Research letters · 13 November 2026
Research letter, 13 November 2026
This week
The most careful papers this week mostly find nothing. In one, a live deflated-Sharpe gate inside an LLM strategy search refused to certify 36 of 37 runs. In another, a quantum layer in a stock ranker turned out to add nothing: a frozen random version matched the trained one, and removing it entirely did no harm. The one positive result comes from a paper built so it could fail. A pre-registered retest found the end-of-day reversal in S&P 500 stocks still present after 2019, but every proposed mechanism test failed.
This is a short letter: four items, all from arXiv. We found no new SSRN or NBER papers in these areas from the past two weeks that we could verify. One journal paper we have not yet read in full is listed under Watching.
1. Can a search hold its own bar? In-loop deflation and its exploits in autonomous strategy discovery
Eray Gençay · submitted 14 Oct 2026, announced in the November listings · arXiv:2611.14539 · code, configs and full run traces at Zenodo 10.5281/zenodo.21725589. The full platform is available on request.
Method.
- The bar runs inside the loop. Normally the deflated Sharpe ratio is applied once the search has finished. Here every candidate the LLM proposes is checked against a bar computed live from all trials so far: B_k = √max(V̂_k, V_floor) · K(N_k). K is the Bailey–López de Prado expected-maximum factor, N_k is the trial count, and V̂_k is the variance of the trials' in-sample Sharpe ratios.
- Acceptance: a candidate replaces the current best only if it beats it and clears the bar at that moment. At the end, the pick is re-checked against the final bar. If it fails, the run reports "no certifiable discovery".
- The exploit, "variance dilution": adding near-average trials shrinks the dispersion term faster than the trial-count term grows (Δlog B ≈ −(1/2N)(1 − 1/ln N)). So padding a search with mediocre near-duplicates lowers the bar.
- Defences: a pre-registered variance floor (V_floor = 0.120), a bar that can never fall, and exact-duplicate filtering. The paper also tests three stopping rules (a fixed budget of 100; "evaporation", which stops once the bar has stayed at or above the best score for 3 straight trials; alpha-wealth) and three kinds of feedback to the LLM critic.
- Primary endpoint: out-of-sample Sharpe with a stationary-bootstrap 95% CI. It deliberately doesn't depend on the bar.
What they tested and found.
- Data. Main: 453 US stocks plus SPY; design period 2017–2021, evaluation 2022–2025. Transfer: 39 ETFs; design 2007–2016, evaluation 2017–2025. One cost model carried over from the author's earlier system, with no cost figures stated in the text.
- 53 audited runs: GPT-4.1 in every cell and Claude Sonnet 5 in the headline cells. Total API spend was about $160.
- Ungated controls: all 16 runs report a strategy anyway. Median OOS Sharpe: US equities −0.22 with GPT-4.1, +0.38 with Claude; ETFs −0.13.
- Gated runs: 36 of 37 end with "no certifiable discovery". The one certification scored OOS +0.58, but its CI was [−0.29, 1.54].
- No run anywhere had an OOS CI that excluded zero. The median CI half-width is about 0.9 Sharpe.
- Dilution stress test (a flood of 30 near-average trials): the plain bar fell by a median 0.178 and the floored bar by 0.054. The non-falling bar didn't move. Floods of 15/30/45 trials lowered the plain bar by 0.11/0.19/0.24.
- Effective number of trials: about 100 nominal trials equal only 10–32 effective ones (Kish) and an eigenvalue rank of 6–8. A bar computed on the nominal count is 0.19–0.36 Sharpe higher than one on the effective count.
- Stopping: evaporation stopped after 8–9 trials, about one-twelfth of the cost.
Limitations.
- No true edge was planted. The gate refused nearly everything, and we can't tell how much of that is good judgment and how much is lack of power. This is the same gap as last week's PROMOTE paper, approached from the other side.
- Thin sample: 3 seeds per cell, two models and a single 2022–2025 evaluation window. With CIs this wide (±0.9), every comparison between arms is a direction, not a result.
- Unclear cost model: "one cost model inherited from the prior system" isn't specified, so net numbers can't be checked.
- Weakest finding: the feedback-format result, as the author says.
- The near-duplicate rate is the striking side result. About 0.65–0.69 of GPT-4.1's proposals were near-duplicates, against 0.44 for Claude. LLM searches are much narrower than their trial counts suggest. That cuts both ways: deflating by nominal trials is too harsh, and the dilution exploit is easy to stumble into.
Evidence vs speculation.
- EVIDENCE: deflating by the dispersion of trial Sharpes inside the loop can be gamed by near-duplicate padding, and a floor plus a non-falling bar contains it. This is a proposition plus a stress test, not a market result.
- EVIDENCE: ungated LLM strategy searches on US equities in 2022–2025 produced OOS Sharpes indistinguishable from zero (53 runs, wide CIs).
- SPECULATION: that the gate would let a real edge through. It was never tested with one.
What we will do with it. We run several shadow variants in parallel and judge each on its own, which is exactly the setting this paper warns about. We will treat the whole set as one search, estimate its effective number of distinct trials, and compute the paper's bar on that count. If our live momentum variant's Sharpe since going live sits below that bar, we stop citing its live record as evidence of edge until a full year of live weeks has settled.
2. Trained, Frozen, or Absent: Identifying What a Quantum Layer Contributes to Cross-Sectional Equity Ranking
Chi-Sheng Chen, Xinyu Zhang, En-Jui Kuo, Rong Fu, Qiuzhe Xie, Fan Zhang · 7 Nov 2026 · arXiv:2611.10801 · code, per-cell results and weights at github.com/ChiShengChen/qtcnn-trained-frozen-absent. The JPX data is public but not redistributed.
Ignore the quantum part. This is a useful paper because it is a self-audit, and the design transfers to any added component.
Method.
- The model: a hybrid stock ranker. A causal convolutional encoder feeds an 8-qubit simulated circuit with 18 parameters, and a small head ranks the top and bottom 200 names per date.
- Six conditions: circuit trained; circuit frozen at its random initial values; a classical stand-in with the same number of parameters; no circuit at all; the circuit alone, trained and frozen.
- Baselines: Transformer, LSTM, TCN, MLP, LightGBM.
- Design: 4 rolling folds (500 training days, 60 selection days, a 20-day embargo, 125 test days), giving 500 OOS days from June 2019 to August 2021. 5 seeds per condition. A locked holdout from December 2021 to June 2022. A US replication on 2,000 stocks.
- Statistics: deflated Sharpe over 55 configurations and the probability of backtest overfitting; Romano–Wolf multiple-testing correction; Diebold–Mariano forecast comparisons; equivalence tests; costs from 0 to 50 bp with break-even points.
What they tested and found.
- Trained vs frozen: difference 0.008 (SE 0.0075), equivalent within ±0.03 (p = 0.0055). Per-cell correlation is 1.000, and ICs differ by at most 7.7e−5. Training the circuit did nothing.
- Trained vs no circuit: −0.082 (SE 0.120). Removing the circuit doesn't hurt, though this comparison only bounds the difference within ±0.50.
- Signal strength: IC is about 0.008 (t ≈ 1.0) in every condition.
- Best deflated Sharpe is 0.17 against a 0.95 bar. Probability of backtest overfitting is 0.58. The smallest Romano–Wolf-adjusted p is 0.38.
- Costs: turnover is 44–47% per leg per day. Only the Transformer breaks even, at 0.49 bp.
- US replication: every condition loses money (no circuit −1.44, trained −1.46).
- The authors' own earlier claim: the earlier preprint's Sharpe of 1.80 had a split adjustment applied backwards in time, an un-annualized Sharpe and only 22 test days.
Limitations.
- Post-hoc choices: the equivalence margin wasn't fixed in advance, and the holdout was opened three times. The authors disclose both.
- Shaky reproducibility: the September runs couldn't be reproduced. The November rerun correlates only 0.40–0.82 per cell with the original, which says a lot about how fragile results are at IC ≈ 0.008.
- Universe: the JPX universe has look-ahead bias that the authors acknowledge, and the US universe is survivorship-exposed.
- Seed noise dominates: the standard deviation across seeds (0.15–1.70 Sharpe) is larger than every gap between conditions. "Equivalent" is partly a statement about noise.
Evidence vs speculation.
- EVIDENCE: the trained circuit adds nothing over a frozen random one, and the whole model has no OOS edge net of costs in Tokyo or the US.
- EVIDENCE: the earlier positive claim came from procedural errors, not from signal.
- SPECULATION: nothing important. The paper claims little, which is its strength.
What we will do with it. Our composite shadow score adds a regime term that takes the same value for every stock on a given date, so it cannot reorder stocks against each other. We will recompute the composite with the regime term held constant and with regime labels shuffled in blocks, and compare the resulting top-25 books with the live ones. If the books are unchanged, the regime term is recorded as inert in the composite and no composite result may be attributed to regime again; regime conditioning would then need its own exposure-level test.
3. The End-of-Day Reversal After 2019: A Pre-Registered Test on S&P 500 Stocks Excluding Heavily Traded Names
Alex Vidovich, Zivana Zerjal · 6 Nov 2026 · arXiv:2611.09286 · replication archive with code, point-in-time membership, the leveraged-ETF launch table and the pre-registration documents with SHA-256 hashes at Zenodo 10.5281/zenodo.24003093. The details below come from the abstract and the archive's pre-registration file rather than the full text.
Method.
- Question: does the Baltussen–Da–Soebhag reversal still hold after their sample ended? In that effect, stocks that lost the most from the prior close to 15:00 outperform the day's winners over 15:30 to the last trade before 16:00.
- Samples. Primary (U1): point-in-time S&P 500 members minus about 80 heavily traded names the authors had studied in earlier, unpublished work. Robustness: the full index (U2).
- Statistic: each day, a dollar-volume-weighted slope of the last-half-hour return on the cross-sectional rank of the return to 15:00. Newey–West SEs (5 lags).
- Periods: E = 2016–2019 (overlaps the original sample), T = 2020–2022 (reported, not judged), L = 2023–Oct 2026.
- Protocol. The pre-registration is dated 5 Nov 2026, with an addendum the same day. It hash-pins the code and data manifests. A gate: only 2016–2019 data may be opened first, and it must reproduce the original sign at t ≤ −2. If it fails, no later data is ever opened. The final run executes once. Fixed decision bars: "weakened" needs t(Δ) ≥ 3, and "changed sides" needs a second t ≥ 3.
- Four mechanism tests in one Holm family: index hedging, the 0DTE calendar, and a stacked difference-in-differences around single-stock leveraged-ETF launches. A placebo window at 13:30/14:30 and 200 random half-samples. A power table, and even the authors' stated prior over verdicts. A shuffled-outcome check: a 3.0% false-PASS rate against 2.3% nominal.
What they tested and found (bps per day; positive = reversal).
- Primary sample: 2016–2019, 3.13 (t = 7.5). 2023–2026, 3.05 (t = 3.0); the one-sided bound allows a decline of up to 61%. 2020–2022, indistinguishable from zero. 2020 onward, 1.69 (t = 2.3). 2023 does most of the work in the later estimate.
- Full index: 3.40 falls to 0.74, but the t of the change is 1.83, short of the registered 3. The weakness is concentrated in the very largest stocks.
- Mechanisms: no pre-registered mechanism test passes. The leveraged-ETF launch effect is −3.5 bp with t = −1.3.
- Costs: "no claim net of costs", and no trading strategy is proposed.
Limitations.
- The primary sample can't be rebuilt. The excluded list is not released. The archive offers a proxy that drops the 80 largest stocks by dollar volume, but the headline numbers can't be reproduced exactly from outside.
- The pre-registration was private. It was written the day before the paper was posted. The hashes prove the files weren't changed afterwards, but not when they were written.
- Survival rests on few years. It rests largely on 2023, with 2020–2022 at zero, so "survives" really means "came back".
- Not a tradable result. 3 bp a day on a half-hour window, before spread, says nothing about implementable profit.
Evidence vs speculation.
- EVIDENCE: in the primary sample, the pre-close reversal is present again in 2023–2026 at roughly its 2016–2019 size, gross and before the closing auction.
- EVIDENCE: the hedging and leveraged-ETF explanations do not pass a pre-registered test.
- SPECULATION: that the effect will persist. Most of the post-2019 estimate rests on a single year.
What we will do with it. We don't trade the last half hour, so the finding itself isn't useful to us. The protocol is: a gate on old data before newer data may be opened, a run-once hearing, a power table, and especially the shuffled-outcome false-PASS check. Our own promotion scorecard has never had its false-pass rate measured. We will rebuild our weekly books on shuffled forward returns 200 times and run the unchanged scorecard on each. If it passes noise more than one time in ten, every promotion read is suspended until the thresholds are re-derived from that null; if not, the rate goes into the scorecard header and we continue.
4. Idiosyncratic Market Effects in Global Time Series Momentum
Andrew Butler, Maciej Zawadzki, Adam Butler (ReSolve) · 11 Nov 2026 · arXiv:2611.15646 · no code. The futures data comes from a commercial vendor (CSI).
Method.
- Signal: time-series momentum over 21, 126 and 252 days, divided by volatility, capped at ±10. The target is the forward return divided by volatility.
- Models: one-feature Nadaraya–Watson kernel regressions (Gaussian kernel, bandwidth 0.30), each averaged over 100 models trained on 10% subsamples. Four variants: Global Linear (OLS); Global Nonlinear; one curve per sector; one curve per market.
- Testing: expanding window refit every year with a 22-day gap. OOS from Jan 1995 to Jun 2026 on 50 futures markets, net of per-contract slippage and commissions, scaled to 20% volatility.
What they tested and found.
- Average of the three momentum windows: Sharpe 0.54 (global linear), 0.57 (global and sector nonlinear) and 0.60 (one curve per market). The improvement is not significant (t = 1.03), and the variants correlate 0.95–0.99.
- 6- and 12-month momentum: no reliable gain from per-market curves (t = −0.45 and 0.22). Every model is near zero in the last decade at 6 months.
- Tails: where the vol-scaled signal is at least 3 in absolute value, every model loses money. Global Linear −0.086 (t = 3.46) vs market-specific −0.017. The authors suggest exiting rather than leaning in at extremes.
Limitations.
- The headline is a null that the authors frame as promising. Their own words: "small and inconsistent", "unable to claim with statistical confidence".
- No multiple-testing control across many sector × model × feature t-tests, and no deflated Sharpe.
- Different asset class: futures time-series momentum, not cross-sectional equities.
- Thinly reported tail result: the most interesting finding is reported per model as a mean, not as a portfolio decision. Its sign convention is also hard to verify from the text.
Evidence vs speculation.
- EVIDENCE: nonlinear and per-market momentum response curves don't reliably beat a linear global rule out of sample over 31 years net of costs.
- EVIDENCE (weak, single test, uncorrected): returns after extreme vol-scaled momentum readings are negative.
- SPECULATION: that market-specific curves are signal rather than noise.
What we will do with it. Our clean momentum variant selects on raw 12-1 return, so it probably loads on exactly the extreme readings this paper says do poorly. We will split historical picks by volatility-scaled momentum and compare the extreme group's forward excess return with the rest, across 2008 to 2026 and in both halves of that period. Unless extremes underperform clearly in both, the idea is dropped for good and no vol-capped variant gets built. A pass only earns a shadow variant, not a change.
Promising experiments
- The regime "absent" ablation (item 2). It is the cheapest test here, an afternoon of recompute. The answer is nearly decidable from the arithmetic: a constant added to every stock can't reorder stocks. Running it pins down what the composite shadow's regime channel actually does, and stops us crediting regime for results it can't have caused.
- The scorecard's false-PASS rate under shuffled outcomes (item 3). We have never measured how often our own promotion machinery passes noise. Last week's PROMOTE paper says repeated looks almost always promote something. This test measures it on our own scorecard rather than assuming.
- The in-loop bar on our own variant ledger (item 1). It is mostly bookkeeping, but it would give the first honest count of how many distinct hypotheses we have actually tested.
Watching / not yet credible
- Heterogeneous ensemble learning for cross-sectional prediction (Li, arXiv:2611.12389, ICAIF '26). 50 mixed learners on CSI 300 with Alpha158 factors. RankIC is 0.060 vs XGBoost's 0.059. The only backtest uses daily rebalancing with no costs, on a single unpurged split with tuned-looking parameters (β = 0.8789). The ensemble-diversity idea is sound, but there is no evidence of edge yet.
- Tabular foundation models for financial prediction (deHaan & Huang, arXiv:2611.13550). Google's TabFM beats a fine-tuned LLM and tree models at forecasting next-year earnings changes. The pretraining on synthetic data avoids memorization leakage, which is a real advantage for point-in-time work. But it is one benchmark, the abstract gives no numbers, and it is not a returns test. Worth a look once a returns application appears.
- Brazilian hybrid fundamental + moving-average strategy (arXiv:2611.06919). Four-factor alpha is 0.98% a month, but it comes from a single full-sample backtest with an unexplained SMA 9/46 rule. The Sharpe gap vs the Ibovespa is not significant (p = 0.154). The arXiv page also shows a May 2026 submission date, which doesn't fit the November ID. In-sample only, so skipped.
- "Two Blind Spots in Backtest Validation" (Risks 14(11):247, doi:10.3390/risks14110247, Oct 2026). From the abstract: a data artifact produced a dollar-index anomaly that passed overfitting diagnostics, and the corrected result is a null (DSR 0.046). We have not yet read the full paper. It is relevant to our data-quality checks and will be covered once read.
- Global Seasonality Factor Investing (Butler, Butler, Zawadzki, arXiv:2611.15657). Same authors as item 4. Listed this week; not yet reviewed.
Updates
Nothing previously covered appeared as a revised version in this week's listings. Older items were not systematically re-checked for new versions.
Item 1 adds to last week's thread on gating adaptive searches (PROMOTE, 2611.03384; LLM agents as judges of predictability, 2611.04070) and to "Deflate by Bits, Not Trials" (SSRN-7557458, covered earlier). Taken together: deflating by trial count fails under adaptive search, whether it's applied once at the end or checked live inside the loop. And none of these papers has shown a gate that passes a planted, realistic edge.
This letter is drafted with AI research assistance and reviewed and signed by Bob Katz. It is research commentary, not investment advice. No result described here is a claim net of trading costs unless stated, and the experiments listed are planned tests of our own models, not findings.