acceptodds
Under review as a conference paper at ICLR 2027

Next Demonstration Prediction for Visual In-Context Learning

Abstract

Selecting visual in-context demonstrations requires choosing both examples and their order. Visual nearest-neighbor retrieval can produce redundant prompts, while diversity heuristics cannot adapt their selection to a downstream vision-language model (VLM). We propose Next Demonstration Prediction (NDP), an autoregressive selector initialized by behavioral cloning of maximal marginal relevance and then trained with PPO using a frozen VLM's task reward. On 14 benchmarks with Gemma 3 4B-it at , NDP achieves the lowest mean regression MAE and highest mean VQA accuracy among the evaluated image-only selectors, but trails DPP on classification. Benefits vary by task and are limited at small shot counts. Reordering NDP's selected examples reduces performance in the evaluated in-domain settings, whereas cross-dataset policy transfer can underperform simple heuristics. NDP therefore offers a task-dependent, ordered alternative to static retrieval, at the cost of substantial VLM-based policy training.

Primary area:
foundation or frontier models, including LLMs
Keywords:
In-context learning, Vision-language models, Next token prediction

Reviews

Among:
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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 4 reviews, above 27% of the others.
Reviewer_6sjBOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

Few-shot prompting of vision-language models (VLMs) is powerful but fragile — the choice and order of example images in the prompt can make or break performance. Standard practice is k-nearest-neighbor retrieval, which tends to fetch visually similar but redundant examples.

This paper proposes Next Demonstration Prediction (NDP), a learned selector that builds the prompt one example at a time. The idea is simple: first, teach a small neural network to imitate a classic relevance-plus-diversity heuristic (MMR); then, fine-tune it with reinforcement learning (PPO) so that the examples it picks actually maximize the frozen VLM's accuracy on the task — for example, minimizing age-estimation error or maximizing VQA accuracy. A Perceiver module compresses the large candidate pool, and an autoregressive decoder picks each next shot, so the prompt is constructed as an ordered sequence, not just a set. The authors evaluate on 14 benchmarks spanning regression, classification, and VQA, mostly with a Gemma 3 4B model at 16 shots, plus smaller cross-model and transfer experiments. The results are honest and mixed: NDP achieves the best average regression error and VQA accuracy among the image-only selectors it competes against, but loses to DPP on classification.

Critical strengths
  • The paper is well organized, the abstract accurately reflects mixed results, and limitations are integrated into the main text rather than buried.
  • Treating demonstration selection as an ordered sequential decision problem rather than unordered subset selection is a meaningful conceptual contribution. The permutation experiments (Table 3) provide direct evidence that the learned order carries information beyond the selected set itself — the predicted order (regression MAE 0.62) clearly beats shuffle (0.80) and reverse (0.83).
  • The authors conduct extensive evaluations on 14 datasets across three task families, covering K-shot scaling curves (K∈{1,2,4,8,16}K \in \{1, 2, 4, 8, 16\}) for all datasets in the appendix, three target VLMs, and both in-domain and transfer settings. The qualitative analysis (Figures 3, 4, 9–20) — showing anchor, boundary, global-scale selection dynamics, and NDP spanning the label distribution where k-NN retrieves near-duplicates — is informative and consistent with the quantitative gains.
  • The paper explicitly reports that NDP loses to heuristics on cross-dataset transfer, that it trails DPP on classification, and that ICL can hurt relative to zero-shot. This honesty strengthens the credibility of the positive claims and makes the paper useful to practitioners deciding when RL-based selection is worthwhile.
Critical weaknesses
  • The authors concede that they did not evaluate the behavioral-cloning checkpoint, so it cannot attribute improvements to PPO versus the MMR initialization. This is a critical gap: MMR alone already achieves strong classification results (82.0 avg, beating NDP's 81.1), and other NDP gains (e.g., 54.2 vs. MMR 53.5 on VQA) are within plausible seed/evaluation noise. Without a BC-only ablation, the paper cannot support its framing of "RL fine-tuning" as the active ingredient, nor the claim that NDP "deviates from the MMR heuristic."
  • The paper notes that ~48k–64k VLM generations per policy are required and that matched GPU-hours, latency, and break-even query counts were not measured. For a method whose practical value proposition is "pay training cost once, serve many queries", the absence of any amortization analysis makes the use-case argument (Section 4.7) speculative.
  • Reward is zero until step K; the paper offers no analysis of whether the GAE critic actually provides meaningful credit to early selections, nor any diagnostic (e.g., value-function accuracy, per-step advantage magnitudes).
  • Cross-dataset transfer fails badly (below random on EmoSet→Food-101), cross-model transfer is mixed (helps on Phi EmoSet, slightly hurts on Qwen UTKFace, which is not uniformly better than in-domain or zero-shot), yet the abstract and conclusion still frame transfer as a contribution ("cross-dataset policy transfer can underperform simple heuristics" is acknowledged but the positive transfer cases are given equal billing).
  • Missing related-work positioning.
    • Partial2Global [1] and LLM-R [2] are trained, non-RL selectors for (visual) ICL that the paper neither cites nor benchmarks — without them, "learned selection beats heuristics" is not established as "RL selection beats supervised selection".
    • The ordering claim, the paper's most novel contribution, is never compared against curriculum-based ordering methods such as CDS [3], leaving open whether a training-free complexity ordering captures most of the permutation-sensitivity effect.

References

[1] Towards Global Optimal Visual In-Context Learning Prompt Selection, NeurIPS 2024.
[2] Learning to Retrieve In-Context Examples for Large Language Models, EACL 2024.
[3] Curriculum Demonstration Selection for In-Context Learning, SAC 2025.

Questions for authors
  1. Why don't you evaluate the BC-only checkpoint (after Stage 1, before PPO) on any of the 14 benchmarks? If PPO contributes little or nothing beyond the MMR-imitating policy, the paper's central claim — that RL fine-tuning on VLM reward is the active ingredient — would not hold.
  2. How many independent training seeds or evaluation resamplings were used for the headline Table 1 results? Without variance estimates, the key performance gains cannot be distinguished from noise.
  3. Is there a substantive reason MMICES (or a minimal text-conditioned variant of your own selector) could not be run on cached embeddings?
  4. What is the wall-clock latency of the trained NDP selector (Perceiver encode + K decode steps) relative to, e.g., MMR or DPP over the same 8,192-candidate pool, and roughly how many queries would be needed to amortize the ~48k–64k training generations?
  5. For Qwen-3 on UTKFace, the transferred policy (5.98) slightly beats the in-domain policy (6.28). Do you have any analysis (e.g., embedding-space overlap, dataset statistics) explaining when Gemma-trained selection transfers and when it collapses below random (EmoSet→Food-101)?
2 comments

Thank you for recognizing our transparent reporting, permutation analysis, and qualitative study. We address your five weaknesses and questions below.

W1. BC-only evaluation and PPO attribution

We agree that MMR does not substitute for the BC-only checkpoint: a learned imitator may differ from its teacher. Without checkpoint results, we cannot isolate PPO’s contribution.

We will remove claims that PPO is the established active ingredient or that the NDP–MMR gap measures RL’s benefit. The results support the complete pipeline, not PPO’s necessity or independent benefit.

W2. Training cost and amortization

Approximately 48,000–64,000 reward generations per policy constitute substantial training cost, excluding BC, validation, and development.

Without matched training and serving measurements, “train once, serve many” is a possible deployment setting, not demonstrated cost-effectiveness. We will remove implications that query volume necessarily makes NDP cheaper than heuristics.

W3. Sparse reward and critic diagnostics

The critic estimates return from partial histories, and GAE constructs advantages from temporal-difference residuals. This describes the mechanism but does not establish useful credit assignment to early selections.

We lack value-function accuracy and per-step advantage diagnostics and will acknowledge this limitation. We will also correct the statement that PPO clipping “ensures monotonic improvement”; the clipped objective provides no such guarantee.

W4. Transfer failures and framing

Isolated positive cases do not establish general transfer capability. Cross-dataset transfer can underperform random selection, and cross-model transfer is mixed.

We will present transfer as a limitation analysis. Source-specific preferences and domain mismatch remain hypotheses; the results do not establish a reliable criterion for transfer success.

W5. Missing learned selectors and curriculum baselines

Thank you for identifying Partial2Global, LLM-R, and CDS. We will add related-work positioning and acknowledge that superiority over supervised selectors or curriculum ordering is unestablished.

NDP’s history-conditioned policy differs from ranking or feedback-trained retrieval, but this alone establishes no advantage. Likewise, permutation tests show order sensitivity, not superiority over complexity-based curricula or an optimal order.

Q1. Why omit BC-only evaluation?

We have no methodological reason that makes this omitted control unnecessary. PPO’s benefit over initialization remains unresolved; we will attribute results to the combined pipeline rather than infer the missing comparison.

Q2. Training seeds and evaluation resampling

We will explicitly report these counts. We have no additional independent-run results or significance tests to report.

Small headline differences should therefore not be interpreted as established improvements beyond experimental variability. Shot-count curves do not substitute for seed or resampling uncertainty.

Q3. MMICES or text-conditioned retrieval

Question-aware retrieval is feasible with appropriate cached representations. Our image-only restriction holds retrieval features fixed; it does not establish the strongest VQA system.

We will qualify the findings as comparisons among evaluated image-only selectors, not superiority over MMICES or text-conditioned NDP.

Q4. Selector latency and break-even volume

We lack matched selector latency measurements over the same 8,192-candidate pools and cannot provide a numerical break-even count.

For training cost CtrainC_{train} and matched per-query costs cNDPc_{NDP} and cHc_H, a compute-cost crossover exists only when cHc_H exceeds cNDPc_{NDP}:

Q>CtraincH−cNDP.Q > \frac{C_{\mathrm{train}}}{c_H-c_{\mathrm{NDP}}}.

Otherwise, increasing volume spreads training overhead but never makes NDP cheaper. Generation counts alone cannot establish compute savings; we will distinguish predictive utility from efficiency.

Q5. Explaining transfer outcomes

Qwen UTKFace transfer MAE of 5.98 versus 6.28 in-domain does not establish reliable superiority without uncertainty estimates. Neither beats zero-shot MAE of 5.49.

We lack embedding-overlap or dataset-statistics analyses explaining this difference or the EmoSet-to-Food-101 failure. Source-specific preferences, model-response differences, and optimization variability are possible explanations, not validated mechanisms.

Thank you again. We hope these clarifications and revisions address your concerns and would appreciate reconsideration of the score if you find them sufficient.

Reviewer_6sjBOpenReview ↗

Thank you for your reply

I thank the authors for the detailed responses to my comments. Given that the authors acknowledge limitations and narrow the statements on most issues, I am inclined to maintain my original rating.

Reviewer_TZo1OpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
3
Read review
Paper summary

This paper proposes autoregressive next-demonstration prediction to jointly address demonstration selection and ordering in multi-demonstration visual in-context learning. The method uses MMR for initialization, followed by reinforcement learning with PPO, using downstream task performance as the reward. Experiments on VQA and other tasks demonstrate its effectiveness and highlight the impact of autoregressively constructed demonstration order on performance.

Critical strengths
  1. The paper is well written and easy to follow, with a clear and straightforward method.
  2. Jointly modeling demonstration selection and ordering is a reasonable technical approach.
  3. The evaluation covers a broad range of datasets, and the results are reported transparently.
Critical weaknesses
  1. The distinction from existing sequential retrieval methods is insufficiently established. Since the paper already discusses IterR and LSD, formulating demonstration selection as sequential decision-making is not itself novel. The authors should clarify and empirically isolate the benefits of the Perceiver, the autoregressive architecture, and the terminal reward, showing what each contributes beyond existing approaches.
  2. The limited transfer performance raises concerns about generalization. Improving generalization would strengthen the method’s practical value and broaden its applicability.
Questions for authors

See the weaknesses.

2 comments

Thank you for recognizing the clear presentation, joint selection-and-ordering approach, and evaluation breadth. We address your two weaknesses and associated questions below.

W1. Sequential-retrieval novelty and component attribution

We agree that sequential demonstration selection is not itself novel. IterR and LSD are relevant predecessors, and we will revise the contribution statement to avoid suggesting otherwise.

NDP combines a Perceiver representation of the candidate pool, a history-conditioned autoregressive Transformer policy, and MMR behavioral cloning followed by PPO with terminal task rewards. The evaluated IterR implementation uses a GRU-based sequential policy, while LSD uses a DQN-based regression selector. These are methodological distinctions, not evidence that every NDP component is necessary.

We do not have controlled ablations isolating the Perceiver, decoder architecture, or terminal reward. The permutation experiments show that changing the order of NDP’s selected examples affects performance; they do not establish that its architecture or PPO training is required for this effect. We will make these boundaries explicit and frame the contribution as the complete system and its evaluated behavior.

W2. Limited transfer and generalization

We agree that the transfer findings restrict practical applicability. Cross-dataset transfer fails in the examined settings, and cross-model transfer is mixed rather than uniformly beneficial.

We will present these experiments as an applicability analysis, not evidence of general transfer capability. Freezing the VLM does not make the selector automatically reusable: separately trained target-model policies incur additional training, while frozen-policy transfer requires validation. We will remove recommendations implying reliable cross-domain reuse or established cost-effectiveness.

Q1. Component benefits and stronger generalization

The current evidence does not identify each component’s contribution or establish when transfer will succeed. These questions require controlled evidence beyond the existing experiments.

Our supported findings are narrower: the complete system has task-dependent performance, and its predicted order outperforms the tested permutations in the evaluated in-domain settings. We will distinguish these observations from unverified architectural and generalization claims.

Thank you again for the constructive feedback. We hope these revisions clarify the contribution and its limitations and would appreciate reconsideration of the score if they sufficiently address your concerns.

Thank you to the authors for addressing my concerns. However, as the method’s limitations cannot be overlooked, I am inclined to maintain my initial assessment.

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

This paper introduces Next Demonstration Prediction (NDP), which trains a selector to choose and order a small set of demonstrations for a frozen vision-language model (VLM). Its central premise is that the most similar demonstrations are not necessarily the most useful ones, so selection should be optimized directly for downstream task performance rather than for a proxy such as similarity. NDP first uses behavioral cloning (BC) to imitate MMR and then applies PPO to refine the selector. The problem is relevant, and optimizing for downstream performance is a meaningful alternative to similarity-based selection. However, the reported results raise concerns about the reliability of the empirical evidence, and the paper’s contribution relative to prior work needs to be clarified.

Critical strengths

1.The paper targets an important problem: selecting demonstrations that improve downstream in-context learning performance, rather than assuming that the most similar examples will be the most effective.

2.The approach does not require fine-tuning the VLM, which may make it easier to adapt across models and tasks.

3.Using BC to initialize the selector from MMR, followed by PPO-based refinement, is a reasonable training strategy. The staged approach could help make policy optimization more stable.

Critical weaknesses
  1. In Table 1, the results for SCUT and KADID are identical across two columns. In Table 2, the Qwen results for Emo and VQA are also identical in several rows. These repeated values are a serious concern and make it difficult to assess the reliability of the results.

  2. The reported gains are small, but the paper does not provide significance analyses, results averaged over multiple random seeds, or an evaluation of sensitivity to noise. The observed gains could therefore reflect experimental variability.

  3. A 2026 comparison baseline appears in the first table, but is missing from the other tables. This makes it harder to judge NDP’s performance consistently across the reported experiments.

  4. In particular, the paper does not report a BC-only result without PPO. It is therefore unclear whether the gains come from BC, PPO, or their combination.

  5. The paper combines existing ideas and training methods to select demonstrations. A CVPR 2025 work, Provoking Multi-modal Few-Shot LVLM via Exploration-Exploitation In-Context Learning, also uses reinforcement learning to select multimodal example combinations. In addition, IJCAI-26 paper, “Performance-Driven Demonstration Selection for In-Context Learning” (PDDS), makes essentially the same core argument: selection based on proxy signals such as similarity may not align with downstream ICL performance, and selection should instead be optimized for that performance. The paper should more clearly explain how NDP differs from these works.

Questions for authors
  1. Are the identical results for SCUT and KADID in Table 1, and for Qwen on Emo and VQA in the initial rows of Table 2, intentional? Could you verify these entries and provide corrected results or an explanation?

  2. Can you report results across multiple random seeds, including means and variability, and provide statistical significance tests for the observed gains? How sensitive are the results to noise?

  3. Why is the 2026 baseline included only in the first table? Can you provide consistent comparisons with relevant baselines across the remaining experiments?

  4. What are the results of using BC alone, without PPO? Such an ablation would help identify the contribution of each training stage.

  5. What are the specific methodological differences between NDP and the CVPR 2025 VLM reinforcement-learning-based selection work and PDDS? Beyond the shared motivation of optimizing demonstration selection for downstream performance, what is the paper’s distinct contribution?

2 comments

Thank you for identifying the reporting concerns and relevant prior work. We address your five weaknesses and corresponding questions below.

W1 / Q1. Repeated table entries

We agree that the repeated SCUT/KADID columns and Qwen EmoSet/VQAv2 entries require verification against the underlying records. We cannot responsibly explain systematic repetition as rounding or coincidence without that verification.

We do not have a verified correction or explanation to report here. We will audit the dataset-to-result mapping and table construction, correct any affected entries and averages, and revise conclusions if the rankings change. These entries should not be treated as independently verified evidence until that reconciliation is complete.

W2 / Q2. Variability, significance, and noise

The manuscript does not adequately document independent training seeds, evaluation resampling, and uncertainty. We will make the experimental counts and aggregation protocol explicit rather than imply that shot-count variation establishes across-seed robustness.

We do not have additional multi-seed or noise-sensitivity results to report. Consequently, small gains should be interpreted as descriptive differences, not statistically established improvements. We will qualify the conclusions accordingly. Evaluation-sample uncertainty, even if computed from saved predictions, would not substitute for variability across independently trained policies.

W3 / Q3. Coverage of the 2026 baseline

We understand this concern to refer to LSD. It is included on the five regression tasks in Table 1, but not in the classification, VQA, cross-model, or transfer comparisons.

We will state this coverage explicitly and avoid implying an identical baseline suite across all experiments. Its regression-focused formulation explains the reported scope but does not eliminate the comparison gap. We will not claim superiority over LSD outside the evaluated conditions.

W4 / Q4. Missing BC-only checkpoint

We agree that MMR is not equivalent to the BC-only neural selector. Without evaluating the Stage-1 checkpoint, we cannot separate BC’s contribution from PPO’s.

We do not have those results and will remove claims attributing the NDP–MMR gap specifically to PPO. The reported performance belongs to the complete BC-plus-PPO system.

W5 / Q5. Positioning relative to prior work

Thank you for highlighting the CVPR 2025 exploration–exploitation method and PDDS. We agree that neither RL-based multimodal selection nor optimizing selection for downstream performance is new.

NDP’s specific implementation combines a Perceiver candidate representation, a history-conditioned autoregressive Transformer selector, and MMR behavioral cloning followed by PPO using terminal VLM task rewards. We will position this combination relative to the existing methods, rather than claim novelty for RL selection or performance alignment themselves.

In particular, PDDS’s performance-prediction-and-selection approach and NDP’s history-conditioned next-action policy pursue the same broader goal through different mechanisms. These distinctions do not establish superiority without direct comparisons. We will narrow the contribution to the specified system and its empirical analysis, including same-set order sensitivity and transfer failures.

Thank you again for the detailed feedback. We hope the clarified positioning and reporting revisions address your concerns. We would appreciate reconsideration of the score if you find them sufficient, recognizing that the table-verification issue requires concrete resolution.

I thank the authors for their detailed response. The rebuttal addressed some of my concerns; however, after considering the other reviewers' feedback as well, I believe the current score is consistent with my overall assessment of the paper, and I therefore maintain my score.

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

This paper introduces Next Demonstration Prediction (NDP), which casts visual in-context demonstration selection as a sequential Markov Decision Process. A Perceiver encoder compresses the candidate pool, and an autoregressive Transformer decoder selects demonstrations one at a time. Training has two stages. First, behavioral cloning from Maximal Marginal Relevance (MMR) provides a warm start. Then PPO fine-tuning optimizes a frozen VLM’s task reward. On 14 benchmarks with Gemma 3 4B-it at K=16, NDP achieves the best average regression MAE and VQA accuracy among image-only selectors but trails DPP on classification. Cross-dataset transfer is reported as a negative result.

Critical strengths

The strongest contribution is the principled formulation of demonstration selection as an ordered MDP, backed by convincing evidence that ordering matters. The permutation experiments in Table 3 show that shuffling or reversing the same selected images degrades performance, which validates the sequential modeling choice in a way that ablation over selection alone would not. The qualitative analysis in Figure 3 is also very interesting. The discovered anchor-then-boundary-then-scale curriculum gives interpretable structure to what the policy learns and connects naturally to the quantitative gains on regression tasks like AVA.

Critical weaknesses

The most consequential gap is the missing evaluation of the behavioral-cloning-only checkpoint. Without this comparison, the paper cannot disentangle how much improvement comes from PPO versus the MMR warm start. The authors acknowledge this limitation but do not address it, leaving the central claim about RL’s contribution unsupported. Second, the VQA evaluation restricts retrieval to image-only features while question text is available at inference. Excluding question-aware baselines like MMICES makes the VQA comparisons incomplete, yet VQA is presented as one of the three primary evaluation domains and figures into the headline results.

I will consider raising my score if the authors provide relatively comprehensive baseline of the behavioral-cloning-only checkpoint to address my first point and the results look positive.

Questions for authors
  1. Evaluating the BC-only checkpoint appears straightforward and would directly clarify PPO’s marginal contribution beyond the MMR warm start. Was there a specific reason this ablation was omitted, and can you provide those numbers?
  2. The training cost discussion reports approximately 48,000 to 64,000 VLM generations per policy but omits wall-clock time, GPU-hours, and any estimate of the break-even query count. At roughly what downstream query volume does NDP become cost-effective compared to MMR or DPP?
  3. The permutation sensitivity results show that learned ordering helps, but could a simpler deterministic curriculum (for instance, ordering by decreasing similarity followed by increasing diversity) capture much of this effect without requiring RL training at all?
1 comment

Thank you for the constructive review and for recognizing the ordered-selection formulation, permutation analysis, and qualitative findings. We address your concerns below.

W1. Missing BC-only evaluation

We agree that comparing final NDP against MMR does not isolate PPO’s contribution. A learned MMR imitator need not reproduce its teacher exactly, so differences may arise during either behavioral cloning or PPO.

Our evaluation omitted the BC-only checkpoint, and we do not have those results to report. We will remove statements attributing the NDP–MMR gap specifically to PPO, including “The NDP vs. MMR gap is the PPO stage.” The supported results concern the complete BC-plus-PPO pipeline; PPO’s marginal benefit remains unresolved. The permutation analysis likewise does not establish that PPO is necessary.

W2. Question-aware VQA baselines

We agree that holding image features fixed provides a comparison within an image-only retrieval setting, not a complete VQA comparison. Question text is available at inference, and excluding it limits the selector’s information.

We will consistently qualify the VQA findings as comparisons among the evaluated image-only methods, not superiority over MMICES or other question-aware selectors. This restriction is an experimental scope choice, not a technical reason question-aware retrieval could not be implemented.

Q1. Reason for omitting BC-only results

The experimental design did not include separate evaluation of the Stage-1 checkpoint. We recognize this as a missing control, not something resolved by evaluating MMR itself. Without those results, we cannot determine whether PPO improves on BC alone and will revise the claims accordingly.

Q2. Training cost and break-even query volume

The reported configurations imply approximately 48,000–64,000 VLM reward generations per policy, excluding BC, validation, and development. We do not have matched wall-clock, GPU-hour, or selector-latency measurements and therefore cannot provide a defensible numerical break-even count.

Amortizing training does not necessarily make NDP cheaper than MMR or DPP: all still require downstream VLM inference. A compute-cost crossover exists only if NDP has a lower per-query cost. Otherwise, its justification must be improved predictive utility, not compute savings. We will revise the deployment discussion to make this distinction explicit.

Q3. Could deterministic ordering capture the effect?

Yes; our experiments do not rule this out. Permuting the same selected examples establishes order sensitivity in the tested settings, but not superiority over a deterministic curriculum. The anchor–boundary–scale interpretation is descriptive, not proof that RL is required. We will narrow the ordering claim and acknowledge the missing curriculum comparison.

Thank you again for the helpful feedback. We hope these clarifications and corresponding revisions address your concerns and would appreciate reconsideration of the score if you find them sufficient.

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

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