Every permitted M2 signal recorded as a full 1-second price path, then run through 60 management policies, three significance tests and an out-of-sample split — to find out what the exit rules are actually worth.
The edge is a long right tail, and almost everything that feels like prudent risk management amputates it. No stop level improves expectancy at any width, and at portfolio level no exit rule of any family beat simply holding to the next opposite signal.
Breakeven @ +30 — the rule first proposed as the benchmark — does not survive this analysis. It still tops the portfolio table, but that lead is an artifact of re-entry timing over 26 sessions, not a property of the rule. On identical signals the rule costs −5.45 pts per trade [−9.82, −1.21], and in the parameter sweep it is a lone spike with weak neighbours. It should not be used as a benchmark without this caveat attached.
An earlier version of this page recommended a target at +150 handing over to a 90-point trail, scored at 4,705 points. That was an implementation error, not a result: the rule triggered on a 90-point retrace but filled at max(peak − 90, 150), so any trade peaking between +150 and +240 was paid a price the trail never offered. With the fill corrected the hybrid scores 3,069 and not one cell of the target × trail sweep beats the 3,746 do-nothing baseline. The recommendation below is changed accordingly. Sections 02–07 are unaffected — the paired tests, plateau checks and out-of-sample split all run through a separate code path.
The strategy emits entries only. Every stop, target, trail and time rule is a separate policy replayed over that same entry stream, so the question stops being “what SL and TP” and becomes “does this alpha survive management, and which family suits it”.
2,267 permitted signals were recorded with their full 1-second path: entry at first touch of the Renko close (no look-ahead), then MFE, MAE, time to each, adverse excursion before the peak, give-back, post-peak drawdown and forward closes. Each trade's window ends at the opposite permit, an exit-only signal, the 20:59 session flat, or 8 hours — whichever comes first.
Points, not R. R-normalisation is supposed to remove volatility dispersion. Here it adds it: coefficient of variation on MFE is 0.95 raw versus 1.14 divided by the structural swing. Correlation between any risk-unit candidate and the excursion that follows is only +0.07 to +0.21, because the pre-signal swing width does not predict post-signal travel on this instrument. Dividing by it would have been cosmetic. Everything below is in points; MNQ dollars = points × 2.
Two passes, because they disagree. Pass 1 takes every signal independently — constant n, so policy differences are isolated and testable as paired differences. Pass 2 enforces one position at a time, which is what you would trade. They rank policies almost oppositely, and that disagreement turned out to be the most informative result in the study.
Winners and losers separate cleanly — but not where a stop can reach. The number that decides a stop is not a loser's MAE, it is the adverse excursion a winner has to survive before it turns.
The median winner goes 31 points against you before making its high, and the top quartile goes 76 against. A stop tight enough to keep losses small sits inside the range winners routinely visit.
A stalled trade really is a worse trade. If the peak has not reached +15 by minute 20, expectancy is −6.5 against +13.8 for everything else — a clean separation over 589 trades. That is why time stops keep topping the portfolio table. It is also, as section 06 shows, not enough to make them pay.
The intuition is that a trade going straight against you is a bad trade. It is the reverse. Signals that go 30+ points against you inside the first three minutes win 56.9% of the time, against 49.1% for everything else — a fast adverse move is a mild positive. I built the detector expecting a filter and got a negative result; it is not in the recommendation.
Split the 26 sessions in half and rank the policies in each. The between-halves rank correlation is . The leaderboard does not survive its own sample, so no policy should be chosen by reading down it. Everything recommended here had to clear a paired significance test and a plateau check instead.
Because pass 1 shows every policy the same 2,267 signals, policy-minus-baseline is a paired difference — a far tighter instrument than comparing two totals. A policy whose interval straddles zero is not an improvement, whatever it scored.
A parameter worth trusting sits in the middle of a broad flat region. A good number with bad neighbours is a fitting artifact.
Confidence 3 and the below-VWAP zones both hold their sign across halves, and filtering to them lifts expectancy sharply. It also removes most of the trades, and with one position in one market there is nothing to redeploy the freed capital into — so the total falls and the interval widens.
83.8% of permitted signals are discarded by the one-position rule, so relaxing it is the largest untested lever in the system. Allowing up to five units nearly quadruples the P&L, and per-unit expectancy rises — which looks like the added units being better than average. Normalise for the exposure actually carried and the entire gain disappears.
Equal-risk = the total rescaled to the same average concurrent exposure as the one-position baseline. Scaling in is a position-sizing decision, not a strategy improvement: same edge per unit of risk, more of it, and a proportionally deeper drawdown.
MNQ fell 1,896 points across the sample, so the short book's headline number is not all edge: +2,669 over 193 short trades against +1,896 for simply holding short the whole month. The long book made +1,125 into that headwind. On a drift-adjusted basis the longs are the stronger half of this system, which is the opposite of what the raw direction split suggests.
A wide target and a wide disaster stop both cleared the paired test on their own, and the give-back data argued the target should hand over to a fixed-distance trail rather than cap the trade. Built and measured properly, that construction does not survive the portfolio pass: it lands at 3,069 against the baseline's 3,746, and every variant of it lands below the baseline too.
What is left is the answer the rest of the study kept pointing at: hold to the opposite signal, and add only the disaster stop. The wide target really does earn more per signal — that part is significant and reproducible — but with one position at a time, going flat early hands the re-entry decision to whatever signal happens to come next, and that costs more than the target gains.
Between a 250-point stop and none at all the difference is 3,600 versus 3,746 — inside the noise, and max drawdown barely moves. It buys no return; it costs little either, and it converts an unbounded tail into a bounded one. That is the whole case for it, and on this evidence it is the only addition to the raw signal I would make.