acceptodds
Under review as a conference paper at ICLR 2027

FALD: Fine-grained Adaptive Latent Detection for LLM Hallucination

Abstract

Hallucination detection is essential for the reliable deployment of large language models, yet latent-space methods often treat all tokens uniformly during intervention and fix the readout at the final layer, which can dilute token-localized hallucination evidence and limit feature separability. We propose FALD, a fine-grained adaptive latent detection framework that addresses both limitations. FALD first learns a token-level probe—trained under multiple-instance weak supervision from sequence-level labels only—to identify hallucination-prone tokens and modulate latent intervention per token, so that the separator focuses on the most informative evidence. It further performs layer-wise probing to select the most hallucination-sensitive readout layer rather than assuming the final layer is optimal. By combining token-aware intervention with adaptive feature-layer readout while keeping the backbone frozen, FALD learns more discriminative latent representations. Across four QA benchmarks and three LLM families (LLaMA, Qwen, Mistral), FALD consistently outperforms the strongest latent baseline (TSV) by 2.7-7.6% AUROC, and surpasses multi-sample methods by >24% AUROC at a fraction of the inference cost, highlighting the value of fine-grained training signals and layer-adaptive readout.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Large language model, Hallucination detection, Factual consistency

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_4STAOpenReview ↗
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2
Confidence
3
Informativeness
2
Presentation
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Paper summary

This paper proposes FALD, a latent-space hallucination detection framework intended to address two limitations of existing internal-representation methods: uniform treatment of tokens during latent intervention and the use of a fixed, typically final, layer for hallucination readout. FALD introduces a token-level risk probe that assigns hallucination-risk scores to generated tokens and uses these scores to modulate the magnitude of a trainable latent intervention vector. The modified representations are then propagated through the frozen backbone, and a validation-selected intermediate layer is used to produce a sequence-level hallucination score.

A central claim is that the token-level probe can be learned using only sequence-level hallucination labels through multiple-instance learning (MIL), avoiding explicit token-level hallucination annotation. The framework additionally performs layer-wise probing to select a dataset-dependent feature extraction layer and separately tunes an insertion layer at which the risk-weighted latent vector is injected.

The empirical evaluation uses four QA datasets and three approximately 7-8B-parameter open-weight LLMs. FALD is compared against output-based uncertainty methods and several latent-space baselines, including HaloScope, SAPLMA, TSV, and HalluGuard. The paper reports that FALD achieves the highest AUROC in the main evaluation and includes component ablations, cross-dataset transfer, label-source checks, layer/insertion-position studies, and computational-cost analyses.

The overall concept is compelling, and the empirical results reported are promising. Nevertheless, I have some concerns regarding the specification of the core multiple-instance learning (MIL) procedure, the interpretation of inference cost, and the validity of several evaluation claims.

Critical strengths

The rationale that hallucination evidence may be localized to a small subset of generated tokens is well-founded. Uniform intervention across all tokens could dilute these signals, whereas FALD's risk-weighted intervention offers a principled approach to prioritizing potentially informative token representations.

The adaptive layer analysis is also useful. The reported performance varies meaningfully across layers, with intermediate representations often outperforming final-layer representations, supporting the broader point that fixed last-layer readout can be suboptimal.

The paper evaluates three model families and four datasets rather than restricting evaluation to a single backbone. It also includes component-wise ablations, cross-dataset transfer, insertion-layer and extraction-layer sensitivity, label-source comparisons, and comparisons against larger multi-sample budgets. For example, the authors report a human/GPT label agreement study on a subset of TruthfulQA and show that the relative FALD–TSV difference remains similar under alternative label sources. These analyses substantially enhance the empirical section compared to reporting only a single benchmark table.

Critical weaknesses
  1. This is my main concern. The paper claims that FALD requires only sequence-level labels, yet Eq. (2) trains the token probe with token-level labels yiy_i, and Eq. (3) again uses yiy_i to select the extraction layer. The subsequent prose invokes MIL and Soft Top-K but never gives the actual MIL loss that maps a sequence-level bag label into the optimization objective.

This distinction is fundamental to the paper's contribution. If pseudo-token labels are constructed, the process must be explicitly defined. Alternatively, if the probe is optimized using a bag-level aggregation of token scores, the aggregation method and loss function should be specified. If yiy_i merely replicates the sequence label for each token, the interpretation as hallucination-token localization is considerably weaker than currently suggested.

The appendix's reference to “token-level weak-supervision labels” and an approximately 15% default noise rate further suggests that an additional labeling/pseudo-labeling mechanism exists but is not described clearly.

  1. FALD computes token-level risk at an insertion layer, modifies the corresponding hidden states, propagates those modified states through subsequent transformer layers, and then reads out the detection score. The paper states that keeping backbone parameters frozen “preserves the original LLM generation behavior.”

However, freezing weights does not imply unchanged generation if hidden activations themselves are modified. If the intervention is applied during autoregressive generation, the downstream logits—and potentially subsequent generated tokens—can change. In that case, FALD is no longer purely detecting hallucinations in the originally generated answer.

Alternatively, if the response is generated first and the intervention is applied in a separate teacher-forced or replay pass over the completed response, then the original generation is preserved, but this appears to require additional backbone computation. That would conflict with the appendix claim that FALD uses “a single forward pass” and adds essentially no inference latency beyond a lightweight MLP.

The paper should explicitly detail the inference execution graph and report measured end-to-end detection latency. This clarification is particularly important given that inference efficiency is a central claim.

  1. The abstract and conclusion describe TSV as the “strongest latent baseline” and claim improvements of 2.7–7.6 AUROC. However, Table 2 shows that TSV is not consistently the strongest latent baseline. HalluGuard outperforms TSV in many model/dataset combinations. For example, on LLaMA-3.1-8B, HalluGuard scores 85.4 vs. TSV's 84.2 on TruthfulQA, 87.5 vs. 85.8 on SciQ, and 79.4 vs. 76.1 on NQ Open. On Mistral NQ Open, HalluGuard reaches 78.1 and FALD reaches 78.3, so the margin over the actual strongest listed latent baseline is only 0.2 AUROC.

Furthermore, the reported 2.7–7.6 AUROC improvement range does not encompass all three model families; for Qwen and Mistral, some gains relative to TSV are below 2.7. The paper should report improvements relative to the strongest baseline for each model and dataset pair, rather than uniformly referencing TSV as the strongest baseline.

This observation does not negate FALD's advantage in Table 2, but it significantly alters the magnitude of the claimed improvement.

  1. The paper emphasizes that FALD surpasses multi-sample approaches by more than 24 AUROC at a fraction of their inference cost. However, FALD is a trained detector utilizing approximately 2,000 labeled training examples per dataset, while several multi-sample baselines are zero-resource or unsupervised inference-time methods. Consequently, the substantial accuracy difference should not be interpreted primarily as an inference-efficiency advantage, as the methods differ significantly in supervision and access assumptions.

There is also ambiguity regarding the “zero-shot cross-dataset transfer” experiment. Table 5 indicates that models are trained on one dataset and evaluated on the other three, while elsewhere the method selects a different extraction layer for each dataset using validation AUROC. It is essential to clarify whether the extraction layer and insertion hyperparameters selected on the source dataset are held fixed during transfer. If target-domain validation labels are used to reselect LextractL_{\text{extract}}, the experiment does not constitute zero-shot transfer in the conventional sense.

Questions for authors
  1. What is the exact MIL training objective for the token-level probe? Eq. (2) requires token labels yiy_i, but the paper states that only sequence-level labels zz are available. Please provide the exact mathematical loss actually optimized, including the Soft Top-K aggregation/weighting mechanism and how positive and negative bags contribute. Similarly, how is Eq. (3) computed without token-level ground truth?

  2. What exactly happens at inference time? Is the risk-weighted latent intervention applied during the original autoregressive generation, or in a second forward pass over an already-generated answer? If it is applied during generation, does it change the generated output? If it is applied afterward, how is the “single forward pass / essentially unchanged latency” claim obtained? End-to-end latency measurements against TSV would be helpful.

  3. Why is TSV described as the strongest latent baseline? Table 2 shows HalluGuard outperforming TSV on many model/dataset combinations. Please report FALD's gain over the strongest baseline for each individual setting and revise the 2.7–7.6 AUROC headline accordingly.

  4. How is layer selection performed in the cross-dataset transfer experiment?
    When training on, e.g., TruthfulQA and testing on TriviaQA, SciQ, and NQ Open, are LextractL_{\text{extract}}, LinsertL_{\text{insert}}, Top-K, and all separator parameters selected exclusively using the TruthfulQA train/validation split? If target-domain validation data are used for any of these choices, the experiment should not be described as zero-shot transfer.

  5. Can the authors report variability across training seeds or confidence intervals for AUROC?
    The reported gains over the strongest baseline are relatively small in several settings, especially Mistral NQ Open. Repeated probe/separator training or bootstrap confidence intervals would help establish whether these differences are statistically reliable.

  6. Why are only GPT-4.1 positive labels re-checked and inconsistent cases discarded?
    The appendix states that samples labeled correct are re-evaluated in a second pass, but does not describe symmetric re-checking of negative labels. Please clarify the rationale and whether asymmetric filtering changes the class distribution or AUROC. It would also be useful to report results without discarding inconsistent examples.

Reviewer_8noWOpenReview ↗
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2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper introduces FALD, a method to detect hallucinations by learning a token-level risk probe and an intervention vector to separate hallucinated and truthful generations. The method has two phases: it first learns an MLP probe to localize hallucinated tokens via Multiple Instance Learning, then learns a vector to intervene LLM's hidden states with a weight determined by the MLP probe to make hallucinated and truthful generations more separable. The authors conduct experiments on four commonly used hallucination detection datasets and compare FALD against 9 baselines. The results show that FALD consistently outperforms baselines on response-level hallucination detection.

Critical strengths
  1. FALD is simple yet effective to detect hallucinated outputs.
  2. The authors conduct extensive experiments and ablations to justify the design choices.
  3. The paper is generally well written and easy to read.
Critical weaknesses
  1. The paper misses two critical ablations (removing the token-level probe or the intervention latent), making it hard to determine where the performance gain comes from.
    • FALD learns a token-level probe in the first phase. One natural ablation is to directly aggregate token-level risk probability as response-level hallucination prediction.
    • FALD learns an intervening latent in the second phase. One natural ablation is to set risk probability for all tokens to 1 and see how the intervening latent affects the performance of hallucination detection.
    • The authors seem to be performing a similar ablation on TSV, which is less straightforward.
  2. The effectiveness of the token-level probe is important, as it directly affects the intervention in the 2nd phase. However, it is only assessed by an experiment on TruthfulQA and a small-scale qualitative analysis, and is reported only in the appendix. It is necessary to conduct a larger-scale experiment and/or qualitative analysis in the main paper to understand whether the probe reflects hallucination risk, as the paper claims.
  3. Section 4.2 says that the design choice of FALD "improves sensitivity to sparse hallucinations, variable-length sequences, and diverse reasoning patterns" (Line 273). However, the experiments are performed mainly on short-form QA without reasoning, which can not validate the above claim about variable-length sequences and diverse reasoning patterns.
Questions for authors
  1. It is unclear how adaptive layer selection and token-level probing are integrated into TSV (Lines 349-353). Could the authors provide more details on the experimental setup?
  2. What's the optimal α\alpha learnt after training?
  3. Can FALD be used to detect hallucinations generated by closed-source LLMs? For example, using LLaMA-3.1 to encode answers generated by GPT-5.
  4. How much data is required to train FALD? TSV is trained only with 32 labeled data points. It would be interesting to see if FALD can achieve good performance with less data.
  5. Swapping Tables 1 and 2 can increase readability.
  6. Figure 5 is too small.
Reviewer_mxfVOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper proposes FALD, a hallucination detector that builds on TSV (Park et al., 2025). TSV adds one trainable vector to the hidden states of all tokens and reads out a separator score. FALD makes two changes. First, it trains a token-level MLP probe from sequence-level labels using multiple-instance learning with a Soft Top-K objective, and uses the probe’s per-token risk score to scale how much of the trainable vector each token receives at an early-middle insertion layer (around layer 9). Second, it picks the readout layer by validation AUROC instead of fixing it to the final layer, then mean-pools the intervened representations at that layer and applies a linear head. The backbone stays frozen. Across four QA datasets (TruthfulQA, TriviaQA, SciQ, NQ Open) and three LLMs (LLaMA-3.1-8B, Qwen-2.5-7B, Mistral-7B), FALD reports AUROC gains of 1.7–7.6 points over TSV and more than 20 points over multi-sample methods. The authors also report a component ablation, cross-dataset transfer, a label-reliability check, and a separability analysis.

Critical strengths
  1. Weighting the intervention by per-token risk is a reasonable extension of TSV, since hallucinated content in free-form answers tends to be sparse.
  2. The method runs in a single forward pass, keeps the backbone frozen, and adds little inference cost.
  3. The authors include several useful extras: a component ablation, cross-dataset transfer, a human-agreement check on the GPT-4.1 labels, and sensitivity sweeps for Top-K and the insertion layer.
Critical weaknesses
  1. The dataset sizes don’t add up. Table 3 lists 2,000/300/400 train/validation/test questions for every dataset, including TruthfulQA. TruthfulQA only has 817 questions. Either the description is wrong or the authors built the data in some way they don’t explain, such as counting multiple generations per question. Either way, I can’t tell what the TruthfulQA numbers actually measure, and if the same questions appear across splits, the results would be inflated.

  2. Table 5 computes the “drop” inconsistently, in a way that favors FALD. For FALD, the drop always equals the target dataset’s in-domain AUROC minus the transferred AUROC. For several baselines, the authors subtract from the source dataset’s in-domain score instead. In the SciQ->NQ column, TSV’s ↓25.3 equals 85.8 − 60.5 (source SciQ), HalluGuard’s ↓22.5 equals 87.5 − 65.0, and SAPLMA’s ↓28.8 equals 77.3 − 48.5. FALD’s ↓13.6 equals 83.7 − 70.1, which uses the target NQ score. The HaloScope rows in the TruthfulQA block have the same problem: ↓14.8 equals 70.6 − 55.8 rather than 76.2 − 55.8 = 20.4. The claim that FALD degrades least rests partly on this mismatch. The caption also says FALD wins “in every setting,” while the appendix text says “the vast majority.”

  3. I’m not convinced the baselines run under the same setting as FALD. The LLaMA numbers for TSV and the uncertainty baselines appear to match those reported in the TSV paper, which used a small labeled exemplar set plus unlabeled data. FALD trains on 2,000 labeled examples per dataset. The main text even says FALD reaches its results “with a small exemplar set, demonstrating label efficiency compared with fully supervised methods such as SAPLMA,” which contradicts the setup in Section 5.1. If the baselines saw far fewer labels, the comparison isn’t fair. The authors should state clearly whether they re-ran every baseline with the same 2,000 labels, splits, and GPT-4.1 judge.

  4. The method description contradicts itself in several places.

  • Eq. 2 trains the probe with token-level labels, but the next paragraph says no token labels exist and the probe learns via MIL.
  • Eq. 3 selects the extraction layer by token-level AUROC using those same nonexistent labels. Section 5.1 instead says the selection uses the last token’s hidden state. Figure 5 shows the probe peaking at layer 14 and says this “justifies our choice,” yet Table 6 picks layer 16 for TruthfulQA.
  • The authors select the readout layer offline, before any intervention, but then read out the intervened representations, so the selection criterion doesn’t match what the detector uses.
  • The label-noise study says MIL supervision has “∼15% noise,” but MIL doesn’t produce fixed token labels and the paper has no token-level ground truth, so I don’t know where that number comes from.
  • The AUROC formula in Appendix C averages a per-sample function, which isn’t how AUROC works.
  • The label quality control re-checks only positive (“correct”) labels and drops any that disagree. This one-sided filtering can make the test set easier.
  1. The key baselines are missing, and the mechanistic claim is circular. FALD stacks a supervised token-level MLP on top of TSV, so the gain could simply come from extra supervised capacity. I’d want to see at least two simpler baselines: (a) the probe’s own Top-K risk score used directly as the response score, and (b) a linear probe on mean-pooled states at the selected layer. Figure 6 shows that separability rises after the intervention, but the authors train v with a classification loss, so that’s expected and doesn’t explain anything about the mechanism. The paper also reports no seeds, variances, or confidence intervals, while FALD’s lead over HalluGuard is under 2 points in many cells (e.g., 78.3 vs. 78.1 on Mistral/NQ Open).
Questions for authors
  1. How did you obtain 2,700 TruthfulQA questions when the dataset has 817? Do any questions appear in more than one split?
  2. Did you re-run all baselines with the same 2,000 labeled training examples, splits, and GPT-4.1 labels, or did you take any numbers from prior papers?
  3. How does FALD compare with (a) the probe’s Top-K risk score used directly and (b) a linear probe on mean-pooled states at the selected layer, averaged over several seeds?

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

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