Ranking the true answer among 25 look-alikes: calibration and re-ranking tricks from differential diagnosis, transient astronomy, eDNA taxonomy and open-set recognition, applied to the CASMI 2026 open-set problem

TL;DR. Four unrelated fields solve "rank the truth inside a short candidate list", and each has a published trick worth stealing: a context prior (host-galaxy features alone separate supernova types at ~70 % accuracy; a biological-source prior lifts rank-1 natural-product annotations from 10.2 % to ~72 %), a hubness correction (CSLS adds +2.1 to +6.5 precision@1 points on word translation), bootstrap-over-features confidence (IDTAXA mis-assigns 0.01 % of sequences whose genus is missing from the reference, against 17.3 % for a BLAST top hit), and an explicit "none of the above" training class (BirdCLEF 2024 winner: private score 0.655 → 0.671). The Morelli hypothesis survives contact with the MS/MS literature: every optimised intensity exponent published since 1994 is below 1 (0.25–0.6), and Li et al. show why — ADP and ATP share the adenine base peak and differ in the small ions. The silent killer for us is the opposite lesson: the single largest published re-ranking gain in metabolite ID (MetFrag, ~6 % → 89 % top-1) comes from literature-reference counts, a prior that is actively inverted on a test set defined as never previously published.

1. Five systems that rank a true answer among look-alikes

Machine-readable version of this table: healthcare_diagnosis_astronomy_ecology_other_rank_25_problems.json.

2. What each field does when the answer is not in the reference — and what we can actually do

The structural asymmetry is the whole lesson. Every field surveyed is rewarded for saying "unknown"; we are not permitted to. So the import from IDTAXA and OpenMax is not the abstention step — it is the detector that precedes it. Their contribution is a calibrated signal "the truth is probably not in my reference", which for us becomes a routing decision, not an output.

3. Hubness and popularity bias in nearest-neighbour retrieval

Radovanović, Nanopoulos & Ivanović (JMLR 11:2487, 2010) define hubness as right-skew in the distribution of k-occurrences N_k — how often a point appears in other points' k-nearest-neighbour lists. Across 50 real data sets the Spearman correlation between embedding dimensionality and the standardised skewness S_N10 is 0.62, and the correlation with intrinsic dimensionality (maximum-likelihood estimator) is stronger still; shuffling features to destroy dependencies raises skewness further, which is their evidence that hubness tracks intrinsic rather than embedding dimension. They separate N_k into "good" and "bad" k-occurrences by label agreement, and show that down-weighting a point's vote by exp(−h_B), where h_B is its standardised bad-hubness score, raises leave-one-out k-NN accuracy on six real data sets (their Fig. 11 — the deltas are plotted, not tabulated, so I cannot quote a number). Schnitzer et al. (JMLR 13:2871, 2012) report mutual proximity raising k = 5 accuracy on Corel-1000 from 65.2 % to 70.3 % (taken from the authors' project page, not the PDF — medium confidence).

CSLS (Conneau et al., ICLR 2018, arXiv 1710.04087) is the cheapest fix and the one with the cleanest numbers:

CSLS(Wx_s, y_t) = 2·cos(Wx_s, y_t) − r_T(Wx_s) − r_S(y_t), with K = 10

where r_T is the query's mean cosine to its K nearest gallery items and r_S is the gallery item's mean cosine to its K nearest queries. The paper's framing is exactly ours: "some vectors, dubbed hubs, are with high probability nearest neighbors of many other points, while others (anti-hubs) are not nearest neighbors of any point."

Gain from CSLS alone: +2.1 to +6.5 P@1 points in the supervised setting, largest on the hardest pairs. A 2026 preprint (arXiv 2605.26575) argues hubness rather than anisotropy drives cross-lingual retrieval asymmetry — hub mass carries a 49.5 % dominance share and partial R² 0.302 against 0.003 for anisotropy — and that CSLS closes 63.5 % of the worst-to-best reciprocity gap.

Nothing comparable has been published for spectrum→structure embeddings. I searched and did not find hubness or CSLS treatment in DreaMS, SpecBridge, FLARE or the contrastive spectrum-embedder literature; that is a genuine gap, and the experiment is a few lines of code. The mapping: queries are the ~1,500 hidden-test spectrum embeddings, the gallery is the candidate-structure embedding set, and r_S must be estimated against a query bank (the test spectra plus, say, 50,000 random training spectra) because the gallery outnumbers the queries by orders of magnitude. The predicted hubs are structurally generic molecules — simple flavonoid glycosides, small terpenoid acids — whose predicted-fingerprint vectors sit near the data mean, which is precisely Radovanović's mechanism. My honest expectation of the size of the effect here is small, because the per-molecule exact-mass window already reduces each ranking problem to isomers of one formula, and hubness is a global-neighbourhood pathology. The place to look for a real gain is inside the largest isomer families, where several hundred candidates compete and one or two of them are everybody's nearest neighbour.

4. Morelli secondary test: are the quiet peaks the informative ones?

Morelli attributed paintings from earlobes and fingernails on the theory that a copyist reproduces the celebrated features and betrays himself in the unconsidered ones. The mass-spectrometric translation: the base peak is the celebrated feature — a stable heteroatom ring, a dominant neutral loss — shared across an entire structural family, while the low-abundance ions carry what separates its members. Li et al. 2021 assert this directly: "highly abundant MS/MS fragment ions are often shared between structurally similar molecules … ADP and ATP both showing the adenine fragment m/z 136.062 as base peak. Hence, the difference between highly similar structures may best be discerned from low-abundant ions."

4.1 Evidence table: intensity transforms and what they were shown to do

Verdict on the analogy: it holds, with a measured boundary. Every optimised exponent published since 1994 is below 1, which is the quantitative form of "attend to the quiet peaks". But Li et al. located the point where it reverses — in ion-rich, high-entropy spectra, amplifying small peaks amplifies noise instead of signal. Nobody has published the extreme Morellian version (delete the base peak; use only sub-10 % peaks) as an identification experiment, only as similarity-metric tuning. That is the gap worth filling, and it is cheap.

4.2 Proposed MRR@25 experiment

Hold-out construction. From train.parquet, select molecules whose Bemis–Murcko scaffold appears nowhere else in the training set (scaffold-disjoint), whose molecular formula has at least 20 isomers in the candidate pool, and which carry at least 3 spectra. Target ~2,000 molecules. Keep the true structure in the pool for this experiment — this test is about ranking, not coverage. Mimic the hidden-test distribution where possible: timsTOF rows, merged multi-collision-energy spectra, the 7 permitted adducts.

Arms. Score every pool candidate with the identical ranker under: (i) full spectrum, relative intensity; (ii) base peak deleted — and for merged multi-CE spectra, the surviving precursor ion deleted as well; (iii) only peaks below 10 % of base; (iv) I^0.5, I^0.25, and log(1 + 100·I); (v) the entropy-dynamic rule w = 0.25 + 0.25·S capped at S = 3; (vi) two-stage: full spectrum to shortlist 100, then re-rank that shortlist by arm (iii).

Reporting. MRR@25 and recall@25, stratified by spectral entropy (S < 1.5 / 1.5–3 / > 3), by isomer-family size, and by number of spectra per molecule. Report paired bootstrap confidence intervals over molecules, not spectra.

Prediction, stated before running it. Arms (iv) and (v) win overall and land within ~0.01 MRR of each other; (i) is a few points behind; (ii) is roughly neutral for S < 1.5 and clearly harmful above, because the base peak in a merged multi-CE timsTOF spectrum aggregates several genuinely informative channels; (iii) alone loses badly on MRR but wins the tie-break inside large isomer families, which is why (vi) is the arm to watch. If (vi) beats (iv) by more than 0.01 MRR, Morelli is confirmed for this data and the production ranker should be two-stage. If (iii) alone lands within 0.02 of (i), the base peak is carrying far less identity information than intuition suggests, which is itself a publishable negative result for the write-up.

5. How much does a prior actually buy in metabolite identification?

6. Forced analogy: art attribution and the Rembrandt Research Project

The analogy, stated precisely. The Rembrandt Research Project's Corpus (Bruyn, Haak, Levie, van Thiel, van de Wetering, from 1982) sorted paintings into three categories: A, by Rembrandt; B, authorship neither securely accepted nor rejected; C, not by Rembrandt. Two well-known verdicts moved when evidence of a different kind arrived. For The Polish Rider (Frick Collection), Josua Bruyn of the project suggested in 1984 that characteristics of Rembrandt's pupil Willem Drost could be seen in it; that view did not hold, Ernst van de Wetering argued for Rembrandt at the 1997 Melbourne symposium, and a 1998 project study concluded that a second hand had worked on the painting alongside Rembrandt — the doubt resolved into "Rembrandt, plus a collaborator", possibly a canvas he left unfinished. For The Man with the Golden Helmet (Gemäldegalerie Berlin), a Dutch curators' commission raised doubts in 1984, Jan Kelch announced a stylistic mismatch in November 1985, and in 1985–86 the Doerner Institut in Munich examined the painting by autoradiography, infrared and ultraviolet photography, X-radiography and paint-sample analysis, after which the museum concluded it was by someone in Rembrandt's circle rather than by Rembrandt. (Whether the project itself issued a formal C is not established by the sources I opened.)

The mapping to our problem: connoisseurial style corresponds to learned similarity — predicted fingerprints, contrastive spectrum–structure embeddings, library cosine. Technical examination corresponds to hard physical constraints, and the important property is that they are orthogonal to the learned score rather than better than it: the neutral mass implied by each of a molecule's 1–16 spectra under its own adduct, agreeing to within a few ppm; the ring-and-double-bond equivalent and element counts of the candidate formula; the fraction of total ion current assignable to subformulas of the candidate; whether fragment formulas stay consistent as collision energy rises. Dendrochronology cannot tell you who painted a panel — it can only tell you the wood was felled too late. Exact mass is the same kind of evidence: it excludes, it does not attribute.

The derived, testable idea: an A/B/C triage with an explicit routing rule.

Per-molecule features, all computable without knowing the answer:

1. a COSMIC-style calibrated top-1 score — the top candidate's score expressed as an e-value against the score distribution of that molecule's own candidate pool, so molecules with 12 and 1,200 candidates are comparable;
2. the score gap from rank 1 to rank 2, and from rank 1 to the median of the top 25;
3. RDP-style bootstrap stability — resample 1/8 of the peaks 100 times, re-rank, record how often the same candidate stays top-1;
4. an energy-style openness score, log Σ exp(s_i/T) over the top 25 unnormalised candidate scores, following Liu et al.'s point that softmax normalisation destroys exactly the magnitude information that separates in-distribution from out-of-distribution inputs;
5. explained intensity — fraction of total ion current the top candidate can account for by subformula assignment;
6. cross-spectrum agreement — whether the molecule's several spectra independently rank the same candidate first.

Tiers and routes. A — ranker output is kept as-is; the submission's 25 are the top 25. B — keep the top 25 but diversify the tail: the bottom 10 slots are filled by maximal-marginal-relevance over scaffolds rather than by score, on the symptom-checker logic that a near-duplicate in slot 18 buys nothing. C — the top 3–5 pool candidates are retained as insurance, and the remaining ~20 slots are filled from the generative branch: analogs of the best library hit generated by mass-difference rules consistent with the inferred formula, filtered by NP-likeness, de-duplicated by InChIKey14 after RDKit 2026.03.3 tautomer canonicalisation.

Proposed thresholds. Because the quantity we care about is a rate, set the thresholds by quantile rather than by absolute score: calibrate a single scalar triage score (logistic regression on features 1–6, trained on the hold-out described below) and route the bottom ~30 % to C and the next ~25 % to B, since the back-solved public-LB recall@25 of ≈ 0.55 implies roughly 45 % of molecules have no reachable answer. Then tune: the right C fraction is the one that maximises held-out MRR@25, and it should be smaller than 45 % because the generative branch is itself unreliable.

Validation protocol — the part that matters. Build a hold-out of ~1,000 natural products with timsTOF-like spectra and scaffolds disjoint from training. For a randomly chosen half, delete the true structure from the candidate pool, which manufactures exactly the condition we cannot otherwise observe. Report (a) the AUC of the triage score for separating truth-present from truth-deleted molecules — the directly comparable number from another field is OpenMax's F-measure of 0.595 versus 0.568, i.e. open-set detection is hard and the honest expectation is an AUC around 0.7–0.8, not 0.95; (b) MRR@25 with and without routing, separately on the truth-present and truth-deleted halves, because the test of a triage is that it does not damage the molecules it should have left alone; (c) the fraction of truth-deleted molecules for which the generative branch puts the true structure anywhere in the 25 — if this is below a few percent, the C route is not worth its risk and the correct decision is to use the triage only for tail diversification.

Where the analogy breaks — three places, honestly.

First and most importantly, the art historians were allowed to answer "C: not by Rembrandt" and stop. We cannot. A C verdict in our setting is not a conclusion, it is a request for a different generator, and nothing in the art-historical method tells us how to invent the painter. Second, the technical evidence in art attribution is often decisive on its own — a canvas woven after the artist's death ends the discussion — whereas our hard constraints are weak: thousands of COCONUT entries share a formula, so exact mass narrows the field and never closes it. Dendrochronology excludes one candidate; our mass filter excludes 10^7 and leaves 10^2. Third, the RRP had no metric and no cost function. It could spend twenty years on one panel, revise in 1998 what it wrote in 1984, and treat an unresolved B as an acceptable permanent state. We have MRR@25, a fixed submission deadline of 2026-12-14, and a scoring rule under which an honest "uncertain" is worth precisely zero. There is also a sampling caveat worth stating: The Polish Rider and The Man with the Golden Helmet are famous precisely because the verdicts moved, so reasoning from them overstates how often orthogonal evidence overturns a stylistic judgement — the same survivorship trap as reading only the Kaggle write-ups of teams whose trick worked.

Gotchas / what could silently fool us

1. Popularity priors are inverted on this test set. MetFrag's ~6 % → 89 % top-1 gain comes from literature reference counts. The hidden molecules are "none previously published". Any feature correlated with how well-studied a structure is — reference counts, patent counts, PubChem CID low numbers, presence in HMDB/KEGG, number of GNPS spectra, even COCONUT occurrence counts — will push the truth down. A model trained on public libraries will learn this prior implicitly whether or not we add it as a feature; that is the subtle version of the trap.
2. Validating on in-pool molecules measures the wrong thing. Nearly all published top-1 numbers (CSI:FingerID's 74.0 %, RDP's 89 %, GPT-4's 64 %) are closed-set. The eDNA field is the only one that systematically reports the open-set number, and the gap is enormous: RDP looks superb at 98 % precision in-set and forces 3.83 % of absent-genus sequences into a wrong genus, while a BLAST top hit does it to 17.3 % and invents 65 spurious genera. Our analogue of "BLAST top hit" is naive nearest-neighbour library search.
3. Abstention has a coverage price that is invisible in error rates. IDTAXA's near-zero over-classification costs it genus-level coverage (19.9 % versus RDP's 22.5 % of gut reads). Any confidence threshold we introduce trades recall for precision, and MRR@25 only rewards precision at the top. A triage that abstains without a generative branch is strictly worse than no triage.
4. Intensity transforms reverse sign with spectral entropy. Li et al. switch the weighting off above S = 3 because up-weighting small ions in ion-rich spectra degrades scoring. Merged multi-collision-energy timsTOF spectra are ion-rich by construction, so a weighting exponent tuned on single-energy library spectra may be mistuned for the actual test data. Always stratify the ablation by entropy.
5. Isomers set a floor that no amount of weighting removes. In NIST20, roughly 30 % of Li et al.'s false positives at similarity > 0.95 were one-bond isomers and 21.5 % two-bond isomers. Since the metric is InChIKey14 after tautomer canonicalisation, a methoxy on the wrong ring carbon scores zero. Part of our 45 % miss is irreducible from MS/MS alone and is not a modelling failure to be optimised away.
6. Multiple spectra per molecule are not independent samples. With 1–16 spectra (median 3) of the same compound, treating them as independent votes will overstate confidence — the same mistake as counting correlated catalogue cross-matches as independent evidence. Any bootstrap or ensemble confidence must resample at the molecule level.
7. Hubness is a property of the metric, not of a molecule. Correcting it with CSLS changes every score, including the ones that were already right. The 2026 preprint's framing is explicit on this point, and a naive CSLS application can lower P@1 if the query bank is unrepresentative of the test distribution — ours must be drawn from timsTOF natural-product spectra, not from the full heterogeneous training mixture of 82 instrument types.
8. The visible test set is a decoy (verbatim enveda-180 training rows), so any local score computed on it measures memorisation. Every number in this document should be re-derived on a scaffold-disjoint, timsTOF, natural-product hold-out before being believed.
9. Open-set detectors degrade under the exact shift we face. OpenMax's margin over thresholded softmax is 0.595 versus 0.568 — real but small, on a benchmark designed for the task. Expect our truth-absent detector to be mediocre, and design the routing to be robust to a mediocre detector (keep the top pool candidates even in C) rather than betting on a good one.
10. Vendor and secondary numbers leak into the literature. Isabel's "96 % top-10" is a vendor claim; the peer-reviewed numbers for the same class of system are 34 % top-1 / 58 % top-20 (Semigran) and 3.45/5 (Bond). Several intensity exponents in Section 4 (Sokolow, Kim, Horai) reach us through Hart et al.'s compilation rather than from the primary papers. Marked, and not to be quoted as primary.

Implications for the challenge

1. Do not add any popularity or well-studiedness feature (reference counts, patent counts, database occurrence, spectrum counts). Actively audit the existing ranker for an implicit version of it: correlate the model's score on held-out molecules against the number of training spectra for structurally similar compounds, and if the correlation is strong, consider a de-biasing term.
2. Build the truth-absent hold-out this week. ~1,000 scaffold-disjoint natural products; delete the true structure from the pool for a random half. This single artefact is what lets every other idea here be measured, and nothing in the public write-ups suggests other teams have one.
3. Implement the A/B/C triage of Section 6 with the six features listed, thresholds set by quantile and then tuned for held-out MRR@25. Insist on the negative control: routing must not reduce MRR on the truth-present half.
4. Spend the tail slots, not the head slots, on diversity. Slots 1–5 by score; slots 6–25 by maximal-marginal-relevance over Murcko scaffolds for B-tier, and by generated analogs for C-tier. Semigran's data says a list of near-duplicates wastes its length (3 → 20 slots bought 7 points).
5. Adopt the entropy-dynamic intensity weighting (I^w, w = 0.25 + 0.25·S for S < 3, w = 1 above) as the default spectrum preprocessing, and run the arm comparison of Section 4.2 to confirm it on timsTOF merged spectra rather than assuming the NIST20 result transfers.
6. Add bootstrap-over-peaks stability (resample 1/8 of peaks, 100 iterations) as a confidence feature. It is model-agnostic, costs one extra forward pass per resample on the candidate scoring only, and in taxonomy it is the single mechanism that distinguishes "found the right thing" from "found the nearest wrong thing".
7. Use the unnormalised log-sum-exp of the top-25 candidate scores as the openness feature, not a softmax probability (Liu et al.: FPR95 51.04 % → 33.01 % from exactly this change).
8. Test CSLS on the spectrum→structure retrieval step, with the query bank restricted to timsTOF natural-product spectra. Expected gain is small because the formula window already localises each problem, but the published effect in an analogous cross-modal setting is +2 to +6.5 P@1 and the implementation is a few lines. Measure it inside the largest isomer families specifically.
9. Apply NP-likeness only to generated candidates, never as a re-ranker on a COCONUT pool where everything already scores high. Ertl's figure that 93.9 % of natural products absent from the reference dictionary were still called natural products is the evidence it will not systematically reject genuinely novel chemistry.
10. Build the generative C-branch around mass-difference analog enumeration first (methyl +14.0157, hydroxyl +15.9949, acetyl +42.0106, hexose +162.0528, deoxyhexose +146.0579, pentose +132.0423, and their combinations consistent with the inferred formula), because it is cheap, interpretable and directly targets "analogs of known natural products" — the stated chemistry of the hidden set. De novo generation is the second-order option.
11. Report every result with a paired bootstrap over molecules, not spectra, and stratify by isomer-family size. The 400-molecule hidden test means a 0.01 MRR difference is close to noise; do not chase it.

Open questions

1. What is the actual AUC of a truth-absent detector on natural-product MS/MS? No one appears to have published this. COSMIC's AUC 0.82 for correct-versus-incorrect annotation is the closest proxy and is a different question.
2. Does hubness measurably exist in spectrum→structure embedding spaces? Unanswered in the literature I opened. Measuring the skewness S_N10 of the candidate-pool embedding would settle it in an afternoon.
3. What is the ceiling imposed by MS/MS-indistinguishable isomers on a COCONUT-sized pool under InChIKey14 matching? Li et al.'s one-bond/two-bond breakdown (30 % / 21.5 % of high-scoring false positives) suggests it is substantial but is specific to NIST20.
4. Do the per-scheme top-1 numbers in Hart et al.'s supplementary tables show any intensity weighting beating unweighted cosine for exact identification, or only for analog alignment? The main text hints at the latter. Worth pulling the supplement.
5. Would a Sherlock-style deterministic rule layer (hard constraints applied before any learned score, with explicit precedence) outperform feeding the same constraints as features? Astronomy chose rules-first; our field almost always chooses features.
6. Is there any exploitable context prior analogous to Rutz's producing-organism prior — which was worth a 7× F1 improvement — recoverable from the hidden test's metadata (adduct set, collision-energy pattern, which molecules share a submission batch)? If molecules arrived in related batches, that is a weak taxonomic prior in disguise.

Sources

Opened and read (full text or extracted PDF text) unless noted:

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• "The Rembrandt research project." Editorial, Burlington Magazine 1983;125(968):661 (locally extracted text — the Corpus's team authorship, Bruyn and van de Wetering's leading roles, the project's stated aim of establishing a "logical evolution" as the basis for attribution decisions).
• Wikipedia, "The Polish Rider" and "The Man with the Golden Helmet"; rembrandtdatabase.org in-focus article 43 (Doerner Institut 1985–86 autoradiography, infrared, UV, X-radiography and sample analysis; Berlin's "circle of Rembrandt" conclusion). Encyclopaedic and museum-database sources, not primary art-historical scholarship; the A/B/C category definitions and the 1984 Drost suggestion are reported at second hand. The claim that van de Wetering abandoned A/B/C in the later Corpus volumes is my recollection and is NOT verified by anything I opened — treat as unverified.

Not obtained despite trying: the Stein & Scott full text (paywalled), the SINTAX preprint (rate-limited), Kim et al. 2012 Bioinformatics (paywalled; its I^0.53 exponent reaches this document only through Hart et al.), and Hart et al.'s supplementary tables with the per-scheme top-1 precisions.