acceptodds
Under review as a conference paper at ICLR 2027

The Evaluation Bottleneck: Your Biggest Judge Is Not Your Best Judge

Abstract

Agentic LLM systems generate outputs faster than they can be reliably reviewed: generation is cheap, evaluation is not. The common responses are to make the judge bigger or more specialized. We ask a more basic architectural question: where should specialization live in an evaluation system—in the judge itself, or in the rule that decides when its verdict can be trusted? We test both placements. In the first, we split a judge's training data across expert evaluators, one per family of criteria. In the second, we keep judges of different sizes frozen and train a small trust head that either accepts a cheap judge's verdict or defers to a stronger one, with every automatic release audited against a predeclared risk target. The findings reverse intuition. Specializing the judge backfires: splitting supervision across eight experts costs 10 accuracy points and shrinks the fraction of judgments that can be safely released more than fourfold—a loss that vanishes once the experts start from a shared trained judge. Specializing the trust decision wins: on RewardBench 2, a 15-parameter trust head routes a cascade of small-to-large judges to an accuracy 4.7 points above the largest judge alone at 0.42× its compute, passing exact 95% risk audits in all 20 runs, while naive confidence-based escalation yields neither an accuracy gain nor compute savings. The design rule is simple: share judgment learning by default, and specialize when to trust, not what judges know—provided the earlier judges are genuinely cheap.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM-as-a-judge, Selective prediction, Learning to defer, Model cascades, Reward models, Parameter-efficient specialization, LoRA, Mixture of experts

Reviews

Among:
Shape:
1234this paper, Bottom 9%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.50 over 4 reviews, above 9% of the others.
Reviewer_kgBhOpenReview ↗
Rating
1
Confidence
3
Informativeness
2
Presentation
3
Soundness
1
Read review
Paper summary

The paper asks where specialization should live in an LLM evaluation system: in the judge’s weights, or in the rule that decides when a judge’s verdict can be trusted. In the first study, a small learned trust head over frozen reward models of increasing size (0.6B–8B) routes a cascade on RewardBench 2. It reaches 4.7 points higher accuracy than the largest judge alone at roughly 0.42× its parameter compute, with held-out risk audits passed in all 20 repartitions, while margin-based escalation yields no gain. The authors also report boundary conditions where the cascade fails to be Pareto-improving. In the second study, splitting a rubric-conditioned judging corpus across eight criterion-family LoRA experts costs about 10 accuracy points and sharply reduces audited coverage relative to a single shared adapter. Capacity, step, and learning-rate controls attribute this to fragmented supervision, and initializing experts from a shared trained judge recovers the loss. The authors conclude that judgment learning should be shared by default and that the trust decision, not the judge, is where specialization pays.

Critical strengths
  1. Careful evaluation protocol with deployment-relevant metrics. The paper uses disjoint fit, calibration, and test partitions, holds out entire rubrics, runs a counterfactual rubric swap showing the judge actually uses the rubric, and includes capacity-matched controls. It also reports audited coverage at a fixed risk target rather than accuracy alone. This matters because it makes the individual measurements credible and reusable, and it shows that accuracy can hide deployment failures, such as global thresholds that appear safe but violate the risk target.
  2. Honest boundary conditions for cascades. The rescue/harm decomposition (Eq. 4) and the two measured failure cases (near-equal-cost stages; an accuracy gain at higher compute) turn “cascades help” into a testable, conditional claim. This is a transferable insight for practitioners.
Critical weaknesses
  1. The headline result is under-verified and under-baselined. The paper’s biggest claim is that a very small trust model, using a handful of numbers about how the judges scored the candidates, beats the largest judge by almost 5 points and gets close to the best possible result. That is surprising and needs extra checking, and the paper doesn’t provide it. One of the trust model’s inputs is where the winning answer sits in the list of candidates. If the correct answer tends to appear in a particular position (for example, always first), the trust model could be picking up on that rather than on anything meaningful. That would also explain why the simpler confidence-based methods, which don’t use position, show no improvement. The authors should shuffle the candidate order or remove this input and show the result still holds. The comparison is also uneven. The trust model is trained on labeled examples from the same benchmark it is tested on, while the largest judge gets no such help. The gain could come from that extra labeled data rather than from “learning when to trust.” The paper doesn’t test simple alternatives such as emsembling all the judges’ scores, recalibrating the largest judge on the same data, or the existing cascade methods it cites. Because this result is the basis of the title and the main claim, this gap weighs most heavily in my rating.
  2. The central comparison is not controlled, and the negative result is largely expected. The paper claims to compare two places to put specialization: inside the judge, or in the trust decision. But the two ideas are tested on different tasks, different datasets, and different kinds of models, so they are never compared fairly side by side. The “specialized” trust model also isn’t really specialized: removing the information about which topic each example belongs to makes almost no difference. So the success comes from a general-purpose confidence estimator, not from specialization. The negative finding is largely expected. Splitting the training data eight ways and training eight separate models from scratch, each seeing only a small slice once, will naturally do worse than one model trained on everything. The fix the authors propose, starting each expert from the shared model, gives only a tiny gain (+0.47 points), and that gain could simply come from the extra training rather than from specialization. Taken together, the paper’s broad framing isn’t supported, and what remains is a carefully audited but incremental cascade result plus an expected ablation.
Questions for authors
  1. How were candidates ordered when fed to the reward models, and does the correct answer’s position correlate with correctness? Please report the cascade’s results with shuffled candidate order and with the winning-position feature (and candidate count) removed. If the gain largely disappears, the headline result does not stand.
  2. How does the cascade compare to baselines that use the same labeled RewardBench 2 data, such as ensembling all four judges’ scores, recalibrating the 8B judge, or existing cascade methods like Trust or Escalate and Gatekeeper? If these match the cascade, the gain comes from extra labeled data rather than from learning when to trust.
  3. Does a trust head fit on one dataset still work on a different one, for example fit on RewardBench 2 data and applied to another preference benchmark? Without this, the method requires in-distribution labels at deployment, which limits its practical value.
  4. Given that removing the skill indicator changes accuracy by only 0.03 points, in what sense is the trust head “specialized”? If it is a general confidence estimator, how do you justify framing the paper as a comparison between two placements of specialization?
Reviewer_BfyxOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

The paper asks where specialization should live in an LLM evaluation system: in the judge's weights, or in the rule that decides when a judge's verdict can be trusted. Study 1, in Section 5 and Table 2, freezes a Skywork-Reward-V2 ladder of 0.6B, 1.7B, 4B, and 8B judges and fits 15-parameter logistic trust heads separately for the non-terminal stages using score features and a skill-family indicator. On the 1,763 non-tie tasks of RewardBench 2, the 0.6B-4B-8B cascade reaches 89.40% top-choice accuracy at 0.415x the 8B judge's parameter compute, versus 84.75% for the 8B judge alone, while raw-margin escalation reaches 84.81% at 0.944x. Study 2, in Section 6 and Tables 3-5, splits Feedback Collection training across eight criterion-family LoRA "judgelets" and finds that this loses 10.05 accuracy points relative to a shared monolith, which the authors attribute to fragmented supervision. The paper concludes that judgment learning should be shared by default and that specialization belongs in the trust decision, with Eq. 4 stating when a cascade can beat its largest judge.

Critical strengths
  1. The paper reports useful failure boundaries. Section 5.3 shows that near-equal-cost stages move accuracy from 77.50% to 77.52% at 1.720 times the forward passes, while the OpenAssistant base-large pair gains 8.64 accuracy points at Cnorm = 1.122. Eq. 4 distinguishes helpful from harmful early exits and makes clear why complementary errors and a sufficiently cheap first stage are both needed.

  2. The control experiments and audit design are informative. A parameter-matched rank-64 monolith exceeds the independently trained expert bank by 11.16 points. Increasing the bank's update budget by 2.7 times recovers 6.22 points but leaves a gap, showing that under-training contributes without fully explaining the result. Study 1 separates fitting, calibration, and evaluation and uses exact one-sided Clopper-Pearson audits; Study 2 uses Wilson bounds on held-out release risk. The authors also correctly describe the 20 repartitions as partition sensitivity rather than independent sampling uncertainty.

Critical weaknesses
  1. The main accuracy-compute frontier is demonstrated on one benchmark, and the main table does not show stage-matched margin baselines. The 20 RewardBench 2 runs reuse 1,763 tasks, so passing all audits is evidence of partition stability rather than independent replication. Table 2 contrasts the 0.6B-4B-8B learned cascade with 4B-8B margin policies. Section 5.1 states that all stage subsets were enumerated and the Figure 2 caption points to an artifact sweep, but the paper as submitted does not expose the matched 0.6B-4B-8B margin operating points. Those results, plus single-judge micro-accuracy points, would make the attribution clearer.

  2. Deployment cost and the generality of the specialization comparison remain open. Cnorm is a parameter-count proxy, and the submission does not report measured throughput or latency for the headline Study-1 cascade. The principal trust and weight-specialization studies also use different data and model arrangements. Section 5.3 does provide a diagnostic cascade of the Study-2 judges, but a fully matched experiment varying both weight specialization and trust routing is still absent. Finally, the strong response-only baseline in Table 3 limits external validity, although the counterfactual-rubric intervention demonstrates that rubric content does affect predictions.

Questions for authors
  1. Can you show raw- and calibrated-margin policies for the same 0.6B-4B-8B stages, alongside single-judge micro-accuracy and compute points, including the relevant artifact sweep?

  2. Does the headline frontier replicate on a second benchmark or independent task sample?

  3. Can you provide measured throughput or latency for the Study-1 cascade, and a matched experiment varying weight specialization and trust routing within one task setup?

  4. Please present both shared-initialization contrasts clearly: 19.94 points versus the low-learning-rate matched scratch run, and 10.51 points versus the default scratch run. Since their learning rates and total training histories differ, how should each contrast be interpreted, and what total-budget-matched evidence is available?

Reviewer_rdBhOpenReview ↗
Rating
1
Confidence
3
Informativeness
1
Presentation
2
Soundness
1
Read review
Paper summary

The paper investigates the evaluation bottleneck in LLM-based systems: generating model outputs is relatively inexpensive but assessing their correctness and compliance can be costly. It compares two approaches: 1. Specialize the trust decision: keep pretrained judges frozen and train a small logistic classifier to decide whether to accept a cheaper judge's decision or escalate to a larger model; 2. Specialize the judge: divide training data by rubric families and train separate LoRA adapters, comparing them against a single shared judge. The authors conclude that sharing judgment learning is generally preferable to specializing the judges themselves, while specializing the decision of when to trust a judge is beneficial.

Critical strengths

The paper provides empirical findings of where to place specialization in an LLM evaluation system.

Critical weaknesses

Overall I find this mainly an empirical paper which only demonstrates some phenomenon while lack of a new methodology. The main proposed solution is a learned trust-based judge cascade. Every step such as training a logistic regression classifier, applying a calibrated threshold to decide whether to accept or escalate is not new or interesting to me. I don't think the main theme of the paper is related to foundation or frontier models as the paper suggests.

Besides, the central comparison in paper is not established through a controlled experiment. The two approaches (study 1&2) are evaluated under substantially different experimental settings. The two differ in various dimensions including dataset, task, model setup, target, metric etc. Consequently, the experiments do not isolate the placement of specialization as a single variable. For example, Study 1 demonstrates that routing between complementary pretrained models is beneficial. Study 2 demonstrates that dividing a training dataset across independently optimized adapters can reduce performance. Both results may be correct without implying that trust specialization is inherently preferable to judge specialization.

Finally, the paper contains lots of long sentences with ";" which makes me hard to read.

Questions for authors

How does the proposed approach differ experimentally from existing cascaded selective evaluation methods, beyond using a logistic correctness predictor?

Reviewer_crjgOpenReview ↗
Rating
2
Confidence
2
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

The paper asks whether specialization in an LLM evaluation pipeline belongs in the judge's weights or in the decision about when to trust a verdict. Study 1 cascades four Skywork-Reward-V2 Qwen3 reward models (0.6B to 8B) on RewardBench 2, with a small logistic "risklet" deciding when to release each stage's answer. The best cascade (0.6B, 4B, 8B) reaches 89.40% accuracy at 0.415 of the 8B model's compute, against 84.75% for 8B alone. Study 2 splits Feedback Collection training across criterion-specific LoRA adapters. At K=8 this loses about 10 points, unless the experts start from a trained monolith.

Critical strengths

1.The question matters to anyone building judge pipelines, and selective risk and coverage are the right main metrics. 2.The statistics are careful: disjoint splits, a buffer between calibration and held-out targets, and an explicit statement that repartitions measure partition sensitivity, not sampling uncertainty. 3.The rescue/harm decomposition (Eq. 4) explains when a cascade can beat its top model. The failure cases in Section 5.3 are reported in the main text, which is a real strength.

Critical weaknesses
  1. Possible label leak. "Winning position" is a risklet input (Section 5.1). RewardBench 2 stores correct and incorrect completions in separate lists. If candidates were flattened correct-first, position 0 means "correct." The numbers fit this: the 0.6B judge scores 61.39 officially, yet the 0.6B–8B cascade releases 71.52% of tasks at the first stage with under 5% error. The authors must state whether candidate order was shuffled and report results without this feature. If the result does not survive, Study 1 does not stand.
  2. Baselines. Margin baselines are run only on the 4B–8B pair, so stage choice and signal choice are confounded. The gain comes mostly from complementary errors, so an ensemble over the three judges is required as a comparison.
  3. Weak top judge. The Llama-3.1-8B variant from the same release scores 84.1 on RewardBench 2, against 78.2 for the Qwen3-8B used here. The authors should show the gain survives a stronger terminal judge.
Questions for authors
  1. Were RewardBench 2 candidates shuffled before scoring? What are the Table 2 risklet and geometry probe numbers with winning position removed?

  2. What exactly are the 14 risklet inputs? "The largest scores" (Section 5.1) is ambiguous. With two non-terminal stages in the best cascade, is the "15-parameter trust head" in the abstract actually two heads with 30 parameters?

  3. What do the raw-margin and isotonic baselines give on the 0.6B–8B and 0.6B–4B–8B subsets?

  4. How does a score-averaging or stacked ensemble of 0.6B, 4B, and 8B compare in accuracy and Cnorm?

  5. Did you check for overlap between Skywork-Reward-V2 training data and RewardBench 2 prompts? Size-dependent contamination could produce some of the complementary errors.

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

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