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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.
6 comments
Author Response (2/4)
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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 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.
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Recognizing undesirable features does not reliably correct the phenomenon. GPT judges do recognize limits to attention and readability while still assigning 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 – tasks within 10% in word count, humans prefer in 9/10 judgments for both quality and usefulness (lines 2981–2983). In the – tasks within 20%, humans prefer in 22/25 quality judgments, versus just one for (lines 2983–2986). Length-based regression adjustment changes the – 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 over ?
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 .
5. Are human judgments consistent across tasks and reader groups?
Yes. Human preference percentages and 95% confidence intervals are:
| Preference measured | Tasks | Quality, % [95% CI] | Usefulness, % [95% CI] |
|---|---|---|---|
| over | 10 | 22.0 [12.0, 32.0] | 30.0 [20.0, 42.0] |
| over | 25 | 22.4 [14.4, 31.2] | 21.6 [13.6, 30.4] |
| over | 10 | 46.0 [32.0, 58.0] | 26.0 [12.0, 40.0] |
| over | 25 | 8.0 [4.0, 12.8] | 8.8 [4.0, 14.4] |
| over | 25 | 8.0 [4.0, 12.0] | 8.0 [4.0, 12.8] |
| over | 25 | 27.2 [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 –, 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 for quality in every task, whereas in stark contrast, at least six of eight model judges all favor in exactly the same tasks. Each model’s preference is determined by majority vote across its six evaluations of that task.
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 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 –:
| Reading-time quartile | Judgments | Preferred : quality | Preferred : usefulness |
|---|---|---|---|
| Fastest | 31 | 87.1% | 77.4% |
| Second | 31 | 93.5% | 90.3% |
| Third | 31 | 90.3% | 87.1% |
| Slowest | 32 | 90.6% | 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.
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 A0 with A16, not one task has a human majority favoring A16, for either quality or usefulness, while only 8% of pooled human judgments favor A16. 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 A16 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: