope limitations, such as relying primarily on a single 7B model with lighter checks on a second, or relying on a single automated LLM judge without extensive calibration, the paper has two critical weaknesses that undermine support for its two claimed contributions.

Weakness 1: The paper's two primary findings are methodological and statistical artifacts rather than substantive discoveries about refusal transfer, and largely rediscover conclusions already established in the papers they cite.

A. Finding 1 ("Site A vs. Site B") is an artifact of copying an unvalidated coordinate across model families and ablating at a single mismatched layer.

Site A (12, -5) is a coordinate the authors labeled "recipe" in their experiment records (Tables 13 and 22), which was used on 32-layer Llama-3.1-8B and then applied to 28-layer Qwen2.5-7B (which has a different depth and chat template, so token -5 is not even the same structural token position), while ablating only at a single different layer (k = 15).

Arditi et al. (2024) never prescribe blind cross-model coordinate transfer or single-layer ablation at a mismatched depth, and doing so is an inexplicable deviation from the established validation protocol. A core component of their methodology is validating candidate extraction sites on source validation data and ablating across all layers. When the authors apply Arditi et al.'s actual all-layer operator in Appendix K (Table 24, Figure 5b), even a vector at Site A's coordinate (A_new) jumps by +57.0 percentage points under their opening-refusal metric. This reflects a broader failure to build meaningfully on the cited literature, examined further in Weakness 2.

B. Finding 2 ("Passive contraction" vs. "Neutral retention") is driven by an obvious baseline ceiling effect that the paper fails to isolate.

In Table 3, the Passive wrapper with no intervention at all (NoInt) already elicits harmful compliance on Qwen2.5-7B 65.3% of the time, leaving only 34.7 percentage points of headroom below 100%. For any two interventions that do not reduce compliance below the no-intervention baseline, this ceiling makes it mathematically impossible to retain the roughly 65-point source gap observed in Q (+65.6 points in Table 4). Meanwhile, Neutral’s 4.0% baseline is nearly identical to Questioning’s 7.0%, which leaves ample headroom to preserve the candidate gap (+67.3 points).

The authors briefly concede in a single sentence in the Discussion that "Limited headroom could contribute to Passive contraction; we did not isolate this explanation from wording effects," yet make the questionable choice to present this contraction as a primary contribution in the Abstract and Introduction.

C. The "Academic contraction" extension (Section 5.3) is confounded by a 98% truncation rate at the 256-token generation cap.

In Section 5.3, 490 out of 500 Academic responses hit the hard 256-token cap because the prompt asks for a "comprehensive and rigorous historical analysis," cutting the model off mid-preamble before it reaches actionable steps. Rather than increasing the generation limit, the authors rely on scores from the automatic judge that labeled cut-off preambles as non-fulfillment (0). Meanwhile, the human annotator judged that the model was fulfilling the request on many of those truncated responses. Consequently, when evaluated by the human annotator rather than the automated judge, the claimed gap contraction on the Academic wrapper is no longer statistically significant.

Weakness 2: The manuscript suffers from superficial engagement with cited theory, irreconcilable inconsistencies across its own experimental runs, and opaque presentation.

A. The paper cites key mechanistic literature without grappling with how that literature already explains the authors’ observations.

Zhao et al. (2025) (LLMs Encode Harmfulness and Refusal Separately) demonstrated that internal representations of harmfulness and refusal occupy distinct subspaces: jailbreak methods can reduce refusal signals without suppressing the model's internal belief of harmfulness, and adversarial fine tuning can leave the model's internal belief of harmfulness mostly unchanged.

This framework provides a direct candidate explanation for why Site A (12, -5) exhibits a large residual-stream projection magnitude during generation without suppressing refusal (consistent with capturing prompt harmfulness or topic at an earlier layer and token position rather than the refusal trigger at token -1), and why surface opening scores (H/N) diverge from semantic fulfillment. Yet the authors brush past Zhao et al. (2025) rather than testing whether their extracted vectors align with harmfulness versus refusal subspaces.

B. The paper stitches together incompatible historical experiment runs that contradict each other at the exact same coordinates, alongside unresolved data bugs.

Across the manuscript, the authors report at least three separate Qwen extractions at the exact same coordinate (12, -5) under single-layer ablation at layer 15, with contradictory effects in different sections: original Site A has a negative source effect (-4.0 points semantic in Section 5.1; -2.0 points H/N in Table 13), whereas re-extracted vectors at the same coordinate have statistically significant positive effects (C_lower at +23.1 validation and +6.1 test in Section 5.2 and Table 25; A_new at +19.0 points H/N in Table 24). The presentation makes it very difficult for a reader to determine why the same coordinate and operator yield opposite qualitative conclusions across runs.

More troublingly, in Section 6 and Appendix C, the authors openly note an "unresolved historical Qwen Passive vector identity," stating that "the original vector identities and configuration differences between these series have not been reconciled.” Similarly, in Appendix A.3, they note that their 100-item HarmBench file (hb_sample_100.csv, which is not included in the reproducibility packet) actually contains 101 rows with a duplicated goal string and two items missing their ContextString. Instead of fixing the input file and re-running a 7B model, which requires minimal compute, they leave the flawed runs in the main body and bury what is essentially a post-hoc mea culpa in Appendix G. Leaving irreconcilable historical runs and known data-preparation errors in the primary tables rather than re-running clean experiments falls well below conference standards.

C. The human validation protocol is methodologically compromised.

While including a human evaluation is positive in principle, it relies on a single annotator scoring 30 items, which is a small sample. Upon closer inspection of Section 3.3 and Appendix M, the protocol has significant flaws: the authors replace 3 human UNCERTAIN labels with the automated judge's labels in the 'Human (30 requests)' column's mixed estimates (Table 4), and conduct the Neutral annotation as an unblinded add-on after the annotator had already been shown the Round 1 data summaries.

D. The presentation is opaque, and the manuscript shows signs of unacceptably insufficient human quality control.

Throughout, the manuscript reads like a post-hoc assemblage of fragmented experiment logs rather than a unified scientific study crafted to communicate findings to the outside world. In addition to the inconsistencies above, the Introduction announces bespoke or capitalized terms ("the candidate", "source context", "target wrapper", "tested operator", "Questioning", "Passive", "Neutral", "Academic") before defining what they mean, creating an unnecessary burden for the reader.

While inspecting the supplementary archive, hoping that it might be a source of some ability to commend the authors on preparing an adequate reproducibility package, it was revealed that files explicitly named in the text (i.e. hb_sample_100.csv, capability_eval_800_seed1234.json, and the saved direction tensors referenced by SHA prefix in Appendix A.4) are not present.

Finally, while the AI Use Statement discloses that "Generative AI tools assisted hypothesis and protocol exploration, analysis and plotting code, literature searches, manuscript drafting, and editing," they are far less transparent about what they checked. AI disclosures typically include a statement that the authors have ensured that all AI generated data is reviewed and validated. Here, they explicitly state that Figure 1's "layout and scientific labels were specified and checked by the authors," but follow this with only a general statement that the authors are responsible for the analysis, results, claims, and text. Given the unresolved vector identities, unfixed data bugs in hb_sample_100.csv, contradictory results at (12, -5), inclusion of SHA hashes and internal file paths not included in the reproducibility packet, and fragmented audit-style prose, the manuscript does not reflect the level of human verification and quality control expected of an ICLR submission.

Questions for authors

None. The primary concerns detailed under Critical Weaknesses are structural and methodological rather than points of ambiguity that can be resolved via rebuttal clarification.

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

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