Five things we tested this summer that do not work (and three of our own “no improvement” verdicts that were really “we could not tell”)

The idea is textbook: stocks that move less return more than their risk justifies. We tested six definitions (volatility over 252, 126 and 63 sessions, downside deviation over 252 and 63, and beta) at two weights. All twelve made the portfolio worse. The strongest t-statistic is −1.85, meaning the one result that comes close to significance points the wrong way.

But the two underlying reasons matter more than the numbers:

• In our universe the factor sorts backward. Splitting the 500 into ten buckets, least to most volatile, the excess return runs: −0.99, −1.03, −0.39, −0.32, −0.47, +0.02, −0.17, +0.24, +0.55, +2.54. The anomaly does not fail to show up: it shows up inverted.
• The engine already had volatility inside it. Our momentum is divided by 252-session volatility. This was not a new dimension: it was doubling down on one already present.

The one thing that did improve: portfolio volatility falls from 21.9% to 17.7%. But the maximum drawdown barely moves: from −36.8% to a range of −35.5% to −37.0%. You buy less daily noise, not fewer scares. The scare is market risk, and everybody eats it.

And a control worth copying: we tried adding a fifth factor carrying no information at all, pure noise, five times over. Simply by diluting the four that do measure something and adding turnover, that costs 1.11 points a year on average. Any fifth factor has to win that back before it starts contributing anything.

All of it in medicion_baja_volatilidad.json, generated by medir_baja_volatilidad.py. The base portfolio returns 17.09% gross and 16.40% net (10 bps per side) over that window.

PEAD is one of the most cited effects in the literature: after a positive earnings surprise, the stock supposedly keeps rising for weeks. The classic window (2 to 20 days) does not fit a portfolio that rebalances monthly; the 63-session window does fit, with 81% to 87% coverage. So that is the one we measured.

First we checked that the surprise itself was built correctly, because without that a “does not work” would be indistinguishable from a miscalculation. Sorted by surprise, the announcement window sorts perfectly: monotonicity of 1.00 across 24,321 events, with t = 5.21. The market pays for the surprise, and our calculation sees it.

What is not there is the drift afterward. The highest number in the entire study is t = 2.38, and with 84 cells tested the multiple-testing correction demands 3.43. Out of sample it collapses: the best cell chosen using data through 2018 gave t = 2.51, and from 2019 to 2026 it gives t = 0.15.

And the literature points the same way: Martineau (Critical Finance Review, 2022) concludes that in large caps PEAD has not existed since 2006. Our universe is the S&P 500 — precisely where it is said to be dead.

In medicion_pead.json, generated by medir_pead.py: the validity check under prueba_de_validez_reaccion_en_el_anuncio, the attempt count under intentos, the out-of-sample test under fuera_de_muestra, and the placebo under placebo.

The list was closed and justified before a single result was seen. With eleven tests the bar is |t| ≥ 2.88. The highest that came back is 2.31, and it points against (removing sales-to-price from the Value factor makes things worse). In the improving direction, the best reaches 1.04.

The trap that nearly worked, written down here in case somebody ever shows you the chart: classic momentum, without dividing by volatility, leaves the portfolio at 17.30% net versus 16.40%. Almost a point a year more, if you only look at the curve. But its predictive power is worse and the sign flips with portfolio size: −0.85 at 10 positions, +0.81 at 20, +1.64 at 50. That is not a signal, that is the noise of twenty stocks.

And something came out that we did not know. An arithmetic average of four normalized scores does not split 25/25/25/25: it splits according to how much each one disperses. Here that is momentum 34.0%, growth 23.4%, value 22.2% and quality 20.3%. Actually equalizing them makes things worse: the portfolio drops from 17.09% gross to 16.05%, and from 16.40% net to 15.43%.

In medicion_definiciones_factores.json, generated by medir_definiciones_paso2_variantes.py. The split comes from dispersion_media_de_los_cuatro; the paired t-statistics from pruebas_pareadas.

A company issuing shares nonstop dilutes its owners; one buying them back does the opposite. The hypothesis was that this signal would be a close cousin of our value and quality factors, and would therefore add nothing. It was false: once you strip out the part already explained by our model, its predictive power does not collapse.

At a one-year horizon, 36-month net issuance sorts better than any of the four factors we use. But at 21 sessions, which is where the portfolio actually lives, it barely sorts at all. Out of that comes the only actionable thing from the whole summer, and it is not a new signal: it is changing when you trade, not what you buy. A portfolio rebalancing once a year measures something else. That is a new measurement, and it has not been run yet.

In medicion_emision_devengos.json, generated by medir_emision_devengos.py. The discards are counted under huecos_no_rellenados.

FINRA publishes, free and twice a month, how many shares of each company are sold short. We hold 138,452 observations going back to December 2017, each with its real publication date and not one gap in the range.

The result: the conditional predictive power comes in at +0.0117 with t = 1.07, but the decile ladder is flat (monotonicity of 0.08). A positive number with no economic shape behind it is not a signal: it is an average. And the power gate finishes it off: with 102 rebalances, deciding the one percentage point we were looking for would take 2,135 observations, roughly 178 years.

The control everyone should copy. Every FINRA data point has two dates: the settlement date it refers to, and the date it was published, about nine days apart. Using the settlement date — that is, looking at the data before it existed — raises the result by 14%. Anyone measuring this without the publication date will publish a prettier number that is false.

Data in datos/construido/interes_corto_manifiesto.json and interes_corto_bruto.csv; measurement in medicion_interes_corto.json (medir_interes_corto.py) and the gate-by-gate verdict in veredicto_interes_corto.json.

To judge these five measurements we first wrote a bar: six gates in series — power, multiple testing, overlap, benchmark, cost, and chance — and, above all, three verdicts instead of two: PASS, FAIL, and CANNOT BE DECIDED.

The third one is half the value of the tool. “I found no effect” is not “I proved there is no effect”: if the sample never had the power to detect an effect of the size being looked for, the experiment says nothing in either direction.

We ran the six rejections this house had already made through it. Five had power below 55%, and three below 20%. The clear case is “lowering turnover does not improve net returns”: the effect in play was 0.93 points, and the smallest effect that experiment could detect was 2.86. Deciding it would take 146 years of data. Not changing the recipe is still correct, but out of prudence, not out of measurement. Writing “we measured turnover and it does not help” was an overclaim.

One of them is properly rejected for the right reason (risk overlays on the portfolio), and one is properly rejected for the wrong reason: sector neutrality. What supports that decision is the four points of annual return it costs, not its t-statistic. If somebody reopens the topic citing the t, the argument is lost.

The bar is liston_estadistico.py, written on August 31 before any result was seen — a bar written after seeing the numbers is not a bar, it is a rationalization. Run python liston_estadistico.py --historicos and it reviews the earlier rejections on its own.

• Zacks advertises 23.89% a year. Its own disclaimer explains how.
• We lowered our own published returns, and here is why