# Pre-registered hypotheses — ThePickLog **Registered:** 2026-06-22 · **Why this file exists:** these filters were spotted in an *in-sample* cut of the first 52 graded picks. In-sample patterns overfit. To be honest, the rules are frozen here **with a date**, and only picks logged **after** the registration date count as the real (out-of-sample) test. `weekly_report.py` tracks both all-time and post-registration performance automatically, so the forward log is the judge — not me. ## Baseline at registration (N=52 graded) - Win rate (same-day open→close, net of 2% haircut): **44%** - Avg net/trade: **−2.4%** · median **−2.8%** - 5-day hold: 31% win, **+0.3%** mean (a few big winners carry it → expectancy, not win rate, is the real target). ## Selection-filter hypotheses Each says "**skip** these picks." A filter passes only if, on **post-registration** picks, the kept subset beats the unfiltered baseline on **avg net/trade** (the expectancy metric), without shrinking the sample to uselessness. | id | rule (skip if…) | rationale | in-sample signal at registration | |----|------------------|-----------|-----------------------------------| | **H-F1** | price < $1.00 | sub-$1 = manipulation / delisting risk | sub-$1 win 22% vs ≥$1 49% | | **H-F2** | float ≥ 3M shares | the screen's edge is the *thinnest* floats | ≥3M win 25% vs <3M 48% | | **H-F3** | gap ≥ +20% at screen | chasing an extended gap buys the top | ≥+20% was 0/2 | | **H-F4** | tier A or B (hot) | Finding A: hottest momentum = deepest drawdown | already holds out-of-sample | | **H-CLEAN** | any of F1–F4 | combined "only the clean setups" filter | — | ## Open question (no pre-set direction) | id | question | why two-sided | data status | |----|----------|---------------|-------------| | **H-SI** | does short interest ≥20% separate winners from losers? | high SI is squeeze-prone — violent *both* ways, so neither direction is assumed | short-interest capture began 2026-06-16; **no graded pick carries it yet** (all 65 graded predate capture). Tracked in the weekly report; evaluate once enough SI-bearing picks have graded. | | **H-DIL** | does an active offering/shelf (`dilution_flag` = offering/shelf) separate winners from losers? | dilution caps a squeeze (new supply at the top) → plausibly *worse* forward returns, **but** an offering is also the very catalyst that ignites these names, so direction is not assumed | `dilution_flag` + `catalyst_type` capture began **2026-06-28** via free SEC EDGAR (`edgar_lens.py`); **no graded pick carries it yet**. Forward-only. Evaluate once enough dilution-bearing picks have graded. | | **H-INS** | does net open-market insider buying (`insider_net` = +1) separate winners from losers? | insiders buying their own money in is a classic conviction tell → plausibly *better* forward returns, **but** in spike-prone microcaps a filed buy can also be a pump signal, so direction is not assumed | net open-market insider buy/sell (Form 4 codes P/S only, 90-day window) capture began **2026-07-08** via free SEC EDGAR (`edgar_lens.py`) → `edgar_snapshot.csv`; **no graded pick carries it yet**. Forward-only. Most microcap picks show *no* open-market activity in-window (`insider_net` blank), so expect this to accumulate slowly like H-DIL. Evaluate once enough insider-bearing picks have graded. | **Data note — `catalyst_type` is a filing proxy, not a news classifier.** It is derived only from SEC filings (`offering` = 424B* in 7d · `8K` = recent 8-K · `filing` = other recent filing · `none`), because a true news/PR catalyst is not reliably in EDGAR. Per the roadmap guardrail "don't half-build a lever off an unreliable source," only the EDGAR-truthful part is captured, and it is labelled as such. **Data note — `insider_net` is open-market ONLY, and insider *ownership %* is deliberately not synthesized.** `insider_net` nets only Form 4 discretionary trades (code `P` buy / `S` sell); grants, option exercises, tax-withholding and gifts (`A`/`M`/`F`/`G`…) are excluded so a "+1" means an insider chose to put their own money in, not comp mechanics. Insider *ownership %* stays "not checked" because an honest figure needs an all-insiders aggregate against shares outstanding that Form 4 alone can't give — same guardrail as above. `insider_net` also feeds the point-in-time Quality-Lens grade (the `management` category) via the `insiderNet` input, so the snapshot grade reflects it going forward. **Finding B (quality → shallower drawdown) is now testable forward.** Phase-1 (in-sample, as-of grader) was a **NULL** after removing look-ahead. The blocker to a forward test was that quality was never logged at screen time. As of **2026-06-28** the Quality-Lens grade (overall/label/classification + 7 category scores) is snapshotted per pick into the forward-only sidecar `edgar_snapshot.csv` (point-in-time via `asof_grader.grade_asof`, so no Yahoo-style revision drift). This does **not** re-open Finding B as a claim — it merely preserves the *option* to test it OOS later. Still recommended-skip unless a real reason to sharpen the score emerges. ## Exit-rule hypothesis **H-EX1 — registered 2026-06-23.** *The screen's edge is in the exit, not the selection.* The in-sample evidence (first 65 graded picks) is that these names **spike then fade**: 82% touch +5% intraday within the 5-day window, 63% touch +10%, 54% touch +15%; the typical pick reaches **+16.4%** max-favorable (median MFE) while the current same-day-close exit realizes **−2.8%** avg. The hypothesis is that a disciplined profit target monetizes the spike the screen is genuinely good at finding. - **Rule (frozen):** rest a **+10% limit** over the 5-trading-day hold. If the 5-day high (`mfe_5d`) reaches +10%, the order fills → realized **+8% net** (target −2% cost haircut). Otherwise exit at the 5-day close (`ret_open_5dclose_net`). Deterministic from the forward log; no discretion. - **Baseline to beat:** the **current** exit = same-day open→close, net (avg **−2.8%**, median −3.6%, win 40% at registration). - **Pass criterion:** on **post-2026-06-23** graded picks, the H-EX1 arm's **avg net/trade (expectancy)** must exceed the same-day-close baseline, with the direction stable across weekly snapshots. Median and win% are secondary readouts. - **In-sample signal at registration (not the test):** +10% target → 63% win, **+8.0% median**, −1.6% avg vs −2.8% same-day-close — i.e. **+1.2pp expectancy, +11.6pp median.** - **Slippage caveat (must stay attached to every report):** fills are assumed exactly at +10%. On thin low-float names, limits gap through and fill quality is poor, so **real-world results will be worse than the proxy.** The 2% haircut does not capture gap-through. This is why H-EX1 is a *hypothesis to be falsified forward*, not a result. - **Tracked by:** `weekly_report.py` §4d (all-time + post-registration), alongside the exit study (`exit_sim.py` → `reports/exit-study-LATEST.md`) which walks the daily path as the rigorous cross-check. - **Bayesian read-out (added 2026-07-02, priors frozen that date):** `bayes_h_ex1.py` maintains a Beta-Binomial posterior on the +10% touch rate (headline flat Beta(1,1); Jeffreys(0.5,0.5) and skeptical Beta(10,10) as sensitivity), reporting P(touch rate > breakeven) for both the beat-baseline and absolute-profit lines → `reports/bayes-h-ex1-LATEST.md` + a live dashboard panel (browser recomputes independently from the CSVs; parity-tested). This is a *read-out* of how much the log has learned, not a new pass/fail criterion — §4d expectancy vs baseline stays the registered judge, and the breakeven lines are plug-in translations whose own noise is not propagated (see BAYESIAN-ROADMAP.md R3). ## Exit-rule hypothesis #2 — does a stop add value? **H-EX2 — registered 2026-06-24.** *A profit target without a stop ignores the fat left tail.* H-EX1 monetizes the spike but says nothing about the downside; the live log shows a brutal left tail (median 5-day MAE ≈ −16%, worst −50%, **17% catastrophic-rug rate** with MAE < −30%). H-EX2 asks whether pairing H-EX1's target with a disaster stop **improves expectancy** versus the target alone. - **Rule (frozen):** over the 5-trading-day hold, rest a **+10% limit AND a −20% stop**. Whichever level the daily path touches first exits the trade; if neither is touched, exit at the 5-day close. **Conservative same-day-collision convention: if a single session's range spans BOTH levels, assume the STOP filled first** (results can't be optimistically inflated). Fills assumed exactly at the level; same 2% cost haircut. Deterministic from the committed daily path (`paths.csv`); no discretion. - **Why −20% (and not tighter):** the median pick already dips ≈ −16%, so a stop inside that would book a loss on the *typical* wobble and shred the spike H-EX1 is trying to catch. −20% sits **beyond** the median drawdown — it is a *disaster* stop aimed only at the −30%-and-worse rug tail, not a tight trade-management stop. (Frozen, not tuned; OOS judges.) - **Baselines to beat (two):** primary = **H-EX1 (+10% target alone)** — does adding the stop raise avg net/trade? secondary = the current same-day-close exit. All three arms are computed on the **same path-bearing subset** so the comparison is apples-to-apples. - **Pass criterion:** on **post-2026-06-24** graded, path-bearing picks, H-EX2's **avg net/trade (expectancy)** must exceed H-EX1's, with the direction stable across weekly snapshots. A null (the stop costs more in booked losses than it saves in avoided rugs) is a fully valid, expected outcome and would *keep H-EX1 stop-less*. - **Data dependency / honesty note:** unlike H-EX1 (evaluable from `mfe_5d`), a target+stop rule needs the **order** of touches, which only the daily path resolves. `paths.csv` is **forward-only** (capture began ~2026-06-22), so the post-registration, path-bearing sample starts near zero and accumulates — exactly like H-SI. Until it does, §4e reports *pending*, not a result. - **Slippage caveat (must stay attached):** thin low-float names **gap through stops** — a −20% stop can fill far below −20% on a halt-and-reopen. The 2% haircut does **not** capture gap-through, so realized H-EX2 results will be **worse** than this proxy, and worse for the stop arm specifically. This is why H-EX2 is a hypothesis to be **falsified forward**. - **Tracked by:** `weekly_report.py` §4e (all-time context + post-registration test), with `exit_sim.py` (rule *"H-EX2 +10% target / −20% stop"*) walking the full daily path as the in-sample cross-check. ## Exit-rule batch #2 — registered 2026-07-02 Seven further exit hypotheses, frozen together on this date. All follow the H-EX1/H-EX2 conventions unless stated: 2% cost haircut, fills assumed exactly at the level, conservative same-day-collision rules (ambiguity resolves against the strategy), deterministic from outcomes.csv / paths.csv, no discretion. **Judged on post-2026-07-02 graded picks only.** **⚠️ Family-wise honesty note (must stay attached):** registering seven rules at once means one may beat baseline **by luck**. No single arm from this batch is "validated" merely by winning its own comparison — the batch is a *ranked screen*. Any winner must (a) beat its baseline on avg net/trade, (b) hold direction across ≥3 consecutive weekly snapshots, and (c) remain the winner while the sample keeps growing. Prefer the simplest rule among statistical ties. | id | rule (frozen) | baseline to beat | data needed | |----|---------------|------------------|-------------| | **H-EX3** | **Target sweep:** as H-EX1 but at **+5%** (net +3%), **+15%** (net +13%), **+20%** (net +18%); unfilled → 5-day close | H-EX1 (+10%) and same-day close | outcomes.csv (`mfe_5d`) | | **H-EX4** | **Time stop:** +10% limit; if unfilled by the **day-2 close**, exit at day-2 close (don't wait out days 3–5) | H-EX1 | paths.csv (touch day + day-2 close) | | **H-EX5** | **Hold-length baselines:** no target — exit at **day-1 close** (arm a) or **day-2 close** (arm b) | same-day close AND 5-day close | paths.csv | | **H-EX6** | **Partial exit:** sell **half** at +10% (net +8%), half rides to the 5-day close | H-EX1 (does keeping half the tail beat full exit?) | outcomes.csv | | **H-EX7** | **Trail after target:** once a daily high touches +10%, arm a trailing stop **15% below the running max daily high** (trail level computed from *prior* days' highs only — no same-day ratchet); exit when a day's low touches it; never armed → 5-day close | H-EX1 | paths.csv | | **H-EX8** | **Tier-conditioned target:** tier A/B → **+20%** target, tier C/D → **+10%**; unfilled → 5-day close | H-EX1 (uniform +10%) | outcomes.csv + picks.csv tier | | **H-EX9** | **Stop sweep:** as H-EX2 but with **−10%** and **−30%** stops (same stop-first collision convention) | H-EX2 (−20%) and H-EX1 (no stop) | paths.csv | Registration rationale (in-sample context, not the test): most picks touch +5% (82%) and +10% (63%) but finish negative (median 5-day −7.9%); MFE clusters early in the window; the return distribution is fat-tailed right (a few +100%+ runs) and fat-tailed left (≈16% rug rate) — so target level, exit timing, tail participation, and disaster stops are the four levers worth sweeping. Prior expectations, stated for honesty: H-EX9 tighter stops likely **hurt** (gap-through), H-EX5 short holds likely **beat** 5-day hold, H-EX7 trailing is the most slippage-fragile arm in the batch. - **Slippage caveat (inherited from H-EX1/H-EX2, applies to every arm):** thin floats gap through limits and stops; real fills are worse than the proxy. Any edge under ~+1%/trade is treated as noise. - **Tracked by:** wiring into `exit_sim.py` / `weekly_report.py` is a follow-up; **the registration date above governs the out-of-sample window, not the code date.** Until wired, arms are computable by hand from the committed CSVs. ## Success / kill criteria - **Evaluate** once there are **≥ 30 post-registration graded picks** per arm (directional before that). - **Keep** a filter only if post-registration kept-subset avg net/trade **> baseline** and the direction is stable across the weekly snapshots. - **Kill** any filter that doesn't separate winners from losers out-of-sample. A null is a valid, honest result — most patterns in 52 picks will not survive. - Win rate is a **secondary** readout; the objective is positive expectancy with bounded drawdown. Never optimize win rate at the expense of expectancy. --- ## Validity-study registrations (frozen 2026-07-07) Emerged from the empirical validity studies (`ThePickLog-Empirical-Validity-Studies-2026-07-07.md`). In-sample findings are diagnostics only; these are frozen here so only picks logged **after 2026-07-07** count, and none changes the live model (P5). | id | test | direction / rationale | |----|------|-----------------------| | **H-SUB1** | does 5-day MFE (spike size) scale monotonically with rvol at screen time? | the unique prediction of the fade thesis; absence means the "spike" label is mis-specified | | **H-STR1** | does a **float-only** score reproduce the 4-factor tier ordering? | rvol sub-score is <10 for 81% of picks → the .35 rvol weight may add no ordering info | | **H-STR2** | re-derive weights + cutpoints from post-reg data, register, judge OOS vs v0.2 | cutpoints/weights are currently unjustified; never promote an in-sample fit | | **H-REG** | skip picks tagged `market_regime = risk-on`; does the kept subset beat baseline OOS? | in-sample risk-on was −5.49% vs −1.7% otherwise (regime-fragile) | | **H-CTRL** | capture matched random in-universe microcaps the screen did **not** pick (forward-only) | enables a proper screened-vs-unscreened discriminant test | | **H-REFLEX** | does publishing a pick move the name? (post-publication drift/volume vs audience size) | reflexivity is CIV; ~nil now (no traffic), monitor as reach grows | --- ## Batch #3 — exit rule + methods registrations (frozen 2026-07-08) Registered together on this date. Only picks logged **after 2026-07-08** count toward any verdict below. Conventions inherited from H-EX1/H-EX2 (2% haircut, fills at level, conservative collisions, deterministic from committed CSVs). ### H-EX10 — tier-gated, amplitude-matched exit **Rule (frozen):** tier **A/B** picks → **+20% target** (net +18%), unfilled → 5-day close. Tier **C/D** picks → **same-day close** (no overnight hold, no target). **Baselines to beat:** same-day close on all picks (primary) and H-EX8 (secondary — does gating C/D out of the target beat giving them a +10% target?). Judged on avg net/trade. **Registration rationale (in-sample context, NOT the test):** tiers rank spike *intensity* (A/B median 5-day MFE 23–28%, P(touch +10%) 75–81%; C/D ≈ 10–13% and ~50%), so the target should be scaled to the tier's amplitude and withheld where the amplitude isn't there. In the daily-path replay, A/B + 20% target returned +2.8% avg vs −0.6% same-day baseline (n=15), while every C/D target variant lost to same-day close. **⚠️ Concentration caveat (must stay attached):** 7 of 28 in-sample A/B picks are CUPR — the single best ticker in the log (median MFE +61.7%). The in-sample signal may be one name's pump. **Robustness clause:** a post-registration win only counts if it (a) survives a leave-one-ticker-out check (drop the largest-contributing ticker; direction must hold) and (b) survives the H-IND1 cluster bootstrap. Slippage caveat applies with extra force: A/B names are the thinnest in the log. ### H-IND1 — effective sample size / independence correction (methods, not a trading rule) **Registered acknowledgment:** the scan universe is a **fixed 16-ticker list** (`CONFIG["UNIVERSE"]`), and 13–16 of the 16 pass the screen on every scan day. Outcomes on the same ticker across consecutive days share overlapping 5-day price paths and are mechanically correlated. Headline stats quoted as "n=165 picks" therefore carry the precision of roughly **n≈16 name-level bets** (fewer, counting episodes: the 31 rug rows collapse to ~10 tickers / a handful of collapse events). Per-ticker avg net spans −13.3% (HKIT) to +1.9% (CUPR) — ticker fixed effects plausibly dominate every subgroup table. **Rule (frozen):** from this date, every hypothesis verdict (including the Gate-1 verdict scheduled 2026-07-27) must report, alongside the pooled stat: (a) a **cluster bootstrap by ticker** (resample tickers with replacement, recompute the arm-vs-baseline delta; report the bootstrap interval), and (b) the **per-ticker sign count** (how many of the 16 names individually favor the arm). A pooled win that fails both is reported as **not established**, not as a win. This applies retroactively as a re-read of prior tables, and prospectively to all OOS windows. The R1 Beta-Binomial tracker's iid assumption is flagged as violated; its posterior is directional only until re-specified with clustering. ### H-DEDUP — one-entry-per-episode re-read **Rule (frozen):** re-evaluate the headline stats and every registered filter/exit arm on a **deduplicated pick set**: keep only the *first* pick of each ticker per episode, where an episode ends after 5 consecutive trading days without that ticker being re-picked (i.e., no overlapping holds of the same name). In the current log this collapses ~300 picks to roughly one row per ticker-episode. **Question:** does *any* in-sample or OOS finding (Finding A, H-F1..F4, H-EX1..EX9, tier tables) survive dedup? A finding that exists only in the duplicated view is an artifact of repeated sampling, not a property of the picks. ### H-UNIV1 — universe expansion (structural, forward-only) **Registered intent:** nothing in this log generalizes beyond the 16 hardcoded names. The external-validity claim ("this screen finds low-float spike-fade names") requires a market-wide candidate pool. Plan: replace or augment `CONFIG["UNIVERSE"]` with a true market-wide low-float gap scan (or, minimally, a rotating universe), version-bump the model (v0.3), and treat the fixed-16 record as its own closed cohort. Complements H-CTRL: the matched-control test is uninterpretable while the "screen" admits ~100% of its universe daily — there is no unscreened in-universe control to match against. **Execution (frozen 2026-07-08; free-feed amendment 2026-07-09):** implemented as `universe.py` + `ignitionscan.py scan-market`. **Operating source = free Yahoo screeners** (`UNIV_SOURCE=yahoo`), cohort tag `model_version = v0.3-yf` — zero data cost, same feed lineage as the v0.2 record. An optional later upgrade to Alpaca SIP (`UNIV_SOURCE=alpaca`) would start a NEW sub-cohort tag (`v0.3-alpaca`); tags are never mixed, so provenance stays attributable per row. - **Candidate pool (yahoo):** custom market-wide criteria query (percent change ≥ the +10% gap gate, price inside the frozen 0.50–10 band, US-listed; paged) ∪ predefined lists (day gainers, small-cap gainers, aggressive small caps, most actives). OTC / pink sheets excluded; symbol hygiene drops units/warrants/rights/share-classes. Per-name quotes are premarket-aware (preMarketPrice preferred at scan time); float = Yahoo floatShares (fallback sharesOutstanding), same as v0.2. **Documented limitation:** before the open Yahoo's list rankings lag, so a name moving ONLY in today's premarket may not surface until the open; yesterday's movers gapping again are caught (the premarket gap gate does the real selection). This biases v0.3-yf toward continuation gappers — acceptable and disclosed; the Alpaca upgrade closes it. - **Candidate pool (alpaca, dormant):** Alpaca screener, top-50 pre-market gainers ∪ top-100 most-actives (by volume), same hygiene; float = free SEC EDGAR shares-outstanding proxy. - **Eligibility gates (frozen):** price 0.50–10.00 (the v0.2 band) · gap ≥ **+10%** (up-gaps only) · rvol ≥ **2.0** · EDGAR shares-outstanding float proxy **0 < shares ≤ 50M** (missing share data EXCLUDES — never a free float score). - **Scoring:** the UNCHANGED v0.2 formula/weights/tier cutpoints (PRINCIPLES P5). Selection = **top 10 by score** per day. - **Control pool:** every screened candidate — eligible or not, published or not — is logged to `candidates.csv` with a reject reason / published flag. The eligible-but-unpublished names are H-CTRL's forward-only unscreened control group. - **Cohort separation:** the v0.2 fixed-16 record is CLOSED. `weekly_report.py`, `hypo_eval.py` (leaderboard/gate), `bayes_h_ex1.py`, and `exit_sim.py` all read the v0.2 cohort only; v0.3 appears as its own report section. No existing hypothesis verdict (incl. Gate-1 on 2026-07-27) reads a v0.3 row. New v0.3 rules require new registrations with their own baselines. - **Changing any gate or the top-N cap requires a new registration** — they are part of the frozen definition, not tunables. --- ## Batch #4 — v0.3-yf cohort exit-rule family (frozen 2026-07-13) Every exit rule registered above (H-EX1…EX10) reads the **closed v0.2 fixed-16 cohort only** (H-UNIV1 cohort seal). This batch registers the exit-rule question fresh against the **v0.3-yf market-wide cohort**, where independent N actually accumulates. Registered **before any v0.3 pick has graded** (0 graded at freeze; first grades expected ~2026-07-16), so the entire v0.3 outcome stream is out-of-sample by construction. Only v0.3-yf picks with `trading_date` **after 2026-07-13** count toward any verdict (the 14 pre-existing ungraded picks from 07-09/07-10 are excluded by the standard convention). Conventions inherited from H-EX1/H-EX2: 2% cost haircut, fills assumed exactly at the level, conservative same-day-collision rules (stop assumed first), deterministic from committed CSVs, no discretion. H-IND1 applies: every verdict must report the cluster bootstrap by ticker and the per-ticker sign count (the evaluator emits both). Baseline for every arm = **same-day open→close, net, on v0.3 picks** (paired, same subset). | id | rule (frozen) | evaluator exit id | |----|---------------|-------------------| | **H-V3-EX1** | +10% limit over the 5-day hold; unfilled → 5-day close | `target_10` | | **H-V3-EX2** | +5% limit, same structure | `target_5` | | **H-V3-EX3** | +15% limit, same structure | `target_15` | | **H-V3-EX4** | +20% limit, same structure | `target_20` | | **H-V3-EX5** | +10% limit AND −20% disaster stop (stop-first collisions) | `target_10_stop_20` | **Honest prior, stated at registration (in-sample v0.2 context, NOT the test):** on the v0.2 cohort, net of the 2% haircut, **every** target arm *loses* to same-day close in the full daily-path replay (−3.6% to −4.9% pooled vs −2.6%), per-ticker sign counts are coin flips (best arm 8/15 tickers), and the H-DEDUP re-read collapses to a single path-bearing episode (uninterpretable). So the registered expectation is **skeptical**: this family is registered because v0.3-yf selects *different* names (market-wide continuation gappers, top-10-by-score, real ticker diversity) where the v0.2 null may not transfer — not because the v0.2 evidence supports it. A null here is a valid, expected outcome. **⚠️ Family-wise honesty note (must stay attached):** five arms registered at once = a ranked screen, not five independent claims. Any winner must (a) beat baseline on avg net/trade, (b) hold direction across ≥3 consecutive weekly snapshots, (c) survive the H-IND1 cluster bootstrap + per-ticker majority, and (d) remain the winner as the sample grows. Prefer the simplest rule among statistical ties. Slippage caveat inherited: fills at level are optimistic on thin names; any edge under ~+1%/trade is noise. **Wiring (code date = registration date, for once):** `hypo_eval.py` now supports a per-hypothesis `"cohort"` field; these five arms are live in `hypotheses/registry.json` with `"cohort": "v0.3"` and appear on the Test board scored strictly against v0.3 rows. The board's headline baseline remains the v0.2 cohort; each v0.3 card carries its own paired baseline. ### H-V3-PAPER — paper-execution instrumentation (measurement, not a trading claim) **Registered intent:** every exit verdict above rides on the *fills-at-level* proxy. To measure the proxy's optimism directly, an **Alpaca paper account** (`paper_trader.py`, hardcoded to `paper-api.alpaca.markets` — it cannot touch a live account) trades the H-V3-EX1 rule mechanically on published v0.3 picks: fixed small notional per pick, buy at the open (OPG market order), +10% GTC limit armed from the actual fill price shortly after the open, time-exit near the close of the 5th session. Every order and fill is committed to `paper_trades.csv` (forward-only, verifiable). - **Readout:** realized paper return per pick vs the `paths.csv` proxy return for the same pick under H-V3-EX1. The gap estimates real slippage/fill quality — the number every slippage caveat above currently guesses at. - **Known gaps (disclosed):** the TP limit is armed a few minutes after the open, so a touch inside that gap is missed (conservative — can only understate the paper arm); Alpaca paper fills are themselves idealized vs real routes, so the measured gap is a *lower bound* on true slippage; OPG orders may be rejected on some venues/names — rejects are logged, not silently skipped. - **This is instrumentation.** It produces no pass/fail of its own and changes no verdict; it calibrates the haircut assumption for every exit hypothesis. NOT INVESTMENT ADVICE — paper money only, and nothing here authorizes a live-money deployment (that remains gated behind MONETIZATION-GATE / Gate-1 and an explicit human decision). --- *Pre-registration, not investment advice. The forward log (picks.csv/outcomes.csv) is the only judge; everything here is a hypothesis until post-registration data says otherwise.* --- ## Registration batch #5 — frozen 2026-07-29 Three registrations arising from the **2026-07-29 full audit**, which evaluated six previously registered-but-never-computed hypotheses (H-REG, H-SI, H-DIL, H-SUB1, H-STR1, H-CTRL) and audited the exit study. **Provenance, stated plainly: the motivating patterns below were found by looking at the existing log.** Under P2 that makes them *variable selection*, not evidence — which is exactly why they are frozen here with a date before any of them is allowed to mean anything. Only picks with `trading_date` **after 2026-07-29** count. In-sample numbers are quoted solely to record what motivated the guess and how large an effect would have to be to matter. The audit's headline context: **Gate 1 has already failed** (H-EX1 significantly negative). These are not an attempt to rescue it. Two are genuinely open questions with a mechanism; one is a structural question about the scoring model. ### H-DIL2 — skip names carrying an active offering or shelf (SELECTION) **Rule (frozen).** Keep only picks whose point-in-time EDGAR `dilution_flag` is `none`; skip `offering` and `shelf`. Judged on **avg net/trade vs the unfiltered baseline**, same-day-close exit, on the **v0.3-yf cohort only** (the v0.2 fixed-16 record is a closed cohort per H-UNIV1). Machine-registered in `hypotheses/registry.json` so the leaderboard scores it automatically. **Mechanism (why this is not pure data-mining).** A live offering or shelf is dilution overhang: an issuer with an effective registration can and does sell into exactly the retail volume spike this screen selects for. That caps the pop and supplies persistent offer-side pressure. This is a directional prediction from a stated mechanism, not a pattern with a story bolted on afterwards. **Motivating in-sample split (H-DIL, evaluated for the first time 2026-07-29, all graded picks carrying the flag, n=343, ticker-clustered CIs).** `offering` mean **−3.02%** (CI [−5.43, −0.81]) · `shelf` **−4.31%** (CI [−6.17, −2.71]) · `none` **+1.79%** (CI [−3.66, +21.79], n=54 across 13 tickers). Keeping `none` only: Δ **+4.56pp** vs all, CI [−0.44, +23.96] — **not significant**, and the interval is so wide it is nearly uninformative. `catalyst_type` points the same way (`none` −1.38% ns vs `8K` −4.69%, `filing` −3.80%, `offering` −4.44%, all significantly negative). **Registered prior: skeptical-but-curious.** The point estimate is the largest in the dataset and the mechanism is real, but (a) the CI is enormous, (b) `none` is the smallest bucket and is plausibly just "names EDGAR had nothing recent on," which correlates with being less promoted, and (c) five of five previously registered selection filters came back flat. **Pass requires** ≥ 30 post-registration graded v0.3 picks in the kept subset, Δ > 0 vs baseline, direction stable across ≥ 3 consecutive weekly snapshots, **and** survival of the H-IND1 cluster bootstrap plus a per-ticker majority. The ~+1pp/trade noise floor applies: a Δ under ~+1pp is treated as noise even if nominally positive. **Not registered (deliberately):** the "clean EDGAR" conjunction (`dilution_flag == none` **and** `catalyst_type == none`) showed the largest in-sample effect of all (n=28, mean +6.39%, Δ +9.16pp, CI [−0.91, +62.36]) and is **left unregistered** because n=28 across 8 tickers with a 63-point-wide interval is not a testable claim, and registering both it and H-DIL2 would be two shots at the same mechanism. If H-DIL2 survives, the conjunction can be registered separately afterwards. ### H-SHORT1 — is the 5-session fade tradeable from the short side? (EXIT / DIRECTION) **Rule (frozen).** On **v0.3-yf** picks after 2026-07-29: hypothetical short at the entry session's open, cover at the close of the 5th session, with a hard **−25% adverse stop** (i.e. cover if the price rises 25% above entry; conservative same-session convention — if a session's range spans both the stop and the target, **the stop is assumed to fill first**, as everywhere else in this file). Costs: the standard 2% round-trip haircut **plus an explicit borrow accrual** at a disclosed annualized rate applied per session held. Position sizing for any reported equity curve is capped at **2% of notional per trade**. **Why this is registered at all.** The 2026-07-29 audit found that the single most robust fact in the entire dataset is not an edge but a **decline**: over a 5-session hold these names fall about 6–7% on average, and it survives everything — on v0.2, **15 of 16 tickers** have a negative mean, **7 of 7 weeks** are negative, and leave-one-ticker-out moves the mean only within [−3.10, −2.63]; on v0.3, **54 of 67 tickers** are negative with a median of −13.2%. The honest question that raises is whether the fade is monetizable from the other side. Registering it is the only legitimate way to find out. **Registered prior: strongly skeptical — expected to fail, for four stated reasons.** 1. **It already failed to generalize.** The positive expectancy exists only on the closed v0.2 cohort (5-day short ≈ **+5.21%/trade** net of 2%, cluster CI ≈ [**+0.85, +9.58**] — note the lower bound sits *below* the Gate-2 floor of +1.0%). Pooled across both cohorts the CI is ≈ [**−1.19, +8.57**] and **no longer excludes zero**, and on v0.3 alone the mean is **negative (−2.67%)** despite a **+11.20%** median, because the right tail eats it. H-UNIV1 exists to catch exactly this, and it caught it. 2. **The tail is ruinous.** Skew −2.3 (v0.2) to −6.3 (v0.3). Worst single 5-session short outcomes in the log: **DFNS −665%, STAK −195%, CUPR −175%, JLHL −124%, CJMB −106%**; six v0.2 trades worse than −50%. A sequential-compounding sketch grows at 2/5/10% of equity per trade and goes to **zero at 25%**. The −25% stop above is what makes the rule testable at all; it will also be gapped through on exactly the names that matter. 3. **Borrow and locate are probably decisive, and are not modelled by the 2% haircut.** At the point estimate the v0.2 5-day short survives borrow up to ~200%/yr (+0.04%/trade at 200%). But sub-$5 low-float names are routinely hard-to-borrow *when locatable at all*, short-sale restriction binds after −10% from the prior close, and halts are common. **Availability, not cost, is the binding constraint** — which is why locate feasibility is a disclosed field of this test, not an afterthought. 4. **It is post-hoc.** It was found by inspecting the same log it would be judged on, which is why only post-2026-07-29 picks count. **Pass requires all of:** ≥ 30 post-registration graded v0.3 picks; **both the mean and the trimmed mean (10% each tail) and the median** positive net of the 2% haircut *and* a disclosed borrow accrual — the mean alone is explicitly **not** sufficient, because the right tail controls it; direction stable ≥ 3 consecutive weekly snapshots; survival of the H-IND1 cluster bootstrap **and** a per-ticker majority; and a stated locate-feasibility rate. **Explicit measurement caveat:** this is a *hypothetical* short computed from committed daily bars. It is a research measurement, **not a strategy, not a recommendation, and not authorization for any live or short position** — no short is executed anywhere in this project, in paper or in live money. ### H-STR3 — does the four-factor composite add anything over gap alone? (STRUCTURAL) **Rule (frozen).** Compare the ranking produced by the live composite score against a **gap-only** ranking, on post-2026-07-29 picks, per cohort. The composite "adds information" only if it separates outcomes better than gap alone by a pre-stated margin: the composite's top-vs-bottom-half spread in avg net/trade must exceed the gap-only spread by **≥ 1pp**, with the direction holding on the H-IND1 cluster bootstrap. Reported per cohort and **never pooled**. **Motivation (2026-07-29 audit).** The composite is a four-factor label over what is, in practice, one or two live factors — and *which* factors are live depends on the universe. On v0.2: `float_score` sd **0.26**, `price_score` sd **0.00** ⇒ 40% of nominal weight contributes **0.0%** of variance; live variance rvol **54.8%** / gap **45.2%**; rank correlation ρ(score, gap) **+0.925** vs rvol **+0.576** vs float **+0.081**. On v0.3: variance rvol **66.0%** / float **26.4%** / gap **7.6%**; ρ rvol **+0.738** / float **+0.529** / gap **+0.395**. **The same formula is a different ranking construct in each cohort**, and ~83% of v0.3 picks are tier A. **Registered prior: the composite adds nothing over gap alone on v0.2, and the cohorts are not comparable.** If that is confirmed, the honest response is to simplify the published model description — not to re-fit weights (P2 forbids promoting an in-sample fit; any re-derivation is H-STR2's job, with its own forward window). **Two-sided and diagnostic:** this is a structural claim about what the score measures, not a performance claim, and it cannot produce a buy/sell rule either way. ### Amendment to H-CTRL (control capture) — 2026-07-29 H-CTRL has been unanswerable because no forward outcome was ever captured for the control pool. `candidates.csv` holds 3,867 rows, but `eligible` is a **reason code, not a boolean**: only **165 rows are eligible**, of which **133 were published (an 81% publish rate)**, leaving **32 eligible-but-unpublished controls across 9 trading days, none graded.** `grade_controls.py` (added 2026-07-29) now grades the unpublished eligibles forward into `control_outcomes.csv` (append-only, forward-only, graded from the same fetch that establishes the entry — so entry and outcome are internally consistent, exactly as `outcomes.csv` is produced for picks). **Two limitations registered now, before any control comparison is read:** 1. **The publish rate is ~81%, so the control pool is small and not a random sample** — controls are by construction the *lowest-scoring* eligible names each day (the screen publishes the top 10 by score). Any screened-vs-unscreened comparison is therefore confounded with score rank and must be read as "top-10 vs the eligible remainder," never as "screened vs comparable unscreened." 2. **Quote-budget truncation.** **707 candidate rows (18%) were never priced at all**, rejection reason `quote_budget` — the scan exhausts its quote allowance before evaluating them. This is a silent, previously undocumented selection effect on the v0.3 cohort. It is **disclosed rather than fixed** for now: raising the budget changes the universe definition, and H-UNIV1 freezes that definition, so a change requires a new registration rather than a quiet tweak. --- ## Registration batch #6 — frozen 2026-07-29 (second registration of the day) Everything in this registry until now asked one question: **does the model predict profit?** The answer is no, and Gate 1 published that today. A follow-up analysis asked a question nobody had tested: **does it predict anything else?** It does — and these two registrations put that claim on the same forward-only footing as every failed one. **Provenance, stated plainly.** Both were found by inspecting the existing log on 2026-07-29. Under P2 that is variable selection, not evidence. Only picks with `trading_date` **strictly after 2026-07-29** count. The in-sample numbers below are recorded so the motivation is auditable and so a later reader can see whether the forward result matched the guess. **An evaluator ships with this registration** (`risk_eval.py`, wired into the daily workflow, writing `reports/risk-eval-LATEST.md` + `risk_snapshots.csv`). The 2026-07-29 audit found six hypotheses that were registered and then never computed; registering these without an evaluator would repeat that failure. ### H-RISK1 — the score ranks MAGNITUDE, not DIRECTION **Rule (frozen).** Per cohort, on post-2026-07-29 graded picks, compute Spearman rho between `score` and (a) `|mae_5d|` (drawdown depth) and (b) `range = mfe_5d − mae_5d`, with a ticker-clustered 95% bootstrap CI (H-IND1: the unit is the name, not the row). **Pass requires ALL of:** n ≥ 30 post-registration picks; rho > 0 with the clustered CI excluding zero for **both** magnitude measures; the sign holding across ≥ 3 consecutive weekly snapshots; **and — the discriminant half — the rho between `score` and signed return REMAINING NON-SIGNIFICANT.** A result where the score predicts magnitude *and* direction fails this hypothesis as stated; the claim is specifically that it separates the two. **In-sample motivation (2026-07-29, ticker-clustered).** v0.2 (n=444, 16 tickers): score→|MAE| rho **+0.206**, score→range **+0.277**, score→same-day return **+0.004 (ns)**. v0.3 (n=80, 67 tickers): **+0.320**, **+0.440**, **−0.054 (ns)**. Mean |rho| across the family was **0.258 for magnitude vs 0.072 for direction**. It survived: replication across two disjoint universes; a within-day test that differences out the market (v0.2 score→range mean rho +0.255, positive on 77% of 30 days, p=0.0001); Benjamini–Hochberg correction across 26 tests (10 survived, the top 8 all magnitude, the 4 worst p-values all direction); an out-of-time split (score→|MAE| +0.149 early → **+0.328 late**, both significant); and a partial correlation controlling for price level (+0.206 → +0.196, +0.440 → +0.443). **Registered prior: this is EXPECTED TO PASS** — and it is registered *because* it is expected to pass. The record currently contains only refutations, which leaves an honest reader unable to distinguish a rigorous instrument from a broken one that returns "no" to everything. A pre-registered confirmation is the missing evidence that this apparatus can detect a real effect, not merely reject false ones. **Registered framing — binding, and not to be dropped if it passes.** A confirmation demonstrates **volatility persistence**, one of the most documented regularities in markets and the basis of GARCH modelling. The score is built from gap and relative volume, both volatility measures, so predicting future volatility from current volatility *should* work. This is the instrument correctly detecting a known effect — **it is NOT alpha, must never be presented as alpha, and does not reopen Gate 1** (failed 2026-07-29). Magnitude without direction is not tradeable here: it would require options, and options on floats this thin are typically absent or spread far wider than the effect. ### H-RISK2 — the risk gauge is CALIBRATED, not merely correlated **Rule (frozen).** **v0.2 cohort only.** Assign each post-registration pick to a quintile using these **frozen absolute score cutpoints** — `≤42.12 | ≤43.90 | ≤46.98 | ≤54.02 | >54.02` — and score the **frozen predicted probabilities** of a deep drawdown (`mae_5d ≤ −20%`): | quintile | Q1 | Q2 | Q3 | Q4 | Q5 | |---|---|---|---|---|---| | predicted P(drawdown ≥ 20%) | 20.22% | 39.56% | 34.88% | 38.20% | 48.31% | **Pass requires both:** a **Brier score beating the no-skill baseline** (the registration-date pooled base rate, **0.3626**), and a realised **Q5 − Q1 gap ≥ 15pp**. **Explicitly NOT applied to v0.3.** The two cohorts have different score distributions (v0.2 median 45.2, v0.3 median 92.5), so these probabilities are declared **non-transferable** here rather than silently reused — the direct consequence of today's H-STR3 cohort-incomparability finding. A v0.3 calibration would need its own registration and its own cutpoints. **In-sample motivation.** Realised P(drawdown ≥ 20%) ran **20.2% (Q1) → 48.3% (Q5)**, a 2.4× spread, with P(≥35%) running 4.5% → 18.0% (4×). A back-dated dry run of the shipped evaluator over post-2026-06-30 data returned Brier **0.2214 vs baseline 0.2379** (beats) with a realised **Q1 15.0% vs Q5 56.4%, gap 41.4pp**. **Registered prior: partial pass expected.** The ordering will very likely hold; the exact probabilities will drift, and the Q2–Q4 plateau (39.6 / 34.9 / 38.2 — non-monotone) is likely to persist, because the gauge is genuinely coarse in the middle. This is a materially stronger claim than H-RISK1 and the one worth publishing if it lands. ### Drafted and deliberately NOT registered today Recorded so they cannot be quietly registered later once more data has been seen: **H-A2** (Finding A re-specified as a continuous within-day rank test rather than the underpowered binary tier filter H-F4 used — A/B is only 11.7% of v0.2 picks but 97.5% of v0.3), **H-STR3-B** (does the composite beat its own best single input for risk while failing to for return?), and **H-SIZE1** (inverse-predicted-range position sizing — the one practical use the evidence supports, and risk management rather than alpha). All three were written out on 2026-07-29; none is registered. Registering any of them later requires a new dated entry and a fresh out-of-sample window that starts then, not today. --- ## Registration batch #7 — EXPERIMENT 02, frozen 2026-07-29 The first test of **somebody else's** published method rather than our own. Experiment 01 (this project's low-float momentum screen, Gate-1 verdict 2026-07-29) is closed and failed; this opens the series proper. Evaluator ships with the registration: `rsi2_scanner.py`, wired into the daily workflow, writing `rsi2_signals.csv` (append-only, logged before the entry session) and `rsi2_outcomes.csv`. ### H-EXP02 — the 2-period RSI mean-reversion trade ("high win rate") **The claim under test.** Buy a large-cap when its 2-period RSI collapses while the stock is still above its 200-day moving average; exit on a short bounce. One of the most widely published retail setups of the last two decades, and almost always marketed on its **win rate**. **Why this claim.** Experiment 01 produced the cleanest possible demonstration that a win rate and an expectancy are different animals: a +5% target returned a **67% win rate at −4.4%/trade**. This strategy is maximally exposed to that confusion. Second reason: Experiment 01's microcap universe had raw drift under 1%/session against a ~2% round-trip cost, so **nothing could have worked there in either direction** — the friction exceeded any available signal. Liquid large caps invert that (≈0.10% round trip), so a real effect is *detectable* and a failure is a failure on the merits. **Rule (frozen — every constant lives at the top of `rsi2_scanner.py`; changing any of them voids the test and requires a new registration with a new window):** - **Universe:** 40 liquid US large caps across sectors, fixed at registration. - **Entry condition** (evaluated after the close): `close > SMA(200)` **and** Wilder `RSI(2) < 5`. If more than five names qualify, take the five most oversold (`MAX_PER_DAY = 5`) so no single day can dominate the sample. - **Entry price:** the next session's open. Signals are logged before that open. - **Exits graded (all three, every trade):** same-day close; 5th-session close; and the published exit — first close with `RSI(2) > 70`, else the 5-session time exit. - **Costs:** 0.10% round trip, applied to every trade, stated in advance. - **Benchmark — the design fix Experiment 01 lacked:** a **day-matched control**, the equal-weight return of the *entire* frozen universe over the identical window, computed from the same fetch. The scored quantity is the **excess** over that control, so market moves difference out. This is the discriminant comparison H-CTRL was meant to supply and never could. - **Window:** only signals with `signal_date` strictly after 2026-07-29 count. **Pass requires ALL of:** n ≥ 30 post-registration graded signals; **both the mean and the median** day-matched excess return positive net of costs (not either — both; Experiment 01 established that means on financial data can be a single lucky trade); a ticker-clustered 95% CI on the excess excluding zero; and the direction holding across ≥ 3 consecutive weekly snapshots. **WIN RATE IS REPORTED BUT IS EXPLICITLY NOT A PASS CRITERION.** Frozen here so it cannot later be substituted for the result if expectancy disappoints. That substitution is the exact failure mode the experiment exists to expose. **Registered prior (stated before any data).** Short-horizon mean reversion in liquid equities is a **real, documented effect** — this is not expected to be nonsense. But this formulation has been public and heavily traded since roughly 2008–09, and published effects tend to get arbitraged. Prediction: **the high win rate replicates (~65–75%) and the day-matched excess is small or zero after costs.** Estimated probability it clears the full bar: **~1 in 3.** A high win rate with no excess return is the *most useful* outcome available, because it is precisely what the strategy is sold on. **Scope limits registered in advance.** A verdict here describes *this rule*, on *these 40 names*, over *this window*. It is **not** evidence about mean reversion in general, and it is **not** a claim about any author, book or service — this tests a **published technique, not a person**. No trade is executed anywhere in this project, in paper or in live money. --- ## Registration batch #8 — EXPERIMENT 03, frozen 2026-07-31 First experiment declared through the new **`experiment_harness.py`** rather than a bespoke scanner. The harness applies the same guarantees to every experiment automatically: forward-only, append-only, a **day-matched control always**, declared costs, and mean + median + ticker-clustered CI reported together, with win rate reported but never a pass criterion. ### H-EXP03 — the MACD bullish crossover **The claim under test.** Buy when the MACD(12,26,9) histogram crosses from at-or-below zero to above zero while the close is above its 200-day simple moving average. Long-only trend following. This is arguably **the most widely taught indicator signal in retail trading** — it ships on every charting platform and appears in essentially every beginner course. **Rule (frozen; constants live in `experiment_harness.py`, and changing any of them voids the test and requires a new registration with a new window):** - **Universe:** the same 40 liquid US large caps as Experiment 02, fixed. - **Entry condition** (evaluated after the close): MACD histogram crosses `<=0` → `>0` **and** `close > SMA(200)`. Max 5 per day, strongest crossover first. - **Entry price:** the next session's open; signals logged before it. - **Exits graded:** same-day close and the 5th-session close. - **Costs:** 0.10% round trip. - **Benchmark:** day-matched — the equal-weight return of the entire frozen universe over the identical window, from the same fetch. The scored quantity is the **excess**. - **Window:** only signals dated strictly after 2026-07-31 count. **Pass requires ALL of:** n ≥ 30 post-registration graded signals; **both mean and median** day-matched excess positive net of costs; a ticker-clustered 95% CI excluding zero; direction holding across ≥ 3 consecutive weekly snapshots. **Win rate is reported but is explicitly not a pass criterion.** **Registered prior.** Published, universally known, and taught to every beginner — which makes it the *least* likely thing in the world to still contain an edge, since anything this widely followed has had eighteen years of arbitrage. Registered expectation: **the day-matched excess is indistinguishable from zero.** Estimated probability it clears the bar: **~1 in 6.** Being widely believed is not evidence, which is precisely why it is worth testing in public. **Scope limits.** A verdict describes *this rule*, on *these 40 names*, over *this window*. It is not a claim about MACD in general, about any author or platform, and it is not advice. No trade is executed anywhere in this project. --- ## Registration batch #9 — EXPERIMENTS 04 + 05 (calendar/timing), frozen 2026-08-06 Two claims surfaced by the 2026-08-06 exploratory calendar sweep (25 declared tests on QQQ, 1999–2026, BH-FDR(25), split-sample, SPY replication — **0 of 25 survived FDR in-sample**, which is exactly why these are registered forward rather than believed backward). Both are TIMING claims on a single asset, so they run on **`calendar_eval.py`**, not `experiment_harness.py`: the harness's day-matched control is cross-sectional (a signal vs its universe), and for a timing claim on one ticker the universe IS the position — the correct control is **time-matched** (other sessions, or the same session's other leg). All other harness guarantees carry over unchanged: forward-only, append-only, declared costs, mean AND median AND clustered 95% CI together, win rate reported but never a pass criterion, constants frozen — changing one voids the test. Calendar claims have a property worth recording: **there is no signal-capture race.** Whether a future session is a turn-of-month session is fixed by the exchange calendar; every session has an overnight and an intraday leg. The Experiment-01 pre-open failure mode cannot occur here by construction. Grading is derived, idempotent, and can lag without bias. ### H-EXP04 — the turn-of-month effect **The claim under test.** QQQ's mean close→close return on turn-of-month sessions — the **last 4 plus first 3 trading days of each month** — exceeds its mean on all other sessions. Documented in the academic literature since the late 1980s (Ariel; Lakonishok & Smidt) and still sold today in seasonality newsletters and "smart timing" content — a publicly documented TECHNIQUE, not a named person. **Rule (frozen; constants live in `calendar_eval.py`):** - **Asset:** QQQ decides. SPY graded in parallel as a replication read — reported, never a pass criterion. - **Window definition:** last 4 + first 3 trading days, derived from the exchange calendar itself. The final (incomplete) month of any fetch grades only its first-3 sessions, since its last-4 flags are not yet determined and outcomes are append-only. - **Scored quantity:** per-TOM-session excess over the contemporaneous non-TOM mean, forward window only. - **Costs:** the claim is scored gross at day level; the strategy expression (~12 round trips/yr) is reported with a 0.02%/RT footnote — at that frequency costs cannot decide the verdict either way, which is one reason this claim was chosen (selection rule #2). - **Window:** only sessions strictly after **2026-08-06** count. n ≥ **30 TOM sessions** (~4½ months, expected verdict window around **2026-12**). **Pass requires ALL of:** n ≥ 30 post-registration TOM sessions; TOM mean AND median both above the non-TOM mean and median; a **month-clustered** 95% CI of the TOM excess excluding zero (sessions inside one month are not independent evidence); direction holding across ≥ 3 consecutive weekly snapshots. Win rate reported only. **Registered prior.** In the 1999–2026 backtest the effect is directionally stable in all three decades and replicates in SPY (t = 2.43 there), but the QQQ t is only 1.41 and the family-wide FDR pass rate was zero. Forty years of publication is forty years of arbitrage opportunity. Registered expectation: **more likely than not, no edge** — estimated probability it clears the bar: **~1 in 3** (the highest prior yet registered, and deliberately so: this is the strongest surviving candidate from a 25-test sweep, and the register-then-watch discipline is the point). **Scope limits.** A verdict describes this window definition on QQQ over this period. It is not a claim about seasonality in general and not advice. No trade is executed. ### H-EXP05 — overnight vs intraday (an ATTRIBUTION claim, explicitly not a trading claim) **The claim under test.** QQQ's overnight leg (previous close → open) exceeds its intraday leg (open → close), per session. In the 1999–2026 backtest this is the strongest structure in the data: $1 compounded overnight-only grew to ~$35 while intraday-only fell to ~$0.47; the paired difference is +5.6 bp/session (t = 2.71) and positive in every 5-year block. The claim was literally productised — the NightShares "night effect" ETFs — and those funds **closed in July 2023**, which is precisely why the registered scope stops at attribution. **Rule (frozen; constants live in `calendar_eval.py`):** - **Asset:** QQQ decides; SPY replication read only. - **Scored quantity:** the per-session **paired difference** overnight − intraday — the same day is its own control, the cleanest control in the project. - **Costs:** none apply to an attribution claim; the report carries a permanent tradeability footnote (capturing the overnight leg costs one round trip per session; at 0.02%/RT the mean must exceed 2 bp/session net just to break even, before slippage and taxes). - **Window:** only sessions strictly after **2026-08-06** count. n ≥ **30 sessions** (~6 weeks, expected first verdict window around **2026-09**). **Pass requires ALL of:** n ≥ 30; mean AND median paired difference positive; a **week-clustered** 95% CI excluding zero; direction holding across ≥ 3 consecutive weekly snapshots. Win rate reported only. **Registered prior.** Backed by a large academic literature and 27 years of in-sample structure, but the gap has been narrowing (intraday positive since 2010) and six weeks is a short window for a ~5 bp/day effect against ~100 bp/day noise — power is the risk, not direction. Registered expectation: **direction positive but quite possibly not resolvable at n = 30; ~1 in 3 it clears at the first snapshot**, higher if allowed to accrue. **BINDING SCOPE NOTE (mirrors H-RISK):** a pass means the attribution is real over the window. It does NOT mean the effect is tradeable at retail, and it must never be presented as a tradeable edge — the NightShares closure is the cited evidence for why. **Scope limits.** Attribution on QQQ over this window; not advice; no trade executed. --- ## Registration batch #10 — EXPERIMENTS 06–09 (the Tier-A retail-technique family), frozen 2026-08-06 Four techniques currently sold to retail traders, selected from a 2026-08-06 survey of what is being discussed and sold (Supertrend/"one indicator" video content; swing-trading course pullback entries; the high-win-rate mean-reversion pitch; breakout-course volatility contraction). All four are **cross-sectional signal claims on the frozen 40-name large-cap universe**, so they run on `experiment_harness.py` with every harness guarantee: forward-only, append-only, day-matched control (the scored quantity is the EXCESS), 0.10% round trip declared, mean AND median AND ticker-clustered 95% CI together, win rate reported but never a pass criterion, constants frozen — changing one voids the test. Shared mechanics: entry next open, exits at the same-day close AND the 5th-session close, max 5 signals/day per experiment with a declared tie-break. n ≥ 30 per experiment before any verdict. **Numbering note.** These were drafted as EXP04/05/06/08 and renumbered to **EXP06–EXP09** before any signal was logged or scored, because batch #9 (registered ~4 minutes earlier the same evening) took EXP04/EXP05 for the calendar experiments. An ID is a label, not a frozen constant; no data existed under the old labels. **FAMILY POLICY, declared before any result exists.** With EXP02–EXP09 running concurrently (~8 experiments at ~1-in-6 priors), **approximately one chance pass is EXPECTED across the family**. The published family verdict applies Benjamini–Hochberg FDR across all concurrently registered experiments; a single pass is reported as *consistent with chance* until it survives that correction and a fresh forward window. EXP06–EXP09 share one universe, so they are **correlated tests, not independent replications** — same-day signal overlap across experiments is reported alongside the verdicts. ### H-EXP06 — the Supertrend flip Supertrend(10, 3), Wilder ATR, trend flips −1 → +1 at the close. Deliberately **no trend filter** — the claim as sold has none; adding one would test our idea, not theirs. Tie-break: largest distance of the close above the flip line. Registered prior: the most heavily marketed single indicator in current retail video content, at exactly these default settings, on forty of the most liquid names on earth — expectation **excess indistinguishable from zero; ~1 in 6 it clears**. ### H-EXP07 — the moving-average pullback Close above SMA(200); today's low touches or pierces SMA(20); close back above SMA(20). Tie-break: deepest touch first. Registered prior: the most widely taught swing entry in existence; the mechanism (short-term reversion inside medium-term momentum) is at least coherent, which earns the highest prior in this batch: **~1 in 5**. Expectation is still zero excess — textbook status is what arbitrages an edge away. ### H-EXP08 — Bollinger Band mean reversion Close below the lower Bollinger Band (20, 2.0) with the close above SMA(200) — the taught, Connors-style long-only version. Tie-break: most negative z-score first. Registered prior: the same high-win-rate sales pitch as EXP02's RSI(2) through a different mechanism; win-rate-flattering by construction (many small reverts, occasional large losses) — exactly the shape the mean/median/clustered-CI reporting exists to expose. **~1 in 6.** ### H-EXP09 — volatility contraction (NR7) in an uptrend Today's high–low range strictly the narrowest of the last 7 sessions, close above SMA(200). Tie-break: narrowest relative range first. **Disclosed deviation:** the sold version buys an intraday break of the range; ours enters at the next open because the pre-open logging gate forbids acting on the open print. What is tested is "contraction precedes upward expansion in uptrends," and every publication of this experiment must say so. Registered prior: contraction preceding expansion is documented (Crabel); the **direction** is the sold part and the part with no documented edge. **~1 in 6.** **Deferred from the same survey** (with reasons, so they are not re-litigated casually): gap-and-go continuation (frequency on a large-cap universe needs a dry-scan check first; microcap version fails on costs per EXP01), TTM Squeeze (needs a Keltner built-in), opening range breakout and ICT/fair-value-gaps (intraday data the project does not ingest), 0DTE and wheel strategies (options cost model), congress-trade copying (needs a disclosure feed), AI-picker services (named operators — WEDGE gate, counsel required). **Scope limits.** Each verdict describes its frozen rule on this universe over its window. Not advice; no trades executed. --- ## Amendment to H-EXP04 / H-EXP05 (calendar experiments) — 2026-08-07 **Registration dates are UNCHANGED (2026-08-06). Zero outcome rows had been graded when this amendment was made** — the first grade run had not yet occurred, so no observed data informed any part of it. This is recorded in full because the standard this project holds others to is that the *apparatus* gets audited, not just the measurements. An adversarial review one day after registration found six defects in `calendar_eval.py`. Four were bugs in the measurement apparatus and were simply fixed. Two changed the pass bar, and those are amended here. ### Fixed without changing the registered rule (apparatus bugs) - **Partial-bar bias, asymmetric.** The incomplete-month guard deferred every non-TOM session of the current month, so the only sessions gradeable on the day they occurred were positions 0/1/2 of a month — which are *always* turn-of-month. A grade run before the closing bell would have frozen a live intraday snapshot into the treatment arm and never into the control arm. The CI cron is 21:00 UTC, which is 4:00pm ET in winter — the bell itself, in the months EXP04's verdict lands. The evaluator now never grades the final fetched session. - **Truncated leading month.** TOM position was derived from the fetched session list, so the first (partial) month of the ~400-day window had its first three *fetched* sessions flagged turn-of-month. The evaluator now never grades sessions in the window's first month. - **Zero-byte outcomes file.** An interrupted first run left an empty CSV with no header; the first data row then became the header and grading raised `KeyError` forever, swallowed by the catch-all so CI stayed green while nothing was collected. Fixed here and in `experiment_harness.py`, which carried the identical bug and therefore exposed EXP03. - **Wrong clustering unit.** The last 4 sessions of month M and the first 3 of month M+1 are one contiguous 7-session run of market time — the most correlated observations in the sample — but were keyed to two different calendar months, understating that correlation. The cluster is now the turn-of-month **cycle**, which also puts each cycle's control sessions in the same cluster as its treatment sessions, making the comparison contemporaneous by construction. ### Amended pass bar (this is the part that changes what the experiments must clear) - **The confidence interval was the CI of the wrong quantity.** The control mean was computed once and subtracted as a *constant* before bootstrapping, so none of the control arm's sampling uncertainty reached the interval. Both arms are now resampled and recomputed inside every bootstrap draw. - **Too few clusters, and a verdict republished at every look.** n>=30 sessions is only about five clusters, and the verdict line was recomputed on every run with no alpha spending — so across a year of looks a no-effect claim had roughly a 1-in-5 chance of printing a pass at least once. **Both experiments now additionally require a minimum cluster count, and no verdict of any kind is computed or displayed until it is met:** | | registered 2026-08-06 | amended 2026-08-07 | single verdict date | |---|---|---|---| | H-EXP04 | n>=30 TOM sessions | n>=30 **and >=12 complete turn-of-month cycles** | **2027-09-01** (was ~2026-12) | | H-EXP05 | n>=30 sessions | n>=30 **and >=20 ISO weeks** | **2027-01-04** (was ~2026-09) | **A floor alone was not enough.** It delays the first look, but after it the verdict would still have been recomputed on every run, and the alpha leak returns. So each experiment now also has **ONE pre-declared verdict date**, above. The verdict is computed at the first run on or after that date at which the floors are met, written once to an append-only `experiments/EXP0405-CAL-verdicts.csv`, and thereafter **displayed from that file and never recomputed**. Re-running the evaluator on any later data cannot change a locked verdict, and that is verified by a test: lock a pass, flip the underlying data to strongly negative, re-run across four later dates, and the output is byte-identical. One experiment, one look, fixed in advance. All other pass criteria are unchanged: mean **and** median both in the claimed direction, a clustered 95% CI excluding zero, direction holding across >=3 consecutive weekly snapshots, and win rate reported but never a pass criterion. ### The residual, measured and published rather than assumed away Simulating the shipped estimator under the null (no effect), the one-sided false-positive rate of the `CI low > 0` test is: | clusters | false-positive rate (nominal 2.5%) | |---|---| | ~5 (the original bar) | 7.6% — and **12.1%** before the frozen-control-mean fix | | 8 | 5.1% | | **12 (the amended EXP04 floor)** | **4.2% ± 0.5%** | | 20 | ~4.5% (within noise of 12) | A percentile cluster bootstrap stays modestly anti-conservative at any cluster count reachable in a sane window, and pushing the floor past 12 buys nothing measurable while costing years. So the floor is 12 and the residual is disclosed on the live report: a bare "clears the bar" on EXP04 should be read as roughly a **1-in-24** false-positive risk, not 1-in-40. **Why amend rather than void.** Voiding and re-registering would reset the window for no gain: the claims, the universe, the window definitions, the control design and the registration date are all untouched, and not one row of data had been observed. Amending a pass bar *after* seeing results would be indefensible; amending it before any result exists, and publishing the diff, is the honest version. Recorded here so the change is checkable against git history. **Known and NOT fixed here:** `experiment_harness.py` republishes its verdict at every look with no alpha spending, exactly as `calendar_eval.py` did. That affects **EXP02 and EXP03**, which already have graded data, so amending their bar mid-flight is a separate decision with its own disclosure requirement. Logged, not silently carried. --- ## Amendment to the EXPERIMENT HARNESS (H-EXP03, H-EXP06 … H-EXP09) — 2026-08-07 The same adversarial review that produced the calendar-experiment amendment above found that `experiment_harness.py` had the identical unlimited-looks property, and it was live for every experiment the harness runs. Fixed the same day, with the same disclosure standard. **What was wrong.** From `n >= 30` graded signals onward the verdict line was recomputed on **every run** — daily in CI — with no alpha spending. A claim with no real effect therefore had roughly a **1-in-5 chance of printing "clears the bar" at least once** across a year of snapshots. The registered "direction holding across >=3 consecutive weekly snapshots" rule is a partial mitigation, but it does not control the error rate. **What changed — reporting logic only.** 1. **A cluster floor: >= 20 distinct names.** `n` counts trades, but the clustered CI's precision is governed by the number of distinct tickers, since repeated bets on one name are not independent evidence. Thirty trades spread over four names is not thirty pieces of evidence. (This is the H-IND1 effective-sample-size finding applied to the pass bar.) 2. **One pre-declared verdict date per experiment: 2026-11-02.** A floor alone only delays the first look. The verdict is now computed at the first run on or after that date at which both floors are met, written once to an append-only `experiments/HARNESS-verdicts.csv`, and thereafter displayed from that file and **never recomputed**. Verified by test: lock a pass, flip the underlying data to strongly negative, re-run across three later dates — the output is identical and the verdicts file still holds exactly one row. 3. Any future declaration that omits an explicit `verdict_on` gets one automatically (registration + 90 days), so a new experiment cannot ship with unbounded looks by oversight. **Why this is not the thing we criticise other people for.** Three reasons, and all three have to hold: - **No result had been observed.** At the moment of the change, **zero graded outcome rows existed for any harness experiment** — signals had been logged since 2026-07-31, but none had matured, so there was nothing to see and nothing informed the change. The outcomes files did not exist yet. - **The dates were not chosen from the data.** 2026-11-02 is the batch's already-planned continue/kill read date, recorded before this review, and was carried over deliberately rather than picked now. - **The amendment can only make a pass HARDER.** It adds a floor and removes looks; there is no configuration of the data under which it makes "clears the bar" easier to print. A mid-flight change that can only reduce the chance of declaring your own success is safe in a way that a loosening change never is. If we ever propose one that runs the other way, it should be refused. **Not affected: H-EXP02.** Experiment 02 runs on its own `rsi2_scanner.py`, which prints a maturity flag only and declares no automated verdict, so it never had the republishing problem. The same one-look discipline applies when its verdict is written up by hand: fix the evaluation date before looking. **Unchanged:** every registered rule, universe, entry condition, exit, cost assumption and registration date. No stored signal or outcome row was altered by this amendment.