acceptodds
Under review as a conference paper at ICLR 2027

Relative Representations Enable Portable White-Box Monitoring Across Language Models

Abstract

Independently trained autoregressive language models often acquire similar capabilities, but it remains unclear whether their internal representations organize behaviorally relevant information in compatible ways. We show that models do in fact organize information similarly by using specific behavioral probes that operate on compatible representations. This unlocks portable white-box monitoring: a probe developed and validated on one model can be reused when the model changes, without requiring labeled target data. To overcome incompatible native activation coordinates, we express each example through its angular distances to a shared set of anchors. We introduce a *global anchored* construction that summarizes information from all transformer layers and removes model-specific layer selection, so the same frozen probe can be straightforwardly applied to another model. We evaluate cross-model probe transfer across monitoring tasks on trivia datasets, safety monitoring, and mathematical reasoning. On average, transferred global anchored probes preserve at least 85% of same-model probe AUROC over chance. Anchored probes also support transfer to related datasets, remain robust across model scale and prompt changes, and retain performance better than standard probes after model updates. Transfer is nevertheless task- and target-dependent and can fail even when the monitored property remains strongly decodable in the target model. Overall, global anchoring reveals substantial task-relevant compatibility across independently trained models and provides a practical basis for portable white-box monitoring.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Activation probing, white-box monitors, representational alignment, AI safety and control

Reviews

Among:
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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_WjG2OpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper uses relative representations to train linear probes that predict properties of model behavior. Empirically, the authors show that these probes can transfer across models, related datasets, and model updates without retraining, suggesting that behaviorally relevant information is organized in compatible ways across different models.

Critical strengths
  1. Evidence of cross-model compatibility in behavioral representations. The authors provide empirical evidence that behaviorally relevant information is organized in compatible ways across different models, as demonstrated by the transferability of probes trained on relative representations.

  2. Extensive empirical evaluation. The paper evaluates the proposed approach across different models, tasks, and settings, including cross-model transfer, cross-dataset transfer, and model updates, helping establish its applicability and limitations.

Critical weaknesses
  1. Limited methodological novelty. The proposed method largely builds on existing relative representation and linear probing techniques, with the main technical additions being all-layer aggregation. While applying these techniques to cross-model behavioral monitoring is interesting, the methodological novelty appears relatively limited, and the main contribution lies in the empirical evaluation.

  2. Missing all-layer Standard baseline for Online MATH. The main experiments compare single-layer Standard probes (at relative depth 0.8) against Global Anchored probes that aggregate information across all layers. Although the authors provide all-layer Standard baselines for Trivia and Guard Distillation in appendix, I could not find the corresponding comparison for Online MATH. Given that Global Anchored outperforms Standard by 3.9 AUROC points on MATH-500 in the same-model setting, including this baseline would help determine whether the improvement comes from relative representations or from concatenating representations across all layers rather than using a single layer.

  3. Organization of experimental results. The experimental results section is somewhat difficult to follow due to the large number of evaluation settings and comparisons. Some important baselines and ablations are also scattered across the appendix, making it harder to assess the main experimental findings.

  4. Minor presentation issues.

    • Figure 1 is not explicitly referenced in the introduction, although it provides an overview of the proposed method.
    • Line 38 contains the duplicated phrase "introduce relative representations".
Questions for authors
  1. Choice of representation extraction protocol. The representation extraction protocols differ across the three settings: Trivia uses the final prompt token before generation, Guard Distillation averages over completion tokens, and Online MATH averages over generated tokens up to a fixed checkpoint. Could the authors elaborate on the motivation behind these choices and whether the results are sensitive to the extraction protocol?

  2. Selection of regularization strength. Is the regularization strength CC independently tuned for Standard and Anchored probes? Given the substantial differences in feature dimensionality, independently tuning CC for each probe type could help ensure a fair comparison.

1 comment

We thank the reviewer for their thoughtful feedback.

The proposed method largely builds on existing relative representation and linear probing techniques, with the main technical additions being all-layer aggregation. While applying these techniques to cross-model behavioral monitoring is interesting, the methodological novelty appears relatively limited, and the main contribution lies in the empirical evaluation.

Novelty. The contribution is indeed new empirical evidence that independently trained LLMs encode information about their own behavior compatibly enough to reuse a frozen monitor. Prior work transferred encoder classifiers (Moschella et al.; Maiorca et al., 2023), while Chen et al. (2025) used affine maps to transfer probes for input-text properties within model families. We test whether compatibility extends to target behavior across families using anchored probe transfer. This is also a stronger test, because we do not learn a mapping between models.

This tests the behavioral side of the Platonic Representation Hypothesis (Huh et al., 2024): whether representational convergence includes information about model-specific behavior. The findings also connect representation alignment with transferable white-box monitoring. We believe these results to be valuable to the community.

Practically, this we find that probes can be reused across model changes without target labels, enabling cross-model monitoring. We now also extend Maiorca et al.'s encoder-classifier transfer to behavioral probes using Procrustes. This provides additional evidence of compatibility through a fitted map (E.2).

Although the authors provide all-layer Standard baselines for Trivia and Guard Distillation in appendix, I could not find the corresponding comparison for Online MATH.

All-layer Standard for Online MATH. Thank you for pointing out this omission. We have added this probe in our revision. Same-model MATH-500 AUROC is:

Single-layer StandardAll-layer StandardGlobal Anchored
77.9 ± 0.377.4 ± 0.381.8 ± 0.3

All-layer Standard remains close to single-layer Standard, while Global Anchored achieves higher AUROC. See 4.1 and D.2 for details.

The representation extraction protocols differ across the three settings: Trivia uses the final prompt token before generation, Guard Distillation averages over completion tokens, and Online MATH averages over generated tokens up to a fixed checkpoint. Could the authors elaborate on the motivation behind these choices and whether the results are sensitive to the extraction protocol?

Q1. Extraction protocol. In trivia, the final prompt state is used to predict the next answer token, making it a natural pre-answer probe input. Guard labels the whole completion, so we average completion-token representations to summarize the labeled text. For online MATH, averaging only the generated prefix summarizes the reasoning available when we want to monitor. Mean pooling gives a fixed-size input, and is a standard approach in the literature.

With Guard completion activations fixed, changing anchors from final prompt states to mean completions changes calibrated transfer by at most 2.7 AUROC points (App. C.5). MATH transfer is similar at 64, 128, and 256 tokens (D.1). Transfer therefore seems stable under a variety of anchor and checkpoint choices.

Is the regularization strength (C) independently tuned for Standard and Anchored probes? Given the substantial differences in feature dimensionality, independently tuning (C) for each probe type could help ensure a fair comparison.

Q2. Regularization strength. MATH already selects C independently for each probe from {0.01, 0.1, 1, 10, 100}. To strengthen the Standard comparison on trivia and Guard, the revised main tables select Standard's C on validation using the same grid; Anchored retains fixed C, which favors Standard. Standard AUROC increases by at most 0.7 points, and Anchored remains within 1.6 points of Standard on every trivia and Guard dataset. See App. A.5 for details.

The experimental results section is somewhat difficult to follow due to the large number of evaluation settings and comparisons. Some important baselines and ablations are also scattered across the appendix, making it harder to assess the main experimental findings.

Figure 1 is not explicitly referenced in the introduction, although it provides an overview of the proposed method.

Organization and minor issues. Sec. 4 now introduces the questions and comparisons before the results. 4.2 includes the raw-coordinate baseline and few-label curves, as well as the Procrustes baseline. Fig. 1 is referenced in the introduction, and the duplicated phrase is removed.

We would ask the reviewer to please share any remaining concerns, which we are happy to address. If the revisions resolve their concerns, we would ask them to please consider raising their score.

Reviewer_E1ZJOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
3(+1)
Presentation
3
Soundness
2(+1)
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Paper summary

The paper addresses the transferability of probing LLM. The paper argues that transferability allows probing models from different model families without retraining the probe. The paper proposes a global anchor construction by taking representations from all layers of the models. The paper shows strong performance in same-model and cross-model settings.

Critical strengths
  • The paper provides a useful global representation construction. Aggregating information across layers removes the need to select corresponding layers across models, making the approach easier to apply.
  • The paper presents strong results on the same-model setup. The anchored probes preserve useful behavioral information, achieving performance comparable to conventional activation probes across the evaluated tasks.
  • The paper shows that probes remain predictive across independently trained models without target-model labels or retraining, suggesting practical potential for portable monitoring.
Critical weaknesses
  • No baselines: The main paper did not establish the effectiveness of the proposed global representation in comparison with baselines before going further into the analysis. Stronger comparisons with existing transfer methods under matched data and adaptation budgets are needed to establish the significance of this extension.

  • Contamination: The evaluation relies on public benchmarks that may have appeared in the monitored models’ pretraining or instruction-tuning data. The probe train/test splits and anchor-selection procedures do not address this possibility, leaving shared benchmark exposure as an alternative explanation for some transfer results. Evaluation on newly created or private examples would help establish whether the findings generalize beyond potentially contaminated benchmarks.

  • Novelty: Shared-anchor representations and zero-shot component reuse were introduced in prior work. The main methodological extension appears to be aggregating activations across layers before constructing relative representations and applying them to behavioral monitoring.

Questions for authors

See weaknessess

2 comments

Thank you. We have added baselines and clarified the scientific contribution: whether independently trained LLMs represent their own behavior compatibly enough to reuse a frozen monitor. We also test the shared-answer explanation on inputs where source and target disagree, finding that predictions track the target’s behavior. These revisions address the missing comparisons and strengthen the evidence for behavioral compatibility.

Shared-anchor representations and zero-shot component reuse were introduced in prior work. The main methodological extension appears to be aggregating activations across layers before constructing relative representations and applying them to behavioral monitoring.

Novelty relative to prior work. The contribution is new empirical evidence that independently trained LLMs encode information about their own behavior compatibly enough to reuse a frozen monitor. We credit Moschella et al. and Maiorca et al. (2023) for encoder-classifier transfer. Chen et al. (2025) transferred probes for input-text properties within model families using affine maps. Our anchored transfer instead tests compatibility across families and scales for model-specific answers without fitting a mapping, including when identical inputs produce different outputs.

This tests the behavioral side of the Platonic Representation Hypothesis (Huh et al., 2024): whether representational convergence includes information about each model's own behavior. It also provides evidence for reusing white-box monitors across model changes without target training labels. Shared-anchor coordinates and global aggregation make frozen-probe reuse possible across different activation widths and depths. The added Procrustes baseline tests the same behavioral compatibility through a fitted map (E.2). Sec. 2 discusses the distinctions from prior work.

Stronger comparisons with existing transfer methods under matched data and adaptation budgets are needed to establish the significance of this extension.

Role of the baseline comparisons. We agree that matched-budget comparisons clarify practical value, but disagree that comparisons with competing transfer methods are a prerequisite for the scientific significance of this paper. Our main finding concerns compatibility of behavioral information across independently trained LLMs, which we test by transferring behavioral probes. In particular, the test is stronger than existing transfer methods, because ours requires no learned mapping and targets model behaviour.

We have added two baselines:

  • Another route to transfer: We have added Procrustes maps fitted on the same unlabeled anchors as our probes (4.2, E.2). Procrustes tests compatibility after fitting a model-pair map. Our anchored transfer is a more constrained test, since the frozen probe predicts target behavior directly in the shared coordinates, without a learned alignment. Procrustes is stronger in several full-budget settings, while anchored transfer is competitive with fewer anchors, consistent with needing no fitted map.

  • Practical value for monitoring: few-label target probes are an alternative when obtaining training labels is not prohibitive. Matching our probes takes 50 labels on TruthfulQA, but more than 1000 on MATH-500 (E.1). This quantifies the training labels saved by monitor reuse, which matters when labels are costly or unavailable.

Sec. 4.2 now presents these comparisons alongside raw-coordinate transfer. We note that secs. 4.1 and 4.3 already compared the global representation with local probes.

The evaluation relies on public benchmarks that may have appeared in the monitored models’ pretraining or instruction-tuning data. Evaluation on newly created or private examples would help establish whether the findings generalize beyond potentially contaminated benchmarks.

Benchmark exposure. Shared memorized answers cannot explain the full transfer pattern. We can test this on questions where source and target model disagree. If the probe predicts the target answer on these data points, then agreement on benchmark answers cannot explain that prediction. Indeed, on trivia questions where models disagree, transferred GT prediction matches the target's answer on 75.0–88.4% of items across our six settings, versus 7.1–19.9% for the source's (B.10). On BeaverTails disagreements, completion transfer reaches 78.0 AUROC versus 52.1–57.5 for prompt-only baselines (C.11). Thus, we observe transfer of target-specific behavioral information even when source and target behavior differ. Shared data exposure could contribute to a general compatibility, but reproducing common benchmark answers is insufficient to explain it. We therefore do not think this concern invalidates our results.

We would appreciate clarification on whether the revised comparisons and disagreement tests address your soundness concerns, or whether a specific issue remains that undermines the behavioral-compatibility finding.

Reviewer_E1ZJOpenReview ↗

Response to the rebuttal

Thank you for providing the additional Procrustes experiments and comparing them. This setup shows that anchored transfer helps (in 2 datasets) while losing on 2 other datasets. As such, my concern about lacking a baseline is fully resolved. However, this result also shows that using all layers is not optimal for a substantial number of tasks. Though it is still a good-enough, simple starting solution. As such, I raised my overall rating to 2.

Reviewer_AERBOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
3
Read review
Paper summary

The core contribution is a demonstration that monitoring probes can be moved between independently trained LLMs without target labels, adapters, or retraining. The device is Moschella et al.'s relative representation: each activation is expressed by its angular distances to a shared set of 300 to 600 anchor examples, so the representation has one coordinate per anchor regardless of model width or depth. The authors add a global version that concatenates all layers before computing distances, removing layer selection, and a source-only calibration rule for choosing which probe to transfer.

The main claims are four.

  • First, anchored probes match standard probes on the same model.
  • Second, frozen probes transfer across models while keeping at least 85% of same-model AUROC above chance.
  • Third, transfer survives joint model-and-data shifts, a 1B-to-70B scale gap (94.8 versus 96.0 for a 70B-trained probe), prompt changes, and LoRA model updates better than standard probes.
  • Fourth, transfer is conditional: it fails for MATH on GPT-OSS (52.4 versus 78.5 when trained on the target) even though the property is decodable there.

The evidence is three task settings (trivia with output and ground-truth prediction; Guard Distillation on BeaverTails and Toxic-chat; online MATH correctness at 128 tokens), six- and four-model pools with leave-one-target-out transfer, external-family targets, a matched-dimension raw-coordinate baseline that transfers at chance (Llama-8B to Mistral-7B, 48.0 versus 94.0 anchored), staleness tests after LoRA updates, anchor-correspondence recovery from geometry alone, and low-FPR recall throughout.

The conclusion is that independently trained models share enough relational structure to reuse monitors, with task- and target-dependent limits. Probe monitors are already deployed in production, so a method that lets them survive model updates and transfer to new checkpoints without relabeling has direct operational value.

Critical strengths

The protocol is strict, and that is what makes the robustness results believable. Source selection uses only source-pool validation. External targets are evaluated after the protocol is frozen, with target-trained probes used only as post-hoc diagnostics. Normalization statistics are frozen from the source. The 1-to-5 source-pool progressions are reported (Tables 19, 31, 56), low-FPR recall is given alongside AUROC, and the matched-dimension standard-probe baseline is exactly the control one wants. The failure cases (Llama-3.2-3B on TruthfulQA, GPT-OSS on MATH, the BeaverTails-to-Toxic-chat direction) are discussed in the main text rather than buried.

The practical case is real and cheap. Deploying a monitor on a new model needs one unlabeled pass over the anchors. A probe trained on a 1B model gets 94.8 on 70B, against 96.0 for a 70B-trained probe (Table 26), which means labeled probe development can happen on the small model. The model-update robustness (Table 61) is directly relevant to production monitoring and may have broader demand than cross-model transfer itself.

Critical weaknesses

Much of the transfer that works is on tasks that are either saturated or predictable from the input alone, which weakens the scientific claim. Trivia output prediction is at 99.5 to 100 same-model, so 99% transfer is uninformative. GT prediction on SciQ (99.4) and MMLU (96.2) is also very high, and I think the reason is that the correct answer can be decoded from the question text itself.

Anchor distances are a relational encoding of input meaning, so similar questions get similar coordinates regardless of what the model does with them. That makes trivia GT transfer mostly a confirmation of what Moschella et al. already showed, that input semantics are compatibly represented, rather than evidence that models represent the results of their own computation compatibly.

On the tasks where model-specific behavior actually matters, the losses are larger: TruthfulQA GT 73, Guard 83 to 86, MATH 78. At 10% FPR the drops are substantial (Guard BeaverTails recall 82 to 63.5, TruthfulQA GT 69 to 34). GPT-OSS BeaverTails transfer is 57.5 plus or minus 12.6 with only 1.0 to 4.8% unsafe completions on the external models. MATH-to-GPT-OSS is 52.4 against 78.5 to 78.7 target-trained (Table 4, Section 4.3.1). As a safety monitor at a realistic operating point, this is not yet reliable.

The only baseline ruled out is "raw coordinates with matching width." Two cheaper or comparable alternatives are missing. One is to fit an unlabeled linear alignment (Procrustes or CCA) from a few target activations and transfer a standard probe. The other is to retrain a probe on a small number of target labels. Without the second especially, the value of "no target labels" is unquantified; if 50 labels get you from 86 to 95, the portable probe matters much less. Also, B.11 and C.13 show that an all-layer standard probe matches the single-layer one, so the global construction's advantage is fixed dimensionality, not performance. The paper should say so plainly.

The global construction is justified empirically rather than by design. Appendix A says layers are concatenated with no per-layer normalization, so high-norm (typically late) layers may dominate the angular distance. Whether this drives per-model transfer differences is unexamined.

There is no label-free way to predict failures. The frame-congruence, CKA, and RSA measures in C.10 do not predict transfer (Spearman 0.15 to 0.27). That is reported honestly, but it leaves practitioners unable to say how much target validation is needed before deployment. The compute estimates in A.10 do not cover online latency for reading every layer.

Questions for authors
  1. Can you separate model-behavior information from question-semantics information in trivia GT prediction? For example, compute transfer AUROC only on items where source and target models give different answers, or train the same anchored probe on a pure text encoder and report GT AUROC. If the latter is near 96, MMLU and SciQ GT transfer does not speak to behavioral compatibility.

  2. How does a probe retrained on 20, 50, 100, or 200 target labels compare to the transferred probe? And have you tried an unlabeled Procrustes or CCA alignment with standard probes on the Llama-Mistral pair?

  3. Without per-layer normalization, how is the norm distributed across layers in the concatenated vector? Does the source-only selection and external-family advantage survive with normalization?

  4. Can anchor coverage or source-pool statistics predict failures like GPT-OSS MATH, where the target still encodes the property? Can the MoE hypothesis be tested by adding an MoE model to the pool?

  5. For the external safety targets, how many unsafe examples are there per seed and what is the uncertainty? With 1.0 to 4.8% unsafe on BeaverTails, would it be more accurate to drop those cells or report Toxic-chat only? How far down in FPR can you go, and what target validation would you require before deployment?

1 comment

We thank the reviewer for their close reading and thoughtful suggestions.

Can you separate model-behavior information from question-semantics information in trivia GT prediction?

Q1. Behavioral information. To test model-specific information on shared questions, we evaluate items where the selected source and target give different answers. The table reports how often probe predictions match each model's answer. We find that probes track the target model's answers much more often.

DatasetTarget (%)Source (%)
MMLU85.214.8
SciQ86.313.7
TruthfulQA80.119.9
MMLU (4)75.013.5
SciQ (4)88.47.1
TruthfulQA (4)76.210.7

This shows that the probes follow model behavior, rather than question-semantics. We note the probe also follows the target when it errors: binary GT AUROC is low when the source is correct and high when the target is correct (B.10).

How does a probe retrained on 20, 50, 100, or 200 target labels compare to the transferred probe?

Q2a. Few-label target probes. We train Standard and Anchored probes on small labeled sets to quantify label savings. The table lists the smallest budget matching calibrated transfer's AUROC (4.2; E.1):

SettingTransfer AUROCStandardAnchored
MMLU GT96.2>400>400
TruthfulQA GT75.35050
BeaverTails86.4100200
Toxic-chat83.6200400
MATH78.4>1000500

Reusing the frozen probe can therefore save hundreds of target training labels, though the savings vary by setting.

And have you tried an unlabeled Procrustes or CCA alignment with standard probes on the Llama-Mistral pair?

Q2b. Unlabeled alignment. Following Maiorca et al. (2023), we fit Procrustes on the same anchors to transfer frozen Standard probes. For Llama-8B ↔ Mistral-7B, AUROC averages 48.0 in raw coordinates, 94.1 with anchoring, and 94.7 with Procrustes. Anchoring is competitive with fewer anchors, while Procrustes is stronger at full budget on several datasets (4.2; E.2), consistent with needing to learn a map.

Without per-layer normalization, how is the norm distributed across layers in the concatenated vector?

Q3. Layer normalization. We measured how layer norms weight the global cosine, and found that the final third accounts for 72–99% of the weight, depending on setting. To test the effect of weighting, we rescale each layer to unit norm before creating the global features. Doing this changes same-model AUROC by at most 0.5 points. Source-only calibrated transfer remains similar or improves in-pool and improves on every external Guard and MATH target. For instance, GPT MATH AUROC rises from 53.9 to 67.9 with 128-token source selection (App. F). We now report this as a variant.

Can anchor coverage or source-pool statistics predict failures like GPT-OSS MATH, where the target still encodes the property?

Q4. GPT-OSS failure. We have not yet found a reliable label-free failure predictor. The Guard anchor-geometry measures we tested were weak or dataset-dependent (C.10). We further investigated the GPT MATH failure, and found it is related to the strong weighting of late layers. Only using the first two-thirds of layers raises AUROC from 52.3 to 73.5 (4.3.1; D.5.1). An unlabeled Procrustes map at depth 0.8 also reaches 75.9 with prefix-mean anchors (E.2), so the failure seems specific to the default anchored representation: local anchored transfer can also reach 76.2 AUROC at depth 0.65. Finally, normalizing each layer improves global transfer on GPT-OSS MATH from 53.9 to 67.9 AUROC (App. F), as above.

For the external safety targets, how many unsafe examples are there per seed and what is the uncertainty? With 1.0 to 4.8% unsafe on BeaverTails, would it be more accurate to drop those cells or report Toxic-chat only?

Q5. External safety. We agree on BeaverTails and have moved it to App. C.3. Toxic-chat has 15–25 unsafe items/seed. AUROC with 95% item-bootstrap CIs is 87.6 [80.4, 93.2] for OLMo-3, 81.8 [75.8, 87.3] for Gemma-3, and 66.9 [55.7, 76.8] for GPT-OSS (C.3).

Also, B.11 and C.13 show that an all-layer standard probe matches the single-layer one, so the global construction's advantage is fixed dimensionality, not performance.

All-layer Standard. The global construction's advantage is indeed fixed a dimensionality that naturally interacts with the anchored construction. Sec. 4.1 now notes similar all-layer and single-layer Standard performance. Note that standard does not transfer.

The compute estimates in A.10 do not cover online latency for reading every layer.

Online latency. A.10 now reports median decoding overhead of 1.4–4.4% for Llama 8B on H100, depending on batch and context size.

We would ask the reviewer to please share any remaining concerns, which we are happy to address. If the revisions resolve their concerns, we would ask them to consider raising their score.

Comments on the paper

1 comment

We thank the reviewers for their careful reading. All three reviewers recognized the evidence for behavioral probe transfer across independently trained models. They also highlighted the strict protocol and practical use (AERB), the global construction (E1ZJ), and the extensive empirical evaluation (WjG2).

The main revisions are:

  1. Behavioral information: disagreement analyses in trivia and Guard Distillation, and a MATH difficulty control (Apps. B.10, C.11, and D.4).
  2. Transfer baselines: few-label target probes and unlabeled Procrustes alignment using the same anchors (Sec. 4.2; Apps. E.1–E.2).
  3. Probe design: layer-normalization checks and validation-tuned Standard regularization (Apps. F and A.5).
  4. Practical evaluation: external safety counts and uncertainty and measured online latency (Apps. C.3 and A.10).
  5. Presentation: a clearer experimental roadmap, motivation for extraction choices, and expanded related-work comparisons (Secs. 2–4).

The responses below address each reviewer point and refer to the revised paper for the full details and results. We have updated the paper pdf, and kept revision changes in blue.

Unless noted otherwise, scores are means over three seeds, averaged across targets for pooled comparisons; ± denotes the standard error over seeds.

Scoring correction. While working on the analyses above, we found that probe probabilities can round to 1 for very confident probes, creating improper ranking ties. We have rescored the reported metrics using the non-saturated logits instead and have updated the tables and figures. Overall, this does not affect same-model scores, slightly improves transfer scores, and leaves the main conclusions unchanged. For example, TruthfulQA GT calibrated-transfer AUROC changes from 73.1 to 75.3, and recall at 10% FPR from 34.0 to 42.6. See App. A.1 for details.

From OpenReview, CC BY 4.0. Authors as signed there; shown unedited.

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