- Rating
- 2(+1)
- Confidence
- 4
- Informativeness
- 2(+1)
- Presentation
- 3
- Soundness
- 2(+1)
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Paper summary
This paper proposes a framework for identifying whether a player’s observed play is substantially stronger or weaker than their recorded Elo rating and warrants further human review. It uses Maia-3 to estimate which playing strength best matches the player’s observed moves through three different methods. It then uses players in a validation dataset to determine whether the discrepancy warrants further human inspection. Its main contribution is the introduction of three methods for estimating playing strength using Maia-3. However, the paper’s experimental design has significant shortcomings, and most of the proposed methods are not compared with existing approaches, making it difficult to determine the paper’s substantive contribution.
Critical strengths
Its main contribution is the introduction of three methods for estimating playing strength using Maia-3.
Critical weaknesses
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Missing comparisons with directly relevant prior methods. The paper does not compare its proposed estimators with Kuboki et al. (2025), or its assistance-screening performance with the detectors of Linich et al. (2026), despite citing both and using the ChessFraud dataset. The included baselines do not establish an advantage over these directly relevant approaches, leaving the contribution of the new estimators and screening pipeline insufficiently demonstrated.
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Insufficient validation of short-window playing-strength estimates. Section 4.1 evaluates ten-game estimates against recorded ratings without establishing that these ratings reliably represent the strength expressed in the selected windows. Consequently, the reported MAE conflates estimation error with the behavioral discrepancies the framework aims to detect. Figure 2(b–c) provides limited independent validation because Maia-3 both generates and scores the games. Although the human-data experiments provide complementary detection evidence, they do not resolve whether the estimated Behavioral Elo accurately measures short-window playing strength.
Questions for authors
- Please refer to the concerns raised in the Weaknesses section.
- Why not use existing methods to estimate playing strength, such as [1] and [2], rather than introduce new Maia-3-based estimators? What advantages do the proposed methods offer over these existing approaches?
- Why use Maia-3 to generate actions and then use Maia-3 again to evaluate playing strength? Several approaches already support strength adjustment, including [2], [3], and [4]. If games were generated using these independent approaches, would the proposed Maia-3-based estimators still accurately estimate playing strength and detect changes?
- Did Section 4.1 select players with stable ratings? If not, what justifies using recorded Elo ratings as labels for the strength expressed in those ten games? Have the authors considered evaluating on strength-adjustable agents under controlled settings to reduce uncertainty about the underlying playing strength? Otherwise, the reported MAE may reflect both estimation error and fluctuations in the player’s performance over those ten games, making it difficult to interpret as evidence of estimation accuracy. References [1] Kuboki et al. Policies of Multiple Skill Levels for Better Strength Estimation in Games. AIIDE, 2025. [2] Chen et al. Strength Estimation and Human-Like Strength Adjustment in Games. ICLR, 2025. [3] Zhang et al. Human-aligned Chess with a Bit of Search. ICLR, 2025. [4] Wu et al. On Strength Adjustment for MCTS-Based Programs. AAAI, 2019.
5 comments
Response to gNyW (2/2) — Recorded ratings and independent strength validation (N-W2, N-Q1, N-Q3, N-Q4)
N-W2. Does agreement with recorded Elo validate the strength expressed over ten games?
Section 4.1 measures agreement with each player's median recorded platform rating over ten games. Its error can reflect both estimation error and a discrepancy between recent play and recorded rating. The independent Stockfish test below supplies a separate check of relative playing strength.
N-Q3. Can the estimators rank strength and flag changes when an independent engine generates the games?
Thank you for suggesting these papers. We reviewed all four and cite them in the revised manuscript. We adapted the strength estimators from Kuboki et al. (2025) and Chen et al. (2025) for our comparisons in Tables 1 and E.5. We used Allie embeddings from Zhang et al. (2025) in the ChessFraud comparison (Appendix G.6), and added Wu et al. (2019) to Appendix E.4 as prior work on adjusting an engine’s strength in Go.
To answer your question about using Maia-3 for both generation and scoring, we kept the Maia-3 estimators fixed and used Stockfish 18 to generate the moves after the opening in 12,450 games across calibration and test. Match results against a fixed Skill 5 opponent confirmed the ordering of the three settings. The test contains 249 matched sets. Within each set, we used the same ten starting positions to generate one ten-game window per setting. The estimates moved in the expected direction on average for both the weaker and stronger settings.
| Estimator | Correct strict ordering /249 | Strong upward alerts vs. control /249 | Weak downward alerts vs. control /249 |
|---|---|---|---|
| Direct likelihood | 67 | 1 vs. 9 | 9 vs. 11 |
| Rating-calibrated | 180 | 20 vs. 8 | 101 vs. 10 |
| Neural residual | 99 | 29 vs. 8 | 4 vs. 3 |
Ordering evaluates the continuous estimates. The alert columns use a nominal 2.5% cutoff per tail. Neural residual flagged 29 stronger windows versus 8 controls in the upper tail and 4 weaker windows versus 3 controls in the lower tail. On unchanged controls, Direct and Rating-calibrated flagged 20 and 18 of 249 windows in either direction, above the nominal 5% level for the two directions combined. Opening reuse limits what those counts establish about calibration. This design tests relative strength against a fixed opponent. Section 4.2 and Tables E.5–E.6 give the full estimates and alert counts. Whether these results carry over to the other suggested generators remains open.
N-Q4. Were players selected for stable ratings, and what can recorded Elo tell us about ten-game strength?
We did not select the original 197 test windows for prior rating stability. Following Herbrich et al. (2006), we distinguish underlying skill from game-to-game performance. Among 1,683 natural-game histories with at least 20 games, the median span from the first to the tenth game start was 46.55 hours. In a 209-window diagnostic, 24 windows overlapped exactly with the original test set. Among 131 accounts whose earlier ten pregame ratings spanned at most 50 Elo, the later window's median recorded rating differed from its first pregame rating by 9.66 Elo on average in absolute terms. This measures recorded-rating variation in that subgroup. The Stockfish outcomes provide separate evidence of relative strength in simulation.
N-Q1. Where do we address the missing comparisons and the validation of ten-game strength?
Part 1 presents the directly relevant comparisons. N-W2 and N-Q3 above explain the rating target and report the independent validation.
Thank you to the authors for the response and for adding several experiments. These additions largely address my questions about why Maia-3 is used for detection, although this rationale could be explained more clearly in the paper. The additional comparisons are also helpful and make the rationale for the overall method more complete.
However, the experiment using a different game generator also reveals potential limitations in the method’s generalization. The original paper used Maia-3 to generate games and then evaluated them using Maia-3, achieving good performance. However, detection performance remains limited in the experiment using Stockfish 18 to generate games. Since the rebuttal period is nearly over, I understand that the authors may not have time to add further experiments. For future work, using more human-like strength-adjustment methods, such as [2][3], could be a better direction. Another possibility would be to use a human-like model to play and have another AI engine modify some of its moves, without requiring those modifications to be human-like. This may also be closer to practical scenarios. Overall, generating games with AI in this way would allow the underlying policy and strength settings to remain fixed across the ten games, enabling further validation of the detector’s generalization ability.
Regarding the score, I will maintain my original overall rating because I still have substantial concerns about the method’s generalization. However, the additional baseline comparisons have provided more information, so I will increase Informativeness to 2.
[2] Chen et al. Strength Estimation and Human-Like Strength Adjustment in Games. ICLR, 2025.
[3] Zhang et al. Human-aligned Chess with a Bit of Search. ICLR, 2025.
Response to gNyW (1/2) — Prior methods and estimator design (N-W1, N-Q2)
Thank you for raising the two main concerns about prior-method comparisons and independent strength validation. We added common-window comparisons in Tables 1 and 2 and an independent Stockfish evaluation in Section 4.2. We address the independent validation and recorded-rating questions in Part 2.
N-W1. How do our estimates compare with Kuboki et al., and our alerts with the ChessFraud detectors?
Table 1 compares the methods on the same 197 ten-game windows, using median recorded platform rating as the target.
We used Chen's released checkpoints and fitted mappings to Elo. For the 12-feature Kuboki-based adaptation, we substituted Chen SE for SE-infty and refit LightGBM on our training data.
The screening comparisons use the same 741 calibration windows and nominal 5% upward level. The classifier heads were trained on ChessFraud-Synth. Our Allie inputs differ from the released cache, and we computed the Stockfish 17 features for the combined classifier because the original annotations were unavailable. Public alerts measure observed review workload, which differs across methods. Table 2, Figure 2D, and Appendix G.6 give the full comparison.
N-Q2. What do the Maia-3 estimators offer over the existing Kuboki and Chen methods?
Kuboki- and Chen-based estimates can also feed our screening rule. The three estimators use the same Maia-3 move evidence in different ways. Direct needs no project-specific fitting. Rating-calibrated maps joint move evidence to ratings, and Neural residual learns a window-level correction to Direct. Neural residual has the lowest recorded-rating error (Table 1). In the independent Stockfish test, Rating-calibrated, Neural residual, and Direct correctly ordered all three strength settings in 180, 99, and 67 of 249 matched comparisons, respectively. The Kuboki, Chen SE, and Chen SE-infty adaptations did so in 86, 63, and 29 of the same comparisons (Table E.5).