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Under review as a conference paper at ICLR 2027

UniGame: A Unified Foundation Model for Board and Card Games via Shared–Specific Fusion of Game Experts

Abstract

Large language models (LLMs) for board and card games offer a promising foundation for developing general-purpose agents capable of strategic reasoning, decision-making and interaction across diverse game environments. However, despite recent progress, game-playing LLMs still underperform specialized conventional methods, and a single model is typically optimized for only one game. Here we introduce UniGame, a unified board-and-card-game model that consolidates multiple game experts through shared–specific fusion while preserving their specialized policies. UniGame comprises three complementary designs: Cross-Game Subspace Sharing, which extracts reusable adaptation directions from independently trained LoRA experts; Game-Conditioned Effect Projection, which maps these shared directions to distinct game-specific updates; and Private Residual Adaptation, which preserves specialized knowledge not captured by the shared subspace. This post-hoc decomposition enables cross-game knowledge sharing without forcing heterogeneous games to adopt identical parameter updates, while using game identity to select the appropriate expert components during inference. Experiments across five board and card games demonstrate that UniGame substantially reduces adapter storage while retaining near-specialist gameplay performance and outperforming static merging approaches.

Primary area:
generative models
Keywords:
card playing, LLM, Multi expert

Reviews

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1234this paper, Bottom 27%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.00 over 3 reviews, above 27% of the others.
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2
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3
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Paper summary

This paper proposes UniGame, a framework for consolidating multiple game-specific LoRA experts into a unified model through shared–specific parameter decomposition. The method consists of three components: Cross-Game Subspace Sharing (CSS), which extracts reusable adaptation directions; Game-Conditioned Effect Projection (GEP), which preserves game-specific transformations; and Private Residual Adaptation (PRA), which compensates for information not captured by the shared subspace. UniGame operates on independently trained experts without requiring joint multi-game training. Experiments across five board and card games demonstrate a 40% reduction in adapter parameters while largely preserving specialist gameplay performance. Additional ablations and representation analyses investigate the contributions of the proposed components.

Critical strengths
  1. Practical and efficient expert consolidation. UniGame addresses a relevant deployment challenge by consolidating independently trained game specialists without requiring additional gameplay training. The reported 40% reduction in adapter parameters while maintaining near-specialist performance demonstrates the practical value of the approach.
Critical weaknesses
  1. Limited methodological novelty. The proposed shared–specific LoRA decomposition is closely related to existing approaches such as LiLoRA [1] and Compress then Serve [2]. The paper does not sufficiently establish its distinctive algorithmic contributions or provide direct comparisons with closely related methods, limiting its novelty.
  2. Insufficient evidence for cross-game sharing. The same-budget Pure-private baseline achieves comparable gameplay performance and better offline policy fidelity. Without statistical comparisons against this baseline, it remains unclear whether cross-game sharing provides a meaningful advantage over independent adapter compression, weakening the paper's central empirical claim.

References

[1] Che, C., et al. "LoRA in LoRA: Towards Parameter-Efficient Architecture Expansion for Continual Visual Instruction Tuning." Proceedings of the AAAI Conference on Artificial Intelligence, 2026. https://doi.org/10.1609/aaai.v40i24.39082

[2] Br̈uel-Gabrielsson, R., et al. "Compress then Serve: Serving Thousands of LoRA Adapters with Little Overhead." Proceedings of the 42nd International Conference on Machine Learning (ICML), 2025. https://proceedings.mlr.press/v267/gabrielsson25a.html

Questions for authors
  1. Methodological novelty: What are the key algorithmic differences between UniGame and existing approaches such as Compress then Serve and Compress then Merge, beyond their different application settings?
  2. Effectiveness of cross-game sharing: Can the authors provide paired statistical comparisons against the same-budget Pure-private baseline to establish whether cross-game sharing yields meaningful performance improvements?
  3. Experimental consistency: Why do Table 4 and Table 8 report different Riichi Mahjong results (34.50% vs. 39.40%) for the activation-weighted configuration? Were different checkpoints or evaluation protocols used?
3 comments

We thank the reviewer for focusing on the closest methods and the evidence specifically attributable to sharing.

W1 and Q1: What are the algorithmic differences from LiLoRA, CtS, and CtM?

Response to W1 and Q1: UniGame fits Tg≈BgAs+CgDgT_g\approx B_gA_s+C_gD_g to frozen source updates under a storage budget. Its independent private residual can represent directions outside the shared input row space. LiLoRA uses a nested form (B0+Bg′Ag′)A(B_0+B'_gA'_g)A and continual training; task-specific changes pass through shared AA. CtS uses shared left/right factors USgVTUS_gV^T with task-specific cores. CtM aligns and merges task coordinates into one update, whereas UniGame retains game-conditioned updates. Section 2 already discusses CtS and MoDE (p. 3, L148–154). The representation and its limits are specified in Eqs. (3) and (5), with derivations in Appendix A.2.1–A.2.4 (p. 13, L648–701). The contribution is this budget-constrained formulation and analysis; standard SVD is not itself a novelty claim.

The direct CtS experiment is new evidence beyond that related-work discussion: we reproduced single-cluster JD-Full at 26.146688M parameters, versus 26.148864M for UniGame. Table S3 gives all five primary metrics. The clearest gain is in Leduc: +0.5504 [0.5128, 0.5888] against rule, with positive pointwise intervals against three additional opponents (Table S4). Limit/rule improves by +0.0285 [0.0195, 0.0375]; the other primary-game intervals include zero. This is a specific advantage over the tested CtS configuration, not a cross-game superiority result. Exact ranks, fitting settings, and the new artifact-consistency checks appear in Table S6 and its accompanying text.

Table S3. Primary-game UniGame–CtS comparison

Primary metricUniGame / CtSDifference [95% CI]
DDZ/WP win rate45.20% / 44.20%+1.00 pp [-0.50, 2.60]
Limit/teacher payoff0.0381 / 0.0379+0.0002 [-0.0292, 0.0299]
Leduc/rule payoff1.0872 / 0.5368+0.5504 [0.5128, 0.5888]
Riichi/v4 Top-238.00% / 38.60%-0.60 pp [-4.40, 3.005]
Guandan/Koi win rate35.50% / 35.25%+0.25 pp [-3.00, 3.50]

Intervals are paired 95% cluster-bootstrap intervals; resampling units and evaluation scope are specified in the evaluation and selection protocol.

Table S4. UniGame–CtS Leduc comparison across opponents

OpponentUniGame / CtS payoffDifference [95% CI]
Rule1.0872 / 0.5368+0.5504 [0.5128, 0.5888]
Teacher0 / -0.0276+0.0276 [0.0226, 0.0330]
Random1.1075 / 0.9570+0.1505 [0.1115, 0.1930]
20%-randomized DQN0.37525 / 0.29525+0.0800 [0.0570, 0.1060]

Rule/teacher use 5,000 paired seeds each; random/20%-randomized DQN use 1,000 each, with two seats. Additional Limit/rule improves by +0.0285 [0.0195, 0.0375]; both added Limit-opponent intervals include zero. For context, at 17.43M UniGame–Shared-only against random Limit is -0.144 [-0.265, -0.0285], illustrating opponent-dependent effects.

W2 and Q2: Does sharing outperform the same-budget Pure-private baseline?

Response to W2 and Q2: The current experiments do not establish that advantage. Pure-private sets shared rank to zero and independently applies truncated SVD under the same uniform Frobenius objective. At 26.15M, its private ranks are [5,5,5,4,5] for [DDZ, Limit, Leduc, Riichi, Guandan]. Its paired differences appear in Table S1. All formal intervals at 26.15M and 34.87M include or touch zero; at 17.43M, Guandan favors Pure-private by 5.00 pp and Limit/rule by 0.0206 Table S2.

The existing and additional controls answer narrower questions. Appendix A.5.5 and Table 12 already report 85.32% explained energy for a leave-one-game-out basis, versus 79.37% for a single-source basis and 65.43% for a random basis (p. 19, L982–1013). They specify target-game calibration and interpret these as recoverability results. The participation discussion likewise excludes direct gameplay claims (Sec. 4.3, p. 9, L467–475). UniGame's Leduc/rule gains over equal-budget Shared-only are +0.4091 [0.3673, 0.4515] at 17.43M and +0.1340 [0.1102, 0.1583] at 26.15M. These support private-capacity allocation within a shared representation, not an advantage of sharing over independent compression. We therefore present sharing as a representation choice with measured trade-offs.

Table S1. Main-table paired differences

Differences are UniGame minus each column comparator. Brackets show paired 95% cluster-bootstrap intervals. Win/Top-2 differences use percentage points; poker differences use native payoff units. See the evaluation and selection protocol for resampling units and scope.

Primary metricSource 43.58MPure-private 26.15MS+P 26.15MS+P 34.87M
DDZ/WP+0.70 [-0.90, 2.30]+1.00 [-0.30, 2.30]+0.70 [-0.90, 2.30]+1.20 [-0.10, 2.60]
Limit/teacher+0.0046 [-0.0029, 0.0117]+0.0030 [-0.0034, 0.0094]-0.0097 [-0.0234, 0.0044]+0.0041 [-0.0031, 0.0110]
Leduc/rule0 [0, 0]0 [0, 0]0 [0, 0]0 [0, 0]
Riichi/v4-0.80 [-4.80, 3.20]-2.40 [-6.20, 1.40]+3.00 [-1.60, 7.60]+0.40 [-3.40, 4.20]
Guandan/Koi+0.50 [-3.25, 4.25]+1.00 [-2.25, 4.50]+2.00 [-1.25, 5.25]+1.75 [-1.00, 4.75]

Q3: Why do the activation-weighted Riichi entries differ between Tables 4 and 8?

Response to Q3: The verified activation-weighted Riichi result is 39.40% (197/500), as reported in Appendix Table 8 (p. 16, L811–822). Table 4 incorrectly prints 34.50% for “Shared basis, activation” in the Riichi column (p. 8, L410–416). The basis_activation record gives 197/500, versus uniform's 190/500 = 38.00%, on seeds 62000–62124, seed key 20260907, with four seats per seed.

We will correct the Table 4 entry to 39.40% and replace the accompanying statement that uniform fitting outperforms activation weighting on Riichi (p. 8, L402–405) with Table 8's observed +1.40 pp [−2.40, 5.20] activation-minus-uniform comparison. This does not establish a statistically significant advantage.

The separate readout comparison in Table S7 also contains a 39.40% Shared B + private result and a 34.50% Pure-private Guandan result. These are different configurations and records; their attribution does not by itself explain the printed Table 4 entry. The earlier 35.0%/Mortal v4 and 38.6%/release4p labels likewise concern separate matchups and do not relabel CtS's 38.6%/v4 result.

Table S7. Additional readout comparison: configuration–game–opponent–metric attribution

Configuration (approximately 26.15M)Riichi / Mortal v4 / Top-2Guandan / Koi / win rate
UniGame38.00%35.50%
Shared B + private39.40%35.00%
Pure-private40.40%34.50%

The 39.40% Shared B + private entry belongs to this additional readout comparison; this table does not resolve the printed manuscript Table 4 discrepancy by itself. A separate activation-weighted shared-basis run also gives 39.40% (197/500) versus uniform's 38.00% (190/500); those are distinct configurations and records. The 34.50% entry above is Pure-private's Guandan win rate; GEP Shared matrix, activation independently also reports 34.50% on Guandan. Riichi values are Top-2 rates, not first-place rates.

Thank you again for your time and thoughtful feedback on UniGame. We would like to kindly follow up on our response and would be grateful to hear whether it has helped address your concerns, when you have a chance.

If any questions remain or further clarification would be helpful, we would be happy to provide it. We sincerely appreciate your time and consideration.

Reviewer_D9xmOpenReview ↗
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Confidence
3
Informativeness
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2
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Paper summary

This paper proposes UniGame, a post hoc method for consolidating five independently trained board-and-card-game LoRA specialists that share a frozen Qwen3-1.7B backbone into a single packed adapter. The specialist update on each adapted module is decomposed into three parts: a low-rank input basis that is shared across all games and stored once, a game-specific output readout matrix for each game, and a private low-rank residual branch for each game. Under a fixed rank allocation, all factors are fitted after training by minimizing the Frobenius reconstruction error with respect to the source updates, using alternating least squares and truncated SVD; no game data, rewards, or learned routing are required, and at inference time the environment supplies the game identity, which deterministically selects the corresponding branches. The packed adapter reduces the parameter count from 43.58M to 26.15M, a 40% reduction. Experiments cover Dou Dizhu, Limit Hold'em, Leduc Hold'em, Riichi Mahjong, and Guandan, against opponents including DouZero, an RLCard DQN teacher, a rule-based agent, Mortal v4, and the internal Guandan agent Koi.

Critical strengths

1: The problem formalization is clean and the mathematical treatment is rigorous and verifiable. The authors cast post hoc consolidation of multiple specialists as a matrix decomposition problem under a storage budget and establish a set of clear properties: static merging incurs an irreducible residual error, the span that a fixed shared basis can reconstruct is precisely characterized, every step of the alternating fit has a conditionally optimal closed form, and all computations can be carried out equivalently inside the joint source span whose dimension is at most 40.

2: The diagnostic depth and reporting honesty exceed those of comparable work. The paper systematically separates local reconstruction fidelity from actual gameplay outcomes, uses paired cluster-bootstrap intervals, per-game matched changes, and a sign-consistency test to show that improved fidelity does not guarantee improved results, and offers a sequential decision decomposition identity that explains the mechanism behind this decoupling. Evaluation is real gameplay with seat and role rotation on five imperfect-information games that differ substantially in rules, action spaces, and information structure, against strong opponents such as DouZero and Mortal v4, and the paper clearly demonstrates that Task Arithmetic and TIES fail severely on heterogeneous game experts, with TIES reaching only 0.2% on Riichi and 0% on Guandan.

Critical weaknesses

1: The paper's central claim, that shared–specific fusion compresses the adapters while preserving performance, is not supported by the paper's own evidence. In Table 2 the Pure-private control, which uses the same 26.15M parameters and contains no cross-game sharing at all, trades wins with UniGame across the five games, and on Riichi Mahjong it is actually better at 40.40% versus 38.00%; in appendix Table 9 its offline fidelity is also uniformly higher, and the paper itself acknowledges that this control achieves the best fidelity in that table. Under the accounting of equation 20 and Table 6, only about 14.7 of the headline 40 percentage points of reduction come from cross-game sharing, while the remaining 25.3 points come from plain rank truncation that requires none of the proposed machinery. Table 2 reports no uncertainty at all, even though the paper's own paired bootstrap in Table 8 implies 95% interval half-widths of roughly 1.4 to 3.8 percentage points against the primary opponents, which is the same magnitude as these gaps and every such interval contains zero, so the statement that UniGame matches or exceeds the specialists on four of the five games is not statistically established. The ablations further undermine the necessity of the components: in Table 4 the simpler shared-matrix variant with uniform fitting reaches 0.0481 on Limit and 43.20% on Riichi, both above the full model's 0.0381 and 38.00%. Taken together, the current evidence supports a workable specialist compression scheme but not a comparative advantage of the shared–specific fusion design, and this is my primary reason for leaning toward rejection.

2: The experimental record contains a cross-table contradiction, several evaluation metrics appear degenerate, the ablations cannot be traced, and the closest structured methods are not compared. Table 4 reports 34.50% on Riichi for the shared-basis configuration with activation-weighted fitting, while Table 8 reports 39.40% for the same configuration against Mortal v4; the two tables agree exactly on the other four games for this configuration, and since the uniform result is 38.00% in both places, the two records imply opposite conclusions about which fit is better while the main text relies on one of them, so the authors must clarify and correct this. The Limit return of −0.0207 recurs across five mutually unrelated configurations in Tables 3 through 5, and the Leduc return of 1.0872 is identical for nearly all methods while the return against the teacher is always zero, suggesting that these benchmarks are saturated or that some configurations have collapsed to fixed behavior, which the paper never discusses and which means the affected games should not be counted toward the four-of-five claim. In addition, Table 5 is headed probe features and its shared-features-only row is empty, while appendix sections A.5.5 and A.5.6 state that the refitted probes measure linear recoverability rather than gameplay contributions, so the reader cannot determine which branches and rank budgets each ablation row actually deploys. Finally, the structure of a shared input factor with per-task output readouts has precedents in Compress then Serve, MoDE, and the uncited HydraLoRA, yet Table 2 compares only against older static merging methods rather than these closest structured methods at the same 26.15M budget; combined with a single 1.7B backbone and five card and tile games, the title's claim of a unified foundation model exceeds what the evidence supports.

Questions for authors
  1. For the shared-basis configuration with activation-weighted fitting on Riichi, which seeds and record versions do the 34.50% in Table 4 and the 39.40% in Table 8 correspond to? If one of them is an error, please correct it and update every conclusion in the main text and appendix that depends on it. In addition, please state for every row of Tables 3 through 5 which branches are deployed, whether refitting is performed, and the per-module ranks and total parameter count, and clarify whether each row is a genuinely deployed policy or a probe in the sense of appendix A.5.5 and A.5.6; what explains the gap between the all-five basis in Table 3 and the full UniGame, and why is the shared-features-only row of Table 5 empty?

  2. Can you apply the paired cluster-bootstrap method already used in the appendix to the key comparisons of Table 2, reporting per-game 95% intervals for UniGame versus the specialists, versus Shared S+P, and versus Pure-private? If you claim that specialist performance is preserved, please state a pre-specified non-inferiority margin, and if most intervals contain zero, please weaken statements such as matching or exceeding the specialists on four of the five games accordingly.

  3. Please describe the exact construction of the Pure-private baseline in Table 2, including its rank allocation and fitting objective, and provide a budget-versus-performance curve comparing UniGame, Pure-private, and Compress then Serve at several budget points. Could you also add gameplay comparisons with MoDE, KnOTS, and No Task Left Behind at the same 26.15M budget? Only a systematic advantage over a sharing-free control at equal budget would establish the value of cross-game sharing.

  4. The Limit return of −0.0207 recurs across unrelated configurations, and the Leduc return of 1.0872 is identical for nearly all methods while the return against the teacher is always zero. Do these indicate that the corresponding benchmarks are saturated or that some configurations have degenerated to fixed policies? Do these two games still discriminate between methods, and should Leduc be excluded from the headline conclusions?

4 comments

We thank the reviewer for recognizing the formal analysis and for distinguishing the claims that require different controls. We provide the paired comparisons and concrete reproduction details in the relevant responses.

W1 and Q2: What is the contribution beyond rank truncation, and does the 40% reduction preserve performance statistically?

Response to W1 and Q2: These formal results are derived in Appendix A.2.1–A.2.4 (p. 13, L648–701, Eqs. (14)–(18)): static-merge residual error, recoverability from a fixed basis, conditional updates, and computation in the joint source span of dimension at most 40. Section 3.3 explicitly describes four alternating sweeps as an approximate fit without global optimality (p. 6, L308–313). The measured storage reduction is 43.58M to 26.15M adapter parameters; the accounting in Eq. (20) and Table 6 yields 14.74 percentage points from sharing and 25.26 from rank truncation. This decomposition is calculated from the reported factors; those two percentages were not explicitly listed in the manuscript. Pure-private reaches the same budget, so storage alone does not demonstrate a comparative sharing advantage.

Appendix A.4.2 already defines the paired estimator for uniform versus activation weighting (p. 15, L797–804), with results in Table 8 (p. 16). Table S1 extends it to the requested source, Pure-private, and Shared S+P comparisons. No non-inferiority margin was prespecified; these intervals support neither statistical equivalence nor a consistent advantage over Pure-private. The claim supported here is a tractable consolidation framework with explicit storage/performance trade-offs.

W1 and Q3.1: How is Pure-private built and selected, and what do the budget curves show?

Response to W1 and Q3.1: Pure-private uses independent truncated SVD. At 26.15M, ranks are [5,5,5,4,5]. The 26.15M and 34.87M configurations were selected from five remainder-allocation candidates using mean-game JS plus worst-game JS on 128 validation states per game. The recorded selection function uses no gameplay returns. These selection-rule details supplement the offline split sizes already given in Appendix A.5.1 (p. 16, L841–847). Additional 17.43M ranks were not selected by formal gameplay.

Table S2 reports the three budgets. Additional UniGame configurations retain the 26.15M shared basis and refit readouts/residuals, so they test fixed-basis budget changes. The lower-budget losses prevent attributing a systematic advantage to sharing. CtS has one completed budget point; its other budgets remain unevaluated.

Table S2. Three-budget results

Model and adapter budgetDDZ / Riichi / Guandan (%)Limit / Leduc payoff
UniGame 17.43M43.60 / 34.80 / 30.250.0287 / 1.0872
Pure-private 17.43M43.20 / 38.00 / 35.250.0412 / 1.0872
UniGame 26.15M45.20 / 38.00 / 35.500.0381 / 1.0872
Pure-private 26.15M44.20 / 40.40 / 34.500.0351 / 1.0872
CtS approximately 26.15M44.20 / 38.60 / 35.250.0379 / 0.5368
UniGame 34.87M45.00 / 39.20 / 34.000.0342 / 1.0872
Pure-private 34.87M45.00 / 39.60 / 34.500.0348 / 1.0872

DDZ/Riichi/Guandan use WP/v4/Koi; Limit/Leduc use teacher/rule. At 17.43M, UniGame–Pure-private is -5.00 pp [-9.25, -0.75] on Guandan and -0.0206 [-0.0287, -0.0131] on Limit/rule. At 26.15M and 34.87M, all formal intervals include or touch zero.

W1 and W2: Do the component experiments establish that the architecture is necessary, or that offline fidelity cannot select policies reliably?

Response to W1 and W2: Each control supports a narrower statement. Matched-budget Shared-only comparisons support private capacity in the tested poker settings. At 26.15M, sharing the output readout and reallocating saved parameters to private branches increases functional error from 0.008971 to 0.019561 on 128 validation states per game; Pure-private achieves 0.002883. This supports game-specific readouts for local reconstruction under the tested allocation.

The archived matrix_uniform Limit score is 0.0481 versus UniGame's 0.0381. Its Riichi scores are 43.20% against release4p and 33.20% against v4. We will label the opponents explicitly in Table 4 (p. 8, L414) and revise the accompanying comparison (p. 8, L402) to use aligned matchups. Appendix A.5.2 already acknowledges Pure-private’s stronger offline fidelity and excludes universal superiority of sharing (p. 17, L880–885). Appendix A.5.3 and Table 11 specify the two-to-four-game sample and the limited interpretation of the sign tests (p. 18, L943–949). These tests do not establish unreliable policy selection or zero correlation. Equation (25) provides a sequential-decision explanation, explicitly identified as a theoretical characterization rather than another measured result (p. 18, L953–965).

W2 and Q1: What explains the historical Riichi discrepancy and the incomplete ablation descriptions?

Response to W2 and Q1: The verified shared-basis/activation Riichi value is 39.40% (197/500), consistent with Table 8 (p. 16, L820). We will correct the Table 4 entry (p. 8, L410–416) and its dependent comparison (p. 8, L402–405), as specified in the response to NqTf. Table S7 separately identifies the readout-control records.

For deployment, CSS all-five and PRA shared-only reuse one 15.196160M policy with fitted readouts and no private branch; the augmented PRA policy has 31.539200M parameters. These rows change capacity. The new Shared-only controls instead match 17.432576M and 26.148864M with zero private rank. The probe interpretation is already explicit in Appendix A.5.5–A.5.6: target-calibrated readouts measure recoverability and are not deployed-policy interventions (p. 19, L988–992 and L1017–1022; p. 20, L1036–1045). Full UniGame ranks appear in manuscript Table 6 (p. 14, L731–741); the new annotations distinguish the separate ablation candidates. The empty Shared features only row in manuscript Table 5 (p. 9, L433–439) still requires its corresponding gameplay entry.

The repeated CSS all-five/PRA shared-only entry is one reused policy and result, not an independent replication. The 26.15M Shared S+P control is distinct from matrix_uniform.

W2 and Q4: Are the repeated poker returns evidence of saturated benchmarks or fixed policies?

W2 and Q3.2: Where are the close structured comparisons and their implementation checks?

Response to W2 and Q3.2: Table S3 and Table S4 report the completed single-cluster CtS JD-Full comparison. The positive Leduc intervals hold across four opponent policies; Limit/rule also improves. This does not establish universal gains across games or isolate a single component. Table S6 reports actual module ranks, optimization settings, parameter accounting, and the new verification of all 980 exported game–module pairs. This is separate from the exact source loading/routing check already described in Appendix A.3.3 (p. 15, L764–771). Comparisons with MoDE, HydraLoRA, KnOTS, and No Task Left Behind, and other CtS budgets/variants, have not been completed in this five-game setting.

Table S6. CtS configuration and artifact verification

CtS uses one cluster with a full game-specific core on each module. For an output-by-input module of size m×nm\times n, storage is (m+n)r+5r2(m+n)r+5r^2. Layer indices below are zero-based; unlisted layers use rank 23.

ProjectionOutput × inputLayers using rank 24
q2048 × 2048None
k / v1024 × 2048None
o2048 × 20480
gate / up6144 × 20480–3 and 10–27
down2048 × 61440–4 and 10–27

There are 128 rank-23 and 68 rank-24 modules. The packed parameter count is 13,508,608 left-factor + 12,103,680 right-factor + 534,400 core parameters = 26,146,688; the packed file occupies 104,700,896 bytes. Recorded rank allocation is dimension-based, without gameplay-score selection.

Fit settings specify deterministic stacked-source right-SVD initialization, alternating exact SVD updates, at most 1,000 iterations, and a source-energy-relative tolerance of 10−1010^{-10}. All 196 module logs report convergence in 3–24 iterations with nonincreasing recorded loss.

We independently checked all 980 game–module pairs: exported A=VTA=V^T and B=UΣgB=U\Sigma_g agree exactly in float32. Four random inputs per pair (seed 20261114) give a maximum relative forward discrepancy of 4.12×10−74.12\times10^{-7}, using the common LoRA scale α/r=2\alpha/r=2. All five adapter hashes and the packed-model hash match their manifests. This verifies artifact and materialization consistency; it does not establish equivalence to an official implementation, optimal hyperparameter search, or globally optimal fitting.

For full UniGame, the shared/private ranks in manuscript Table 6 (p. 14, L731–741), across all 28 layers, are q/o: 3/[3,3,3,3,3]; k/v: 3/[3,3,4,4,3]; gate/up: 2/[3,3,4,3,3]; down: 4/[3,3,4,3,3], in [DDZ, Limit, Leduc, Riichi, Guandan] order. Four-cell fits use four alternating sweeps and 12 inner ALS iterations for activation-weighted basis updates, as specified in Appendix A.2.5 (p. 14, L708–711).

W2: Is the foundation-model framing justified?

Response to W2: The demonstrated scope is post-training consolidation of five known-game policies on Qwen3-1.7B, with environment-provided game identity (Sec. 3.2, p. 5, L259–266). Appendix A.6 explicitly excludes unseen-game generalization, automatic game identification, and backbone-storage reduction (p. 20, L1075–1079). We will align the title and headline claims with that scope. We ask the reviewer to assess the formal consolidation framework and the reported structural trade-offs, without assuming that cross-game superiority has been established.

Evaluation and selection protocol

We report pointwise 95% CIs from 5,000 paired cluster-bootstrap draws, preserving seats/roles within each opening, without multiplicity correction (Appendix A.4.2; Table 7, p. 15, L783–804). Primary-evaluation cluster counts are DDZ 500, Limit/Leduc 5,000 each, Riichi 125, and Guandan 200. Win/Top-2 differences use percentage points; poker retains native payoff units. Updated aligned DDZ v2 records give Pure-private 44.20%, versus 42.50% in original Table 2.

Pure-private selection uses offline JS. Calibration/selection/audit pools contain 128/128/100 states per game, with disjoint information-set IDs; complete trajectory separation is not established for poker/Riichi (A.5.1, p. 16, L841–847). Evaluations reuse historical openings, including interface-check cases, and provide development evidence. Koi comparisons remain exploratory because its remote version was not frozen (A.4.2, p. 16, L832–836). Bootstrap intervals quantify resampling uncertainty, not the effects of development reuse or opponent changes.

Thank you again for your time and thoughtful feedback on UniGame. We would like to kindly follow up on our response and would be grateful to hear whether it has helped address your concerns, when you have a chance.

If any questions remain or further clarification would be helpful, we would be happy to provide it. We sincerely appreciate your time and consideration.

Reviewer_y39qOpenReview ↗
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2
Confidence
4
Informativeness
2
Presentation
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Soundness
2
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Paper summary

The paper presents UniGame, a method for consolidating game-specific LoRA experts trained on a shared Qwen3-1.7B backbone. Each expert’s parameter update is approximated using a shared input basis, a game-specific output projection, and a private low-rank residual. These components are fitted post hoc to the frozen expert weights under a fixed parameter budget, with game identity selecting the corresponding components at inference. Experiments on Dou Dizhu, Limit Hold’em, Leduc Hold’em, Riichi Mahjong, and Guandan report a 40% reduction in adapter parameters while largely preserving the gameplay performance of the separately trained LLM specialists.

Critical strengths
  1. The central idea is easy to follow, and the shared basis, game-specific projections, and private residuals are clearly described.
Critical weaknesses
  1. Motivation and practical value. The abstract is misleading because it suggests that the proposed approach addresses the performance gap between game-playing LLMs and conventional specialized methods. In fact, the trained models still underperform conventional AI specialists. Moreover, the “near-performance” comparison later in the paper appears to switch from conventional specialists to models trained separately with the LLM, which makes the results difficult to interpret and may overstate the method’s effectiveness. The paper should clearly distinguish these baselines and acknowledge that the proposed models remain inferior to conventional specialized agents. The practical value of a “unified foundation model” needs clearer justification: each game still requires a separately trained LoRA expert, and the experiments do not demonstrate reduced training costs or easier adaptation to new games. The paper should explain what adopting an LLM provides beyond a common interface and why we need to train LLMs on these tasks instead of applying specialists? What is the practical scenarios?

  2. Source-expert training details. Appendix A.1.2 provides supervised fine-tuning settings for Dou Dizhu and training sample counts for Riichi and Guandan, but the training data and supervision are insufficiently described. Where do the examples come from, and who generates the target actions—human players, specialized agents, or another source? Complete training procedures are also missing for the other games. Although the fusion procedure is reasonably specified, these omissions make it difficult to assess how the underlying experts acquire their game-playing abilities.

  3. Presentation. Several citations run directly into the preceding text, such as “playersGuo et al.” on page 1 and “Mixed SFTWang et al.” in Table 2. Citation spacing should be checked throughout the manuscript.

Questions for authors

How substantial are the LoRA parameter savings relative to the size of the base model, and what reduction do they provide in total model storage?

2 comments

We thank the reviewer for the clear questions about the intended use, supervision, and storage accounting.

W1: Does the motivation confuse conventional game agents with source LLM specialists, and what practical problem does consolidation solve?

Response to W1: UniGame consolidates existing game-specific LLM adapters when a service already uses a common language-model backbone. “Source specialist” means an independently trained LoRA policy; DouZero, RLCard agents, and Mortal are conventional policies used for data generation or evaluation as specified for each game. The benefit is post-training adapter storage reduction without additional multi-game SFT, reinforcement learning, or router training. This deployment objective is stated in Section 2 (p. 3, L125–139), and the Introduction acknowledges the gap to conventional agents (p. 1, L43–53). The environment-provided game identity and separate prompt/action interfaces are specified in Appendix A.1.3 (p. 12, L630–638). The experiments do not establish lower source-training cost or unseen-game adaptation.

The adapter collection decreases from 43.58M to 26.15M parameters. Table S1 reports paired gameplay changes relative to the source policies. These measured changes, rather than a claim of statistical equivalence, describe the resulting compression trade-off.

W2: Who generates the target actions, and how are the five experts trained?

Response to W2: Pretrained specialized policies generate the target actions in simulated games. We record decision states and actions, construct game-specific supervised examples, and freeze the fine-tuned LoRA experts before consolidation. Table S5 identifies the recorded datasets, teachers, and source checkpoints. DDZ uses DouZero WP; Limit and Leduc use RLCard DQN teachers at episodes 180,000 and 45,000; Riichi uses Mortal v4 decisions; Guandan uses Koi-labeled decisions from the registered collection.

Appendix A.1.1 already specifies rank 8 over seven projection types in 28 layers, totaling 196 modules, with fixed source experts across merging methods (p. 12, L607–614). Appendix A.1.2 documents DDZ settings and the Riichi/Guandan sample counts (p. 12, L616–628); Table S5 adds the teacher and checkpoint identities. For DDZ, the shared settings in the recorded training configurations are alpha 16, dropout 0.05, learning rate 1e-4, fused AdamW, cosine scheduling, warmup ratio 0.03, BF16, sequence length 4096, per-device batch 6, and gradient accumulation 5. The registered source is checkpoint 13,000, as recorded in Appendix A.1.2 (p. 12, L621–623). These DDZ settings are not assumed to apply to all five source-training runs.

W3: Citation spacing is incorrect in several places.

Response to W3: We will correct “playersGuo et al.” and “Mixed SFTWang et al.” and check citation spacing throughout.

Q1: How large are the savings relative to the backbone and total storage?

Response to Q1: The reduction is 40% of adapter parameters and approximately 1% of total parameters when both systems retain one shared 1.7B backbone. Counts decrease from 43,581,440 to 26,148,864; packed adapter files decrease from 174,583,600 to 104,877,920 bytes, or 39.93%. The total-parameter calculation is (43.58−26.15)/(1700+43.58)≈1.00%(43.58-26.15)/(1700+43.58)\approx1.00\%. The adapter counts and exclusion of the backbone are already explicit in Section 3.3 (p. 6, L314–323) and Appendix A.3.1 (p. 14, L739–747). Appendix A.3.2 distinguishes packed storage from materialized evaluation views (pp. 14–15, L749–762). Total storage depends on bytes per parameter; latency and device-memory savings have not been measured.

Thank you again for your time and thoughtful feedback on UniGame. We would like to kindly follow up on our response and would be grateful to hear whether it has helped address your concerns, when you have a chance.

If any questions remain or further clarification would be helpful, we would be happy to provide it. We sincerely appreciate your time and consideration.

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

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