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Under review as a conference paper at ICLR 2027

Depthwise Trajectory Signatures: Detecting Hallucination from Inside

Abstract

Large language models can produce fluent answers that are wrong, and most safeguards verify the answer only after it is complete. We take a different approach. Instead of checking what the model said, we monitor how it decided. Inside a transformer, a token prediction is built block by block, so the hidden state traces a trajectory across depth. We summarize this trajectory with a small set of geometric quantities, trajectory signatures, constructed to be invariant to the arbitrary choices that normally make depthwise measurements incomparable across layers, samples, and models. On these signatures we train a lightweight validator that detects hallucinations without modifying the base model. The same signatures localize the depth the validator finds anomalous, enabling a targeted correction at a single block during generation. Across 12 benchmarks and 5 LLMs, the validator achieves the best AUROC in 45 of 60 settings against baselines, and the refinement reduces the hallucination ratio by at least 10% relative in 29 of 45.

Primary area:
interpretability and explainable AI
Keywords:
hallucination detection, large language models, inference-time intervention, transformer internals, geometry analysis

Reviews

Among:
Shape:
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_zsbCOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
1
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2
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Paper summary

The paper constructs geometric features of token-wise hidden-state trajectories across transformer depth, using competitor-based subspaces, orthogonal alignment, and module-attribution statistics. A supervised validator detects hallucinations, and its event scores guide rollback and single-block intervention. Evaluation covers five LLMs and twelve detection benchmarks, with refinement tested on nine benchmarks

Critical strengths
  1. The paper presents a concrete construction of depthwise geometric features and connects supervised detection to targeted inference-time intervention without updating the base LLM.

  2. Evaluation spans five LLMs and twelve benchmarks across several task categories, with feature-group ablations, refinement results, and measured extraction costs.

Critical weaknesses
  1. Experiments. Broad coverage does not resolve the key attribution questions. ICR Probe (ACL 2025), which already studies cross-layer updates and module contributions, is omitted. Matched-supervision comparisons with ordered hidden states or simple differences, and ablations of subspace construction, alignment, and path integration, are needed; feature-group ablations cover only HaluEval QA. Refinement lacks matched regeneration-only and random/fixed-site controls, so improved outputs do not establish causal localization. Repeated-run uncertainty and human checks of judge labels are missing; a shared judge does not rule out differential bias. A newer open-weight model would also help test applicability.

  2. Presentation. Even after careful reading, dense multi-index notation and abrupt transitions make the pipeline and its assumptions difficult to follow. The introduction overstates the static/dynamic distinction and moves too quickly from detection to error localization. Invariance claims need qualification for median centering, direction sampling, and weak-overlap identity resets. Online monitoring claims should be distinguished from replay-based evaluation, and the twofold decode bound from total runtime including extraction, fitting, and calibration. Figure 1(b–c) contains blurry elements, and the conclusion section opens with an editing fragment. A notation table and clearer separation of definitions, assumptions, and guarantees would help.

Questions for authors
  1. How does the method compare with ICR Probe and similarly sized supervised detectors using ordered hidden states or simple differences? Which gains require subspaces, alignment, and path integration beyond HaluEval QA?

  2. Does refinement outperform matched regeneration-only and random/fixed-block interventions? What supports interpreting the highest event score as an error source?

  3. Please provide repeated-run uncertainty and manual label checks, and qualify the claim that judge noise cannot favor the method. Can applicability be checked on a newer open-weight model?

  4. Please reconcile invariance with median centering, sampling, and identity resets, distinguish replay from online monitoring, and account for all overheads in the cost bound.

8 comments
AuthorsOpenReview ↗

Question 1

We thank the reviewer for pointing us to ICR Probe, which is indeed closely related. We added it to Table 1 for all five base LLMs and twelve benchmarks. We use the official implementation and probe with the paper's settings, trained on the same training split as our validator. Our validator exceeds ICR Probe in 44 of 60 combinations, by +1.20+1.20 AUROC on average, and has the higher mean on every base LLM.

Base LLMICR ProbeOursOurs > ICR Probe
Qwen2.565.3267.5010 / 12
Gemma264.6565.647 / 12
Phi-363.6264.379 / 12
LLaMA365.2266.329 / 12
Mistral63.4364.419 / 12
All64.4565.6544 / 60

Matched-supervision comparison with ordered hidden states and simple differences. We replaced our signatures with two inputs read by the same GRU validator under the same training setup, so the detector, its size, and its supervision are matched. The first is the simple differences of consecutive hidden states (Simple diff.), and the second is the ordered hidden states themselves (Ordered states). Both fall well below our signatures in all 10 cells, by 14.514.5 and 14.314.3 AUROC on average.

Construction ablations beyond HaluEval QA. We extended Table 3 from HaluEval QA to HaluEval General, with the feature groups, the three construction steps, and the two replacements above. Each construction step lowers AUROC when removed. Fixing a single subspace for all depths (w/o Moving subspace) lowers it in 10 of 10 cells by 6.06.0 on average, replacing the path integral by the endpoint linearization (w/o Path integration) in 10 of 10 by 4.54.5, and removing the transport (w/o Transport) in 9 of 10 by 4.44.4. The one exception is Phi-3 on HaluEval General, at +0.6+0.6. The table gives the mean AUROC over the five base LLMs from a single training run.

DatasetFullw/o Transportw/o Moving subspacew/o Path integrationSimple diff.Ordered states
HaluEval QA67.663.961.963.952.952.1
HaluEval General67.062.060.761.852.853.9

Revisions. ICR Probe is added to Table 1 and to the baseline list in §4. Table 3 now covers HaluEval QA and HaluEval General and includes the construction steps and the two replacements, and §4.3 discusses them.

AuthorsOpenReview ↗

Question 2

We thank the reviewer for asking for these controls, and we agree that a lower hallucination ratio after refinement does not by itself establish that the selected event is the source of the error. We have revised both the evidence and the claim.

Controls. We added the controls you requested to Table 2. On the same flagged responses, with the same rollback position and the same decoding budget, we compare the validator-selected block with regeneration without intervention (Regen-only), the same clamp on a random block (Random layer), and the same clamp on the middle block (Fixed layer). The table gives the mean hallucination ratio (%) over the eight refinement benchmarks.

Base LLMBeforeRegen-onlyRandom layerFixed layerOurs
Qwen2.523.0123.9224.0421.6217.86
Gemma220.9921.4721.8721.9518.55
Phi-319.8623.9222.6621.3514.05
LLaMA326.2728.5429.0128.6222.71
Mistral29.5533.2434.6432.8023.01
All23.9326.2226.4425.2719.24

The validator-selected block gives the lowest ratio in 33 of 40 cells and never raises the ratio above its initial value, while the controls raise it in 24 (Regen-only), 29 (Random layer), and 25 (Fixed layer) of 40 cells. Since all variants share the rollback position, this comparison isolates the choice of block, and the gain comes from where we intervene rather than from resampling.

Interpretation of the top event. We do not interpret the highest-scoring event as the error source, and we have removed wording that suggested it. The validator is trained with response-level labels, so the top event marks where the evidence for hallucination peaks, which may come after the error first appeared. We now describe it as an intervention site, an effective place to correct the generation, and the controls above support this narrower claim. We also compared it with intervening at the first event above the decision threshold, on TriviaQA and HaluEval QA for all five models (Appendix E.1, Table 5). The earlier site gives the lower ratio in 3 of 10 cells, which shows that some errors do begin earlier, and the top event gives the lower ratio in the other 7.

Revisions. Table 2 adds the three controls. The Introduction (first and third paragraphs), the overview of the method section, and "Signature-guided single-block refinement" describe the selected event as an intervention site, and the Introduction and the refinement section state that it is not claimed to be the origin of the error. The term "culprit" is replaced. Appendix E.1 adds the earliest-site comparison.

AuthorsOpenReview ↗

Question 3

Repeated-run uncertainty. We thank the reviewer for these requests. We retrained our validator three times with different random seeds for every model and dataset combination, and Table 1 now reports the mean ±\pm standard deviation. The standard deviation ranges from 0.330.33 to 1.741.74 AUROC across the 60 combinations, with a mean of 0.880.88, and is below 1.01.0 in 38 of them. The detection results are therefore stable across training runs.

Manual label check. We manually labeled 100 outputs of Qwen2.5, 25 each from TriviaQA, HaluEval General, xSUM, and GSM8K, sampled to include both judge labels in near-equal numbers. The judge agrees with the human labels on 89 of 100 outputs, with Cohen's κ=0.78\kappa = 0.78. Of the 11 disagreements, 7 are hallucinations the judge missed and 4 are false alarms.

Judge: Halluc.Judge: Not halluc.
Human: Halluc.447
Human: Not halluc.445

On judge bias. We agree and have qualified the claim. A shared judge cancels label noise that is unrelated to the detectors, but, as you note, it does not rule out bias that correlates with what a particular detector reads, and for refinement the judge scores different texts before and after the intervention. The revised text no longer states that judge noise cannot favor our method, and states explicitly that we do not claim immunity to judge error. What remains is a narrower observation about one asymmetry we can identify. The supervised detectors, ours included, train on the noisy labels that the score-based baselines only face at evaluation, so noise of this kind lowers rather than raises our advantage. The manual check above indicates the size of the noise, with 89 of 100 labels in agreement.

Revisions. Table 1 reports the mean ±\pm standard deviation over three training runs for our validator. The manual check is added as Appendix E.3 with Table 7. The "Labels and baselines" paragraph in §4 is revised accordingly.

Reviewer_FqhYOpenReview ↗
Rating
3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

The paper suggests a new white box method for hallucination detection in LLM’s outputs using Different geometric features of the changes of the hidden state representations of the tokens during generation. The main contributions are: Providing geometric features for the changes between adjacent layers, that are invariant to orthonormal basis changes, and an answer refinement method based on those features to choose one layer and one token to regenerate the response from that point. There are 5 models and 12 datasets being tested and an improvement over 5 baselines in 3.3 AUC points on average. The refinement method gives at least 10% improvement in hallucination count in 29 out of 45 cases.

Critical strengths
  1. There are a comprehensive experiments, and a consistent improvement over many baselines overall.
  2. Not only does the paper show a method to detect hallucinations, but it also shows how using the same method can help one to refine and “correct” mistakes in generation time.
Critical weaknesses

My main concern is that the experiments do not establish whether the improvement over HalluShift stems from the proposed geometric features or the use of a different classifier. To isolate the source of the improvement, the authors should compare both feature sets (the proposed features and those of HalluShift) using the same classifier and conduct an ablation study of the alignment step. See question 4 below.

Questions for authors
  1. Lemma 2 shows invariance to orthonormal basis changes within fixed subspaces. However, more complex changes between layers, including nonlinear ones, are not covered by this result. Why is this enough to say that the features measure “the decision and not the instrument”? Which parts of this claim are proved, and which are assumptions?
  2. The validator is trained with labels for the whole response, and the GRU uses information from previous events. How do we know that the event with the highest score is the source of the error, rather than a sign of an error that happened earlier? Does the method aim to find where the error started, or a useful place to correct it?
  3. Does choosing the layer using the validator work better than choosing a fixed or random layer and applying the same correction? This should be tested on the same flagged responses, with the same rollback positions and decoding budget. How does the method compare with other correction methods using a similar amount of computation?
  4. HalluShift already uses changes between layers, so it is not clear why earlier methods are described as using only “snapshots”. Have you compared HalluShift’s features and your features using the same classifier and training setup? Testing both feature sets with MLP and GRU classifiers would help show where the improvement comes from. For the GRU, HalluShift’s features could be used before averaging them. Also, how does the method perform without the alignment step?
5 comments
AuthorsOpenReview ↗

Question 1

We thank the reviewer for this precise question, which helped us separate the two parts of the claim, and we agree that the original wording did not draw this line clearly.

What is proved concerns the instrument. Lemma 2 shows that the signatures are unchanged by the arbitrary choices of the measurement, namely which orthonormal basis, sign, or rotation the SVD returns within each depth-local subspace, with the transport between windows rotating accordingly (for the centered step st,bcs^c_{t,b}, provided the center μb\mu_b is rotation-equivariant, as stated in the scope paragraph after Lemma 2). As the reviewer notes, Lemma 2 does not cover changes between layers, including nonlinear ones. This is by design. The map from one block to the next is the computation we aim to measure, so the signatures should respond to it rather than be invariant to it.

What is assumed concerns the decision. We assume that the subspace spanned by the readout directions of the top token and its competitors captures the part of the state that carries the current decision, and that hallucination leaves a trace in how the state moves within it. This is not proved, and we now state it explicitly as an assumption. We test it by removing the construction steps that rely on it (Table 3). Fixing a single subspace for all depths (w/o Moving subspace) lowers detection AUROC in all 10 cells, by 6.0 points on average, and removing the orthogonal transport (w/o Transport) lowers it in 9 of 10 cells, by 4.4 points on average.

DatasetBase LLMFullw/o TransportΔ\Deltaw/o Moving subspaceΔ\Delta
HaluEval QAQwen2.576.572.4−4.1-4.170.2−6.3-6.3
Gemma266.761.0−5.7-5.758.4−8.3-8.3
Phi-367.662.3−5.3-5.358.7−8.9-8.9
LLaMA365.764.4−1.3-1.363.4−2.3-2.3
Mistral61.759.3−2.4-2.459.0−2.7-2.7
HaluEval GeneralQwen2.569.858.6−11.2-11.258.9−10.9-10.9
Gemma265.1760.8−4.4-4.460.6−4.6-4.6
Phi-365.7966.4+0.6+0.659.4−6.4-6.4
LLaMA367.0764.2−2.9-2.963.8−3.3-3.3
Mistral67.0160.1−6.9-6.960.6−6.4-6.4
Mean−4.4\mathbf{-4.4}−6.0\mathbf{-6.0}

These changes are reflected in the revised paper. In the Introduction (third paragraph), we replaced "the decision and not the instrument" with the two parts above: invariance to the measurement is proved, and relevance to the decision is an empirical claim. The opening of Section 3 now states invariance to the choice of basis within the scope of Lemma 2, and the scope paragraph after Lemma 2 lists the implementation choices that the lemma does not cover. Table 3 now covers HaluEval General and the three construction ablations, from which the excerpt above is taken, and the "Feature group ablation" paragraph reports these results. The new Appendix F also lists, in one table, which statements are proved and which are empirical claims.

AuthorsOpenReview ↗

Question 2

We thank the reviewer for this question, which goes to the heart of how the event scores should be read. The method aims to find a useful place to correct the generation, not where the error started, and we have made this explicit in the revision. You are right that the two can differ. The validator is trained with response-level labels, and the GRU carries information from earlier events, so the score at an event reflects the trajectory up to that point. The highest score therefore marks where the evidence for hallucination peaks, which may come after the error first appeared. We now describe this event as an intervention site rather than an error source, in the Introduction (first and third paragraphs), in the overview of the method section, and in "Signature-guided single-block refinement," where the term "culprit" is replaced by "intervention site."

We also tested whether intervening earlier helps. On TriviaQA and HaluEval QA for all five models, we compare the default rule (Argmax), which intervenes at the highest-scoring valid event, with an earliest rule (Earliest), which rolls back to the first valid event whose score exceeds the validator's decision threshold of 0.5. Both use the same flagged responses, the same single-block clamp, and the same judge. The earliest rule gives a lower hallucination ratio in 3 of 10 cells, which confirms that some errors start before the top event, but the argmax rule is lower in the other 7, and in 4 cells the earliest rule raises the ratio above its initial value. Early threshold crossings are often premature, so rolling back to them regenerates more of the answer and intervenes before the evidence for the error has formed. We added this comparison as Appendix E.1 (Table 5).

DatasetRuleQwen2.5Gemma2Phi-3LLaMA3Mistral
TriviaQABefore35.4833.2130.8033.7527.25
Earliest31.2626.6024.5434.2127.78
Argmax (Ours)33.7327.5020.5024.5022.25
HaluEval QABefore15.2514.9012.6515.1014.05
Earliest16.7013.355.4916.8013.79
Argmax (Ours)10.9512.346.557.7111.70

Hallucination ratio (%), lower is better. Bold marks the lowest ratio per column.

What we claim instead is that the selected site is effective for correction, and the controls you asked for support this. On the same flagged responses, with the same rollback position and decoding budget, the validator-selected block gives the lowest hallucination ratio in 33 of 40 cells against regeneration alone and against the same clamp on a random or fixed block (Table 2). Since all variants share the rollback position, this comparison isolates the choice of block.

AuthorsOpenReview ↗

Question 3

We thank the reviewer for suggesting this control, which we agree is the right test of the block choice. We added it to Table 2. On the same flagged responses, from the same rollback position, and with the same decoding budget, we apply the same clamp to a random block (Random layer) or to the middle block (Fixed layer), and we also regenerate without any intervention (Regen-only). Random and Fixed layer are compute matched to our correction, since each pays the same calibration, clamp, and regeneration cost and differs only in where it intervenes, and Regen-only pays the same regeneration cost without any intervention. The signature-guided clamp gives the lowest hallucination ratio in 33 of 40 cells, while the controls often raise the ratio above its initial value. The exceptions are mostly on SAMSum and xSUM.

On other correction methods at a similar cost, Regen-only is itself such a method. It spends the same regeneration budget from the same rollback position and corrects by resampling, yet it often raises the hallucination ratio above its initial value (e.g., BBH with Qwen2.5, 21.40 to 40.53), while our clamp lowers it. We therefore compare against alternatives that spend exactly the same budget and differ only in how and where they correct.

LLMMethodTriviaQAHaluEval QAHaluEval GeneralFELMxSUMSAMSumGSM8KBBH
Qwen2.5Before35.4815.2511.9637.4325.5921.7415.2121.40
Regen-only33.7513.8210.6529.6520.7824.7817.4140.53
Random layer31.7515.4612.8732.5621.9221.0918.3038.40
Fixed layer32.5014.2613.7625.4922.7620.0417.8626.28
Ours33.7310.958.7511.7021.6721.4314.6520.03
Gemma2Before33.2114.906.7632.2428.5410.257.6034.39
Regen-only30.5014.316.8927.6820.5119.1415.5337.23
Random layer34.0014.267.6725.3426.5614.2010.6742.28
Fixed layer30.5013.668.0028.3428.3312.6512.9141.23
Ours27.5012.345.7630.9224.126.526.8334.39
Phi-3Before30.8012.657.6431.7420.3316.1512.1727.37
Regen-only38.5011.4410.8646.2023.3215.1218.6327.30
Random layer36.0011.5410.5336.7824.9913.5817.1130.71
Fixed layer38.0010.4410.5325.6121.4917.2815.5931.90
Ours20.506.556.3113.4517.8314.6011.0322.11
LLaMA3Before33.7515.1013.0735.5624.2122.0519.7746.67
Regen-only39.2516.0014.2133.1431.3319.2125.8649.31
Random layer37.2515.3013.9834.1434.8320.6826.2449.65
Fixed layer40.0015.8513.8731.9833.0019.7525.8648.61
Ours24.507.7111.7431.5822.3318.8319.3945.61
MistralBefore27.2514.0510.8537.0824.8316.1547.9158.25
Regen-only35.7517.5712.6036.2029.8115.4957.7960.67
Random layer35.5015.7213.1544.4432.6917.2757.0361.36
Fixed layer35.0018.1713.2730.6134.6216.6557.4156.67
Ours22.2511.7010.1916.9621.3315.8434.6051.23

Hallucination ratio (%), lower is better. Bold marks the lowest ratio after regeneration per model and dataset.

Reviewer_wbCtOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper proposes Depthwise Trajectory Signatures for detecting and mitigating LLM hallucinations by analyzing hidden-state trajectories across transformer layers. The method constructs gauge-invariant geometric features through bias centering, depth-local subspaces, and orthogonal transport. A lightweight validator detects hallucinations and localizes anomalous token-layer positions, enabling targeted single-block refinement. Experiments across 12 benchmarks and 5 LLMs show superior detection AUROC in 45/60 settings and at least 10% relative hallucination reduction in 29/45 refinement settings.

Critical strengths
  1. The paper is clearly written and well-organized, making the overall methodology easy to follow.
  2. The authors conduct extensive experiments across 12 benchmarks and 5 LLMs.
  3. The proposed trajectory-based perspective is interesting and provides a useful alternative to conventional hallucination detection methods.
Critical weaknesses
  1. The experimental comparison misses several relevant hallucination detection methods, such as TSV [A], SAPLMA [B], and HaloScope [C]. It would also be helpful to discuss recent approaches such as HCPD [D], which detects hallucinations without accessing the model's internal states, to better clarify the advantages and limitations of the proposed method.
  2. If I understand correctly, Lemma 1 assumes that normalization is applied after each block's residual update. However, several evaluated models, such as LLaMA3 and Qwen2.5, use pre-norm architectures. In this case, the residual stream is not normalized after each block, so I wonder whether the shell bound in Lemma 1 still holds. Could the authors clarify this?
  3. I have some concerns about the gauge-invariance claim in Lemma 2. When the weak-overlap fallback in Appendix B.3 is triggered, setting the transport matrix to identity seems to break the invariance. For example, in the 1D case, if pb=pb+1=1p_b=p_{b+1}=1 and R=1R=1, then ∣Δp∣=0|\Delta p|=0. However, flipping the basis sign in the second window gives pb+1′=−1p_{b+1}'=-1, while R′=1R'=1, resulting in ∣Δp′∣=2|\Delta p'|=2. Also, the coordinate-wise median used in Appendix B.4 is not rotation-equivariant. Could the authors clarify whether Lemma 2 still holds under these implementation choices?
  4. The validator is trained only with response-level hallucination labels, but the paper uses the resulting event-level scores to localize hallucinations at specific tokens and layers. I am not sure why these scores can be interpreted as reliable token- or layer-level hallucination indicators without any corresponding supervision. Could the authors provide more justification or experimental evidence for this localization assumption?
  5. What if the hallucination originates at an earlier token, while a later event receives a higher anomaly score? Since the method only regenerates the suffix from the selected position, the original error may already be part of the fixed prefix and cannot be corrected. It would be helpful to compare the current argmax strategy with interventions at earlier high-scoring events to better justify the localization strategy.
  6. It would be helpful to include a few examples showing which tokens and layers are assigned high anomaly scores, and how the generated responses change before and after refinement. This would make the proposed localization and refinement mechanisms more interpretable.

Reference

[A] Steer LLM Latents for Hallucination Detection, ICML 2025.

[B] The Internal State of an LLM Knows When It's Lying, EMNLP Findings 2023.

[C] HaloScope: Harnessing Unlabeled LLM Generations for Hallucination Detection, NeurIPS 2024.

[D] Zero-source LLM Hallucination Detection with Human-like Criteria Probing, ICML 2026.

Questions for authors

NA

6 comments
AuthorsOpenReview ↗

Weakness 1

We thank the reviewer for pointing us to HCPD, and we added it to the Related Work paragraph on post-hoc detection. HCPD judges hallucination from the query and answer text alone, with a fine-tuned 7B judge that scores weighted criteria over several samples. Because it needs no access to the generator, it applies to closed API models and transfers across target models. In exchange, it requires a second model at inference and returns a sample-level verdict only after the answer is complete. Our approach makes the opposite trade. It needs open weights and a validator trained per base model, but it adds no second model, reads the generator's own internal states, and returns a token and block at which to intervene, which is what makes single-block refinement possible. We therefore see the two as complementary, a zero-source judge for black-box auditing and an internal monitor for open models that also supplies a site for correction.

Missing baselines (TSV, SAPLMA, HaloScope).

Thank you for pointing out these methods. We added SAPLMA [B] to Table 1, together with ICR Probe (Zhang et al., ACL 2025), another layer-wise internal-state detector. Both are trained on the same training split as our validator, and Table 1 now compares against seven baselines on all 60 model and dataset combinations. Among the three methods you list, we prioritized SAPLMA because the comparison in HCPD [D] ranks it above TSV and HaloScope on both of its backbones, with average AUROC 77.9977.99 / 79.4779.47 for SAPLMA, 74.8274.82 / 70.4970.49 for TSV, and 65.6865.68 / 63.1663.16 for HaloScope on LLaMA-3.1-8B / Qwen-3-8B.

The table below summarizes the updated Table 1 by base LLM, as the mean AUROC (%) over the twelve benchmarks.

Base LLMHalluShiftSAPLMAICR ProbeOurs
Qwen2.557.9062.1465.3267.50
Gemma259.2471.3964.6565.64
Phi-356.2760.7463.6264.37
LLaMA356.2662.9065.2266.32
Mistral58.5963.0963.4364.41
All57.6664.0564.4565.65

Our validator attains the best AUROC in 36 of 60 combinations and the highest mean AUROC over all of them. The two supervised probes are the strongest baselines, and SAPLMA leads on Gemma2, mainly on CoQA, NQ, TruthfulQA, HaluEval QA, and FELM. By category, our validator has the highest mean on QA (67.2067.20), summarization (61.8661.86), and reasoning (66.1666.16), and SAPLMA on general-domain factuality (66.9766.97 against our 64.2864.28). Beyond the score itself, our validator scores every token and block, which provides the intervention site for refinement (Table 2). A sample-level probe such as SAPLMA returns only a verdict.

Revisions. Table 1 adds SAPLMA and ICR Probe for every base LLM. The baseline list in §4 and the detection numbers in the Abstract, Introduction, §4.1, Discussion, and Conclusion are updated accordingly.

AuthorsOpenReview ↗

Weakness 2

We thank the reviewer for this careful question, and we are glad to clarify. Lemma 1 holds for the pre-norm models we evaluate, because it bounds the state we read, not the residual stream. We read ht,bh_{t,b} at the output of the normalization the model applies at each boundary, which in pre-norm models such as LLaMA3 and Qwen2.5 is the input normalization of the next block. The proof uses only h~t,b=ΓbS(ut,b)\tilde h_{t,b} = \Gamma_b \mathcal{S}(u_{t,b}), where ut,bu_{t,b} is whatever enters that normalization. Since S\mathcal{S} divides its input by its own scale, the bound does not depend on how ut,bu_{t,b} was produced. In a pre-norm model ut,bu_{t,b} is the unnormalized residual, whose norm can grow with depth, but the normalized output stays inside the shell.

We agree that the original text invited the reading you describe, since it called ht,bh_{t,b} the residual-stream state and wrote the update in post-norm form.

Revision. In §3.1 we now define ht,bh_{t,b} as the normalized state read at the output of the boundary normalization, and denote the residual entering block bb by hˉt,b\bar h_{t,b}, which equals ht,bh_{t,b} in post-norm blocks and the unnormalized residual stream in pre-norm blocks.

AuthorsOpenReview ↗

Weakness 3

We thank the reviewer for checking the claim against a concrete example. It exposed an error in our description of the implementation, not in the computation behind the reported results, and we have corrected the text.

Identity fallback. Appendix B.3 described a stabilization rule that replaces the transport by the identity when adjacent windows overlap weakly. This rule is not part of the implementation used for any reported result, and the description was a mistake on our part. At every window boundary the code computes the transport as the orthogonal polar factor of Uj+1⊤UjU_{j+1}^\top U_j, with no replacement by the identity. The polar factor is unique whenever Uj+1⊤UjU_{j+1}^\top U_j is nonsingular, and under a basis change Uj↦UjQjU_j \mapsto U_j Q_j it transforms as R↦Qj+1⊤RQjR \mapsto Q_{j+1}^\top R Q_j, so it rotates together with the bases. In your 1D example, flipping the sign of the second basis gives Qj+1=−1Q_{j+1} = -1, so the transport becomes −1-1 rather than 11. Then ∣pb+1′−R′pb∣=∣−1−(−1)⋅1∣=0|p_{b+1}^{\prime} - R^{\prime} p_b| = |-1 - (-1)\cdot 1| = 0, the same as before the flip, and invariance holds. The counterexample is correct for the rule we described, which is exactly why that description was wrong for our method.

Median centering. You are right that the coordinate-wise median is not rotation-equivariant. The center enters only one of the ten signatures, the centered step length ∥Δpt,bc∥2\lVert\Delta p_{t,b}^{c}\rVert_2. The other nine do not involve it and are covered by Lemma 2 without condition. For the centered step, Lemma 2 states the condition explicitly: it is invariant when the center is rotation-equivariant, as the Euclidean mean is. We keep the median as a robust choice, and replacing it by the mean changes AUROC by less than 0.3%.

Revisions. (i) Appendix B.3 now describes the transport as implemented, the polar factor at every boundary with no identity fallback. (ii) The sentence in the proof of Lemma 2 that referred to the identity replacement is removed. (iii) The text introducing Lemma 2 now notes the condition on the center for the centered step. (iv) A new paragraph after Lemma 2 lists the implementation choices that bear on the guarantee and what each one covers.

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