MemeTrans Explained: What Solana Launch Risk Data Shows

How did the paper decide a launch was “high risk”?

Short answer: By combining a fast price collapse with an automated manipulation score, both measured after migration. It is a rule-based proxy label, not a finding of fraud.

What it means: High risk captures two different failure shapes — a sharp drawdown, or behaviour a detector scores as manipulative — so one label bundles crashes and suspected manipulation together.

Limit: Both inputs are proxies. A 70% drawdown can happen without wrongdoing, and the detector is itself a model. The labels are annotations, not adjudications of any creator or wallet.

Source: Hu et al. 2026, labelling methodology

How many launches ended up labelled high risk?

Short answer: Most of them: Table 8 counts 34,890 of 41,470 migrated launches as High — 84.13% by our arithmetic. Nearby prose in the paper gives 82.44%; we could not reconcile the two.

Discrepancy disclosed: 84.13% follows from Table 8's counts. The paper's surrounding text states 82.44%. We attribute 84.13% to Table 8 only and do not claim either figure is the correct one.

What it means: In this window, a clean post-migration path was the exception. A classifier that always guessed “High” would already be right most of the time, which is why the paper's choice of imbalance-aware metrics matters.

Limit: This is the share meeting the paper's proxy definition among migrated launches in early 2025 — not a universal Solana rug rate, and not a measure of fraud.

Source: Hu et al. 2026, Table 8 and accompanying text

What kind of pre-migration signals did the model use?

Short answer: 122 predictors in five families, all computed from activity before the token migrated. The paper then evaluated how well models recover the post-migration label from them.

What it means: Concentration measured before migration is a position; what drives the outcome is whether those wallets actually sell afterwards. The predictors capture the setup, the label captures what followed. Wallets the paper links together are inferred links, not proof of shared control.

Limit: We have not verified individual feature definitions against the authors' code, and family-level descriptions here are simplified.

Source: Hu et al. 2026, feature construction section

Did complex models beat simple ones?

Short answer: Greater model complexity did not guarantee a better reported score. Of the three individual models shown below, a multilayer perceptron (MLP) scored above logistic regression and a Transformer. Ensembles are not shown.

The benchmark used 21,635 tokens (16,048 High) after excluding launches with a bonding-curve sale shorter than a minute or fewer than 100 holders. It used a random 70/30 split, five-fold cross-validation for training and five runs. Paper, benchmark setup

What it means: Well-chosen tabular signals, not model size, appear to carry most of the information. That is consistent with how practical scanners — including ours — favour explainable signals.

Limit: The split was random, not chronological: tokens from later weeks can train a model tested on earlier weeks. Launch mechanics can change, so out-of-time performance may differ. The table's random AUPRC baseline (0.2589) aligns with the non-high-risk share, not the high-risk share; the positive-class orientation should be checked against the evaluation code before comparing absolute AUPRC values. These are reported values, not our validation.

Source: Hu et al. 2026, Table 9

Would using the model have made money?

Short answer: No — in the paper's simulation both strategies lost money. Picking the model's 100 lowest-risk tokens lost less than picking 100 at random.

Simulated entry at the migration price, with exit at 100 random sale times within the next hour. Paper, Table 12 and simulation description

What it means: The model helped avoid the worst launches, but avoiding the worst still meant losing money on average. “56% less loss” is not “56% profit”, and none of these numbers are MemeAssist returns.

Limit: This is a simulation, not funded, executable performance. We do not assert that fees, slippage or failed transactions were modelled, and no uncertainty interval was supplied for the difference.

Source: Hu et al. 2026, Table 12

Could MemeAssist's own data test the same question?

Short answer: Not as an exact replication today. A read-only audit on 20 October 2026 found a usable outcome ledger, but its fields differ from the paper's in ways that matter.

What it means: We have analysis-time scores tied to later outcomes, which is the right shape for this kind of question. But our saved sub-scores cover six domains (distribution, holder quality, insider risk, liquidity, momentum, whale confidence) plus risk-rule keys — not the paper's 122 raw launch features. Current token reports are overwritten snapshots, so today's raw fields cannot stand in for historical predictors.

Limit: The audited score ledger does not establish coverage of pre-migration transactions, historical linked-wallet clusters, an exact migration anchor, a 20-minute minimum price or execution quotes. Its observations end on 15 September 2026, while scoring snapshots continue to 20 October — this page claims no current validation. Collector startup is controlled by product operating settings, including Product Focus; this audit did not diagnose the runtime cause of the gap. Restarting collection or backfilling is a separate decision, not part of this editorial work.

Source: MemeAssist read-only production aggregate queries, 20 October 2026 (internal audit record).