# S/R levels: detection quality, the target exit, and the entry gate

**Date:** 2026-07-12
**Question that started it:** are our support/resistance levels built the way best
practice says they should be, and do we actually use them that way?

Short answer: the detector is weak against best practice, but its reach into P&L
runs entirely through the **entry gate** — not the exit. Honoring the target as a
take-profit was tested and is decisively worse. Whether the S/R-derived gate is
net-positive is the open question, tracked below.

---

## 1. How the levels are built today

> **Update (2026-07-12 detector rewrite):** several gaps below were addressed in
> `sr_service` / `indicator_service` — close-bin VP, local-peak HVN, POC/VAH/VAL
> as candidates, LVN dropped from S/R, pivot prominence + lookbacks, rejection-
> weighted recency strength, ATR-adaptive merge, hard cap, round numbers. The
> table documents the *pre-rewrite* failure modes measured on the snapshot; keep
> it for historical context. Re-measure density on prod after deploy if gate
> rates shift.

`app/services/sr_service.py::detect_sr_levels` (post-rewrite):

1. Candidates = VP **POC / VAH / VAL / local HVN peaks** (lookback 252) +
   **prominent** swing pivots (lookback 504) + nearby **round numbers**.
2. Strength = rejection-weighted touches on last 252 bars with recency decay
   (pass-throughs down-weighted); method base + confluence on merge.
3. Nearby levels merged with **ATR-adaptive** tolerance (clamped ~0.4–1.5%);
   capped (~16, interleaved S/R); tagged `support` if below spot, else `resistance`.

### Where the pre-rewrite detector departed from best practice

Measured on `backtest_snapshots/prod.sqlite` (AAPL, 1261 bars, spot $308.63):

| Gap | Evidence |
|---|---|
| **POC / VAH / VAL are computed then discarded.** `sr_service` reads only `hvn`/`lvn`. The canonical volume-profile levels never become S/R. | POC $148.32, VAH $230.45 — unused |
| **HVN = "any bin above the mean"**, so nearly every bin is a candidate. A real HVN is a *local peak* in the histogram. | 8 of 20 bins HVN, other 12 LVN → 73 levels, median spacing $2.44 (0.79% of spot) — a price grid, not detected structure |
| **HVN and LVN are scored and used identically**, though they encode opposite dynamics (acceptance vs. rejection). | both appended as plain candidates |
| **Volume is double-counted**: a bar's full volume is added to *every* bin it spans rather than distributed. | binned total = 1.48× true volume |
| **"Touch" = level fell inside the bar's range** — a pass-through counts the same as a rejection. Strength therefore measures *how central a price is in the 5-year range*, not how often price reversed there. | 21 of 73 levels pin at exactly 100 → the `sr_strength` magnet in the probability model is near-constant |
| **No recency decay, unbounded lookback.** | 35 AAPL "support" levels sit >35% below spot |
| **Round-number levels absent** — the mechanism with the best empirical support ([Osler 2000](https://papers.ssrn.com/sol3/papers.cfm?abstract_id=888805)). | not implemented |

Not a defect: the pivot `window=2` is the standard 5-bar Williams fractal. What it
lacked pre-rewrite is a **prominence filter** — AAPL yielded 338 pivots over 1261
bars, one every ~3.7 bars.

### The structural problem: resistance famine

Levels are tagged relative to spot, so a stock near its highs has almost nothing
above it. Across all 504 tickers in the snapshot, grouped by proximity to the
52-week high:

| Population | Median resistance levels | % with <3 |
|---|---|---|
| **≥98% of 52w high — what the momentum gate buys** | **1** | **64%** |
| 90–98% | 7 | 12% |
| <90% | 22 | 0% |

AAPL at $308: **71 support levels, 2 resistance levels.** 26 tickers have *zero*.

This matters because `_build_setups_at` does `if not targets: continue` — **no
resistance above ⇒ no long setup at all**, and `<3 targets` adds a
`target-availability` conflict. The detector is structurally most blind exactly
where the momentum edge is strongest. `recommendation_service.py:521` already says
so out loud: *"price is extended near highs (no resistance target above), so no
high-conviction long setup is available."*

---

## 2. Does the target even act as an exit? No.

Production runs `paper_exit_mode = "atr_trailing"` (`DEFAULT_EXIT_MODE`), and
`_atr_trailing_close(direction, entry, init_stop, atr_multiplier, hold_days, ...)`
**does not take `target` as a parameter**. Only the non-default `mode == "target"`
branch consults it.

So the S/R target's real causal role is:

1. the **entry gate** — `rr ≥ 1.5`, primary-target `prob ≥ 20%`, `≥3 targets`, and
   no-resistance-above ⇒ no setup;
2. the **displayed** target table.

It decides *whether you enter* and plays no part in *how you exit*.

---

## 3. Experiment: should the target be honored as a take-profit? — REJECTED

Dennis's proposal: keep the 3× ATR trail, but also take profit when the S/R target
is hit. This was not representable in the simulator (`exit_policy` is one string;
the existing `"target"` policy *replaces* the trail). Added `atr_trail3_target`,
which runs both — trade ends at whichever comes first.

Identical 80/20 momentum entry and qualification for every row — the exit is the only
policy that changes. (Trade counts still vary 303–427, because exits free portfolio
slots at different times; the conclusion is robust to that.)
Report: `reports/backtest-20260712-sr-target-exit.json`

| exit policy | Sharpe | CAGR | MaxDD | trades | win% |
|---|---|---|---|---|---|
| `low20` | 2.04 | 53.2% | 21.9% | 305 | 37.7 |
| **`atr_trail3` (production)** | **2.04** | **50.4%** | **21.4%** | 320 | 37.5 |
| `hold` | 2.00 | 51.9% | 22.2% | 303 | 38.6 |
| `technical40` | 2.00 | 51.9% | 22.2% | 303 | 38.6 |
| `sma50` | 1.76 | 40.8% | 24.4% | 385 | 33.8 |
| `target` (take-profit, no trail) | 1.59 | 32.4% | 25.0% | 415 | 41.9 |
| **`atr_trail3_target` (trail + take-profit)** | **1.47** | **28.9%** | 23.5% | 427 | 40.0 |

**Decision: do not ship. The target must not become an exit.**

- Adding the take-profit to the trail: Sharpe **2.04 → 1.47**, CAGR **halved**
  (50.4% → 28.9%), and drawdown got *worse* (21.4% → 23.5%). No risk compensation.
- **Win rate rose** (37.5% → 40.0%) — the tell. You win more often and earn far
  less: the take-profit converts the few 5R/8R/15R runners into 1.5R wins while
  every loser still costs a full −1R. Momentum's edge is that right tail.
- The combination (1.47) is worse than the take-profit alone (1.59): once upside is
  capped at the target, the trail's benefit (riding a winner far past any target)
  is gone but its cost (shakeouts on pullbacks) remains. Worst of both.

This confirms and extends the note at `backtest_service.py:450` — swept *fixed*
take-profits never found an interior optimum; the S/R target is no better.

Caveat: single in-sample run over full history. The effect is large (CAGR halved),
not marginal.

---

## 4. Open: is the S/R entry gate net-positive?

The target is now proven useless as an exit, so the gate is its **only**
justification — and the gate is what starves the momentum names.

Evidence *for* keeping it (`gate_ablation`, prod baseline): dropping the R:R floor
**halves per-setup expectancy**, 0.583 → 0.301 net avg R (`momentum_only` = 0.345).
Inside the tradeable pool the S/R-derived R:R floor is doing real selection — it
favors names whose nearest resistance is far away, i.e. clear air above.

But that ablation **cannot see the famine**: it re-qualifies candidates that already
exist, and starved names never enter the candidate set (`if not targets: continue`).
So "remove the floors" is the wrong test — it just reproduces the rows above.

**The right test changes target *generation***: when a direction has no S/R target,
synthesize one at k×ATR so the name becomes a candidate. One variable moves; the
previously-vetoed names now trade. Implemented behind
`BACKTEST_ATR_TARGET_FALLBACK=<k>` (k=3 matches the trail; rr = 3/1.5 = 2.0, which
clears the 1.5 floor, and an aligned momentum name lands ~34% probability, clearing
the 20% floor).

Read the result against the production baseline (`atr_trail3`, Sharpe **2.04**):

- **> 2.04** → the veto costs money; let the breakouts in.
- **≈ 2.04** → famine is a wash; a detector rewrite is cosmetic.
- **< 2.04** → the veto earns its keep by keeping us out of over-extended names, and
  S/R gating is vindicated.

### Result: the veto EARNS ITS KEEP. Keep S/R in the gate.

Treatment `reports/backtest-20260712-sr-gate-ablation-treatment.json` vs control
`reports/backtest-20260711-prod-baseline.json`. Admitting the vetoed names is a big
change: **qualified setups go 1089 → 4230 (~4×)**.

Production exit (`atr_trail3`), full history:

| | Sharpe | CAGR | MaxDD | Calmar | trades |
|---|---|---|---|---|---|
| control (veto ON) | **2.04** | 50.4% | 21.4% | 2.36 | 320 |
| treatment (veto OFF) | **1.82** | **58.6%** | 21.0% | **2.79** | 404 |

Full history alone looks like a genuine trade-off — more return, more volatility,
Sharpe down but Calmar up. **The lookback split is what settles it:**

| window | control (veto ON) | treatment (veto OFF) |
|---|---|---|
| **6m** | **Sharpe 2.87, CAGR 76.6%, DD 8.1%** | Sharpe 1.50, CAGR 53.6%, **DD 15.8%** |
| **1y** | **Sharpe 2.47, CAGR 66.8%, DD 8.8%** | Sharpe 1.69, CAGR 66.0%, **DD 15.8%** |
| 3y | Sharpe 2.12, CAGR 52.3%, DD 17.7% | Sharpe 2.11, CAGR **75.9%**, DD 21.0% |
| 5y | Sharpe 1.83, CAGR 38.8%, DD 21.4% | Sharpe 1.62, CAGR 44.9%, DD 21.0% |
| all | Sharpe 2.04, CAGR 50.4%, DD 21.4% | Sharpe 1.82, CAGR 58.6%, DD 21.0% |

Per-setup expectancy: `all_floors` net avg R **0.583 → 0.280**.

**Decision: do not ship the fallback. Keep the gate as it is.** The flat 3×ATR
fallback is worse on Sharpe and on per-setup expectancy, and production needs no
further defense than that.

### But be careful what this run does and does not prove

**It does not isolate the famine hypothesis.** The fallback fires on *any* empty
`generate_targets` result — and that includes the ATR/R:R distance filters in
`TargetGenerator` (target closer than 1 ATR, or beyond `max_atr_multiple`), not just
"no resistance above." Measured at the last bar across 502 tickers, of the long
setups the fallback admits:

- **26 (35%)** have genuinely *no resistance above* — the clear-air famine case
- **49 (65%)** *do* have resistance above; the ATR/R:R filters rejected it — **a
  different population entirely**

That matches the report's own tell: qualified setups exploded **1089 → 4230 (~4×)**
while candidates rose only ~16%. So the degradation may be driven mostly by that
65%, and the clear-air breakouts this investigation was *about* are a minority of
what was admitted.

**What the run actually supports:** *"a flat 3×ATR fallback for all S/R-starved
setups degrades performance."* It does **not** support the stronger claim that a
stock in clear air is a worse risk-adjusted buy, or that the veto is functioning as
an over-extension filter. That mechanism is unproven.

**The window split is also less clean than it first looks.** The verdict rests on the
two *smallest* samples — 6m (n=30) and 1y (n=72) — where Sharpe 2.87 is
noise-dominated. The statistically sturdier 3y window (n=230 → 303) shows
**equal Sharpe (2.12 vs 2.11) with substantially higher treatment CAGR (52.3% →
75.9%)**. Full-history Calmar also favors the treatment (2.79 vs 2.36). So the result
is metric- and window-dependent; only the flat-fallback rejection is solid.

**Second contamination (by design):** the fallback gives every admitted name the same
`rr = 3/1.5 = 2.0`, so there is no R:R discrimination *within* the admitted set.

**To actually test the famine**, the fallback must fire *only* when there is no
resistance above (not on ATR/R:R filter misses). That is the clear-air run below.

---

## 4b. The clean test: fire the fallback ONLY in clear air — **the veto DOES cost money**

`BACKTEST_FALLBACK_CLEAR_AIR_ONLY=1` restricts the fallback to setups with no S/R
level ahead at all, excluding the 65% that were merely ATR/R:R distance-filter
misses. Same whole-portfolio simulation, same 10-slot book, same momentum ranking.

Report: `reports/backtest-20260712-sr-gate-ablation-clearair.json`

**Production exit (`atr_trail3`), full history:**

| arm | Sharpe | CAGR | MaxDD | Calmar | trades |
|---|---|---|---|---|---|
| control — veto ON (production) | 2.04 | 50.4% | 21.4% | 2.36 | 320 |
| blanket fallback (contaminated) | 1.82 | 58.6% | 21.0% | 2.79 | 404 |
| **clear-air-only fallback** | **2.07** | **62.3%** | **20.1%** | **3.10** | 363 |

**Strictly better than production on all three headline metrics at once** — higher
Sharpe, ~12 points more CAGR, *and* lower drawdown. Qualified setups 1089 → 2072
(vs. 4230 for the blanket version).

**By lookback** (production strategy):

| window | control (veto ON) | clear-air fallback |
|---|---|---|
| 6m (n=30→38) | Sharpe 2.87, CAGR 76.6%, DD **8.1%** | Sharpe 2.21, CAGR 78.8%, DD 13.0% |
| 1y (n=72→86) | Sharpe 2.47, CAGR 66.8%, DD **8.8%** | Sharpe 2.28, CAGR **87.6%**, DD 12.9% |
| **3y** (n=230→270) | Sharpe 2.12, CAGR 52.3%, DD 17.7% | **Sharpe 2.18, CAGR 68.6%, DD 14.3%** |
| **5y** (n=320→363) | Sharpe 1.83, CAGR 38.8%, DD 21.4% | **Sharpe 1.85, CAGR 47.6%, DD 20.1%** |
| **all** | Sharpe 2.04, CAGR 50.4%, DD 21.4% | **Sharpe 2.07, CAGR 62.3%, DD 20.1%** |

In every statistically sturdy window (3y, 5y, all) the clear-air fallback wins on
Sharpe, CAGR **and** drawdown. The short windows (6m n=30, 1y n=72 — noise-dominated)
favor control on Sharpe/DD while the treatment still earns more (1y CAGR 66.8% →
87.6%).

**This reverses §4 and confirms the hypothesis that opened the investigation.** The
S/R veto on clear-air names *was* costing money; the blanket run masked it because
the 65% loophole population (ATR/R:R filter misses) is genuinely bad and dominated
the result. Isolate the two, and they pull in opposite directions:

- clear-air names (no resistance above): **portfolio-accretive**
- ATR/R:R distance-filter misses: **portfolio-destructive**

Per-setup expectancy is consistent with this: net avg R `all_floors` — control 0.583,
clear-air 0.402, blanket 0.280. The admitted clear-air setups are individually a bit
weaker, but they carry the highest momentum ranks, so they win book slots and deliver
outsized portfolio returns.

**Caveats before shipping:** in-sample, single snapshot; the fallback still assigns a
constant `rr = 2.0` to every admitted name (no discrimination within the set). Needs
an out-of-sample run before production — see §4c, which is where it comes undone.

---

## 4c. Out-of-sample holdout — **the §4b result does NOT survive**

Everything in §4b is in-sample: the rule was chosen by looking at the same 5 years it
was then graded on. The `portfolio_monitor` lookbacks (6m/1y/3y/5y) are **not** a
holdout — they are nested windows all ending today, so each one overlaps the data the
idea came from.

Real split (`BACKTEST_HOLDOUT_SPLIT=2024-07-01`, production strategy, disjoint books):

- **train** = entries before 2024-07-01 (~3y)
- **test** = entries on/after 2024-07-01 (~2y, never informed the rule)

Reports: `reports/backtest-20260712-holdout-control.json`,
`reports/backtest-20260712-holdout-clearair.json`

| window | arm | Sharpe | CAGR | MaxDD | trades |
|---|---|---|---|---|---|
| train (2022-06 → 2024-08) | control | 1.31 | 29.6% | 21.4% | 174 |
| train | **clear-air** | **1.63** | **42.6%** | **20.1%** | 191 |
| **test** (2024-07 → 2026-07) | **control** | **2.78** | 73.3% | **11.7%** | 150 |
| **test** | clear-air | 2.45 | **83.0%** | 14.3% | 176 |

> **Harness bug, found and fixed 2026-07-12.** The train row first reported Sharpe 0.95 /
> CAGR 14.6% — wrong. Its equity curve ran to the *end of the data* while its entries
> stopped at the split, so the book sat in flat cash for two years and deflated its own
> metrics. `_simulate_portfolio` now truncates the calendar to `hold_days` after the last
> entry whenever `end_date` is set. **The verdict is unaffected** — it rests on the test
> row, whose entries and curve both start at the split and were always clean. But the
> broken numbers *looked* like a result, and nearly produced a false conclusion ("the
> first half of the sample was mediocre"). Corrected numbers above.

**In train the clear-air rule wins on every metric. Out of sample it does not.** On
the held-out two years it delivers **more raw return (+9.7pp CAGR)** but at
**lower Sharpe (2.78 → 2.45)** and **higher drawdown (11.7% → 14.3%)**.

So the §4b headline — *"strictly better on all three metrics"* — was **an in-sample
artifact.** Out of sample the rule is not a free win; it is a **risk/return trade**:
it buys extra return by taking more risk, and on a risk-adjusted basis it is slightly
*worse* than production.

**Decision: do NOT ship the clear-air fallback.** This project's decision metric is
Sharpe throughout (every ranking in the report, and the 2026-07-10 primary-target A/B
was accepted on Sharpe 1.51 → 2.00). By that standard the honest read of the only
uncontaminated evidence is *no improvement*.

Notes for anyone revisiting:
- Both arms show a large regime shift (train Sharpe ~1.3–1.6, test Sharpe ~2.5–2.8) —
  the test window was simply a much better market. That is why *relative* comparison
  within a window is the only valid read.
- n = 150/176 in test is decent but not large; the Sharpe gap (0.33) is not
  overwhelming. This is "not confirmed," not "definitively refuted."
- The famine hypothesis is therefore **real but not exploitable as tried**: the
  clear-air names do add return (consistently, in both train and test), but the flat
  3×ATR target admits them at a risk cost that eats the risk-adjusted benefit. A
  better target model for those names (§ next runs) is the remaining avenue.

A wholesale "ATR target for everyone" variant was deliberately *not* run as the
headline: with a fixed k×ATR target and a 1.5×ATR stop, `rr = k/1.5` is constant
across every name, which erases the very selection the 0.301 credits. A loss there
would be uninterpretable.

---

## 5. Reproducing

Both research paths are **off by default** — the default report is byte-identical to
the shipped baseline (5 exit rows, no fallback), and the full unit suite including
the backtest↔prod parity guard passes.

```bash
# Exit book incl. the rejected take-profit rows
BACKTEST_RESEARCH_EXITS=1 python scripts/run_backtest_snapshot.py \
    backtest_snapshots/prod.sqlite --workers 7 --allow-spawn

# S/R gate ablation: synthesize a 3xATR target where S/R offers none
BACKTEST_ATR_TARGET_FALLBACK=3 python scripts/run_backtest_snapshot.py \
    backtest_snapshots/prod.sqlite --workers 7 --allow-spawn
```

Note `--allow-spawn` is required on Windows: `_mp_context()` has no `fork`/
`forkserver` there and silently falls back to a single thread without it.

---

## 6. Standing decisions

**Measured:**

1. **The target must not be an exit.** Tested, rejected, decisively — Sharpe
   2.04 → 1.47, CAGR halved. Momentum's edge is the right tail; a take-profit
   truncates it. (§3)
2. **Do NOT ship the clear-air fallback — it failed out-of-sample.** In-sample it
   looked strictly better (Sharpe 2.04 → 2.07, CAGR 50.4% → 62.3%, DD 21.4% → 20.1%),
   but on a genuine holdout (entries after 2024-07-01, never seen by the rule) it is
   **worse on Sharpe (2.78 → 2.45) and Calmar, better only on raw CAGR (+9.7pp)**. The
   in-sample "free win" was an artifact. **Production gate stays as-is.** (§4b, §4c)
3. **The famine is real, but not exploitable as tried.** Clear-air names *do* add
   return consistently (train and test) — the veto genuinely leaves money on the
   table. But a flat 3×ATR target admits them at a risk cost that cancels the
   risk-adjusted benefit. (§4c)
4. **Do NOT relax the veto indiscriminately.** The ATR/R:R distance-filter misses
   (65% of a blanket fallback) are portfolio-destructive and swamp everything —
   Sharpe 1.82, net avg R 0.280. The two populations pull in opposite directions and
   must be separated. (§4)

**Reasoned, not measured — treat as hypotheses:**

5. **The detector's flaws probably don't reach P&L directly.** *No run ever varied
   detection quality* — "good S/R vs bad S/R → P&L" has never been measured. Fix the
   §1 gaps for the *displayed* levels and the UX; do not promise a return improvement.

**Method note (the expensive lesson):** the in-sample result in §4b was clean,
large, consistent across five nested windows — and still didn't survive a holdout.
Nested lookbacks are not out-of-sample. Split by entry date before believing anything.

## 7. S/R v2 research harness (implementation started 2026-07-12)

The detector rewrite is decomposed into causal, research-only arms. The live
scanner does not read `BACKTEST_SR_VARIANT`; these switches exist only in the
offline snapshot harness:

| arm | behavior |
|---|---|
| `production_control` | deployed detector plus legacy 1.5 primary selection |
| `rr_aligned_control` | deployed detector; primary selection uses activation `min_rr` |
| `rewrite` | rewritten detector with activation-aligned primary selection |
| `soft_zones` | rewrite plus max-strength/confluence zone aggregation |
| `confirmed_rounds` | soft zones; standalone rounds need two rejection clusters |
| `gate_v2` | confirmed rounds plus uncapped gate evidence |

Detector evidence (`sources`, rejection count, last rejection age) stays in the
pure backtest objects. It is deliberately not migrated into the production DB
schema until a variant passes validation.

The cross-platform matrix runner is only an orchestrator around the existing
`run_backtest_snapshot.py`; it contains no duplicate backtest logic. On macOS:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py train --workers 14
```

Choose one arm and record that lock before running exactly control and that arm:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py validate \
  --locked-arm confirmed_rounds --workers 14
```

Replace `confirmed_rounds` with the recorded winner. The validation command also
calls `scripts/compare_sr_variants.py` to produce the paired cohort CSV and JSON.

> Validation result: `confirmed_rounds` is rejected and is no longer a lockable
> arm. It remains in the corrected training matrix only to preserve the causal
> experiment record. The first training reports used an entry end bound without
> forwarding it to the portfolio calendar, leaving each book in flat cash through
> the test period. The simulator now treats `BACKTEST_ENTRY_END` as an inclusive
> entry bound and truncates the calendar after the final position can resolve.

The isolated `rr_aligned_control` validation also failed (Sharpe 2.78 to 1.32,
CAGR 73.3% to 33.1%, drawdown 11.7% to 18.4%). The live 1.5 primary-selection
behavior is therefore frozen: although it predates the 2.0 activation gate, it
acts as a useful selectivity mechanism. The final detector matrix holds that
behavior constant and varies only detection/zone policy:

- `rewrite_legacy_primary`
- `soft_zones_legacy_primary`
- `confirmed_rounds_legacy_primary`
- `gate_v2_legacy_primary`

The post-2024 interval has informed earlier research, so this is validation rather
than a pristine holdout; do not sweep variants on it. No deployment follows
automatically. A lower validation Sharpe or higher drawdown remains a no-ship
result even when CAGR rises.

## 8. Final detector-only result: no rewritten gate arm advances

The last matrix froze production's effective gate (`primary min_rr=1.5`,
activation `min_rr=2.0`) and varied only level detection/zone policy on entries
through 2024-06-30. Corrected portfolio calendars end after the last position can
resolve; there is no flat-cash tail.

| arm | Sharpe | CAGR | MaxDD | qualified | net avg R | ex-top-5% |
|---|---:|---:|---:|---:|---:|---:|
| production control | **1.28** | **28.8%** | 21.4% | 676 | **0.230** | **0.066** |
| rewrite + legacy primary | 0.96 | 21.0% | 22.2% | 1,200 | 0.037 | -0.102 |
| soft zones + legacy primary | 1.08 | 25.1% | **17.8%** | 1,161 | 0.045 | -0.096 |
| confirmed rounds + legacy primary | 1.14 | 22.1% | 20.2% | 570 | 0.189 | 0.045 |
| gate v2 + legacy primary | 0.87 | 16.7% | 20.7% | 604 | 0.187 | 0.041 |

No arm advances to validation. The raw rewrite retains only 249 of 676 production
setups, removes 427 good setups, and adds 951 setups with negative expectancy.
Round confirmation repairs the added cohort but still removes 430 production
setups whose 30-day average (+0.680R) exceeds the additions (+0.511R). Uncapping
recovers only 16 of those missing setups. The old detector averages 43.3 gate
levels versus 15.0 rewritten and 24.0 rewritten-uncapped levels.

**Standing no-ship decision:** keep both the deployed detector and the legacy 1.5
primary-selection behavior in the trading path. The rewritten structure may only
proceed as a separately computed display model. Do not merge this research branch
into production as-is.

### Hidden-feature isolation

The deployed detector accidentally measures long-memory historical price traffic
rather than genuine S/R. A dedicated matrix holds the complete gate fixed and
changes one legacy component at a time:

- `legacy_geometry_neutral`: old locations, every merged strength fixed at 50;
- `legacy_pivots_only`: unfiltered full-history pivots, no VP grid;
- `legacy_traffic_grid_only`: deployed HVN+LVN grid, no pivots.

Run on macOS:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py traffic --workers 14
```

Do not validate any traffic arm yet. First establish whether geometry, pivots, or
the range-occupancy grid reproduces production on pre-2024 training data.

Corrected training result:

| arm | qualified | Sharpe | CAGR | MaxDD | net avg R | ex-top-5% |
|---|---:|---:|---:|---:|---:|---:|
| production control | 676 | 1.28 | 28.8% | 21.4% | 0.230 | 0.066 |
| corrected neutral geometry | 505 | 1.48 | 33.5% | 18.2% | 0.230 | 0.087 |
| pivots only | 717 | 1.38 | 32.9% | 25.2% | 0.236 | 0.076 |
| traffic grid only | 504 | **1.72** | **41.8%** | **16.8%** | **0.271** | **0.136** |

The traffic grid is the first research arm to beat control simultaneously on
Sharpe, CAGR, drawdown, and robust expectancy. It retains 264 production setups
at +0.214R ex-top-5%, adds 240 at +0.051R, and removes 412 at only +0.010R.
Against corrected neutral geometry, only 239 qualified setups overlap; the 265
traffic-only setups return +0.140R ex-top-5% versus +0.073R for the 266
neutral-only setups. This is different selection, not merely a lower trade count.

The old `volume_profile` name is misleading. Its helper returns both HVN and LVN
bins, so their union retains almost every one of the 20 evenly spaced centers over
the expanding historical high-low range (19.987 levels on average in the audit).
The later strength calculation does not use volume; it counts bars whose ranges
cross each center. The candidate feature is therefore:

1. a normalized, expanding 20-bin price-range grid;
2. range-touch occupancy strength;
3. no full-history pivot ladder or pivot/grid strength saturation.

Two final training arms isolate the first two items explicitly:

- `legacy_range_grid_touch`: all 20 range centers, no volume calculation, legacy
  touch strength;
- `legacy_range_grid_neutral`: identical centers, strength fixed at 50 after
  clustering.

Run only these new arms on macOS:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py traffic \
  --only-arm legacy_range_grid_touch --workers 14

.venv/bin/python scripts/run_sr_v2_matrix.py traffic \
  --only-arm legacy_range_grid_neutral --workers 14
```

The touch arm reproduced `legacy_traffic_grid_only` exactly: all 121,464
candidates, 504 qualified setups, cohort membership, expectancy, and portfolio
metrics match. Volume contributes nothing. Neutral strength won the training
portfolio comparison (Sharpe 1.98 versus 1.72), but failed the locked validation:

| validation arm | Sharpe | CAGR | MaxDD | net avg R | ex-top-5% |
|---|---:|---:|---:|---:|---:|
| production control | **2.78** | **73.3%** | **11.7%** | 0.174 | 0.022 |
| neutral range grid | 1.85 | 43.2% | 15.2% | **0.178** | **0.039** |

The neutral grid is a no-ship. The validation failure prompted a causal audit of
the control rather than another detector sweep. One relationship survives both
periods: dense legacy ladders are a proxy for a wide multiplicative price range.

| control cohort | training ex-top-5% | validation ex-top-5% |
|---|---:|---:|
| at least 70 legacy levels | +0.165R | +0.185R |
| fewer than 70 levels | +0.004R | -0.379R |

Level count is not independently useful after controlling for the last 504
trading days' range. For `log(max(high) / min(low)) >= 1.0315` (about a 2.8x
high/low ratio), the overlap cohort returns +0.292R training and +0.322R
validation ex-top-5%. High density without high range returns -0.096R and
+0.029R. Correlation between the explicit range and legacy level count is 0.864
training and 0.822 validation.

This isolates the hidden feature as a two-year realized price-excursion factor,
accidentally encoded by how many full-history pivots survive a 0.5% merge. It is
not evidence that the arbitrary lines are structural. A rounded threshold of
`log range >= 1.0` remains positive across a 0.9/1.0/1.1 sensitivity plateau.

Two diagnostic-only arms now test whether the explicit scalar replaces the side
effect:

- `production_range504`: deployed targets plus the explicit range gate;
- `rewrite_range504_legacy_primary`: clean targets, frozen primary selection,
  plus the identical range gate.

Run on pre-2024 training data only:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py factor --workers 14
```

Result:

| training arm | qualified | Sharpe | CAGR | MaxDD | net avg R | ex-top-5% |
|---|---:|---:|---:|---:|---:|---:|
| production control | 676 | 1.28 | 28.8% | 21.4% | 0.230 | 0.066 |
| production + range504 | 180 | **1.65** | 31.4% | **15.9%** | **0.476** | **0.250** |
| clean rewrite | 1,200 | 0.96 | 21.0% | 22.2% | 0.037 | -0.102 |
| clean rewrite + range504 | 291 | 1.46 | **31.5%** | 18.4% | 0.292 | 0.158 |

The scalar recovers most of the detector rewrite's regression. The clean arm now
beats the original production baseline on Sharpe, CAGR, drawdown, and robust
expectancy. Old target geometry retains a smaller edge over the equally filtered
clean arm.

The residual cohort is target selection, not another range feature. The clean arm
retains 63 exceptionally strong common setups (+0.665R ex-top-5%), adds 228 weak
setups (+0.018R), and misses 117 strong old-geometry setups (+0.175R). Of the
clean-only additions, 156 have a standalone round-number primary; all 162
round-only qualified setups have fewer than two observed rejections and return
-0.024R ex-top-5%. Structural-only and round-confluent primaries return +0.394R
and +0.369R.

For 113 of the 117 missed setups, the clean detector does produce a target, but
its selected primary averages 1.56R; 77 land in the 1.5-2R veto band. A final
two-arm residual matrix therefore holds the clean detector and range factor fixed:

- `rewrite_range504_structural_legacy_primary`: exclude standalone round targets,
  retain the deployed 1.5 primary floor;
- `rewrite_range504_structural_primary2`: identical, but select the primary from
  targets clearing 2.0R.

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py residual --workers 14
```

### Full-period production comparison

After freezing `rewrite_range504_structural_legacy_primary`, run it beside a
fresh `production_control` over the complete snapshot with identical portfolio
and exit settings:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py full --workers 14
```

The command deliberately supplies neither `--entry-start` nor `--entry-end`.
It writes both audited reports plus a paired cohort comparison:

- `reports/backtest-sr-full-production_control.json`
- `reports/backtest-sr-full-rewrite_range504_structural_legacy_primary.json`
- `reports/sr-full-production-vs-candidate-cohorts.csv`
- `reports/sr-full-production-vs-candidate-comparison.json`

This is an apples-to-apples full-history diagnostic against the current live
production path. It is not a new untouched holdout because the post-2024 data
was already inspected while isolating the range factor.

Full-period results reject the clean range-gated candidate as a replacement:
it improves robust setup expectancy and drawdown, but cuts the qualified set
from 1,086 to 290 and the live-path book from 321 to 170 trades. Its 73 unique
qualified symbols are also concentrated (36.2% of setups in the top ten names),
so overlapping setup expectancy does not translate into independent portfolio
opportunity.

### Structural confirmation as a ranking overlay

The next experiment preserves the production detector, setup geometry,
qualified universe, activation gate, and live exit. For each production setup,
the clean detector is evaluated point-in-time only to attach a binary feature:
whether `rewrite_range504_structural_legacy_primary` also clears its core gate.
That confirmation receives a single pre-registered 5% weight:

```text
overlay_rank = 95% * production_80_20_rank + 5% * structural_confirmation
```

There is deliberately no weight sweep and no union with clean-only setups. The
report must first reproduce the production qualified count and production book;
otherwise the comparison is invalid. Run the one-arm full-period diagnostic:

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py overlay --workers 14
```

Output: `reports/backtest-sr-overlay-full.json`. The candidate advances only if
the overlay improves full-period Sharpe, does not worsen drawdown, and retains
at least 90% of production CAGR. The 1-year and 6-month rows must not both
deteriorate. This remains contaminated full-history research, not promotion
validation.

Result: **reject the overlay**. Production parity is exact, but the overlay
reduces full-period Sharpe from 2.03 to 2.00 and CAGR from 50.0% to 48.4%; max
drawdown improves from 21.4% to 20.0%. Confirmation has real standalone quality
(+0.263R ex-top-5% versus +0.024R), but little marginal ranking value: confirmed
setups already average production rank 92.3 and 46.1% come from ten symbols. The
5% boost changes ordering on only 45 active dates and overweights the same
concentrated names.

### Explicit gate target ladder

The legacy detector's volume-profile label is misleading. It returns both HVN
and LVN bins, whose union is the complete 20-bin price-range grid, then adds
unfiltered pivots and touch strength. For the gate this behaves as a broad
target-proposal ladder, not human-facing support/resistance.

The `explicit_target_ladder` arm therefore replaces only the irrelevant volume
pass with the complete range grid. It retains pivots, touch strength, merge
geometry, primary selection, qualification, ranking, and exit behavior. Grid
levels are labelled `range_grid`, making the internal purpose explicit.

```bash
.venv/bin/python scripts/run_sr_v2_matrix.py ladder --workers 14
```

The arm advances only on exact parity with the full-period production control:
no added or removed qualified setups and identical production-book Sharpe,
CAGR, drawdown, and trade count. Passing parity supports a dual-purpose design:
clean structure for charts and alerts, explicit target ladder for the gate.
Failing parity means the supposedly irrelevant volume pass still affects an
edge case and must be located before any architectural change.

The post-2024 window has been opened and is now analysis data, not a valid final
promotion holdout. These arms can isolate mechanism, but neither may ship without
new future data or a separately pre-registered walk-forward protocol.

**Next runs, if picked back up:**

- A **per-name target model** for clear-air setups instead of a constant k×ATR. This
  is the one avenue left: the return is demonstrably there (§4c), it's the flat target
  that makes it too expensive in risk. Grade on the §4c holdout, not full history.
- Sweep **k** (fallback distance); only k=3 was tried. Grade on the holdout.
- A **volatility-aware** admission rule for clear-air names — the OOS failure is a
  drawdown/vol story (11.7% → 14.3%), so sizing them down may recover the Sharpe.