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Under review as a conference paper at ICLR 2027

When Should a VLM Look? Paying Only for Visual Calls That Were Needed and Used

Abstract

Vision-language agents that crop and zoom are trained with rewards that credit a successful tool call, yet a successful call does not show that the model needed to look or used the pixels it received. On our cold-start checkpoint only 10% to 12% of visual calls were both needed and used, and released agents make spurious calls 36% to 87% of the time on individual benchmarks. Outcome rewards, judge rewards, and branch probes each observe one side of this failure, and about two thirds of what an outcome reward pays goes to calls that were neither needed nor used. CounterCredit asks both questions of every image-returning call at its realized pre-call state, using the policy’s own gold-answer score. A decision value compares the realized visual branch with answering immediately; an evidence value compares the returned crop with random same-size patches substituted into the same call. A call verified on both earns cashback and every other executed call pays rent; the price is bounded so that every correct trajectory outranks every wrong one, and a dual-channel GRPO advantage keeps the price in its own units. From the same cold start, prompt pool, and budget, CounterCredit reaches 89.5% on V∗, 80.2% on HR-Bench-4K, and 76.4% on HR-Bench-8K, 6.3 to 9.4 points above outcome-only GRPO at 1.78 against 1.84 calls per question, and lowers the spurious-call rate to 31% to 36%, the lowest among the agents evaluated. The same recipe lifts a Qwen3-VL-8B base from 75.4 to 80.8 on average.

Primary area:
reinforcement learning
Keywords:
Vision-Language Models, Visual Tool Use, Thinking with Images, Credit Assignment, Counterfactual Evaluation, Process Reward, Reinforcement Learning, GRPO, Multimodal Agents

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_BvAtOpenReview ↗
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Paper summary

This paper proposes CounterCredit, a training method that rewards visual requests only when they are both needed and used. Using gold-answer scores, it compares the actual crop with answering immediately and with matched random crops. Verified requests on correct trajectories receive cashback, while other requests incur charges. Outcome rewards and crop prices enter training through separate channels.

The main empirical evidence supports the complete training recipe. However, the external-scorer validation and the interpretation of the single-channel ablation require correction or qualification.

Critical strengths
  1. The matched training comparison supports the complete method.

Table 3 reports average accuracy of 76.1% for CounterCredit, compared with 68.9% for outcome-only training and 71.6% for the tested branch-reward control. This provides direct evidence that the proposed recipe improves performance under the evaluated conditions.

  1. The gains are not explained merely by making fewer requests.

On V*, CounterCredit and outcome-only training make similar numbers of requests: 1.78 and 1.84 per question, respectively. The performance difference therefore supports examining request quality rather than request count alone.

  1. Answer-level interventions provide additional behavioral evidence.

Table 9 reports that, at the first request, returning the actual crop instead of removing the request raises CounterCredit's V* accuracy from 78.5% to 85.3%. The corresponding change under outcome-only training is -1.1 percentage points. This supports the claim that CounterCredit learns to make requests whose returned information is useful to subsequent answers.

Critical weaknesses
  1. The external-scorer claim needs correction.

Section 4.2 describes the common and external scorers as preserving the spurious-call result and changing the baseline ranking by at most one adjacent swap. However, Appendix F.1 states that the external scorer checks only the actual crop against random patches. It omits the decision comparison and verification margin, so it does not reproduce the full spurious-call rate.

The reported correlation of 0.75 is against the common scorer, not the agents' own scorers. The adjacent-swap description instead belongs to the common-versus-own comparison. One adjacent swap among seven untied ranks gives a Spearman correlation of approximately 0.964, not 0.75.

The paper should report these diagnostic endpoints and ranking comparisons separately. The external check provides partial validation, but should not be described as reproducing the complete diagnostic.

  1. The single-channel ablation changes more than channel separation.

The single-channel arm achieves 64.5% average accuracy, compared with 76.1% for CounterCredit. This supports the complete implementation, but does not isolate the effect of channel separation because the ablation also lacks the variance floor.

Moreover, the single-channel arm can retain all-wrong groups with unequal crop charges, whereas CounterCredit masks the price advantage in those groups, as described in Section 3.5 and Appendix C, Algorithm 1. These differences can affect the training signal independently of channel separation.

Proposition 4's scale-cancellation argument remains valid. However, attributing the full empirical difference to channel separation requires either a comparison using the same variance floor and masking rule or a narrower interpretation of the existing ablation.

Questions for authors
  1. Can the scorer-validation results be revised to separate the full spurious-call diagnostic from the external actual-versus-random-crop check?

  2. Can the authors explicitly identify which scorer pairs produce the reported correlation and adjacent-swap ranking results?

  3. Can the single-channel comparison use the same variance floor and all-wrong-group masking rule as CounterCredit? If not, can the attribution claim be narrowed to reflect the combined implementation differences?

  4. Can the key matched comparisons be repeated across additional seeds to assess the stability of the reported gains?

4 comments

We thank the reviewer for the careful reading and for recognizing the gains under matched training conditions. We have added the requested controls to address the scorer validation and single-channel ablation, and repeated the central comparison across seeds. Changes are marked in blue in the revised PDF.

W1 / Q1 / Q2. Scorer validation‾\underline{\textbf{W1 / Q1 / Q2. Scorer validation}}

We agree that the original outside check validated only EE and did not establish the full spurious-call result. We have now added the answer-now comparison and evaluated the complete diagnostic.

Two ranking statements also need correction. The original ρ=0.75\rho = 0.75 compared the outside scorer with the common scorer. The “one adjacent swap” result (ρ=0.964\rho = 0.964) compared the common scorer with the agents' own scorers on V*. Section 4.2 should have reported these separately.

Both the common SFT scorer and GPT-5.6 Terra now compute DD, EE, and the fraction of calls with min⁡(E,D)≤ε\min(E, D) \leq \varepsilon, for all eight agents on V* and HR-Bench-4K. Each ρ\rho below compares the seven baselines' ranking under the indicated scorer with their ranking under their own scorers (Table 2).

BenchmarkScorerCounterCredit (%)Lowest baseline (%)ρ\rho vs. ownBaseline pairs reordered
V*common (SFT)32.334.60.9641/21
V*outside (Terra)34.138.50.8213/21
HR-4Kcommon (SFT)39.050.40.8214/21
HR-4Koutside (Terra)39.548.90.8932/21

CounterCredit has the lowest full spurious-call rate in all four comparisons. Baseline ranks do change: 1–4 of the 21 pairs are reordered. Thus, the new evaluation supports the result for CounterCredit without requiring the entire baseline ordering to remain unchanged.

In the revision, Appendix F.1 replaces the EE-only analysis with these results (Table 8). Section 4.2 identifies the scorer pair for each correlation and reports that one to four of the 21 baseline pairs change order. “One adjacent swap” is stated only for the common-versus-own comparison on V*, in Appendix F.1. Appendix G reports the lowest rate for CounterCredit and the observed changes in baseline ordering.

W2 / Q3. Single-channel ablation‾\underline{\textbf{W2 / Q3. Single-channel ablation}}

CounterCredit still outperforms single-channel GRPO after matching the variance floor and all-wrong-group mask. We trained the requested control with the same floor (σmin⁡=0.15\sigma_{\min} = 0.15), mask, cold start, prompt pool, budget, and seed.

ArmV*HR-4KHR-8KMME-RWMMStarChartQABLINKAvg.V* callsV* spur. %
Single-channel (paper)62.868.863.957.160.083.755.364.50.7862.5
Single-channel + floor + mask82.775.670.460.563.286.454.570.51.2759.3
CounterCredit89.580.276.467.768.987.162.876.11.7831.4

Adding the floor and mask raises the single-channel average from 64.5 to 70.5, accounting for 6.0 points of the original 11.6-point gap. With these controls matched, CounterCredit retains a 5.6-point advantage and reduces the spurious-call rate from 59.3% to 31.4%. This new ablation uses one seed.

The remaining difference is how the two arms handle the price term. Single-channel GRPO divides it by max⁡(std⁡(O+P),σmin⁡)\max(\operatorname{std}(O + P), \sigma_{\min}), so its scale still depends on group composition and can be amplified by up to 1/σmin⁡≈6.7×1/\sigma_{\min} \approx 6.7\times in all-correct groups. The dual-channel price term is not normalized. This is the distinction analyzed in Proposition 4. The matched single-channel policy also makes fewer calls on V* (1.27 vs. 1.78 per question).

Table 3 now includes both single-channel rows, Section 4.4 reports the controlled comparison first, and Appendix F.6 gives the breakdown above.

Q4. Seeds‾\underline{\textbf{Q4. Seeds}}

The improvement over outcome-only GRPO holds across all three evaluated seeds. We repeated outcome-only GRPO over three seeds. Its seven-benchmark average is 69.0±0.6169.0 \pm 0.61, compared with 76.0±0.4076.0 \pm 0.40 for CounterCredit (Tables 14 and 15, Appendix F.4). Each ±\pm is the sample standard deviation of the three per-seed averages as listed in those tables. CounterCredit is higher on every seed, with a 7.0-point difference between the means.

The remaining ablation arms in Table 3 are single-seed.

AuthorsOpenReview ↗

Thanks to Reviewer BvAt

We would like to sincerely thank you again for your dedicated reviewing effort and constructive feedback. We hope our response has successfully clarified the issues you raised. Please let us know if there are any lingering questions, as we warmly welcome the opportunity for further discussion.

AuthorsOpenReview ↗

Thanks to Reviewer BvAt

We would like to thank you again for reviewing our paper and providing valuable feedback, and particularly for recognizing the strengths and contributions of our work.

With only one day remaining in the discussion period, we would greatly appreciate it if you could let us know whether our responses have adequately addressed your concerns. We would be more than happy to answer any additional questions or provide further clarifications.

Thank you again for your time and consideration. Your feedback would be greatly appreciated.

AuthorsOpenReview ↗

A Gentle Reminder of the Final Feedback

Thank you very much again for your initial comments. They are extremely valuable for improving our work. We would be very grateful if you could take a look at our responses and revisions and let us know if there is anything else we could incorporate into the next version.

Reviewer_V1sQOpenReview ↗
Rating
3
Confidence
3
Informativeness
2
Presentation
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Soundness
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Paper summary

The paper addresses a blind spot in training vision-language agents that use crop-and-zoom tools: a successful tool call does not establish that the look was needed or that the returned pixels were used. The authors introduce CounterCredit, a counterfactual credit-assignment framework that, for every image-returning call, holds the pre-call prefix fixed and scores three continuations - answering immediately, appending the real observation, and appending a matched random observation. These contrasts define a decision value and an evidence value. A call on a correct trajectory earns cashback only when both values exceed a calibrated dead zone, while every other executed call pays rent. The reward is optimized with a dual-channel GRPO objective that normalizes outcome and price separately, preserving the scale of the rent. The authors provide theoretical guarantees (outcome dominance, unprofitability of chance verification, and robustness of the minimum of the two values), audit existing rewards to show that most credited calls are spurious, and demonstrate that CounterCredit leads seven benchmarks while substantially lowering spurious-call rates. Validation includes ablations, a second base model (Qwen3-VL-8B), and a case study illustrating the four call regions.

Critical strengths

The paper’s most consequential strength is the conceptual and operational separation of necessity from use in visual tool calls. The authors show that these are distinct failure modes - a call can be performative (needed but not used) or unnecessary (used but not needed), and that existing rewards conflate them. The paper provides a principled, measurable criterion for what it means for a visual interaction to be valuable. This separation is not merely diagnostic; it directly shapes the reward geometry (Figure 3) and the verification rule, and it is supported by an answer-level counterfactual showing that performative calls change the decoded answer as rarely as waste. This strength is critical because it turns a vague concern about "spurious tool use" into a actionable training signal.

The second critical strength is experimental rigor and the dual-channel design. The ablation in Table 3 is unusually clean: every RL arm shares the checkpoint, prompt pool, budget, and seed, so the causal claim, which calls survive matters more than how many calls are made is well supported. The authors also demonstrate that single-channel normalization erases the scale of the rent in unanimous groups, and the single-channel arm collapses to below the cold start (64.5 average, 0.78 calls/question). This combination of a sharp diagnostic, a targeted reward, and a careful optimizer adaptation gives the paper both explanatory power and practical impact.

Critical weaknesses

A substantive weakness is the scope and robustness of the evidence value. The authors acknowledge that tools returning text or structured output need their own null, but this is not merely a future-work note: the core claim, that the returned pixels caused the improvement, is restricted to a narrow tool class. Moreover, the random patches are unscreened, so a patch that happens to contain the target raises the reference mean and lowers, making the method conservative (under-verifying) rather than invalid, but the paper does not quantify how often this occurs. This matters for assessing whether CounterCredit would generalize to the broader tool-use landscape.

The second concern is metric circularity in the evaluation of spuriousness. The authors partially address this by re-scoring with common and outside scorers (Appendix F.1) and by reporting answer-level counterfactuals (Table 8), which preserve the ordering of agents. However, the headline claim that CounterCredit has the lowest spurious-call rate is still evaluated on the very quantity it optimizes. An evaluation defined entirely apart from the reward, for example, a downstream task where unnecessary calls incur a real cost, would strengthen the claim considerably. The authors themselves flag this limitation, but it remains a material weakness for a paper whose central contribution is a new credit mechanism.

Questions for authors
  1. In the spurious-call-rate evaluation, could the authors report the rate using a held-out deadzone or a different contrast (e.g., an outside reader’s evidence gain, as in Appendix F.1) for all agents, rather than the training deadzone, to rule out the possibility that the comparison is partly an artifact of the optimization target?

  2. For the random-patch reference, what fraction of calls have at least one patch that overlaps the target region (intersection-over-union above some threshold), and how does excluding those calls change E_i and the verification outcomes? This would help assess the practical severity of the conservative bias.

  3. The paper focuses on crop-based tools. Would a learned or screened null reference, for example, a patch selected to be maximally dissimilar from the real crop in a pre-trained feature space, be feasible for text-returning tools, and would the minimum-of-two-values argument still hold?

4 comments

We thank the reviewer for recognizing the value of separating necessity from use. Below, we address the concerns about metric circularity and the null reference through additional evaluation and a search-tool experiment. Changes are marked in blue in the revised PDF.

Q1 / W2. Dependence on the training deadzone and scorer‾\underline{\textbf{Q1 / W2. Dependence on the training deadzone and scorer}}

CounterCredit remains lowest when we change either the deadzone or the scorer. We ran both requested checks for all eight agents on V* and HR-Bench-4K.

(a) Held-out deadzones.‾\underline{\textbf{(a) Held-out deadzones.}} Training used ε=0.05\varepsilon = 0.05 for multiple-choice calls. We recomputed spurious-call rates at ε=0.02\varepsilon = 0.02 and 0.11. Cells report CounterCredit / lowest baseline (%).

Benchmarkε=0.02\varepsilon = 0.02ε=0.11\varepsilon = 0.11Baseline pairs reordered vs. ε=0.05\varepsilon = 0.05
V*29.3 / 30.832.6 / 42.31/21 and 1/21
HR-4K33.8 / 41.937.3 / 52.62/21 and 4/21

Only 1.2%–2.2% of CounterCredit's calls change label when ε\varepsilon moves from 0.05 to either value. Its calls are therefore not concentrated just above the training threshold. The smallest margin is 1.5 points over Thyme on V* at ε=0.02\varepsilon = 0.02, so this setting provides weaker separation.

(b) Alternative scorers.‾\underline{\textbf{(b) Alternative scorers.}} We extended the outside scorer from the original EE-only check to the full diagnostic. Both GPT-5.6 Terra and the common SFT scorer now compute DD, EE, and the fraction with min⁡(E,D)≤ε\min(E, D) \leq \varepsilon. Each ρ\rho compares the seven baselines' ranks with those obtained using their own scorers.

BenchmarkScorerCounterCredit (%)Lowest baseline (%)ρ\rho vs. own
V*common (SFT)32.334.60.964
V*outside (Terra)34.138.50.821
HR-4Kcommon (SFT)39.050.40.821
HR-4Koutside (Terra)39.548.90.893

CounterCredit remains lowest in all four comparisons. These evaluations are now in Appendix F.1 (Tables 8 and 9), and Section 4.2 and Appendix G are corrected: the baseline ordering is similar, not identical.

(c) Evidence beyond the diagnostic.‾\underline{\textbf{(c) Evidence beyond the diagnostic.}} Table 11 (Table 9 of the submission) directly tests whether the returned pixels improve answers: at the first call, returning the real crop rather than removing the call raises CounterCredit's V* accuracy from 78.5% to 85.3%, versus a −1.1-point change for outcome-only GRPO. The search experiment below also improves exact match while reducing calls. These behavioral results complement the diagnostic checks.

Q2. Random patches that overlap the target‾\underline{\textbf{Q2. Random patches that overlap the target}}

At least one random patch overlaps the target in 15.9% of CounterCredit's V* calls. Excluding those calls reduces the spurious-call rate from 31.4% to 30.4%.

We used V* target boxes and three patches per call. We report coverage (intersection ÷ target area), since a crop-sized patch can contain a small target while having low IoU. Positive coverage is equivalent to positive IoU.

Patch coversCalls with ≥1\geq 1 such patchSpurious % among themSpurious % after excluding them
(no exclusion)––31.4
>0%> 0\% of the target15.9%36.530.4
≥50%\geq 50\%11.6%42.130.0
100%10.1%48.529.5

Greater target coverage is associated with a higher spurious-call rate, consistent with conservative verification. Across these exclusions, the aggregate rate falls by at most 1.9 points. This analysis excludes calls rather than re-scoring them with screened patches, so it does not measure changes in per-call EE. This analysis is now in Appendix F.5 (Table 17).

W1 / Q3. Text-returning tools and a screened null‾\underline{\textbf{W1 / Q3. Text-returning tools and a screened null}}

A screened null works for the search tool we tested, and the minimum-of-two identity still applies. We use passages from the same query to preserve topic, format, and length while screening out answer-bearing content.

The experiment uses Search-R1 (Wikipedia-2018, E5 retriever, three passages per search, at most four actions), Qwen2.5-7B-Instruct, and 100 GRPO steps with Search-R1's configuration. Only the reward differs. We sample K=3K = 3 null returns of three passages each from ranks 5–40, after screening by string match and GPT-5.6 Terra. The same leave-one-out procedure calibrates ε\varepsilon to 1.06 nats per token.

RewardHotpotQA2WikiPopQASearches / questionSpurious %
Outcome (EM)0.3620.3280.3993.3978.3
CounterCredit0.3910.3670.4352.7960.4

Scores are exact match, and the last two columns average the three datasets. CounterCredit improves all three scores with 18% fewer searches in this single-seed study.

A maximally dissimilar null could be too weak. If the model ignores an off-topic return, its score approaches the answer-now score and EE approaches DD. Proposition 1 still gives q=Ureal−max⁡(Unow,Uˉrand)q = U_{\mathrm{real}} − \max(U_{\mathrm{now}}, \bar{U}_{\mathrm{rand}}), regardless of null construction. The null determines what EE measures, while q≤Dq \leq D bounds the credit. The search results and these requirements are now in Appendix F.8 (Table 19).

AuthorsOpenReview ↗

Thanks to Reviewer V1sQ

We would like to thank you again for reviewing our paper and providing valuable feedback, and particularly for recognizing the strengths and contributions of our work.

With only one day remaining in the discussion period, we would greatly appreciate it if you could let us know whether our responses have adequately addressed your concerns. We would be more than happy to answer any additional questions or provide further clarifications.

Thank you again for your time and consideration. Your feedback would be greatly appreciated.

AuthorsOpenReview ↗

A Gentle Reminder of the Final Feedback

Thank you very much again for your initial comments. They are extremely valuable for improving our work. We would be very grateful if you could take a look at our responses and revisions and let us know if there is anything else we could incorporate into the next version.

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

The paper points out that VLMs often make unnecessary visual tool calls or fail to use the information they retrieve. The paper introduces CounterCredit, an RL framework that rewards visual tool calls only when they are both necessary and informative. It evaluates each call using two counterfactual comparisons, one in which the model answers without the call and another in which random image patches replace the actual observation. Calls that pass both tests receive positive rewards, while unnecessary or uninformative calls are penalized. CounterCredit improves average accuracy from 68.9% to 76.1% over outcome-only GRPO while maintaining a similar number of tool calls. The results suggest that explicitly rewarding meaningful information acquisition can improve both the effectiveness and efficiency of visual agents.

Critical strengths
  1. The paper presents a well-motivated and principled approach to counterfactual credit assignment for visual tool use. CounterCredit addresses an important limitation of existing outcome-based rewards by distinguishing whether a tool call is necessary from whether its returned visual information is actually useful. The proposed method is supported by strong experimental results and comprehensive ablations. In particular, Table 3 demonstrates a 7.2 percentage point improvement in average accuracy over outcome-only GRPO while maintaining a similar number of tool calls.

  2. Additionally, the first-call intervention experiments in Table 9 provide convincing evidence that the model learns to make meaningful use of retrieved visual information, rather than merely learning when to invoke tools.

Critical weaknesses
  1. The paper's definition of tool necessity could benefit from further investigation. For instance, a model might already be able to answer correctly without a tool call, but the call could still be considered necessary under the proposed definition if it increases the model's confidence in the correct answer. It would be helpful to further examine whether this definition adequately captures tool necessity and explore alternative definitions or additional analyses to validate this choice.

  2. The proposed framework is specifically designed for visual cropping operations, and it would be benefit from additional experiments on whether it generalizes to other types of agentic tools, such as web search or code execution. Additionally, the experiments are limited to models from the Qwen family. It would be better to see whether CounterCredit remains effective with other tool types and model families to better establish its broader applicability.

Questions for authors

see weakness.

5 comments

We thank the reviewer for the positive assessment of the method and the evidence that it learns to use visual information. Below, we examine the definition of necessity and report experiments with a search tool and with InternVL3-8B, a base model from another VLM series. Changes are marked in blue in the revised PDF.

W1. Does necessity over-credit confidence gains?‾\underline{\textbf{W1. Does necessity over-credit confidence gains?}}

Our definition measures necessity through the gain in the gold-answer score. A call can therefore earn cashback even when the answer-now prediction is correct, but only if the real crop improves the score beyond both answering now and matched random patches by more than ε\varepsilon. This allows credit for additional visual evidence that strengthens an answer without changing the prediction.

We tested this choice directly. Among calls that earned cashback during training, 23.95% began with a correct answer-now prediction, and the rest began with an incorrect one. We retrained with flip-only necessity, which excludes the former calls from cashback. All other components, including EE, were unchanged.

RewardNecessityEE testAvg. (7 benchmarks)V* callsV* spurious %
Branch reward (Table 3)flip onlyno71.62.4562.9
Flip-only + EE (new)flip onlyyes74.91.6534.6
CounterCreditflip or confidence gainyes76.11.7831.4

Including confidence gains raises average accuracy by 1.2 points, with gains on all seven benchmarks (+0.4 to +1.6). It also lowers the spurious-call rate from 34.6% to 31.4%, while calls rise from 1.65 to 1.78. This single-seed comparison supports retaining confidence gains in the reward.

Flip-only + EE also exceeds the branch reward by 3.3 points with roughly half its spurious-call rate. That comparison changes more than EE. The comparison between the final two rows isolates the necessity definition.

The deadzone rejects negligible confidence gains. In Appendix F.7, Case 3, the answer-now score is already 0.97, D≈0D \approx 0, and the call pays rent. Section 3.3 now explains this distinction, and the flip-only + EE result is in Table 3 and Section 4.4.

W2. Other tool types‾\underline{\textbf{W2. Other tool types}}

CounterCredit also improves performance with a text-returning search tool. We used Search-R1 (Wikipedia-2018, E5 retriever, three passages per search, at most four actions), Qwen2.5-7B-Instruct, and 100 GRPO steps with Search-R1's configuration. Only the reward differs.

DD still compares answering after the search with answering now. For EE, we construct a null from passages ranked 5–40 for the same query, removing answer-bearing passages by string match and GPT-5.6 Terra. We draw K=3K = 3 null returns of three passages each and recalibrate ε\varepsilon with the same leave-one-out procedure (1.06 nats per token).

RewardHotpotQA2WikiPopQASearches / questionSpurious %
Outcome (EM)0.3620.3280.3993.3978.3
CounterCredit0.3910.3670.4352.7960.4

Scores are exact match, and the last two columns average the three datasets. CounterCredit improves all three scores with 18% fewer searches. The outcome-trained policy also shows a high spurious-call rate under the search diagnostic (78.3% vs. 60.4%). This 100-step, single-seed study is now Appendix F.8 (Table 19). Code execution has not been evaluated.

W2. Models beyond the Qwen-VL series‾\underline{\textbf{W2. Models beyond the Qwen-VL series}}

The gains also hold on InternVL3-8B, beyond the Qwen-VL models in the paper. We trained CounterCredit and an outcome-only GRPO control from the same cold start using the same recipe.

InternVL3-8BV*HR-4KHR-8KMME-RWMMStarChartQABLINKAvg.V* callsV* spur. %
Base, no tools (Table 1)70.270.469.161.768.286.055.668.70–
Outcome-only GRPO75.473.170.460.766.286.654.869.61.9080.2
CounterCredit84.879.176.466.770.287.359.874.91.8235.4

CounterCredit leads all seven benchmarks in this comparison, with an average of 74.9% versus 69.6% for outcome-only GRPO at similar call counts (1.82 vs. 1.90). Its spurious-call rate falls to 35.4%. The pattern is consistent across the two base models:

BaseOutcome-only vs. baseCounterCredit vs. baseOutcome-only spur. %CounterCredit spur. %
Qwen2.5-VL-7B+1.2+8.482.131.4
InternVL3-8B+0.9+6.280.235.4

The InternVL3 results are now in Table 4 and in Table 13 (Appendix F.3). For readability, Section 3.3 now states the operational meaning of necessity before the formal definition in Section 3.4. In the final version, we will further separate the main conclusions from the detailed diagnostic results.

AuthorsOpenReview ↗

Thanks to Reviewer LGBF

We would like to thank you again for reviewing our paper and providing valuable feedback, and particularly for recognizing the strengths and contributions of our work.

With only one day remaining in the discussion period, we would greatly appreciate it if you could let us know whether our responses have adequately addressed your concerns. We would be more than happy to answer any additional questions or provide further clarifications.

Thank you again for your time and consideration. Your feedback would be greatly appreciated.

Comments on the paper

1 comment

Dear Reviewers,

Thank you for your insightful comments and suggestions. We have carefully addressed the raised concerns in our rebuttal and provided additional clarifications and experimental results where applicable. We would greatly appreciate it if you could take some time to review our responses.

Thank you again for your time and consideration.

Best regards,
Authors

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