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- Informativeness
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Paper summary
This paper shows that prompt choices can reverse conclusions about how evaluation awareness scales with model size. It investigates this sensitivity across four model families and evaluates whether averaging across prompts makes model comparisons more reliable.
Critical strengths
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The paper addresses an important measurement problem: whether reported differences between models reflect stable model properties or choices made when constructing probes.
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The crossed design varies both evaluation and deployment framings while keeping task text byte-identical, allowing their effects and interactions to be examined systematically.
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Experiments across multiple model families, split-half analyses, and pooling controls provide substantial evidence that wrapper sensitivity is reproducible rather than merely item-sampling noise.
Critical weaknesses
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Averaging across wrappers makes scores more consistent, but they may still reflect surface features rather than evaluation awareness. Testing on a format-controlled dataset would help resolve this concern.
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The sign-flip baseline may retain part of the original concept direction. Calling it “content-free” therefore needs stronger justification.
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The two disjoint wrapper subsets can still share individual framings. Their agreement does not show whether the results extend to new framings.
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The recommendation to add wrappers rather than items is based on the current benchmark. New, format-balanced items could address problems that wrapper averaging cannot.
Questions for authors
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Do the main findings hold when prompt format is controlled? Does wrapper averaging also improve agreement with behavioral measures of evaluation awareness?
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How similar are the sign-flip directions to the original probe directions? Would other random-direction baselines give the same results?
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Do the two wrapper subsets still agree when they share no framings on either side? How does Equation (1) account for the separate effects of the two framing arms?
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Does the sensitivity persist when the wrappers express the same scenario in different words?
4 comments
Response to Reviewer J3ye (2/2)
W3.
The two disjoint wrapper subsets can still share individual framings. Their agreement does not show whether the results extend to new framings.
We agree: shared framings inflated the agreement we reported (Section 9). Splitting each arm's six framings into halves, in all 200 ways, gives two subsets that share nothing. Their agreement is lower than for random disjoint subsets of the same size on every ladder (Kendall 0.83 against 0.90 on OLMo-2, 0.02 against 0.23 on Qwen2.5). It never exceeds the 95th percentile of the task-permutation null. With four or five models that test sits at a ceiling. On OLMo-2 the real median Spearman and the null's 95th percentile are both 1.0, and on Qwen3.5 with thinking both are 0.9.
| Framing-disjoint halves | Same scaling sign |
|---|---|
| OLMo-2 | 98.5% of splits |
| Qwen3.5 | 98.5% (99.5% with thinking) |
| Qwen3 | 82.5% |
| Qwen2.5 | 20% |
Equation (1) treats the 36 wrappers as exchangeable, pooling the two arms. Section 6 and Appendix B analyse the design as crossed, where the flat form is optimistic (0.629 against 0.257).
| Wrappers for | Crossed | Flat |
|---|---|---|
| Qwen3.5 | 36 (6 framings per arm) | 12 |
| OLMo-2 | 64 (8 per arm) | 10 |
| Qwen3 | no number suffices | 248 |
| Qwen2.5 | no number suffices | never |
Table 1 now prints both. R2 now follows the crossed analysis, and R3 the byte-identical tasks.
W4.
The recommendation to add wrappers rather than items is based on the current benchmark. New, format-balanced items could address problems that wrapper averaging cannot.
We agree, and R3 now says so. On the byte-identical set the largest facet is the pairing of training and test framings. A reliable design must therefore sample the framings of the scored items as well as the wrappers.
Q1.
Do the main findings hold when prompt format is controlled? Does wrapper averaging also improve agreement with behavioral measures of evaluation awareness?
Answered with W1 above.
Q2.
How similar are the sign-flip directions to the original probe directions? Would other random-direction baselines give the same results?
Answered with W2 above.
Q3.
Do the two wrapper subsets still agree when they share no framings on either side? How does Equation (1) account for the separate effects of the two framing arms?
Answered with W3 above.
Q4.
Does the sensitivity persist when the wrappers express the same scenario in different words?
Yes for the folded score, and rewording reorders the models. The signed value and the orientation stay stable.
Two paraphrases of each of the 12 framings keep every scenario fact. A script checked that each shares no content 4-gram with the original and stays within 10 percent of its length. We extracted 11 rungs (Qwen3-0.6B to Qwen3-32B, Qwen3.5-0.8B to Qwen3.5-27B).
| Variance share | Qwen3 | Qwen3.5 |
|---|---|---|
| Rewording | 0.23 | 0.18 |
| Scenario | 0.19 | 0.32 |
| Model wrapper wording | 0.31 | 0.27 |
| Model wrapper | 0.16 | 0.10 |
Rewording carries a share comparable to the scenario's. The registered decomposition asked whether the scenario carries the model-by-wrapper term. It does not: the three-way term, where a wrapper's ordering of the models changes with its wording, is larger.
Under rewording, the folded score reproduces only at Spearman 0.19 to 0.66, and the signed interior-band value at 0.68 to 0.95. Orientation survives on all 11 models (0.75 to 0.998, each above its registered baseline). On the six smaller rungs it is already 0.91 to 0.99 at the paraphrased framings' embeddings. The scaling sign sits in between, following partly the scenario and partly the words:
| Wrappers of 36 keeping their sign | Qwen3 | Qwen3.5 |
|---|---|---|
| Second paraphrase | 29 | 29 |
| Random re-pairings, 95th percentile | 25 | 27 |
| First paraphrase | 26 | 24 |
| Random re-pairings, 95th percentile | 26 | 28 |
The results are labelled descriptive. The registered gate reran the original framings and asked each wrapper's statistic to reproduce within 0.01. It passed on the five largest rungs (largest change 0.004) and failed on three of the six smaller ones (0.030, 0.018 and 0.0115). Two failures came from the change of GPU and software stack, one from batch composition on the same machine. An amended gate, written after that failure and before any paraphrase number was computed, still failed on two. All versions come from one extraction. Stored and rerun statistics agree at Spearman 0.988 to 1.000, far above the 0.19 to 0.66 from rewording (Appendix T).
Sections 6, 9 and 10, Table 1, the new Section 11, the recommendations, the limitations and the appendices are revised accordingly. We hope the answers bear out your reading of the paper's importance.
We are happy to discuss any of these points further.
Rebuttal
The author resolved most of my concerns. I will maintain my score.
Reply to Reviewer J3ye
Thank you for reading our response and for letting us know. If any concern remains open, could you tell us which one? We will answer it before the discussion closes.
Response to Reviewer J3ye (1/2)
Thank you for the review, and for calling this "an important measurement problem". Most of your questions became experiments.
W1.
We ran both. On byte-identical tasks the input embeddings already orient the framings, and agreement with behaviour follows scale and wording.
Format-controlled items (Section 11, Appendix R).
So this test cannot tell a computed representation from the framings' words. Alignment trends take both signs on every ladder, as registered, but no more often than under random framing partitions (12th to 79th percentile). Nor does a wrapper's sign reproduce across disjoint test framings beyond that null.
Behaviour (Section 9, Figure 1e, Appendix S). We registered a comparison with SAD stages-oversight accuracy, the task our scoring set comes from (278 of 400 items shared on Qwen3, Qwen3.5 and OLMo-2). We ran it with its authors' code on all 19 non-thinking checkpoints. The primary variant (sp_large) met all three preconditions: split-half reliability 0.94, between-model SD 0.084, all 19 models included.
Brackets: 95% item-bootstrap interval. p: one-sided within-ladder permutation test. Averaging does improve agreement, descriptively. The two controls computed after the registered result show that scale and wording produce it. This extends the paper's conclusion from probe scores to behavioural anchors. Other registered readings:
W2.
We agree, and renamed it the label-permuted floor. "Content-free" now names a floor that is content-free by construction, and it gives the same picture.
New floor (Appendix N, Table 5): random directions matching the released direction's layer-to-layer autocorrelation.
One model of four clears 2 SD. The floor reaches 63 to 133 percent of the published values (sign-flip floor: 70 to 116 percent).
Sign-flip draws (released 204-item construction). Their median ∣cos∣ with the rebuilt direction is 0.06 to 0.18. But per-state medians reach 0.60, single draws at single states reach 0.97 to 0.99, and the statistic maximises over states. The draws are also nearly collinear with each other (0.84 to 0.98). So the floor's SD understates content-free spread, and its mean may be biased. On the framing ladders the construction is degenerate (median ∣cos∣ 0.98 to 0.99 with the real direction), so the ladder analyses use other nulls.
Other nulls (Appendix N, Table 4). Task-permutation directions sit further from the real ones (mean ∣cos∣ 0.26 to 0.37) than two real wrappers do from each other (0.38 to 0.43). The nulls disagree. Per-wrapper slopes are more reproducible than 98 to 100 percent of isotropic draws on Qwen2.5 and Qwen3, and less than matched rotations on Qwen3.5. The 36-wrapper trend beats matched rotations on Qwen3, Qwen3.5 and OLMo-2, and sits inside the task-permutation null everywhere. That null keeps the framings' words, so we read the trend against it. The appendix reports every null.