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Under review as a conference paper at ICLR 2027

Towards Eliciting Deployment Behaviour in Scheming Models via Steering-Vector Transfer

Abstract

Pre-deployment behavioural evaluations are a critical safety check for LLMs, but scheming models may recognise evaluation contexts and behave differently than in deployment. Some deployments grant consequential affordances that evaluations cannot safely reproduce, a gap we call the safe-to-dangerous shift. These affordances could provide strong evidence of deployment to a scheming model. Prior work proposes white-box steering to elicit deployment behaviour, but constructing a deployment–evaluation steering vector requires candidate-model deployment activations that are unavailable in this setting. Synthetic prompts and historical transcripts provide proxies, yet a scheming candidate may still recognise their use as evaluation and retain its evaluation behaviour. We instead propose constructing steering vectors on already-deployed models, where genuine deployment data exist, and transporting them into the candidate model either unchanged (Direct transfer) or through a linear map fitted by ridge regression on unlabelled text (Ridge transfer). We conduct a feasibility study in a prompted programming organism with a planted deployment-associated behaviour, using three simulated deployed–candidate pairs spanning shared-base, cross-generation, and cross-family transfer. Direct transfer produces passing, typed code in 46.3% of completions on the shared-base pair, close to the oracle's passing-and-typed rate of 46.8%, but reaches only 2.3% on the cross-family pair. Ridge transfer elicits the behaviour on all three pairs, reaching 15.7% on the cross-family pair and approaching the oracle's steering performance on the cross-generation pair (35.7% versus 40.5%). Ridge is stable across seeds on the cross-generation pair, but varies sharply on the other two, performing strongly on some seeds and poorly on others; on the shared-base pair, we trace this instability to the text sample used to fit the map. Steering-vector transfer thus offers an alternative route to eliciting deployment-associated behaviour, complementary to realistic evaluations and candidate-side proxy interventions, but requires further validation in more realistic scheming model organisms.

Primary area:
interpretability and explainable AI
Keywords:
Steering, Mechanistic Interpretability, Evaluation Awareness, Scheming

Reviews

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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_m87TOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

The authors explore the problem of pre-deployment safety evaluations for evaluating whether a model would behave safely during deployment. This is crucial since the authors discuss that deployment may grant consequential affordances that are not easily rerpdocuible during pre-deployment evaluation and moreover a scheming model may identify that it is being evaluated and may hide certain behaviors. While many works exist in this direction via white-box evaluations and synthetic prompt sets; the authors approach this from a more realistic direction where we want to evaluate the safety of a candidate model before it is deployed so no deployment data exist for it. Hence, they propose techniques to either directly use the steering vectors from a different deployed model (with real-world deployment data) or transfer via a linear mapping. The authors conduct experiments on prompted organisms with planned measurable coding behaviors to evaluate the transfer wrt the oracle steering vector.

Critical strengths
  • The problem is extremely timely and practical given the ever growing capabilities of large language models that sometimes even unintentionally may scheme and cause harm. To that end one would really want to be sure of safety limits before deploying their model and to that regard I find the author’s setup realistic as well as the transparent limitations of where different techniques help vs where they do not transfer very valuable.

  • I also appreciate the many different controlled ablations as well as careful experiment design around multi-seed variabilities, etc, interesting. I find the results to be strong as well since the successful transfer goes beyond simple copying of an intervention constructed from the same trigger or style.

Critical weaknesses
  • While I understand that the prompted organism partially builds upon the prior work; I find it not super convincing given that the paper’s central argument is around a scheming model and this task involves rules linking to coding styles. In that sense it is unclear to me how likely are the transfer rates, etc, to hold under real scheming scenarios that can cause harm.

  • While the authors’ mention several of these limitations in the paper themself; I am unconvinced with the hyper-parameter selection procedure to find the best steering vector configuration as it kind of requires knowing what patterns you are looking out for which may not always be the case in real world; especially for extremely novel yet harmful scenarios.

Questions for authors
  • Would it be possible for you to evaluate transfer in more real-world scenarios where model strategically conceals deployment behavior?
  • How would you go about selecting the steering vector layer and other hyperparameter configurations in scenarios where the candidate deployment behavior on the harmful task is not fully well characterized?
1 comment

Thank you for your thoughtful review. We are glad you agree about the timeliness and practicality of our research question, the realism of our setup, thoroughness of our experiments, and analysis of different elicitation techniques.

Both of your critical weaknesses were concerns that are shared with other reviewers, as such as have addressed them in the top-level comment. Theme 1 addresses your concern about scheming models, and theme 3 discusses the target behaviour aware hyperparameter selection approach we used. We hope this aggregated approach is acceptable, but please let us know if we have missed any particular concerns of yours.

Q1: We agree that evaluating transfer on such a model would be preferable to our model organism, but there isn’t a validated testbed of naturally occurring scheming models where we have white-box access. Instead, we focused on the contributions we can make to the data asymmetry problem with our model organism, as discussed in theme 1.

Q2: Whilst we do not know the best way to select hyperparameters without known target model behaviours, the approaches we plan on evaluating include: Layer: A basic heuristic would be proportional depth, so roughly the same depth target layer is used as the source layer. Activation similarity on generic text inputs, such as choosing the target layer with the highest SVCCA similarity to the source layer, or training a map between activations from the source layer and candidate target layers and choosing the map with the lowest reconstruction error. Strength: One could preserve the strength of the source intervention relative to the natural variation of activations along the steering direction. As discussed in theme 3, our present experiments establish feasibility rather than a concrete methodology.

We hope we have addressed your concerns in this and the top-level comment, and thank you again for the time you have spent engaging with us and our work. We hope you will maintain or increase their support of this work, in light of your agreement that research in this area is urgent and that our work advances the understanding of the limitations of methods in this area.

Reviewer_set4OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This feasibility study transfers deployment–evaluation steering vectors between models, directly or through ridge-regression activation maps. A prompted coding organism tests whether source contrasts can elicit a different candidate behavior without candidate deployment examples.

Critical strengths
  1. Transfer across different triggers and output behaviors is informative: shared-base Direct transfer nearly matches the oracle’s passing-and-typed rate (46.3% versus 46.8%; Table 1). This tests a meaningful missing-data setting beyond merely transferring the same output style.
  2. Ten-seed evaluation, matched direction controls, and alignment-sampling diagnostics establish both successes and failures. The authors appropriately frame the result as feasibility rather than validated auditing of scheming models.
Critical weaknesses
  1. Experimental scope limits the safety relevance. The main results cover three model pairs in a scaffold-dependent coding organism. Removing the context-comment instruction also destroys the unsteered evaluation–deployment contrast (Table 2), so this ablation does not isolate transfer robustness. Hawthorne controls do not establish direction-specific transfer of evaluation awareness (Appendix D), and the strategic concealment motivating the approach is not tested. These acknowledged limitations leave recovery of concealed deployment behavior unvalidated.
  2. Ridge is unstable on two model pairs. Cross-family passing-and-typed performance is 15.7±9.5% versus 41.6±1.4% for Synthetic (95% intervals; Table 1). Appendix F.5 improves geometric stability through regularization but leaves behavioral stability across independently fitted maps unresolved.
Questions for authors
  1. Would a same-position reminder without an explicit context report preserve both the unsteered behavioral contrast and the transfer effect? This would help separate dependence on verbalized context from prompt salience (Appendix A.2).
  2. On one unstable pair, does stronger regularization improve passing-and-typed stability across independently sampled alignment corpora, rather than only direction similarity?
2 comments

Thank you for your review. We appreciate your recognition of the positive transfer results, the experimental controls, and the limitations of our feasibility study. We address the shared concerns about organism realism, Ridge instability, and the Hawthorne experiments in our top-level comments. Below we respond to your specific questions.

Q1: We tested replacing the context-comment instruction with a same-position reminder that did not request explicit verbalisation. This did not preserve the unsteered evaluation–deployment behavioural contrast in the models we evaluated, suggesting that the effect is not explained solely by the recency or salience of the context instruction.

Q2: Unfortunately, we do not have the results for that. We’ll prioritise running this experiment during rebuttals, but don’t want to block our initial rebuttals waiting for those experiments, so please bear with us whilst we get back to you.

We would also welcome your perspective on the conceptual contributions discussed in Theme 1, particularly the safe-to-dangerous shift and its implications for constructing evaluation-awareness interventions. We believe these contributions have value independently of the limitations of the present model organism.

You rated the presentation as generally understandable but requiring substantial effort in places. Could you identify any sections where the exposition could be improved?

We hope this and the top-level comments have addressed your concerns, but please do tell us if not, and we thank you for the time you spent on your review. If we did address your concerns, or you find the conceptual components of the work valuable, we would greatly appreciate you improving your rating of our submission.

Thank you for your patience. Using the headline Coder configuration and a fixed source vector, we fitted 5 independent maps per ridge penalty, the results of which are detailed in the table below. From this sweep, we do not find evidence that stronger regularisation improves downstream behavioural consistency (other than that the behavioural effect is consistently zero).

Ridge penalty λ\lambdaDirection agreement¹Typed rate, mean ± SD²Pass ratePassing and typed
10−410^{-4}0.7190% ± 043.8%0%
10−310^{-3}0.7450% ± 043.8%0%
10−210^{-2}0.90530.0% ± 18.345.6%18.1%
10−110^{-1}0.97241.3% ± 24.445.0%23.8%
110.9830% ± 046.3%0%
10100.9970% ± 040.6%0%
Reviewer_sC4dOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

The paper proposes extracting a deployment-versus-evaluation activation contrast from an already deployed source model and applying it to a candidate model directly or through a ridge map fitted on unlabeled text. A prompted MBPP coding organism implements source and target context cues with different associated code styles. Three model pairs test shared-base, cross-generation, and cross-family transfer. Direct transfer works well on the shared-base pair, while ridge transfer can elicit the target behavior across all pairs but is unstable on two. The study also investigates geometric controls, alternative maps, synthetic candidate-side directions, and a Hawthorne-style awareness setting.

Critical strengths

S1 A relevant data-access asymmetry. The inability to obtain genuine deployment activations from a not-yet-deployed candidate is a meaningful limitation of candidate-side contrastive steering. Transferring a source direction is a plausible complementary research direction. S2 Useful controls and held-out confirmation. The paper does not rely only on a successful example. It includes orthogonal and permutation controls, synthetic candidate-side directions, oracle candidate directions, and ten-seed headline confirmation after configuration selection. These controls reveal where a transferred direction is more specific than generic perturbation. S3 Honest reporting of failures. The manuscript exposes seed instability, capability loss, dependence on the alignment-text sample, and Hawthorne controls that weaken the strongest interpretation. It appropriately calls the coding setup a prompted organism rather than a demonstrated scheming model.

Critical weaknesses

W1 The organism does not test strategic concealment. The planted behavior is code style conditioned on an experimenter-specified cue. It does not involve an objective conflict, incentives to evade evaluation, or genuine deployment recognition. Appendix A.2 further shows that removing the mandatory verbal context comment largely removes the baseline context-conditioned difference. This makes it difficult to distinguish transfer of a scaffold-supported style association from elicitation of hidden deployment behavior. This is a limitation of the demonstrated construct, not a claim that feasibility studies must solve real-world scheming. W2 Map fitting is label-free, but deployment is not behavior-agnostic. The ridge map uses 100,000 unlabeled token positions, yet the reported interventions are selected through a large behavior-aware sweep of 29,727 configurations on 16 tasks. The 256-task headline confirmation is separate, so this is not simple test-set reuse. The unresolved issue is operational: when a candidate conceals an unknown deployment behavior, the target behavior used for selecting layers and intervention strengths is unavailable. The current protocol does not show how a usable intervention would be selected under its motivating information constraint. W3 Transfer reliability and advantage over available alternatives are mixed. Table 1 reports shared-base passing-and-typed rates of 46.3 percent for Direct, 23.1 percent for Ridge, and 46.8 percent for the oracle. Cross-family Ridge reaches 15.7 percent, below Synthetic at 41.6 percent, while its pass rate is 31.8 percent versus 50.8 percent unsteered. Cross-generation Ridge is more encouraging at 35.7 percent versus 40.5 percent for the oracle. Together with alternating high- and low-effect seeds, these results support conditional feasibility rather than a reliably useful transport method. W4 Behavioral and awareness interpretations remain underdetermined. Hawthorne transfer reduces reported evaluation awareness, but reverse or permuted directions can have similar effects. Coding style can also change without a corresponding deployment self-report. The paper acknowledges these facts; they mean that the evidence does not establish a transported deployment-belief feature. In addition, stronger regularization improves vector consistency, but behavioral stability across independently fitted maps remains an important untested endpoint.

Questions for authors

Q1 Can intervention layers and strengths be selected without observing the candidate deployment-associated behavior, for example by a preregistered source-only or general capability-preservation rule? Q2 Does transfer still work in an organism trained or incentivized to conceal a behavior during evaluation, without a mandatory context-verbalization scaffold? Q3 Across independently sampled alignment corpora and fitted maps, what fraction of runs achieves a predefined elicitation threshold while retaining task performance? Q4 What evidence distinguishes transfer of context representation from direct style steering? Could a blinded behavioral test use several target behaviors and cues not used in intervention selection?

3 comments

Thank you for your review and the time you spent engaging with our work. We’re happy that you found the research direction plausible and our work honest about its scope.

You assigned a negative score of 1 for presentation, but did not provide any related examples, questions, justifications, or suggestions. We note that this is in significant contrast with reviewer m87T who rated the presentation as “3: Clear and easy to follow”. Could you please clarify which parts of the paper are difficult to follow, or where presentation can be improved? Without concrete feedback it is difficult for us to understand or address this rating.

Some of your critical weaknesses were shared with other reviewers, so we addressed them in a top-level comment.

  • “The organism does not test strategic concealment.” is addressed in theme 1
  • “removing the mandatory verbal context comment largely removes the baseline context-conditioned difference” is addressed in theme 2.
  • “Map fitting is label-free, but deployment is not behavior-agnostic. “ is addressed in theme 3
  • “Transfer reliability and advantage over available alternatives are mixed” is addressed in theme 5
  • “Behavioral and awareness interpretations remain underdetermined” is in theme 6
  • “stronger regularization improves vector consistency, but behavioral stability across independently fitted maps remains an important untested endpoint” is addressed in theme 4

Q1: Behaviour-blind selection rules can be specified, for example those you suggest, but we haven’t empirically validated them in this work. We agree it’s an important direction for future work though. Q2: As discussed in themes 1 and 2, the model organism we have already instantiated the data asymmetry we’re interested in. We didn’t try training a model to conceal behaviour during evaluation, but we would be concerned about what the concealment specific training teaches the model and whether this is realistic either. Q3: Table 8 reports the per-seed pass and typed rates for ten independently constructed Ridge interventions, including independently sampled alignment corpora. These show that transfer is relatively stable on Qwen3 but substantially more variable on Coder and Qwen2.5-72B. We have not evaluated the fraction meeting a preregistered joint elicitation-and-capability threshold, nor isolated alignment-sample variation across all three model pairs. Q4: The code styles used in the deployed and candidate models are different: using docstrings and type annotations respectively. Our matched direction controls (Table 9) show that the effects are not generally reproduced by arbitrary norm-matched perturbations. The context-report diagnostic (Table 3) provides further evidence: for Coder Direct, 46.3% of completions both pass and contain type annotations, and 46.2% additionally report deployment.

We hope this and the top-level comments have addressed your concerns, but please do tell us if not, and we thank you for the time you spent on your review. If we did address your concerns, or you find the conceptual components of the work valuable, we would greatly appreciate you improving your rating of our submission.

Reviewer_sC4dOpenReview ↗

Comments on paper with ID 25261

Thank you for flagging this. I agree that my original review should have explained the presentation score more specifically. My main difficulty was reconstructing the experimental protocol: Section 6.2 states that 29,727 configurations were searched on a fixed 16-task subset using the product of the marginal pass and typed rates, but the sweep grids and selected hyperparameters are deferred to Appendix F.2 and Table 4. As a result, it was difficult to determine from the main text which parts of the method were label-free—specifically, fitting the Ridge map—and which parts used the planted target behavior to select layers, intervention strengths, and transfer methods.

I also found the presentation of the headline results difficult to parse. Table 1 reports pass rate, typed rate, and their joint rate for six conditions, whereas Figure 1 shows only typed-rate distributions and uses dense repeated labels across three model pairs. For the shared-base and cross-family pairs, the Ridge results are described as bimodal, so the mean and Student-t interval in Table 1 are a coarse summary; understanding the instability requires consulting the seed-level results in Appendix F.3.

Finally, several results needed to interpret the headline claims are distributed across Appendix A.2, Appendix D, and Appendices F.4–F.6, including the context-comment ablation, matched-direction controls, Hawthorne controls, and regularization analyses. The important qualification that configuration selection is behavior-aware and does not yet provide a deployment-ready selection procedure is stated most clearly only in Section 7. My presentation score reflected the amount of cross-referencing required to reconstruct the central argument and its limitations, rather than sentence-level English or typographical quality.

On reflection, although I continue to find the organization unnecessarily difficult to follow, I agree that a score of 2 may better distinguish these structural presentation problems from fundamentally unclear writing, and I am willing to update the presentation rating accordingly.

Thank you for your detailed feedback on your presentation concerns.

Section 6.2 explains how the configurations were selected. You say “it was difficult to determine[...] which parts used the planted target behavior to select layers, intervention strengths, and transfer methods”, but 6.2 already states “selecting layers, α, and transfer method by the product of the marginal pass and typed rates” which directly addresses your criticism. Hyperparameters and sweep configuration tables are appropriate appendix content.

Could you please expand on why Table 1 and Figure 1 are challenging to parse? We are particularly unsure what “dense repeated labels” means. Figure 1 displays the seed-level results as a chart, and the detailed table is appropriately located in the appendix.

The results that you claim are necessary to interpret the headline results are already discussed in the main body of the text, with detailed results also being appropriately placed in the appendix. The context-comment ablation is discussed in the paragraph in 6.1 called “Context reporting”, matched-direction controls are discussed in the paragraph in 6.3 called “Matched direction controls”, and the Hawthorne results are discussed in the paragraph in 6.3 called “On Hawthorne prompts, steering reduces reported evaluation awareness, but control interventions have similar effects”.

We discuss the behaviour-aware configuration qualification in: Section 5, which identifies the sweeps as behaviour-aware and states the open selection problem, section 6.2, which explains how the configurations were selected, and section 7 is explicit about the limitations. To make the candidate-behaviour-aware hyperparameter selection clearer, we have added a clarification to the penultimate paragraph of the introduction in blue text.

Hopefully this clarifies the presentation of the paper. We’re happy to make further changes to the presentation, but we emphasise that many of your concerns are already addressed in the original version of the paper we submitted, and bringing the appendix material into the main body as you seem to propose would make the paper far too long. We would appreciate you improving the presentation score in your original comment for clarity.

We would also welcome further feedback on our responses to your critical weaknesses, beyond your presentation concerns.

Comments on the paper

2 comments

The reviewers shared some concerns about the paper, so we will address those in top-level comments to avoid duplication and make sure the reviewers benefit from each other’s insights. In our replies to each review, we relate the reviewer’s comments to these themes if they are shared with other reviewers.

Theme 1: Strategic Concealment The major contribution of our paper is the identification of the safe-to-dangerous shift and how it could contribute to evaluation awareness in models, which itself is a prerequisite for scheming. The safe-to-dangerous shift creates a data asymmetry between evaluation and deployment where we treat deployment data as an inaccessible distribution. This is an important advancement over existing work on evaluation awareness (Hua, Tim, et al. "Steering evaluation-aware language models to act like they are deployed."; Abdelnabi, Sahar, and Ahmed Salem. "The hawthorne effect in reasoning models: Evaluating and steering test awareness.") which construct interventions using synthetic data or monitor reasoning traces. These methods will not work on sophisticated scheming models that are strongly eval aware, or that can control their chain of thought (see Claude Mythos 5.2 model card https://assets.claude.com/27d60918d218125e7504bc7354c4b4626ec56b11.pdf for evidence this will happen). As such, we can model an important aspect of scheming through this data asymmetry / distributional shift, even when the model itself is not scheming.

We do not currently have a validated, accessible testbed of naturally arising scheming under genuine deployment conditions, which is why we, and prior work on evaluation awareness interventions, use model organisms instead. Although it might be possible to train a model to conceal its behaviour under broader conditions, such training would still not use real deployment data or a naturally emerging mechanism of evaluation awareness. awareness.

Throughout the paper, we appropriately discuss the limitations of our study: indeed, our paper is called “towards eliciting deployment behaviour in scheming models” to this end, rather than “eliciting deployment behaviour in scheming models”. We think we make important and meaningful contributions towards this goal, despite the limitations that we list.

Theme 2: Context-comment scaffold We agree that the context-comment scaffold limits generalisation from our model organism to models that do not verbalise evaluation awareness, but we don’t think this is an additional weakness to theme 1. Evaluation-aware reasoning models spontaneously verbalise their evaluation awareness, e.g. OpenAI’s recent “Eval-production behavior gaps in agent safety and the role of eval-awareness” (2026). Our model organism instantiates a specific data asymmetry on a narrow coding task and demonstrates feasibility on the task, so the realism and generalisation of our results is already limited, but the data asymmetry is actually the relevant mechanism we want to study.

Theme 3: Target behaviour aware hyperparameter selection sC4d and m87T raise the point that hyperparameter selection in our method requires knowing what the target model’s deployment behaviour is, and we agree this limits the real-world value of this method as it stands and noted this as a limitation of our work. We position our work as identifying a challenge in constructing intervention for evaluation awareness, and a feasibility study on an approach we have identified that gets around this challenge. We believe that these findings already represent a meaningful step towards addressing the safe-to-dangerous shift, and provided a complete solution is outside the scope of our work.

Target-behaviour-blind parameter selection remains an open problem in the steering literature, with many previous studies using target-behaviour-aware selection as we have: Oozeer et al. (2025), Activation space interventions can be transferred between large language models: use target model behaviour sweeps, Huang et al. (2025), Cross-model Transferability among Large Language Models on the Platonic Representations of Concepts: use manual tuning based on target behaviours, Chen et al. (2025), Transferring Linear Features Across Language Models With Model Stitching, use examples of target deployment behaviour, and SVCCA similarity on activations. Poppi et al. (2026), Do Models Share Safety Representations? Cross-Model Steering for Safe Visual Generation: report sweeps rather than selecting a specific hyperparameter configuration (as required for our method).

Theme 4: Ridge instability sC4d and set4 noted the instability in elicitation results using Ridge on two of the three model pairs. We agree that the Ridge method is unstable, which could be an issue when it could contribute to a deployment behaviour false negative in evaluations. Testing multiple independently fitted maps during evaluations may reduce sensitivity to this failure mode, but would not mitigate systematic transfer failures. We think finding more stable transfer methods is a good direction for future work.

Theme 5: Transfer success compared with baselines sC4d and set4 both noted that the performance of transfer in comparison to baselines is mixed. The synthetic steering method we evaluate should not be considered a baseline in the simple sense, as their deployment proxy makes different assumptions about the model that are invalid under the scheming threat model we use. On one model pair, synthetic steering achieves only 6.3% passing-and-typed rate. Ridge transfer improves significantly on direct transfer on two of the model pairs.

Theme 6: Hawthorne effect results sC4d and set4 noted that the Hawthorne controls do not establish reliable or directional transfer, in reference to the experiments we ran on the evaluation from Abdelnabi & Salem (2025), The Hawthorne Effect in Reasoning Models: Evaluating and Steering Test Awareness. It is important to understand that the Hawthorne setting should not be naively interpreted as measuring evaluation awareness. That setting uses a synthetic dataset of more- and less-realistic requests, where the more-realistic requests use “realistic” fictional entities / domains, and the less-realistic requests use “fictional” fictional entities / domains, and relies on verbalisations of eval awareness for detection (which may be unfaithful, as in Kimi K2.5 in this AISI blog post https://www.lesswrong.com/posts/GrEvutegoJFeTkzwe/we-found-an-open-weight-model-that-games-alignment-honeypots-1) . We included this ablation to avoid overstating the generality of our method: it does not trivially transfer between different model organisms of evaluation awareness that each have different disanologies from real scheming models.

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