Small, Diverse Training Sets for Cross-Market Wash-Trading Detection

Wash trading means trading with yourself, or within a ring of colluding accounts, so that an asset looks more liquid and popular than it is. Detectors for it are built one market at a time: one for Solana memecoin launches, one for Ethereum stablecoin wallets, one for NFT sales. Each is trained on that market's full, enormous transaction log. Manipulators move between markets quickly, and a detector that has learned "what Pump.fun scams look like" may only have learned Pump.fun. This note proposes testing a specific bet. A detector trained on a deliberately small set of examples, chosen to cover the widest range of collusion structures across several markets, will catch manipulation in a market it has never seen better than a detector trained on everything available.

The intuition comes from work outside finance. Small curated subsets of instruction data beat the full datasets they were drawn from. Mixing many data sources matters more than raw token count when models must generalize zero-shot. The finance literature has never run this test. Its datasets are siloed by chain and venue. Its labels are produced by rules or weak classifiers of uneven reliability. Its logs are dominated by repetitive benign trades. The deliverable is a market-agnostic representation of trading behavior, a selection procedure that picks training examples for structural coverage and label reliability, and a leave-one-market-out benchmark that measures whether diversity transfers when volume does not.

Core Claim

The claim has three parts.

First, if every entity is described by features that mean the same thing in any market, then a training set chosen to cover that shared feature space generalizes better to a held-out market than the pooled full data. Examples of such features are how concentrated an account's trading is on few counterparties, how much of its volume returns to it through short loops, and whether its wallets share a funding source.

Second, the selected set will typically be 5–20% of the pool.

Third, the gain comes from covering the space of collusion structures, not from simply rebalancing the mixture of markets. The experiments are designed to separate these two explanations, because the second one is a cheap alternative that might explain everything.

A secondary and more tentative hypothesis concerns noisy labels. Admitting examples in order of label reliability, starting with clean, unambiguous reciprocal wash trades and adding fragmented multi-wallet bundles later, may help a neural detector cope with the noisy labels these datasets carry. We expect this to matter less than diversity and treat it as an ablation, not the headline.

Why this is open

The motivating evidence comes from three groups of work.

The finance datasets show the siloing. MemeTrans builds 41,470 Solana memecoin launches with 122 features. It labels risk with statistical filters plus a temporal convolutional network, and it groups sybil wallets by tracing atomic transactions, funding flows, and bundled block submissions. StableAML engineers 68 behavioral features from USDT/USDC transfer logs on Ethereum. The Dark Side of NFTs finds round-trip, unprofitable, and hidden wash trades across 285 NFT collections using deterministic cycle and rule detection. None of the three tests a model outside its own market.

A second pair of papers supplies the market-agnostic signals we reuse as features. Degree-Strength Correlation Reveals Anomalous Trading Behavior shows that colluding equity traders have high trade counts concentrated on few counterparties, a strength-to-degree ratio more than 3 standard deviations above a shuffled null. Crypto Wash Trading shows that fabricated volume violates Benford's law and natural trade-size clustering. Both signals are defined on any trade log, which is what makes a shared representation possible.

The selection method comes from language-model data curation. SHED clusters instructions and values cluster representatives with approximate Shapley values. With it, a 4,000-example subset reaches 35.92% versus 33.16% for the full 70k WizardLM set. An Experimental Design Framework for Label-Efficient Supervised Finetuning uses facility location, a selection objective that rewards picking examples so every point in the pool has a close representative. It matches 90k random prompts with 45k selected ones. That paper also warns that pure uncertainty selection piles onto redundant clusters of the same ambiguity, which constrains our design toward coverage over uncertainty. DART-Math shows that unweighted selection develops an easy-example bias. This is why our selection stratifies by difficulty: in a manipulation log, the hard fragmented cases are the rare ones.

The diversity evidence comes from What Language Model to Train if You Have One Million GPU Hours? and Transfer Learning for Health-related Twitter Data. Both found that multi-source mixtures generalize better than larger single-source ones. Neither involves adversarial data, extreme class imbalance, or graphs.

One result constrains the design directly. StableAML reports that CatBoost (Macro-F1 0.9775) far outperforms GraphSAGE (0.8048) on its sparse graph. We therefore do not assume a graph neural network. The base detector is a gradient-boosted tree, with a small neural network only where the curriculum ablation requires one.

The curriculum ablation draws on Self-Paced Learning for Latent Variable Models. Self-paced learning admits low-loss examples first and anneals toward harder ones, and that paper shows it avoids bad local minima: it got stuck once versus 18 times out of 100 for the standard optimizer on motif finding. Its relevance here is as a defense against label noise, not optimization difficulty, and we say so explicitly.

Research Program

Shared representation. For each market we rebuild the trade graph from raw transfer events and define the unit of prediction as an entity. An entity is a wallet cluster grouped by shared funding source and same-block co-submission, the MemeTrans bundle-tracing procedure applied uniformly, or a single account where no grouping is possible. Each entity gets the same feature vector everywhere:

  • the strength-to-degree z-score against a degree-preserving shuffled null;
  • reciprocity;
  • the fraction of volume returning within 2- to 5-hop loops;
  • funding-source concentration;
  • timing burstiness;
  • round-size and first-digit deviation statistics;
  • the share of volume carried by the entity's top counterparty.

Market-specific fields such as bonding-curve state or marketplace fees are deliberately excluded from the shared vector. They are kept in a second vector so we can measure how much in-market accuracy is lost by excluding them.

Labels and reliability. The label is "coordinated manipulative entity." MemeTrans gives high-risk launch labels whose bundled wallets we treat as positives. NFT gives rule-derived wash-trading groups. StableAML gives cybercrime/blocklisted wallets, a related but different behavior that we use as a far-transfer target. Each source gets a reliability tier. Hard rule matches, such as closed NFT round trips, are high reliability. Labels from MemeTrans's temporal classifier are lower reliability.

One leakage risk must be handled. The NFT labels come partly from cycle detection, and the loop-fraction feature would simply rediscover the rule. When NFT is the target we therefore evaluate on the unprofitable and hidden-trading labels and report results with and without loop features. The 2004 Chinese equity network contains only 8 manipulated stocks, so it serves as a zero-shot sanity check, not a training source.

Selection. From the pooled training markets we pick a budget of $B$ entities by maximizing a facility-location objective over the shared features. Selection runs within strata defined by class, reliability tier, and difficulty, where difficulty is the out-of-fold loss of a cheap probe model. Within each stratum we optimize

$$F(S)=\sum_{i \in P}\max_{j \in S}\,\mathrm{sim}(x_i,x_j),$$

where $P$ is the pool, $S$ the selected set with $|S| \le B$, and $\mathrm{sim}$ an RBF kernel on standardized feature vectors $x$. Greedy maximization is cheap once background trades are first summarized into k-means prototypes, which addresses the scoring-cost concern raised for million-scale logs. A SHED-style variant, which values clusters by their marginal effect on validation loss in other source markets, is run as an alternative selector.

Baselines

The naive reference point is the in-market detector. CatBoost is trained on the full target market with its full native feature set, as StableAML did. It shows how much a detector loses by never seeing the target market, and it is an upper bound that we do not expect to beat. The reported anchors are Macro-F1 0.9775 for CatBoost on StableAML (StableAML), MemeTrans's MLP cutting simulated top-100 investment loss from 60.7% to 26.6% (MemeTrans), and AMAP's AUC-ROC of 0.9678 on the AliPay M12 data (AMAP). We reproduce the first two on our splits before comparing. There is no reported result on Lacuna for any cross-market wash-trading transfer, so our zero-shot numbers will be the first.

The strongest real competitor is pooled CatBoost: all training markets concatenated, using the shared features, with class weights. Many teams would ship this. It has the same feature vector and the same tuning budget as our method: 50 random-search trials, tuned on a validation split drawn from the training markets only, never from the target. Beating it means higher area under the precision-recall curve (AUC-PR, the right metric under extreme class imbalance) on the held-out market. The gain must hold in at least three of four leave-one-out folds, with bootstrap intervals that exclude zero.

A second strong competitor is market-balanced pooling. This is pooled CatBoost reweighted so each market contributes equal total weight, plus a random subsample at the same budget $B$ as our selection. This baseline isolates the key ingredient. If it matches our selector, the benefit was the mixture ratio and not structural coverage.

The remaining baselines are:

  • the largest single source market trained alone, which is the "more of one market" counterfactual;
  • pure uncertainty selection at budget $B$;
  • difficulty-only selection, taking the hardest $B$ by probe loss, which is the DART-Math intuition without coverage;
  • the degree-strength z-score rule of Degree-Strength Correlation Reveals Anomalous Trading Behavior applied with no training at all, the strongest training-free transferable detector.

For the secondary hypothesis, the comparison is self-paced ordering against random ordering and against simply dropping low-reliability labels. All three use the same MLP, data, and number of epochs.

Why not just…?

Why not just pool every market and let boosted trees sort it out? This is the most serious threat. Tree ensembles are robust to irrelevant mass and already win in this domain. The pooled and market-balanced CatBoost baselines exist to settle it. If balanced pooling at full size matches the selected subset on held-out AUC-PR, we will report that the useful lesson is "mix markets," not "select for coverage," and the selection machinery will have failed its test. Our reason to expect a gap is that pooled logs are dominated by near-duplicate benign trades and by the easiest positives. Both DART-Math and SHED show this kind of skew hurting even when all the data is present. But this is an empirical bet, not a known result.

Why not just use the degree-strength statistic, which already transfers? It does transfer, and it is a baseline. It flags concentrated trading but misses wallets that split activity across fresh addresses. MemeTrans found that true holding concentration is 24% higher than nominal precisely because of this splitting. So we expect the rule to lose most on the memecoin fold. If it wins on the equity and NFT folds, that is informative, and we will report it per fold.

Why not just use uncertainty-based active selection? On language data, An Experimental Design Framework for Label-Efficient Supervised Finetuning found that uncertainty selection collects redundant clusters. In this domain the uncertain cluster is likely to be a single noisy labeling artifact, such as borderline launches from MemeTrans's weak classifier. We run uncertainty selection at the same budget and also report the fraction of its picks that fall in low-reliability tiers, which directly tests this explanation.

Why not just use a graph neural network over the joint graph? The networks are disjoint across chains, and StableAML's 0.8048 versus 0.9775 result argues against message passing on graphs this sparse. Our features already encode the multi-hop structure that a graph network would compute.

Proposed Experiments

The main experiment is leave-one-market-out over the memecoin, NFT, and stablecoin markets, with the equity network as a zero-shot fourth check. We sweep the budget $B$ from 1% to 100% of the pooled pool and plot held-out AUC-PR against $B$ for each selector. The decisive pattern for the core claim has three parts. First, the coverage selector peaks at an intermediate budget above the full-pool value. Second, at matched budget it beats balanced random subsampling. Third, it beats the largest single market trained on all of its data.

Two controls test the mechanism. In the first, we hold total size fixed and vary the number of source markets from one to three. If diversity is the driver, held-out AUC-PR should rise with source count at fixed size. In the second, we measure how much of the target market's feature space is covered by the training set: the mean distance from each target entity to its nearest selected training example. If coverage is the mechanism, this distance should predict transfer AUC-PR across selectors.

A temporal check matters because scam tactics shift. MemeTrans spans December 2024 to March 2025, so we train on the early months and test on the last month, with and without other markets in the training pool. The question is whether diversity across markets also buys robustness to drift within a market.

The curriculum ablation runs only on the MLP, comparing self-paced ordering, random ordering, and filtering out low-reliability labels. It counts as a positive result only if self-paced ordering beats simply discarding low-reliability labels. Otherwise we report that curriculum adds nothing over cleaning the data.

Every result is reported per fold with bootstrap intervals, alongside the in-market upper bound. The size of the remaining gap to in-market performance is itself a finding about how much manipulation looks the same from one market to the next.