acceptodds
Under review as a conference paper at ICLR 2027

PARALLAX: Automatic Layer Selection For Internal-State Hallucination Detection

Abstract

Large language models hallucinate with confidence, producing text that is fluent, authoritative, and wrong. In medicine and other high-stakes uses, that failure can cause direct harm. Detectors that read a model's own hidden activations promise to catch it before the text reaches a user, and they report high AUROC on standard benchmarks. Those performance numbers are fragile for two reasons. First, in three of the four corpora we study, the detector input already contains the candidate answer being judged, and a sentence-embedding classifier with no access to the model reaches 0.65 to 0.79 AUROC on them. Second, existing detectors are static because they read from a layer selected in advance, often the final layer. That layer is rarely the right one. Cross-validation inside the training data did not select it in any of our 1,000 training folds. The depth that works best also moves from one model to the next, although within a model it barely moves across corpora. PARALLAX searches every layer under cross-validation that never touches the test data, and selects the ones that score best. The effect is large. Across five open-weight models and four corpora, one selected layer beats last-layer probing on every one of those twenty model and corpus pairings, by as much as 0.117 AUROC. It carries to full scale. On the complete corpora, up to 15,090 examples and thirty times the data, it holds on all 100 held-out splits and the largest gain reaches 0.123 AUROC. PARALLAX has the highest AUROC of any detector that reads the model only once, on thirteen of the twenty tests. It keeps its advantage in 58 of 60 cross-corpus transfers, where it was tested on corpora it was not trained on. At a hundred labelled examples and below, it beats the strongest detector that scores tokens individually on every seed. This shows that choosing the layer, with no change to the classifier and no extra forward pass, is enough to put a plain linear probe ahead of every published detector that reads the model once. Which layer a detector reads is therefore a design decision worth making, not a constant fixed in advance.

Primary area:
alignment, fairness, safety, privacy, and societal considerations
Keywords:
hallucination detection, large language models, internal states, linear probing, layer selection, truthfulness, evaluation methodology, cross-corpus generalization

Reviews

Among:
Shape:
1234this paper, Bottom 9%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.50 over 4 reviews, above 9% of the others.
Reviewer_rKrhOpenReview ↗
Rating
2
Confidence
4
Informativeness
1
Presentation
2
Soundness
3
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Paper summary

The paper proposes PARALLAX, a supervised linear probe for hallucination detection that uses intermediate layers selected automatically rather than fixed in advance. Specifically, it scores the layers by inner 5-fold cross-validated AUROC on the training split only, selects one layer or a small set, and fits the probe there. Experiments across five open-weight models and four corpora are provided.

Critical strengths

The problem considered in this work is important. Internal-state probes are among the cheapest hallucination detectors available at deployment time, and which layer they read affects the performance a lot.

Critical weaknesses
  • A published, near-identically titled paper [1] on the same problem is not cited, discussed, or compared against. It studies exactly the problem this submission poses: automatically choosing the probe layer for hidden-state hallucination detection, across models and datasets. It seems the method proposed in this work is called validation loss there, as one of the baselines they explored but is shown to be less optimal than their proposed method. It would be helpful to provide a comparison with this work including detection performance, runtime etc.
  • The multi-layer (k>1) component is not justified by the results. Table 4 shows k=1 and the adaptive rule are indistinguishable on three of four corpora.
  • Three of the four corpora are not hallucination detection in the usual sense, and the fourth is not the probed model's text. In TruthfulQA, HaluBench and MedHallu the model is handed a candidate answer it did not write and the probe reads its states over that text; in RAGTruth the responses come from other LLMs. The task is therefore closer to supervised claim verification on supplied text than to detecting the model's own hallucinations, which is the setting of most of the cited baselines in this work.
  • The abstract's "first reason" is unclear and not acted upon. The TXTEMB result is about benchmark construction, not about detectors being fragile, yet it is presented as one of two reasons detector numbers are fragile and the proposed method is not shown to mitigate this issue.

[1] "Automatic Layer Selection for Hallucination Detection" Wang, Cao, Wilson, Zeng, ICML 2026.

Questions for authors
  • Can the authors provide a comparison with the related work mentioned above?
  • What is the recommended k? Given Table 4 and Table 13, is there any setting where you would advise a practitioner to use k>1, and how would they know in advance?
  • Can you report results on at least one setting where the probed model generates the scored text so the method is evaluated on the model's own hallucinations?
  • Does the selected layer change if pooling is switched from mean over the scored text to last-token or first-sentence-token? Does the "stable across corpora" finding survive that change?
Reviewer_GPA2OpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
3
Soundness
2
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Paper summary

This paper re-evaluated existing internal-state and uncertainty-based hallucination detectors under a teacher-forced protocol and introduced PARALLAX, which is an automatic layer selection method that uses greedy forward cross-validation on training folds to select layers for an L2L_2-regularized logistic probe. Experiments across several LLMs and benchmarks demonstrate that intermediate layer selection outperforms fixed last-layer probing and reveal that several existing benchmarks are heavily saturated by surface-level text artifacts.

Critical strengths
  1. This paper introduced a simple model-free sentence-embedding baseline that exposed severe surface-wording shortcuts and saturation in standard hallucination benchmarks, i.e., HaluBench and MedHallu.

  2. Experimental results across different models and corpora with nested 5-fold cross-validation and bootstrap intervals clearly show that optimal probing depth is a property of the model architecture rather than the dataset.

Critical weaknesses
  1. Limited algorithmic novelty in the overall approach, as PARALLAX simply applied standard greedy forward cross-validation to select layers for an existed logistic regression probe.

  2. The proposed multi-layer pairwise difference feature map ϕ(S)\phi(S) for k>1k > 1 offers no meaningful advantage over picking a single best layer, with Table 4 and Table 7 showing a median AUROC difference of −0.0001-0.0001 and 95% confidence intervals containing 0 in 15 of 20 settings.

  3. The re-evaluation protocol feeds static, externally prepared candidate answers into the probed LLM rather than scoring the model's own generations, which turns self-hallucination detection into external text verification and invalidates the paper's negative claims about sampling-based uncertainty.

  4. The performance gains of full layer search over SAPLMA's 5 preset depths largely vanish at full dataset scale, and PARALLAX underperforms the token-level baseline HaMI on RAGTruth at 400 labels as well as in 18 of 24 cross-corpus transfer settings.

  5. The experimental setup confounds model scale with quantization by running Llama-3.3-70B and DeepSeek-R1-32B in 4-bit NF4 while running the smaller models in bfloat16 without ablating the impact of quantization on layer representations.

Questions for authors
  1. How did PARALLAX compare to sampling-based uncertainty detectors and fixed-depth baselines when evaluated on responses generated directly by the probed model itself rather than teacher-forced external text?

  2. Why does the multi-layer feature representation ϕ(S)\phi(S) discard the raw activation vectors hℓh_\ell when k>1k > 1, and does retaining hℓ1h_{\ell_1} alongside the pairwise differences prevent the performance drop observed at k=2k = 2 on DeepSeek-R1-32B?

  3. As Appendix E.1 mentions, HaMI without sample weights is effectively a single-pass detector; why was HaMI omitted from the main five-model single-pass comparisons in Table 2 and the full-corpus experiments in Table 5?

  4. Have the authors validated whether 4-bit NF4 quantization shifts the optimal layer depth or degrades final-layer representations compared to bfloat16 on the same model?

  5. It would be helpful to see whether combining cross-validated layer selection with regularized token-level pooling can close the cross-corpus transfer gap with HaMI.

3 comments

On weakness 4 in all three parts, and Q3. Thank you for the two ablations and the HaMI comparison. HaMI scores every token and pools the top tenth with a learned head, where our probe reads one pooled vector per response.

W4, first part: gains over SAPLMA's five preset depths at full scale. Our four-corpus median gain is 0.0006. Across 20 model-corpus pairs at five seeds the mean is +0.0038, with 17 of 20 positive and a range of -0.0054 to +0.0197. At seed level that is 72 wins, 7 ties and 21 losses over 100 seeds. The median sits inside run-to-run variation from re-extracting the same activations, which moves our numbers by 0.0004 to 0.0088. Two of the four corpora saturate both selection rules, and on the two that do not the medians are +0.0102 on TruthfulQA and +0.0034 on RAGTruth (see our second reply to reviewer QTiD).

W4, second part: label budget and transfer. HaMI leads in 18 of 24 transfer settings, and 19 of 24 on a fresh re-extraction. On the label curve, our probe beats single-pass HaMI at 50, 100 and 200 labels and trails the stronger HaMI variant at 400. The combination your Q5 proposes closes much of the transfer gap (see our third reply).

On the label curve we ran RAGTruth at 50, 100 and 200 labels on Llama-3.3-70B and DeepSeek-R1-32B over ten paired seeds, with each method seeing only its label budget. We lead single-pass HaMI at all three budgets on both models, by +0.0097 to +0.0708, on 10 of 10 seeds in five of the six settings and 4 of 10 on DeepSeek-R1-32B at 200 labels. The margin peaks at 100 labels (+0.0708 and +0.0659) and drops at 200 (+0.0318 and +0.0097).

At 400 labels, the full training fold, the stronger HaMI variant leads by 0.013 on Llama-3.3-70B and 0.026 on DeepSeek-R1-32B under our adaptive rule, and by 0.029 and 0.023 at k=1. Our probe beats single-pass HaMI with 200 or fewer labels, and the stronger HaMI variant beats ours at 400. HaMI's token-level reader may help where the labelled span is a small part of a long response.

W4, third part: our own HaMI comparison, recounted. Both methods use the same 500 rows per corpus (499 on TruthfulQA) and the same five-fold splits for seeds 0 to 9. The table shows our score minus the better HaMI variant, using our adaptive rule:

modelTruthfulQAMedHalluRAGTruthHaluBenchHaluEval-QA
Llama-3.1-8B+0.0515+0.0033+0.0025+0.0220+0.0064
Qwen3-8B+0.0531+0.0054+0.0439+0.0099+0.0082
Phi-4+0.0183-0.0015-0.0289+0.0098+0.0073
DeepSeek-R1-32B+0.0231+0.0104-0.0255+0.0141+0.0076
Llama-3.3-70B+0.0363+0.0011-0.0130+0.0163+0.0034

Our submission reported 21 of 25 wins by counting any positive difference as a win. We now count a difference as a lead only when it exceeds 0.0088, the upper end of run-to-run variation. That is a descriptive band, not a test of equivalence, and it gives 12 leads, 3 losses and 10 differences inside the band. Each pair takes the better of the two HaMI variants where both ran.

At the k=1 we recommend, the comparison is worse for us. On RAGTruth the column becomes -0.018, +0.025, -0.036, -0.023 and -0.029, so HaMI leads on 4 of 5 there instead of 3. Two pairs change category over the full 25, and the count moves to 11 leads, 4 losses and 10 inside the band.

Q3: why HaMI is absent from Tables 2 and 5. Extraction cost. Full HaMI now runs on all 25 within-corpus pairs of the 500-row sets, and the single-pass variant on 17, where it is the better variant on 12. The cross-corpus transfer run covers two models (Llama-3.3-70B and DeepSeek-R1-32B). On the remaining 8 pairs only full HaMI ran, so for a third of the comparison we do not know which variant is stronger, and the caption states that.

Revision. We will report the per-corpus breakdown of the SAPLMA-5 comparison in Section 5. Section 6 will carry the HaMI comparison at both values of k with the band counts, the label curve at all four budgets, with the opponent at each budget stated, the transfer counts, and the RAGTruth losses.

On weakness 1 (novelty), Q2 and weakness 2 (the feature map our search hands the probe when it picks more than one layer), and weakness 3 (the protocol).

W1: algorithmic novelty. Greedy forward selection is standard, and the revision says so. The contribution is the measurement, which your second strength states: "optimal probing depth is a property of the model architecture rather than the dataset". We now report what it costs to reuse a depth. A depth imported from another corpus of the same model costs 0.0026 AUROC on average, and a depth imported from another model costs 0.0288 (see our first reply to reviewer 9M4a).

Q2/W2: the feature map. Keeping the raw activation does prevent the k=2 drop. Our map gives the probe the difference between the two chosen layers and nothing else, so it never sees either layer alone. With only a difference to read, the best-scoring layer pair is one with a large contrast, not a second informative layer. On DeepSeek-R1-32B and TruthfulQA the partner lands at layer 0, 1 or 3 of 64 on three of five seeds, while the first choice sits at 43 or 44.

Why the map discards the raw activation. We built it to describe how a representation drifts between two depths, and dropping the raw vector followed from that framing without a test against keeping it. The table below runs that test.

feature mapk=2 minus k=1, TruthfulQAk=2 minus k=1, RAGTruth
pairwise differences, as published-0.0036 to +0.0005-0.0084
raw activation kept alongside-0.0019 to +0.0025+0.0212
raw only, no differences-0.0016 to +0.0012+0.0180

On TruthfulQA no map makes k>1 worth anything, and the raw-kept gain of +0.0009 on DeepSeek-R1-32B is inside noise, so we do not call it an improvement.

The RAGTruth column is DeepSeek-R1-32B. On Llama-3.1-8B the published map is neutral at +0.0006 instead of -0.0084, while raw-kept gains +0.0186, so the direction replicates on a second model and the size of the harm does not. Measured against k=1, keeping the raw activation is worth +0.0212 and +0.0186 on the two models. Raw-only recovers it too, so the evidence supports keeping the raw activation, not pairwise differences specifically.

The map does not, on its own, explain why the adaptive rule fails on DeepSeek-R1-32B, because Llama-3.1-8B's adaptive rule works on RAGTruth under the same map, by +0.0200 on 10 of 10 seeds. We agree with your reading of the k>1 results (median -0.0001, intervals containing zero).

W3: the protocol. We have adopted external verification as the term for this setting. TruthfulQA, HaluBench and MedHallu supply the answer with the question, and RAGTruth supplies responses written by other models. The revision uses that term in the abstract, Section 3 and Limitations.

W3, second part: our negative claim about sampling methods. We withdraw the general form. Those methods resample the model's own answer, so scoring supplied text is the wrong setting for them. On the models' own generations, the three that need ten generations beat our probe on four of five models, and against SEPs we lead on three of five (see our second reply to reviewer 9M4a).

Revision. Section 3 will restate the contribution with the transfer table. Section 4 will recommend k=1 and report the feature-map ablation with all three maps, and Appendix C will carry the per-seed partner layers. We rename the setting throughout.

On weakness 5 and Q4 (quantization), Q1, and Q5 (selection combined with token-level pooling).

W5/Q4: quantization. We ran both directions, and the effect is model-specific. We compared DeepSeek-R1-32B in bfloat16 with its published 4-bit cache, and Llama-3.1-8B in 4-bit with its published bfloat16 cache, on the same rows and splits. Scores are means over five seeds, ± one standard deviation.

model and corpus4-bitbfloat16selected layers
DeepSeek-R1-32B, TruthfulQA, ours0.9463 ± 0.00320.9509 ± 0.003743,43,44,44,43 vs 43 x5
DeepSeek-R1-32B, TruthfulQA, last0.8636 ± 0.01610.8633 ± 0.0143-
Llama-3.1-8B, TruthfulQA, ours0.9020 ± 0.00780.9054 ± 0.010612,13,13,12,12 vs 12,13,12,12,12
Llama-3.1-8B, TruthfulQA, last0.7935 ± 0.01810.8008 ± 0.0162-

Q4, first half: does 4-bit shift the selected layer? Only slightly. Across the 20 seed comparisons on TruthfulQA and MedHallu, the layer does not move on 13, moves by one layer on 6, and by two on one.

Q4, second half: does 4-bit hurt the last layer most? On Llama-3.1-8B, yes: the last layer loses 0.007 AUROC on TruthfulQA where our layer loses 0.003. It does not hold on DeepSeek-R1-32B, where our layer loses 0.005 and the last layer is flat.

Effect on the published numbers. It is not uniform, and this check covers DeepSeek-R1-32B and Llama-3.1-8B. On Llama-3.1-8B, which the paper reports in bfloat16, 4-bit widens our margin by 0.004. On DeepSeek-R1-32B, which the paper reports at 4-bit, our margin is 0.005 narrower on TruthfulQA and 0.0005 wider on a MedHallu setting not shown above. Llama-3.3-70B needs about 140 GB in bfloat16, so we do not extend the claim to the paper as a whole.

Q1: the model's own responses against sampling detectors and fixed depths. Our selection beats the last layer there and mostly ties tuned presets, and the resampling detectors beat us. Our third reply to reviewer rKrh carries the fixed-depth table, and our second reply to reviewer 9M4a the sampling table.

Q5: selection combined with token-level pooling. A learned aggregator over our selected layer closes most of the transfer gap. A regularized token probe does not.

We followed your protocol, rebuilding our method and HaMI on one fresh extraction so that all four variants share the same activations and splits: 12 train-to-test corpus pairs on each of Llama-3.3-70B and DeepSeek-R1-32B, 10 seeds.

varianttrain-to-test pairs aheadseed winsmean gapworst pair
our submitted method, rebuilt5/2453/240-0.0423-0.1972
our selected layer, HaMI's learned head13/24104/240+0.0065-0.0352
our selected layer set, HaMI's learned head11/24113/240+0.0020-0.0230
our selected layer, top-decile probe1/2434/240-0.0555-0.1166

Reading our selected layer with HaMI's learned head turns a mean deficit of 0.0423 into a surplus of 0.0065, and improves the worst pair from -0.1972 to -0.0352. It closes 10 of the 19 train-to-test pairs where HaMI leads, and two we led move the other way, both trained on MedHallu. It replicates on both models, at +0.0090 and +0.0041. It is better on average and in more corpus pairs, but it still wins fewer than half the seeds, 104 of 240.

Our own regularized token probe does not recover the gap. Our selected layer read by a top-decile logistic probe scores -0.0555, below our pooled probe. The gap to HaMI therefore comes from how the layer is read, through its learned aggregator, and not from which layer is chosen. We have not isolated which part of that reader does the work.

Revision. We will report both quantization directions per model in Section 7 with the Llama-3.3-70B omission. Section 6 will add the HaMI coverage note and the Q5 table, and Limitations will state the extension Q5 implies, a learned reader over the selected layer.

Reviewer_9M4aOpenReview ↗
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1
Confidence
3
Informativeness
1
Presentation
2
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2
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Paper summary

This paper studies hallucination detection from an LLM's hidden states, particularly on selecting which layer a detector should read. The authors re-evaluate seventeen published detectors on the exact text their labels describe, together with a text-only control and propose PARALLAX, a linear probe whose layers are chosen per model and dataset by cross-validated AUROC on the training data. Across five models and four datasets, the selected layer outperforms last-layer probing in every setting, the selected depth lies in the middle of the network and varies across models but not across datasets, and the re-evaluation shows that several published detectors perform much worse than reported.

Critical strengths

The paper provides a systematic re-evaluation of existing hallucination detectors.

All detectors are scored on the exact text that the labels describe, every choice is made by nested cross-validation without access to the test data, and results are reported with paired wins over many seeds and at full dataset scale. The text-only control is useful, since it shows that two of the four datasets can largely be predicted from the wording of the candidate answer alone, and are therefore saturated for comparing detectors. This gives the community a clearer picture of which benchmarks can still separate methods.

Critical weaknesses

While the re-evaluation is valuable, I have concerns about the novelty of the proposed method, the evaluation setting, and the presentation.

The premise that existing detectors fix their layer in advance does not hold, and the proposed layer selection is close to existing practice. The paper motivates PARALLAX by stating that existing detectors are static because they read a layer selected in advance, and that the layer is a hyperparameter set in advance in all of these methods. Prior work, however, already evaluates layers and selects them on validation data. Orgad et al. (2025) [1] select the best token and layer for each dataset on a validation set, Zou et al. (2023) [2] choose the best layer on a validation set and use the middle layers for lie and hallucination detection because they show the strongest reading performance, Kossen et al. (2024) [3] report that their probes peak at intermediate layers, and Vazhentsev et al. (2026) [4] compare individual layers, middle layers, and all layers, and find that selecting the optimal single layer with supervision gives only a slight improvement over a fixed range of middle layers. The paper cites the first three works, but only as a steering method, a baseline, and a study of token-level signals, and does not discuss that they already read intermediate layers or select the layer per dataset. The fourth work is not cited.

Given this, it is unclear what PARALLAX contributes beyond standard practice. The method chooses the layer with the highest validation AUROC, which is standard hyperparameter tuning for probes, and framing it as automatic layer selection does not add to this. Consistent with this, the gains over the closest existing selection rule, SAPLMA with its five candidate depths, are small (on average 0.026 AUROC on RAGTruth and 0.009 on TruthfulQA, with ties on the other two datasets and a median gain of 0.0006 at full scale). The large gains reported in the abstract are over last-layer probing, which prior work already shows to be suboptimal.

The evaluation setting differs from the one the detectors are designed for. In all four datasets, the scored text is not generated by the probed model. Three datasets pair a question with a prepared correct or corrupted answer, and RAGTruth contains responses written by other LLMs. Methods such as semantic entropy, SEPs, and INSIDE measure how uncertain the model is about a question, and they are not designed to judge a supplied answer, so their near-chance results here are expected. The paper acknowledges this, but still concludes that published detectors are weaker than their reported numbers suggest. The same setting also leaves open whether the conclusions about PARALLAX hold for the model's own generations, which is the use case that motivates the paper.

The presentation needs considerable polishing. Several layout problems make the paper harder to read. Algorithm 1 is set in a narrow block with almost no spacing from the surrounding text, so it is difficult to read. Table captions and tables are placed too close to the text, and in Table 2 the caption runs into the top of the table. The bold paragraph headings mix a colon and a period as separators. The abstract and introduction are also dense with numbers, which hides the main message. These issues do not affect the results, but they suggest the manuscript was not carefully prepared.

[1] Orgad et al., "LLMs Know More Than They Show: On the Intrinsic Representation of LLM Hallucinations," ICLR 2025. [2] Zou et al., "Representation Engineering: A Top-Down Approach to AI Transparency," arXiv 2023. [3] Kossen et al., "Semantic Entropy Probes: Robust and Cheap Hallucination Detection in LLMs," arXiv 2024. [4] Vazhentsev et al., "Efficient Hallucination Detection for LLMs Using Uncertainty-Aware Attention Heads," ICML 2026.

Questions for authors
  1. (Relation to prior work) How does PARALLAX differ from selecting the layer per dataset on validation data, as done in prior probing work, beyond searching over all layers?

  2. (Model's own generations) How do PARALLAX and the sampling-based detectors perform when the scored text is generated by the probed model itself and then labeled?

1 comment

I thank the authors for the additional experiments and sincere and detailed responses.

In my review, I raised concerns about the premise and novelty of the method, the evaluation setting, and the presentation. The authors acknowledged that prior detectors already select the layer, added a comparison with the related works I suggested, and ran the sampling-based detectors on self-generated text.

However, I still have a concern about the novelty. Following these changes, the paper no longer presents layer selection as its contribution. The remaining contribution is the finding that the probing depth depends mainly on the model which is quite obvious. Also, the weakness I raised about the presentation was not addressed in the revised manuscript.

Regarding the gains over SAPLMA-5, the values in my review (0.026 on RAGTruth and 0.009 on TruthfulQA) are computed from the averages in Table 2, while the values in the res ponse correspond to the full corpus results in Table 5. Both show that the gains are small.

Overall, I will keep my score of 2.

Reviewer_QTiDOpenReview ↗
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Paper summary

The paper presents a n evaluation protocol for hidden-state detectors. Features are computed on exactly the text the label describes. A text-only control (logistic regression on MiniLM embeddings) shows that HaluBench and MedHallu are largely predictable from wording alone , and that supervised probes saturate on them. The authors rerun 17 published detectors. It also presents a method called PARALLAX that selects layers for a logistic probe by greedy forward selection on inner cross-validated AUROC. With more than one layer, it uses pairwise difference features. it is validated on 5 models and 4 datasets. It beats the last-layer probe in several settings.

Critical strengths

The evaluation is sound . The text-only control and the evidence that HaluBench and MedHallu are saturated tell which benchmarks can still separate methods. Rerunning 17 detectors under one protocol is useful. The experiments are broad. Five model families up to 70B, full-corpus replication on up to 15k examples, label-efficiency curves and cross-corpus transfer strongly support the narrow claim that selecting a layer beats a fixed one.

Critical weaknesses

Novelty is limited and the main baseline is a strawman. Cross-validated layer sweeps are routine in probing work (see these three: Orgad, Tegmark, Skean). The gains are against the last layer only. Against a coarse depth grid the gains are small and disappear at full scale. The pairwise multi-layer features do not add much. The task is mis-framed as the scored text was not generated by the probed model. RAGTruth uses responses from other LLMs. The task is thus truthfulness classification of supplied text with the LLM used as an encoder instead of detection of the model’s own hallucinations. The internal state premise is untested. the MiniLM control is too weak to rule out that any strong encoder would do as well.

Questions for authors

Does the same probe wghen trained on the same text but using a different model’s hidden states (or a fine-tuned NLI or cross-encoder classifier), match PARALLAX? If it does, then the model’s own internal state framing does not hold.

Does layer selection still matter in a setting where the probed model generates the scored answer, such as TriviaQA with the model’s own greedy outputs?

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

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