DJ-Research/GameBoyWorlds-Playthrough-Contamination-Check

Documentation Density Predicts Benchmark Performance: A Contamination Probe Using Official and Fan-Made Pokémon Titles

Abstract. Benchmark scores on well-documented domains conflate what a model can reason about with what it has memorised. We construct a 400-item short-answer benchmark over four Game Boy–era Pokémon titles, paired by surface form but differing sharply in corpus footprint: two officially published games (Red, Crystal) and two community ROM hacks (Brown, Prism). Four models — GPT-5.6-sol, Claude Opus 5, Gemini 3.5 Flash-Lite, and Gemma 4 31B — were queried statelessly with retrieval disabled, and every answer was scored under four independent regimes: human annotation, BLEU-2, BERTScore-F1, and a stateless LLM judge (Claude Sonnet 5). Overall accuracy spans 36.2–64.5%, but this aggregate is an artefact of pooling: all four models score 60.5–100% on the official titles and 12.0–29.0% on the fan-made titles, a gap of 48.5–83.0 percentage points with Fisher exact p < 10⁻²⁴ in every case. The 39.5-point spread that separates the four systems on documented titles narrows to 17.0 points on undocumented ones, where three of the four become statistically indistinguishable. We further find that the choice of scoring regime materially changes the conclusion: the LLM judge reproduces the human ranking (Spearman ρ = 0.949, Cohen's κ = 0.750) while systematically understating accuracy, whereas BERTScore-F1 inverts it, ranking the second-place model last because of a strong length penalty (r = −0.575 between answer length and score among correct answers). We argue that a documentation-density contrast of this kind should be a standard component of benchmark design, and that surface-form metrics are unsuitable for ranking models whose answer-length distributions differ.

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1. Introduction

A benchmark is intended to measure capability, but a model that has read a domain's reference material many times during pre-training can score well on that domain without exercising the capability under test. This is the contamination problem, and it is difficult to detect from a single score: a high number is consistent both with genuine competence and with recall of memorised text.

Retrospective decontamination — searching training corpora for benchmark strings — is unavailable for closed models and imperfect even for open ones, since paraphrase and partial overlap evade string matching. We therefore take a different approach: hold the task constant and vary only how much the world has written about it.

The Pokémon franchise affords an unusually clean instrument for this. Officially published Game Boy titles are among the most thoroughly documented artefacts in gaming, with decades of wikis, printed strategy guides, and forum archives almost certainly present in any large web-scraped corpus. The same franchise also hosts a substantial community ROM-hack scene: full-length games built on the same engines, with the same interface conventions, the same creature and item vocabulary, and the same event-driven structure — but documented only in scattered forum threads and video walkthroughs, and plausibly near-absent from pre-training data.

Questions drawn from the two categories are near-indistinguishable in form. "Which Badge does Brock award after his defeat?" and "Which named tunnel must the player traverse from eastern Mt. Boulder?" demand the same kind of retrieval over the same kind of game state. What differs is corpus exposure. A model's accuracy differential between the two categories therefore isolates memorisation from task competence more directly than any single aggregate score can.

This report makes three contributions:

1. A paired benchmark design (§2) in which documentation density is the manipulated variable and task form is held constant.
2. A measured contamination gap (§4.2) of 48.5–83.0 percentage points, present in all four models tested and significant at p < 10⁻²⁴ throughout, which collapses the apparent model hierarchy.
3. A metric-validity analysis (§4.3) showing that the four scoring regimes applied to identical answers do not agree, that a stateless LLM judge is a usable conservative proxy for human annotation, and that BERTScore-F1 inverts the true ranking on this domain for a mechanical reason (short references, variable answer length).

2. Benchmark design

We constructed 400 short-answer items, 100 per title, over four Game Boy–era Pokémon games selected to vary systematically in documentation density while holding genre, interface, and question style constant.

Table 1. Titles, provenance, and expected corpus footprint.

Title	Year	Provenance	Expected corpus footprint
Pokémon Red	1996	First-party (Game Freak / Nintendo)	Very high — decades of wikis, guides, strategy books
Pokémon Crystal	2000	First-party (Game Freak / Nintendo)	Very high
Pokémon Brown	2003–	Community ROM hack (Rijon region)	Low — scattered forum threads, video walkthroughs
Pokémon Prism	2016	Community ROM hack (Naljo region)	Low

Throughout we refer to Red and Crystal as the official subset (n = 200) and Brown and Prism as the fan subset (n = 200).

2.1 Item and reference-answer provenance

Provenance differs by title, and we disclose it here because it bears directly on how the fan-subset results should be read.

• Pokémon Brown. All 100 questions and reference answers were authored by the first author from a first-hand playthrough, working from their own walkthrough notes. No published guide was consulted. This subset is grounded in directly observed game state.
• Pokémon Red, Crystal, Prism. Questions and reference answers were derived from walkthroughs sourced from well-rated community forums and video walkthroughs, and each item was verified by a human annotator against the source material before inclusion.

Because one subset is author-generated and three are guide-derived, a provenance artefact is a live alternative explanation for any Brown/Prism difference. §4.2 tests for it directly and finds none in a consistent direction.

2.2 Item properties

Items target verifiable, single-fact game state — event triggers, NPC identities, item and badge names, gym specialisations, required field moves, and route topology — rather than opinion or strategy. Reference answers are deliberately terse: median 3 tokens, mean 4.62 (SD 3.58, range 1–21).

This brevity is a property of the domain rather than a design choice, and it has consequences for scoring that we quantify in §4.3. It is the reason standard BLEU-4 is inapplicable here, and the reason embedding-based similarity is length-sensitive on this data.

3. Methodology

3.1 Elicitation constraints

Four models were evaluated. Every pipeline was built to satisfy the same three requirements, since any violation would confound parametric recall with retrieval:

• R1 — Statelessness. One question per request. No conversation history, no prior question or answer, no reference answer, and no other rows appear in any request payload.
• R2 — No retrieval. No tool, function, browsing, or grounding facility is enabled on any request. The model answers from pre-trained weights alone.
• R3 — No account-level personalisation. Raw API or local-server endpoints only, never consumer chat front-ends, so that no chat memory, custom instruction, or profile can influence a response.

All four pipelines share a prompt skeleton: a short instruction forbidding lookup and requesting a bare 1–2 sentence answer, followed by Game: {game} and Question: {question} taken verbatim from the source table. Responses were checkpointed to disk every 5–10 rows so interrupted runs resume without re-querying completed items.

3.2 Per-model elicitation

GPT-5.6-sol (gpt-5.6-sol). OpenAI Chat Completions API. The lookup prohibition is carried in a system message; the user message contains only game and question. The tools argument is never passed, which disables web search, retrieval, and code execution at the API level rather than by instruction. R3 holds by construction — the raw API carries no chat memory or custom instructions. Sampling parameters were left at provider defaults, with a fallback that drops rejected sampling arguments and retries. Transient failures retried with exponential backoff (max 5 attempts). 400/400 answered.

Gemini 3.5 Flash-Lite (gemini-3.5-flash-lite). Gemini generateContent endpoint, standard library only. Each request carries exactly one contents entry. Critically, the tools field is omitted: Google Search grounding is opt-in on this API, so its absence — not a textual instruction — is what enforces R2. Decoding deterministic (temperature = 0.0, maxOutputTokens = 2048). Because the run used a free tier, requests were paced to an explicit RPM ceiling, HTTP 429s were retried using the RetryInfo.retryDelay value the API returns rather than a guessed interval, and per-day quota exhaustion terminated the run cleanly for later resumption instead of consuming remaining items on doomed retries. The API key is read from the environment, sent as a header, and redacted from all logs. The served modelVersion is compared against the requested model on the first successful response and the run aborts on mismatch, so a silent model substitution cannot mislabel the results. 400/400 answered.

Gemma 4 31B (gemma4:31b-cloud). Served via a local Ollama instance using the -cloud routing tag, queried one row at a time against /api/generate, standard library only. That endpoint exposes neither tools nor retrieval, so R2 holds structurally. Decoding fully deterministic (temperature = 0.0, seed = 0). A preflight step verifies the server is reachable and reports whether the tag resolves locally or is proxied. As with the Gemini runner, the served model name is compared against the requested name — after stripping the -cloud routing suffix and :latest, which denote where a model runs rather than which model it is — and the run aborts rather than writing mislabelled results. 398/400 answered; the 2 unrecoverable failures (0.5%) were retained as empty cells and scored incorrect, making the reported accuracy a lower bound.

Claude Opus 5 (claude-opus-5). Elicited via per-question sub-agent dispatch inside a Claude Code session: one freshly spawned sub-agent per question (400 total), each beginning from an empty conversation with no access to the orchestrator's history, the source table, other questions, or reference answers. Sub-agents were launched in concurrent batches of 20 and collected synchronously. This route was chosen because the claude CLI was unavailable on the host and no API key was configured; the resulting isolation is equivalent to a per-question API call for R1 and R3.

R2 differs in kind here and we state the difference plainly. The available sub-agent type exposes the full tool set and tool access cannot be disabled by parameter, so retrieval was prohibited by instruction and verified post hoc from the tool_uses counter in each sub-agent's usage metadata. All 400 completed sub-agents reported tool_uses: 0; a non-zero count would have triggered a re-run of that item. The guarantee is empirical rather than structural — a weaker claim than the other three pipelines support.

Two session rate-limit interruptions occurred. Failed sub-agents produced no final message and contributed nothing; affected items were re-launched as fresh independent instances, preserving statelessness. Answers were logged verbatim to an append-only JSONL keyed by row index and merged by column name, leaving all other data byte-identical. No post-hoc cleaning, normalisation, or quality-based re-querying was applied; where a sub-agent reasoned aloud inside its single message, the raw text was retained. 400/400 answered.

Answer post-processing was identical for the Gemini and Gemma pipelines (strip code fences, wrapping quotes, and leading Answer: labels; collapse whitespace) and absent for the GPT and Claude pipelines beyond whitespace trimming. Because all surface-form scores are computed from these stored strings, this asymmetry propagates into BLEU and BERTScore, and is one reason we do not treat them as primary (§4.3).

3.3 Scoring regimes

Each of the 1,600 (item, model) cells was scored under four independent regimes.

Human annotation (primary). One human annotator assigned each cell Right, Partially Right, or Wrong, judging semantic agreement with the reference answer and ignoring wording, formatting, capitalisation, and ordering. We report strict accuracy — the proportion labelled Right — with a partial-credit variant (Right + 0.5 × Partially Right) alongside; partial labels are rare (1.5–2.8% per model) and change no conclusion. Labels were case-normalised before analysis, as one column used the variant spelling Partially right.

BLEU-2 (smoothed). A dependency-free implementation computing clipped n-gram precision for n ∈ {1, 2} with equal weights, geometric mean, standard brevity penalty, and Chen & Cherry (2014) method-4 smoothing; tokenisation lowercases, strips punctuation, and splits on word characters. Scores are cross-checked against NLTK's sentence_bleu under matched settings when available, but written values always come from the local implementation so results reproduce without dependencies.

The deviation from standard BLEU-4 is deliberate and consequential. With a median reference length of 3 tokens, most items cannot form a single 4-gram, so BLEU-4 collapses to ≈0 irrespective of correctness. BLEU-2 retains some word-order sensitivity while remaining computable. By the same reasoning, an answer with zero clipped unigram matches is assigned exactly 0 rather than the positive floor smoothing alone would award, since a smoothing artefact reads as partial credit an unrelated answer has not earned. Empty answers are left blank rather than scored 0, so missing data is not confused with a genuine zero.

BERTScore-F1. roberta-large embeddings with rescale_with_baseline = True, run on GPU. Baseline rescaling is applied because raw BERTScore compresses all English sentence pairs into roughly [0.85, 1.00]; rescaling subtracts an empirical baseline to spread scores across a readable range, at the cost of admitting small negative values for answers less similar than two random sentences (3–17 cells per model). Text is passed through unmodified — no lowercasing or punctuation stripping — since the encoder handles casing natively. Empty answers left blank.

LLM-as-a-judge (Claude Sonnet 5). Each (item, model) pair was graded by a single, freshly spawned, stateless sub-agent seeing only a fixed rubric, that item's reference answer, and that one model's answer — never the row index, the filename, other rows, other models' answers, other models' judgments, or any corpus-level statistic. The rubric was byte-identical across all calls, defining the three labels in terms of semantic equivalence, completeness, and contradiction, and requiring a bare label as the entire output. Batching multiple comparisons into one call was disallowed: one call, one comparison, ≈1,600 calls.

The judge was explicitly instructed to treat the reference answer as ground truth even where it appeared factually questionable, so that it measures agreement with the reference field rather than real-world truth. Cells resolvable deterministically (empty answer against a non-empty reference → Wrong) bypassed the judge; cells with an empty reference and a non-empty answer were flagged rather than guessed. All returned labels were validated against the three permitted strings (0 malformed returns). As with the Claude elicitation run, absence of retrieval is evidenced by tool_uses: 0 on every call rather than by a structurally tool-free sandbox — the minimal-overhead sub-agent type used still carries file tools in its schema — so this too is a behavioural, not infrastructural, guarantee. Writes used a real CSV parser with atomic replacement, timestamped backups, and post-write verification that every non-judge field was unchanged.

3.4 A data-integrity defect, reported rather than repaired

One defect surfaced during scoring and is disclosed rather than quietly fixed. A single row (question_id 35) contained an unquoted comma inside one model's answer, yielding 26 fields against a 24-column header and silently shifting every downstream column for that row — meaning earlier reads of that row saw the wrong reference answer and the wrong per-model answers. The source quoting was corrected and all 400 rows verified to parse to exactly 24 fields before that row was re-scored.

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4. Results

4.1 Overall accuracy

Figure 1. Strict human-annotated accuracy over all 400 items. Error bars are 95% Wilson score intervals.

Table 2. Overall accuracy by model (human annotation, n = 400).

Model	Right	Partial	Wrong	Strict accuracy	95% CI	Partial-credit
GPT-5.6-sol	258	9	133	64.5%	[59.7, 69.0]	65.6%
Claude Opus 5	214	6	180	53.5%	[48.6, 58.3]	54.2%
Gemini 3.5 Flash-Lite	214	6	180	53.5%	[48.6, 58.3]	54.2%
Gemma 4 31B	145	11	244	36.2%	[31.7, 41.1]	37.6%

GPT-5.6-sol leads by a margin exceeding interval overlap with the next tier (Δ = 11.0 pp). Claude Opus 5 and Gemini 3.5 Flash-Lite are indistinguishable — identical marginal counts, and identical labels on 332 of 400 individual items — while the open-weight Gemma 4 31B trails the leader by 28.3 pp. Partial-credit scoring shifts every model by at most 1.4 pp and preserves the ordering exactly.

These aggregates are the least informative quantity the benchmark produces. Each is a near-arithmetic mean of two radically different regimes, which the next subsection separates.

4.2 The contamination gap

Figure 2. Strict accuracy on the official subset (Red, Crystal; n = 200 per model) versus the fan subset (Brown, Prism; n = 200 per model), ordered by gap size. Error bars are 95% Wilson intervals.

Table 3. Per-title accuracy (human annotation, n = 100 per cell; 95% Wilson intervals).

Model	Red (official)	Crystal (official)	Brown (fan)	Prism (fan)
GPT-5.6-sol	100.0% [96.3, 100.0]	100.0% [96.3, 100.0]	29.0% [21.0, 38.5]	29.0% [21.0, 38.5]
Claude Opus 5	97.0% [91.5, 99.0]	93.0% [86.3, 96.6]	8.0% [4.1, 15.0]	16.0% [10.1, 24.4]
Gemini 3.5 Flash-Lite	92.0% [85.0, 95.9]	94.0% [87.5, 97.2]	13.0% [7.8, 21.0]	15.0% [9.3, 23.3]
Gemma 4 31B	60.0% [50.2, 69.1]	61.0% [51.2, 70.0]	8.0% [4.1, 15.0]	16.0% [10.1, 24.4]

Table 4. Pooled subsets (n = 200 each). Odds ratios and p-values from Fisher's exact test on the 2 × 2 Right / not-Right table.

Model	Official	Fan	Gap	Odds ratio	Fisher p
Claude Opus 5	95.0%	12.0%	83.0 pp	139.3	7.5 × 10⁻⁷²
Gemini 3.5 Flash-Lite	93.0%	14.0%	79.0 pp	81.6	7.5 × 10⁻⁶⁴
GPT-5.6-sol	100.0%	29.0%	71.0 pp	∞	6.0 × 10⁻⁶¹
Gemma 4 31B	60.5%	12.0%	48.5 pp	11.2	6.5 × 10⁻²⁵

Three findings follow.

The gap is large and uniformly significant. 48.5 to 83.0 percentage points, with every Fisher test rejecting independence at p < 10⁻²⁴. GPT-5.6-sol answered 200 of 200 official-title items correctly — perfect recall of a first-party corpus — while answering fewer than three in ten fan-title items correctly. This is the signature of memorised text, not of generalised game-mechanical competence: the subsets differ in documentation density, not in reasoning demand.

The leaderboard in §4.1 is largely a ranking of memorisation. On the official subset the three frontier models compress into a 7-point band (93.0–100.0%) that the fan subset does not reproduce. Conversely, Gemma 4 31B's overall deficit is driven almost entirely by the official subset, where it trails by 32.5–39.5 pp, while on the fan subset it is statistically indistinguishable from Claude Opus 5 (12.0% versus 12.0%, identical counts) and from Gemini 3.5 Flash-Lite. The 39.5-point spread separating the four systems on documented titles narrows to 17.0 points on undocumented ones, where the bottom three become mutually indistinguishable (12.0–14.0%) and only GPT-5.6-sol remains separated. A benchmark composed solely of well-documented titles would have reported a model hierarchy that largely dissolves once documentation is removed.

The fan-subset floor is not a provenance artefact. Brown items were written from the first author's own playthrough while Prism items came from vetted community walkthroughs; if authorship were driving the result, a systematic Brown/Prism divergence would appear. None appears in a consistent direction — Brown versus Prism is 29/29 for GPT-5.6-sol, 8/16 for both Claude Opus 5 and Gemma 4 31B, and 13/15 for Gemini 3.5 Flash-Lite — so the first-hand subset is, if anything, marginally harder rather than idiosyncratically easier. Both fan titles sit at the floor regardless of who wrote the questions.

Failure modes are diagnostic. Models rarely abstained on the fan subset; instead they substituted plausible official-canon content for the fan game's actual content. Asked which named tunnel connects eastern Mt. Boulder to its destination in Brown (reference: Rijon Tunnel), GPT-5.6-sol answered Silk Tunnel. Asked what happens on first entering Gravel Town (reference: Professor Tim meets the player and takes them to his laboratory), it answered that the rival forces a battle — the Red/Blue script transplanted into an unfamiliar region. Fan-subset errors are confident confabulations in the register of the franchise, not acknowledgements of ignorance. That is precisely the behaviour that makes contamination-inflated scores hazardous to trust.

4.3 Metric agreement and metric validity

Figure 3. The same 1,600 answers under four scoring regimes. Models are held in descending human-accuracy order in every panel, so any departure from a monotone staircase is a ranking disagreement. Note that the two right panels are similarity means, not accuracies, and are plotted on their own scale.

Table 5. Each regime's aggregate verdict, and rank correlation with human accuracy across the four models.

Model	Human	LLM judge	Judge (partial credit)	BLEU-2	BERTScore-F1	Mean answer length (words)
GPT-5.6-sol	64.5%	53.2%	57.5%	0.291	0.557	7.5
Claude Opus 5	53.5%	49.2%	53.0%	0.157	0.330	19.2
Gemini 3.5 Flash-Lite	53.5%	37.0%	42.9%	0.173	0.455	4.2
Gemma 4 31B	36.2%	25.5%	30.0%	0.140	0.440	5.9
Spearman ρ with human	—	0.949	0.949	0.949	0.632	—

The LLM judge tracks human annotation closely but is systematically stricter

Pooled over all 1,600 comparisons, exact three-way agreement is 86.1% (Cohen's κ = 0.750; linearly weighted κ = 0.820; κ = 0.775 on the collapsed Right / not-Right decision). Per-model agreement ranges from κ = 0.857 on Claude Opus 5 (92.2% exact) down to κ = 0.671 on Gemini 3.5 Flash-Lite (81.2% exact) — agreement is weakest precisely where answers are terse, which is where semantic equivalence is hardest to adjudicate from surface text.

The disagreement is directional rather than symmetric. Of 831 cells the human labelled Right, the judge downgraded 176 (112 to Partially Right, 64 to Wrong), while upgrading only 5 cells in the other direction.

Table 6. Pooled human × judge confusion matrix (n = 1,600).

Human ↓ / Judge →	Right	Partially Right	Wrong
Right	655	112	64
Partially Right	2	12	18
Wrong	3	23	711

Consequently the judge understates every model's accuracy by 4.3–16.5 pp and inflates the Partially Right rate roughly fourfold (7.5–11.8% versus 1.5–2.8%). It nonetheless preserves the leaderboard (ρ = 0.949) and, notably, breaks the Claude/Gemini tie that human annotation leaves unresolved, separating them by 12.2 pp. Its per-title readings reproduce the contamination gap without qualitative change (for GPT-5.6-sol: 91%/90% official versus 13%/19% fan).

Spot-checks of disagreements found genuine borderline cases on both sides — the judge occasionally penalising a correct answer for volunteering surrounding context, the human occasionally crediting a near-miss. We therefore report the judge as a conservative, well-correlated lower bound on human accuracy rather than a drop-in replacement, and record its verdicts as returned without manual override.

The surface-form metrics are diagnostically weak, and BERTScore is misleading in aggregate

As single-cell classifiers of human correctness, both metrics are only moderately discriminative: pooled ROC-AUC is 0.711 for BLEU-2 and 0.791 for BERTScore-F1, with point-biserial correlations against the human Right indicator of r ≈ 0.40–0.42 (BLEU) and 0.43–0.58 (BERTScore). Mean scores separate correct from incorrect answers in the expected direction (BLEU 0.25–0.40 versus 0.04–0.10; BERTScore 0.43–0.68 versus 0.21–0.34), but the distributions overlap heavily.

Two mechanisms explain the weakness, and both follow from the domain's short references rather than from incidental noise.

Formatting sensitivity in BLEU-2. With references of median length 3 tokens, one token of surface divergence can zero the score. Correct answers scored exactly 0 include Flash against Flash., Pokédex against The Pokédex., Rock against Rock-type Pokémon., and Boulder Badge against The BoulderBadge. The fraction of human-correct answers assigned BLEU-2 = 0 is 43% for Gemini 3.5 Flash-Lite, 36% for Gemma 4 31B, 17% for GPT-5.6-sol, and 3% for Claude Opus 5. That ordering follows verbosity, not correctness: terse models are penalised hardest, because a one-word answer has almost no opportunity to match a determiner or trailing noun phrase. Any threshold on BLEU-2 would encode a preference for reference-matching phrasing rather than for accuracy.

Length bias in BERTScore. Answer length correlates negatively with BERTScore-F1 at r = −0.454 pooled, and at r = −0.575 when restricted to answers the human marked correct — the penalty is strongest exactly where it is least warranted. Within-model, the effect reaches r = −0.710 for Claude Opus 5 and r = −0.681 for GPT-5.6-sol among their correct answers. Claude Opus 5 is the clearest casualty: its mean answer is 19.2 words against a 4.62-word reference, and 71% of its human-correct answers score below 0.5. A correct response such as "Brock gives the player TM34 (Bide) after being defeated at the Pewter City Gym" scores 0.210 against the reference "TM34, Bide."

The aggregate consequence is a reversal, not mere attenuation: BERTScore-F1 ranks Claude Opus 5 last of the four models (0.330) despite its tying for second on human annotation — which is why its rank correlation with human accuracy (ρ = 0.632) is the only one falling materially below the others. This bias is partly pipeline-induced, since the Gemini and Gemma runners strip fences, quote marks, and Answer: prefixes while the Claude runner preserved raw output verbatim (§3.2). It should be read as an artefact of the metric–domain mismatch, not as a property of the model.

The contamination signal survives every regime

Encouragingly, both surface metrics recover the contamination gap qualitatively even though neither is trustworthy for ranking: mean BLEU-2 and BERTScore-F1 are 2.5–5.5× and 1.5–2.0× higher respectively on the official subset than on the fan subset, for every model. The central finding of §4.2 is thus robust to the choice of scoring regime — it appears in all four independently — whereas the leaderboard of §4.1 is not.

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5. Discussion

Aggregate benchmark scores on well-documented domains should be treated as upper bounds contaminated by recall. The four models here span 28.3 points overall, but that spread is manufactured by the official subset. On material the corpus does not contain, three of the four systems land within 2 points of each other at the floor. Any capability claim resting on a single documented-domain number is, on this evidence, substantially a claim about training-data coverage.

Paired documentation-density contrasts are cheap to build and hard to game. The manipulation here required no access to training data, no string matching, and no model internals — only two matched item sets differing in corpus footprint. Many domains admit the same construction: canonical versus obscure case law, popular versus long-tail library APIs, widely-covered versus locally-reported events. We suggest this belongs in benchmark design as a default, reported alongside the aggregate rather than in place of it.

Confabulation, not abstention, is the failure mode. Models did not decline on unfamiliar material; they generated fluent, in-register, wrong answers drawn from the documented sibling domain. A benchmark that only measures accuracy will record this as a wrong answer among others, but for deployment the distinction matters: a system that fails loudly is safer than one that fails in the voice of an expert.

Metric choice is a substantive research decision, not a formality. The same 1,600 answers yield four different verdicts, and one of the four inverts the ranking for a purely mechanical reason. Where answers are short and answer-length distributions differ across systems, embedding similarity measures verbosity as much as correctness. A stateless single-comparison LLM judge was, on this data, the only automatic regime that both preserved the human ranking and reproduced the contamination gap.

6. Limitations

1. Single annotator. Human labels come from one annotator, with no second pass and therefore no inter-annotator agreement estimate. Spot-checks during the judge analysis surfaced cases where the human label was itself arguable, so the primary metric carries unmeasured noise. A second independent annotation pass on a stratified sample is the obvious next step.
2. Behavioural, not structural, retrieval guarantees for two components. The Claude Opus 5 elicitation run and the LLM judge both ran in environments where tool access could not be disabled by parameter. Both rest on tool_uses: 0 in usage metadata across all calls — strong evidence, but not the infrastructural guarantee the GPT, Gemini, and Gemma pipelines provide.
3. Asymmetric answer post-processing. Two pipelines strip fences, quotes, and answer labels; two do not. This does not affect human or judge labels, which are semantic, but it does contaminate cross-model comparison of BLEU and BERTScore.
4. One franchise, one era, one question type. All items are short-answer factual questions about Game Boy–era Pokémon. Whether the gap magnitude generalises to other domains, longer-form answers, or reasoning-heavy tasks is untested here.
5. Documentation density is inferred, not measured. We treat official titles as heavily documented and ROM hacks as sparsely documented on strong circumstantial grounds, but we did not quantify either subset's presence in any specific training corpus. The contrast is real; its exact magnitude in the training data is unknown.
6. Fan-game questions may carry unmeasured difficulty. Although the Brown/Prism comparison rules out a provenance artefact, it cannot rule out that fan-game items are intrinsically harder in some way orthogonal to documentation.

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Appendix A. Reproducibility notes

Component	Setting
Items	400 (100 each: Red, Crystal, Brown, Prism)
Reference answer length	median 3 tokens, mean 4.62, SD 3.58, range 1–21
Answer cells scored	1,600 (4 models × 400 items)
GPT-5.6-sol	Chat Completions API, no tools, provider default sampling, 400/400
Gemini 3.5 Flash-Lite	generateContent, no tools field, temp 0.0, maxOutputTokens 2048, 400/400
Gemma 4 31B	Ollama /api/generate, gemma4:31b-cloud, temp 0.0, seed 0, 398/400
Claude Opus 5	400 isolated sub-agents, tool_uses: 0 verified on all, 400/400
BLEU-2	n ∈ {1,2}, weights (0.5, 0.5), Chen & Cherry method-4 smoothing, zero-unigram → 0
BERTScore	roberta-large, rescale_with_baseline=True, GPU
LLM judge	Claude Sonnet 5, 1 call per comparison, byte-identical rubric, ≈1,600 calls, 0 malformed
Confidence intervals	Wilson score, 95%
Significance tests	Fisher exact (two-sided) on 2 × 2 Right / not-Right
Agreement statistics	Cohen's κ (unweighted, linear-weighted, binary-collapsed)

Figure files. fig1_leaderboard.{png,pdf}, fig2_contamination_gap.{png,pdf}, fig3_metric_disagreement.{png,pdf}. Plotting script: make_figures.py.