Strategy autopsy: WILL 4.0

If part_b_active was false, the function returned before evaluating the hard stop. A trade with trend strength below the minimum that never reached target_a had no way to close: it stayed open indefinitely. And since the results record only counts trades with an exit, those never appeared in any computation. The patch's own comment puts the impact at −169 R.

$ diff exit_logic.py.bak_stop exit_logic.py
70,73d69
<     # PART B — dynamic stop
<     if not part_b_active:
<         return exits if exits else None, position
77a74,85
>     # STOP GLOBAL — aplica aunque Part B no esté activa.
>     # Sin esto, un trade con trend_strength < min y sin tocar target_a
>     # queda abierto indefinidamente (bug forced_exit -169R).
>     if not part_a_closed and bar_low <= hard_stop:
>         exits.append(("part_a", hard_stop))
>         exits.append(("part_b", hard_stop))
>         return exits, None

The entry_date column does not hold the entry time: it holds the exit bar index, duplicating the adjacent column. Checked across both windows without a single exception — 410 of 410 rows in 2023–2025 with origin 1 Jan 2023 at 00:00 UTC, and 241 of 241 in 2021–2022 with a single origin per pair, matching each asset's first available bar. In total, 651 of 701 rows have no entry data.

# solve for the implicit origin: origin = exit - index x 1h
2023_2025  origen 2023-01-01 00:00   match=410  fail=0
2021_2022/BTC   n= 27  origins=1  →  2021-01-01 06:00
2021_2022/AVAX  n= 40  origins=1  →  2021-03-05 10:00  # listing start
2021_2022/SOL   n=  4  origins=1  →  2021-08-04 10:00  # listing start

A consequence beyond formatting. Without an entry time, trade duration cannot be computed; without duration there is no time exposure, no real turnover, and no correct funding cost on perpetuals. The execution cost floor depends on annual turnover: on these files, that figure cannot be computed. The data is only recoverable if the original price panel has been kept.

With the H-01 defect already corrected, the strategy loses money in 12 of the 14 pair-window combinations. The two cases above unity support no conclusion: BNB gives 1.008 — indistinguishable from zero — and SOL gives 1.326 over 18 trades, with no statistical power to claim anything.

The bot directory is not a git repository, so there is no record of how many configurations were tried or in what order. The trace survives indirectly: five major versions in versions/, and 12 oos_trades files in an auxiliary directory with subversions reaching v10 on the same asset and the same out-of-sample window.

This is a crude lower bound on the trial count, not the count. A script may have run once or two hundred times, and an overwritten file leaves no trace. Without that number, the multiple-testing-corrected statistic cannot be computed rigorously — and that, not the sign of the result, is the underlying methodological problem.

$ git log --oneline
fatal: not a git repository
$ ls versions/
2_8   3_0   3_3   4_0   will_2_8
$ ls ChatGPT/ | grep -c oos_trades
12   # subversions up to v10, same asset, same sample

Each trade is recorded in two rows, one per position leg (part_a and part_b), and the metrics computation treats every row as an independent trade. Across the 14 files, total_trades equals the row count and never the trade count. The real trades are 353, not the 701 reported.

The two legs of one trade are not independent observations: they share entry, direction and instrument, and the second is the continuation of the first. It is the effective sample size problem applied inside the unit of analysis.

$ for f in */*/trades.csv; do
    a=$(awk -F, 'NR>1 && $5=="part_a"' "$f" | wc -l)
    t=$(tail -n +2 "$f" | wc -l)
    echo "$f part_a=$a rows=$t"
  done
2023_2025/BTC/trades.csv   part_a=52  rows=103  reports=103
2023_2025/ETH/trades.csv   part_a=41  rows=81   reports=81
2021_2022/AVAX/trades.csv  part_a=21  rows=42   reports=42
... 14 of 14 report rows, none reports trades

Scope of the effect, measured and not assumed. The profit factor turns out to be insensitive to this aggregation, being a ratio of sums that do not change when grouped: BTC 2023–2025 moves from 0.489 to 0.482 and six of the fourteen do not move at all. The counterfactual table holds. What is inflated is anything that scales with sample size — the t statistic, the Sharpe ratio and any significance test.

Measured factor, adding cross-pair dependence. Rebuilding the daily result series per pair from the exit column, the mean cross-pair result correlation across the seven pairs is 0.043 in 2021–2022 and 0.088 in 2023–2025 — far below the price correlation, because each pair enters and exits at different moments. The resulting design factor is 1.26 and 1.53. Combined with the double counting of legs, the total inflation of the significance statistics is 1.59 in the first window and 1.75 in the second.

The r_multiple column takes four values across the whole sample: the design's three exit levels plus the second leg's target. Solving for the risk unit R from each leg of the same trade, 293 of 293 pairs give a 0.0000 % discrepancy. Two exits hours apart cannot give the same R to the last decimal if the prices were real fills.

# solve for R from each leg and compare within the trade
r_multiple distinct values: 4  →  -0.7  -0.42  +1.2  +2.0
comparable pairs: 293   max discrepancy: 0.0000%

Consequence. The degradation from slippage, rounding and fees is not small: it is unobservable with this record. The manager cannot measure what costs him most, and does not know that he cannot. Any break-even computed from these figures is understated by construction.

Measuring dispersion inside the dominant cluster instead of over a fixed window that mixed two design levels: 5 of 5 clusters with 0.0000 % dispersion across 393 trades, in both files. Eleven independent clusters, each with a single distinct value.

# observed clusters and their cardinality
2021-22:  -0.7(88)  -0.42(5)  +1.2(30)  +1.6(8)  +2.0(12)
2023-25:  -0.7(152) -0.42(11) +1.2(55) +1.6(9) +2.0(22)
# a real execution record produces dispersion: tick, rounding, fees

The mean gross effect is −0.4258 against a cost floor of 0.5842 per trade. The observed ratio is 0.73: fees take 137.2 % of the gross. There is no effect from which to deduct costs.

# gross measured from prices and size, not reconstructed
mean gross  -0.425841    cost floor  0.584161
ratio  0.73

Comparing config_4_0.yaml against the levels the record produces: 65.0 % of trades (93 of 143) end at a level the configuration neither declares nor allows to be derived. The targets match exactly; the entire loss geometry sits outside the config.

# declared config against observed record
declares  part_a_target_r +1.2   part_b_target_r +2.0
          part_b_stop_loss_r -0.5   part_b_be_buffer_r +0.3
observes  +1.2(30)  +2.0(12)   declared
          -0.7(88)  -0.42(5)   orphans: neither declared nor derivable

The manager documents a six-hour offset in the ETH series relative to the rest of the panel. This audit has not checked it. What does appear on disk is four scripts dedicated to the problem — check_eth_align.py, diag_eth.py, fix_eth_data.py, refix_eth.py — all dated 31 July, which is consistent with the account but does not prove it. Verifying it requires running the cross-correlation over the original panel.

The engine accused WILL 4.0, at terminal severity, of not reaching its own break-even. It counted each leg as an independent trade, and splitting every winner across two different levels while both losing legs exit at the same one sinks the hit rate. All of the bias ran in the same direction.

# the same sample, two units of count
legs        (2021-22)  n=258  hit rate 28.3%  break-even 32.8%  FIRES
R per trade          n=143  hit rate 35.0%  break-even 32.0%  does not fire
legs        (2023-25)  n=443  hit rate 27.3%  break-even 32.9%  FIRES
R per trade          n=250  hit rate 34.8%  break-even 32.2%  does not fire

100 % of trades were flagged by the noise of execution itself, not by the configuration: the attack could not tell a dishonest record from a merely executed one. We checked whether adjusting the criterion resolved it, and no adjustment separated the defect from the noise.

The distribution analysis took the 90th percentile in money while the rest of the attack measured in risk multiples. In money, the tails are the biggest bets, not the best trades.

# tails identified by unit
in currency  15 tails   in risk multiples  20 tails   overlap  8
# and in the right unit the 90th percentile falls on +2.0R, a design level
# the "tails" would be every trade that reached the larger target