Auditable alpha research, built to falsify itself.

The live record, redrawn every day

A frozen specification (dea0e608) holds the single best-ranked eligible name and rotates every session. Fetching, selection, scoring and redrawing all run on a GitHub runner from public data, so a reader can rerun it and reach the same name. A separate job re-fetches the index series and fails if any committed benchmark return no longer matches its source; it writes nothing, because a verifier that can rewrite the file it verifies is not a verifier.

Two records run and answer different questions: this one-name, one-session rotation published in advance, and a ten-name, ten-session record (b19bbc74, c0768449) carrying the four factors that survived the 456-candidate search.

The dashed, shaded span on the left proves nothing, and it is drawn that way on purpose. Those four factors were chosen from a 456-candidate search whose data overlaps that window, and on this panel the selection step alone is worth about 3 bps per day — more than most published equity-factor results. An in-sample curve that beats every index is what a selected strategy always looks like.

Only the solid span to the right of the divider is evidence, it begins the day the specification was frozen, and at the start there is almost none of it. The strategy line is a raw return net of realised cost so that it is comparable to an index; the excess line answers a different question and is labelled separately, because plotting an excess against a raw index is the oldest trick in the genre.

The name is published before the session it applies to. Each evening the frozen specification selects one name from roughly 4,700 eligible, and it is committed here with a timestamp, at the top-right of the chart, before that market opens. A record scored afterwards always invites the question of whether the rule moved once the outcome was visible. One committed in advance cannot: it can be shown to be wrong, but never edited. The file is append-only — next_pick.json, published_picks.jsonl, rotation.jsonl.

Research only. This is a record of what a frozen rule selected, published to test that rule in public. It is not advice, not a recommendation, and no order-placement path exists anywhere in the codebase — CI asserts that on every commit.

What the search actually produced

Every factor in four published libraries (Kakushadze 101, GTJA 191, Qlib 158, academic) over a point-in-time A-share panel, ranked only on the training window by the mean excess of a ten-name book, then reported on the untouched test window. 900 sessions split at 2024-12-31, rebalanced every session, ten sessions held, entry and exit at the open after the signal, limit-locked legs dropped rather than priced. Excess is against the equal-weight eligible universe, which returned +0.85% per hold on the test window.

Costs are excluded, and said to be. On an overlapping series three defensible turnover conventions give three different answers, and a gross figure anyone can recompute is worth more than a net one nobody can; at 30 bps a round trip, a book that fully rotates each hold gives back 0.30% of every number above. All 456 rows are published in library_ranking.json.

Selection works, and it is not enough

The number that matters is not in the table. Across all 456 factors, training-window excess predicts test-window excess at Spearman ρ = +0.48 (p < 0.001). Training-side ranking carries real information; anyone calling this pure noise is contradicted by that number. Then look at what it buys.

Choosing cleanly on the training window is worth +0.47 percentage points per hold over choosing at random, and is still negative. The best ten of 456, selected without a glance at the test window, went on to underperform the universe they were drawn from — before a single basis point of cost. That is neither of the two stories usually told: the signal is real, and it is smaller than what decay and concentration take away.

Row 1 is the problem in one line. hml leads the training window by a mile and lands at zero out of sample, while the fifth-placed factor, at a third of its training excess, is the best of the five on test. Ranks are correlated across the full 456 and nearly unrelated at the top — which is exactly where everyone selects. The libraries also contain duplicates: gtja191/alpha_120 and alpha101/alpha_042 are identical formulas published under different names, and this run reproduces them to the digit, so a deflated-Sharpe denominator should count distinct behaviours rather than files.

The table this replaces could not be reproduced. An earlier version reported a different top five and nothing on disk could regenerate it. Rebuilding from its description recovered the universe benchmark exactly, and matched no individual factor under any of three rebalancing and cost conventions — one came out with the opposite sign. Varying the convention until the numbers agreed would have been fitting the method to the answer, so the table was replaced rather than reconciled. The four factors under forward observation were chosen by that ranking; under this one they place 4th, 30th, 57th and 234th of 456. That does not weaken the forward record, which is tested by what happens after the freeze rather than by how it was picked — but the account of why those four were chosen cannot be checked.

Four biases, measured and removed

Each was quantified on a real equity panel while building this pipeline, and each is large enough to invent a strategy on its own. Red is what the flaw reports; violet is what survives once it is removed. Neither column is a return claim.

The first row is the one worth sitting with. Same panel, same cost model, same portfolio construction — only the rule for choosing factors differs, and the gap is about 3 bps/day. That exceeds most published equity-factor results, which is why a pipeline unable to audit its own selection step cannot separate a discovery from an artifact of choosing. The mechanism reproduces on synthetic data containing no signal at all: an information ratio of 4.53, manufactured in ten seconds by examples/selection_artifact.py.

Status, stated plainly: candidates are generated and fully evaluated; none has yet cleared the counterfactual, walk-forward and multiple-testing gates together. That is the gates working on a price-and-volume library, not the engine failing to run — and unlike most backtests, this one reports the count.

Research architecture

Discovery is separated from acceptance. Candidate generation receives training data; validation and shadow windows are structurally excluded from parent selection and refitting.

Scientific primitives

The library exposes compact reference implementations. A primitive is available for preregistered falsification; availability is not evidence of predictive power.

Dependence-aware Evidence Lab

A standalone falsification workbench for a searched family of factors, forecasts, or policies. One shared resampling design preserves serial and cross-candidate dependence, then tests both the global winner and individual survivors.

Research basis

The code follows published methods while retaining explicit implementation boundaries.

Factor research surface

Research integrity contract

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