acceptodds
Under review as a conference paper at ICLR 2027

OpenHalDet: A Unified Benchmark for Hallucination Detection across Diverse Generation Scenarios

Abstract

Hallucination detection is essential for the reliable deployment of large language models (LLMs). However, existing evaluations face two core challenges: inconsistent inference configuration and evaluation, and limited coverage of downstream domains and tasks. Consequently, reported detector performance is often difficult to compare, reproduce, and generalize beyond specific experimental settings. We introduce *OpenHalDet*, a unified benchmark for hallucination detection across diverse generation scenarios. OpenHalDet standardizes the evaluation pipeline, from prompt construction and response generation to truthfulness annotation, detector scoring, and metric computation. It supports heterogeneous detector families under different access settings, including black-box methods that use only generated outputs, gray-box methods that rely on probability-based signals, and white-box methods that exploit internal model signals. By bringing diverse tasks, models, and detectors into a shared framework, OpenHalDet enables controlled comparison and provides a systematic view of how different detection paradigms behave in LLM applications. We release OpenHalDet as an open and extensible codebase to facilitate reproducible evaluation and future development of hallucination detection methods. The code and datasets are available at https://anonymous.4open.science/r/Hallucination-Detection-60C7.

Primary area:
datasets and benchmarks
Keywords:
Hallucination Detection, Large Language Models, Benchmarking, Model Reliability

Reviews

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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_cDmbOpenReview ↗
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1
Confidence
3
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2
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3
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Paper summary

This paper composes OpenHalDet, a unified benchmark for hallucination detection across various generation scenarios, including QA, RAG, Maths, Science, Code, Agentic and Multilingual tasks. OpenHalDet standardize a uniform task interface to adapt to differently-formatted datasets, implemented the evaluation pipeline, and conducted evaluation on Llama and Qwen3 families of models. The results provides a comprehensive view on the effectiveness of heterogenious hallucination detectors under diverse task modalities, along with insights on inference-time compute tradeoff across methods, and the contribution of labels or hidden states to detector performances.

Critical strengths

S1. The paper provides comprehensive testing across many dataset-model-detector triplets.
S2. The paper provides interesting (non-positive) insights on the effect of access to hidden states for hallucination detection.
S3. The paper publishes artifact that is potentially useful for evaluation of future works.

Critical weaknesses

W1. Hallucination is not clearly defined beyond in-context learning tasks (Context-based QA, summarization). Without context, hallucination reduces to wrong answer, and I doubt wrong-answer detection is aligned with the purpose of the tested methods.
W2. The hallucination label is generated with gpt-4o-mini without verification or correlation analysis. The reliance on gpt-4o-mini also increases the cost and reduces the feasibility of the proposed work to academic community.
W3. The inference-time cost tradeoff is analyzed without emphasis to detector modality (white/black box), which reduces the value of the analysis. Looking into the per-color cluster of dots in Figure 2, the result is not inspiring.

Questions for authors

Q1. How do you define hallucination without a context? How does the definition still fit in the setup of tested methods?
Q2. Is there any agreement between gpt-4o-mini and human annotation on hallucination?
Q3. Is there significant transformations, done by the proposed pipeline, on the curated data that is necessary to bridge the datasets and detectors of varying modality?

8 comments
AuthorsOpenReview ↗

Response to Reviewer cDmb (1/2)

Thank you for the detailed review and the concrete questions.

W1 / Q1: Definition of hallucination without context, and fit with the tested methods

Definition. Eq. (2) in our paper calls a response A\mathbf{A} truthful when A\mathbf{A} is semantically aligned with T∼PT∣Q(⋅∣Q)\mathbf{T}\sim\mathbb{P}_{T|Q}(\cdot \mid \mathbf{Q}), where Q\mathbf{Q} is the full input. If Q\mathbf{Q} has no context, a hallucination is a response that is not factually correct. If Q\mathbf{Q} has a context, a hallucination is a response that the context does not support. These are the two established categories, factuality and faithfulness (Huang et al., 2025). A wrong answer without context is therefore itself an established type of hallucination, a factuality hallucination.

Fit with the tested methods. Several of the detectors were evaluated on closed-book answer correctness in their own papers (Appendix B, Table 6). For example, Semantic Entropy and ICR Probe were evaluated on TriviaQA without context. Semantic Entropy was also evaluated on the math word problems of SVAMP. A benchmark of these detectors therefore has to cover this setting. On math, code and tool calling, OpenHalDet tests whether the same detectors still work, with task-specific correctness labels.

Results. Grounded datasets: the 7 datasets with a source passage or document in the prompt (SQuAD v2, HotpotQA, CoQA, HaluEval-QA, RAGTruth, XSum, Belebele). Ungrounded datasets: the other 10.

Family avg. AUROC, grounded / ungroundedQwen3-8BLlama-3.2-3BLlama-3.1-8BQwen3-14B
Black-box59.6 / 61.266.8 / 65.567.0 / 68.160.7 / 62.6
Gray-box62.4 / 66.267.2 / 66.066.8 / 68.563.0 / 66.7
White-box63.2 / 66.264.7 / 66.866.8 / 70.264.5 / 66.6
  • The averages are similar on both groups. For every family and every backbone, the grounded average and the ungrounded average differ by at most 3.8 AUROC points.

Changes in the paper. Section 2.1 states the two instantiations of Eq. (2). Table 1 marks the grounded datasets. New Table 19 reports all 17 implementations on both groups.

W2 / Q2: Label verification, agreement with human annotation, and cost

We verified the GPT-4o-mini labels on eight datasets against a second label source that does not use GPT-4o-mini (Llama-3.1-8B outputs).

DatasetSecond label sourcenAgreementCohen's κCorrect, but GPT-4o-mini says hallucinatedHallucinated, but GPT-4o-mini says correct
GSM8Kfinal-number exact match747398.9%0.950.2%0.8%
ARC-Challengeoption-letter match108994.6%0.825.1%0.3%
xLAM-Agentstructured tool-call match902788.9%0.713.2%7.9%
HumanEvalunit-test execution16476.8%0.5418.3%4.9%
MBPPunit-test execution37473.3%0.4924.3%2.4%
TriviaQAhuman, 100 balanced10096.0%0.92
CoQAhuman, 100 balanced, 1 ill-formed question excluded9973.7%0.47
XSumhuman, strict source-only, 100 balanced10049.0%−0.02
  • Verification: agreement is 89 to 99% (κ 0.71 to 0.95) on GSM8K, ARC-Challenge, xLAM-Agent and TriviaQA.
  • Agreement with human annotation (Q2). Agreement is 96.0% on TriviaQA, 73.7% on CoQA, and 49.0% on XSum. Reference quality helps explain the lower agreement. CoQA agreement rises to 85.9% after excluding 14 samples with incorrect or incomplete references. Maynez et al. (2020) found that 73.1% of the reference summaries for 500 sampled XSum articles contained information unsupported by the source. Removing XSum does not change the comparison between grounded and ungrounded datasets: the grounded averages move by at most 1.8 points.
  • Code (73 to 77%): GPT-4o-mini does not run the program, so we re-ran 16 detectors with labels from the datasets' unit tests (a program is correct only if it passes every test), for training and evaluation. Under these labels (Table 11), the gray-box family scores highest in three of the four settings, which agrees with our finding that hidden-state access alone does not guarantee better detection.
  • Cost: about 150 USD for 17 datasets on four backbones, paid once. The labeling model is a configuration option (--judge_model), so researchers can use a different model to label new generations.

Changes in the paper. New Appendix D.1 reports the label verification (Table 10) and the re-run of 16 detectors on code with unit-test labels (Table 11).

AuthorsOpenReview ↗

Response to Reviewer cDmb (2/2)

W3: Cost analysis without emphasis on detector access level (white/black box)

We added the access level to the cost analysis. Each cell gives the number of detectors, their cost per 100 examples and their AUROC (Llama-3.2-3B). A range covers all detectors in the cell.

Access levelNo extra generationOne extra generationFive extra generations
Black-box (4 detectors)0 detectors1 detector: 10.9 s, AUROC 583 detectors: 435 to 444 s, AUROC 77 to 79
Gray-box (5 detectors)1 detector: 4.5 s, AUROC 771 detector: 173.9 s, AUROC 753 detectors: 435 to 444 s, AUROC 64 to 85
White-box (8 detectors)6 detectors: 4.6 to 84.3 s, AUROC 53 to 690 detectors2 detectors: 434 to 453 s, AUROC 73
  • Cost depends on the number of extra generations, not on the access level. In every access level, a detector with five extra generations costs 434 to 453 s. A detector without extra generations costs under 85 s.
  • With the same number of extra generations, the access levels differ in accuracy. Without extra generations, gray-box Perplexity reaches 77 AUROC and the six white-box detectors reach 53 to 69. With five extra generations, the best gray-box detector reaches 85, the best black-box detector 79 and the best white-box detector 73.

Changes in the paper. The cost table (Table 25) now groups detectors by the number of extra generations and colors each row by access level. Table 26 summarizes cost by access level. Figure 2 is redrawn with the new SAR cost.

Q3: Transformations applied to curated data

Appendix C describes every step. In short, the pipeline does two things to connect datasets and detectors. Neither of the two changes the content of a dataset.

  • Datasets: one shared format (Appendix C.2, C.3). Each example keeps its original text and is stored in fixed fields: instruction, context, question, task-specific items (answer options, tool specifications or test cases) and reference answers. The task type only decides which fields go into the prompt.
  • Detectors: saved model signals (Appendix C.4). For each prompt we generate the response once. We save the response, the token probabilities, the hidden states and five extra samples. Each detector reads the cached signals it needs within its access level. All detectors are evaluated on the same primary responses, labels, and splits. No dataset is changed to fit a detector.

Dear Reviewer,

We would be grateful if you could let us know whether our responses address your concerns. For W1, we gave the two definitions of hallucination used in the literature and reported grounded and ungrounded datasets separately. For W2, we verified the GPT-4o-mini labels against exact matching, unit tests, and human annotation across eight datasets, with 89 to 99% agreement on GSM8K, ARC-Challenge, xLAM-Agent and TriviaQA. For W3, we added the cost breakdown by access level. If any point remains open, we would be very glad to clarify before the discussion closes.

Reviewer_nT5ZOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper introduces OpenHalDet, a unified benchmark for hallucination detection across diverse generation scenarios. The framework integrates 17 datasets and 16 method families, comprising 17 evaluated implementations, spanning black-box, gray-box, and white-box detectors. It provides a systematic evaluation on four main LLM backbones. The authors standardize prompt construction, response generation, annotation, detector scoring, and metric computation to improve comparability and reproducibility across methods.

The experiments highlight three findings: detector rankings vary across backbones; access to internal model states does not necessarily improve detection, and supervision is particularly important for some white-box methods; and methods that require multiple sampled responses incur substantial computational costs without consistent performance gains.

Critical strengths

S1. The paper is well motivated, and the unified evaluation framework has practical value.

Existing hallucination detection studies differ considerably in their models, tasks, evaluation protocols, and access to model information, making their results difficult to compare directly. The paper addresses this practical problem by integrating different types of detectors into a common evaluation pipeline and providing a modular, extensible codebase. This reduces the effort required to compare and reproduce methods and provides a useful resource for subsequent hallucination detection research.

S2. The systematic analysis across models, tasks, and detection paradigms provides useful empirical context.

Beyond comparing overall detection performance, the paper examines changes in detector rankings across backbones and tasks, as well as the effects of supervision and computational cost. These analyses help characterize the applicability and limitations of different detectors under the evaluated settings and inform subsequent method selection and evaluation design.

Critical weaknesses

W1. The substantive contribution over existing hallucination detection benchmarks is limited.

The unified evaluation of hallucination detection and uncertainty estimation methods has already received considerable attention. For example, LM-Polygraph (Vashurin et al., TACL 2025) provides a unified framework for evaluating uncertainty estimation methods, while HalluMix (Emery et al., 2025) evaluates hallucination detection across domains and tasks.

Relative to these works, the paper primarily expands the datasets, detector families, and software interfaces covered by the benchmark, particularly by incorporating more white-box detectors into a common pipeline. These extensions have practical value, but the paper does not sufficiently explain which unresolved core research questions it addresses or which important capabilities it provides that existing evaluation frameworks cannot offer. I therefore find the substantive contribution insufficiently distinctive.

W2. The main empirical findings offer limited novelty and depth.

The paper presents three empirical findings as a major contribution, but these phenomena have already been discussed to varying degrees in prior work. Differences in detector performance across tasks and models, the dependence of internal-representation methods on training and supervision, and the computational cost of multiple sampled responses are not new observations.Quantifying these phenomena under a broader, unified evaluation setting is useful. However, the analysis largely remains descriptive and comparative, without further investigation into the causes of the observed performance differences.

For example, the paper observes that label-free white-box methods underperform gray-box methods on average. However, this comparison is also affected by the particular methods selected, their feature construction, and their supervision conditions, so it is insufficient to support general conclusions about the detection paradigms. Similarly, changes in cross-backbone rank correlations demonstrate that method performance depends on the evaluation setting, but do not identify the key factors underlying these differences. Thus, despite the breadth of the experiments, the paper does not provide sufficiently novel or in-depth insights beyond prior work to establish a stronger research contribution.

Questions for authors

Q1. What is OpenHalDet's most important contribution that existing benchmarks such as LM-Polygraph and HalluMix cannot offer? Beyond expanding the datasets, detectors, and unified software interfaces, does the paper address a key question that existing frameworks cannot effectively investigate, or introduce a substantively new evaluation capability?

Q2. Could the authors clarify the novelty of the three main insights relative to prior work? Specifically, which conclusions about unstable cross-backbone rankings, the dependence of white-box methods on supervision, and the trade-off between sampling cost and performance go beyond observations already made in the literature? What new research insights does this paper provide?

Q3. Could the authors further analyze the main factors behind the performance differences across detection paradigms? For example, does the weaker performance of label-free white-box methods primarily stem from limitations of internal representations, the design of the particular detection algorithms, or differences in training and supervision? To what extent do the current results support conclusions about the detection paradigms as a whole?

4 comments

Thank you for the careful review and specific questions!

W1 / Q1. Contribution over LM-Polygraph and HalluMix

OpenHalDet compares black-box, gray-box, and white-box detectors on the same generated responses with shared binary hallucination labels, including for code generation and tool calling. This comparison extends beyond the published evaluations of HalluMix and LM-Polygraph.

  • HalluMix evaluates external detectors on fixed (context, response) pairs without the generating model signals required by gray-box and white-box detectors.
  • LM-Polygraph uses PRR to measure the benefit of rejecting uncertain outputs in selective generation. Its detection AUROC results are limited to claim-level fact-checking, and its hidden-state methods comprise four density-based methods. Its evaluation scope excludes code generation and tool calling.

New capability. A single interface lets researchers compare a new detector with 17 existing implementations across 17 datasets and four backbones. The protocol uses shared responses, labels, splits, and cached signals, and measures detector runtime.

What this shows. This setup lets us test how detectors previously evaluated on closed-book QA perform on code generation and tool calling. Table 2 shows that the results depend on the task.

  • Tool calling. A white-box probe leads on every backbone, with 88 to 92 AUROC.
  • Code generation. The best mean AUROC across the two code datasets is below 78. The gray-box group averages higher than the white-box group on three of four backbones.

Changes in the paper. Section 3.4 specifies what the protocol holds fixed. Section 5 and the new Table 4 compare the three benchmarks.

W2 / Q2. Novelty and depth of the three findings

FindingReported beforeWhat OpenHalDet adds
Rankings vary across backbonesIndividual detectors are sensitive to the backboneHow much rankings shift. The gap between best and worst rank averages 5.8 positions for black-box detectors and 3.5 to 4.0 for the other groups. SAPLMA, MIND-Sup, and PRISM stay in the top five on every backbone.
Hidden-state access alone does not guarantee better detectionHidden states carry a truthfulness signalHow much performance the same features can support. EigenScore and CCS average 4 to 8 AUROC points below the gray-box group on each backbone. On Llama-3.1-8B, a supervised linear probe reaches 80.0 AUROC on the same features as HaloScope, which reaches 60.1 (see Q3).
Sampling adds substantial runtimeSampling costs moreThe measured trade-off between cost and performance. In our profiling, detectors using five extra generations take 434 to 453 s per 100 examples and score 64.4 to 84.8 AUROC. Single-pass Perplexity takes 4.5 s and scores 77.3 AUROC (Llama-3.2-3B, Table 25).

Changes in the paper. Section 4.2 adds the rank stability and probe results. Appendix G.1 (Table 22) lists all implementation ranks across the four backbones, and Appendix E.18 (Table 13) reports the probe comparison.

Q3. Do the gaps between detection paradigms stem from representations, algorithms, or supervision?

We trained a supervised linear probe on the same hidden-state features as HaloScope, using the paper’s train/validation/test splits. We evaluated it on nine datasets covering QA, summarization, math and tool calling (Table 13), on two backbones.

Mean AUROC across nine datasetsLlama-3.1-8BLlama-3.2-3B
Linear probe on the same hidden states80.080.1
HaloScope60.159.5
EigenScore63.264.6
MIND-Sup (MLP probe)79.178.0
Perplexity (gray-box)77.069.6
Datasets where the probe outperforms HaloScope9 / 99 / 9
  • Internal representations. The same features support about 20 points higher mean AUROC with the linear probe, which outperforms HaloScope on all nine datasets on both backbones. On Llama-3.1-8B, taking the best test AUROC across layers and pooling choices for each dataset raises the probe’s mean from 80.0 to 82.9.
  • Scoring methods. The linear probe’s mean AUROC is within 2.1 points of MIND-Sup on both backbones. MIND-Sup uses an MLP and a different hidden-state feature.
  • Training and supervision. The linear probe and MIND-Sup fit directly to the training labels and reach about 80 AUROC. HaloScope uses those labels to select its PCA and pseudo-label settings, then fits its classifier on pseudo-labels, and reaches about 60.

In our comparison with HaloScope, the gap comes from how the detector is trained and how it scores responses. Changing both while holding the hidden-state features fixed improves mean AUROC by about 20 points on both backbones.

These results apply to the evaluated implementations on the tested datasets and backbones.

Changes in the paper. Appendix E.18 (Table 13) reports the experiment, and Section 4.2 discusses the result.

Dear Reviewer,

We would be grateful if you could let us know whether our responses address your concerns. For W1 / Q1, we added a comparison with LM-Polygraph and HalluMix (Section 5, Table 4). For W2 / Q2, we stated for each finding what was reported before and what OpenHalDet adds. For Q3, a linear probe on the same hidden-state features as HaloScope reaches about 80 AUROC, compared with about 60 for HaloScope. If any point remains open, we would be very glad to clarify before the discussion closes!

Thanks for the detailed responses and additional experiments. The clarifications on the benchmark's contribution and the new results have addressed my main concerns. I appreciate the authors' efforts and will raise my rating to 3.

Thank you so much for taking the time to go through our response and the new experiments, and for confirming that your main concerns have been addressed! We really appreciate you raising the rating and your engagement throughout the discussion.

Reviewer_395kOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
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Paper summary

This paper introduces OpenHalDet, a shared evaluation system for hallucination detection across 17 datasets, four fully tested Llama/Qwen models, and 17 implementations from 16 method families. It uses common model outputs, cached signals, GPT-4o-mini labels, data splits, and AUROC scoring. The paper also studies ranking changes, statistical uncertainty, and runtime costs.

Critical strengths
  • The shared data format and cached model outputs address a real reproducibility problem and make comparisons across several tasks easier. Per-dataset results, alternative averaging rules, selected confidence intervals, and cost measurements provide useful context for the main rankings.

  • The appendices clearly describe changes to existing detectors, including the different training labels used by MIND-Sup and SEP-Sup.

Critical weaknesses
  • The benchmark mixes hallucination with general task errors. A wrong option, calculation mistake, or failed program does not necessarily involve fabricated facts.

  • Yet all tasks use GPT-4o-mini labels without checks against human review, code execution, or exact answers. The annotation examples explain the rules but do not measure their accuracy. Since these labels define both training and evaluation, their quality needs to be tested for each task.

Questions for authors

The runtime accounting needs clarification. Table 19 gives SAR and LN-Entropy the same five extra generations and 224.3 extra tokens, but Cost@100 is 5.1 s versus 435.3 s. It is unclear whether both include producing the cached samples.

3 comments

Thank you for the positive assessment and the clear questions!

W1: Hallucination mixed with general task errors

This question lets us clarify the scope of Eq. (2). It uses hallucination in the broad sense established in the literature, where a fabricated fact is only one of several types.

  • The established taxonomy is broader than fabrication. Huang et al. (2025) list fabrication as one type, next to factual inconsistency and logical inconsistency. An example of logical inconsistency is a final answer that does not follow from the reasoning steps. Eq. (2) covers all three types: a response A\mathbf{A} is a hallucination when A\mathbf{A} is not semantically aligned with a truthful response T∼PT∣Q(⋅∣Q)\mathbf{T}\sim\mathbb{P}_{T|Q}(\cdot \mid \mathbf{Q}). A wrong option, a wrong final number and a program that fails its tests are therefore hallucinations under Eq. (2).
  • Several of the detectors we test were evaluated on these tasks in their own papers. Self-evaluation (Kadavath et al., 2022) was evaluated on GSM8K (math) and HumanEval (code). Semantic Entropy (Farquhar et al., 2024) was evaluated on the math word problems of SVAMP (Appendix B, Table 6). A benchmark of these detectors therefore needs to cover these tasks.
  • Results on these tasks can be read separately. Table 2 reports math, science, code and tool calling in separate columns. Tables 14 to 17 report every dataset.

Changes in the paper. Section 2.1 now states how Eq. (2) applies to math, code and tool calling.

W2: Labels not checked against human review, code execution or exact answers

We checked the labels with all three. For eight datasets, we built a second set of labels without GPT-4o-mini and measured how often the GPT-4o-mini labels agree with it (Llama-3.1-8B outputs).

DatasetSecond label sourcenAgreementCohen's κCorrect, but GPT-4o-mini says hallucinatedHallucinated, but GPT-4o-mini says correct
GSM8Kfinal-number exact match747398.9%0.950.2%0.8%
ARC-Challengeoption-letter match108994.6%0.825.1%0.3%
xLAM-Agentstructured tool-call match902788.9%0.713.2%7.9%
HumanEvalunit-test execution16476.8%0.5418.3%4.9%
MBPPunit-test execution37473.3%0.4924.3%2.4%
TriviaQAhuman, 100 balanced10096.0%0.92
CoQAhuman, 100 balanced9973.7%0.47
XSumhuman, strict source-only, 100 balanced10049.0%−0.02
  • Reliable where an exact or human check is possible: 89 to 99% agreement on GSM8K, ARC-Challenge, xLAM-Agent and TriviaQA.
  • The lower agreement on CoQA (73.7%) and XSum (49.0%) comes mainly from the reference answers of the original datasets, not from the labeling protocol. CoQA reaches 85.9% without 14 samples whose reference is wrong or incomplete, and over 70% of XSum reference summaries contain content that is absent from the article (Maynez et al., 2020).
  • On code (73 to 77%), GPT-4o-mini does not run the program, so we re-ran 16 detectors with unit-test labels for both training and evaluation. In the new results (Table 11), the gray-box family scores highest in three of the four settings, consistent with our finding that hidden-state access alone does not guarantee better detection.

Changes in the paper. New Appendix D.1 reports the label verification (Table 10) and the re-run of 16 detectors on code with unit-test labels (Table 11). Removing XSum barely changes the grounded averages in Table 19 (at most 1.8 points).

Q1. Runtime accounting of SAR and LN-Entropy

Thank you for pointing this out. The pipeline generates and caches five samples once for all sampling-based detectors. LN-Entropy’s 435.3 s is almost entirely sampling time, with scoring taking only 0.03 ms per example. SAR’s original 5.1 s covered scoring alone. Adding the shared sampling time brings SAR’s Cost@100 to 440.4 s.

This strengthens our third finding. SAR was the only apparent exception in the submission. With consistent accounting, all eight sampling-based detectors take 434 to 453 s per 100 examples, roughly 100 times the runtime of single-pass likelihood detectors.

Changes in the paper. Table 25 (Table 19 in the submission) reports the shared sampling time and the revised SAR cost. Figure 2 reflects the revised cost.

Thank you for the thorough response and the additional experiments. The additional clarifications and explanations have addressed my concerns. I will maintain my positive rating of 3 (weak acceptance).

Thank you very much for reading our response and for confirming that it addressed your concerns! Your comments made our paper clearer and more complete. We really appreciate your support and your positive assessment of our work!

Comments on the paper

2 comments
AuthorsOpenReview ↗

General response to all reviewers and the AC

We thank the reviewers for their thoughtful comments. We responded to each concern raised in the three reviews with new experiments, additional analyses, or revisions to the manuscript. The table summarizes what we did and where the corresponding changes are in the revised manuscript. Our individual replies provide further details.

ReviewerConcernWhat we did and what we foundWhere in the revision
395kW1. Hallucination and general task errorsWe clarified how Eq. (2) applies to task correctness in math, code, and tool calling. We also identified prior studies that evaluated several of these methods against answer correctness on math or code tasks.Section 2.1, Appendix B
395k, cDmb395k W2 and cDmb W2 / Q2. Verification of GPT-4o-mini labelsWe checked labels on eight datasets using exact matching, unit tests, or human annotation. Agreement ranged from 88.9% to 98.9% on GSM8K, ARC-Challenge, xLAM-Agent, and TriviaQA. We re-evaluated 16 detector implementations on code using unit-test labels and retrained the supervised detectors on those labels.Appendix D.1, Tables 10 and 11
395kQ1. SAR runtimeWe included shared sampling in SAR's Cost@100. The revised total is 440.4 seconds, comprising 435.3 seconds for sampling and 5.1 seconds for scoring.Table 25, Figure 2
nT5ZW1 / Q1. Contribution over LM-Polygraph and HalluMixWe added a comparison with both benchmarks and clarified what OpenHalDet enables. It evaluates black-box, gray-box, and hidden-state detectors on the same generated responses with shared binary labels, including on code generation and tool calling.Section 5, Table 4
nT5ZW2 / Q2. Novelty and depth of the findingsWe quantified how detector rankings vary across backbones and added an experiment comparing a supervised linear probe with HaloScope on the same hidden-state features.Section 4.2, Appendices G.1 and E.18
nT5ZQ3. Sources of performance differencesWe trained a supervised linear probe on the same hidden states as HaloScope. On Llama-3.1-8B, it achieved 80.0 AUROC compared with 60.1 for HaloScope. It outperformed HaloScope on all nine evaluated datasets on both backbones.Appendix E.18, Table 13
cDmbW1 / Q1. Definition of hallucination without contextWe clarified how Eq. (2) applies to factuality in closed-book QA and faithfulness in tasks with source evidence. We reported results separately for the two subsets and found that their detector-group averages differ by at most 3.8 AUROC points.Section 2.1, Tables 1 and 19
cDmbW2. Labeling cost and reliance on GPT-4o-miniWe report a one-time labeling cost of about $150 for 17 datasets across four backbones and clarify that researchers can configure a different model to label new generations.Appendix D.1
cDmbW3. Cost analysis by access levelWe added a breakdown of runtime and AUROC by detector access level and number of additional response generations.Tables 25 and 26
cDmbQ3. Data transformationsWe clarified how the dataset adapters map the original task content into a shared format and how each detector scores the same primary responses using the cached signals it requires.Appendix C, Section 3.4

Changes in the revised PDF

New and revised text is shown in red.

Main text

  • Section 2.1 and Table 1 clarify the two applications of Eq. (2) and identify the seven grounded datasets.
  • Section 3.4 explains which parts of the evaluation protocol are held fixed across detectors.
  • Section 4.2 adds the rank-stability and linear-probe results and specifies that the findings describe the evaluated implementations.
  • Section 5 and Table 4 compare OpenHalDet with LM-Polygraph and HalluMix.
  • Figure 2 reflects the revised SAR runtime.
  • Sections 1 and 6 state that OpenHalDet is a shared resource and that a detector designed for inputs with context is not expected to report results on datasets without it.

Appendix and result tables

  • Appendix D.1 (Tables 10 and 11) reports label verification and the code re-evaluation using unit-test labels.
  • Appendix E.18 (Table 13) compares the supervised linear probe with HaloScope on the same hidden-state features on two backbones.
  • Table 19 reports results separately for the grounded and ungrounded datasets.
  • Appendix G.1 (Table 22) reports detector ranks across the four backbones.
  • Tables 25 and 26 report runtime by the number of additional generations and by access level.
  • Tables 2 and 16 contain updated results for HaloScope and SAPLMA on Llama-3.1-8B, as noted in the tables.

The added and updated results continue to support the paper's three main findings.

AuthorsOpenReview ↗

Update after the discussion

We sincerely thank all three reviewers for their time and for a discussion that made the paper clearer. Here is a short summary of where things stand.

Reviewers 395k and nT5Z have both confirmed that our responses addressed their concerns. We are grateful for their careful reading and their support.

Reviewer cDmb stayed in the discussion with us and made two points specific, which helped us a lot. We list them here together with what we did.

Point raisedWhat we didWhere
A context-based method might be asked to report results on the context-free tasksWe state that OpenHalDet is a shared resource, and that a detector designed for inputs with a context is not expected to report results on the datasets without one. Results with and without a context are already reported separately.Introduction and Conclusion, Table 19
Label reliability on CoQA and XSumThe paper marks the XSum labels as provisional. The release will include the exact-match and unit-test labels for GSM8K, ARC-Challenge, xLAM-Agent, HumanEval and MBPP next to the GPT-4o-mini labels, and will list the label agreement of each verified dataset.Appendix D.1, Table 10

We hope these changes answer the two points, and we remain happy to discuss anything further. Thank you all again!

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