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Under review as a conference paper at ICLR 2027

TiaoQi: A Solved Game as Exact Ground Truth for Concept Discovery and Its Validators

Abstract

Concept-discovery methods return features with names, and the field validates a name against the model, its activations or human labels, never against whether the concept is true. A strongly solved game supplies that ground truth. Every position has an exact value, so a claimed concept can be checked against it, and so can the test that validated it. We introduce TiaoQi, a benchmark on Chinese checkers that, to our knowledge, is the first to check every concept claim about a network against exact truth, and the first to use the same truth to grade its own tests: how often they pass a random direction, and how often a passing feature passes again. On it, a standard sparse-autoencoder pipeline returns few but real causal handles on the network's moves, 39–62 per agent where noise would earn 0–3.8. The handles sit on the game's own folk concepts, the features found for a fact are needed for play as a set, and the count replicates across seeds, layers, positions, dictionaries and rule variants. The same truth also grades four of the field's validation practices. A shuffled-label control certifies every dictionary where a matched random slice does not, a value-readout pass rule admits 1.8% to 5.5% of noise, a single feature's label is one draw, and decodable and used come apart in both directions.

Primary area:
interpretability and explainable AI
Keywords:
interpretability, mechanistic interpretability, concept discovery, concept validation, sparse autoencoders, activation patching, ground truth, solved games, game-playing agents, benchmark, probing

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_Y6zKOpenReview ↗
Rating
4
Confidence
2
Informativeness
2
Presentation
2
Soundness
3
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Paper summary

The paper explores concept discovery, the task of finding neuron activation patterns that correspond to a concept, in the context of a game where the concepts are strategies.

Critical strengths
  1. The work is original in looking for concepts that are strategies rather than board positions, and that it validates the discovered concepts against the ground-truth of game play.

  2. The authors report limitations openly, including that the self-play agents play little better than the base control.

Critical weaknesses
  1. The discovered activation patterns are correlated with a particular strategy, but might not be causally related.
  2. Missing closely related work: Jenner et al. (NeurIPS 2024), "Evidence of Learned Look-Ahead in a Chess-Playing Neural Network," uses causal interventions on a game agent's internals. See also (Geiger et al., NeurIPS 2021) for the D2/D3 coordinate swap.
Questions for authors

Lots of newly introduced vocabulary makes the paper hard to read (eg. race class, named vs unnamed, etc). Could you try to make at least the abstract readable and self-contained.

1 comment
AuthorsOpenReview ↗

Response to Reviewer Y6zK

Thank you for the review, and for the two references, both of which we have added.

W1, correlation versus causation. You raise the possibility that the activation patterns we find are correlated with a strategy but not causally related to it. That is the right worry about a concept-discovery result, and it is the one the protocol is built around, so we think the paper failed to make it visible rather than failed to address it. Of the three tests a feature must pass, only the first, D1, is correlational, and it sets no bar and declares no handle. D2 is an intervention: we overwrite one coordinate of the feature with its value at a matched position where the fact is false, re-run the network, and score the change in the network's play against 40 random pushes of the same size and a value-blind fake. D3 is a second intervention on the same pairs: the swap from a fact-false twin must cost more than the swap from a fact-true twin, beyond a band of random directions, so that the change depends on the fact's content and not on the swap itself. A feature is called a causal handle only if it passes both. We have now said this in Section 4's opening paragraph, before any test is described (p. 4), and a planted handle sent through the same rule gives the two interventions the positive control they lacked (new Appendix R, pp. 45–46). The claim this supports is a handle on play on the fact's positions; we do not claim that the network computes the strategy, and the limitations say why (p. 10).

W2, Jenner et al. (2024) and Geiger et al. (2021). Thank you for both. We added Jenner et al. to the games paragraph of Section 2 (p. 3): activation patching on a chess network shows that it represents a puzzle's future moves and that its choice of the solution move depends on them, with the puzzle's annotated line as the yardstick. We added Geiger et al. at D2's definition (p. 5): the coordinate swap is an interchange intervention restricted to one coordinate, and Appendix I now names it alongside the activation-patching term it had used.

The vocabulary and the abstract. You ask that at least the abstract be readable and self-contained. We rewrote it in plain words with every claim and number kept (p. 1), so a reader meets no coined term before its meaning. In the main text we replaced coined terms with plain phrases wherever one existed; your example "race class" now reads "set aside if its fact is a value class (who is winning) or the negation of a fact" (Section 4, p. 6), and Section 4's new opening paragraph defines candidate, causal handle and noise count before they are used. The glossary (Appendix A) remains for the terms the appendices need.

Thank you again; both points improved the paper, and we are glad to discuss either further.

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

This paper presents an interpretability evaluation framework built on a solved Chinese checkers game. The authors train game-playing agents and evaluate extracted features through representation analysis, activation interventions, and dependence tests. They find that a small number of sparse-autoencoder directions substantially influence the agents’ move quality.

Critical strengths

Using a solved game provides exact strategic labels and objective measurements of decision quality, creating a controlled setting for examining interpretability claims.

Critical weaknesses
  • The manuscript is difficult to follow.
  • The paper does not introduce a new interpretability method, and its comparison of existing methods is narrow. It does not provides actionable guidance for improving interpretability approaches.
  • The experiments are restricted to a single game family and relatively small networks trained specifically for this setting. The manuscript does not establish how its findings inform the interpretation of modern LLM agents operating across diverse domains.
Questions for authors

The current manuscript reads primarily as a case study of particular game-playing networks. What is its core transferable insight about interpretability methods, and what evidence supports that insight beyond this game experiment?

2 comments
AuthorsOpenReview ↗

Response to Reviewer aXrJ

Thank you for the review. You ask what the paper's transferable insight is and what evidence supports it beyond this game; we answer that first, because it decides how the four weaknesses should be read, and then take the four in order.

The question: the transferable insight and its evidence. Concept-discovery methods are validated against the model they describe, its activations, its outputs or human labels, and never against whether the concept is true, because where they are used nobody knows the truth. The insight the paper rests on is that this can be fixed in one place: on a strongly solved game a real network, trained by ordinary self-play, can have every concept claim about it checked against exact truth, and so can every test used to validate such claims. That makes two things measurable that are elsewhere taken on trust: the rate at which a validator passes a direction with no content, and the rate at which a passing feature passes again on a fresh draw. The evidence is what those measurements showed on the first network graded. Two common validators fail: a control that shuffles the labels certifies every dictionary we graded, and a pass rule read on the value head admits 1.8% to 5.5% of random directions (Section 5.4). A single feature's label survives a fresh draw about half the time, so claims belong at the level of counts. And what a probe can decode and what play uses come apart in both directions (Section 5.2). The first two of these hold by construction and would hold on any network; the others are measurements on this network, and Section 6 now says so (p. 10). What transfers is not a number but a requirement, that a method and its validators be given error rates before they are trusted where no truth exists, and an instrument on which that can be done.

(a) Hard to follow. Two other reviewers said the same, and we take it as the paper's main fault. We rewrote the abstract in plain words with every claim and number kept (p. 1); we stated the premise of the benchmark in one sentence in Section 1 (p. 1); we added an opening paragraph to Section 4 that says what each stage rules out and defines candidate and causal handle before use (p. 4); and we replaced coined terms with plain phrases where a plain phrase existed. If one passage stood out as the hardest to follow, we would gladly rewrite it in this round.

(b) No new method, a narrow comparison, no guidance. The paper proposes no discovery method by design: it is a benchmark, and its contribution is the grading, not the discovery. Three methods are graded on one report card, sparse autoencoders, concept vectors and a linear probe as the reference, because those are the three the field uses on game agents. The guidance is the protocol and its four lessons: which control to report beside a dictionary (a matched random slice, since the shuffled-label control certifies everything), which readout admits noise and at what rate, why claims about what a network carries belong at the level of counts beside a noise count, and that decodability is not use (Section 6).

(c) One game family and small networks. Agreed, and the paper says so (Section 6, p. 10). Within the family the handle count holds across three seeds, two training arms, two position pools, a freshly extracted dictionary and two rule variants, and we claim nothing for other architectures; Section 6 now names which lessons a different network could overturn.

(d) LLM agents. The paper claims no result about them. What it offers is a place to calibrate the instruments used on them and a route to grading them. The validators the field applies to language models are used without a known error rate, because nothing there can check them; here the same kinds of validator are given measured false-pass and re-pass rates on a real network, and two common ones fail, which is the argument of Section 1 (p. 1). The protocol reads activations at one layer and patches one direction, so it applies without change to a transformer trained on the game, and an agent acting where a checker decides every step, code, proofs or a game with an oracle, has exact truth about its behaviour in the same sense as our move readout; Appendix S sets out that route as a direction, not a result. The gap between what a probe decodes and what the network uses, which we measure against exact truth, is the dissociation concurrent work reports in language models against the model's own behaviour (Section 2); we cite it as consistent and do not claim it.

Thank you again for the review; its question about the transferable insight is the one the paper most needed to answer plainly, and we are glad to discuss any point further.

AuthorsOpenReview ↗

Following up on the revised PDF and our replies

We wanted to make sure the revised PDF and our reply (posted 9 Nov) reached you before the discussion closes on 18 Nov, and we would value your thoughts on them. The reply answers your question about the transferable insight first and then the four points. The revision addresses readability directly: the abstract is rewritten in plain words (p. 1), the benchmark's premise is stated in one sentence in Section 1 (p. 1), and Section 4 opens with a paragraph that explains what each test rules out and defines its terms before use (p. 4). We would welcome your view on whether the revised paper reads more clearly, and we would be glad to address anything that remains open in the time left.

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

The paper presents TiaoQi, a benchmark that relies on a strongly solved 6x6 Chinese checkers game as exact ground truth for discovering and validating causal handles for concepts in a neural network trained to play the game. The authors train agents by self-play and extract from them a set of sparse-autoencoder latents as candidate directions encoding the concepts related to facts. These candidates are then graded through a multi-stage protocol consisting of a purity margin test, single-direction activation patching, dependence test comparing patches from twin positions where the fact is true and false, and finally an ablation of all the features assigned to a fact and a null program (accounting for noise). The headline result is 39-62 discovered handles per self-play agent, against a noise count of 0-3.8. The authors also draw lessons for best validation practices.

Critical strengths

Concept-discovery claims are rarely checked against an exact ground truth in a chosen domain of interest. Grading against the ground-truth provided by a strongly solved game is the most original point of the paper.

Critical weaknesses

The main weaknesses of the paper are listed below.

W1.) Poor quality of writing.

First, the language lacks scientific rigor. For example, some of the verbs the authors use are "earn", "buys", "travels" and similar, while they also use imprecise expressions like "few but real handles". More importantly, Section 4 is presented through a series of (loosely connected) paragraphs, each introducing a test in isolation but none explaining what gap each one closes and/or why this is the right set of tests to run in the first place. Some of the key objects are also used before being defined: for instance, the notion of candidate is formalised only in D2, but D1 already relies on it (it is even in the title of the paragraph). Similarly, the central notion of handle is never explicitly defined in the main body of the paper. The main text suggests a handle is a candidate that passes D2, but the glossary gives a different definition, in terms of one that passes both D2 and D3.

W2.) The restriction of concepts to facts is barely motivated.

That only concepts expressible as binary facts are graded finds as only (briefly mentioned) justification a decidability argument. However, the paper should discuss what this choice excludes and how this impacts the presented results. Also, (cf. W1) the definition of a fact appears in Section 3 only while it is needed earlier.

W3.) Many thresholds are set arbitrarily and no sensitivity analysis is provided.

Beating the value-blind fake by 2 game-clustered standard errors, bands defined through 10 random directions, a candidate pass under "40 random pushes of equal size by three of their standard deviations", the REAL candidate firing on at least 6000 held-out scoring positions (and similar others) are arbitrarily set. All the hand-picked thresholds should be motivated and their impact on the results should be discussed by including a sensitivity analysis under different thresholds.

W4.) The rule's sensitivity is never measured.

The authors state that "no direction known in advance to be a handle was sent through D2 and D3". It is appropriate to ask what would happen if a direction is engineered to drive the policy on a fact.

W5.) The findings are weaker than what the presentation suggests.

Appendix L shows that REAL handles are poor detectors of their assigned facts with median precision of 0.23, 0.05 and 0.03. The handles associated with forced-wait are the largest group and they fire mostly on stall positions (median 0.88–0.94), where the mover has no advancing move. This property refers to the board alone and needs no solved table, which was the main motivation for the paper. Also, the named handles fall on facts being properties of the board alone. Finally, the claim that "carries causal handles for the concepts that players of the game name" is not currently supported by the results and should be narrowed down according to what the paper is actually able to quantify.

W6.) The scope is quite limited, especially for an experimental only paper.

The paper is an experimental one, and it makes claims about methods and validators (e.g. "the shuffled-label control certifies everything"). These claims are only supported by a single domain and a single architecture, which limits the generalizability of the results. The authors should test at least one more domain (for example, chess endgames with tablebases, other solved games) and at least one more architecture (for example, a transformer). Without any of these, it is unclear whether the measured rates and lessons are properties of the validators or of the particular network and pipeline object of the study.

W7.) The reported effect sizes are small.

Appendix J shows that the D3 effect of REAL move-side features has a median of 0.016, 0.016, 0.014, but the game-clustered standard error is 0.013, 0.014, 0.013. The effect is thus comparable to its standard error.

Given the severity of several of the above weaknesses, I recommend a weak reject decision for this paper.

Questions for authors

Q1. How did you choose all the thresholds? Q2. Given their low precision and coverage, in what sense the REAL handles "sit on" the folk-concepts? Q3. Would the validation lessons hold for a transformer-based agent?

5 comments
AuthorsOpenReview ↗

Response to Reviewer TGBq (1 of 2): W1 to W4 and Q1

Thank you for a careful review. W3 and W4 asked for experiments, and both are now in the revised PDF; the writing points changed Sections 1, 3 and 4. We take the weaknesses in order, in two comments because of the length limit: W1 to W4 with Q1 here, W5 to W7 with Q2 and Q3 next.

W1, the writing. You name three faults: verbs such as "earn", "buys" and "travels" and the phrase "few but real handles"; a Section 4 that presents its tests one by one without saying what gap each closes; and objects used before they are defined, with "handle" meaning one thing in the text and another in the glossary. Each of these is fair. We removed the verbs from the main text and kept "few but real" once, in the abstract beside its numbers. We added an opening paragraph to Section 4 that says what each stage rules out and why the chain has this shape, and defines "candidate" and "causal handle" before D1 uses them (p. 4); "handle" now has one meaning throughout, a candidate that passes D2 and D3 and fires often enough to be tested, and we renamed the D2 heading (p. 5).

W2, the restriction of concepts to facts. You ask that the restriction be motivated, that the paper say what it excludes and how that affects the results, and that the definition come before Section 3. We now introduce the word where the idea is (p. 2) and added a paragraph to Section 3 on what cannot be a fact and on what happens to a feature for such a concept (p. 4). That paragraph also says what happens to the counts: such a feature is assigned the nearest fact in the family and then tested against that fact's labels rather than its own concept, so it is more likely to fail the causal tests than to pass them, and the counts err low for concepts outside the family. Part of what the family misses is nevertheless visible: 7, 17, 15 of the self-play agent's handles per seed pass the causal tests and match no fact in the family. We kept the restriction itself: it is what makes every claim in the paper decidable, which is the paper's purpose, and the field made the same trade once before, when board-state recovery became the ground truth for evaluating dictionaries because open domains offered none (Section 1, p. 2).

W3 and Q1, the thresholds. You are right that no threshold was motivated and no sensitivity analysis given; Appendix Q (pp. 43–45) now does both. Table 29 lists every constant of the causal rule with its role and how it was chosen: the pass bars (three standard deviations over the random pushes, two standard errors over the value-blind fake, one band width in D3) are conventions fixed before the data, and the floors (1,000 held-out firings to enter D1, 6,000 to be counted REAL) are derived from the counts a proportion needs to be estimable. Table 30 moves each bar and the floor to a stricter and a looser value and recomputes the count beside its noise count: the bars move the count by at most 41%, the floor moves it severalfold (150, 128, 52 at 3,000 fires to 21, 28, 24 at 12,000), and the noise count stays near zero at every setting (largest 5.6). Table 31 does the same for the set-level bar. The three sample sizes you list (40 pushes, 10 directions, 500 pairs) are a different kind of constant. A threshold says where a pass line sits; a sample size says how precisely the quantities the line is drawn from are estimated, the pushes' mean and spread and the D3 band. A larger sample does not move the line's intended position; it makes the realised line less noisy from one draw to the next, and the "beat every push" clause stricter, never looser. How much that noise affects the counts we measured directly: the re-pass experiment of Section 5.4 redraws pushes, directions and pairs at exactly these sizes, and under it single labels flip about half the time while the count per method holds.

W4, the rule's sensitivity. You quote the sentence "no direction known in advance to be a handle was sent through D2 and D3" and ask what happens when a direction is engineered to drive the policy on a fact. We did that. A random unit direction in the first layer was set positive where the rear-piece rule holds and negative where it does not, we made the network's move choice depend on it, and we sent the result through the unchanged rule at six strengths, where a handle's strength is how much value-keeping play the network loses when the direction is removed (Appendix R, pp. 45–46; Section 5.4, p. 9). The control passed: the planted handle comes out REAL. It does so from a strength of 0.08, where all five planted directions are counted; at 0.04 none is, because each beats every random push but not the value-blind fake, whose margin of about 0.045 is the binding bar. So the rule detects an engineered handle once its effect on play reaches a third to a half of the effect of the handles the paper reports (0.13 to 0.21), and a real handle weaker than that floor is missed, so the counts err low. The Appendix I sentence you quoted now points at this result.

AuthorsOpenReview ↗

Response to Reviewer TGBq (2 of 2): W5 to W7, Q2 and Q3

W5 and Q2, whether the findings are weaker than the presentation. You read in Appendix L that the REAL handles are poor detectors of their facts (median precision 0.23, 0.05, 0.03) and that the largest group fires mostly on stalls, which the board alone defines; you conclude that "carries causal handles for the concepts that players of the game name" is not supported, and ask in what sense the handles "sit on" the concepts. You are right about the numbers: the handles are poor detectors of their facts, and most forced-wait handles fire on stalls. Where we disagree is what the numbers show, because a handle was never claimed to be a detector. A handle is a direction whose patching, where the fact holds, moves play as the fact predicts, beyond matched random pushes and a value-blind fake, and more from a fact-false twin than a fact-true one. Precision measures something else, how often the direction fires only where the fact holds; a handle can move play on a fact's positions while firing on many others. Each handle also carries two labels, which the review merged: the fact it is graded against in D2 and D3, the label the count uses, and the fact the representation test names, which applies only to the small subset whose purity margin beats all of its own random slices. It is that subset, not the handles, that falls on the easy board facts. Forced wait holds on every stall, so on the agent-free pool its handles are mostly stall handles; the test of whether that is all they are is a pool where stalls are rare. On the cross-play pool the handles fall on the rear-piece rule (13), greedy-wrong positions (13) and the entry trap (8), facts that cannot be read from the board without the table, and on forced wait (6), against 22, 23, 11 forced-wait handles per seed on the agent-free pool (Appendix M). We added that sentence to Section 5.2 (p. 8). We agree the claim sentence overreached as worded, and we rewrote it: "carries causal handles on the positions of the concepts that players of the game name", in the abstract and the conclusion, which is what "sit on" meant.

W6 and Q3, one domain and one architecture. You ask whether the measured rates and lessons are properties of the validators or of this particular network. The answer differs by lesson, and Section 6 now says so (p. 10). Two are properties of the validators: a control that shuffles the labels within distance cells destroys the labels' content and keeps the feature's density, so it certifies every dictionary wherever it is applied; and a single feature's label rests on finite random bands, so it is one draw on any network. Two are measurements on this network: the rate at which a pass rule read on the value head admits random directions (1.8% to 5.5%) and the size of the gap between what a probe can decode and what play uses; the first was measured across three seeds, two arms and two pools, the second on one seed of each of four networks, and we claim them for this network only. The sentence you quote, that the shuffled-label control "certifies everything", now reads "certifies every dictionary we graded". The paper reports these as what the instrument found on its first subject, not as laws of validators; its claim is the instrument, on which the generality question becomes decidable. Whether the two measured lessons hold for a transformer (Q3) is the first question we would put to it, since the protocol applies to any architecture whose layer can be read and patched; we did not run one and do not claim the answer.

W7, the size of the effects. You point out that the D3 effect of a REAL feature, a median of 0.016, 0.016, 0.014, is about the size of its game-clustered standard error, so the effects look small. That is true of the increment, and a third of the features sit inside their error. The main text had not shown the effect itself. Patching a REAL feature from a position where its fact is false costs a median 0.21, 0.18, 0.13 of value-keeping play, against 0.027, 0.015, 0.023 for a random push of the same size; that is the handle's effect, about eight times its control. The D3 increment is the extra cost of the fact-false swap over a fact-true swap from a twin just as far away in activation space, and it is a tenth of the drop because the fact-true swap costs nearly as much: the fact's label is a small part of what the direction carries. No claim in the paper rests on that increment alone. A feature is REAL only if it passes D2, the D3 condition and the firing floor together, and the rate at which random directions pass that whole rule is measured, 0 to 1.5% of trials on the move readout; the counts are read against that rate. We now give the drop and the increment side by side in Section 5.1, with this reading (p. 7).

Thank you again for the review; its two experiments and the clearer statement of what a handle is have made the paper more exact about its claims. If any of these points remains open, we are glad to discuss it further.

AuthorsOpenReview ↗

Following up on the revised PDF and our replies

We wanted to make sure the revised PDF and our two replies (posted 9 Nov) reached you before the discussion closes on 18 Nov, and we would value your thoughts on them. The two experiments you asked for are in the revision: the threshold sensitivity analysis, with every constant of the rule listed and each bar and the firing floor swept (Appendix Q, pp. 43–45), and the planted handle that measures what the causal rule catches (Appendix R, pp. 45–46; Section 5.4, p. 9). Section 5.1 now puts the D2 effect beside the D3 increment (p. 7), and Section 6 says which lessons depend on the network and which do not (p. 10). If any of W1 to W7 remains open after the replies, we would be glad to address it in the time left.

Comments on the paper

1 comment
AuthorsOpenReview ↗

General response: the purpose of the paper, and what changed in the revised PDF

We thank the three reviewers. A revised PDF is uploaded (the chairs allow a tenth main-text page). This comment first states what the paper is for, since that frames every point below, then lists what changed and where, so nothing needs rereading beyond the passages named. Point-by-point replies follow under each review.

The problem the paper addresses. A concept-discovery method returns a feature with a name, and the field checks the name against the model: its activations, its outputs or labels people wrote. Nothing checks it against whether the concept is true, because where these methods are used nobody knows the truth. The validators themselves are never checked either, and two of the common ones fail when they finally are: on our networks a control that shuffles the labels certifies every dictionary we graded, and a pass rule read on the value head admits 1.8% to 5.5% of random directions. Neither failure could have been seen without a setting in which truth is exact.

What the paper builds. That setting is a network trained the ordinary way, by self-play, on a strongly solved game, where every position has an exact value. Any yes-or-no concept that can be written from the board and the solved table is decidable for every position, so a claim that a feature tracks a concept, or that patching it moves play as the concept predicts, can be checked exactly, and so can every test used to make such a claim. The contribution is the instrument: the testbed, and a grading protocol whose own false-pass rate (what random directions earn under the full rule) and re-pass rate (how often a passing feature passes a fresh draw) are measured on the network it grades. The findings, 39–62 causal handles per agent against a noise count of 0–3.8 and four lessons on validation practice, are what the instrument produced on its first subject. What follows for the field is that a method and its validators can be given error rates before they are trusted where no truth exists, and the testbed and protocol are released for that.

What the reviews asked, and what we did. Reviewer TGBq asked for a sensitivity analysis of the thresholds and for a test of what the causal rule catches; both are new experiments in the revised PDF. In Appendix Q (pp. 43–45) every constant of the rule is listed with its role and how it was chosen, and each bar and the firing floor is moved to a stricter and a looser value with the count recomputed beside its noise count: the three bars move the count by at most 41%, the floor moves it severalfold (150, 128, 52 at 3,000 fires to 21, 28, 24 at 12,000), and the noise count stays near zero throughout (largest 5.6). The number of handles is set by how rare a feature may be and still be testable, not by where the pass lines sit. In Appendix R (pp. 45–46) a direction known to be a handle was wired into the network and sent through the unchanged rule at six strengths: the rule counts it once removing it costs 0.08 of value-keeping play, the value-blind fake's margin of about 0.045 is what sets that floor, and the handles the paper reports cost 0.13 to 0.21 when patched, two to four times the floor. This is the positive control the causal test lacked, and it fixes the direction of the error: a real handle weaker than the floor is not counted, so the reported counts err on the low side.

Changes by section. Writing. We rewrote the abstract in plain words with every number kept (p. 1), introduced the word "fact" where the idea is (p. 2), and replaced verbs such as "earn" and "travel" throughout. Definitions and structure. Section 4 now opens with a paragraph on what each stage rules out, D1 correlational and D2 and D3 interventions, with candidate and causal handle defined before use (pp. 4–5); Section 3 gains a paragraph on what cannot be a fact and what that does to the counts (p. 4); Section 1 states the premise of the benchmark in one sentence (p. 1). Claims and evidence. The handle claim now reads "handles on the positions of" the named concepts in the abstract and the conclusion (pp. 1, 10); Section 5.1 puts the D2 cost beside the D3 increment (p. 7); Section 5.2 adds the handles' counts on the cross-play pool, where stalls are rare (p. 8); Section 6 says which lessons hold by construction and which were measured here (p. 10); Geiger et al. (2021) is cited at D2 (p. 5) and Jenner et al. (2024) in related work (p. 3); Appendices Q and R are new (pp. 43–46).

What we did not change. The scope, one game family and one architecture, and the restriction of concepts to exactly decidable facts are the premise that makes every claim checkable; both are stated as limitations and nothing is claimed beyond them. We ran no second domain or architecture; Section 6 says which lessons depend on the network and which do not, so a reader knows exactly what a second subject could overturn.

We are grateful for reviews that led to two experiments and a clearer paper, and welcome further discussion.

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

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