acceptodds
Withdrawn from ICLR 2027

SR-Search: Structured Routing of Search and Refine Information Gains for Fine-Grained Credit Assignment

Withdrawn from ICLR 2027, so left out of the paper lists and the map.

Abstract

Reinforcement learning (RL) has become a dominant paradigm for enhancing retrieval-augmented generation (RAG) in large language models. However, existing frameworks such as Search-R1 rely on trajectory-level outcome rewards assigned to all generated tokens along an execution path. This coarse and sparse signal cannot credit intermediate decisions, and in complex multi-hop question answering (QA) it fails to isolate whether a specific retrieval acquired relevant information or whether the subsequent refinement preserved and used that evidence. To address these limitations, we propose SR-Search, a fine-grained credit-assignment framework for search agents trained via Group Relative Policy Optimization (GRPO). Within each valid search–refine cycle, the policy evaluates the log-probability of the ground-truth answer before search, after retrieval, and after refinement; the resulting likelihood differences define Search Information Gain (SIG) and Refinement Information Gain (RIG), respectively, without any auxiliary reward model. SR-Search routes SIG to search actions and RIG to refinement actions, and further introduces a short-horizon delayed advantage that propagates refinement gains backwards to optimize the preceding retrieval decisions. Across seven QA benchmarks, SR-Search outperforms outcome-reward baseline AutoRefine by 3.7 points and the strongest step-reward baseline GiGPO by 2.1 points. These results demonstrate that temporally localized credit assignment can improve both retrieval and evidence refinement in RL-based search agents.

Primary area:
reinforcement learning
Keywords:
Reinforcement Learning、Retrieval-Augmented Generation、LLM Agents、Credit Assignment、Multi-hop Question Answering、Process-Level Supervision

Reviews

Among:
Shape:
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_akijOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

SR-Search proposes action-specific credit assignment for search-and-refine agents trained with GRPO. The old policy evaluates the gold-answer log-likelihood before search, after retrieval, and after refinement. The resulting search and refinement information gains are normalized separately and assigned to their corresponding action spans, with a fraction of refinement credit also propagated back to the same-cycle search. The paper evaluates Qwen2.5-3B and 7B Base/Instruct models on seven QA benchmarks, reporting improvements over AutoRefine and step-reward baselines. Validation includes component ablations, training dynamics, search-frequency analysis, and a reported 11.2% increase in per-step training time.

Critical strengths
  1. Separating evidence acquisition from evidence refinement is a useful and practically motivated credit-assignment design. The method provides dense supervision using the existing policy and gold answers, without requiring a separate critic, process reward model, or step-level annotations.

  2. The reported improvements extend across seven benchmarks and two model sizes. The component ablations and computational-cost analysis provide useful evidence about the method’s practical behavior and tradeoffs, beyond final-answer accuracy alone.

Critical weaknesses
  1. The main comparisons are insufficiently specified to support the claimed attribution of gains to credit assignment. Sections 4.2 and A.2 describe a matched AutoRefine comparison, but the original AutoRefine uses a refinement-dependent retrieval reward in addition to final-answer F1 and reports 250 training steps, versus 300 here. The AutoRefine rows in Table 1 match the original published results. It is therefore unclear which baselines were rerun under matched settings and which results were taken from prior work. The evaluation protocol also needs clarification: with 125 Bamboogle questions, single-run EM changes in increments of 0.008, whereas reported values such as 0.645, 0.641, and 0.383 cannot result from rounding a correct-answer count divided by 125. Averaging across runs could explain this, but repetitions, seeds, and uncertainty are not reported. These issues limit confidence in the comparative conclusions, particularly the 0.003 average improvement over GiGPO with the 7B Instruct backbone.

  2. The experiments do not sufficiently isolate the benefit of structured routing from the benefit of adding dense answer-aware supervision. IGPO already uses gold-answer probability gains and backward credit propagation; the distinctive contribution here is the separation and routing of search/refinement credit. Table 2 removes channels or replaces normalized gains with raw gains, but does not keep the information signals and their scale comparable while changing the routing. A matched cycle-level or uniform-routing control would directly test the central contribution. Moreover, the answer-containment metrics in Figure 3 do not establish that retrieved or refined content supplies the evidence needed for the inference. The reported analyses therefore support a useful training configuration more clearly than the proposed credit-assignment mechanism.

Questions for authors
  1. Clarification: Which baseline rows were retrained and reevaluated in your environment, and which were taken from published results? For AutoRefine specifically, was its original retrieval-specific reward retained, and what training budget was used?

  2. Clarification: What evaluation procedure produces the reported Bamboogle values given its 125 questions? Please specify the metric implementation, number of runs, aggregation procedure, and uncertainty, including for the comparison with GiGPO.

  3. Evidence request: Under identical interaction, outcome-reward, and training-budget settings, does structured SIG/RIG routing outperform a control that uses the same scoring checkpoints but assigns a cycle-level information-gain signal uniformly to search and refinement actions, with comparable reward scaling?

2 comments

Thank you for the specific questions. The revised paper adds baseline provenance and a three-seed study that reproduces SR-Search's main performance result.

Q1 / Weakness 1. Baseline sources, AutoRefine reward, and budget

Section 4.1 and Appendix A.3, Table 6 (pp. 13-14) distinguish quoted results from our experiments. All non-SR-Search main-table rows are quoted, not retrained or reevaluated by us. SR-Search results, ablations, sweeps, behavior/cost measurements, and new seed runs are our experiments.

Table 6 lists AutoRefine as the numerical source for Direct Generation, SFT, R1, Naive RAG, IRCoT, Search-o1, Search-R1, and AutoRefine; GiGPO for StepSearch and GiGPO; and IGRPO for IGPO. The appendix specifies that IGPO EM values come from the IGPO rows in IGRPO v1. The baseline seed statistics come from AutoRefine Appendix C.2, Table 7.

AutoRefine's quoted results include its original refinement-dependent retrieval reward; we did not replace it with an outcome-only reward.

SR-Search trains for 300 steps on eight A100-80GB GPUs; AutoRefine's published hyperparameter table lists 250 steps. Figure 3(a) shows SR-Search's training reward reaching a plateau before step 250, with limited later improvement. Its reward advantage is already visible before the additional 50 steps. This addresses convergence timing, rather than constituting a matched-budget final-EM rerun.

Q2 / Weakness 1. Bamboogle aggregation and variability

Evaluation uses greedy decoding (temperature=0, n=1), one rollout per question, and binary EM after answer extraction and normalization. Our loader is:

self.val_dataloader = DataLoader(
    dataset=self.val_dataset,
    batch_size=self.config.data.val_batch_size,
    shuffle=True,
    drop_last=True,
    collate_fn=collate_fn,
)

It shuffles a mixed-dataset pool and drops the final incomplete batch. EM is computed over retained questions, so Bamboogle's denominator can differ from 125. Archived EM and action-count metrics reconstruct counts of 118-125 for Bamboogle and 484-498 for the other six datasets. This explains non-1/125 values from this evaluator, without multiple-rollout averaging. The overall score is the unweighted mean of seven dataset scores.

The quoted IGPO/GiGPO values were not generated by this loader. GiGPO's public search-QA code retains the last batch but averages episode rewards over records expanded by interaction step, which is not constrained to multiples of 1/125. Table 6 identifies the sources rather than implying a common evaluator.

Appendix B.1, Table 7 (pp. 14-15) reports three independent SR-Search runs, one per seed. Qwen2.5-3B-Base achieves 0.441 +/- 0.009, compared with published three-seed results of 0.408 +/- 0.014 for AutoRefine and 0.315 +/- 0.015 for Search-R1: gains of 3.3 and 12.6 percentage points. SR-Search's mean is higher than AutoRefine's on every benchmark, and closely matches the original 0.442.

Given the limited rebuttal period and multi-GPU cost, we prioritized SR-Search repetitions and quoted baseline seed statistics from AutoRefine Appendix C.2, Table 7. Table 7's two-sided paired tests use seven benchmark means (N=7, df=6): p=7.51e-4 versus AutoRefine and p=3.65e-3 versus Search-R1. These are cross-benchmark tests; the standard deviations separately describe seed variation.

The new repetitions concern 3B Base, not the Instruct models. They do not supply uncertainty estimates for the small 7B Instruct gap against GiGPO.

Q3 / Weakness 2. Simpler information-gain assignment and routing

We tested a trajectory-level alternative during development, aggregating action-level information gains into the outcome reward. Its overall performance was approximately at the AutoRefine level, without the improvement of the final action-specific design.

SR-Search preserves which stage produced each gain: SIG goes to search, RIG to refinement, and bounded same-cycle RIG feedback goes to the search supplying the input. This differs from adding answer-aware supervision alone or propagating a single turn-level gain. Table 2's channel ablations provide complementary support. We have not completed the scale-matched cycle-uniform control.

Figure 3 and Appendix E connect the signals to answer-related behavior. RIG is a likelihood-based utility signal; answer containment is not itself proof of document support. The QA, ablation, and repeated-run results support the training method's practical effectiveness.

We hope the new evidence and clearer provenance address your concerns, and respectfully ask you to consider a more favorable score.

Dear Reviewer, thank you again for your review. We have posted our detailed response and added new three-seed results and baseline-source clarifications to the revised manuscript. With limited time remaining for discussion, we would appreciate your feedback and any remaining questions as soon as possible, so that we can address them before the discussion closes. Thank you for your time and consideration.

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

SR-Search trains a search-augmented language model with separate search and refinement stages. It constructs information-gain rewards from changes in the old policy's gold-answer log likelihood before retrieval, after retrieval, and after refinement. The rewards are normalized separately and assigned to the corresponding action spans. Part of the refinement gain is also passed back to the preceding search through a short-horizon delayed advantage. These rewards supplement terminal-answer reinforcement learning without requiring a learned critic. Experiments cover seven QA benchmarks and 3B/7B backbones, with component ablations and a training-time breakdown.

Critical strengths
  1. A search may become useful only after its results have been refined. Immediate retrieval feedback can therefore undervalue a good search, and passing back refinement reward is a reasonable way to address this. The method does not require a separately trained critic. Using gold answers to construct training rewards is also appropriate here and does not itself imply test leakage.

  2. Table 1 reports average EM of 0.442 for the 3B base model, compared with 0.405 for AutoRefine-Base. Table 2 shows substantial drops when either direct reward, delayed credit, or normalization is removed. The paper also includes 7B results and measures the added training cost: step time rises from approximately 239.5 to 266.5 seconds. This gives a concrete view of the overhead despite the absence of a critic.

Critical weaknesses
  1. The ablations change reward strength as well as credit assignment. Removing delayed credit changes both where refinement feedback goes and how much feedback search tokens receive. Removing normalization changes the scale and distribution of the rewards. These results show that the training choices matter, but do not establish that pairing refinement credit with the correct preceding search explains the gain. A comparison that preserves reward magnitude while changing the pairing would help. Gold-answer log-likelihood change is also a training surrogate, and does not by itself measure an action's causal contribution to answer quality. Since earlier work such as StepSearch already uses dense information-gain rewards, the contribution of the proposed routing needs to be clearer.

  2. It is unclear how much the gains over the strongest comparable baselines vary across training runs. For the 3B instruction-initialized models, the averages are 0.432 for SR-Search and 0.421 for GiGPO-Instruct. Comparing SR-Search-Base with GiGPO-Instruct gives a larger gap, but also changes initialization. At 7B, the instruction-matched averages are approximately 0.475 and 0.472. These differences could be useful, but their size makes run-to-run variation important. There is also a large Bamboogle deficit relative to GiGPO in Table 1. Finally, the validation split used for hyperparameter selection needs to be specified so that the protocol can be reproduced; its omission alone does not establish leakage.

Questions for authors
  1. Do any existing experiments keep the total auxiliary-reward magnitude fixed while changing only whether refinement credit is paired with its preceding search? If not, please limit the mechanism claim to what the removal ablations show. A matched comparison would be useful follow-up work.
  2. How many independent training runs were used for the reported averages? Please provide any available uncertainty for comparisons with the same initialization, especially the small 7B gap from GiGPO. How were results aggregated on the 125-example Bamboogle benchmark?
  3. Which split was used to tune the gain weights, delayed-credit coefficient, and normalization choices? Was it disjoint from all reported evaluation splits?
2 comments

Thank you for recognizing the motivation for linking refinement feedback to search. The revised paper adds three-seed results and explicit baseline sources.

Q1 / Weakness 1. Reward magnitude, pairing, and contribution

SHDA follows the search-refine dependency: refinement uses documents from its preceding search. A search with little immediate gain may provide material that becomes useful after refinement. Same-cycle feedback credits that search, while the coefficient lambda bounds the feedback and reuses RIG without extra scoring.

Removing SHDA lowers average EM from 0.442 to 0.411 (Table 2). This tests the delayed channel's contribution; it is not a fixed-magnitude pairing-permutation test, which we have not run. Removing normalization also changes signal scale, so its ablation evaluates calibration rather than pairing.

During development, we also aggregated action-level gains into the outcome reward. Performance remained approximately at the AutoRefine level. The final design keeps separate signals for search and refinement and assigns them to the corresponding actions.

StepSearch and IGPO already use dense information-gain supervision. Our contribution is the separation of search and refinement within a cycle, independent normalization, and bounded refinement feedback to the search supplying its input. Likelihood gain is a training signal, not an estimate of each token's causal effect. The component ablations support the reported design; they do not isolate pairing from reward magnitude.

Q2 / Weakness 2. Independent runs, matched initialization, and Bamboogle

Appendix B.1, Table 7 (pp. 14-15) reports three independent Qwen2.5-3B-Base runs, one per seed. SR-Search obtains 0.441 +/- 0.009 average EM, close to the original single-run 0.442. Published three-seed means are 0.408 +/- 0.014 for AutoRefine and 0.315 +/- 0.015 for Search-R1. The gains are 3.3 and 12.6 percentage points. SR-Search's mean exceeds AutoRefine's on all seven datasets.

Table 7's two-sided paired tests use seven benchmark means (N=7, df=6): p=7.51e-4 versus AutoRefine and p=3.65e-3 versus Search-R1. These test cross-benchmark differences; the standard deviations describe training-seed variation.

Given the limited rebuttal period and multi-GPU cost, we prioritized SR-Search repetitions and used published baseline seed statistics from AutoRefine Appendix C.2, Table 7. Appendix A.3, Table 6 identifies the quoted sources; Sections 4.1-4.2 refer to the additions.

These new repetitions are 3B Base results. The Instruct-to-Instruct GiGPO gaps remain 0.011 at 3B and 0.003 at 7B; we do not use Base-run variability to characterize them. The 2.1-point headline comparison uses different initializations.

Evaluation uses greedy decoding, one rollout per question, and binary normalized-answer EM. The loader is:

self.val_dataloader = DataLoader(
    dataset=self.val_dataset,
    batch_size=self.config.data.val_batch_size,
    shuffle=True,
    drop_last=True,
    collate_fn=collate_fn,
)

Shuffling the mixed pool and dropping the incomplete final batch changes each dataset's retained count. Archived metrics reconstruct Bamboogle counts of 118-125, so EM need not be a multiple of 1/125. This is a denominator effect, not rollout averaging. Overall EM averages the seven dataset scores equally. Quoted baseline numbers follow their source protocols.

SR-Search remains below GiGPO's quoted Bamboogle score. Our multi-hop improvement is an aggregate trend, not superiority on every benchmark.

Q3 / Weakness 2. Hyperparameter and checkpoint selection

Figure 4 varies one parameter at a time, with the others fixed, selecting alpha_S=0.05, alpha_R=0.1, and lambda=0.1. Clipping bounds are fixed at (1.0, 2.0); normalization is assessed by the w/o-Norm ablation. We use best-checkpoint selection rather than automatically taking the last step.

The selection questions come from the same benchmark evaluation pools as the reported results; they are not disjoint. Here, validation means the data used for parameter/checkpoint selection, not a separate untouched test set. The new seed study measures training variability under this protocol.

We hope these results and clarifications strengthen your assessment of the contribution, and would appreciate your consideration of a more favorable score.

Dear Reviewer, thank you again for your review. We have posted our detailed response and added new three-seed results and baseline-source clarifications to the revised manuscript. With limited time remaining for discussion, we would appreciate your feedback and any remaining questions as soon as possible, so that we can address them before the discussion closes. Thank you for your time and consideration.

Reviewer_6btGOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

SR-Search is a credit-assignment method for search agents trained with GRPO. It uses the old policy's log-likelihood of the gold answer at three checkpoints: before a search query, after retrieval, and after refinement. The successive differences define Search Information Gain (SIG) and Refinement Information Gain (RIG). After separate group-wise normalization and clipping, the method routes SIG to search tokens and RIG to refinement tokens, and returns a fraction of the same-cycle RIG to the preceding search. It needs no separately trained reward model. Experiments on seven QA benchmarks with Qwen2.5-3B and Qwen2.5-7B report gains over AutoRefine, supported by component ablations, behavioral analyses, and a training-cost breakdown.

Critical strengths
  1. A practical design for action level credit. Specifically, Search and refinement have different roles, and the method assigns them distinct signals rather than sharing only a terminal outcome reward. Same-cycle feedback addresses the plausible case in which retrieved evidence becomes useful only after refinement. The design fits an existing GRPO pipeline without an auxiliary learned critic or process-reward model (Sections 3.2–3.5).

  2. Encouraging gains over the closest baseline. The Base-backbone average EM increases from 0.405 to 0.442 at 3B and from 0.455 to 0.482 at 7B relative to AutoRefine. Every ablation in Table 2 lowers average EM, providing initial support for the components. The cost breakdown in Section 5.5 also makes the additional scoring expense visible rather than treating the method as computationally free.

Critical weaknesses
  1. Evaluation transparency and robustness of the main comparisons. Tables 1–3 do not report the number of independent training runs, variability across runs, or confidence intervals. This matters particularly for the strongest step-reward comparisons. The matched Instruct-backbone gains over GiGPO are 0.011 at 3B and only 0.003 at 7B. The headline 2.1-point advantage at 3B instead compares SR-Search-Base with GiGPO-Instruct. The paper does provide matched Instruct comparisons, so the issue is not a complete absence of controls, but the smaller matched gains and the lack of uncertainty estimates. A Base-backbone comparison with GiGPO/IGPO, if available, would clarify the stronger headline claim. The Bamboogle score aggregation also needs explanation. Appendix Table 4 lists 125 examples. Under a single evaluation with one binary EM outcome per example, scores would change in increments of 1/125 = 0.008. Values such as 0.383 for SR-Search-Instruct and 0.645/0.641 for IGPO/GiGPO-Instruct cannot result from that protocol after rounding to three decimals. Averaging runs or samples, or using a different effective sample count, could explain them; this is a clarification request, not evidence of misconduct. Because Bamboogle enters the seven-dataset average with equal weight, its protocol and the provenance of the baseline scores affect confidence in the overall ranking (Tables 1–4, Appendix A).

  2. The contribution of structured routing is not sufficiently isolated. The ablations show that removing individual channels hurts, but do not directly establish that routing the same information-gain signal to specific actions is better than a simpler reward-shaping scheme. A control that keeps the gain information and approximately matches its scale, but distributes it uniformly over generated tokens or assigns the combined cycle gain to search, would help isolate the value of the routing in Equations 7–9. This distinction matters because structured routing is a central claimed contribution, not merely an implementation detail (Table 2).

The mechanism analysis also does not fully establish evidence grounding. Figure 3 measures whether retrieved documents and refinements contain the gold answer; Appendix E gives useful qualitative examples. Neither, however, systematically tests whether refinements are supported by retrieved evidence. RIG can in principle increase when a refinement asserts the answer without document support, and SIG includes both the query and retrieved documents by design. I am not arguing that these definitions are intrinsically invalid. Rather, the evidence supports improved QA scores more directly than it supports reliable attribution of evidence acquisition and faithful preservation. A targeted grounding or counterfactual analysis would test that stronger interpretation (Equations 4–5, Figure 3, Section 6).

Questions for authors
  1. How many independent training runs and evaluation samples underlie each main result? Please specify the decoding settings, effective Bamboogle sample count, and aggregation rule that produce values such as 0.383, 0.645, and 0.641 on a nominal 125-example set. Were the strongest baseline scores reproduced under the same protocol or taken from prior reports? Can you provide variability estimates, especially for the matched Instruct comparisons with GiGPO, and Base-backbone results if available?

  2. Do you have a control that preserves the information-gain signals and approximately matches their scale, but uses uniform trajectory-level credit or a simpler cycle-level assignment instead of the proposed routing? This would help determine whether the gains arise specifically from structured credit assignment rather than additional reward shaping.

  3. Beyond Figure 3 and the qualitative examples, is there evidence that positive RIG corresponds to refinements supported by retrieved documents? For example, with the documents fixed, do faithful refinements receive different credit from unsupported answer-asserting refinements?

1 comment

Thank you for the constructive review. We added a three-seed study and a baseline-source table to the revised paper.

Q1 / Weakness 1. Repeated runs, evaluation, and baseline sources

Appendix B.1, Table 7 (pp. 14-15) reports three independent Qwen2.5-3B-Base training runs, one per seed. SR-Search achieves 0.441 +/- 0.009 average EM, closely matching the original single-run 0.442. The published three-seed results are 0.408 +/- 0.014 for AutoRefine and 0.315 +/- 0.015 for Search-R1. SR-Search improves their means by 3.3 and 12.6 percentage points, respectively, and exceeds AutoRefine on all seven benchmarks.

Table 7 reports two-sided paired t-tests on the seven benchmark means (N=7, df=6): p=7.51e-4 versus AutoRefine and p=3.65e-3 versus Search-R1. These tests measure cross-benchmark differences; the standard deviations measure variation across training seeds.

Given the limited rebuttal period and multi-GPU training cost, we prioritized new SR-Search runs and quoted baseline three-seed statistics from AutoRefine Appendix C.2, Table 7. Appendix A.3, Table 6 identifies all baseline sources; non-SR-Search main-table results were not rerun in our environment. Sections 4.1-4.2 now point to these additions.

The new runs concern 3B Base. The Instruct-to-Instruct comparisons with GiGPO remain 0.432 vs. 0.421 at 3B and 0.475 vs. 0.472 at 7B. We distinguish these from the Base-to-Instruct 2.1-point difference. No Base GiGPO/IGPO reruns are available.

Evaluation is greedy (temperature=0, n=1), with binary normalized-answer EM. We average retained questions within each dataset, then average the seven dataset scores equally. The loader is:

self.val_dataloader = DataLoader(
    dataset=self.val_dataset,
    batch_size=self.config.data.val_batch_size,
    shuffle=True,
    drop_last=True,
    collate_fn=collate_fn,
)

Because it shuffles the mixed pool and drops the incomplete last batch, Bamboogle's effective count can be below 125. Archived metrics reconstruct counts of 118-125, explaining how this evaluator can produce non-1/125 scores such as 0.383. This is not multiple-rollout averaging; these archived counts do not recover every main-table cell's exact denominator.

The quoted IGPO/GiGPO scores 0.645/0.641 have separate sources. GiGPO's public search-QA code retains the last batch but averages episode rewards over records expanded by interaction step; this aggregate need not be a multiple of 1/125. We distinguish that code path from our retained-question EM, rather than assigning all three scores the same cause.

Q2 / Weakness 2. Trajectory-level information-gain rewards

Yes. During development, we aggregated action-level information gains into the outcome reward. Overall performance was approximately at the AutoRefine level, without the improvement of the final action-specific design.

A useful search can be followed by poor refinement, while refinement can reveal value not apparent immediately after retrieval. A trajectory-wide reward gives these actions the same feedback. SR-Search instead gives SIG to search, RIG to refinement, and bounded refinement feedback to the preceding search. Table 2 supports the components: removing SIG, RIG, SHDA, or normalization reduces EM from 0.442 to 0.402, 0.392, 0.411, or 0.372. The development result is qualitative, not a completed scale-matched cycle-level test.

Q3 / Weakness 2: grounding. RIG and evidence support

In Figure 3, rising RIG accompanies improved refinement answer containment and QA reward; Appendix E gives concrete examples. These results support useful answer-related refinement. The final-answer objective remains active alongside local gains.

RIG measures answer-likelihood gain, not document entailment. Figure 3 measures answer containment; we have not added the fixed-document supported-versus-unsupported refinement test. SIG likewise measures the joint effect of query and documents (Eq. 4). We distinguish these measured utilities from a guarantee of document support.

We hope the new reproducibility evidence and clearer evaluation details address your concerns, and respectfully invite you to consider a more favorable score.

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

Related papers

Discussion (0)

Sign in to comment.