192 ideas tested. 105 of them didn't work.

If a test assumes you buy at the same closing price that triggered the decision, it is crediting you with information you did not have. Correcting one strategy to buy at the next morning's open dropped its Sharpe ratio from 1.22 to 0.62 — the same strategy, honestly measured, was half as good.

Around twelve separate attempts to forecast which stocks would fall, over horizons from one week to three months. All failed, and all failed with the same signature. Manage how much you are exposed; don't try to see it coming.

Only 44.5% of stocks beat the S&P 500 over our window. Every classifier we built to sort future winners from losers performed at chance. What worked slightly was predicting how big a move might be, never which way it would go.

After thirteen failed attempts to find an exit trigger, the framing that survived is that you don't sell because a stock looks bad. You sell because the money has somewhere better to be.

Among large US stocks over our test window, more volatile names paid better, and low-volatility and market-decoupled names were a drag. Stated as an observation about this universe in this era — not a law. The widely cited "betting against beta" effect ran backwards here.

Keeping existing positions rather than constantly swapping them helped on returns — and, discovered later and independently, on risk too. A portfolio that rotates slowly ends up holding stocks bought at different moments, and those move together less than a fresh basket picked all on one day.

"First half versus second half" is the standard robustness check and it is close to useless. Market regimes don't align with calendar halves; you have to split on the actual regime.

Measure against the index rather than in raw terms. Include the companies that went bust or were taken over. And compare a stock against its own history rather than against other stocks — several effects that looked real across stocks vanished, or flipped sign, when measured within each stock.

When a stock stops leading, it takes a median of nine trading days. But it happens to entire cohorts of similar stocks simultaneously, not to individual companies — and in advance it is indistinguishable from an ordinary wobble, which is five times more common. About 83% of apparent leadership losses recover.

Trading frequently looks skilful in choppy markets and foolish in trending ones — regardless of whether the trading rule has any merit. This means you can never compare two strategies that trade at different rates without a control that trades at the same rate randomly.

Twice in one day, data that appeared to be missing turned out to be a loading error. The most costly instance: a belief that our price history only reached back five years — repeated as a caveat across dozens of studies — was simply false. It reaches 2018 and spans three bear markets.

The most useful single distinction we found. If a measurement keeps its rank between stocks over time, it is a characteristic and it will predict volatility, never direction. If it doesn't persist, it is a condition — and conditions are the only place return has ever lived here. You can tell which you have before running any return test at all.

A census of every arm ever tested found real structure: 100% of validated results were sign-stable across eras versus 10% of rejected ones, and six recurring failure modes covered 95% of the 184 rejections. Then we ran a pre-registered test on a decade of data we had never examined. Both of our flagship entry edges failed it. Nothing in the programme cleared a trial-count-adjusted significance test.

Any rolling, smoothed or differenced construction inherits a long memory from its own arithmetic. Before treating persistence as evidence, run the identical calculation on random data and confirm you can tell the two apart.

A construction screen costs about an hour, touches no outcomes, and therefore cannot contaminate anything. It is the cheapest filter available and it kills most ideas before they consume a full study.

First: compute your measure on the index itself. If the index scores higher than every individual company, you have found a market-wide phenomenon that cannot possibly rank companies against one another. Second: any measure taken over a limited window carries built-in random error — if the spread between companies is no larger than that error, the entire spread is measurement noise and there is nothing to rank on.

Narrowing to a subgroup before running the wider test contaminates the wider test, because the subgroup sits inside it — you already know part of the answer. Run the wider test first, or declare the subgroup in advance.

The hardest lesson here. A locked-in pass/fail threshold tests a number; it cannot tell you the number was computed on garbage. One of our runs passed all six of its pre-registered criteria on corrupted prices. Locked criteria don't prevent a wrong answer — they make a wrong answer look official. Every study now carries a separate plausibility check against something independently known.

A stored series can have years missing with nothing marking the gap, and every standard "look back N days" calculation reads straight across it as though no time passed. In our data this affected about 0.5% of rows and manufactured roughly a full percentage point of phantom edge. Corruption scanners cannot catch it, because the prices on either side of the hole are individually valid.

Rare signals look spectacular and mostly aren't. The rarest tier of results we examined retained only 15% of its apparent advantage on retest, and 26% of rare strategy variants cleared our cost threshold on noise alone. Concentrated, high-conviction, rarely-firing ideas are where self-deception is easiest.