# 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.

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.

**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.