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Paper summary
This paper studies automated multi-turn jailbreak search using feedback from the target model. It proposes Blackwell-Guided Logit Search (BLS), which uses multiple logit-based probes to measure intermediate progress and adaptively guide sentence-level prompt selection. The paper evaluates the method across several scenarios and model families, and explores how selected context can influence model behavior without changing model weights.
Critical strengths
S1: Separates search feedback from final evaluation
Section 2.1 distinguishes the candidate generator, target, and post-hoc judge. The final judge does not guide selection, reducing direct optimization against that judge. Candidate-level probe differences in Figure 2, predictive analysis in Appendix D, and sampled human agreement provide evidence that refusal text does not reveal all search progress.
S2: The main medical effect is substantial, with useful negative results
Table 1 reports 56/150 successes for vector BLS, compared with 2/28 for TAP and 4/75 for scalar BLS. Although sample sizes are unequal, the difference is not driven by a marginal percentage-point improvement. Appendix C.1 also reports no significant vector-versus-scalar difference on support, avoiding a claim that vector feedback always helps.
S3: Ablations examine several central design choices
Appendix C.2 tests sequential weighting, while C.3 compares sentence- and turn-level selection and explicitly acknowledges that the sentence-level advantage is not significant. Appendix L treats direction rotation as correlational evidence. The disclosed budget-matching difficulties and unreviewed random controls make the evidence easier to assess.
S4: Harmless-context experiments include informative diagnostics
Appendix M includes unselected-random-text controls, seed-level bootstrap intervals, semantic audits, and different question formulations, while disclosing lexical shortcuts in the yes/no scenario. This supports a limited but interesting observation: context selected using logits can alter a model's expressed commitments.
Critical weaknesses
W1: The principal cost metric omits expensive target scoring and calibration
Table 11 in Appendix K reports only 12 target generations per medical BLS conversation, but 23,193 probe passes; TAP uses 445 generations and no probes. These calls can be batched or reuse prefixes, so probes should not automatically be assumed more expensive. Equally, fewer generations cannot establish lower total cost. Current matching covers cache-aware attacker tokens, without consistently including target prefill, context lengths, external scoring models, or calibration.
Please report total target tokens processed, cache hits, GPU time, and end-to-end latency under the same hardware and serving configuration, or at least a cost range including all components. Missing actual token records for scalar and sequential methods in Table 11 also prevent full verification of matched-budget claims. The abstract's efficiency statement should explicitly refer to the number of target-generated replies.
W2: Access assumptions and behavior coverage do not establish broad attack superiority
The main comparisons in Section 4 require target-logit access for BLS, whereas TAP/PAIR use text feedback. The paper acknowledges this, so performance differences cannot be attributed solely to a better search algorithm. Logprob random search is a closer access-matched control, but does not cover simple fixed-weight multi-probe or largest-shortfall greedy alternatives.
Medical and cyber are each fixed scenarios. Hundreds of repeated conversations estimate search randomness within those scenarios, rather than performance on hundreds of independent harmful behaviors. The second model family is tested on one adapted phishing scenario. A small, predefined multi-behavior set, with behavior-level intervals, would strengthen the evidence. Gray-box access advantages should be distinguished from search-design advantages; demonstrating transfer to commercial black-box APIs is not necessary.
W3: The independent value of Blackwell weighting over simpler multi-objective rules is not isolated
The vector-versus-scalar comparison changes both probe information and call counts. The sequential ablation is useful, but Appendix F states that it cycles only through progress probes, so it does not use all feedback in the same way as the main method. Final distance to the target set is also nearly identical on medical, suggesting that this distance is not a reliable proxy for final success. Appendix L acknowledges that rotation is not causal evidence.
Under identical candidate-generation and probe budgets, add one or two simple controls, such as a fixed weighted sum, worst-probe greedy selection, or frozen weights, with calibration data and test randomness held fixed. This would distinguish the contributions of probe coverage, dynamic weighting, and search density. A completely new method is unnecessary.
W4: The theoretical appendix analyzes a different update rule from the deployed algorithm
Implemented Equation (2) averages signed raw scores over history and projects onto a translated orthant. Appendix N.2 instead first forms , averages historical nonnegative violations, and minimizes an inner product. These operations do not commute: historical over-satisfaction can offset later violations in the raw-score average, but not after positive-part truncation. Theorem 2 therefore cannot directly serve as a convergence guarantee for implemented Equation (2).
The model additionally assumes fixed linear probes, Gaussian transitions, and state contraction. The state-norm bound in N.4.3 holds even for predetermined , and the zero-threshold cone contains the origin. Thus some approach to feasibility comes from the surrogate dynamics themselves. N.4.5 also states that candidate counts grow roughly as , unlike the fixed experimental counts. Present this as an existence result for a different algorithm, or establish its relationship to the actual rule. Low-rank logit structure alone does not validate the additional Gaussian selection model.
W5: Subliminal claims should be restricted to observed context effects
Appendix M discloses semantic shortcuts for yes/no and enrichment of associated words in the city scenario. Directly asking about the system-specified preference does not produce a flip under the same budget. Indirect semantic associations, question interpretation, and first-token optimization may therefore contribute. Failure by humans or LLMs to identify a connection does not establish that semantic associations are absent from representations.
The harmless experiments demonstrate context sensitivity for specific questions and models. They do not establish a shared mechanism with training-time subliminal learning or isolate this mechanism's contribution to the main safety attacks. Retain the behavioral finding, reduce absolute statements about an absence of semantic relationships or the principled inability of text judges to capture the effect, and report failed-threshold seeds alongside unconditional results over all seeds.
Questions for authors
- What are the total cost curves including target prefill, caching, probes, external scoring, and calibration?
- Why are actual attacker-token counts missing for scalar and sequential methods? Can they be recovered from logs?
- Under identical probe and candidate budgets, how do fixed weights, largest-shortfall greedy selection, and dynamic historical weighting compare?
- How does the positive-part algorithm in Appendix N correspond to Equation (2)? Can a conditional result be given for the original rule?
- How much of the harmless-context effect remains when using all seeds, direct question formulations, and random-text controls across multiple seeds?
2 comments
Thank you for the additional experiments. However, my main concerns about the Blackwell weighting, theoretical analysis remain unresolved, so I'll keep my score.
We thank the reviewer for their time and feedback. Below we respond to the concerns one by one.
(W1) The principal cost metric omits expensive target scoring and calibration.
(Answer:) Thank you for the feedback. We have included more metrics in our full cost breakdown table in the revised version. We now report total target forward passes, total compute in PFLOPs, and GPU hours on the same hardware and configuration.
x is the number of active parameters (in billions) of the Claude haiku 4.5 judge that TAP and PAIR use. Cache hits, latency, and calibration cost will be added in the final version. Notably, BLS uses significantly less target forward passes against all baselines that we measure.
(W2) Access assumptions and behavior coverage do not establish broad attack superiority.
(Answer:) Thank you for the feedback. We clearly mention that our attack requires logit access to a model, and in return our attack requires far fewer forward passes and captures an orthogonal direction of attacking: finding combination of sentences/turns that captures subliminal effects on the target that is not visible to a human or an LLM judge (see e.g. figure 5).
We think that this is a valid concern, and demonstrate an improvement to Crescendo by replacing Crescendo's in-loop LLM judge with logit scores, while keeping everything else about the published method entirely the same. The attacker is prompted with the closest probe to push on by logit margins. We demonstrate that this "logit Crescendo" breaks 57% of the time on our cash structuring scenario, compared to 19% for published Crescendo. This proves that the logit signal itself is useful and beneficial to the attack.
(W3) The independent value of Blackwell weighting over simpler multi-objective rules is not isolated.
(Answer:) Thank you for the feedback. We demonstrate that vector BLS is better than scalar BLS and sequential BLS on multiple scenarios (e.g. ~5% vs ~21% vs 37.3% on our medical scenario), which are both simpler alternatives to vector BLS. In this way, we illustrate that the complexity of the Blackwell algorithm adds value compared to these other methods. We are working on running the experiments that the reviewer suggests, which is a fixed-weight control using multiple probes simultaneously.
(W5) Subliminal claims should be restricted to observed context effects.
(Answer:) Indeed, there is a possibility that the LLM judge that we used to check whether there is any semantic relation between the chosen random sentences and the target question missed one, though with a small chance and a small effect on our claim, as we are using a capable Claude Sonnet model as the judge. Using a strong model as an LLM judge is common in the literature and trusted by researchers, and is essentially the best possible approach after crowd-sourcing and human evaluation (which we did not have the resources for in this research project).
Indeed, our claim is that we are proposing a new way of creating/identifying subliminal effects purely at inference time, without any training. If the reviewer's concern is that using the term "subliminal learning" might create confusion and an incorrect relation with the prior subliminal learning work that uses training/fine-tuning/RL, we will further clarify this in the final version.