acceptodds
Under review as a conference paper at ICLR 2027

WHEN DOES A RANDOM SUBSET PRESERVE THE FULL-BENCHMARK MODEL RANKING?

Abstract

Evaluating large language models (LLMs) is expensive, so a natural strategy is to evaluate each model on only a random subset of benchmark questions. But how many questions are enough? We show that subset size alone is a poor guide: at the same evaluation budget, the agreement between the subset ranking and the full-benchmark ranking can vary substantially across benchmarks. The missing factor is how informative benchmark questions are for distinguishing the particular models being compared. We characterize this using population-relative item discrimination and combine it with classical measurement theory to predict how closely a random subset recovers the full-benchmark model ranking. Across 114 benchmark instances from 11 suites and five evaluation budgets spanning 1%–20%, predicted and observed ranking agreement correlate at , with correlations ranging from to when evaluated separately at each budget. The predictor also estimates the subset size required for a target level of ranking agreement and the potential for further improvements from evaluating more questions. Finally, we show that achievable ranking agreement depends on the model population itself: when evaluated models become more similar, benchmarks can become substantially less informative, and discrimination estimates from a mismatched source population may not transfer. Overall, our results provide a simple way to assess when random sampling can recover full-benchmark rankings, how many questions are needed, and when benchmark properties limit how well a subset can recover the full ranking.

Primary area:
applications to computer vision, audio, language, and other modalities
Keywords:
Large Language Models, Evaluation, Classical Test Theory

Reviews

Among:
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1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_2zFVOpenReview ↗
Rating
3(+1)
Confidence
2
Informativeness
2(+1)
Presentation
2
Soundness
2
Read review
Paper summary

The paper studies when random subsets of an LLM benchmark preserve the full-benchmark model ranking. It combines population-relative item discrimination with the classical Spearman–Brown relationship to predict ranking agreement and estimate evaluation budgets.

Critical strengths

The proposed predictor is easy-to-use, interpretable, and requires no fitted coefficients.

Critical weaknesses

Related work already studies evaluation size, ranking reliability, and population dependence [1,2]. [2] is particularly relevant but is not discussed in Sec. 2. The paper’s main distinctive contribution is therefore using DD as a compact predictor. However, the experiments in Sec. 5 establish its predictive accuracy without comparing it against straightforward alternatives. Since the source models already have full evaluations, repeated random subsampling on their cached responses could directly estimate ranking agreement at each budget. A comparison under the same source-data budget would clarify whether DD provides additional accuracy, stability, or computational benefits. Moreover, Sec. 5.3 does not directly validate whether budgets selected through Eq. 8 achieve the requested agreement on target models. Thus, the reported correlations support the usefulness of the predictor, but its additional practical value remains unclear.

[1] SubLIME: Subset Selection via Rank Correlation Prediction for Data-Efficient LLM Evaluation. ACL '25.

[2] How Reliable is Language Model Micro-Benchmarking? ICLR '26.

Questions for authors
  1. When Eq. 8 selects a budget for a target agreement of 0.9, what agreement is actually achieved on target models? It's better to report deviations from the target, particularly for low-DD instances and small source pools.

  2. Sec. 4 explicitly distinguishes latent-ability reliability from agreement with the full-benchmark ranking. How should the ceiling and “unreachable targets” in Sec. 5.3 be interpreted for the objective in Eq. 3, given that evaluating all questions necessarily reproduces the full ranking?

6 comments
AuthorsOpenReview ↗

Thank you + W1.1

Thank you for the careful review. We answer each point below and have updated the revised PDF accordingly.

W1.1 Related work and our contribution

We agree that our main contribution is using population-relative discrimination DD as a compact predictor. We have expanded §2 of the revised PDF to discuss both works and to state this contribution directly: the predictor is parameter-free, closed-form, and depends only on DD and the budget kk.

  • SubLIME [1] trains a model that predicts rank correlation from dataset features and anchor-model evaluations, and uses it to select informative subsets (1–20%). We instead predict the expected agreement of uniform random subsets as a function of their size, without fitting a prediction model, and invert it to get the budget for any feasible subset size.
  • Yauney et al. [2] introduce MDAD to measure empirically which model pairs a micro-benchmark can distinguish. We instead predict overall ranking agreement from DD and the budget before evaluating the target models. The two views are complementary.
  • Agreement with their findings. Yauney et al. find that random sampling becomes competitive with selection methods at larger budgets. SubLIME reports GPQA and MuSR among its hardest cases, and these have the lowest DD in our collection (0.060.06 and 0.100.10). This matches our finding that low discrimination predicts lower ranking agreement under random subsets.

[1] Saranathan et al. SubLIME: Subset selection via rank correlation prediction for data-efficient LLM evaluation. ACL 2025.

[2] Yauney, Warraich, and Swayamdipta. How reliable is language model micro-benchmarking? ICLR 2026.

AuthorsOpenReview ↗

Response to W1.3 + Q1

W1.3 + Q1 Agreement achieved by budgets from Eq. 8

We ran this validation. We estimate DD on source models, compute the budget k⋆k^\star for a target agreement ρ⋆\rho^\star (Eq. 8), sample k⋆k^\star questions, and measure the agreement of disjoint target models with their full-benchmark ranking (the objective in Eq. 3):

Target ρ⋆\rho^\starAchieved agreementDeviation
0.900.899−0.001
0.950.952+0.002
  • On feasible instances (k⋆≤Nk^\star \le N), the budget from Eq. 8 gives the requested agreement on target models that were not used to estimate DD.
  • For 15% of benchmark–population pairs, k⋆>Nk^\star > N. Here the method reports that the target is above the predicted ceiling instead of returning a budget (see Q2).
  • Low-DD instances. Where a budget exists, it is conservative on average: achieved agreement is 0.93 for a target of 0.90. For most low-DD instances, k⋆>Nk^\star > N, so no budget is returned.
  • Small source pools. The results hold for source pools of M=10M=10 and M=30M=30 models.
  • Added as a budget-validation paragraph in §5.3 of the revised PDF.
AuthorsOpenReview ↗

Response to Q2

Q2 Interpreting the ceiling and "unreachable targets" under Eq. 3

We agree this needed clarification. Eq. 3 measures agreement with the finite full-benchmark ranking, which reaches 1 at k=Nk=N. The revised PDF now separates two objectives:

  • Reproducing the full-benchmark ranking (Eq. 3). There is no ceiling below 1. We add a finite-population form, ρfull(k)=ρ(k∣D)/ρ(N∣D)\rho_{\text{full}}(k)=\rho(k\mid D)/\rho(N\mid D), which equals 1 at k=Nk=N and predicts observed full-benchmark agreement at r=0.96r=0.96 (MAE =0.039=0.039).
  • Reproducibility on an independent question set. The ceiling ρ(N∣D)\rho(N\mid D) predicts how reliably the full benchmark measures latent ability, which approximates how well its ranking would reproduce on new questions. It agrees with an independent split-half estimate at r=0.94r=0.94 (MAE =0.017=0.017). This supports it as a ceiling for reproducibility, not for Eq. 3.
  • "Unreachable targets." A target above the ceiling is unreachable only for the reproducibility objective, using the NN available questions. It does not mean the full-benchmark ranking cannot be reproduced. The 15% of pairs with k⋆>Nk^\star > N are those predicted unable to reach the target latent reliability with at most NN questions.
  • Clarified in the §4, §5.3, and Appendix A (derivation of ρfull\rho_{\text{full}}) of the revised PDF.
Reviewer_xeQrOpenReview ↗
Rating
3
Confidence
3
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates how well a downsampled benchmark preserves full-benchmark model rankings. By combining classical item response theory (Spearman-Brown prophecy formula) with population-specific item discrimination, the authors predict ranking correlation as a function of sample size. They test this across 114 benchmark instances, showing strong fits to observed reliability curves, and analyze how rankings degrade when switching model cohorts.

Critical strengths

Clear, practical problem. Knowing how much we can downsample a bloated benchmark without wrecking the leaderboard ranking is useful for real-world eval budgets.

Zero-parameter analytical formula. Deriving the estimate directly via Spearman-Brown without fitting downstream regressors keeps the method clean and easy to adopt.

Good analysis on population sensitivity. Showing that benchmark reliability is not an intrinsic property of the test set, but strongly tied to the cohort of models being

Critical weaknesses

Mismatch between the theory and the evaluation target. The mathematical derivation targets correlation against a theoretical latent ability. But in practice, you evaluate Spearman rank correlation against the finite full-benchmark score. These diverge at the limit. Under your formula, the rankability ceiling can plateau below 1.0, yet by definition, evaluating 100% of the benchmark items gives a rank correlation of exactly 1.0. This mismatch makes the asymptotic predictions awkward to apply in practice.

Missing direct validation on budget planning. The paper pitches this for sample-budget estimation, but never directly tests if the predicted item count actually hits the target ranking stability. For hard, low-discrimination benchmarks where Table 2 shows large estimation errors, does the budget formula systematically under- or over-allocate questions?

Inflated benchmark count. Claiming 114 benchmark instances sounds huge, but many are just granular subject splits within MMLU or similar test suites. The actual dataset diversity is much narrower than the headline number implies.

Questions for authors

Can you run a direct validation for budget sizing? Pick a target rank correlation (e.g. 0.95), compute the predicted question budget, sample that many items, and check the actual observed rank agreement against the full set.

How should a practitioner use your "rankability ceiling" if their sole objective is reproducing the full empirical leaderboard order rather than estimating latent ability?

How sensitive is the discrimination estimate to the sample size of the initial pilot model cohort?

6 comments
AuthorsOpenReview ↗

Thank you + W1 + Q2

Thank you for the positive and careful review. We answer each point below and have updated the revised PDF accordingly.

W1 Mismatch between the theory and the evaluation target

We agree. The derivation predicts correlation with latent ability, while we evaluate agreement with the finite full-benchmark ranking. The two differ at k=Nk=N, where agreement with the full ranking is exactly 1. The revised PDF now separates the two:

  • For agreement with the full-benchmark ranking, we add a finite-population form, ρfull(k)=ρ(k∣D)/ρ(N∣D)\rho_{\text{full}}(k)=\rho(k\mid D)/\rho(N\mid D). It equals 1 at k=Nk=N and predicts observed full-benchmark agreement at r=0.96r=0.96 (MAE =0.039=0.039).
  • The ceiling ρ(N∣D)\rho(N\mid D) is not an upper bound on agreement with the full ranking. It predicts how reproducible the full-benchmark ranking is on an independent set of questions. It agrees with an independent split-half estimate at r=0.94r=0.94 (MAE =0.017=0.017).

Q2 Using the ceiling when the goal is the full leaderboard

GoalUseValue at k=Nk=N
Reproduce the existing full-benchmark rankingρfull(k)\rho_{\text{full}}(k)1
Get a ranking that would hold on new questions of the same kindρ(k∣D)\rho(k\mid D), ceiling ρ(N∣D)\rho(N\mid D)ρ(N∣D)≤1\rho(N\mid D)\le 1
  • If the only goal is reproducing the full leaderboard, the ceiling is not needed. Use ρfull\rho_{\text{full}} to choose kk.
  • The ceiling still tells a practitioner whether the full leaderboard is itself a reliable ranking. For low-DD benchmarks such as GPQA, it is well below 1, so even the full ranking may not reproduce on a fresh question set.
AuthorsOpenReview ↗

Response to Q1 + W2

Q1 Direct validation of budget sizing

We ran the validation you describe. We estimate DD on 30 source models, compute the budget k⋆k^\star for a target agreement ρ⋆\rho^\star (Eq. 8), sample k⋆k^\star questions, and measure the agreement of disjoint target models with their full-benchmark ranking:

Target ρ⋆\rho^\starAchieved agreementDeviation
0.900.899−0.001
0.950.952+0.002
  • On feasible instances (k⋆≤Nk^\star \le N), the predicted budget gives the requested agreement on target models that were not used to estimate DD.
  • For 15% of benchmark–population pairs, k⋆>Nk^\star > N. Here the method reports that the target is above the predicted ceiling instead of returning a budget.
  • Added as a budget-validation paragraph in §5.3 of the revised PDF.

W2 Over- or under-allocation on low-discrimination benchmarks

On low-DD benchmarks the formula tends to over-allocate, so it errs on the side of too many questions rather than too few.

  • In Table 2, most of the low-DD error is a negative bias (−0.097-0.097): ρ(k∣D)\rho(k\mid D) predicts lower agreement than we observe. A predictor that underestimates agreement asks for more questions than needed.
  • The bias has a clear source. ρ(k∣D)\rho(k\mid D) targets latent ability, and for low-DD benchmarks the full ranking is itself noisy (ρ(N∣D)\rho(N\mid D) is well below 1). Agreement with that full ranking is therefore higher than agreement with latent ability. The finite-population form ρfull\rho_{\text{full}} (see W1) accounts for this.
  • For low-DD instances where a budget exists, achieved agreement is 0.93 on average for a target of 0.90. The budget is conservative on average, though not in every run.
  • For most low-DD instances k⋆>Nk^\star > N, so no budget is returned. Where a budget exists, it tends to be conservative.
AuthorsOpenReview ↗

Response to W3 + Q3

W3 Inflated benchmark count

We agree that 114 instances are not 114 independent benchmarks. They come from 11 suites, and several suites contribute subject- or task-level splits. We now report both counts (11 suites / 114 instances) in the text.

  • We keep the splits because each one is scored separately and has a different discrimination. For example, DD ranges from 0.05 to 0.48 across MMLU subjects (Appendix B).
  • The fit does not depend on this overlap:
SettingInstancesPearson rr
All instances1140.947
Five aggregate splits removed1090.946
Entire MMLU suite removed560.949
  • Within each suite, correlations are r=0.95r=0.95–1.001.00.
  • Added to §5.2 and Appendix B of the revised PDF.

Q3 Sensitivity of DD to the size of the pilot cohort

We estimate DD from MM randomly drawn source models (300 draws per MM) and compare it with DD on the full population:

MMCorr. with full-population DDMAE of estimated DDPrediction rr (k=10%k=10\%)
50.9080.0550.949
100.9480.0300.952
150.9620.0240.953
300.9840.0110.958
500.9910.0070.961
  • The estimate of DD improves steadily with MM. The predicted ranking agreement saturates early: r≈0.95r\approx0.95 at M=5M=5–1010, versus 0.9690.969 with the full-population DD.
  • These results are in Appendix E, and §5.2 summarizes them.
Reviewer_J252OpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
1
Soundness
2
Read review
Paper summary

In this paper, the authors investigate how to use a subset of benchmark to evaluate the model with a high accuracy. The authors reveal that the subset size is not a good metric, while the informativeness of the question should be measured to provide a better signal. The experiments are conducted across 114 benchmarks and the results demonstrate that the prediction can maintain the relative ranking of the models.

Critical strengths
  1. The effectiveness of subset is important in benchmark evaluation.
  2. The prediction method is easy to implement and the results have a wide coverage.
Critical weaknesses
  1. The baseline comparison and ablation study are not sufficient. There is no comparison with baseline directly predicting the consistency of the ranking. Current experiments only support the comparison under known evaluation results, but they can not support the scenario where we do not have the performance on the whole benchmark. At least a resampling baseline should be incorporated. Moreover, the ablation study does not have the comparison with the use of only k, k and N and k, N and D. Therefore, the contribution of D is not revealed.
  2. The budget selection is not supported. When we have a new model, we don’t know the distribution of k. Therefore, the performance under unknown models should be tested.
  3. The contribution may be limited. Since prior works have investigate the subset stability and ranking consistency, the contribution of this work should be further clarified.
  4. The benchmark selection requires further clarification. The authors say that they test on 114 benchmarks, but this is counted by separating MMLU into 58 instances, which is not a common practice for benchmark evaluation. In that sense, the number of tested benchmarks will be limited. The benchmark coverage seems also limited, since the post-training benchmarks are less compared with QA benchmarks. The generalization of this method across dfferent areas (e.g., multimodal, post-training, agentic) is not valiadated.
  5. The models used in the experiments are not revealed. More details should be added. Whether this method can generalizes across different model sizes, model capabilities, model types is not studied.
Questions for authors
  1. How would the method perform under different model settings? (e.g., model sizes, model architecture, training stage, etc)
  2. Whether the method can used to predict the performance if a new model emerges? If so, what's the role of the rest of the benchmarks?
  3. How would the post-training or multimodal benchmarks affect the performance?
10 comments
AuthorsOpenReview ↗

Thank you + W1.2 + W1.3

Thank you for the detailed review and the concrete suggestions. We answer each point below and have updated the revised PDF accordingly.

W1.2 Ablation study is missing

We added the ablation. We fit linear models that predict the observed full-benchmark ranking agreement from evaluation size alone, and then with DD added:

InputsR2R^2
kk0.07
kk, NN0.09
kk, NN, DD0.46
  • Adding DD raises explained variance from 0.09 to 0.46, so DD carries information that evaluation size does not carry alone.
  • The predictor ρ(k∣D)\rho(k\mid D) itself has no fitted coefficients and correlates with observed agreement at r=0.95r=0.95.
  • Added as a new ablation table in §5.2 of the revised PDF.

W1.3 Scenario without full-benchmark performance

The source models do not need the full benchmark. We estimate DD from a random fraction of the questions on the source models and predict ranking agreement on disjoint target models:

Source questions usedPrediction rr
25%0.91
50%0.94
100%0.96
  • With 25% of the questions the prediction is r=0.91r=0.91, compared with 0.960.96 using all questions.
  • Full source evaluations are therefore not required, though some representative source evaluations are.
  • Added to Appendix E (Partial Source Evaluations) of the revised PDF.
AuthorsOpenReview ↗

Response to W2 + Q2

W2 Budget selection for new models

The budget is chosen without evaluating the new (target) models at all. It depends only on DD, which is estimated from source models:

  • Estimate DD on source models, then compute the required budget k⋆k^\star for a target agreement ρ⋆\rho^\star (Eq. 8).
  • Evaluate disjoint target models, which were never used to estimate DD, on a random k⋆k^\star-question subset.
  • Measure how closely their ranking matches their full-benchmark ranking.
Target ρ⋆\rho^\starAchieved agreementDeviation
0.900.899−0.001
0.950.952+0.002
  • On feasible instances (k⋆≤Nk^\star \le N), the budget chosen from source models gives the requested agreement on unseen target models.
  • For 15% of benchmark–population pairs, k⋆>Nk^\star > N. Here the method reports that the target is above the predicted ceiling instead of returning a budget.
  • This holds when source and target models come from similar populations. §5.4 shows that under a large capability shift, DD changes and prediction accuracy drops.
  • Added as a budget-validation paragraph in §5.3 of the revised PDF.

Q2 Using the method when a new model emerges, and the role of the remaining questions

  • The method predicts how reliable a ranking will be, not the new model's score. The new model is scored by its accuracy on the k⋆k^\star sampled questions and ranked by that score.
  • The remaining questions are needed only once, when the source models are evaluated on them to estimate DD. A new model is evaluated on the k⋆k^\star questions alone.
  • In our experiments, full evaluations of target models are used only to check the prediction. They are not part of the method.
AuthorsOpenReview ↗

Response to W3

W3 Contribution relative to prior work

Prior work mostly estimates model scores or selects questions. We instead predict how well a uniform random subset will preserve the ranking, before evaluating the target models.

WorkWhat it doesHow
tinyBenchmarks, Anchor Points, metabench, DISCO, PPI++/AIPWEstimate each model's benchmark score from fewer questionsFitted models or estimators on source-model data
SubLIME [1]Selects a subset expected to preserve the rankingLearned predictor from anchor-model results and dataset features
Yauney et al. [2]Measures which model pairs a small benchmark can separate (MDAD)Empirical, after evaluation
OursPredicts ranking agreement of a random subset of size kk, and the kk needed for a target agreementClosed form from DD and kk, no fitted coefficients
  • With DD estimated from source models, the same formula gives three things: the expected agreement at a budget kk, the budget k⋆k^\star needed for a target agreement, and a full-benchmark ceiling.
  • Our contribution is using Spearman-Brown form with population-relative discrimination DD for LLM rankings, and testing it on 114 instances from 11 suites, where predicted and observed agreement correlate at r=0.95r=0.95.
  • DD adds information beyond size: explained variance rises from R2=0.09R^2=0.09 (kk, NN) to 0.460.46 with DD (see W1.2).
  • Our results agree with prior findings. The benchmarks SubLIME reports as hardest (GPQA, MuSR) have the lowest DD in our collection (0.060.06 and 0.100.10).
  • We expanded §2 of the revised PDF to state these distinctions.

[1] Saranathan et al. SubLIME: Subset selection via rank correlation prediction for data-efficient LLM evaluation. ACL 2025.

[2] Yauney, Warraich, and Swayamdipta. How reliable is language model micro-benchmarking? ICLR 2026.

Comments on the paper

2 comments
AuthorsOpenReview ↗

General Response

We thank all three reviewers. The predictor was found easy to use, practical, and free of fitted parameters (J252, xeQr, 2zFV). All three raised concrete, fixable points. We have uploaded a revised PDF with the changes below, and each reply names the section where a change appears.

  • Ablation (J252). Added the ablation isolating the contribution of DD: explained variance rises from R2=0.09R^2=0.09 (kk, NN) to 0.460.46 when DD is added.
  • Budget validation (J252, xeQr, 2zFV). The budget predicted from source models gives the requested agreement on unseen target models: target 0.90 gives 0.899, target 0.95 gives 0.952.
  • Suite-level results (J252, xeQr). Removing the five aggregate splits leaves the fit unchanged (rr 0.947 → 0.946), removing the entire MMLU suite gives 0.949.
  • Rankability ceiling (xeQr, 2zFV). Clarified what the ceiling means, and validated it against an independent split-half estimate (r=0.94r=0.94).
  • Related work (2zFV, J252). Added the two related works [1, 2] and stated how our work differs.
  • Resampling baseline (J252, 2zFV). Added the resampling baseline with complete source data, resampling is slightly more accurate and our predictor is comparable while using a single statistic DD. With partial source evaluations, our predictor is more accurate (MAE 0.091 vs 0.116 at equal source cost).

[1] Saranathan et al. SubLIME: Subset selection via rank correlation prediction for data-efficient LLM evaluation. ACL 2025.

[2] Yauney, Warraich, and Swayamdipta. How reliable is language model micro-benchmarking? ICLR 2026.

AuthorsOpenReview ↗

Summary for the Area Chair

Dear Area Chair,

Below we summarize the main concerns raised by the reviewers and our responses.

Contribution. A parameter-free, closed-form predictor of how well a random benchmark subset preserves the full-benchmark model ranking, based on population-relative item discrimination DD. It predicts the agreement at a given budget, the budget needed for a target agreement, and a full-benchmark ceiling, validated on 114 instances from 11 suites (r=0.95r=0.95).

Reviewer xeQr

  • Concern: The derivation targets latent ability, while experiments measure agreement with the full leaderboard. Response: We added the finite-population form ρfull\rho_{\text{full}}, which reaches 1 at k=Nk=N, and clarified the meaning of the ceiling (§4, Appendix A).
  • Concern: No direct validation of budget selection. Response: Budgets chosen from source models reach the requested agreement on unseen models (target 0.90 → 0.899, target 0.95 → 0.952; §5.3). We answered the follow-up questions with additional results (Appendix D.4, E.1).

Reviewer 2zFV

  • Concern: Closely related work was not discussed. Response: We added SubLIME and Yauney et al. to §2 and stated how our work differs.
  • Concern: No resampling baseline. Response: We added it (Appendix E.5). Resampling is slightly more accurate with complete source data, while our predictor is more accurate with partial source evaluations.

Reviewer J252

  • Concern: The contribution of DD was not isolated. Response: We added the ablation: explained variance rises from 0.09 to 0.46 when DD is added (§5.2).
  • Concern: The models and settings used were not described. Response: We added the model composition, released per-model metadata (Appendix B), and showed that budgets transfer to unseen models (§5.3).

We would also like to note that Reviewer xeQr has not yet had the opportunity to respond to our additional experimental results, and Reviewer 2zFV has not yet responded to our rebuttal. We hope these additions address their remaining concerns and would appreciate their reconsideration in light of the new evidence.

Reviewer J252 raised further questions approximately three hours before the discussion deadline. We responded to these within the remaining time and hope our additional analyses help clarify the outstanding concerns.

We thank all three reviewers for their constructive feedback, which has substantially strengthened the paper. We believe the paper should be accepted, as it is practically very relevant: it offers a simple, interpretable tool for deciding how many questions are needed to rank models reliably, which matters more as evaluation costs grow.

We hope the Area Chair will take these additional results and clarifications into account when assessing the remaining concerns.

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

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