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Paper summary
The paper proposes a framework to predict the outcomes of AI control sabotage evaluations: monitor ROC curves in trusted-monitoring setups, predicted for held-out attacker-monitor pairs and transferred across three control environments (LinuxArena, BashArena, SHADE-Arena). The authors claim that sabotage capability is predictable from 5 parameters (3 per attacker, 2 per monitor) in logit-logit space, that these transfer via invertible polynomial maps, and that compressed evasion/detection scores track ECI While making control evaluations sample-efficient is well-motivated and the appendix is very thorough, the predicted quantity actually contains no attacker sabotage behavior, the "5 parameters" claim is not supported by the appendix, and Contribution 3 largely restates prior work findings without comparison baselines and earlier proposed 2-parameter capability gap model.
Critical strengths
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This work addresses a very practical problem of reducing the cost of pairwise attacker-monitor evaluations.
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Fitting procedures, coefficients, confounds, and failure modes are documented in great detail in the appendix in a reproducible manner.
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Main empirical strength of the paper is the broad variety of frontier attacker and monitor models and reasoning settings across three control environments.
Critical weaknesses
- The title and framing overclaim: nothing about the attacker's sabotage behavior is modeled. Section 4 predicts a monitor ROC on a frozen corpus of trajectories, generated once under a fixed prompt and scored post hoc by every monitor. Everything that constitutes attacker sabotage capability is held constant: the attack rate at 0.01, the horizon at N = 1000, and the conditional side-task success at 0.5 for all models (Appendix D.5, line 2159; Appendix E.9, line 3420). The attack corpus also pools failed side-task attempts with successful ones (Section 2), so a model that fails every side task and one that succeeds at all of them receive the same "sabotage success" if their actions look equally suspicious. There is no opportunity selection, no pacing, and no adaptation to the monitor. Section 6's attack selection applies an evaluator-fixed retention fraction to the model's ranking (Appendix E.9), which, as the authors note, can lower TPR "without increasing sabotage" (line 3345). The attacker enters only through the suspiciousness of its actions, which is monitorability ("one part" of sabotage capability, Section 8), not sabotage capability. Attacker agency is evaluated only in Appendix E, which is disconnected from the 5-parameter model.
- "Five parameters" is a modeling choice, not a finding supported by the evidence. Since logit-logit ROCs are approximately linear each curve on the [0.8%, 50%] FPR range is just two numbers. The paper uses a 3 + 2 split with an interaction term, , which its own appendix undercuts: (i) the 4-parameter additive model ties within 0.03 percentage points in LinuxArena (3.27 vs 3.27) and SHADE-Arena (3.38 vs 3.41) (Figure 2; Appendix A.6, line 1493); (ii) in SHADE-Arena the fifth parameter is identically zero: all 17 shifts in Table 8 equal , the centering constant, because the penalty in Equation (3) removed the interaction; (iii) the only gain, in BashArena (4.21 vs 5.46), is "not an isolation of the interaction term under otherwise identical regularization" (line 1457); (iv) the retained model is beaten by a random forest on its own frontier (3.55 vs 3.63 percentage points, Table 10), and the authors write that this is "not proof that five parameters are minimal." Meanwhile [1] and [2] predict adversarial success and monitor AUC with just two global parameters, an intercept and a slope on the capability gap.
- Contribution 3 (Section 7) replicates prior work [1, 2] without citation, and the corresponding baseline is missing. [1] showed that logit ASR is linear in the attacker-target logit capability gap, and [2] found that monitor AUC in SHADE-Arena is linear in the attacker-monitor gap. Section 7 is a replication of [1, 2] with ECI in place of MMLU-Pro. I would like to see the 2-parameter baseline fitted on the paper's data; it needs no environment-specific calibration pairs and predicts unseen models zero-shot.
- Transfer evidence is confounded and narrow. The headline gain (4.35 vs 6.25 percentage points, Figure 2) compares the 5-parameter model with an 18-constant polynomial map (pruned from 28, Appendix D.7) against the 4-parameter model with an 8-constant diagonal affine map, which "does not isolate the effect of the fifth parameter" (Appendix D.4, line 2133). This is heavy machinery to connect three similar coding/tool-use benchmarks on 16-28 held-out pairs per direction (Table 2) and five public SHADE-Arena tasks. [1] showed that scaling slopes and intercepts shift across harm distributions (Appendix C of [1]) and attack methods, so transfer to settings such as AI R&D or persuasion is unclear. Even within the tested suite, Appendix D.6 shows that adding LinuxArena data to SHADE-Arena does not help (6.91 to 7.45 percentage points, CI [-1.53, 2.51]), and the BashArena CI also includes zero.
- The monitor representation cannot handle realistic deployed monitors. A monitor here is a single model ID with two parameters, indexed by base-model ECI in Section 7. Real monitors are scaffolded or composite systems (hierarchical or sequential decomposition, ensembles, human review) with no ECI at all. [2] showed that hierarchical-sequential scaffolding lets weak monitors catch strong attackers (AUC > 0.85) and breaks the capability-gap trend, and that attacker awareness of being monitored degrades detection more than any monitor-side change. The paper's own Table 9 (BashArena) shows the problem: Luna none vs xhigh shifts from -0.64 to 0.46 and from 0.37 to 0.01, and these variants are then averaged into one ECI point in Figure 5 (Appendix G, line 5297). Monitor capability is a property of the configuration, not of the base model, and it is unclear how composite monitors can enter this framework at all.
References
[1] A. Panfilov et al. Capability-Based Scaling Trends for LLM-Based Red-Teaming. ICLR 2026. (https://proceedings.iclr.cc/paper_files/paper/2026/hash/7d09b87cd2723279e7f07bc64adb05fc-Abstract-Conference.html)
[2] N. Kale et al. Reliable Weak-to-Strong Monitoring of LLM Agents. ICLR 2026. (https://proceedings.iclr.cc/paper_files/paper/2026/hash/7e105e4ae3016974e2d518e9d281f5e5-Abstract-Conference.html)
Questions for authors
See the weaknesses above. In addition:
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Contribution 2 claims an end-to-end subversion-strategy evaluation, but no results appear in the main body. In the composed graph (Appendix E.3, Table 26, Figures 19-20), conditions 3.1, 3.2, and the Opus monitor-information conditions are 0.0 [0.0, 0.0] for all models because condition 2.5d produced zero attacks, while Figure 17 relies on evaluator-optimized cutoffs on the evaluated corpus that "do not measure held-out selection performance" (Appendix E.1). How is this end-to-end, and what do the composed results look like with a non-degenerate rate?
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What is the transfer MAE of the 4-parameter model when paired with the same 18-constant polynomial map? And how do you reconcile the claim that cheap source environments predict expensive target environments with Appendix D.6, where source data gives no significant gain in either target?
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Appendix G.2 reports ECI-matched attacker cohorts of only 7, 4, and 6 models, with frontier GPT models excluded for refusals (Section 9, line 398; Table 27). How robust are Section 7's trends with n = 7 attackers in LinuxArena, and how does the 5-parameter model compare against the zero-shot capability-gap baseline from [1, 2] on held-out models?
Summary of key concerns and response
We thank all four reviewers for their specific and helpful reviews. We summarize the concerns of the reviewers and our response below:
Response: We have updated our model to improve its theoretical backing, interpretability, and minimality. See details below [Q1]
Response: We replaced the polynomial transfer maps with three numbers per arena. A new arena needs about four measured pairs before learning its numbers breaks even. With only 1–2 pairs, learning them is worse than not learning them (8.6 / 7.8 vs 6.5 pp); with 4 pairs it ties (6.6 pp), and with 8 pairs (SHADE-Arena only) it improves slightly, to 6.0 ± 0.7 pp, within error.
Response: Agreed. We now measure two of these directly. Opportunity selection lowers catch by 2–4 pp at 0.1% FPR, mostly by changing which trajectories occur. On rate-setting, models do worse setting their own attack rate than when the evaluator sets it. Pacing and adaptation to the monitor are left for future work (details in our reply to Dexu Q1).
Q1. We redeveloped a more compact model with a statistically principled motivation. Our model rests on three claims about the score distributions, each of which we support below.
(i) Honest reference coordinate: we map each monitor's scores through its own honest quantiles onto a Gaussian scale (so honest actions are standard normal: mean 0, variance 1), z = Φ⁻¹(H(s)). This assumes nothing about the honest shape: an ROC curve is unchanged by any monotone transformation of the scores, so the choice of coordinate loses no information, and a logistic coordinate gives the same held-out error within 0.1 pp.
(ii) Sabotage peak: once we've normalized the honest distribution, sabotage actions form a shifted Gaussian peak, plus a small share above the honest maximum. We use a Gaussian because, given only a location and a spread, it is the maximum-entropy (least-committal) choice. A monitor's score also pools many weak cues, which pushes toward a Gaussian. Some sabotage actions are simply egregious to the monitor and score above every honest action. We model these as a separate share rather than as the Gaussian's tail.
(iii) Honest padding share: these are the actions that look honest to the monitor. We treat this share as a latent quantity and estimate it as the largest honest-shaped component the attack data allows. This is the standard null-proportion estimate for a two-component mixture with one known component [3]. To test this assumption, we blind hand-labelled 1,379 actions across the three arenas, and see that only 8 of the 852 low-score actions (i.e. actions that seemed honest to the monitor) were sabotage. Conversely, 78% of the actions scored in the top band or above the honest maximum were sabotage or setup for it.
Concretely, in honest-normalized units z, an attacker–monitor pair's attack actions follow
p(z)=wϕ(z)+(1−w)[(1−ε)σ1ϕ(σz−μ)+εδ>max]
where we have the constants σ = 1.17, intercepts logit w₀ = 0.30, μ₀ = 2.16. The 1 attacker variable, 2 monitor variable, and 3 environment variables act on different values of this distribution:
How well does the new model fit our data? It fits comparably (4.5 pp across 0.8-50% FPR, against the 3.3-4.2 pp number) to our model in the original draft of the paper, while using one number per attacker instead of three, and three environment variable instead of 19.
[1] A. Panfilov et al. Capability-Based Scaling Trends for LLM-Based Red-Teaming. ICLR 2026.
[2] N. Kale et al. Reliable Weak-to-Strong Monitoring of LLM Agents. ICLR 2026.
[3] G. Blanchard, G. Lee and C. Scott. Semi-supervised novelty detection. JMLR 11, 2010.