acceptodds
Under review as a conference paper at ICLR 2027

GENSTRAT: Toward a Science of Strategic Reasoning in Large Language Models

Abstract

Fixed game suites for evaluating strategic reasoning in large language models (LLMs) saturate and are hard to keep free of contamination. We introduce GENSTRAT, a system for evaluating the strategic capabilities of LLMs driven by procedural generation of two-player zero-sum imperfect-information betting games, allowing an evaluator to draw novel, fresh games on demand. Each game is characterized on a scale of five complexity axes (state space, temporal contingency, opponent dependence, private information, precision) and measured by Monte Carlo simulation. Using this generator, we construct a 50-game benchmark and hold a tournament of twelve frontier and open-weight models, gathering data from over 40,000 LLM vs. LLM matches. We further construct a composite complexity axis, and find that, on the eight hardest games, the gap between the best and worst model is 1.7 times its value across the whole set of games (1.6 times with weights learned on held-out games). Ablations show that a higher thinking budget, disclosing the opponent's strategy, and higher reasoning matched to a game's specific demands (for private information and planning depth) were associated with higher margins for the LLM player.

Primary area:
foundation or frontier models, including LLMs
Keywords:
large language models, strategic reasoning, game theory, procedural generation, multi-agent evaluation, benchmarking, imperfect-information games, robustness

Reviews

Among:
Shape:
1234this paper, Top 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.33 over 3 reviews, above 51% of the others.
Reviewer_2QgeOpenReview ↗
Rating
1(−1)
Confidence
3
Informativeness
1
Presentation
2
Soundness
1(−1)
Read review
Paper summary

This paper introduces GENSTRAT, which uses a parameterized generator to combine game phases, actions, information visibility, and settlement rules into two-player, zero-sum betting games with imperfect information. Of 12,351 generation seeds attempted, 2,000 passed the acceptance checks. The authors selected 50 of these games to evaluate 12 models, retaining 40,412 matches after data cleaning. The paper estimates five game characteristics through simulation and examines their relationships with model performance. The results show that newer frontier models generally perform better, while models with similar overall strength can excel at different types of games.

Critical strengths
  • By generating new game flows, opportunities to acquire information, and payoff rules, GENSTRAT helps reduce the risk that models have memorized specific game instances and tests how they handle new combinations of rules.

  • The authors swap seats to reduce positional effects on match outcomes. Experiments that remove individual games or use randomly sampled subsets of games also show that the overall ranking of model strength is relatively stable.

  • Beyond model rankings, the authors conduct additional experiments to analyze model behavior. For example, they disclose or hide a programmed opponent's strategy to test whether models can use information about the opponent to improve their returns, extending the evaluation beyond comparisons of which models win against one another.

Critical weaknesses
  • The complete games and rulebooks assembled from components require more thorough validation. Unlike established games whose rules have been tested through extensive use, newly generated games introduce an additional validation burden. Appendix A explains that the system programmatically combines preimplemented mechanics and stitches together their natural-language descriptions. Even if each component functions correctly on its own, this does not ensure that the combined mechanics work coherently or that the rulebook fully explains the relationships among action order, costs, and information visibility. Appendix A reports that 2,000 of 12,351 candidates were accepted, a rejection rate of approximately 83.8%. The screening criteria include whether phases can be reached, game length, and seat balance under random play. Nevertheless, games that passed these checks and were ultimately used for evaluation still had problems in their rule descriptions. In Appendix J, the authors and LLM auditors checked the served rulebooks against the engine and found omissions or errors in 34 of the 50 games. In 12 games, the rulebooks stated that costs for hidden actions were settled at the end of the game, whereas the engine deducted them immediately and the opponent could observe the change in chips. A model that trusts the stated timing may assume that its action does not immediately change its publicly visible chip count, thereby underestimating the opponent's opportunity to infer its action from that change. Stable rankings after excluding games in each defect class only show that this leaderboard is relatively robust to those exclusions. This is a post hoc check of existing results; it does not answer the underlying question of how to validate new games reliably and identify omissions or contradictions in their rules. The persistence of these rule problems despite screening that rejects a large proportion of candidates indicates a need for more thorough validation of the entire process, from generation and screening to rulebook checks.

  • Novel instances do not necessarily pose novel strategic problems. Section 3 defines the generated games as generalized betting games (GBGs), a family that includes Kuhn poker and Leduc poker and extends them with non-betting actions, information structures, and conditional branches. These games are built around decks, private hands, and chips. The generator varies the organization and parameters of betting, simultaneous-move, auction, and observation phases. Appendix A further explains that games combine preimplemented operations such as dealing, peeking, swapping cards, and wagering, with conditional branches and bounded loops creating different game flows. This can reduce the likelihood that models have seen or memorized a complete game instance. However, different rules and flows do not necessarily require different strategic experience. Even without having seen a particular game, a model may perform well by transferring general strategic knowledge—akin to "meta-knowledge"—from similar games, such as inferring private information from an opponent's actions, weighing betting risks, and deciding when to bluff. Thus, while the paper makes a reasonably clear case for instance-level novelty, the experimental evidence and discussion remain insufficient to establish how much generating new instances reduces reliance on prior strategic experience.

  • The formatting and presentation of the main text could be improved. In the "Models" paragraph of Section 5, Tournament Design, excessive spacing between model names makes the text difficult to read. A clearer, more consistent presentation would help. In addition, ICLR allows up to 9 pages of main text for the initial submission, rather than 8. The authors could use the remaining space to include more material that helps readers assess the paper's contribution.

Questions for authors
  • Q1: In light of the rule omissions and errors identified in Appendix J, could the authors further examine the limitations of the current screening and rulebook checks? Which key steps in generating new games still require manual inspection?

  • Q2: Could the authors further discuss whether, although the game instances are newly generated, the methods for solving them may still come from models' prior experience with similar games? If models' pretrained knowledge contains substantial general strategic knowledge applicable to the different generation components, would this weaken the claimed advantages of the benchmark?

  • Q3: Section 6 reports that, on the eight difficult games selected using the composite score, the gap between the highest and lowest fitted model strength scores increases from 3.3 on the full game set to 5.6 on the difficult subset, approximately 1.7 times the original gap. If the difficult games themselves allow more chips to be won or lost, the larger gap may partly reflect differences in payoff scale. Please clarify whether the chip settings are comparable across games.

6 comments

Thank you for your thoughtful review. You raise two fundamental points: whether generated games can be trusted, and whether they sufficiently pose novel strategic problems.

Q1. Validation and inspection. GENSTRAT consists of modules, each with engine logic and a natural-language description, and a generator that provides minimal structure but otherwise stitches modules together at random into a novel multi-agent game. Two things must work for the result to be trusted: the generator must assemble a working game (and append any preambles correctly), and each module's description must fully and correctly explain its code. Since every rulebook sentence comes from a module or a shared preamble, each is checked once, and a fix reaches every game that uses it. Verification therefore scales with the number of modules rather than the complexity of the games, and once modules are verified, with every composed game then checked automatically (below), we can generate games of new structures and kinds without verifying each one by hand (Appendix O). Two steps remain manual: checking the text of each new module once, and adjudicating the discrepancies the automated checks raise. The acceptance gates screen whether a game is playable and balanced.

Beyond pre-tournament screening, over Oct/Nov, we used LLMs to run many audits: (1) of individual modules, checking each module's rule text against what its code does, with a runnable example for every mismatch; (2) of generated rulebooks, for consistent and unambiguous rules; (3) seeded replays of the engine against recorded play, and a checker for 19 kinds of rulebook–engine consistency. A frontier model also re-implemented each generated game from its rulebook alone, to confirm that rulebook and engine match. We will release these audit results in the camera-ready repository.

On the 50 benchmark games these checks found (1) one engine bug, in about 1% of matches, now fixed, and (2) wording issues, mostly omitted details. Your hidden-cost example is one: a single shared sentence, now fixed in all 12 games, that moved no chips, since the rulebook also says both stacks are public. To test whether wording changed decisions, we re-asked models the same prompts with only that sentence clarified, and no model's decisions changed in any of the 12 test games, except for one auction sentence we already knew about. We reran that game and the engine-bug games in full, and no model moved more than one rank. We reran 542 matches across all 34 games with revised rulebooks, on the same deals but with the corrected text and engine. Models made the same decision 84-94% of the time (a similar rate to repeating a prompt), and no model changed tier.

Q2. Prior strategic knowledge. We agree that a genuine question exists about the degree to which a new instance is a new strategic problem, rather than a repackaging of existing strategic thinking. Novel games rule out memorizing a game's solution, but not transferring general strategic knowledge, a kind of "compositional generalization" from principles learned elsewhere. We note that transfer is in many ways what we intend GENSTRAT to measure.

Stated this way, prior knowledge does not weaken the benchmark's advantages: games cannot be memorized, complexity can be raised on demand. The ranking also holds on generated games with no betting and on six games built with the same engine outside the betting-game generator, including a board game, a market and a negotiation. Controlling for the complexity axes, a game's resemblance to Kuhn or Leduc poker does not predict how well it reproduces the leaderboard.

Composing existing pieces in unusual ways can also produce qualitatively different games: Go and Chess are both built from a board, pieces and rules for moving and capturing, yet call for very different skills. Even at the simplest level, making a player's card public in Kuhn poker removes any reason for that player to bluff. Our results show this too: playing at equilibrium quality requires solving each new game, and only one model manages that on almost every game we could solve (Appendix L). Finally, by expanding to non-betting-game environments, and showing a high correlation in rankings, we show that performance seems to generalize even if we move beyond the card based features you mentioned. Future work would incorporate further abstraction and unusualness into the modules from which our procedural generators are built.

Q3. Payoff scale. You are right that stakes differ across games, so chips are comparable within a game but not between games. With each game's margins divided by the standard deviation of its payoff under random play, hard games still spread the models 1.35 times as far as the full set (Appendix E).

Presentation. The model list is reformatted, and the ninth page now holds Section 9.

We would be grateful to hear whether these results address your main concerns.

Thank you again for your detailed review. Since the discussion closes tomorrow, we wanted to check whether our reply and the revised paper address your concerns, and please let us know if any further analysis would help. A brief recap:

Validation. Each rulebook sentence comes from a module or a shared preamble: each is checked individually and a fix reaches every game that uses it. Every composed game is then checked automatically by code that compares the rulebook with the engine, and we also had an LLM rebuild each game from its rulebook alone. Most of these checks, including the audits by LLM reviewers, were built after the tournament. We applied them to the games we added during the discussion period. On benchmark games, they found one engine bug, now fixed. They also found wording issues in the rule text, mostly details omitted from the text that created some small ambiguities. To confirm that these did not change the results, we reran in full the four games where they were most likely to matter. In the overall leaderboard, no model moves more than one rank, and the maximum change in a model's strength is 0.13 chips per game. Each issue we found was fixed at its source, in a module or the shared rule text, so all future games will inherit the fix. Once the module library is verified in this way, the code checks run on every new game, and neither manual auditing nor an LLM rebuild is needed, although we recommend LLM checking new games as a cheap safeguard.

We also reran 542 matches across all 34 games with revised rulebooks, on the same deals but with the corrected text and engine. No model changed tier (Appendix O). Finally, gpt-6-astra picks an equilibrium-quality move in 99% of its decisions on the solved games. This suggests that rulebooks convey rules consistent with engine logic. All reruns and audit results will be released with the final version.

Prior strategic knowledge. We note that games composed from the same base pieces, but with different objectives and scoring rules, can pose new strategic problems/trade-offs. Model rankings hold on games outside the betting family, and controlling for the complexity axes, a game's resemblance to Kuhn or Leduc poker does not predict how well the ranking holds (Section 9, Appendix M).

Payoff scale. With a game's payoffs scaled by their standard deviation under random play, hard games still spread the models 1.35 times as far as the full set (Appendix E).

Following your suggestion, the main text now uses the full page allowance for the new Section 9. We would be glad to clarify anything before the deadline.

Thank you very much for your responses. I recognize GENSTRAT's value as a new-game-generation framework. However, its positioning as a benchmark imposes stronger requirements on the reliability and validity of the generated games and their ability to produce meaningful strategic measurements.

1. Task reliability as a benchmark prerequisite. Unlike QA tasks, where the outputs can be directly checked against an external answer (or rubric), game benchmarks evaluate agent capability from outcomes generated through the game. The evaluation signal is therefore only as meaningful as the game itself: for example, an executable but poorly designed game can distort model scores rather than measure true strategic ability. The current checks for aspects like runnability and reachability are basic filters that remove obvious failures. Passing these checks does not establish that the retained games are reliable and well-designed evaluation environments. In contrast, using mature games can mitigate this concern because their rules and strategic properties have already undergone substantial test.

2. Reliability of the new games and rulebooks. Validating individual modules is not equivalent to validating their composition. Locally correct modules can produce an engine that executes successfully but implements unintended global interactions. The same composition issue applies to rulebooks: individually accurate text fragments need not fully or accurately describe these interactions when stitched together.

3. Incremental value over established games. The benefit of generating new game instances, rather than directly using existing mature and well-validated games, remains insufficiently established to me. In particular, if the authors can show that memorization of established games actually produces misleading evaluations, while GENSTRAT provides a more faithful assessment of strategic capability or even can reveal some model capability gaps that old games fail to expose, I believe it would substantially strengthen the paper's contribution and constitute an important as well as interesting finding to the community.

After carefully reconsidering the authors' response and revisions, I do not believe these concerns have been resolved. The authors could reposition GENSTRAT primarily as an automated pipeline for synthesizing new game environments. Alternatively, retaining the benchmark positioning would require addressing the above concerns. As for the current version of the manuscript, it does not meet the bar for acceptance at ICLR. I respect the other reviewers' assessments and my review only reflects my own judgment regarding the evidence required for a reliable and informative benchmark. I am comfortable leaving the decision to the AC.

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

The paper proposes GenStrat, an evaluation benchmark of two-player zero-sum games. 50 games are constructed and 40k games between language models are evaluated.

Critical strengths
  1. The synthetic task generator is useful for future research. It provides a controllable and abundant source of test environments.
  2. Statistical analysis is done properly. Confidence intervals are reported, Benjamini–Hochberg correction is performed to make reported results reliable.
Critical weaknesses

What would a prefect strategy's evaluation metrics be? The current paper compares various LLMs but is missing an upper-bound baseline that evaluates how far an LM is from the rational strategy.

Questions for authors
  1. Please see the weakness section above: How do the LMs behave compared with perfect strategy?
5 comments

Thank you for your review. We appreciated your comment about full-equilibrium solving and were able to get equilibrium solving on 27 out of 50 games. Of the hardest tertile of games, we were only able to solve 3, due to the prohibitively large state spaces of the hardest games. We generally agree that a relative ranking is better with an absolute reference point. The revision adds one in Section 9 and Appendix L.

For ten models and each solved game, we played both seats of the same random seed against the equilibrium. We outline findings:

  • The frontier models roughly break even against perfect play, meaning almost every move they make is a best response to it, while the weakest lose almost a chip per deal, and no model beats the equilibrium (Figure 10).

  • The frontier on easy games: almost all frontier model moves consistent with the equilibrium's on easy games.

  • Every tier on harder games: all models decline in performance on harder games with the exception of gpt-6-astra, which almost always played actions consistent with equilibrium (although it did not mix at equilibrium rates) across all games for which we could compute equilibrium.

  • Mixing: no model mixes consistently with the equilibrium, although in these games that costs little. Figure 12 shows how often each model makes the equilibrium's move, and Table 19 how far its mixing is from the equilibrium's. That means that even gpt-6-astra, which plays consistent with equilibrium almost everywhere, would be (very slightly) exploitable by a best-responding opponent. We note this in the new version of the paper.

For the hardest games, exact solving is not feasible, since one game alone has millions of distinct states. Here play between models remains the best way to measure behavior. One benefit of the engine is that it can generate games of any size, so we get exact baselines where games are small enough to solve, and tournaments where they are not, and once models reach equilibrium play on the solvable games, harder games can be drawn.

You noted that the generator could be useful for future research. Appendix M may be of interest here: using the same engine we built new card games, a board game, a market and a negotiation, and model rankings on betting games carry over to all of them (Figure 14). We note that even on dissimilar games (like the board game with fog of war) we see high correlations with rankings obtained on the original 50-game benchmark for GBGs. We highlight our work as the basis for future research on highly complex and unusual synthetic environments.

On statistics, we kept the same approach as the original paper. Analysis for the new games was decided before play, and for ten fresh games we fixed predictions of each model's strength before any match was run; observed strength matched them well (Appendix M).

We have also improved the presentation, notation, the model list and the use of the ninth page.

We would be grateful to hear whether these results address your main concern.

We wanted to add a short clarification on how the two equilibrium results fit together. Against the equilibrium, every action in its support earns the same, so breaking even shows that a model playing nearly "consistent with equilibrium", such as gpt-6-astra, almost never makes a move equilibrium punishes. Whether it also randomizes like the equilibrium is a separate question, which we measure as exploitability. With every other move held at equilibrium, a best-responding opponent could exploit how models play at the decisions where the equilibrium randomizes by about 0.02 chips per deal against gpt-6-astra, 0.06 against the top tier and 0.13 against the tail (Appendix L).

An example of why exploitability might matter: if you are deploying a model in a strategic setting on your behalf, and your opponent understands that this is the model you are using, they may be able to successfully exploit your model's play, even if it plays consistent with equilibrium, if it does not also mix in the correct way.

Again we thank you for your review.

Thank you again for your review. Because the discussion period ends tomorrow, we wanted to check and see whether our new results answer your question asking how models perform relative to equilibrium or solved play.

In short, on the 27 games we were able to solve, the frontier models were able to break even against the exact equilibrium while the weakest lose almost a chip per deal. Impressively, gpt-6-astra makes an equilibrium-quality move in 99% of its decisions. No model randomizes like the equilibrium, but a best-responding opponent could gain only a few hundredths of a chip per deal from that against the top models (Section 9, Appendix L).

The hardest games are too large to solve exactly; for those games, play between models remains the reference.

We would be glad to clarify anything, or run a further analysis if it would help, before the deadline. We also note as before our additions in Section 9 and Appendices K-O as work that may be of interest and in our view bolsters the external validity of our evaluation.

Reviewer_hAZKOpenReview ↗
Rating
3(+1)
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper focusses on the problem to evaluating strategic reasoning capability of LLMs. They identified a gap with existing benchmarks -- static benchmarks saturate quickly. To fix this issue, the authors proposed to generate procedurally novel two-player zero-sum imperfect-information betting games. These can be generate in a controllable manner by varying -- state space, temporal contingency, opponent dependence, private information, precision. Using this method, they generated 50-game benchmark and compared 12 frontier and open-weight models, gathering data from over 40,000 LLM vs. LLM matches. By analyzing this data, they found that newer (reasoning capable) models do better than older ones, knowing opponent's strategy helped, etc.

Critical strengths
  • Assessing strategic reasoning gap of LLMs is an important problem. Doing this without benchmarks getting saturated is one of the keys to keep making the progress on this problem.

  • I like the idea of procedural generation of two-player zero-sum imperfect-information games where one can control the complexity in a predictable manner - in this case across five complexity axes in sec 3.1 (state space, temporal contingency, opponent dependence, private information, precision). This can help generate novel benchmarks without performance getting saturated with the release of new LLMs.

  • I also like the thorough analysis carried out in the paper where they generated 50 new games and did 40K matches between 12 LLMs. For example, the analysis of LLM performance across the five complexity axes and the ablations on thinking budget and opponent strategy disclosure provide useful insights into where LLMs perform differently and what can improve their performance.

Critical weaknesses

My only concern with this paper is that their benchmarks appear quite artificial to me. This is fine if it reveals any previous unknown insight for the community. However, this seems not to be the case. I have clarifying questions on this for the authors below.

Questions for authors
  • Beyond methodological contribution of procedural generation, which findings provide new insights into strategic reasoning gaps that existing benchmarks have not shown? I ask this question because I feel that strategic reasoning benchmarks are artificial and the value is not in generation method but outcomes / findings you get by evaluating on these benchmarks. So, more than a new benchmark(s), I encourage authors to highlight new findings that were previously unknown and only uncovered by their evaluation. This will make value of this paper clearer and stronger.

  • Did you you test any other model family than Gemini as your judge? How sensitive are these findings to the LLM judge family given that judge may prefer/bias based on the reasoning trace style?

  • Any concrete ideas on how these findings can be used to design LLMs that are better at strategic reasoning? i.e. which of your findings are actionable?

  • How do you validate that the five complexity axes indeed capture current LLM reasoning challenges? Maybe some justification on this deisgn choice if any could help.

  • Notations like αm,g should be defined when they appear first. I found reading later sections not smooth as I was consistently switching between Appendix and main text.

3 comments

Thank you for your comments. We spent substantial time exploring your central question of what we can learn from synthetic games.

Artificial games measure real skill. While the games are artificial, our hope is that environments are rich and invoke novel trade-offs and planning problems arising from interactions with other players, thus testing a model's ability to reason competently about such things from just a rulebook. For a sufficiently rich generator, the hope is that many real-life interactions between agents whose interests are only partly aligned are close to distributions we can generate. From there, we can use evaluation on generated games as a much better basis to make claims about how models behave when deployed alongside other agents. The betting games are a first version of this, and furthermore GENSTRAT supplies a methodology for adding richness: games are composed from modules, so generators can easily be extended to generate new types of environments.

In the updated paper, we show that skill on the GBGs transfers to other kinds of games. Using the GENSTRAT engine, we built ten generated card games with no betting (Appendix M), and six new games of quite different kinds: three card games, a board game with fog of war, a repeated market and a negotiation. The leaderboard measured on the betting games predicts how models do on the six new games closely, with a rank correlation of 0.95. A general-capability leaderboard (LMArena) reaches only 0.72, and controlling for it the prediction still holds (Figure 14). Results on the betting games already generalize.

Q1. New insights. We highlight two new findings.

First, frontier LLMs plan well but lag in their ability to model opponents. The gap between strong and weak models grows with how much a game rewards planning ahead and shrinks with how much it rewards opponent modeling. Reasoning about the opponent does not pay off in the traces (for any judge we used to classify reasoning traces). Models exploit an opponent's strategy that they are explicitly informed about, but are less able to exploit opponent strategies they are not explicitly told about.

Second, frontier models come impressively close to equilibrium play: the actions they choose are almost always consistent with the equilibrium, but models do not mix consistently with it. On the 27 solved games they break even against perfect play. Only one model, gpt-6-astra, chooses equilibrium-quality actions almost everywhere we can measure, about 99% of the time. The other frontier models lose ground on the hardest games (Section 9, Appendix L).

Q2. Judges. We re-scored the traces with four judges from three model families. Every judge-based finding holds under each of them (Appendix I.4). Judges from different families agree with each other as closely as two judges from the same family, and they rank the model variants almost identically.

Q3. Actionability. First, a model's strategic skill matters even in environments where there are strong motives to cooperate: in bargaining, stronger models claim more of each deal. For choosing a model for a new strategic setting, performance on generated games is a better guide than general-capability rankings. To evaluate frontier models, hard games that reward planning are needed, because easy games no longer separate them.

Second, we think opponent modeling is a natural target for training: models are good at planning, but are less able to reason about what their opponent is doing, and when they do, it does not seem to help them win more chips.

Third, exact or approximate equilibrium solutions can provide a useful signal to evaluate and train weaker models, and most frontier models on hard games, but the ability of the strongest models (e.g. gpt-6-astra) makes this a less convincing method for the best models.

We are also exploring LLM-based teachers of strategy (prompt optimization) as future work.

That said, more work is needed to fully characterize model performance over environment space, and GENSTRAT offers scalable ways to do so.

Q4. Axes. The axes are computed without any LLM data, so it is a fair question whether they track what LLMs actually find hard. The paper gives good evidence that they do. When we regress each model's strength on the axes, 11 of the 60 model-by-axis slopes are significant after correcting for multiple comparisons, and six of these are on temporal contingency (Section 7). On the eight games the axes rank as hardest, the gap between the best and worst model is 1.7 times (1.35 if we normalize games by payoff standard deviation). And on the solved games, every frontier model except gpt-6-astra gives up more chips per decision as games get harder (Appendix L). Reasoning that matches an axis also pays off on games high on it (Section 8, Appendix N).

Notation. α^m,g\hat\alpha_{m,g} is now defined where it first appears.

We would be grateful to hear whether these results address your main concerns.

Thank you for your responses and updated paper. They have addressed some of my concerns, and I have updated my score to reflect it.

Thank you for your engagement and for updating your score. We really appreciate it, and we’re happy to clarify any remaining concerns.

Comments on the paper

3 comments

Thank you for your comments. Our revision adds Section 9 and Appendices K–O. The new appendices were put together during the discussion period, and we will keep tightening their presentation for the final version.

We agree with reviewer Gcwq that GENSTRAT is a synthetic task generator that is useful for future research. We emphasize GENSTRAT as a general-purpose modular engine for constructing multi-agent imperfect information environments. We show this in our revisions, extending GENSTRAT to construct novel and complex non-betting card games, a board game, a market game and a negotiation game. Harder games can be drawn as models improve, and validation scales with modules, allowing for highly complex and multi-stage environments to run with high trust. Evaluation works: rankings from generated games predict play on unseen games of entirely different kinds better than general-capability rankings.

  • Specific responses per reviewer:
    • Gcwq: We solved 27 of the 50 games and played every model against the equilibrium. The hardest games are intractable to solve. For those games that we could solve, frontier models play near equilibrium, and gpt-6-astra plays a move consistent with equilibrium almost every time (Section 9, Appendix L).
    • hAZK and 2Qge: rankings transfer to fresh games, games with no betting, and six new games including a board game, a market and a negotiation, and this is not general capability (Appendix M).
    • hAZK: the main new findings are that current models plan well but model their opponents poorly, and that they reach the equilibrium's value without matching its mixing (Section 9, Appendices L and N). This points to opponent modeling as a training target, and the exact solutions give a per-move error signal. The trace results hold with judges from three model families (Appendix I.4). The axes are computed without any LLM data, and each one separates models in the direction it measures (Appendix N). Notation is now defined at first use.
    • 2Qge: we note that once modules are verified, new games can be generated with automated gates only. Validation therefore scales with modules. We discuss issues with validation in our reply and in Appendix O, and conclude that results are almost entirely unaffected. In the camera-ready version we will include results of detailed LLM-driven auditing of generated games. On prior knowledge, we have narrowed the claim in the introduction: fresh games rule out memorized solutions, not the transfer of general strategic knowledge, which is what we aim to measure, and a game's distance from known poker games does not predict where the ranking holds (Appendix M). We also address issues with payoff scale (Appendix E).
    • Gcwq and 2Qge: the model list is reformatted, and the ninth page now holds Section 9.

Revised PDF (15 Nov) We have uploaded a small update to the revision, mostly making changes to wording. We use the tenth page ICLR allows during the discussion, and moved the figure for the six new games from Appendix M into Section 9, where it is now Figure 4. We also state certain findings more precisely.

Figure numbers in our earlier replies refer to the previous PDF. Figure 14 is now Figure 4, Figure 10 is now Figure 11, and Figure 12 is now Figure 13.

Revised PDF (18 Nov)

Following reviewer 2Qge's suggestion, the revision frames GENSTRAT as a pipeline for generating validated strategic game environments, with the 50-game benchmark as its first instance (Abstract, Introduction, Sections 3, 4 and 10). Validation now has its own subsection in the main text (Section 3.1), and Appendix O adds a test of the checks themselves: an independent rebuild of each game from its rulebook caught 66 of 68 planted harmful rule changes and flagged none of the harmless ones. No results changed. The complexity axes are now Section 3.2, and figure numbers are unchanged.

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

Related papers

Loading the map…

Discussion (0)

Sign in to comment.