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Under review as a conference paper at ICLR 2027

Beyond Average Gains: Replay-Based Post-Intervention Control

Abstract

Training-free mitigation methods can reduce multimodal hallucinations on aver- age, but fixed, always-on use still leaves a practical problem: an intervention can improve aggregate performance while turning some originally correct outputs into wrong ones. We study this as post-intervention risk control, where the goal is to identify harmful method-induced changes after generation and apply the small- est possible correction. We find that standard generation-time signals, including confidence, margin, entropy, selective prediction, and self-consistency, provide little information about whether an intervention was warranted. In contrast, re- playing the committed intervention output through the unmodified frozen back- bone exposes a substantially stronger signal for separating harmful from helpful changes. Based on this observation, we propose RAPIC, a lightweight replay- based control layer that selectively retains or reverts intervention outputs. In our primary LLaVA-1.5 + VGA setting, RAPIC improves accuracy by +1.21, +1.61, and +0.67 points on MSCOCO, AOKVQA, and GQA, respectively, with paired image-clustered bootstrap confidence intervals excluding zero. Repeated calibra- tion shows that changed-answer labeling is more efficient than uniform sampling.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
hallucination mitigation, vision-language models

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
Reviewer_qN4POpenReview ↗
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3(+1)
Confidence
2(−1)
Informativeness
2
Presentation
2
Soundness
2
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Paper summary

This paper examines the harmful changes that training-free hallucination mitigation methods can introduce into vision-language model predictions, even when overall accuracy improves. The authors propose RAPIC, a post-intervention controller that compares the original and modified answers and uses the frozen backbone to replay the modified output when the two differ. Based on replay-consistency features and thresholds calibrated on labeled examples, RAPIC decides whether to keep the modified answer or revert to the original one. The method is mainly evaluated on POPE across different vision-language models and mitigation methods, with additional experiments on routing strategies, calibration, multiple-choice VQA, and image captioning.

After Rebuttal

Critical strengths

(i) The paper addresses an important reliability problem in hallucination mitigation. Average accuracy improvements can conceal harmful changes to individual predictions, and examining these changes provides a useful perspective for evaluating inference-time interventions.

(ii) The experiments cover three vision-language models, multiple hallucination mitigation methods, and three POPE datasets. The paper reports confidence intervals for the main results and includes settings where RAPIC provides little improvement or even causes slight performance degradation, giving a more complete picture of its empirical performance.

Critical weaknesses

(i) The proposed post-intervention risk control formulation is not clearly distinguished from existing selective prediction and post-hoc correction methods. Section 3.1 defines helpful and harmful intervention-induced changes, while Eq. (2) describes the accuracy change when selected predictions are reverted to the baseline. RAPIC then uses replay-based likelihood and margin features to rank changed answers and selects fallback thresholds using labeled examples. Although the paper identifies its focus on intervention-induced changes and same-backbone replay as differences from prior work, it does not clearly explain why these constitute a distinct risk-control framework rather than a calibrated selective fallback procedure applied to hallucination mitigation.

(ii) The results raise questions about whether RAPIC consistently identifies harmful changes at the individual-sample level. Appendix C.5 reports that replay scores provide little separation between harmful and helpful No-to-Yes changes, with an AUROC of only 0.52–0.58. Table 9 further shows that RAPIC reverts 147 of 152, 86 of 91, and 87 of 89 No-to-Yes changes across the three POPE datasets in the primary setting. This is effectively a near-complete rollback rather than selective identification of harmful changes in this direction. Although the paper shows stronger separation for Yes-to-No changes, the results do not clearly establish whether RAPIC provides effective sample-level discrimination for No-to-Yes changes, beyond relying on the overall proportion of harmful changes in that direction.

Questions for authors

(i) Please clarify what distinguishes the proposed post-intervention risk control formulation from existing selective prediction and post-hoc correction methods, and how the replay-consistency score relates to the intervention risk defined in Section 3.1.

(ii) Please explain whether RAPIC genuinely identifies harmful changes at the individual-sample level and how this ability is demonstrated.

3 comments

Thank you for the precise questions. In short: RAPIC is a fallback rule like selective prediction, but it decides a different thing using information from a different model, and this difference is what makes it work.

(i) Distinction from selective prediction and post-hoc correction.

Selective predictionPost-hoc correction (e.g., Woodpecker)RAPIC
Acts onevery output of the deployed modelevery outputonly where baseline and intervention disagree
Actionabstainverify and rewrite with external toolschoose one of the two existing answers
Signaldeployed (intervened) model's uncertaintyexternal modelspre-intervention (frozen) model

Of these, the difference that matters empirically is the signal. Under the same candidates, fallback action and supervision (Table 3, MSCOCO):

SignalΔ vs. VGA (pp) [95% CI]
Selective prediction (intervened model)−0.011
Best decode-time confidence (intervened model)+0.011
Replay C3 (pre-intervention model)+1.201 [+0.62, +1.77]

The deployed model's own uncertainty does not help; the gain comes from the pre-intervention model's support.

Link to the risk in Sec. 3.1. Reverting a changed candidate x replaces aMa_M by aBa_B, so its expected contribution to Eq. 2 is P(aB correct∣x)−P(aM correct∣x)P(a_B\text{ correct}\mid x)-P(a_M\text{ correct}\mid x). For a binary changed candidate exactly one answer is correct, so

E[Δfb(S)]=1N∑x∈S(2P(aB correct∣x)−1),E[\Delta_{fb}(S)]=\frac{1}{N}\sum_{x\in S}\big(2P(a_B\text{ correct}\mid x)-1\big),

and fallback helps exactly when P(aB correct∣x)>1/2P(a_B\text{ correct}\mid x)>1/2. Replay scores the intervention's answer under the frozen backbone, and its first step is the backbone's own distribution on (I, q) (99.5% argmax agreement with the recorded baseline answer). Weak support for yMy_M therefore means that the backbone prefers aBa_B, and it is a proxy for this probability to the extent that the backbone's confidence ranks the correctness of its own answers; the calibrated threshold estimates where the probability crosses 1/2. This ranking ability is high for "Yes" predictions (AUROC .927, RePOPE labels) and low for "No" predictions (.747), which is why the two directions behave differently in (ii). We will add this derivation to Sec. 3.2.

(ii) Does RAPIC identify harmful changes at the sample level? For Yes→No, yes. For No→Yes, your reading is correct, and below we explain why a direction-level decision is the right policy there rather than a failure. Primary setting (LLaVA-1.5 + VGA, Table 9; MSCOCO / AOKVQA / GQA):

Yes→NoNo→Yes
Held-out AUROC.771 / .830 / .761.522 / .424 / .445
Changes (harmful / helpful)272/393, 264/469, 198/53974/78, 55/36, 59/30
Reverted by RAPIC (harmful / helpful)133/21, 147/22, 69/3672/75, 53/33, 57/30
Net contribution (harmful − helpful reverted)+112 / +125 / +33−3 / +20 / +27

Yes→No selection holds under corrected labels: on the RePOPE-matched subset its AUROC is .804 with original and .859 with RePOPE labels, and RAPIC's overall gain over VGA increases from +1.21 to +1.75 pp. Further, the top replay-risk quintile is 87.7% harmful (Fig. 3c).

No→Yes changes help only when the baseline's "No" was wrong, and such errors are rare and poorly ranked. The baseline's "No" predictions are 90–96% accurate; on RePOPE-matched MSCOCO, 197 of the 319 POPE "No" errors are actually correct, and 24 No→Yes changes counted as helpful become harmful. The remaining errors are also hard to rank: the baseline's confidence has AUROC .747 for its "No" predictions vs. .927 for its "Yes" predictions (difference 95% CI [+.11, +.26]). Because these errors are poorly ranked, no selection rule can do much better than reverting the whole direction or keeping it; because they are rare, most No→Yes changes are harmful (AOKVQA, GQA), so reverting the whole direction is the better of the two. A direction-level decision is therefore near-optimal, and RAPIC's result is indeed indistinguishable from it (difference CIs include zero). The same direction-specific calibration thus yields sample-level selection where the scores separate harmful from helpful changes (Yes→No) and an effectively direction-wide decision where they do not (No→Yes), without being told which case applies. We will make this distinction explicit in Sec. 4.

I appreciate the authors' detailed response and the additional evidence, which have addressed my main concerns. I suggest incorporating the clarifications provided in the rebuttal into the revised manuscript to make the contributions and conclusions clearer. And I will raise my rating.

Thank you for raising your rating and for the constructive suggestion. Following your advice, we have incorporated the clarifications from the rebuttal into the revised manuscript. We appreciate your time and engagement throughout the discussion.

Reviewer_XswtOpenReview ↗
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1
Confidence
3
Informativeness
1
Presentation
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1
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Paper summary

The paper introduces RAPIC, a method to reduce errors introduced by hallucination mitigation methods. The authors define three replay-consistency metrics: minimum token log-probability, minimum target-token logit gap, and first-token logit gap. Based on the median of these metrics and a threshold calibrated on a labeled discovery set, the proposed method decides whether to retain the intervention's response or revert to the original model's response. The authors evaluate their method on three VLM backbones with several hallucination mitigation methods using the POPE benchmark to demonstrate its effectiveness.

Critical strengths

1.The paper is well written and easy to follow. 2.The motivation is clear, and the problem is interesting. 3.The authors conduct experiments with several hallucination mitigation methods.

Critical weaknesses
  1. The main weakness of the paper is that it is not clear why the proposed method should work. The authors define three metrics, but it is not clear why these metrics should help detect harmful interventions. For example, the original model can be confidently wrong about an object, and the intervention can correctly change its prediction. In this case, the original model would assign a low probability to the correct response of the intervention. So why should these metrics be able to distinguish harmful changes from helpful ones? Additionally, the results are very different for Yes → No and No → Yes transitions, and the results for No → Yes are as convincing as the other transition. The paper does not explain why these two directions behave so differently.

  2. The results on Qwen2.5-VL do not sufficiently support the effectiveness of the proposed method. In several cases, the improvements are very small, and in some cases, the method even reduces the performance. Therefore, it is not clear how well the proposed method generalizes to different models.

  3. The open-ended captioning part feels like a separate method from the main proposed method. It uses a different approach to detect hallucinated objects and suppress them during generation. However, there is not enough explanation or analysis in the main paper to support this method. Suppressing the tokens of an object during re-decoding can affect the plausibility and consistency of the generated caption. I believe a separate method like this needs more experimental analysis and discussion in the main paper.

  4. The ablation results in the appendix show that using all three proposed metrics may not be necessary. Using individual metrics sometimes performs as well as or even better than combining all three. I'm not clear on why all three metrics are needed in the proposed method. I believe these results should be included and discussed in the main paper, as they are directly related to the main components of the method.

Questions for authors

Why should the proposed replay-consistency metrics be effective in identifying harmful interventions? The ablation results in Table 12 show that individual replay-consistency metrics can perform as well as or even better than their combination. So why is it necessary to use all three metrics? What is the benefit of combining them using the median? Why does the proposed method perform worse on Qwen2.5-VL compared to LLaVA?

4 comments
AuthorsOpenReview ↗

Response (1/2): why the method works and why the directions differ (W1, Q1–Q2)

Thank you for the thoughtful review. Your two central questions, why the method works (Q1) and why the directions differ (Q2), have one answer: a change should be reverted when the pre-intervention answer was right, and the pre-intervention model's confidence predicts this for Yes→No but not for No→Yes. Your counterexample is the key to both. Q3–Q5, in the next comment, address Qwen2.5-VL, captioning, and the three metrics.

Q1. Why should replay identify harmful changes? Reverting a changed candidate x replaces the intervention's answer by the baseline's, so on a binary question its expected value is (2P(aB correct∣x)−1)/N(2P(a_B\text{ correct}\mid x)-1)/N (Eq. 2); what must be ranked is thus the probability that the pre-intervention answer was right. Replay evaluates the intervention's answer yMy_M with the frozen backbone on the same (I, q); its first step is the backbone's own first-step distribution (99.5% argmax agreement with the recorded baseline answer), so weak support for yMy_M means the backbone prefers the baseline's answer. For this preference to estimate the probability of being right, the backbone's confidence must rank the correctness of its own answers. It does for "Yes" predictions (AUROC .927, RePOPE labels) and much less for "No" predictions (.747; difference +.18 [+.11, +.26]). Reverting Yes→No relies on the first, No→Yes on the second (Q2). Compared with the intervened model's confidence (Table 3 protocol, MSCOCO):

SignalComputed byΔ vs. VGA (pp) [95% CI]
Decode-time confidence (best scalar)intervened model+0.011
Replay C3pre-intervention model+1.201 [+0.62, +1.77]

The intervened model's confidence says how firmly it produced its answer, not whether it was right to change the baseline's.

Q1 (cont.). What if the baseline is confidently wrong? This is where the premise above fails, so we measured how often it occurs among Yes→No changes in the top quintile of baseline first-step confidence:

DatasetRevertedHarmful (baseline right)Helpful (your case)
MSCOCO1321248
AOKVQA14713215
GQA103 of 1456934

A confident "Yes" is usually right, so reverting gives up a few correct changes to recover many errors. On GQA, where the baseline is least accurate, your case is more common and the trade less favorable, though still positive; the calibrated threshold sets it from data.

Q2. Why do Yes→No and No→Yes behave so differently? A No→Yes change helps only when the baseline's "No" was wrong (a missed object). Such errors are rare and, as shown in Q1, poorly ranked (AUROC .747 vs. .927):

Baseline prediction"Yes""No"
Accuracy (MSCOCO / AOKVQA / GQA)82 / 71 / 69%90 / 96 / 96%
Changes that would fix these errorsYes→No: held-out AUROC .771 / .830 / .761No→Yes: .522 / .424 / .445

The two facts play different roles. Poor ranking means no selection rule can do much better than reverting the whole direction or keeping it; rarity means most No→Yes changes are harmful (AOKVQA 55/36, GQA 59/30; Table 9), so reverting is the better of the two. RAPIC's calibration indeed reverts almost all of them, with a result indistinguishable from reverting the whole direction (difference CIs include zero). The same direction-specific calibration thus yields sample-level selection where the scores separate harmful from helpful changes (Yes→No) and an effectively direction-wide decision where they do not (No→Yes), without being told which case applies. We tested three alternative explanations:

Alternative explanationTestResult
POPE label noiseRePOPE labels (MSCOCO)197 of 319 POPE "No" errors are label errors, so genuine ones are even rarer; No→Yes AUROC stays .525
Narrower margin range of No→Yesreweight Yes→No to No→Yes margins.721 vs. .487, difference CI [.119, .349]
Specific to one settingall 24 settingsYes→No significantly more separable in 5 (LLaVA-1.5 + VGA ×3, + VAF on AOKVQA/GQA), the reverse in 0; 7 not significant; 12 lack one change type in one direction

We will add this as a subsection of Sec. 4.

AuthorsOpenReview ↗

Response (2/2): Qwen2.5-VL, captioning, and the three metrics (W2–W4, Q3–Q5)

Q3. Why are gains smaller on Qwen2.5-VL? Because the interventions give RAPIC little to correct on Qwen (Table 2):

LLaVA-1.5 + VGAQwen2.5-VL + VGAQwen2.5-VL + VAF
Changed answers (MSCOCO / AOKVQA / GQA)817 / 824 / 826135 / 191 / 125224 / 284 / 345
Harmful-change rate (%)3.84 / 3.54 / 2.861.19 / 1.12 / 0.630.52 / 0.96 / 0.88
Intervention net gain (helpful − harmful)+125 / +186 / +312−79 / −11 / +11+130 / +112 / +187
RAPIC ΔR (pp)+1.21 / +1.61 / +0.67+0.84 / +0.20 / −0.01+0.07 / −0.02 / −0.07

The reason lies in the baseline's errors: most of Qwen2.5-VL's errors are omissions (false "No": 96.5% / 71.6% / 65.1%), whereas LLaVA-1.5's are mostly false "Yes". Hallucination interventions target false "Yes", so on Qwen they change few answers and rarely harm. RAPIC behaves accordingly: where VGA hurts (MSCOCO), it recovers +0.84 pp; where VAF already helps, it falls back on 0.07–0.13% of the data and preserves the gain; the small negatives occur where harmful changes are rarest and fallback precision is 25–50%. This is consistent with Sec. 4.3: across the 24 settings, the gain increases with held-out separability, by +0.29 pp per 0.1 AUROC (95% CI [+0.11, +0.54]) after controlling for the routing regime. We will extend Sec. 4.3 with this regime-level analysis.

Q4. Captioning. The captioning variant applies the same principle (frozen-backbone support for a committed output) through an object-level yes/no probe; we will describe this decision rule explicitly in Sec. 3.4. To address your concern about plausibility and consistency, we measured caption quality on 500 paired COCO-CHAIR captions (LLaVA-1.5 + VGA; RAPIC − VGA):

MetricK = 1K = 2K = 3
Δ words [95% CI]–−0.92 [−3.04, +1.16]−1.16 [−3.49, +1.10]
Sentences (median)–5 → 55 → 5
Repetition (distinct-1/2/3, repeated 3/4-grams)–no significant changeno significant change
Δ perplexity under the backbone LM (text only) [95% CI]+0.071 [+0.022, +0.124]+0.028 [−0.028, +0.084]+0.033 [−0.024, +0.090]

At K = 2 and 3 we detect no degradation. At K = 1, for which only perplexity is available, perplexity rises slightly but significantly (about 2% of the median of 2.99). We will report all of this in Sec. 4.7.

Q5. Why three metrics and the median? Indeed, single features perform comparably. Over the 24 settings of Table 2:

ScorerMean Δ (pp)Negative settings
f_first+0.8122
f_gap+0.8193
f_LP+0.8160
Median (C3)+0.8203

The differences are not significant (Wilcoxon signed-rank, p ≥ .79): consistent with Table 3 (right), the gain comes from the replay information, not from the combination rule. The median was fixed in advance as a selection-free default, and any single feature is an equally valid instantiation.

Where the median makes a difference is in settings where relying on the first-token score alone fails. To test this directly, we compared the median against f_first alone under the same discovery calibration in five settings (LLaVA-1.5 + VGA on MSCOCO, AOKVQA and GQA; Qwen2.5-VL + VAF on AOKVQA and GQA), with image-cluster bootstrap 95% CIs:

Settingmedian − f_first (pp) [95% CI]
LLaVA-1.5 + VGA, MSCOCO+0.20 [−0.04, +0.47]
LLaVA-1.5 + VGA, AOKVQA+0.33 [+0.07, +0.63]
LLaVA-1.5 + VGA, GQA−0.13 [−0.33, +0.08]
Qwen2.5-VL + VAF, AOKVQA+0.01 [−0.13, +0.13]
Qwen2.5-VL + VAF, GQA+0.54 [+0.32, +0.76]

The median is significantly worse in no setting and significantly better in two. On Qwen2.5-VL + VAF (GQA), the first-token score alone gives −0.61 pp and the median −0.07 pp. We also compared against choosing a single feature in advance. When the best single feature per direction is selected on discovery data only and matched to the same fallback budget, the median is significantly worse in none of the eight setting–direction pairs (lowest −0.06 pp, CI including 0). On LLaVA-1.5 + VGA the three features tie on discovery, and on Yes→No the median differs from the selected feature by 0.00 pp [0.00, 0.00]. On Qwen2.5-VL + VAF (GQA, Yes→No), by contrast, discovery selects f_first, and the median is better by +0.54 pp [+0.34, +0.72]. A single feature chosen in advance can thus be the wrong choice in some settings; the median avoids this risk while matching the best single feature.

I thank the authors for the detailed response and additional experiments. The response clarifies some of my questions. However, I believe my main concerns remain.

1.The authors explain that the method works because the baseline model's confidence can help distinguish harmful changes from helpful ones. However, this confidence is already available during the original generation and It is not clear why replay is needed. The additional ablation results also show that using a single metric performs comparably to combining all three. So, if f_first can achieve the same performance as replay, while this information is already available during the decoding stage, what is the role of replay here?

  1. The explanation for the different results on Yes → No and No → Yes raises another concern about generalizability. The authors explain that No → Yes corrections are less relevant for LLaVA-1.5 because the baseline rarely makes false "No" predictions. Then they also explain that the limited improvements on Qwen2.5-VL are because most of its errors are false "No" predictions. This suggests that the method mainly works for the error patterns of LLaVA-1.5 and may not generalize well to models with different types of errors.

Thank you for the follow-up. We address the two remaining points.

1. The role of replay. By construction, the first step of replay conditions only on the image and the question, so it coincides with the unmodified backbone's first-step distribution in its original generation (consistent with the 99.5% agreement with the recorded baseline answer). The first-step score can therefore be read from that generation without a separate pass. We regarded this as immediate and therefore did not emphasize it in the paper.

The relevant distinction in the paper is which model supplies the signal, not when it is computed. Confidence produced by the intervened model during its own decoding does not identify harmful changes (best decode-time scalar +0.011 pp; selective prediction −0.011 pp), whereas the support of the frozen, unmodified backbone does (+1.201 pp). RAPIC uses teacher-forced replay as a uniform post-hoc way to obtain this support for the intervention's answer, including the scores defined over all of its content tokens, at the cost of one forward pass on the changed answers only (about 9% of the data). As reported in Q5, the median of the three scores is a pre-specified default that performs on par with the individual scores, so our conclusions do not depend on looking beyond the first token.

This point concerns how the score is computed. It leaves the paper's main contributions unchanged: interventions that raise average accuracy still turn up to 4.8% of all answers from correct to wrong, these changes cannot be identified from the intervened model's own signals, and they can be identified from the unmodified backbone's support.

2. Generalization beyond LLaVA-1.5. Our two explanations describe one condition rather than a model-specific pattern: RAPIC can only undo harm that an intervention causes, and it cannot create corrections that the intervention never proposes.

(a) The effect is not confined to LLaVA-1.5. On LLaVA-NeXT + VGA, RAPIC exceeds both the intervention and the baseline on all three datasets, with paired 95% CIs excluding zero:

DatasetRAPIC − VGA (pp)RAPIC − baseline (pp)
MSCOCO+0.13 [+0.01, +0.29]+0.64 [+0.08, +1.18]
AOKVQA+0.44 [+0.27, +0.63]+1.17 [+0.62, +1.72]
GQA+0.58 [+0.34, +0.83]+2.09 [+1.52, +2.64]

LLaVA-NeXT's error profile also differs from LLaVA-1.5's: on MSCOCO, 45.8% of its baseline errors are false "No", compared with 31.4% for LLaVA-1.5.

(b) Across all 24 settings (three backbones, three interventions), RAPIC is significantly better than both the baseline and the intervention in 9, significantly worse than both in none, and within 0.07 pp of the better of the two in every setting. A practitioner therefore does not need to know in advance whether an intervention helps or hurts a given model.

(c) Qwen2.5-VL shows the condition at work. Its baseline errors are predominantly false "No" (65–97% across the three datasets), whereas VGA and VAF target false "Yes" answers, so they change few of its answers (125–345 of 9,000) and leave RAPIC little to correct. Where the intervention does harm (VGA on MSCOCO: 107 harmful vs. 28 helpful changes, −0.88 pp relative to the baseline), RAPIC recovers +0.84 pp; where it already helps (VAF: +1.24 to +2.08 pp over the baseline), RAPIC preserves the gain to within 0.07 pp.

We hope this clarifies both points. If a specific analysis would help resolve your remaining concern, we would be glad to provide it during the discussion period.

Reviewer_MfLQOpenReview ↗
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Confidence
4
Informativeness
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Paper summary

The paper introduces a post-intervention controller to reduce multimodal hallucination. When a mitigation method changes the baseline answer, the method uses log probability, target gap, and first token gap to decide whether to keep the intervention output. The main results are on binary POPE benchmarks.

Critical strengths
  1. The controller is training-free and makes a targeted decision only when the intervention changes the parsed answer.
  2. The paper acknowledges that the method does not help consistently across all backbone and mitigation combinations, and that calibration is task-specific.
Critical weaknesses
  1. The paper offers limited novelty, and its contribution may not meet ICLR’s bar. The method is simple and applies only to a narrow range of prediction settings.
  2. The method is not described clearly enough. How is u_{k,d} computed? I can infer its intended construction from the notation and description, but the roles of “LP,” “gap,” and “first” (corresponding to responses 1–3) should be explained explicitly. The equation defining u_{k,d} should also be presented.
  3. The primary evidence is on binary object-existence prediction. These results provide limited evidence that the method generalizes beyond yes/no prediction.
Questions for authors

Why use “LP,” “gap,” and “first” as signals? More discussion is better; it is also closely related to the conference. And need to discuss the yes/no binary prediction and the multiple-prediction case.

3 comments

Thank you for the careful reading and the concrete questions. After the definition you asked for (W2), we answer your remaining points (signals, binary vs. multiple-choice, scope) with one argument.

Definition of uk,du_{k,d} (W2). We will add to Sec. 3.2:

uk,d(x)=okfk(x)−μk,dσk,d,k∈{LP,gap,first},u_{k,d}(x)=o_k\frac{f_k(x)-\mu_{k,d}}{\sigma_{k,d}},\qquad k\in\lbrace \mathrm{LP},\mathrm{gap},\mathrm{first}\rbrace ,

where μk,d\mu_{k,d} and σk,d\sigma_{k,d} are the mean and standard deviation of fkf_k over discovery candidates of direction d, and oko_k is an orientation sign, set to ok=−1o_k=-1 for all three features so that a larger u means weaker replay support (higher risk). These are the three inputs u1,d,u2,d,u3,du_{1,d},u_{2,d},u_{3,d} of Eq. 6.

Why LP, gap and first (Q1). The signals follow from what has to be estimated. Reverting a changed candidate x replaces the intervention's answer aMa_M by the baseline's answer aBa_B, so its expected value is P(aB correct∣x)−P(aM correct∣x)P(a_B \text{ correct}\mid x)-P(a_M \text{ correct}\mid x). On a binary changed candidate exactly one of the two is correct, so this becomes 2P(aB correct∣x)−12P(a_B\text{ correct}\mid x)-1 (Eq. 2): we need the probability that the pre-intervention answer was right. The frozen backbone is the natural estimator: its confidence separates correct from incorrect "Yes" predictions well (AUROC .927, RePOPE labels) and "No" predictions less well (.747). Replay queries this estimator on the intervention's answer:

  • first is the backbone's support for the first token of yMy_M. On POPE its first step is the backbone's own first-step distribution (99.5% argmax agreement with the recorded baseline answer), and low support for yMy_M means the backbone prefers aBa_B.
  • LP and gap apply the same query to every content token and keep the weakest one, so they remain informative when the answer is not decided at the first token.

Accordingly, replay predicts harm, while the intervened model's confidence, which does not estimate this probability, does not (Table 3 protocol, MSCOCO, N = 8,996):

SignalWhat it measuresΔ vs. VGA (pp) [95% CI]
Intervened model's decode-time confidencehow firmly the intervened model produced yMy_M+0.011
Replay C3pre-intervention support, all content tokens+1.201 [+0.62, +1.77]

How firmly the intervened model produced yMy_M says nothing about whether its change was warranted.

LP and gap are added to first because they do not reduce to the first-token score. On Qwen2.5-VL + VAF (GQA), where first-token scoring alone loses 0.61 pp, the median corrects a net 49 more cases than first alone (+0.54 pp): 27 from candidates whose LP or gap minimum lies after the first token, and 22 where both minima are at the first token. Later tokens contribute, and even at the first token the median decides differently from f_first.

Binary vs. multiple-choice (Q1, W3). The derivation above uses one property of binary decisions: every changed candidate is either harmful or helpful, so the baseline's support alone settles the decision. With K > 2 options a change can be neutral (both answers wrong); the value of reverting is then P(aB correct)−P(aM correct)P(a_B\text{ correct})-P(a_M\text{ correct}) with no complementarity, and the support for both answers must be estimated. This is why our evidence is concentrated on binary decisions, and it is consistent with MMStar (Table 5), where gains are small and uncertain (VAF: +1.8 pp, CI [−0.1, +3.7]). We will state this condition in Sec. 4.6.

Novelty and scope (W1). The method is deliberately simple. What we consider new is the finding it rests on and its limits: the pre-intervention model's confidence predicts whether a change should be kept while the intervened model's does not (table above), and this holds where the baseline's errors can be ranked. That is the case for Yes→No but not for No→Yes (.927 vs. .747 above). The same direction-specific calibration thus yields sample-level selection where the scores separate harmful from helpful changes (Yes→No) and an effectively direction-wide decision where they do not (No→Yes), without being told which case applies.

Thank you again for your review. As the discussion period continues, we would like to check whether our response has addressed your concerns, in particular the definition of uk,du_{k,d}, the rationale for the three replay signals, and the scope beyond binary prediction. If any point remains unclear, we would be glad to discuss it further.

Thank you for the detailed reply, the paper is limited to yes/no and multi-selection. I maintain my score.

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