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Under review as a conference paper at ICLR 2027

When Models Prefer What Humans Strongly Reject: Revision in Open-Ended Domains

Abstract

AI systems increasingly use frontier language models both to improve an answer and to judge whether it improved. This couples the optimizer to an evaluator that may share its blind spots. We introduce SlopBench, a stress test for this failure mode in open-ended conceptual domains, where no binary verifier can determine whether a revision improved the answer. SlopBench follows 50 answers written by Opus 4.8 through sixteen rounds of recursive revision and evaluates them with five Claude-family and three GPT-family judges. After sixteen rounds, Claude judges choose the deeply revised endpoint over the initial essay in 98–100% of comparisons, while GPT judges do so in 69–86%. By contrast, humans choose the deeply revised endpoint in only 8.0% of judgments–an overwhelming divergence from frontier model preferences. SlopBench shows that whole-essay critique–revision can create a powerful improvement signal for frontier model judges even as blinded humans overwhelmingly judge the resulting writing far worse and less useful. This reversal exposes a consequential blind spot in frontier model evaluation and a concrete target for calibration.

Primary area:
datasets and benchmarks
Keywords:
Model Evals, GPT, Claude

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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.
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Paper summary

The paper studies LLM judgments on whether LLM revisions to long-form answers improved the writing. They find overall that these judgments are misaligned with human preferences.

They introduce SLOPBENCH with 50 open ended tasks which has 16 rounds of revision using either (1) a fresh revising LLM responds to LLM critiques under a revision policy or (2) a bounded LLM edit. They use 8 LLM judges (5 Claude, 3 GPT 5.6) for pairwise revision comparisons and compare these preferences with those of 273 human readers.

They find Claudes prefer Claude's final revision >98% of the time and GPTs prefer it 69-86% of the time. They find, in general, the opposite is true of humans.

The primary contributions are

  • The reporting of striking misalignment in LLM preferences with those of humans, and the strength of LLM preference across LLM provider lines
  • The release of their data as SLOPBENCH, which is Opus 4.8-generated and revised essays with human annotations for 1000 comparison instances

As a note, while Fig. 4-5 findings are interesting, that space could have been used for more thorough interrogation of the GPT mini-study, the presentation order ablations, the effects of separation of questions, length residualization, embedding space analyses, etc. The word choice and survey comments analyses do little to strengthen the main argument against the intended claims (which would benefit from more decision-relevant evidence). the selected human quotations (e.g., "the will to live!") are rhetorically loaded and appear cherry-picked rather than systematically coded. Also, the appendices are very long without strong justification in the writing to go to them. If the analyses contribute to the claims, make space for them.

Critical strengths

(1) Clean evidence for a human alignment failure mode.

WHY: Common practice uses model-judged self-refinement and model-curated synthetic data in open-ended domains, and the study questions that practice. They show that a LLM refinement loop can move away significantly from human preferences. This framework of revision policies can be interrogated further in future work to separate generic preference for elaboration or in-family text against different models.

Critical weaknesses

(1) The conclusions may not generalize beyond the single revision approach used

WHY: The paper's significance depends on the claim that LLM judge miscalibration, not an idiosyncratic revision regime or a particular model instance/provider subset, drives the failure. To make that claim, the paper would need at least one revision policy with a stop/no-edit option or a controlled length constraint, or a series of representative revision policies, or a judge-gated loop, evaluated by humans. Otherwise the scope of the claims should be narrowed to match the particular revision process that requires the critic to judge "harshly" and to always "fix the weaknesses identified" with no history of earlier rounds nor acceptance gate. Humans already reject the first rewrite, suggesting that the forced rewrite itself may be contributing to the misalignment. For the claims to be novel and to extend beyond current understanding of LLM judge biases (e.g., length and self-preferences), analysis would need to be done to establish what distinguishes these preferences. Otherwise, the results remain a compelling demonstration of how known biases compounded in a loop diverge from human preferences (such readers who are reading 2000 word essays and experiencing reading fatigue).

Questions for authors

Please report task-clustered confidence intervals or a mixed-effects analysis for the human results in Table 1, and the number of the 25 tasks in which a majority of readers preferred A16. Are there tasks where humans favored deep revision, and what characterizes them?

What exactly is the proposed SLOPBENCH benchmarking for a new judge (e.g., agreement with majority human preference over the cells, rank correlation over checkpoints, etc.), and how stable is that score given the human sample size? How would that score be used and what would maintenance of the benchmark look like?

Given the moderate human agreement (70%) only when they expressed a preference, did you control for reader population and effort? Did any readers have domain expertise relevant to the tasks? Were reading times recorded, and do longer reading times (or attention checks) predict different preferences? could you share any reader-conditional analyses that might explain preference differences?

Have you, or can you, run a recursive arm where a revisor may return the essay unchanged (no-edit), or in which a judge-gated acceptance step keeps a revision only if the judge prefers it, given the target criteria? How often would such a loop accept revisions, and do humans prefer its endpoint to A0? Can you report results for a revisor constrained to keep length within 10% of the incoming essay? Right now the small length adjustment seems to rely on extrapolating to lengths unobserved by humans.

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Author Response (1/4)

Thank you for your review. We agree with the reviewer that the paper provides very clean evidence for a human alignment failure mode. However, we clarify that whether a revision policy improves writing is a different question than whether an evaluator correctly judges the writing that policy produces. Our contribution mainly concerns the latter.

This distinction matters empirically. When comparing A0A_0 with A16A_{16}, not one task has a human majority favoring A16A_{16}, for either quality or usefulness, while only 8% of pooled human judgments favor A16A_{16}. By stark contrast, model evaluations on SlopBench very strongly favor deep revision, giving 98–100% for Claude judges and 69–86% for GPT judges, in contrast to 8% for humans. This is an overwhelming misalignment with human preferences. A frontier LM evaluator intended to understand human preferences should recognize this failure, especially in open-ended domains where no executable test or formal verifier determines whether an answer has improved. A different revision policy does not explain away this misalignment in judgment.

Below, we address the reviewer’s comments.

1. Requiring revision does not require judges to reward it.

The paper’s central claim is that frontier judges can overwhelmingly endorse revisions that the intended human readers find worse and less useful. It is not that all revision policies lead to misalignment. Across the 50-task model evaluation, Claude judges prefer A16A_{16} in 98–100% of comparisons and GPT judges in 69–86%; humans prefer it in only 8% of pooled judgments on the prespecified 25-task subset. We do not require every possible revision policy to produce the same outcome.

The revision prompt also deserves its complete context. The critic, rather than the evaluator, is asked to critique “harshly but fairly,” identify weaknesses in thinking and writing, explain why they matter, and list the 3–5 most important weaknesses. The revisor is asked to address those weaknesses. Both the initial writer and revisor are instructed to use only as many words as necessary, with responses of 500 words or fewer explicitly permitted. The critic is instructed not to recommend additional length or comprehensiveness for its own sake. This procedure requires a rewrite, but it does not instruct indefinite elaboration.

Forced or continual rewriting contributes to the novelty of our approach. This allows us to examine whether model-judged preference for continued rewriting eventually plateaus or reverses. We find that four Claude judges assign monotonically increasing preference scores across all sixteen Opus-written revision rounds, even as humans overwhelmingly reject the final output (Figure 9; Appendix G.1.1, lines 1727–1732). All model judges strongly prefer the final output to the initial draft, in direct contrast with humans (§4.1, lines 319–323; Table 1). This design therefore reveals a sustained signal of apparent improvement from model evaluators despite growing human disagreement.

In addition, SlopBench’s second editing policy, local editing, already permits a no-edit operation (§3.2, lines 230–233; Appendix C.1, lines 1038–1048). The requested new stopping, gating, and length-constrained experiments would concern how to prevent the demonstrated failure, not whether it exists, and are currently outside the scope of our work. We explicitly identify calibrated stopping rules and more bounded editing policies as future research directions (Appendix A.2, lines 880–888). SlopBench tests whether model evaluators recognize when revision fails to serve human readers. They fail to recognize this even at the very first revision (Table 1; Appendix G.2.1, lines 1844–1848).

2. Known LM biases do not make this result redundant.

Our contribution is a reproducible human-gold benchmark demonstrating the magnitude and persistence of a substantial failure mode across eight frontier judges and two evaluator families, without ever optimizing against judge feedback in the revision loop. Several findings make that failure informative:

  • The effect generalizes across evaluator families. Frontier GPT judges also overwhelmingly favor Claude-written revisions, in stark contrast with human readers.
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Author Response (2/4)

  • The effect persists even when judges are explicitly asked to select for human preferences. In Appendix I, judges are tasked with predicting a human reader’s preference. Yet Claude judges still select A16A_{16} in 75.0–97.3% of staged comparisons and GPT judges in 75.3–88.7%, against just 8% of actual human judgments (Appendix I.2, Table 20). This failure also persists when Claude judges are given a rubric identifying the textual signature of recursive revision (Appendix K.3, lines 3760–3764 and 3784–3788; Table 23). Therefore, this is not merely a mismatch in evaluation objectives. Even when explicitly asked to predict human preferences, the judges overwhelmingly get them wrong. This suggests a capability issue, not just an alignment issue.

  • Recognizing undesirable features does not reliably correct the phenomenon. GPT judges do recognize limits to attention and readability while still assigning A16A_{16} higher overall quality, usefulness, and reasoning quality (§4.1, lines 349–354; §4.2, lines 371–377; Appendix G.2.6, lines 2095–2100; Table 10). Claude judges identify the deeply revised essays as more strange or “off” in 91–99% of comparisons while overwhelmingly preferring them overall (Appendix G.3.1, lines 2304–2307; Figure 19).

Our benchmarking results also distinguish noticing a defect from assigning it the weight human readers do (Section 4.1, lines 349–354). Identifying possible LM biases does not negate a benchmark that exposes their consequences for model-judged refinement and synthetic preference data.

3. Length does not invalidate our observed evaluation failure.

The primary question we study is whether model judgments track human judgments of the essays actually produced. Length is one consequence of revision and one component of the reading experience. If unnecessary length makes an answer worse for readers, an evaluator intended to represent reader value should penalize it. Rewarding that answer instead is another source of the mismatch under study.

The human-model misalignment strongly persists even after controlling for response length (Appendix H.4). In the A0A_0–A16A_{16} tasks within 10% in word count, humans prefer A0A_0 in 9/10 judgments for both quality and usefulness (lines 2981–2983). In the I16I_{16}–A16A_{16} tasks within 20%, humans prefer I16I_{16} in 22/25 quality judgments, versus just one for A16A_{16} (lines 2983–2986). Length-based regression adjustment changes the A0A_0–A16A_{16} quality score only from −1.54 to −1.37, preserving nearly 90% of the effect (Table 19, lines 3000–3006).

Our study neither requires nor purports to measure reader fatigue. Regression-based length adjustment is a standard and well-established technique used in prior work to study precisely these situations [1–3]. We show that neither the comparable-length comparisons nor the regression adjustment eliminates the massive disagreement in human and model preferences (Appendix H.4, lines 2981–2986; Table 19, lines 3000–3006).

4. Are there tasks where a human majority favors A16A_{16} over A0A_0?

No. The count is 0 out of 25, for both overall quality and usefulness. There is therefore no such exception group to characterize in this comparison. In particular, human preferences for quality are stronger than a bare majority, as every task has at least four of five readers favoring A0A_0.

5. Are human judgments consistent across tasks and reader groups?

Yes. Human preference percentages and 95% confidence intervals are:

Preference measuredTasksQuality, % [95% CI]Usefulness, % [95% CI]
A16A_{16} over A1A_11022.0 [12.0, 32.0]30.0 [20.0, 42.0]
A1A_1 over I16I_{16}2522.4 [14.4, 31.2]21.6 [13.6, 30.4]
I16I_{16} over A0A_01046.0 [32.0, 58.0]26.0 [12.0, 40.0]
A16A_{16} over I16I_{16}258.0 [4.0, 12.8]8.8 [4.0, 14.4]
A16A_{16} over A0A_0258.0 [4.0, 12.0]8.0 [4.0, 12.8]
A1A_1 over A0A_02527.2 [18.4, 36.8]29.6 [23.2, 36.8]

We report 95% percentile task-cluster bootstrap confidence intervals from 100,000 resamples. Within each comparison, we resample tasks with replacement, retaining all five reader judgments for each selected task. Neutral responses remain in the denominator. Readers are not independently resampled.

The approximately 70% agreement quoted by the reviewer pools all endpoint comparisons (Appendix H.3, lines 2941–2945; Table 17). For A0A_0–A16A_{16}, same-choice agreement is 83.5% for quality and 83.0% for usefulness, conditional on both readers expressing a preference (lines 2946–2949), which further strengthens the point made in our paper. More directly, at least four of five human readers favor A0A_0 for quality in every task, whereas in stark contrast, at least six of eight model judges all favor A16A_{16} in exactly the same tasks. Each model’s preference is determined by majority vote across its six evaluations of that task.

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Author Response (3/4)

6. What are the backgrounds of the human readers?

The tasks in SlopBench were deliberately designed to be answerable from ordinary background knowledge, as detailed in §3.1, lines 213–219. They assess writing for a general reader, rather than specialist knowledge requiring domain-expert annotators. Readers came from Surge AI’s vetted, English-qualified workforce, had a sustained record of high-quality work on similar projects, and completed an intake task explaining the reading commitment. Available metadata in SlopBench shows A0A_0 preferred for quality in 75/84 judgments from readers with at least a bachelor’s degree and 37/40 below that level; the counts are 64/68 among US residents and 48/56 outside the US.

Recorded reading time is available in SlopBench. This records elapsed time from page opening until the reader confirms finishing both essays. For A0A_0–A16A_{16}:

Reading-time quartileJudgmentsPreferred A0A_0: qualityPreferred A0A_0: usefulness
Fastest3187.1%77.4%
Second3193.5%90.3%
Third3190.3%87.1%
Slowest3290.6%87.5%

The strong preference for the initial draft persists in every reading-time quartile.

7. What is SlopBench evaluating?

SlopBench tests whether a judge endorses revisions that intended readers find worse or less useful. New judges can be scored by agreement with human majorities on the annotated pairs, with quality and usefulness reported separately.

SlopBench provides 1,000 essay-pair evaluations from 273 readers, releasing high-quality human gold responses to 15,000 structured questions as well as 16,000 written explanations across quality, usefulness, and diagnostic dimensions (Appendices E.1 and H). By comparison, the human study in Prometheus [4] comprises 405 annotation instances from just 9 annotators, yielding 405 response scores and 405 feedback-preference judgments, alongside categorical reason selections. Panickssery et al. [5] collect 900 summary-pair preference judgments from just 20 annotators, covering 300 distinct pairs with three annotations each. Neither study’s protocol requests written explanations. In contrast, SlopBench’s 10,000+ written explanations from hundreds of human readers enable additional high-quality qualitative analysis of the reasons for human preferences and how these differ from model judges’ assessments.

8. Why include Figures 4–5 in the main text?

Because they directly address an explanatory question left open by the percentages in Figure 3. Figures 4–5 show that Claude judges repeatedly describe the revised essays as rigorous, while readers describe confusion and difficulty extracting the argument. This helps interpret the disagreement rather than merely restating its magnitude. Figure 4 reports descriptor frequencies. Figure 5 illustrates the reasons behind the judgments.

Figure 5 explicitly presents selected explanations (caption, lines 397–402), and Appendix G.6.2 clearly states that excerpts in the extended gallery were selected for brevity and vividness (lines 2756–2759). The main endpoint study includes 600 human pairwise evaluations, each with descriptions and accompanying rationales for both essays, all available in the supplementary material (§3.3, lines 260–269; Appendix E.1, lines 1493–1504; Appendix H.2, lines 2891–2894). A figure in the paper thus necessarily presents a selection. The illustrative quotations do not determine our quantitative results, which are computed independently from the full set of human judgments. Additionally, the appendices document the exact procedures and other analyses needed to inspect our results, which contributes to their length as noted by the reviewer. Retaining that detail makes the study reproducible.

The suggested experiments with alternative editing policies would investigate different revision procedures, rather than the central question our paper addresses. Our contribution is to establish that frontier evaluators can overwhelmingly endorse the outputs of a given revision procedure even when human readers strongly disagree and prefer the originals. This is the misalignment that SlopBench exposes, supported by extensive quantitative and qualitative evidence from hundreds of human readers and tens of thousands of written human and model-judge explanations.

Please let us know if you have any remaining questions or concerns. We are more than happy to discuss further.

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Paper summary

Authors propose the public stress test (SlopBench) for evaluators of recursively revised outputs, that they release in open source. SlopBench is a benchmark and experiment suite for studying long-form writing quality under iterative revision. The test contains 50 open-ended essay tasks across five domains through sixteen rounds of revision, two sixteen-round revision policies, evaluations by eight named frontier model judges, and 1,000 blinded human evaluations from 273 readers. SLOPBENCH follows 50 answers written by Opus 4.8 through sixteen rounds of recursive revision and evaluates them with five Claude-family and three GPT-family judges. The part of experiments was repeated also for the Sol model. SLOPBENCH shows that whole-essay critique– revision can create a powerful improvement signal for frontier model judges even as blinded humans overwhelmingly judge the resulting writing far worse and less useful. SLOPBENCH therefore tests whether model evaluations are calibrated to human judgments.

Critical strengths

It is an interesting observation that humans and machines often hold fundamentally conflicting views when it comes to evaluating revisions. This raises a broader question: to what extent can we trust LLM-as-a-Judge to assess iterative improvements? It’s a particularly relevant issue given the growing prevalence of critique revision loops and agentic systems. The case study on the alignment between model-based evaluations and human preferences, while conducted within a narrow scope, is both detailed and well-executed.

Critical weaknesses

This is more a very detailed case study in a narrow experimental setup; for ICLR it seems like there isn't enough novelty, but too strong a generalization of the conclusions is being claimed; this phenomenon cannot be extrapolated on this basis. It is not proven that recursive editing leads to quality degradation for humans, or that LLM-as-a-Judge creates a systemic threat to inference-time scaling and synthetic data.

There may be bias due to models from a single family in the generations + judges. Add to the main text experimental confirmation for Sol-written trajectories — human evaluations. The existing design does not allow independently assessing the contribution of the generator, critic, editor, and judge to the final result, so why this observation occurs is, in fact, a question the work does not answer.

The fact that humans fundamentally contradict machines may occur purely because the editing is accompanied by a substantial increase in length. This is a cognitive load for humans and may therefore lower the rating. The authors were unable to fully test the effect, since there are very few texts comparable in length.

I would advise moving parts of the methodology text from the Appendix to the main text of the work. In particular, define the quality metrics in the experimental setup more transparently. The authors use overall quality and usefulness as central indicators, while reader preference actually serves as the gold standard of quality.

Questions for authors

Is it unreliable to give judges in the form of models connected to the internet prompts like "Do not search for or consult outside information," since models of this level may go online despite the instruction (just as a human annotator might as well) and should this therefore be physically prohibited and incorporated into the experimental setup?

Maybe you check and could add a full-fledged analysis of inter-annotator agreement reliability, corrected for chance agreement and the specifics of ordinal labels (Krippendorff's alpha or weighted kappa)?

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Author Response (1/2)

We thank reviewer vfED for recognizing that the study is detailed and well-executed. We strongly agree with the reviewer that the reliability of model-judged revision is important for critique–revision loops and agentic systems. We also agree that the disagreement between human readers and model judges in evaluating revisions is an important observation. We address the reviewer’s comments below.

1. What is the contribution of your work?

Our contribution is a reproducible benchmark showing that frontier evaluators overwhelmingly endorse revisions that their intended human readers find worse and less useful. It is not that all revision policies necessarily lead to quality degradation. Appendix A.1 states this explicitly (lines 868–874).

In SlopBench, Claude judges prefer A16A_{16} over A0A_0 in 98–100% of comparisons and GPT judges in 69–86%, while humans prefer it in only 8% of judgments (Table 1). Not one task has a human majority favoring A16A_{16}, for either quality or usefulness. For quality, four or five of the five readers prefer A0A_0 on every task. This failure arises without ever optimizing against judge feedback (Appendix B, lines 940–943). In addition, this failure appears in the very first revision. Frontier model judges strongly and unanimously favor the first rewrite in 94–100% of comparisons, versus just 27.2% for humans (Table 1; Appendix G.2.1, lines 1844–1848).

We do not claim that every revision policy must fail in this way, nor that revision must “create a systemic threat to inference-time scaling and synthetic data.” On the contrary, we explicitly state that the benchmark “does not imply that revision is generally harmful” (Appendix A.1, lines 868–870). We also note that the lesson is not to abandon revision, but to calibrate frontier model judges to be better able to decide what revision in open-ended domains is worth for humans (§6, lines 481–484).

We further establish that recognizing defects does not prevent frontier models from endorsing the defective output. Claude judges identify the deeply revised essays as more strange or “off” in 91–99% of comparisons while overwhelmingly preferring them overall. Explicitly asking judges to predict human preferences also completely fails in resolving this misalignment (§1, lines 96–99; Appendix I.2, lines 3064–3070). These findings establish how an apparently successful revision procedure can pass frontier LM model evaluation with flying colors while completely failing its intended human readers.

2. Can you provide additional human evaluations, including while changing model writers, critics, and judges?

Unfortunately, this is not possible. Additional human studies, including annotations of the Sol-written trajectories, are not feasible within the rebuttal’s time nor the annotation budget. The existing study already supplies substantial and extensive human evidence for the paper’s central contribution, identifying a clear regime in which frontier judges overwhelmingly endorse revisions that their intended readers find worse and less useful. Establishing that failure does not require every writer or revision policy to produce the same outcome. The released benchmark also permits substantial further analysis without collecting new judgments.

SlopBench provides 1,000 essay-pair evaluations from 273 contracted human readers, releasing high-quality human gold responses to 15,000 structured questions as well as 16,000 written explanations across quality, usefulness, and diagnostic dimensions (Appendices E.1 and H). By contrast, prior human studies, e.g., Prometheus [4] comprises 405 annotation instances from 9 annotators, yielding 405 response scores and 405 feedback-preference judgments, alongside categorical reason selections. Panickssery et al. [5] collect 900 summary-pair preference judgments from just 20 annotators, covering 300 distinct pairs with three annotations each. Neither study’s protocol requests written explanations. In contrast, SlopBench’s 10,000+ written explanations from hundreds of human readers enable additional high-quality qualitative analysis of the reasons for human preferences and how these differ from model judges’ assessments.

Independently varying the generator, critic, and editor while contracting additional blinded human readers would investigate a different question, and is a follow-up work that is enabled by our released benchmark. It is explicitly outside of the scope of the current work. We have already identified this as a future research direction (Appendix A.2, lines 883–888).

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Author Response (2/2)

3. Length does not invalidate the observed evaluation failure.

The primary question asked in our work is whether model judgments track human judgments of the essays actually produced. Length is one consequence of revision and one component of the reading experience. If unnecessary length makes an answer worse for readers, an evaluator intended to represent reader value should penalize it. Rewarding that answer instead is another source of the mismatch under study.

The human-model misalignment strongly persists even after controlling for response length (Appendix H.4). In the A0A_0–A16A_{16} tasks within 10% in word count, humans prefer A0A_0 in 9/10 judgments for both quality and usefulness (lines 2981–2983). In the I16I_{16}–A16A_{16} tasks within 20%, humans prefer I16I_{16} in 22/25 quality judgments, versus just one for A16A_{16} (lines 2983–2986). Length-based regression adjustment changes the A0A_0–A16A_{16} quality score only from −1.54 to −1.37, preserving nearly 90% of the effect (Table 19, lines 3000–3006).

Our study neither requires nor purports to measure reader fatigue. Regression-based length adjustment is a standard and well-established technique used in prior work to study precisely these situations [1–3]. We show that neither the comparable-length comparisons nor the regression adjustment eliminates the massive disagreement in human and model preferences (Appendix H.4, lines 2981–2986; Table 19, lines 3000–3006).

4. Can you define the quality metrics in the experimental setup more transparently?

We clarify that we already provide this verbatim in the paper. Section 3.3 defines the overall-quality question and its five-point scale (lines 256–258). We specify human reader-blinding, presentation order balancing, and staged/isolated evaluation procedures while permuting A/B pair ordering during both human and LM evaluations in Appendix H.1, lines 2866–2872, and Section 3.3, lines 253–269, etc.,. Appendix E.1 gives the complete questionnaire verbatim (lines 1336–1504). We have also released all code as supplementary material for reproducibility. We note that usefulness asks whether an essay helps the reader make a decision, form a view, or understand the issue (lines 1361–1369).

There is no inconsistency between measuring overall quality and usefulness for human readers and using human judgments as the reference standard. Quality and usefulness specify what readers are asked to judge; their judgments provide the benchmark against which model evaluations are tested. Humans and models assess the same essays against the same questions. SlopBench measures whether model judgments track value to the intended reader, as stated explicitly in the main text (§3.3, lines 267–269). Their overwhelming disagreement is the evaluation failure mode revealed by SlopBench.

To incorporate the reviewer's feedback, we will highlight this further in the main text.

5. Web access is already prevented in the evaluation code.

We query frontier judges through APIs and prevent web use in the evaluation code through API settings. Thus, compliance is not entrusted solely to the prompt.

6. Suggestion for further agreement analysis.

Thank you for the suggestion. The released reader-level annotations already permit reliability analysis. We also report in Appendix H.3 pairwise directional agreement of 83.5% for quality and 83.0% for usefulness on A0A_0–A16A_{16}, conditional on both readers expressing a preference (lines 2946–2949). More directly, every one of the 25 tasks has four or five readers preferring A0A_0 for quality, and none has a human majority favoring A16A_{16} for either quality or usefulness. The observed reversal is consistent across tasks and readers.

Please let us know if you have any remaining questions or concerns. We are more than happy to discuss further.

References

[1] Dubois et al., Length-Controlled AlpacaEval: A Simple Way to Debias Automatic Evaluators. Conference on Language Modeling (COLM), 2024.

[2] Li et al., From Crowdsourced Data to High-quality Benchmarks: Arena-Hard and Benchbuilder Pipeline. International Conference on Machine Learning (ICML), 2025.

[3] Huang et al., Post-hoc Reward Calibration: A Case Study on Length Bias. International Conference on Learning Representations (ICLR), 2025.

[4] Kim et al., Prometheus: Inducing Fine-Grained Evaluation Capability in Language Models. International Conference on Learning Representations (ICLR), 2024.

[5] Panickssery et al., LLM Evaluators Recognize and Favor Their Own Generations. Advances in Neural Information Processing Systems (NeurIPS), 2024.

Thank you again for your feedback. Please let us know if any questions or concerns remain. We are more than happy to discuss further.

Reviewer_pgvfOpenReview ↗
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Paper summary

This paper investigates the divergence between LLM judges and human evaluations when large language models repeatedly revise open-ended responses. The authors introduce SLOPBENCH, a benchmark consisting of 50 open-ended writing tasks. The benchmark generates different versions of essays through 16 rounds of whole-essay rewriting and local editing, and evaluates them using eight LLM judges and human readers. The results show that LLM judges generally prefer essays that have undergone multiple rounds of whole-essay rewriting, whereas human readers strongly prefer the original versions, revealing a substantial divergence between model evaluations and human preferences during automated revision.

Critical strengths
  1. Practical significance of the research problem. The paper addresses the misalignment between model evaluation signals and human preferences during iterative self-revision, providing valuable insights for LLM-as-a-Judge and automated model improvement systems.

  2. Novelty of the benchmark design. The authors construct SLOPBENCH, which incorporates multi-round revision trajectories, different revision strategies, and human evaluations, providing a valuable testbed for studying biases in model-based evaluation.

  3. Strong empirical evidence. The experiments cover multiple LLM judges and validate the evaluation divergence through blinded human assessments. The substantial and directionally opposite preferences between models and humans are noteworthy.

Critical weaknesses
  1. Limited task diversity in the benchmark. SLOPBENCH contains only 50 open-ended questions across five domains, with tasks primarily focused on long-form conceptual analysis. For a benchmark intended to evaluate model self-revision and evaluation reliability, the current task scale and diversity remain limited. It is unclear whether the findings generalize to a broader range of open-ended tasks.

  2. Limited human evaluation coverage across revision trajectories and generation models. Although the paper generates complete 16-round revision trajectories for each task, human evaluations focus on six pairwise comparisons among four representative versions, with each comparison covering only a subset of tasks. Furthermore, human evaluations are restricted to Opus 4.8-generated essays and do not include the separate Sol 5.6-generated essay bank. While the existing evaluations strongly support the main finding of preference reversal, their limited coverage restricts the ability to assess whether this phenomenon generalizes across different revision stages and generation models.

  3. The practical value of the benchmark relative to existing evaluation methods requires further validation. Previous studies have proposed various methods to improve the alignment between LLM-as-a-Judge evaluations and human preferences. This paper primarily evaluates different models and prompting settings but lacks systematic comparisons with existing calibration or bias-mitigation methods. Consequently, it remains unclear whether SLOPBENCH can effectively measure improvements achieved by existing evaluation methods and what additional evaluation capabilities it provides beyond existing judge benchmarks.

Questions for authors
  1. Could the authors further clarify the selection criteria for the 50 tasks? Could the benchmark be extended to additional types of open-ended tasks to validate its coverage and the generalizability of the findings?

  2. Could the authors provide additional human evaluations across different revision stages or generation models to examine whether the observed evaluation divergence persists throughout the complete revision trajectories?

  3. Could the authors evaluate existing judge calibration or bias-mitigation methods on SLOPBENCH to further demonstrate the benchmark's practical value in distinguishing the effectiveness of different evaluation methods?

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Author Response (1/2)

We thank reviewer pgvf for their review and for recognizing the practical significance of the problem, the novelty of the benchmark design, and the strength of the empirical evidence. We agree that SlopBench reveals a substantial divergence between frontier model and human judgements that is relevant for open-ended task revision. Below, we incorporate the reviewer's feedback.

1. Why does SlopBench have only 50 open-ended tasks?

Our benchmark requires substantial human evaluation of long-form answers. Each task produces 33 recorded versions per writer, i.e., the initial answer and sixteen revisions under each of two editing policies. Across 50 tasks, this gives 26,400 possible pairs for the Opus bank alone (§3.1, lines 221–225). Therefore, the limiting resource is careful human annotation, and not the availability of candidate comparisons.

We therefore allocate human evaluation to all six pairs among A0A_0, A1A_1, I16I_{16}, and A16A_{16}. These comparisons examine the first rewrite, further revision, and the alternative editing policy (§3.3, lines 244–249). Each pairing receives five independent human readings, and the complementary task sets collectively cover all 50 tasks (Appendix H.1–H.2, lines 2866–2872 and 2916–2925).

SlopBench provides 1,000 essay-pair evaluations from 273 readers, releasing high-quality human gold responses to 15,000 structured questions as well as 16,000 written explanations across quality, usefulness, and diagnostic dimensions (Appendices E.1 and H). By comparison, prior human studies, e.g., Prometheus [1] comprises just 405 annotation instances from 9 annotators, yielding 405 response scores and 405 feedback-preference judgments, alongside categorical reason selections. Panickssery et al. [2] collect 900 summary-pair preference judgments from just 20 annotators, covering 300 distinct pairs with three annotations each. Neither study’s protocol requests written explanations. In contrast, SlopBench’s 10,000+ written explanations from hundreds of human readers enable additional high-quality qualitative analysis of the reasons for human preferences and how these differ from model judges’ assessments.

2. How are SlopBench tasks selected?

The selection criteria are detailed in §3.1, lines 213–219, and Appendix C.2. We deliberately target open-ended domains where no executable test or formal verifier determines whether an answer has improved. This makes the frontier model’s evaluative judgment--and its taste among competing qualities--the object of study.

SlopBench contains ten questions in each of five domains: public services and shared spaces; work and education; consumer technology; environment and infrastructure; and history, media, and cultural interpretation (§3.1, lines 213–219; Appendix C, Figure 6, lines 983–998). The questions require explanation, interpretation, or judgment among competing open-ended considerations and are answerable from ordinary background knowledge. The benchmark tests whether a model’s judgments of reasoning, clarity, and usefulness track what human readers actually value. Its task design directly serves that objective.

3. Can you provide additional human evaluations?

Unfortunately, additional human studies, including annotations of the Sol-written trajectories, are not feasible within the annotation budget nor the rebuttal period. The existing study already supplies tens of thousands of substantial and extensive human explanations across hundreds of human readers for the paper’s contribution. This clearly identifies a regime in which frontier judges overwhelmingly endorse revisions that their intended readers find worse and less useful.

The released benchmark also permits substantial further analysis without collecting new judgments. For example, our task-level analysis of A0A_0 versus A16A_{16} shows that none of the human-evaluated tasks has a human majority favoring A16A_{16}, for either quality or usefulness. For quality, four or five of the five readers prefer A0A_0 on every task. Meanwhile, model evaluations favor A16A_{16} in 98–100% of Claude judgments and 69–86% of GPT judgments (Table 1). The disagreement is systematic across the tested tasks and judges.

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Author Response (2/2)

4. Can you evaluate existing judge calibration or bias-mitigation methods on SlopBench?

A systematic comparison of published calibration methods is not the focus of this work. However, we clarify that the paper already measures how interventions change both diagnostic judgments and selection decisions.

  • Explicit prediction of human preferences. Asking judges to predict a human reader moves Claude endorsement of A16A_{16} from 98.3–100% to 75.0–97.3%, but moves GPT endorsement from 69.3–86.3% to 75.3–88.7%--farther away from the observed human rate of 8% (Appendix I.2, Table 20; staged evaluations). The benchmark detects different intervention effects across evaluator families, while showing that the resulting verdicts still overwhelmingly disagree with readers.

  • An explicit rubric for revision-induced textual patterns. For Fable 5, the rubric increases identification of the more revised essay as robotic from 16.9% to 72.4%, yet preference for that essay falls only from 99.2% to 90.9% (Appendix K.3, Table 23; directional shares pooled across the six comparison types). The rubric changes the diagnosis while leaving the preference for deeper revision overwhelming. That is a distinction a useful evaluation benchmark would expose.

A new judge or calibration method can be scored on SlopBench by agreement with human majorities on overall quality and usefulness. Also, our Likert-scale questionnaire probes twelve additional diagnostic dimensions, providing a fine-grained basis for evaluating model judgments against human assessments of reasoning, task responsiveness, reading experience, style, length, and the need for further revision.

Comparing additional calibration methods is an impactful follow-up work enabled by our publicly released benchmark. We explicitly identify stronger calibration of model judges to human readers as a future research direction (Appendix A.2, lines 877–882), and call for testing calibration methods across model families and open-ended domains (Appendix A.2, lines 887–888). SlopBench demonstrates that frontier models overwhelmingly select answers that humans reject, and releases high-quality human gold responses to 15,000 structured questions as well as 16,000 written explanations across various diagnostic dimensions for follow-up work.

Please let us know if you have any remaining questions or concerns. We are more than happy to discuss further.

References

[1] Kim et al., Prometheus: Inducing Fine-Grained Evaluation Capability in Language Models. International Conference on Learning Representations (ICLR), 2024.

[2] Panickssery et al., LLM Evaluators Recognize and Favor Their Own Generations. Advances in Neural Information Processing Systems (NeurIPS), 2024.

Thank you again for your feedback. Please let us know if any questions or concerns remain. We are more than happy to discuss further.

Comments on the paper

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Area_Chair_55mMOpenReview ↗

Reminder: Please Review the Author Response and Reconsider Your Final Decision

Dear Reviewers,

This is a gentle reminder to review the authors’ response to your comments. After considering their clarifications and rebuttals, I kindly ask you to reassess your review and update your final recommendation if warranted.

Thank you for your time and thoughtful consideration.

Best regards,

Area Chair

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