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Under review as a conference paper at ICLR 2027

Skill Training with Corruption and Reconstruction Loop

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Abstract

Large Language Models (LLMs) often struggle in highly specialized domains. Rather than parameter-level adaptation of LLMs which is costly and difficult to interpret, external skills (often defined as text files) have been recently proposed to augment LLMs for specialized domains. However, such skills rely on costly active human annotations or passive summarization of high-quality examples. In this paper, we propose a self-supervised approach for agent self-evolution that learns domain-specific skills directly from existing high-quality human artifacts, without additional human annotations or external rewards. Inspired by diffusion models, our approach follows a forward–loss–backward process to reconstruct human artifacts by iteratively learning the agent's external skill library rather than updating its model parameters. Experiments on short-drama screenwriting demonstrate that our approach enables agents to autonomously extract generalizable writing skills from human-authored scripts and substantially improve domain-specific generation quality. Our approach provides a scalable paradigm for agents to continuously learn many kinds of complex skills from existing high-quality human artifacts.

Primary area:
foundation or frontier models, including LLMs
Keywords:
LLM agents, short drama scriptwriting, self-supervised learning, reconstruction, test-time learning, agent skills

Reviews

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Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.67 over 3 reviews, above 70% of the others.
Reviewer_FhQ7OpenReview ↗
Rating
2
Confidence
3
Informativeness
1
Presentation
2
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2
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Paper summary

A Framework Paper on Agent Self-Evolution. By using the diffusion model "corruption-reconstruction" and text gradient back propagation, the 20 professional short plays were pressed into an outline, and the script agent reconstructed, the loss agent produced the semantic difference report, and the backward agent performed the addition, modification and merging of the text skill library organized by MoE, and the parameters were frozen in the whole process. 1,200 token linter hard regular, 6 novels 385 sets set, 10 event-level metrics + 5 people blind rating.

Critical strengths

1.The "professional finished product does not contain amateur errors" is transformed into an operational error-driven signal, that is, a self-supervised pair is constructed by corrosion-reconstruction, which is an exact design and is supported by +Distill control experiments.

2.Rule linter forces the abstraction of skill cards with hard capacity constraints, which is a practical engineering technique to curb the expansion of skill library, and brings a certain degree of attribution to the training process.

3.The phenomenon of "weak model mining rules, strong model execution" in cross-model experiments is a valuable side observation.

Critical weaknesses

Reproduction Concern. 1.The evaluation system is completely private and closed loop: neither the training corpus nor the reserved test set is distributed, the ten indicators are customized for this paper and there is no public benchmark anchor, two of the five readers are the authors, so all the core figures cannot be reproduced by the third party or compared horizontally.

2.The paper abandoned the public evaluation method on the basis of "LLM referee scoring is unreliable ", but its own five episode level indicators still rely on LLM referee, and it has never done meta-verification on the form of referee on public data, and there is no evidence whether the criticized failure mode has been eliminated.

3.Several key designs have only qualitative support: the contribution of key component without performance ablation.

Questions for authors

1.Could you run one inference-only control: give Opus the +Distill rule library (or any comparably strict, non-error-driven rule set) and compare it with Sonnet's loop-trained library? If the non-error-driven library matches the gains, the paper's central "error-driven" attribution is falsified — the benefit would come from rule strictness, not from the reconstruction loop.

2.Could you report, from your existing logs, the recurrence rate of errors after the corresponding rule was added to the library? If a large fraction of loss items re-flag errors that already have a matching rule, the credit-assignment claim is falsified — the backward agent would be compensating for retrieval/execution failures that the framework never models, rather than learning new skills.

3.Could you retrain the loop with the learned corruption step replaced by a fixed, non-learned compressor (e.g., extractive scene headers)? If the learned skills and downstream metrics are statistically unchanged, the diffusion-style corruption is falsified as a mechanism — it serves only to construct pairs, and the analogy should be removed from the framing.

4 comments
AuthorsOpenReview ↗

Response to Reviewer FhQ7 (Part 1 of 2): W1, W2, W3 & Q1

We thank the reviewer for the thorough reading and for highlighting our error-driven learning signal, the rule linter constraint, and our cross-model findings. Below we address each weakness and question in detail.

W1. The evaluation is private and cannot be reproduced by third parties.

Because our training and test screenplays are commercial scripts under copyright, we cannot redistribute the raw text. To ensure our methodology and evaluation are fully reproducible on any screenplay corpus, we will open-source the complete training framework, the deterministic line-level parsers, the exact definitions of all ten metrics, and all LLM judge prompts. More importantly, to provide a fully public benchmark anchor with objective horizontal comparison, we also evaluated our exact corruption-and-reconstruction loop on the public SWE-bench Pro benchmark (Deng et al., 2025), where correctness is strictly verified by executable unit tests (pass@1). On SWE-bench Pro with Claude Sonnet 4.6, our loop raises pass@1 from 34.0% (Base) to 42.5%* (+Ours), also outperforming +Few-shot (35.5%) and +Distill (31.0%). Please see our response to Reviewer YAJd (W1) for the full setup and table. Finally, regarding the two author-readers in the human study, we recruited five additional external readers during the rebuttal period. With both authors completely excluded, the eight external readers prefer our trained library over the empty library by 77 wins to 28 losses (net preference +40.8%, 95% CI: [+20.8%, +59.2%], permutation test p = 0.003), and the professional screenwriter alone prefers it 10 to 2 (sign test p = 0.039). Please see our responses to Reviewers YAJd and rePM for the full breakdown.

W2. The paper criticizes LLM-as-judge scoring but still relies on an LLM judge for five episode-level metrics.

We appreciate the opportunity to clarify this distinction. What we criticize in Section 4.1 is unanchored holistic scoring, where an LLM judge assigns an overall impression score from 1 to 5. As noted in Section 4.1, holistic scores are highly unstable and can swing from 2 to 4 on the exact same script across runs. In contrast, our five episode-level metrics reformulate judging into narrow, evidence-grounded event detection, four yes-or-no checks and one count of plot conflicts: the judge only checks whether a specific structural event occurred, such as whether the final scene cuts mid-action before the outcome lands, and is required to quote the exact script lines supporting its verdict. We verified empirically that this formulation eliminates the run-to-run instability of holistic scoring: across five independent re-evaluations of the same 385 scripts, the hard-cut ending rate varies by at most 1.3 percentage points and cold opens by at most 0.8 percentage points (test-retest Cohen's κ=0.94–0.97\kappa = 0.94\text{--}0.97), and cross-checking our primary judge (Gemini 3.1 Pro Preview) against Claude Opus 4.8 yields 94% verdict agreement.

W3 & Q1. Key designs lack ablations. Would Opus with a strict but non-error-driven library, such as the +Distill library, match the gains?

This is a great falsification test, and we ran this exact experiment during the rebuttal period. We evaluated Claude Opus 4.8 across all 385 held-out episodes under three conditions: with an empty library (Opus Base), with the 20-novel +Distill library (131 strict rule cards distilled directly from the human scripts under the same 1,200-token linter limit), and with our 20-novel loop-trained library (23 rule cards).

MetricOpus BaseOpus + Distill libraryOpus + our libraryHuman
Unfilmable action lines ↓0.60.8*0.1*0.4
Stimulus words ↑8.89.111.0*9.2
Plot conflicts / 1k words ↑2.592.24*4.02*3.47
Hard-cut ending ↑46%42%67%*62%
Cold open ↑68%70%83%*59%
Prop activation ↑56%59%77%*57%

* denotes that the 95% paired bootstrap confidence interval against Opus Base excludes zero.

When Opus is given the non-error-driven +Distill library, 0 of the 6 directional metrics improve significantly and 2 actually degrade significantly (Unfilmable action lines and Plot conflicts). In contrast, with our loop-trained library, all 6 directional metrics improve significantly across the held-out novels. This directly confirms that the gains come from the error-driven reconstruction loop rather than rule strictness alone. The other components, including the 1,200-token card limit, the routing of cards by their descriptions, and the serialized micro-steps, are shared by +Distill and +Ours. Since the two methods differ only in the source of the learning signal, the advantage of +Ours over +Distill does not come from these shared components.

AuthorsOpenReview ↗

Response to Reviewer FhQ7 (Part 2 of 2): Q2, Q3

Q2. What is the recurrence rate of errors after the corresponding rule was added?

First, once a concrete rule is added to the library, the corresponding error drops sharply and stays low. As shown in Figure 7 of Appendix G, unfilmable action lines fall by 70% within the first five backward micro-steps, from 1.31 to 0.39 per episode. Over the full training, missing hard-cut endings drop by half, from 66% of episodes for Base to 33% for the final library (Table 2).

Second, we sampled 276 of the 687 loss reports from the 20-novel run, comprising 1,758 diagnosis items across all training steps, and checked how each item relates to the library at that step. 29% of the items had no matching rule in the library yet. 55% fell under a topic card that the forward agent had read, and 16% fell under a topic card that was not retrieved. GPT-5.5 and Claude Opus 4.8 agreed on these proportions within 1.5 percentage points.

Crucially, the 55% that fall under a read card do not mean that the agent ignored the card. Our library organizes knowledge into 23 broad topic cards that are mostly built early in Epoch 1, when most of the library growth happens (Figure 6b), so later problems naturally fall under these same cards. Each card bundles many rules within 1,200 tokens, and an early rule is usually stated as a broad principle. Different novels and different stages of a drama, such as an opening setup versus a mid-story betrayal or climax, present new situations where the broad rule is not yet concrete enough to be applied reliably. When the backward agent updates a read card, it rewrites the broad rule into a more concrete procedure for these situations. This is consistent with Appendix F, where libraries trained on more novels turn broad instructions into more precise, context-aware procedures. Similarly, for the 16% where a card was not retrieved, the backward agent broadens the card's description so that it is triggered in the newly encountered scene types. Credit assignment therefore keeps expanding the coverage and precision of existing cards, rather than merely compensating for execution failures.

Q3. Would replacing the learned corruption step with a fixed, non-learned compressor leave the results unchanged?

We clarify a slight misunderstanding here: just as the forward noising process in standard diffusion models (Ho et al., 2020) is a fixed, non-learned operator and only the reverse denoising process is trained, our corruption step is already a fixed, non-learned compressor. Specifically, it is a frozen LLM call with a fixed prompt that strips dialogue and action details into a story outline, receiving zero updates during training. Only the skill library used in the reverse reconstruction step is trained. What matters for our diffusion-inspired loop is that the forward corruption strips away domain craft while preserving the story skeleton, forcing the reconstruction step to recover that craft and exposing capability gaps when compared against the human original. Replacing the prompt-based summarizer with another fixed compressor that strips the same craft details would serve the same functional role. We will add these clarifications to the revised manuscript, such as the Opus control with the +Distill library, the recurrence analysis, and the role of the corruption step in Section 3.1.

Thank you for the substantial rebuttal. Running the Opus +Distill control during the rebuttal period is exactly what I asked for, and I accept its result: rule strictness alone does not explain the gains. The stability checks and the new external readers also help.

Still, a few things keep me at a 2. First, in your own table the trained library beats the human reference on 4 of 6 metrics (cold open 83% vs 59% for humans, prop activation 77% vs 57%). If these metrics really track professional craft, the system should approach human values, not shoot well past them. To me this pattern suggests the loop may be optimizing the LLM-judged metrics themselves, and I would like to see this addressed head-on rather than with more gains on the same metrics. Second, the comparison still lives entirely inside the private evaluation loop, and the +Distill arm differs from yours not only in the learning signal but also in size (131 vs 23 cards), which muddies the attribution. Third, SWE-bench Pro is encouraging, but it is a different domain and the setup details are in another thread; the screenplay claims themselves remain unverifiable by third parties. The new human study compares against an empty library, which is a low bar.

On Q2, 71% of loss items fall under cards that already existed. Your concretization reading is plausible, but a split of that 55% into "same specific rule re-flagged" vs "genuinely new situation" would settle it. On Q3, thanks for the clarification; I had misread the corruption step as learned. I would still suggest softening the diffusion framing, since with both directions frozen it is mostly a metaphor.

I appreciate the work that went into this response. With the human-overshoot pattern unexplained and the in-domain numbers still private, I keep my score at 2, though this rebuttal has genuinely narrowed my concerns.

Thank you very much for taking the time to review our rebuttal and for acknowledging that the Opus +Distill control, stability checks, and expanded human study have genuinely narrowed your concerns. We briefly address your remaining points below:

  1. Human-overshoot & whether the loop optimizes the LLM-judged metrics: We addressed this head-on in Response to Reviewer rePM (W1 & Q1) and Appendix J (Table 18) of the revised PDF. First, the loss agent never sees the 10 evaluation metrics or judge prompts during training (Section 3.3, Appendix A), so it cannot optimize the metrics directly. Second, in a direct episode-level fidelity test asking two independent judges which script is closer in craft to the held-out human original of the same episode (Appendix J, Table 18), +Ours is judged closer to the human original than Base (84%), +Few-shot (90%), and +Distill (95%), and episode-level Cohen's κ\kappa on prop activation rises from 0.35 to 0.55. Why do aggregate hook rates exceed the human average? Because human writers use hooks in ~60% of episodes and relax pacing on transition episodes, whereas our compact rules apply hooks consistently across every episode—which is why the professional screenwriter preferred +Ours even over the human original in 9 of 15 pairs (Appendix H, Table 16), noting that the human originals occasionally failed to hold the ending hook.

  2. Library size (131 vs. 23 cards) & inference budget: Both +Distill and +Ours were trained on the exact same 20 novels for 174 micro-steps under the identical 1,200-token card limit. More importantly, at inference time the agent does not load the entire library into context: under our MoE routing mechanism and identical context budget (Section 4.1, Appendix A), the agent only opens the subset of cards relevant to the current outline. Furthermore, in our 5-novel multi-run experiments (Appendix E.1, Table 12), where both libraries are much smaller, +Ours still consistently outperforms +Distill on every directional metric.

  3. Human study comparisons, SWE-bench Pro details, and diffusion framing: Our expanded 8-reader study (Appendix H, Tables 15–16) does not only compare against an empty library—it explicitly evaluates against Human Originals as well (narrowing the net preference gap to human scripts from +69.2% to +41.7%), and the full SWE-bench Pro setup and results are integrated into Appendix I (Table 17) of the revised PDF. Unlike our screenplay corpus, SWE-bench Pro is fully public. Its tasks, repositories, and unit tests are all open, so third parties can directly verify our results on this benchmark. Finally, we appreciate your suggestion on Q3 and will gladly soften the diffusion framing to make clear that it serves as a conceptual inspiration for self-supervised pair construction.

Reviewer_rePMOpenReview ↗
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3
Confidence
3
Informativeness
2
Presentation
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2
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Paper summary

The paper learns an external skill library for an LLM agent without annotations or rewards. Human screenplays are compressed into outlines, and the agent reconstructs them using rule cards. A loss agent compares each reconstruction with the original, and a backward agent edits the cards. On short-drama screenwriting (20 training and 6 held-out novels), the learned library significantly improves all six directional craft metrics over an empty library. Few-shot prompting and a matched rule-distillation baseline do not. The learned skills transfer to other models, and blind readers prefer scripts written with the trained library.

Critical strengths
  1. A simple and general learning signal for open-ended domains. Reconstructing existing human artifacts provides supervision where verifiable rewards are unavailable, and the resulting skills are human-readable and portable across models (Sec. 4.3, App. F).
  2. A well-controlled key comparison. +Distill uses the same novels, schedule and card limits, and differs only in whether the agent learns from its own reconstruction errors. +Ours wins with 23 cards where +Distill's 131 cards bring no structural gain, and the paired bootstrap shows consistent improvements across held-out novels (Table 3).
Critical weaknesses
  1. There is a misalignment between the training objectives and the evaluation criteria. While the training process aims to replicate scripts created by humans, its success is measured using proxy metrics that may introduce specific biases. In some respects, the model even outperforms human benchmarks: for instance, it achieves a score of 67% for "hard-cut endings" (compared to 62% for human-authored examples) and 74% for "cold opens" (compared to 59% for human-authored examples). Consequently, it remains unclear whether the training loop has truly acquired the craft of human creators or has simply amplified specific features that boost metric scores.

  2. The human evaluation component has notable limitations. Only five readers participated in the assessment—two of whom were themselves writers—and there was low inter-rater agreement (κ = 0.197). Excluding the two writers, the comparison between the "trained" model and the "untrained" (null) model yielded scores of 24 and 14, respectively.

  3. Each configuration was trained only once within a single, proprietary domain. This makes it difficult to assess variability between different training runs—such as the performance decline observed when processing 10 novels, as noted in Section 5.1.

Questions for authors
  1. Were the ten metrics fixed before inspecting the learned libraries? Can you report a direct fidelity measure against the held-out human scripts?
  2. What are the preference results and intervals when the two author-readers are excluded?
  3. Can you report ≥2–3 independent training runs for +Ours and +Distill at 20 novels?
3 comments
AuthorsOpenReview ↗

Response to Reviewer rePM (Part 1 of 3): W1 & Q1

We thank the reviewer for the positive assessment of our work and for recognizing both the generality of the reconstruction signal and the rigor of our +Distill control experiment. Below we address each weakness together with its paired question.

W1 & Q1. The training objective differs from the evaluation metrics, and some gains exceed the human reference. Were the metrics fixed before inspecting the libraries, and can you report a direct fidelity measure?

Yes, we can confirm that all ten metrics were designed together with professional short-drama practitioners before we ran training or inspected any learned library. Moreover, the loss agent never sees these metrics or the judge prompts during training, so the skill library is never optimized toward the evaluation metrics directly. Instead, it is learned in a self-supervised way from the gap between its own reconstructions and the human scripts, and it discovers on its own the craft differences that the expert-defined metrics measure.

To measure direct fidelity against the held-out human scripts, we point to both our existing episode-level error metrics and two new analyses. In Table 2 of the main paper, the auxiliary dd columns already report the episode-level paired mean absolute error against the human originals, where +Ours achieves lower error than Base and +Distill on five of the six count and density metrics. We also ran a blind pairwise fidelity test over 120 held-out episodes: an independent judge read the human original alongside two generated scripts for the same episode and chose the one closer to the human original in writing craft. Scripts written with +Ours were judged closer to the human original than Base in 84% of comparisons, closer than +Distill in 95%, and closer than +Few-shot in 90%. GPT-5.5 and Claude Opus 4.8 agreed on 88% of these decisions. In addition, using the existing episode-level verdicts from Table 2, we checked whether the agent activates key props in the exact same episodes where the human writer did. Cohen's κ\kappa against the human script rises from 0.35 for Base to 0.55 for +Ours, showing that the learned library places this device where human writers use it.

On why hard-cut endings and cold opens exceed the human average, this comes from how our backward agent abstracts rules. Human writers use these two hooks in roughly 60% of episodes, whereas Base defaults to slow openings and resolved endings. Because our backward agent distills recurring gaps across novels into general rules under a 1,200-token limit, the script agent applies these rules consistently across episodes, which explains why the hook rates exceed the human average that includes slower transition episodes. Importantly, this consistent execution reflects desirable short-drama craft rather than metric gaming. In our blind human study in Appendix H, the professional screenwriter actually preferred +Ours over the human original in 9 of 15 pairs, noting that the human scripts sometimes failed to hold the ending hook or had low information density.

AuthorsOpenReview ↗

Response to Reviewer rePM (Part 2 of 3): W2 & Q2

W2 & Q2. The human study is limited, two readers are authors, agreement is low, and excluding the authors gives 24 vs. 14.

We agree that the original panel was small, and we appreciate the request to examine the author-excluded results directly. During the rebuttal period, we recruited five additional external readers, graduate students who had no involvement in this project, bringing our non-author panel to eight external readers in total. All new readers evaluated the exact same 45 episode pairs under the blind protocol of Appendix H. The table below reports the main comparison between the empty library and the trained library across both the original three external readers and the expanded panel.

ReadersTrained winsTiesEmpty winsNet preference [95% CI]
Original three external readers, authors excluded24714+22.2% [−8.9, +51.1]
Professional screenwriter1032+53.3% [+13.3, +86.7]
Expanded eight external readers, authors excluded771528+40.8% [+20.8, +59.2]
All ten readers1021731+47.3% [+30.7, +63.3]
Original five readers, as in the paper49917+42.7% [+22.7, +61.3]

On the original three external readers, the votes favor the trained library at 24 wins to 14 losses (+22.2% net preference, 95% CI: [−8.9%, +51.1%]). The confidence interval is wide because three readers provide only 45 votes, though the professional screenwriter alone already shows a strong and statistically significant preference (10 wins to 2 losses, sign test p = 0.039). When we expand the panel to eight external readers with both authors excluded, the trained library wins 77 to 28 with a statistically significant net preference of +40.8% [95% CI: +20.8%, +59.2%] (episode-level permutation test p = 0.003), and 7 of the 8 external readers individually favor the trained library.

Regarding inter-rater agreement, expanding the panel raises κ\kappa among the eight external readers to 0.24, up from 0.11 for the three external readers of the original panel and 0.197 for the original five-reader panel. Their raw pairwise agreement reaches 53.7% over the three choices, well above the 33.3% random chance level. In open-ended script evaluation, episode-level κ\kappa is naturally moderate because readers from different backgrounds prioritize different dimensions, such as cliffhanger pacing versus dialogue naturalness, as we analyze in Appendix H. Even so, their overall preference for the trained library is clear and consistent.

AuthorsOpenReview ↗

Response to Reviewer rePM (Part 3 of 3): W3 & Q3

W3 & Q3. Each configuration is trained once, so run-to-run variance, for example the dip at 10 novels, is hard to judge. Can you report two to three independent runs?

We agree that single-run results make it harder to separate genuine method gains from run-to-run variance. Because a single 20-novel run takes 57 hours of wall-clock time, we ran three additional independent training runs from scratch for both +Ours and +Distill under the 5-novel, 3-epoch configuration. Each run starts from an empty library and is evaluated on the full set of 385 held-out episodes. The table below reports the mean and standard deviation across the three new runs.

MetricBase+Ours (3 runs)+Distill (3 runs)Human
Unfilmable action lines ↓1.20.3 ± 0.01.0 ± 0.20.4
Stimulus words ↑3.35.8 ± 0.54.1 ± 0.39.2
Plot conflicts / 1k words ↑2.103.19 ± 0.142.03 ± 0.133.47
Hard-cut ending ↑33.8%55.1 ± 6.0%42.2 ± 5.0%62.1%
Cold open ↑51.7%69.4 ± 2.6%57.1 ± 2.3%59.0%
Prop activation ↑46.0%57.5 ± 3.4%47.7 ± 1.1%57.4%

All four +Ours runs, including the original 5-novel run in Section 5.1 and the three new runs, improve over Base on every directional metric. On five of the six metrics, the original run falls within one standard deviation of the new three-run mean. On the sixth, unfilmable action lines, the new runs are even better than the original run (0.3 vs. 0.46). The advantage over +Distill holds consistently across every run. This confirms that the improvements come from the training framework rather than a lucky run.

To understand the dip at 10 novels in Section 5.1, we compared it with the fluctuation between consecutive library snapshots within our 20-novel run. Even after the first epoch, the hard-cut rate between adjacent snapshots still moves by 6 to 12 percentage points. The gap between the 5-novel and 10-novel libraries falls within this range, indicating that the dip reflects normal checkpoint fluctuation rather than a negative effect of corpus size. Finally, regarding the concern about evaluating on a single proprietary domain, we also tested our framework on the public SWE-bench Pro benchmark, where correctness is verified by executable unit tests. Please see our response to Reviewer YAJd (W1) for the results.

We will add these clarifications to the revised manuscript, such as the fidelity analyses, the expanded human study, and the repeated training runs.

Reviewer_YAJdOpenReview ↗
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3
Confidence
2
Informativeness
2
Presentation
3
Soundness
2
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Paper summary

This paper proposes a method for learning skills from high-quality human artifacts without updating model parameters. It first compresses artifacts made by human experts (e.g., screenplays) into outlines, then asks an agent to reconstruct the scripts using its current skills. It alsos have a loss agent that comparing the generated scripts with the human originals, and a backward agent that updating the skills based on the differences. Experiments on short-drama screenwriting the effectiveness of the proposed method.

Critical strengths
  • The idea of learning skills from noising and denoising is interesting. It's reasonable to model this idea as learning from the differences between an agent’s outputs generated via a corrupted version and the original human references is interesting.

  • This paper is well written.

Critical weaknesses
  • The experiments in this paper mainly focus on short-drama screenwriting. This paper presents the method as a general approach for learning complex skills from human artifacts. Evaluation in additional domains would strengthen this claim. Also, it would be interesting to evaluate the method on the tasks with more objective correctness criteria to demonstrate the capability improvements beyond the changes in writing/presentation style.

  • The learning signal comes from the differences (identified by an LLM) by comparing a generated script with a human reference. However, differences from the reference are not necessarily errors in most open-ended tasks. It would be beneficial to have an detailed analysis of the reliability of this learning signal and whether it can penalize valid alternative approaches and therefore penalize some useful capabilities such as the creativity.

  • The human evaluation in this paper is relatively small-scaled. It only involves five readers, including two paper authors.

Questions for authors

see above

2 comments
AuthorsOpenReview ↗

Response to Reviewer YAJd (Part 1 of 2): W1

We thank the reviewer for finding the idea of learning skills through corruption and reconstruction interesting and the paper well written. We address each concern below.

W1. Evaluation is limited to short-drama screenwriting, and a task with objective correctness criteria would strengthen the generality claim.

We initially focused on screenwriting because domains with verifiable rewards, such as coding and math, already let agents filter successful trajectories with an external checker (Section 2), whereas open-ended domains offer no such signal and are where our method is most needed. However, we do agree that evaluating our framework in an additional domain with objective correctness criteria strengthens our generality claim. To test our method on tasks with strict, executable verification, we apply our corruption-and-reconstruction loop to repository-level software engineering on the public SWE-bench Pro benchmark (Deng et al., 2025), where correctness is objectively measured by human-written unit test suites (pass@1).

We sample 50 tasks across 10 open-source repositories on SWE-bench Pro. For each task, we collect historical human commits strictly prior to the task's base commit as clean human artifacts. During training, the corruption step strips away concrete code diffs, file paths, and internal symbols, compressing each commit into a high-level task outline. The coding agent (Claude Sonnet 4.6) then reconstructs the code patch from the outline using the current skill library, the loss agent compares the generated patch against the human commit to identify discrepancies in file localization and internal API usage, and the backward agent updates the skill cards under the same 1,200-token linter limit. We evaluate the trained skill library on held-out future tasks across 4 independent rollouts under the official Dockerized test harness, comparing Base (empty skill library), +Few-shot (in-context historical commits), +Distill (distilling rules directly from human commits without reconstruction), and +Ours (learned via the corruption-and-reconstruction loop).

Metric (SWE-bench Pro, Claude Sonnet 4.6)Base+Few-shot+Distill+Ours
Unit-test pass rate (pass@1, %) ↑\uparrow34.0%35.5%31.0%42.5%*

* denotes that the 95% paired bootstrap confidence interval against Base excludes zero.

As shown in the table, providing historical commits as in-context examples (+Few-shot) yields only a marginal change over Base (35.5% vs. 34.0%), while passively summarizing rules from human commits (+Distill) actually degrades performance to 31.0%. Consistent with our findings in Section 4.2, because finished human commits contain no amateur mistakes, +Distill accumulates unfocused, overly broad rules that distract the agent during codebase exploration. In contrast, learning from the reconstruction gap (+Ours) significantly raises the unit-test pass rate to 42.5%* (+8.5 percentage points over Base). Inspection of the trajectories shows that the compact, error-driven skill cards help the agent locate non-obvious companion files (such as central configuration registries and test mocks) and follow repository-specific abstraction contracts required for the unit tests to pass. This confirms that our framework improves objective problem-solving capabilities beyond stylistic adaptation.

AuthorsOpenReview ↗

Response to Reviewer YAJd (Part 2 of 2): W2, W3

W2. Differences from the reference are not necessarily errors, and the signal may penalize valid alternatives such as creative choices.

We agree with this insightful point, and we view this as a genuine limitation and trade-off of reference-based skill training. In open-ended generation, departing from a human reference is not necessarily an error. Because our training corpus consists of commercial vertical short dramas, contrasting against these references naturally steers the skill library toward a specific, high-intensity style. This style favors fast pacing, direct conflict, and hard-cut cliffhangers. It can narrow stylistic diversity and discourage valid alternatives such as slower atmospheric buildup or subtler emotional expression. Adding scripts of more diverse styles to the training corpus could alleviate this.

At the same time, we analyzed the training loss reports to understand why the learned skills still generalize well to unseen stories rather than overfitting to individual scripts. When we sampled 200 diagnosis items across all epochs and novels and asked a Claude Opus 4.8 judge to evaluate them with the full episode context, we found that 81% of the diagnoses target genuine craft defects rather than valid alternative choices. Typical defects are unfilmable psychological lines, static dialogue volleys, and missing hooks. Moreover, much like how diffusion models learn an average direction across examples despite computing loss against a single reference at each step, our backward agent updates rules only from reduced summaries of cross-novel commonalities under a 1,200-token card limit. Incidental differences on single episodes tend to cancel out across stories, and an audit of all 23 cards confirms that zero cards severely memorize plot details from specific novels.

W3. The human evaluation is small and two of the five readers are authors.

We agree that the original panel was small. During the rebuttal period, we added five readers to complement the three short-drama practitioners. The new readers are graduate students who were not involved in this project, and they represent the general audience that short dramas are written for. All readers rated the same 45 pairs under the blind protocol of Appendix H: the source of each script was hidden and the left-right order was randomized. With both authors excluded, the eight external readers give the following results.

Comparison (8 external readers)Former winsTieLatter winsNet preference [95% CI]
Empty vs. Trained library281577+40.8% [+20.8, +59.2]
Empty vs. Human101793+69.2% [+55.0, +81.7]
Trained library vs. Human271677+41.7% [+28.3, +55.8]

Without the authors, readers clearly prefer the trained library over the empty library (episode-level permutation test p = 0.003), and 7 of the 8 external readers individually favor it. The professional screenwriter, the only reader who writes scripts for a living, preferred the trained library in 10 of 15 comparisons and the empty library in only 2 (sign test p = 0.039). The panel also distinguishes quality reliably: human scripts are preferred over the empty library by +69.2%, but over the trained library by only +41.7%, so training narrows the gap to human writing without closing it. Agreement among the external readers rises to κ = 0.24, compared with 0.197 for the original panel. In the revised manuscript, we will report the expanded study in Appendix H and present the author-excluded results as the main human evaluation.

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Summary of Uploaded Revision and New Experiments

Dear Area Chair and Reviewers,

We sincerely thank all three reviewers for their thoughtful and constructive feedback. We are encouraged that the reviewers recognize our corruption-and-reconstruction framework as an interesting, simple, and general self-supervised learning signal for open-ended domains (Reviewers YAJd, rePM, FhQ7), highlight our error-driven formulation and well-controlled +Distill comparison (Reviewers rePM, FhQ7), and value the rule linter regularization as well as our cross-model transfer findings (Reviewer FhQ7).

We have now uploaded the revised manuscript (all changes are highlighted in blue), which incorporates all the new experiments, controls, and analyses conducted in response to the reviews:

  1. Generalization to a Public Objective Benchmark (Section 3.1; Appendix I, Table 17): To evaluate our method on a public benchmark with strict, executable verification, we applied our corruption-and-reconstruction loop to repository-level software engineering on SWE-bench Pro. With Claude Sonnet 4.6, our loop raises the unit-test pass rate (pass@1) from 34.0% (Base) to 42.5%* (+Ours), outperforming both +Few-shot (35.5%) and +Distill (31.0%).
  2. Expanded Author-Excluded Human Evaluation (Section 4.4; Appendix H, Tables 15–16): We recruited five additional external readers, expanding our non-author panel to eight external readers (120 blind judgments per comparison across 45 episode pairs). With both authors completely excluded, external readers prefer our trained library over the empty library by 77 wins to 28 losses (net preference +40.8%, 95% CI: [+20.8%, +59.2%], p = 0.003), with 7 of the 8 external readers individually favoring the trained library and the professional screenwriter favoring it 10 to 2.
  3. Error-Driven Attribution Control on Opus 4.8 (Appendix C.3, Table 6): Testing whether rule strictness alone explains cross-model gains, we evaluated Claude Opus 4.8 across all 385 held-out episodes with the 20-novel +Distill library (131 strict rule cards). While +Distill improves 0 of 6 directional metrics and significantly degrades 2 metrics, our 23-card loop-trained library significantly improves all 6 metrics.
  4. Multi-Run Training Stability (Appendix E.1, Table 12): Across three new independent training runs from scratch for both +Ours and +Distill on the 385 held-out episodes, +Ours consistently improves over Base and outperforms +Distill on every directional metric with low run-to-run variance.
  5. Episode-Level Alignment and Error Recurrence Analyses (Appendix G.1; Appendix J, Table 18): We added blind pairwise comparisons against held-out human scripts (+Ours judged closer to the human original in 84%–95% of comparisons across baselines), episode-level agreement with the human originals on prop activation (κ\kappa rising from 0.35 to 0.55), and an audit of 1,758 loss diagnosis items showing how backward updates progressively expand card coverage and precision. As the discussion period will close on November 18, we warmly welcome any further questions or feedback, and we would be very grateful to know if our responses and the revised manuscript have addressed your concerns.

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

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