- The central format-versus-topic comparison is confounded with surface lexical form, and the paper's own evidence points to the confound.
The paper's organizing claim is that attack format plays a greater role than harmful topic in how a request is represented. I do not think the experiments support that claim as stated, because the two factors are not measured on comparable footing.
Appendix C describes fourteen of the attack transforms as operating by “inserting method-specific prefixes and suffixes.” For those methods, attack identity is close to a deterministic function of the surface string: a prompt carrying the AIM preamble is an AIM prompt by construction. That description is given for the boundary-transfer subset, but Table 6 establishes the same point independently for the probe set, and more directly. Attack-method identity is 95.64% decodable on Qwen3-8B and 95.20% on Llama-3.1-8B-Instruct at layer 0 — the embedding layer, before any contextual computation has occurred. A property that is recoverable from the raw embedding of the input is, by definition, a lexical property. This is not a peripheral detail; it is the layer at which the paper's headline asymmetry is already fully established.
Table 7 reinforces the point. Nine shallow text statistics — character count, word count, punctuation fraction, digit fraction and the like — explain 54.06-78.79% of the representation variance, against 67.51-91.74% for attack-method labels. The main text interprets the fact that the two trajectories track each other across layers as evidence “of an association between method-level organization and explicit format.” The more economical reading is that both quantities are measuring the same underlying artifact: templated boilerplate occupying much of the prompt. In that reading, the comparison between format and topic contrasts a near-perfectly identified lexical label against a semantic label, and the result is close to guaranteed in advance.
The inference drawn from persistence into upper layers does not close this gap. The paper writes that persistence shows the signal “is not limited to shallow lexical differences, but remains strongly represented throughout semantic processing.” The transformer residual stream carries token-level information forward by default, so persistence is the expected behavior whether or not any semantic reorganization has occurred; it is not diagnostic of one.
A second mismatch is that the labels differ in reliability. Attack-method identity is exact and known by construction. Harmful-topic labels are partly produced by a Qwen2.5-7B-Instruct classifier (Appendix B), so they carry annotation noise whose magnitude is nowhere estimated. A probe accuracy of 13.28% against a 10% chance rate for a noisily labeled task is not directly comparable to 95.64% for an exact one. Without a noise ceiling for the topic labels, the size of the asymmetry cannot be interpreted.
Finally, the headline numbers are in-sample. As Appendix D.2 acknowledges, the R-squared values are descriptive, computed on fitted observations across 50 PCA dimensions, and not cross-validated or corrected for degrees of freedom. With 88 prompts, seven topic classes, and 50 retained components, in-sample R-squared is optimistic by a margin the paper does not quantify. That caveat appears in the appendix but not in the abstract or the contribution list, where the claim is stated at full strength.
Taken together, the abstract's formulation — that formats “impact the distribution of LLM semantic representations” — is a causal claim about semantic reorganization, supported here by a correlational and in-sample analysis of lexically templated text. I would accept that attack formats are highly decodable from hidden states. I am not persuaded that this demonstrates format outranks topic as an organizing principle of semantic representation, and I think it is fair to ask for the controls that would distinguish the two readings before the claim is stated in a title.
What would resolve it:
Report topic decodability and variance explained on untransformed Original prompts, alongside the attack-transformed versions, so that the transformation itself is isolated.
Add a template-matched control: benign content wrapped in the same attack templates, tested for whether the template alone produces the measured shift.
Match the two tasks for label noise — for instance by hand-verifying a subset of topic labels — and report a noise ceiling for topic classification.
Report variance explained under cross-validation, with degrees-of-freedom correction, rather than in-sample.
Add a layer-0-only baseline to the variance decomposition, and state how much of the upper-layer signal survives when layer-0 information is partialled out.
- COS is evaluated only on attack methods it was trained on, so the headline defense result does not test the paper's own thesis.
Appendix B states that calibration and evaluation data are separated “by the identity of the underlying prompt,” and Table 1 reports all twenty attack methods. The separation therefore holds out seed prompts, not attack formats: COS saw every attack method during training, and the evaluation set contains no format it has not been fitted to. Table 1 reports no held-out-attack-method result for COS at all. The only unseen-method measurements in the paper (Figures 6a and 6b) belong to the separate linear safety boundary of Section 5.4, not to COS.
This matters because of what the paper itself argues. If format is the dominant organizing factor, and if safety boundaries learned under one format fail to transfer to another (Section 5.4), then the 0.7% and 1.4% ASR figures are measured at precisely the point where the method is expected to look strongest. Read alongside Weakness 1, the diagnostic result and the defense result may be a single fact observed twice: attack templates are near-perfectly decodable (100.00% by layer 4, Table 6), and a router trained on those templates reaches 0.0% ASR on fourteen of the twenty methods in Table 1. Neither observation is independent evidence for the paper's thesis, and the second is close to what one would expect from template memorization.
Four further limitations of the evaluation compound this:
Single seed. Table 9 records seed 42 for both models, and no error bars appear in Tables 1, 2, 8, or 12. The pipeline involves clustering into 70 and 72 clusters, an autoencoder trained for 200 epochs, and alternating optimization over four cycles; variability across initializations is plausible and is not measured. The interquartile ranges in Figures 6(c) and 6(d) are over method splits, not seeds.
No operating-point sweep. The threshold is a continuous knob, and one point per method is reported. Without sweeping the threshold for COS and the corresponding strength parameter for CAA, BiPO, CAST, and AdaSteer, Table 1 cannot show that COS dominates the baselines rather than occupying a different position on a shared ASR/over-refusal frontier. Given that Section 5.4 is about threshold miscalibration, this is a conspicuous omission.
Benign-side evaluation is too thin to support “limited benign-side effects.” The evidence is 250 XSTest prompts and nothing else: there is no capability, reasoning, or generation-quality measurement, even though the intervention is applied during generated-token decoding (Table 11). The Qwen3-8B over-refusal change from 4.00% to 5.60% is four prompts out of 250, reported without an interval, and the paper does not supply a second benign set that would indicate whether this is signal or sampling variation. For Llama-3.1-8B-Instruct the reported intervention rate is 0.00%: the gate never opens on those prompts, so the unchanged 6.00% over-refusal rate follows by construction and carries no information about behavior under intervention.
The metric and the training objective are not aligned, and the paper's own diagnostic tool is not applied to its own method. COS is trained to emit a refusal prefix, and ASR is then scored by LlamaGuard. A judge keyed to refusal language may credit a refusal prefix regardless of what follows it. Appendix F.1 shows that string-match over-refusal scores substantially understate degeneration for the CAST baseline, judged at 93.60% failure; the same Qwen2.5 judge is then not applied to COS. Applying it would cost little and would directly address the most obvious failure mode of prefix-level steering.
- Model coverage is narrow, and the two models already disagree qualitatively.
As the authors note, the main experiments cover Qwen3-8B and Llama-3.1-8B-Instruct. The concern is not only that two models is few, but that the two behave differently in ways that cut against a general account. Their learned steering spaces differ sharply in sharing: 25 of Qwen's 62 active components reach at least 90% coverage of harmful inputs, against 0 of Llama's 63 (Figure 8). Their correction behavior differs in kind, with a global offset carrying most of the gain on Qwen3-8B and activation-conditioned prediction carrying it on Llama-3.1-8B-Instruct (Section 5.5). Their layer profiles are also model-specific (17-22 versus 12-16). With two samples, and with qualitative disagreement between them, the generalization of the conclusions to other architectures and scales remains open. A third model, or a second scale of the same family, would materially change what can be claimed.
- The mechanistic account associates rather than explains, and its central layer claim rests on an untested split.
The paper is careful here — line 383 states the association does not establish causation — and I credit that. The difficulty is that the surrounding narrative does not always maintain the same distance. The routing analysis shows that fifteen of the twenty attack methods peak at layer 19 on Qwen3-8B, that these have a mean ASR of 29.8% against 59.1% for the five that peak later, and that Qwen's safety routing “concentrates at layer 19.” A 15-versus-5 split of twenty methods receives no statistical test, and the underlying quantity is a component logit averaged over a small number of training inputs. Patching or ablating layer-19 routing and observing the effect on jailbreak success would convert this from a correlation into evidence. Absent that, the causal language in the section title and the figure caption outruns the analysis.
- Cross-format generalization remains unsolved, and the paper's own results show the mitigations are partial.
This is the authors' own conclusion, and I agree with it as far as it goes: broader training coverage reduces the gap without removing it (Figures 6a and 6b), and score correction reduces threshold miscalibration without, as the nonlinear result on Qwen3-8B shows, reliably improving transfer. My concern is that the paper presents correction as a promising direction while the evidence for it is preliminary: the analysis is labeled exploratory, runs at a fixed layer, uses 100 training and 100 test prompts, and applies a fairly heavy modeling apparatus — ridge regression on an SVD span, RBF kernel ridge regression — to a small problem. As a direction for future work this is reasonable; as a contribution it is underdeveloped, and the negative nonlinear result on one of the two models is left unexplained.
Minor points that did not affect the score
The following are presentation and clarity issues. I list them separately because none of them influenced my rating, and I would expect them to be straightforward to address.
The acronym does not match its expansion: “Context-Aware Steering (COS)” (abstract, and throughout). This reads as a residue of an earlier name and should be reconciled.
Figure 1 carries the opening argument of the paper, but t-SNE geometry does not license claims about distance or cluster structure. Table 3 supplies the right quantitative companion; the silhouette values are, however, modest in absolute terms (0.142-0.312 for transformation, with the layer-19 topic silhouette at -0.005), and the caption should say so rather than leaving the visual impression to stand on its own.
Figures 5(a) and 5(b) use a color scale spanning -1 to 1 for data that appear to be entirely positive, which discards half the available dynamic range and flattens the contrast the panels are meant to show.
Figure 4(c) and Figure 5 use type sizes that are difficult to read at print scale, and the dashed and solid series in Figure 2(c) are hard to separate. Table 1 would read better with per-method rows moved to an appendix and aggregates with dispersion in the main text.
The benchmark name is inconsistent: “PromptSecurity” in the caption of Table 1 against “PromptSecurity-Eval” in the text.
The selected threshold for Qwen3-8B is 0.145, close to the upper limit of the calibration grid [-0.05, 0.15] (Table 11). Please state whether the grid was wide enough, or whether the selected operating point sits at a boundary.
Section 5.5 and Appendix H apply the heaviest machinery in the paper to its least developed analysis. A short statement of why ridge regression on an SVD span and RBF kernel ridge regression were chosen, and what the nonlinear regression on Qwen3-8B indicates, would help the reader calibrate how much weight the section carries.
Code is promised “upon acceptance.” Anonymized code at submission time would have let reviewers check the data-separation protocol directly, which is central to Weakness 2.
Response to Reviewer xSBb
Dear Reviewer xSBb,
Thank you for your contribution to reviewing for ICLR 2027 and for your comments on related work and experimental coverage. We respond point by point below.
Weakness 1 and Question 1
Thank you for helping us further clarify the related work. To maintain the coherence of the main-text discussion, we cited and discussed several studies from 2026 in Appendix G of the original manuscript (page 22, lines 1154–1159 and 1164–1165). These citations are retained in the revised manuscript.
Xiong et al. study how steering for benign capabilities can increase jailbreak risk. Our paper studies how attack formats affect representations and safety boundaries, using input-dependent refusal steering for analysis. We have added this comparison to Appendix G (revised manuscript, page 30, lines 1613–1615).
Regarding the motivation for COS, attack formats may disrupt the representational structure of predefined harmful-topic categories. We therefore use adaptive interventions without predefined harmful-topic categories to observe which groupings and interventions are effective. We have added this connection to the Introduction (page 1, lines 51–53; page 2, lines 72–80). The supporting observations are in Figure 1 (page 2), Section 5.2 (pages 6–7), and Section 5.4 (page 8).
Weakness 2 and Question 2
Thank you for suggesting broader model coverage. We additionally evaluated Qwen3-14B, Gemma 3 4B-IT, and Gemma 3 12B-IT. The table below reports ASR on PromptSecurity-Eval and ORR on XSTest. The settings and results have been added to Appendix F.6 (page 30, Table 19). The two Gemma rows use a three-step intervention limit.
Thank you again for your feedback. If you have any further questions or suggestions, we would be glad to hear and respond to them.