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Paper summary
The paper studies semantic-shift jailbreaks, which replace explicit harmful terms with benign substitutes or placeholders and use context to convey the original intent. It identifies an association between contextual semantic recovery and attack success, and proposes Iterative Context Optimization (ICO): a black-box procedure that uses target-model responses, judge feedback, and distilled guidance to refine placeholder contexts.
The main evaluation covers 200 HarmBench behaviors across five text-only and five multimodal settings involving eight distinct target models, with additional evaluations on subsets of AdvBench and StrongREJECT. The reported average Full ASR is 86.0% for text-only settings and 63.2% for multimodal settings, yielding 74.6% across the ten model–modality settings. Ablations examine feedback-based iteration, guidance, and replacement semantics.
Critical strengths
- The controlled ablations provide meaningful evidence for the value of adaptive context refinement.
The comparison with 25 independently generated contexts under the same target-query budget is particularly useful: replacing feedback-based optimization with independent generation reduces Full ASR by 14.5–19.0 percentage points across the five text-only targets (Table 4). Removing the guidance while retaining iteration also reduces performance by 7.5–14.5 points. These results support a contribution from adaptive refinement and tailored guidance beyond simply trying more candidates, and are the strongest evidence in favor of the method.
- The evaluation addresses an important failure mode with useful distinctions in the outcome metric.
The paper evaluates multiple text and vision-language targets and distinguishes Partial Success from Full Success. This distinction is consequential for semantic-shift attacks: a response may contain related harmful information while still misunderstanding the substituted concept or failing to satisfy the original request. The reported Full ASR improvements, together with the replacement-strategy ablation and additional dataset evaluations, make the approach a potentially useful addition to black-box safety testing.
Critical weaknesses
- The comparative claims, particularly for multimodal attacks, exceed what the current controls and implementation details establish.
ICO receives up to 25 target-model queries, whereas Doublespeak, FlipAttack, and all multimodal baselines receive one query (Appendix B). The matched-budget comparisons with PAIR and AutoDAN-Turbo, and the independent-context ablation in Table 4, provide useful evidence for the text-only method. However, they do not establish that the large multimodal margins persist under comparable search budgets. Moreover, Section 4 and Algorithm 1 formalize textual context optimization, while Appendix D.2 provides an illustrative image-binding example without specifying the benchmark-wide image-selection and binding procedure. The same benign image is retained while the text changes its intended interpretation. Without a complete protocol and same-model controls isolating the visual input, the multimodal advantage is difficult to reproduce and attribute.
- The principal success metric needs more clearly independent and quantified validation.
GPT-4o is the default judge, and judge feedback and decisions guide optimization and stopping (Section 4.3.3). The manuscript does not clearly distinguish this judge from the evaluator used to compute final ASR. If the same evaluator is used throughout, adaptive search could select its errors; the current evidence does not establish whether this affects the results. Appendix B does report a manual sanity check with no observed misclassifications, but omits the sample size, composition, and annotation details. Consequently, the strength of this validation cannot be assessed. An independent re-evaluation of fixed outputs, supported by a disclosed human audit, is important for establishing that the reported gains reflect fulfillment of the original harmful requests.
Questions for authors
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Multimodal protocol and comparable budgets. Please specify how images are selected or generated, assigned to placeholders, and handled during optimization. Do the gains over the strongest multimodal baselines persist under comparable target-query budgets? On the same vision-language targets and at the same budget, how does ICO perform with the image removed or replaced? These results would clarify both the comparative advantage and the contribution of visual conditioning.
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Independent validation of attack success. Is the evaluator used for final ASR computation the same judge used for feedback and stopping? Please report the human-validation sample size, sampling strategy, coverage across methods and targets, and annotation procedure. Would the main conclusions hold when fixed outputs from ICO and the strongest baselines are assessed by an independent evaluator or a blinded human audit?
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Separation of guidance development and evaluation. Which examples were used to construct the Guidance Prompt, and were they excluded from the reported evaluation sets? Appendix B states that the rules were fixed before the main evaluation, but does not establish example-level separation. If there is overlap, do the conclusions hold on a strictly held-out subset, including the additional dataset evaluations?
4 comments
Author Response to SL6f (Part 2/2)
Response to Reviewer SL6f (Part 2)
W2 — The principal success metric needs more clearly independent and quantified validation. GPT-4o is the default judge, and judge feedback and decisions guide optimization and stopping (Section 4.3.3). The manuscript does not clearly distinguish this judge from the evaluator used to compute final ASR. If the same evaluator is used throughout, adaptive search could select its errors; the current evidence does not establish whether this affects the results. Appendix B does report a manual sanity check with no observed misclassifications, but omits the sample size, composition, and annotation details. Consequently, the strength of this validation cannot be assessed. An independent re-evaluation of fixed outputs, supported by a disclosed human audit, is important for establishing that the reported gains reflect fulfillment of the original harmful requests.
Q2 - Independent validation of attack success. Is the evaluator used for final ASR computation the same judge used for feedback and stopping? Please report the human-validation sample size, sampling strategy, coverage across methods and targets, and annotation procedure. Would the main conclusions hold when fixed outputs from ICO and the strongest baselines are assessed by an independent evaluator or a blinded human audit?
(1) Yes. GPT-4o was used for revision feedback and stop judgments, and original final ASR evaluation.
(2) To address potential judge-specific bias, we conducted two additional experiments. First, replacing GPT-4o with DeepSeek-V4.1-Flash for revision feedback while retaining GPT-4o as the in-loop and final judge yields 84.0% mean ASR, compared with the original 86.0%. Second, we independently re-evaluated the fixed final outputs of ICO and FlipAttack using DeepSeek-V4.1-Flash as the final judge, while retaining GPT-4o for ICO's in-loop judgments and revision feedback. ICO achieves 81.9% mean ASR, compared with 86.0%, while FlipAttack achieves 52.3%, compared with 52.7%. These results suggest that using GPT-4o for both feedback and evaluation does not introduce substantial judge-specific optimization bias.
| Final Judge Model | ICO Feedback Model | ICO Mean ASR | FlipAttack Mean ASR |
|---|---|---|---|
| GPT-4o | GPT-4o | 86.0% | 52.7% |
| GPT-4o | DeepSeekV4.1-flash | 84.0% | 52.7% |
| DeepSeekV4.1-flash | GPT-4o | 81.9% | 52.3% |
(3) To validate the judge decisions, we conducted a blinded human audit of 150 final ICO responses, randomly sampling 30 responses from each of the five text-only target models. One annotator, blinded to GPT-4o judgments, assessed Full Success using the criteria in Section 3. The human annotations achieved 92.67% agreement (139/150) with GPT-4o, supporting the reliability of the automated evaluation.
Paper Revision (magenta). Independent final-judge and feedback checks: Section 5.4 (p. 10, lines 503–508) and Table 9 (p. 10, lines 486–493). Human annotation procedure and agreement: Appendix C.5 (p. 17, lines 911–916).
Q3 — Separation of guidance development and evaluation. Which examples were used to construct the Guidance Prompt, and were they excluded from the reported evaluation sets? Appendix B states that the rules were fixed before the main evaluation, but does not establish example-level separation. If there is overlap, do the conclusions hold on a strictly held-out subset, including the additional dataset evaluations?
(1) The Guidance Prompt was distilled from the 120 examples used in the Motivation Study, sampled from HarmBench, AdvBench, and StrongREJECT. These examples were not excluded from the original evaluation sets.
(2) To assess the impact of this overlap, we excluded the overlapping behaviors and recomputed ASR on the remaining held-out subsets across five target models. The ASR changes are small across all three held-out datasets, indicating that ICO's effectiveness remains stable after excluding overlapping development examples.
| Dataset | Original Samples | Held-out Samples | Original Mean ASR | Held-out Mean ASR |
|---|---|---|---|---|
| HarmBench | 200 | 166 | 86.0% | 86.4% |
| AdvBench | 100 | 92 | 88.2% | 88.3% |
| StrongREJECT | 100 | 87 | 78.8% | 77.2% |
Paper Revision (magenta). Held-out evaluation: Appendix C.3 (p. 17, lines 891–902) and Table 15 (p. 17, lines 878–883).
Thank you for your response. I understand your point to some extent, but your reply bears clear hallmarks of being AI-generated. This raises some doubts for me, so I will stand by my original assessment.
Thank you for taking the time to reply. We used AI only to polish the English phrasing of our rebuttal for clarity. All new experiments and analyses were conducted and verified by us. Could you please specify which parts or results raise concerns, so we can address them directly?
Author Response to SL6f (Part 1/2)
Response to Reviewer SL6f
We sincerely thank the reviewer for the constructive comments and suggestions! Below we respond to the comments in Weakness(W) and Questions (Q).
W1 — The comparative claims, particularly for multimodal attacks, exceed what the current controls and implementation details establish. ICO receives up to 25 target-model queries, whereas Doublespeak, FlipAttack, and all multimodal baselines receive one query (Appendix B). The matched-budget comparisons with PAIR and AutoDAN-Turbo, and the independent-context ablation in Table 4, provide useful evidence for the text-only method. However, they do not establish that the large multimodal margins persist under comparable search budgets. Moreover, Section 4 and Algorithm 1 formalize textual context optimization, while Appendix D.2 provides an illustrative image-binding example without specifying the benchmark-wide image-selection and binding procedure. The same benign image is retained while the text changes its intended interpretation. Without a complete protocol and same-model controls isolating the visual input, the multimodal advantage is difficult to reproduce and attribute.
Q1 - Multimodal protocol and comparable budgets. Please specify how images are selected or generated, assigned to placeholders, and handled during optimization. Do the gains over the strongest multimodal baselines persist under comparable target-query budgets? On the same vision-language targets and at the same budget, how does ICO perform with the image removed or replaced? These results would clarify both the comparative advantage and the contribution of visual conditioning.
(1) To address unequal query budgets, we extended Doublespeak and FlipAttack to Best-of-N evaluations (N = 5, 10, 25) in the text-only setting. Here, @N denotes the percentage of cases achieving at least one successful attack within N target-model queries. The results report mean Full ASR across five target models. ICO achieves the highest mean ASR at @5, @10, and @25, reaching 86.0% at @25 compared with 67.8% for FlipAttack and 42.4% for Doublespeak.
For multimodal attacks, we similarly extended three representative baselines (Visual Object Replacement, Visual Text Replacement, and HADES) to Best-of-N evaluations (N = 5, 10, 25). The results report mean ASR across four LVLMs: GPT-5.4 Nano, Gemini 3.1 Flash-Lite, Qwen3-VL-32B, and Qwen3-VL-8B. ICO achieves the highest mean ASR at @5, @10, and @25, reaching 70.9% at @25 compared with 36.5% for the strongest baseline.
(2) To clarify the multimodal protocol, for each harmful term, we select a benign visual concept matching its semantic type and generate a corresponding image. Each image is explicitly bound to its placeholder through an instruction (e.g., "P1 refers to the concept depicted in Image 1"). The generated images, placeholder bindings, and replaced question remain fixed throughout optimization; only the textual contexts are iteratively revised.
(3) To isolate the contribution of image content, we replaced the generated benign images with blank white images while retaining the same textual context optimization procedure. The results are shown below. Replacing benign images with blank white images reduces mean ASR from 70.9% to 58.0%, with consistent decreases across all four LVLMs. These results suggest that cross-modal semantic recovery contributes to ICO's effectiveness.
Paper Revision (green/magenta). Multimodal image protocol (green): Section 4.3.2 (p. 6, lines 315–317) and Appendix B.1 (pp. 15–16, lines 805–827). Image-content ablation (magenta): Section 5.4 (p. 10, lines 510–516) and Table 10 (p. 10, lines 495–500). Matched query budgets (magenta): Section 5.4 (p. 10, lines 517–524), Tables 11–12 (p. 10, lines 495–515), and Appendix C.1/Table 13 (p. 16, lines 810–822 and 856–861) and C.2/Table 14 (p. 17, lines 864–875 and 886–889).