acceptodds
Under review as a conference paper at ICLR 2027

Still Correct, Already at Risk: Pre-Onset Hallucination Forecasting in Vision–Language Models

Abstract

Existing approaches primarily predict hallucination risk in vision–language models (VLMs) before generation or detect local errors during decoding. We study the forecasting opportunity between these settings: predicting future hallucinations after generation has begun but while the output remains visually supported. We formalize this task as Pre-Onset Hallucination Forecasting: continuously predicting whether the remaining response will contain a hallucination using only currently available information. We find that still-supported generation provides predictive information beyond the generation-start state, enabling warnings several tokens before the first error, with gains that vary non-monotonically over the monitoring horizon. To study this predictive ability, we construct PreHallu, comprising approximately 85K generation trajectories and more than 180K unique continuations sampled from supported prefixes, enabling systematic study of hallucination onset and alternative futures. We further introduce RiskTrace, which combines current multimodal evidence with observed decoding history for continuous response-level early warning. Dynamic monitoring consistently outperforms generation-start prediction across InstructBLIP, LLaVA-NeXT, and Qwen3-VL. On InstructBLIP, using the same frozen scorer, dynamic monitoring raises response-level AUROC from 75.43% to 83.58%. Matched-false-alarm comparisons and lead-time analyses further show that pre-onset forecasting improves future-hallucination prediction while providing a window for verification or intervention before the first unsupported token appears.

Primary area:
foundation or frontier models, including LLMs
Keywords:
Vision-Language Models, Hallucination Forecasting, Multimodal Hallucination, Pre-Onset Hallucination Forecasting

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_UT5XOpenReview ↗
Rating
2
Confidence
3(+1)
Informativeness
2
Presentation
2
Soundness
3
Read review
Paper summary

This paper studies whether future hallucinations in VLM responses can be predicted before the first unsupported token is emitted. It defines a response-level false-alarm protocol, constructs PREHALLU with onset-annotated trajectories and prefix-conditioned continuations, and introduces trained risk predictors under the RISKTRACE framework. Experiments report improvements over initial prediction across distinct models, together with warning lead times and alarm-triggered interventions.

Critical strengths
  1. Practically relevant task formulation. Early warnings enable targeted verification or correction, while response-level false-alarm accounting captures the cost of repeated monitoring.
  2. Useful experimental controls. Comparisons with initial prediction and optimized static baselines, together with lead-time analysis, frozen-threshold evaluation, and a future-information leakage audit, support the presence of additional predictive information during generation.
Critical weaknesses
  1. Unclear advantage over simpler dynamic predictors. Existing ablations support the value of historical information but do not establish the necessity of the full fusion design. Removing some gates does not reduce low-false-alarm recall, and a simple token-peak predictor outperforms the main dynamic implementation on this metric in some settings.
  2. Incomplete evaluation of practical warning value and cost. Predictors differ across backbones, and LLaVA additionally samples auxiliary continuations, introducing different evidence sources and computational budgets. Existing timing measurements do not cover the complete monitoring pipeline, while some Qwen3 warnings occur immediately before onset. Despite encouraging intervention results, warning coverage, available intervention time, and end-to-end cost still need to be assessed jointly.
Questions for authors
  1. Beyond existing ablations, could the authors compare against independently optimized per-prefix classifiers and fixed early-window baselines under matched information and compute budgets? Could they also shuffle or replace input histories before rescoring to test the value of historical content and order?
  2. Could the authors report end-to-end latency separately for passive and continuation-assisted monitoring and, with frozen thresholds, jointly report minimum-lead recall and the actual time required for scoring and intervention?
4 comments
AuthorsOpenReview ↗

Response to W1: Simple Dynamic Predictors and Component Ablations

W1. Comparison with simpler dynamic predictors and component ablations

Thank you for the careful review and for recognizing the value of pre-onset hallucination forecasting and the response-level false-alarm rate (FAR) protocol. We distinguish comparisons with independently trained predictors from ablations within the full model.

Comparison with simpler predictors. On the mixed Test set, Full-original, Per-prefix MLP, and Simple GRU achieve AUROCs of 59.58%, 53.98%, and 53.68%. With the same onset target and matched update budgets, Full improves over MLP and GRU by 5.60 and 5.91 percentage points (pp), with 95% CIs [+3.95,+7.26] and [+4.25,+7.56]. This supports better overall risk ranking in this setting; it does not imply superiority on every metric.

The Token-Peak result concerns a particular Qwen3 setting. Token-Peak retains the full network's visual, cross-layer, and GRU representations, but uses only the temporal maximum of the token-risk head. Full also incorporates the initial risk anchor and full risk aggregation. Their tradeoff is:

Qwen3 batchToken-Peak R@5Full R@5Token-Peak Lead>=5Full Lead>=5
Fresh29.49%21.66%4.15%10.60%
Fresh226.03%15.53%2.74%7.31%
Fresh322.60%16.83%1.68%6.49%

Here R@5 is recall under an empirically matched response-level FAR<=5% budget; Lead>=5 is coverage over all event responses. Token-Peak captures more events near onset, whereas Full has higher point estimates for earlier coverage. We do not claim significance for these lead-coverage differences or extrapolate this Qwen3 comparison to InstructBLIP or LLaVA.

With the same upstream signals and matched retraining, Full-control also improves R@5 over simple layer averaging by 6.91, 7.08, and 4.81 pp across the three Fresh batches. This supports learning how to organize cross-layer evidence, beyond merely supplying additional inputs.

Component roles. In the reported InstructBLIP ablation, Full achieves 83.58% AUROC. Removing Critical Attention, Champion-tail Protection, or all tail protection gives 81.34%, 81.37%, and 81.70%. The existing out-of-fold refit using only the actual-current component gives 80.42%. These results support complementary ranking information; they do not establish that every layer or submodule is individually indispensable.

Gate serves a different purpose: protecting the response-level false-alarm budget when auxiliary branches produce anomalously high scores. Under a stress test corrupting all four auxiliary branches, the same frozen threshold gives:

SettingClean FARDynamic event recall
With Gate6.53%51.16%
Without Gate18.11%56.29%

Gate reduces FAR by 11.58 pp, with a simultaneous 95% CI [+9.88,+13.28]. The higher recall without Gate accompanies more false alarms and cannot alone establish better prediction. After separately matching FAR<=5% under the same corruption:

SettingAUROCR@5Lead>=5 coverage
With Gate83.12%40.96%32.74%
Without Gate78.52%32.74%23.46%

This supports false-alarm protection and ranking robustness under auxiliary-branch failures. It is a controlled stress test, not evidence of universal gains on naturally shifted data. The full design therefore offers benefits in ranking, evidence organization, and earlier coverage, while simpler predictors remain competitive on some metrics.

AuthorsOpenReview ↗

Response to W2: Practical Value, Zero-Lead Interception, and Runtime

W2. Practical value, zero-lead interception, and runtime

We agree that practical value requires measuring coverage, executable interventions, answer quality, and total latency separately.

Quality and usable prefixes. In the reported intervention experiment, visual selection improves over the same-alarm reject-and-resample baseline, reducing Qwen3 CHAIRs from 10.175% to 9.775% on Fresh2 and from 9.875% to 9.475% on Fresh3, a 0.40 pp decrease in each case. On a separate fixed set of 200 inputs, original, alarm-time grounding, and post-hoc grounding give CHAIRs of 9.50%, 9.50%, and 10.00%; post-hoc grounding introduces one additional error. Alarm-time grounding generates 3.14 fewer tokens on average (paired 95% CI [-4.765,-1.850]). This supports prefix reuse and reduced generation, without establishing a significant quality or wall-clock improvement in that experiment.

At Development-frozen thresholds, coverage is:

Model / splitEvent recallActual FARLead>=5Lead>=10
InstructBLIP49.28%5.36%41.10%30.51%
Qwen3 Fresh17.05%2.64%5.53%5.07%
Qwen3 Fresh212.79%3.14%4.11%4.11%

Lead coverage uses all event responses as its denominator. These are separate backbone-specific populations and thresholds. Longer token lead provides earlier warning; the wall-clock opportunity also depends on generation speed, action cost, and scheduling.

Zero lead can still permit interception. Qwen3's median lead among successful alarms is zero. State t has consumed t answer tokens; the next token has zero-based index t. If the first error is at k and the alarm occurs at state k, L=k-k=0, yet that token has not been committed. Our synchronous controller computes the state, waits for the risk decision, and pauses on an alarm; otherwise, it commits the next token. Pausing preserves the correct prefix for grounding, abstention, resampling, or candidate selection before the error is exposed.

We tested 48 retrospectively stratified COCO images with ordinary decoding, monitoring only, and interception before token commitment: 144 real greedy decodes, with the model, three-seed detector, and Selection threshold frozen. Because new answers can differ from archived trajectories, a supplementary analysis relabeled all new answers after decoding using the same frozen CHAIR evaluator:

  • Ordinary and monitoring-only outputs were token-identical on 48/48 images.
  • Of 24 historical zero-lead cases, 22 again triggered at zero lead. All 22 withheld the first erroneous token; monitoring-only controls emitted that same token in 22/22 cases.
  • The other two cases did not alarm and were not intercepted.

The detector reads neither onset labels, candidate-token identity, nor future answers. The 22/22 result is conditional on triggered alarms, not population recall or corrected-answer accuracy. The original strict archive-matching analysis separately gives 9/9; we retain both analyses. Commitment was audited at the output callback.

Full runtime and acceleration. In this 48-image feasibility experiment, alarm computation averages 6.51 ms per state (P95 8.53 ms), and complete monitoring-only answers add 0.223 s on average. Each mode ran once per image on a shared server; shorter stopped outputs do not demonstrate faster complete answers.

A separate 200-input experiment used 20 warmups and three repetitions. Timing includes preprocessing, input transfer, generation, state capture, risk computation, updates, thresholding, and synchronization; it excludes disk reads and one-time model loading.

ModeMean E2EP90
Natural generation0.8179 s1.0160 s
Full passive monitoring1.1523 s1.3451 s

Overhead is 0.3344 s (40.9%); mean per-state monitoring is 7.789 ms. All 600 paired outputs are token-identical, and 3,452 legal states show no online-versus-cached alarm flips.

A separate 32-input evaluation includes corrective candidates, object checking, and selection:

ModeMean E2EP90
Natural generation1.5673 s2.0062 s
Serial full controller2.9541 s3.0637 s
Accelerated full controller1.7504 s2.2741 s

Our earlier work focused primarily on monitoring effectiveness, with limited efficiency optimization. This comparison demonstrates scope for acceleration: runtime falls 40.7% versus serial execution, with 183.1 ms (11.7%) overhead over natural generation. Only two inputs triggered correction, so this is engineering evidence, not a large-scale deployment estimate. In a separate small passive-pipeline experiment, token buffering, incremental scoring, CUDA Graphs, and detector heads on a second GPU reduce overhead from 22.1% to 4.35%. These timings use different settings and are reported separately.

AuthorsOpenReview ↗

Response to Q1: Prefix Classifiers, Early Windows, and History Interventions

Q1. Independent prefix classifiers, fixed early windows, and history interventions

Thank you for suggesting these comparisons. We have evaluated independently optimized Per-prefix MLP and Simple GRU predictors, fixed early-window models, and interventions on explicit history. These experiments address different aspects of dynamic observation. Here pp denotes percentage points, and R@5 is recall under a response-level FAR<=5% budget.

Independent classifiers and fixed windows. The original fixed-scorer observation-window analysis holds the alarm model unchanged and restricts the prefix range it can observe. Extending the range to K=20 gives 83.59% AUROC and 47.57% R@5. Thus, observing additional legal prefixes can improve prediction without retraining the scorer.

In the separate mixed Test comparison, Full-original, Per-prefix MLP, and Simple GRU achieve AUROCs of 59.58%, 53.98%, and 53.68%. Full's gains are 5.60 pp over MLP (95% CI [+3.95,+7.26]) and 5.91 pp over GRU ([+4.25,+7.56]). These AUROC comparisons do not imply significant R@5 gains.

We also trained fixed early-window models with the same future-event supervision:

ModelK=5 R@5K=10 R@5K=20 R@5
Per-prefix MLP9.98%9.52%6.76%
Full8.91%9.83%9.98%

MLP performs better at K=5, while Full has higher point estimates at the longer windows; its K=20 advantage is 3.22 pp. We therefore distinguish independently trained dynamic predictors, retrained fixed-window models, and restricting the observation range of a fixed scorer. The 83.59%/47.57% fixed-scorer result and the mixed Test comparisons are different evaluations and should not be read as one experimental population.

History order and content. We kept the current and initial representations unchanged and altered only the explicit history sequence consumed by Full-control. R@5 is:

History settingFreshFresh2Fresh3
Full-control20.74%16.89%15.62%
Shuffled order23.96%21.00%21.88%
Replacement content22.58%17.81%18.27%

For shuffled order on Fresh3, the simultaneous 95% CI for the difference from Full-control is [+1.57,+10.93] pp. This is evidence against a claim that the particular explicit history order is always necessary. Current states and other evidence paths already encode prefix information, which may limit the need for an additional ordered history sequence.

The replacement-content difference intervals cross zero. These results do not establish that replacing history degrades performance or that explicit history content is indispensable. They show sensitivity to history interventions, while leaving its necessity unsupported in these settings.

Our conclusion is therefore limited: continued observation of legal prefixes can be useful, but that does not establish that a particular explicit history structure is necessary. The full model has an overall ranking advantage in the independent-predictor comparison and higher recall point estimates at longer trained windows, while simple models remain competitive. We will make this distinction explicit rather than infer the necessity of every temporal component from the value of dynamic monitoring.

AuthorsOpenReview ↗

Response to Q2: LLaVA Rollout Costs, Distillation, and the Core Finding

Q2. Auxiliary rollouts, distillation, and the core finding

Thank you for asking about the cost of continuous auxiliary monitoring. We distinguish the ability to identify future risk while the visible answer is still correct from the computational budget used to obtain that evidence. Passive monitoring and auxiliary rollouts have different costs. The passive coverage, complete Qwen3 runtime, zero-lead interception, and serial-versus-accelerated controller measurements are reported in our response to W2.

LLaVA auxiliary evidence and cost. The auxiliary path samples possible continuations from the current prefix and evaluates their risk. It does not read the original answer's actual future suffix or its future error labels. It can therefore identify risk before the original answer reaches its first error, although obtaining this estimate takes additional time.

On LLaVA Fresh, this path gives 40.38% event recall at 6.34% actual FAR, with Lead>=5 and Lead>=10 coverage of 20.88% and 7.97%. Separately, a complete synchronous timing study on 200 inputs using LLaVA with a local Qwen judge gives 1.431 s for natural generation and 32.699 s for auxiliary monitoring. This is substantial overhead. The local-judge timing variant differs from the historical effectiveness configuration; these numbers are not a joint quality-latency estimate for one identical system.

Existing results without additional rollouts. We also recovered and recomputed earlier LLaVA results:

SettingOwn-t0 R@5Dynamic R@5Evaluation scope
Sampled original answers4.46% (10/224)8.48% (19/224)600 independent Test images
v101: suppress clean false peaks10.89% (441/4049)13.51% (547/4049)12,000 training answers
v103: causal global deadzone10.89% (441/4049)14.10% (571/4049)Same training population

R@5 uses empirically matched response-level FAR<=5%; pp denotes percentage points. Lead coverage uses all event responses as its denominator. In the first experiment, sampling is the original answer's decoding strategy; the monitor generates no additional continuation. Dynamic recall improves by 4.02 pp, capturing nine more events (paired image-bootstrap 95% CI [+0.41,+8.50] pp). Actual FAR is 3.72% for t0 and 4.52% for dynamic. AUROC does not improve, so the positive result concerns low-FAR recall.

That early monitor uses the probability of the currently selected candidate token. It is a candidate-available interface without additional rollouts; online commitment timing for this historical model has not been audited. It is not evidence of forecasting before candidate selection using only the visible prefix.

v101/v103 use legal prefixes and observed history, with no inference-time rollouts. Their training-set gains capture 106 and 130 additional events, supporting the ability to fit dynamic signals. Generalization is not established: on independent Confirmation, v103 R@5 is 8.22%, versus 11.33% for its own t0. We report training diagnostics separately from held-out evidence.

Distillation as a concrete cost-reduction path. Rollouts can be moved to training: a teacher estimates future hallucination risk from multiple continuations, and a student learns this soft target from current hidden states, visual information, and observed history. At inference, the student predicts risk directly, without continuation generation or judging.

We have implemented and evaluated such a student. On a retrospective evaluation of historical disjoint images, the full-hidden-state student achieves 12.09% dynamic R@5 versus 11.26% at its own t0. The +0.82 pp gain has a 95% CI [-1.70,+4.75] pp. This validates an executable interface without online rollouts, but does not establish a dynamic gain or preservation of the strong teacher's performance. The student also requires an additional substituted-image forward pass, and its full online cost remains to be measured. Distillation offers a specific optimization route; lossless removal of rollout cost has not been demonstrated.

Core finding. Even without these supplementary no-rollout results and student experiments, the original pre-onset evaluations support the central finding: risk can be identified while the visible answer prefix is still correct. Auxiliary samples estimate possible futures from that prefix; they do not wait for the original answer to become erroneous. Computational cost affects practical applicability and intervention benefit and must be measured explicitly. Distillation, incremental computation, and parallel execution offer ways to reduce it, with concrete Qwen3 acceleration already measured. Improving efficiency and preserving LLaVA teacher performance remain separate goals; the core finding does not depend on claiming that every implementation is already inexpensive.

Reviewer_ibYqOpenReview ↗
Rating
3
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper studies whether hallucinations in VLMs can be predicted before they occur, using information from earlier, still-correct response prefixes (t<τt < \tau). The authors introduce an online monitoring protocol that tracks the maximum risk score across prefixes while controlling the false-alarm rate on clean responses. They construct the PREHALLU dataset, containing approximately 85k onset-annotated trajectories and 181k prefix-conditioned continuations, and propose RISKTRACE, which combines prefix features, their changes over time, and a calibrated logistic classifier. Experiments on InstructBLIP, LLaVA-NeXT, and Qwen3-VL show that prefix-based monitoring outperforms both pre-generation baselines and a static classifier selected from 124 candidates. The authors also find that the predicted risks can be used to trigger visual selection, helping reduce object hallucinations measured by CHAIRs.

Critical strengths
  1. Definition of Pre-Onset Hallucination Forecasting: Instead of only looking at static t=0t=0 states or local token-level errors, this paper cleanly targets the pre-onset window (0≤t<τ0 \le t < \tau) where generated prefixes are still factually correct. Evaluating running-max alarms (Ri=max⁡t<τri,tR_i = \max_{t < \tau} r_{i,t}) under matched response-level FARclean\text{FAR}_{\text{clean}} properly controls for false-alarm accumulation across decoding steps.

  2. Construction of the PREHALLU dataset: Collecting ~85k onset-annotated trajectories and 181k prefix-conditioned rollouts from 22,668 supported prefixes is a very useful contribution for analyzing branching future risks from the exact same prefix state.

  3. Non-Monotonic Prefix Risk Evolution and Closed-Loop Proactive Intervention: The authors show that forecasting gains are non-monotonic over time (dropping at t=1t=1 before rising strongly by t=10∼20t=10 \sim 20), achieve a 12-token median warning lead time on InstructBLIP, and use these frozen alarms to guide visual selection on Qwen3-VL, cutting CHAIRs further than simple resampling.

Critical weaknesses
  1. Three incompatible pipelines under one "RISKTRACE" label: Section 4 presents RISKTRACE as a single unified framework, but the three backbones actually use completely different methods: InstructBLIP uses 24-dim handcrafted quantile features + CCEA; Qwen3-VL uses a multi-layer Transformer + GRU; and LLaVA relies on sampling ~5.77 online rollouts per prefix because passive hidden-state probing fails to beat the static baseline.

  2. Zero median lead time on Qwen3-VL and high latency on LLaVA: The main selling point—early warning well before onset—does not hold across models. On Qwen3-VL, the median lead time under frozen thresholds collapses to L=0L=0 (App. G.1, line 1277), meaning it mostly fires right before the error token like a local detector. Meanwhile, LLaVA's rollout scorer takes ~12–16.5s per response (Table G.2), which is too slow for real-time decoding.

  3. Missing decoding-time baselines and no code/data release: Table 1(a) only compares against pre-generation HALP and basic token entropy, leaving out existing decoding-time probes (e.g., TruthPrInt, HalLoc) or early-window methods (e.g., MTRE) under the same max⁡t<τ\max_{t < \tau} protocol.

Questions for authors

Fig. 3(c) shows an architecture that is never used in the InstructBLIP main experiments: Fig. 3(c) takes up a large part of the method section to show a Causal Transformer with Risk/Peak/Hazard heads. Yet App. C.1 admit this is just an "illustrative multi-head design" and the main InstructBLIP scorer actually uses handcrafted features with logistic regression (CCEA). Putting an unevaluated architecture in the main method figure is very misleading

3 comments
AuthorsOpenReview ↗

Framework, Backbone-Specific Predictors, and Figure 3(c)

Thank you for asking us to clarify the relationship between the framework, the evaluated predictors, and Figure 3(c).

Shared task and backbone-specific implementations. RiskTrace shares a prediction target, causal information constraint, dynamic monitoring mechanism, and response-level false-alarm protocol. It does not assume identical predictor networks or transferable weights across different VLM architectures. InstructBLIP uses Q-Former representations and CCEA fusion; Qwen3-VL uses cross-layer features and a GRU to track changing risk in its DeepStack-based architecture; the original LLaVA-NeXT implementation uses prefix-conditioned auxiliary continuations. These continuations sample possible futures from the current correct prefix; they do not reveal the actual future suffix or its error labels.

Table 1(b) reports AUROC improvements from initial to dynamic prediction: 75.43% to 83.58% for InstructBLIP, 79.09% to 81.12% for LLaVA-NeXT, and gains of 3.28, 3.63, and 3.71 percentage points on the three Qwen3-VL sets. This supports the value of newly available prefix information across the evaluated implementations. It does not establish that the same predictor transfers across backbones without training.

Figure 3(c) and the actual BLIP scorer. We agree that the main figure should distinguish a conceptual design from an evaluated implementation more clearly. Its causal Transformer with risk/peak/hazard heads is an illustrative design, not the InstructBLIP scorer used for the main results. The evaluated BLIP pipeline transforms multiple signals from the current decoding state, visual evidence, and history into a 24-dimensional CCEA input and uses logistic regression for risk scoring. The reported BLIP results come from this pipeline, not the illustrated Transformer. We will label this distinction explicitly and add the actual backbone-specific flows, linked to Appendix C.1 and Table C.1.

LLaVA without inference-time rollouts. We additionally trained lightweight causal predictors using the frozen LLaVA model's current hidden state, distribution statistics, and changes relative to t0 and preceding states. They generate no auxiliary continuations and call no teacher at inference. Training uses existing trajectory labels; some later candidates also use offline teacher soft labels. Thus, zero inference rollouts and zero-token warning lead are different concepts.

On 6,000 images and 12,000 responses, the mean dynamic Recall@FAR<=5% across four initializations was 36.58%, versus 29.01% for an independent static predictor and 26.17% for the dynamic model's own t0 score. These are training-response results: they demonstrate that a passive predictor can learn dynamic signals, not generalization to unseen images.

We also trained and selected on two of COCO, Flickr30k, and NoCaps, then evaluated on the entire held-out source, grouping responses from the same image. An improved route used cross-fitted static scores and paired training:

Held-out sourceStatic R@5Passive dynamic R@5Gain, pp
COCO9.82%10.08%+0.25
Flickr30k11.53%12.00%+0.47
NoCaps9.52%9.67%+0.15

Gains use unrounded scores. Recall divides by all event responses, and FAR by all clean responses. These exploratory comparisons match FAR<=5% on each target set; they do not test deployment with a frozen source threshold. Image-grouped tests do not establish a statistically significant advantage. This supports the feasibility of forecasting without online rollouts, while leaving its generalization benefit unresolved.

We will report this variant separately. It neither replaces the original LLaVA result nor combines its passive inference with the original rollout model's accuracy. The paper's central claim concerns future-risk information in correct prefixes under the evaluated evidence interfaces; it does not require rollouts for every backbone.

AuthorsOpenReview ↗

Warning Lead Time, Intervention, and End-to-End Cost

Thank you for raising warning coverage, usable intervention time, and total monitoring cost. We distinguish prediction quality, intervention opportunity, and runtime.

Zero-token lead can still precede output commitment. After t correct output tokens, the monitor checks risk before the next token is committed. With zero-based indexing, if the first error is token k and the alarm occurs at state t=k, lead L=k-t=0. The erroneous token has not yet reached the output callback. A synchronous controller can pause there; longer lead provides scheduling slack, while any subsequent correction time must still be counted.

We tested this ordering with 144 real greedy decodes on 48 images, comparing natural generation, monitoring only, and precommit pausing. Of 24 archived zero-lead cases, 22 again triggered a zero-lead alarm; all 22/22 withheld the first erroneous token, whereas monitoring-only emitted it in all 22 cases. The other two did not alarm. This is conditional interception success, not population recall or correction success; the live experiment paused output without generating replacements.

Historical correction evidence and its denominators. Separately, we linked archived Qwen alarms to complete-response CHAIR object-hallucination labels. A repair means an original event response became clean:

CohortZero-lead repairs / triggered zero-lead event responsesZero-lead repairs / all original event responses
Fresh, 2,000 images38/4938/217 (17.51%)
Fresh2, 4,000 images62/9062/438 (14.16%)
Fresh3, 4,000 images37/8437/416 (8.89%)

Thus, 49/90/84 are alarmed zero-lead event responses, not all hallucinated responses. There were 137 zero-lead repairs across these different action policies. Overall CHAIRs fell from 10.850% to 9.250%, 10.950% to 9.775%, and 10.400% to 9.475%, respectively. These overall changes include all lead times and newly introduced errors; they cannot be attributed entirely to zero-lead repairs.

These historical actions used original-response length constraints, and Fresh3's protection step also inspected the complete archived original response. They are prefix-triggered suffix-action replays, not a fully causal live correction experiment or a unified correction rate at exact FAR5. They are separate from the 22 live pauses above.

Multi-token warning coverage across all three backbones. Saved score streams yield:

BackboneTimely event recallLead>=5Lead>=10Actual clean FAR
InstructBLIP49.28%41.10%30.51%5.36%
LLaVA-NeXT, original v129 rollout40.38%20.88%7.97%6.34%
Qwen3-VL, Fresh/Fresh212.79-17.05%4.11-5.53%4.11-5.07%2.64-3.14%

Every recall/coverage denominator is all event responses, including misses. Thresholds were frozen on Development for BLIP, Train for LLaVA, and Selection for Qwen. Qwen ranges describe two cohorts, not pooled estimates. Populations and realized FAR differ: this is warning-coverage evidence, not a matched-FAR ranking or a table uniformly at FAR<=5%. LLaVA's row belongs to the original rollout model, not the new passive variant in Reply 1. Its lead coverage alone does not establish successful correction. Qwen's smaller positive-lead coverage motivates distinguishing multi-token warning from immediate precommit interception.

Complete monitoring and intervention cost. On 32 Qwen inputs, including two that triggered correction, we timed generation, risk scoring, correction candidates, visual checks, and final selection:

ModeMean E2E (s)P90 (s)
Natural generation1.56732.0062
Serial full controller2.95413.0637
Accelerated full controller1.75042.2741

Acceleration reduced mean runtime by 40.7% versus serial execution, with 183.1 ms (11.7%) overhead over natural generation. With only two triggered corrections, this is an engineering feasibility result, not a large-scale deployment estimate.

For LLaVA, a 200-input timing variant using a local Qwen judge measured 1.431 s for natural generation and 32.699 s for auxiliary monitoring. This substantial cost limits that rollout implementation. Its judge configuration differs from the historical quality configuration, so we do not combine them into one accuracy-latency claim. Reply 1 reports the separate no-rollout feasibility study. We will report prediction, intervention, and cost for each implementation separately.

AuthorsOpenReview ↗

Task-Aligned Decoding-Time Baselines and Reproducibility

Thank you for requesting comparisons with decoding-time methods and clearer reproducibility information. Appendix D.5 and Table D.3 discuss task alignment; we supplement this with experiments adapting TruthPrInt, MTRE, and HalLoc to future-event forecasting.

A common forecasting target. Our evaluation asks whether a later hallucination will occur while the observed prefix is still correct. Scores must therefore use only information causally available at that prefix. Evaluating a detector's original token-localization or completed-response metric would not directly answer this question. We instead adapt the methods to the same future-event target and evaluate response-level recall at FAR<=5% (R@5). Recall uses all event responses as its denominator, and FAR uses all clean responses.

MethodFresh R@5Fresh2 R@5Fresh3 R@5
TruthPrInt adaptation9.68%8.22%10.34%
MTRE adaptation11.52%6.39%9.13%
HalLoc adaptation2.30%1.37%2.40%
RiskTrace Full21.66%15.53%16.83%

TruthPrInt is adapted from the available checkpoint architecture; MTRE uses hidden-state representations; HalLoc is adapted to the causal, still-correct-prefix setting. These are task-aligned adaptations, not full reproductions of the official systems. The results support RiskTrace's higher R@5 under this forecasting protocol; they do not establish superiority on the methods' original detection tasks. We will document the adaptations and evaluation conditions in the appendix so the comparison can be interpreted and reproduced accurately.

Code and data release. We plan to release RiskTrace's implementation and the shareable PreHallu resources, including backbone-specific predictor configurations, training and inference pipelines, causal-prefix construction, data splits, and response-level FAR evaluation scripts. Where underlying images or other third-party content have redistribution restrictions, we will provide permissible annotations, source indices, and construction scripts in accordance with their licenses.

We will also distinguish the original evaluated pipelines from supplemental predictors, and report the corresponding evidence sources, supervision, and inference requirements. This will make clear which results use auxiliary continuations, which use passive prefix states, and which are training-set fits or held-out evaluations. Together, these additions address comparison coverage and enable reproducibility without conflating different implementations or claiming unrestricted redistribution of third-party data.

Reviewer_LFtxOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Existing methods predict hallucination risk before generation or detect errors during decoding. This paper studies the gap between them: continuously forecasting whether future tokens will hallucinate while current outputs remain visually supported (Pre-Onset Hallucination Forecasting). It proposes RISKTRACE, a token-level early warning and mitigation method that combines multimodal evidence with generation history to intervene before errors occur.

Critical strengths

This paper presents a new dataset (PREHALLU), comprising ~85K generation trajectories and >180K unique continuations sampled from supported prefixes for studying hallucination onset and alternative futures, and a new method (RISKTRACE), which is a token-level continuous early warning and mitigation framework integrating current multimodal evidence with observed history to trigger warnings and interventions several tokens before the first error.

Critical weaknesses

W1: Unclear Motivation and Triviality of Pre-Onset Token-Level Forecasting. The fundamental advantage of pre-onset (prior) token-level forecasting over well-established post-hoc (posterior) hallucination detection remains insufficiently justified. The motivation for predicting hallucinations before they fully manifest appears trivial without a rigorous analysis of its practical significance. Specifically, the paper fails to articulate the core value proposition of this paradigm shift: What are the concrete benefits of early warning compared to posterior detection? How does pre-onset forecasting compare against post-hoc methods in terms of detection accuracy, computational efficiency during decoding, and the actual effectiveness of subsequent mitigation interventions?

W2: Insufficient Engagement with State-of-the-Art Methods, Lack of Standard Benchmarks, and Questionable Generalizability. The evaluation relies heavily on the newly constructed PREHALLU dataset, overlooking several highly relevant, recent token-level hallucination detection and mitigation studies. The related work and experimental sections fail to engage with concurrent state-of-the-art approaches. Furthermore, the paper does not report performance on standard, widely recognized hallucination benchmarks (e.g., POPE, CHAIR, MME, or Object HalBench) utilized by previous works. This absence raises significant concerns regarding the generalizability of the proposed method. It remains unclear whether RISKTRACE and the CPRN Module can effectively generalize to other datasets with different distributions, image complexities, or prompt styles outside the specific scope of PREHALLU. Consequently, verifying whether the proposed pre-onset forecasting and dynamic monitoring genuinely outperform existing solutions under standardized conditions is challenging.

The experimental setups in the following papers can serve as a reference:

[1]Nguyen T D, Ho M K, Chen Q, et al. Beyond the Global Scores: Fine-Grained Token Grounding as a Robust Detector of LVLM Hallucinations[C]//Proceedings of the IEEE/CVF Conference on Computer Vision and Pattern Recognition. 2026: 40235-40244.

[2]Zhu Y, Luo H. Token-Guard: Towards Token-Level Hallucination Control via Self-Checking Decoding[C]//International Conference on Learning Representations. 2026, 2026: 71431-71456.

[3]Lu P, Lu J, Liu A, et al. TPA: Next Token Probability Attribution for Detecting Hallucinations in RAG[C]//Proceedings of the 64th Annual Meeting of the Association for Computational Linguistics (Volume 1: Long Papers). 2026: 25273-25292.

Questions for authors

Q1. Ambiguity in Task Formulation and Training Paradigm Based on my understanding, the proposed method trains a supervised model to fit intermediate-layer features for predicting whether the current token carries a high risk of hallucination. However, due to the unclear data format and confusing formal definitions, the exact training pipeline remains ambiguous. Specifically, what are the precise inputs, outputs, and optimization objectives? I strongly recommend providing a concrete, step-by-step example (e.g., detailing a specific input sequence, its corresponding feature representation, the target label, and the loss function) to clarify the training process.

Q2. Mechanism for Cross-Model Generalization The paper claims that the proposed method supports cross-model transferability. However, as illustrated in Figure 3, the CPRN Module takes model-specific features as input. Since different VLMs inherently possess distinct architectures, hidden dimensions, and feature structures, how does the CPRN Module handle these discrepancies? Please elaborate on the specific architectural designs or alignment strategies that enable true cross-model generalization despite heterogeneous input features.

Q3. Insufficient Details on Dynamic Monitoring Implementation The experimental results indicate that the proposed method underperforms compared to the "Optimized static baseline" in the static setting, yet achieves optimal performance in the dynamic setting. However, the paper provides very few details regarding the implementation of this dynamic mechanism. What exactly constitutes the "dynamic" aspect here? Does it refer to dynamically adjusting the warning threshold during generation, or does it involve continuously updating the monitoring state based on accumulated context? Please provide a rigorous definition and detailed explanation of the dynamic implementation to justify the reported performance gains.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.