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Under review as a conference paper at ICLR 2027

Evaluating and Improving Human Behavior Modeling in Chess

Abstract

Human behavior models should reproduce not only likely actions, but also the stochastic structure and skill-dependent patterns of human decisions. We study rating-conditioned chess models and show that imitation policies can remain highly predictive while producing systematically mismatched move-quality distributions at higher ratings. To characterize this mismatch, we introduce three complementary diagnostics: mean highest-probability-density calibration error (mHPD-Err), which measures aggregate coverage calibration of high-probability move sets; move-class L1 error (Class L1), which measures differences in the frequencies of engine-derived move-quality classes; and move-class severity mean absolute error (Severity MAE), which measures differences in error severity within move-quality classes. We then propose an engine-informed information projection that minimally modifies the learned human policy to match population-level move-quality class frequencies and error severity. Across ratings 2100–2500, our method improves all three diagnostics relative to KL-regularized Monte Carlo tree search, while achieving comparable top-1 move matching accuracy and improving cross-entropy. At rating 2500, it reduces mHPD-Err from 5.10 to 1.73 percentage points, Class L1 from 1.89 to 0.43 percentage points, and Severity MAE from 1.027 to 0.010 centipawns, while also improving cross-entropy from 1.202 to 1.181 and top-1 move matching accuracy from 58.95% to 59.25% on the established ALLIE test set. These results demonstrate the importance of evaluating predictive accuracy, probability calibration, and skill-relative error structure as complementary aspects of human behavioral fidelity.

Primary area:
other topics in machine learning (i.e., none of the above)
Keywords:
Human behavior modeling, chess, policy correction, information projection

Reviews

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1234this paper, Bottom 10%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 1.67 over 3 reviews, above 10% of the others.
Reviewer_tburOpenReview ↗
Rating
2
Confidence
4
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper introduces new metrics for evaluating how human-like a model is. Previous approaches have largely relied on human move-matching accuracy to assess human likeness. Using additional metrics, this paper shows that models with similar move-matching accuracy may nevertheless differ from humans in their overall move-quality distributions, including error frequency and error severity.

The paper therefore proposes a post-hoc correction method for these distributions. It uses Stockfish to evaluate the quality of each candidate move in the model’s predicted probability distribution, then adjusts that distribution using human data from different skill levels. The results show improvements on several of the metrics presented in the paper. However, in the actual gameplay experiments, matches between agents conditioned and calibrated for different ratings still produce smaller performance gaps than those observed between corresponding human rating groups.

Critical strengths
  1. The paper introduces complementary metrics beyond move-matching accuracy, revealing differences in error frequency and severity that similar prediction accuracies can conceal.
  2. The proposed correction effectively aligns the model with the authors’ chosen targets: aggregate class frequencies and class-conditional mean error severity estimated from human players at each rating level.
Critical weaknesses
  1. The relevance of the proposed metrics to human likeness requires further validation. Players at the same rating may have different error rates and compensate through different strengths, so deviation from a group average does not necessarily imply non-human-like behavior. Reporting player-level distributions within each rating group, including medians and interquartile ranges, would help assess how representative the aggregate targets are. Human evaluation is also needed to determine whether these statistical differences actually make an agent appear less human-like.

  2. Improvements on the metrics targeted by the correction are expected, but better scores do not necessarily mean the model is more human-like. In actual gameplay, the corrected agents still do not reproduce the performance gaps observed between human rating groups. A human study comparing the original and corrected agents is therefore needed to evaluate whether the correction actually makes their behavior more human-like.

Questions for authors
  1. Please refer to the concerns raised in the Weaknesses section.

  2. Matching aggregate error rates does not necessarily mean that the model makes errors in the same positions as humans. Why does the correction target aggregate error rates rather than position-specific error probabilities for players at the corresponding rating? Is there evidence that the correction also improves this position-level agreement?

  3. The proposed correction focuses on the move policy, but value estimates may also be important for modeling players at different skill levels. If applied to a system such as ALLIE, could correcting the policy without corresponding adjustments to value estimates disrupt other human-like behaviors, such as deciding when to resign? How would the authors assess whether these behaviors are preserved?

11 comments
AuthorsOpenReview ↗

Official comment by authors - part 1

Thank you for the thoughtful and constructive review. Below, we provide new player-level and position-level results to address your concerns.

Players at the same rating may have different error rates and compensate through different strengths, so deviation from a group average does not necessarily imply non-human-like behavior.

We agree. Our goal is to estimate the average move distribution expected from players at a given rating. Modeling individual players is a separate problem. A population average can miss unusual player profiles, and individual deviation alone does not establish non-human behavior.

The population model is useful precisely because players differ: a reliable rating-conditioned policy lets us study how a player differs from average expectations, identify strengths and weaknesses, and investigate what they could improve.

Reporting player-level distributions within each rating group, including medians and interquartile ranges, would help assess how representative the aggregate targets are.

We conducted player-level analysis at rating 2500, where the raw-policy deficit is largest. We report players from the broader Lichess data with at least 20 games and 500 moves (61,578 positions), and a stricter group with at least 1,000 moves (32,348 positions). The table gives each class's player median and 25th-75th percentiles.

Move class≥500 moves, 64 players≥1,000 moves, 21 players
Best47.82% [45.89-51.19]49.17% [47.32-59.35]
Excellent21.00% [19.23-22.57]21.88% [20.26-23.68]
Good13.04% [11.83-14.44]12.69% [8.92-13.43]
Inaccuracy8.31% [7.13-9.46]7.63% [4.68-8.55]
Mistake6.29% [4.72-7.16]5.03% [2.10-6.64]
Blunder3.15% [2.21-3.66]2.63% [0.41-3.31]

For each player, the reference is the class frequencies and mean CPL observed in that player's human moves. On exactly the same positions, we calculate the class frequencies and mean CPL expected under the raw policy, MCTS baseline and ALLIE projection. Both corrections use their ALLIE-calibrated settings. We then measure each policy's error against the player's observed values. Results show that ALLIE projection produces distributions that are closer to player class frequencies and mean CPLs.

Result≥500 moves≥1,000 moves
Raw policy: median Class L1 error (pp)15.2115.87
MCTS baseline: median Class L1 error (pp)7.267.55
ALLIE projection: median Class L1 error (pp)6.956.68
Players whose class frequencies are predicted more closely by projection than by raw policy63/64 (98.4%)21/21 (100%)
Players whose class frequencies are predicted more closely by projection than by MCTS baseline42/64 (65.6%)20/21 (95.2%)
Raw policy: median absolute mean-CPL error14.6816.04
MCTS baseline: median absolute mean-CPL error4.626.15
ALLIE projection: median absolute mean-CPL error3.664.05
Players whose mean CPL is predicted more closely by projection than by raw policy62/64 (96.9%)21/21 (100%)
Players whose mean CPL is predicted more closely by projection than by MCTS baseline49/64 (76.6%)20/21 (95.2%)

Why does the correction target aggregate error rates rather than position-specific error probabilities for players at the corresponding rating?

Each position usually has only one observed human action, so its full human move distribution cannot be estimated directly. If the question instead refers to pooling similar types of positions (or positions that are similar in perceived difficulty), we do not currently have a validated way to do so and this is still an open problem. What we could try is to fit separate error targets for opening, middlegame and endgame positions; this remains future work.

This question also ties nicely into one of the main ideas for practical use of accurate behaviour models -> we can use them to try and find positions that are of similar difficulty to players at some given rating. While current raw policy models may still not be accurate enough, they can be useful for approximately grouping the positions by difficulty. Analysing these positions gives further evidence for position-level agreement (shown in the next part).

AuthorsOpenReview ↗

Official comment by authors - part 2

Is there evidence that the correction also improves this position-level agreement?

Yes, there is. The paper already reports improved human-move cross-entropy (CE) at higher ratings. We now examine positions that are similar in expected difficulty, using 321,836 broader-Lichess positions at rating 2500. MCTS baseline and projection both use their ALLIE-calibrated settings, without recalibration on these positions.

For each position, we sum the raw policy's probabilities of mistakes and blunders, then group positions by that predicted error risk. Higher risk means greater difficulty to find good moves according to the model. Every policy is evaluated on exactly the same positions within each group; the table compares predicted mistake-or-blunder rates with observed human rates.

Position difficulty groupPositionsObserved human error rateRaw policy error rateMCTS baseline error rateALLIE projection error rate
0-5%170,6800.61%1.13%0.93%0.73%
5-10%33,9754.27%7.26%5.06%5.53%
10-20%36,8078.89%14.45%9.92%11.10%
20-30%21,80014.91%24.70%17.06%15.96%
30-40%15,19021.28%34.73%24.38%22.60%
40-50%11,32128.84%44.81%31.98%29.56%
50-60%8,89736.27%54.82%39.99%37.47%
60-70%7,34142.98%64.78%48.51%46.43%
70-80%5,95853.09%74.86%57.91%57.12%
80-90%5,14160.69%84.86%68.05%72.45%
90-100%4,72675.35%95.07%86.20%91.13%

Projection is closer to human error rates than MCTS in the medium-to-high risk range (20-80%), while MCTS baseline has an edge in the rare highest-risk positions (80-100%). This shows different strengths of the two approaches. However, both corrections still hugely overpredict errors in the highest-risk group, which highlights positions that should be focused for improvements.

In actual gameplay, the corrected agents still do not reproduce the performance gaps observed between human rating groups.

The remaining gap does not negate the improvements in human-move prediction and error-distribution agreement, but identifies a limitation that needs to be addressed. The paper’s game-phase analysis suggests one possible cause. The 30-second clock cutoff removes 45–53% of endgame positions, leaving practical endgames underrepresented in both training and calibration. Generated games show a large increase in endgame CPL, even though the projection closely matches human CPL within each phase of the filtered evaluation data. We suspect that this missing endgame behavior contributes to the remaining rating performance gap. Testing this explanation through better endgame coverage in training and phase-specific calibration is a natural direction for future work.

A human study comparing the original and corrected agents is therefore needed to evaluate whether the correction actually makes their behavior more human-like.

Our objective is to match the move distribution expected at a given rating, rather than maximize perceived human likeness. Human judgments are subjective: an accurate population distribution may appear less human-like than a model with distinctive quirks (e.g. aggressive style of play). Assessing rating-specific behavior also requires familiarity with the relevant rating population. A human study would provide useful evidence about perception, but would not directly establish whether the predicted move distributions match observed human behavior.

If applied to a system such as ALLIE, could correcting the policy without corresponding adjustments to value estimates disrupt other human-like behaviors, such as deciding when to resign? How would the authors assess whether these behaviors are preserved?

Correcting the policy would likely affect behavioral decisions that depend on its probabilities. ALLIE compares the resignation token’s probability with legal-move probabilities and also checks the value estimate. Our correction would leave the value estimate unchanged and retain the resignation token’s probability, but changing move probabilities could still change the resignation decision. We would assess this by comparing decisions on identical positions before and after correction.

Thank you for the clarification. I now have a clearer understanding of both the statistical analysis and the paper’s objective. I found the additional results for the 2500 rating group particularly informative and encourage you to include them in the paper.

I agree that matching the move distribution of players at a given rating is distinct from making an agent feel more human-like to its opponents. My remaining concern is how to interpret the trade-off even under the distributional objective. As Reviewer kkvQ noted, the correction improves agreement with human error patterns but worsens mHPD-Err relative to the uncorrected policy. My question about resignation in ALLIE raises a related but untested possibility: correcting move probabilities could also affect a behavior that was not targeted by the correction.

I do not expect every metric to improve. However, when measures of human behavior move in different directions, counting how many improve does not establish that the corrected policy is closer to human behavior overall. What makes the gain in error-distribution agreement more consequential than the loss in HPD calibration for the paper’s intended application? A human study could provide complementary evidence about how players experience this trade-off. Evidence that the correction better serves the stated application would also be persuasive.

Without stronger evidence that this trade-off improves the model for its intended use, I find the contribution too limited to support a claim of improved behavioral fidelity overall. The results more clearly establish that the correction brings the model closer to the specific human error statistics it was designed to match.

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

The paper focuses on evaluating and improving policies that imitate human players of various skill levels in Chess. Evaluating such policies is an important step before they can be used as behavioural reference in downstream use cases. First, the paper argues that top-1 accuracy and cross-entropy are not enough as evaluation metrics and proposes three new evaluation criteria: mean highest-probability-density calibration error, move-class L1 error and move-class severity mean absolute error. Second, the paper introduces a method that alters the raw learned policy to match the latter two metrics using KL-minimizing information projection. All three proposed metrics are used to evaluate the raw Chessformer policy, its combination with KL-regularized MCTS and the proposed method. The methods are evaluated in several different ways with additional supporting experiments in the Appendix.

Critical strengths
  • Adequately evaluating and thoroughly understanding skill-conditioned human behaviour models is an important step before applying them to downstream tasks, such as providing appropriately human-like artificial opponents on sites like chess.com or further studying the human decision-making, and is an active and important area of research.
  • The proposed metrics capture more information about the approximated human behaviour than those used in prior work, and the presented results reflect this well. However, I would appreciate a more compact discussion of the metrics, as well as slightly less cryptic names. Currently, the motivations for the metrics are spread throughout the paper.
  • The paper contains a significant number of additional experiments supporting many of the design choices and possible questions.
Critical weaknesses

The abstract claims that the proposed method achieves substantially lower Class L1 and Severity MAE. However, the method directly minimizes these two quantities, so this claim is misleading and inflates the perceived strength of the method. Although, this is later acknowledged on Line 361, the authors should state this outright. The abstract also states in one sentence that the method achieves top-1 accuracy comparable to MCTS, and then claims an improvement in the next.

The paper would also benefit from improved clarity: even after two readings, some things still confuse me. In particular:

  • The Abstract and Introduction use terms such as move sets, move class, and HPD that are only (partially) defined in Section 4, which makes some earlier claims hard to understand.
  • The notation is inconsistent. For example, Section 3 defines the imitation model as pθp_\theta, but the cross-entropy and centipawn losses use undefined policies qq and qiq_i.
  • Terminology is inconsistent. “(Rating) cohort” is used vaguely, and the introduced metrics appear under various names.
  • It is not clear which of subsections 4.2, 4.4, 4.5, and 4.6 describe contributions and which provide methodology details. Subsection 4.4 in particular is written in unnecessarily complex language and required multiple re-reads.
Questions for authors
  1. How often does a position miss engine-annotated features? In other words, how often is the proposed method applicable in real-world?
  2. The discussion mentions that mHPD-Err of the proposed method is higher than that of the raw policy without any further discussion. Why is that the case? The same can be observed in Table 3 where Allie projection achieves lower mHPD-Err then BL projection. Why is that the case?
3 comments
AuthorsOpenReview ↗

Official comment by authors - part 1

Thank you for the review and for recognizing the effort put into additional experiments and the value of evaluating skill-conditioned behavior beyond move matching. We will improve the paper’s clarity. We address your concerns below.

The abstract claims that the proposed method achieves substantially lower Class L1 and Severity MAE. However, the method directly minimizes these two quantities, so this claim is misleading and inflates the perceived strength of the method.

We agree that the abstract should make clearer that class frequencies and error severity are targets of the correction. We understand that showing improvement in paper-introduced metrics alone would not establish a broader advantage over MCTS baseline. This is why we also report improved human-move cross-entropy (CE).

To examine whether the improvements also matter beyond population averages, we conducted additional player-level and position-level analyses following Reviewer tbur’s suggestions. The player-level results show that our correction brings predictions closer to the observed behavior of most sufficiently sampled players, rather than achieving aggregate agreement through errors that cancel across individuals. For the position-level analysis, we grouped positions by expected difficulty. Within each group, we compared the policies’ predicted error rates with the observed human rate. Both MCTS baseline and our correction improve substantially over raw policy. Their predictions are broadly similar in lower-risk groups, while our correction more closely matches human behavior in medium-to-high-risk positions. MCTS baseline has an edge in the rare highest-risk positions, suggesting that the approaches have different strengths rather than one being uniformly better. Full analyses are provided in our response to Reviewer tbur.

The abstract also states in one sentence that the method achieves top-1 accuracy comparable to MCTS, and then claims an improvement in the next.

We intended to describe comparable top-1 accuracy overall. The next sentence gives a small numerical increase at rating 2500, rather than an established general improvement in top-1 accuracy. We will use consistent wording and emphasize comparable accuracy.

The Abstract and Introduction use terms such as move sets, move class, and HPD that are only (partially) defined in Section 4, which makes some earlier claims hard to understand.

We will introduce these terms in plain language before using them in claims. A move set is a subset of legal moves in a position. An HPD set contains moves selected from most to least likely until their probabilities sum up to at least the desired mass. Move classes are engine-derived quality labels such as best, mistake and blunder.

The notation is inconsistent. For example, Section 3 defines the imitation model as pθp_\theta, but the cross-entropy and centipawn losses use undefined policies qq and qiq_i.

We will define qq as any policy being evaluated or corrected, and qiq_i as its move distribution at position sis_i and rating rir_i, before using them in the CE and CPL equations.

AuthorsOpenReview ↗

Official comment by authors - part 2

Terminology is inconsistent. "(Rating) cohort" is used vaguely, and the introduced metrics appear under various names.

By “rating cohort,” we mean the group of positions whose active players fall within a specified rating interval. We use the term consistently in this sense, but will define it explicitly at first mention. The metric abbreviations are also used consistently overall, although some tables shorten “Severity MAE” to “Sev. MAE.” We will standardize these small variations.

It is not clear which of subsections 4.2, 4.4, 4.5, and 4.6 describe contributions and which provide methodology details. Subsection 4.4 in particular is written in unnecessarily complex language and required multiple re-reads.

Sections 4.5 and 4.6 present our proposed correction and its HPD-preserving extension, while Sections 4.2 and 4.4 provide supporting methodology. Section 4.4 already identifies KL-regularized MCTS as a baseline from prior work. However, we agree that its explanation is unnecessarily complicated. We will simplify it and move the details to the appendix.

How often does a position miss engine-annotated features? In other words, how often is the proposed method applicable in real-world?

All legal moves can be evaluated and assigned a move-quality class. However, CPL is undefined when the comparison involves a mate score. If the engine-best move has a mate score, this affects every candidate move, and our current correction leaves the policy unchanged. In the broader-Lichess data we have 1.86% such positions meaning that, in practice, the correction can be applied to almost all positions. Also, many positions with obvious mating continuations are also less central to one of our intended application: assessing difficulty where positions are less clear. This does not mean that all forced-mate positions are easy, but that leaving these positions unchanged has limited impact on the method’s overall coverage.

The discussion mentions that mHPD-Err of the proposed method is higher than that of the raw policy without any further discussion. Why is that the case? The same can be observed in Table 3 where Allie projection achieves lower mHPD-Err then BL projection. Why is that the case?

Since the raw policy already has near-zero coverage error, there is little room for improvement on this metric. This initially surprised us as well and motivated us to examine move-class frequencies and error severity. As discussed in the appendix, mHPD-Err measures aggregate coverage, not complete agreement with the human move distribution. Errors across positions can cancel, so low coverage error can coexist with incorrect move-quality probabilities. This is why we use mHPD-Err as one complementary diagnostic.

Our correction can change move rankings and probability masses. These adjustments can increase mHPD-Err while improving other aspects of agreement with human behavior. The BL projection makes a larger adjustment to the raw policy than the ALLIE projection to match the broader population’s quality statistics. Its higher mHPD-Err is consistent with that larger adjustment.

Thank you for the response and detailed answers to my questions. The promised changes to the abstract, notation, and Section 4 would address most of my presentation concerns. The player-level and position-level analyses are useful additions. My remaining concern is the one Reviewer tbur raises regarding the trade-off benefits relative to the paper's intended application. I have read through all reviews and author responses and will consider them for the remainder of the discussion period, but for now I will maintain my score.

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

This paper identifies and narrowly fixes issues that human behavioral models in chess have with modeling very high-skill play. The fixes are straightforward injections of engine evaluations at inference time.

Critical strengths

The paper supplies useful metrics for evaluating chess behavioral modeling beyond centipawn loss and move matching.

The paper is honest in its negative results as well (failure to transfer to broader Lichess data, etc.).

Critical weaknesses

The paper's goals are modest. Fixing the problem of too-weak prediction of very-high-rated play with inference-time Stockfish is uninspiring: it seems obvious that one can fix this with access to a superhuman evaluator at inference time. It would be much more interesting to train a network to do this on its own. In my opinion, the scope of this contribution is too narrow for ICLR and is better-suited to a computer games venue. Even then, the methodology has issues that I think should be resolved.

The improvements are on metrics that the paper introduces and trains for directly. The MCTS tests are mostly "unfair" as the paper's method trains with 10 moments while the MCTS method just has one knob. Also, the stated goal of more faithful game-level behavior is not achieved.

Questions for authors

Can you address the problems of overly-weak prediction at high levels with a training-time-only intervention?

1 comment
AuthorsOpenReview ↗

Official comment by authors

Thank you for the review. Below, we address your concerns.

The paper's goals are modest. Fixing the problem of too-weak prediction of very-high-rated play with inference-time Stockfish is uninspiring: it seems obvious that one can fix this with access to a superhuman evaluator at inference time. It would be much more interesting to train a network to do this on its own. In my opinion, the scope of this contribution is too narrow for ICLR and is better-suited to a computer games venue.

We believe this assessment overlooks the evaluation contribution. Correcting the high-rating deficit is one goal, but closing the evaluation gap is equally important. At the moment, the main human-move modeling papers largely rely on cross-entropy (CE) as the distribution-level measure. We show that strong human-move prediction can coexist with incorrect move-quality probabilities, motivating additional metrics that reveal where current SOTA behavioral policies fail. We believe that emphasizing clearer evaluation is especially important for behavior models.

Using a strong engine to improve move quality may be straightforward, but it is not obvious how to change move probabilities to recover broader human behavior. Inference-time policy correction is already explored by Jacob et al. (2022) and Zhang et al. (2025), using search with learned value estimates. Our approach uses engine-derived evaluations, but this choice does not make the behavioral modeling problem trivial. The relevant question is whether the correction recovers human error patterns while retaining or improving human-move prediction.

Training a standalone network is a natural next step, which we are now investigating (see our response to the final question). However, improving training requires understanding which aspects of behavior existing models fail to capture and how to measure progress. The analyses in this paper provide that direction. We therefore believe this work fits well alongside the published research on human chess modelling.

The improvements are on metrics that the paper introduces and trains for directly.

We understand that showing improvement in paper-introduced metrics alone would not establish a broader advantage over MCTS baseline. This is why we also report improved human-move CE.

To examine whether the improvements also matter beyond population averages, we conducted additional player-level and position-level analyses following Reviewer tbur’s suggestions. The player-level results show that our correction brings predictions closer to the observed behavior of most sufficiently sampled players, rather than achieving aggregate agreement through errors that cancel across individuals. The position-level results show that our correction improves predictions in medium-high risk positions, while MCTS baseline has an edge in the rare highest-risk positions. Full analyses are provided in our response to Reviewer tbur.

The MCTS tests are mostly "unfair" as the paper's method trains with 10 moments while the MCTS method just has one knob.

The methods use different calibration information because they address the correction differently. Matching human mean CPL provides a common reference for comparing their error behavior; requiring identical numbers of parameters is not necessary for this comparison to be informative.

Also, the stated goal of more faithful game-level behavior is not achieved.

The remaining performance gap does not negate the improvements in human-move prediction and error-distribution agreement, but identifies a limitation that needs to be addressed. The paper’s game-phase analysis suggests one possible cause. The 30-second clock cutoff removes 45–53% of endgame positions, leaving practical endgames underrepresented in both training and calibration. Generated games show a large increase in endgame CPL, even though the projection closely matches human CPL within each phase of the filtered evaluation data. We suspect that this missing endgame behavior contributes to the remaining rating performance gap. Testing this explanation through better endgame coverage in training and phase-specific calibration is a natural direction for future work.

Can you address the problems of overly-weak prediction at high levels with a training-time-only intervention?

One promising training-time intervention is distilling the corrected policies into the network. We have now tested this in a preliminary experiment, fine-tuning the original model for one epoch on 2.14 million broader-Lichess positions. The resulting model reduces Class L1 by 20–59%, mean-CPL mismatch by 22–56%, and Severity MAE by 16–42% across ALLIE test set ratings 2000–2600. Interestingly, the improvements extend to ratings 2000 and 2600, which were outside the distillation cohorts. Top-1 accuracy and CE remain roughly the same. Before the final distillation, however, we will first retrain the model with better game filtering to include valuable endgame data.

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

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