Signal-to-Cost Trade-Offs for Independent Quantitative Researchers

# Where is the signal-to-cost ratio least unfavorable for an independent quantitative researcher?


# Where is the signal-to-cost ratio least unfavorable for an independent quantitative researcher?












I built a research infrastructure designed to reduce the risk of fooling myself:

decision-to-outcome datasets covering both accepted and rejected signals; hypotheses preregistered before inspecting results; strict separation between decision-time features and future labels; session-level block bootstrap; independent temporal validation; explicit transaction-cost modelling.

Using this process, I rejected my initial strategy: short-horizon intraday momentum on four highly liquid US energy stocks, with an average holding period of roughly three minutes.

The main findings were:

the raw forward return was approximately zero across all deciles of the signal; large recent moves showed some subsequent mean reversion, but only around 1–2 bps; estimated round-trip costs were approximately 6.5 bps; the strategy therefore had no economically exploitable edge, even before considering further implementation uncertainty.

I am not looking for ways to rescue or retune this strategy. I consider the original hypothesis rejected.

My broader question is:

For an independent or retail quantitative researcher using standard bar and quote data, where is the signal-to-cost ratio structurally less unfavorable?

For example, is the most realistic direction generally to investigate:

longer holding horizons; slower-moving cross-sectional signals; broader universes; less liquid instruments with larger movements but higher execution risk; relative-value or spread trades; lower-turnover portfolio construction; markets where public data may contain more persistent structure?

I am particularly interested in answers grounded in research experience rather than in specific profitable signals.

What market-design, execution-cost, data-quality, or research-process lessons would you have wanted to understand before spending several months building and testing short-horizon strategies?

I would also appreciate references on how independent researchers should think about the trade-off between:

signal amplitude; turnover; liquidity; spread and slippage; holding horizon; and the amount of competition in a given market.

## Answer by Adol (score 1)

https://quant.stackexchange.com/a/85740

Your rejection looks correct, and the structure of it generalizes further than the energy sector.

I run a similar setup on crypto news sentiment, and I can give you the horizon ladder from real measurement rather than intuition. Pooled across all signals, gross directional hit rate at 1h, 4h and 24h came in at 49.6%, 49.0% and 50.4%. Wilson intervals straddle the coin flip at all three. Spearman IC over the same windows was +0.033, +0.012 and +0.023. So stretching the holding period from minutes to a day did not, on its own, produce an edge. It bought bigger moves and it bought a correspondingly noisier estimate.

What moved the number was conditioning, not horizon. The same overlay at 24h, traded on every signal, is net negative at roughly -17.5 bps per trade. Restricted to three event categories it turns positive at about +4.9 bps per trade, at roughly a fifth of the drawdown. Same data, same horizon, same costs. The only difference is which trades were taken.

I want to be precise about the status of that second number, because it is the part people quote and the part that is weakest. The filter was chosen after looking at the slices, so it is an in-sample illustration and we publish it labeled that way. What I would defend is the direction of the advice, which is that selectivity is where to look. I would not defend +4.9 as an out-of-sample expectation.

The mechanism is simple enough that it should transfer. Round-trip cost is roughly fixed per trade. That gives you two levers, take fewer trades and take larger moves. A longer horizon only pulls the second one, slowly. Conditioning pulls both at once, which is why it dominates in the arithmetic even when the conditional sample is small.

One result worth more than the positive one. Not every category helps. Our "listing" event slice runs at 36.0% directional accuracy at 24h on n=175, which is a usable anti-signal and a guaranteed way to dilute a pooled average. If you condition, you have to be willing to find that one of your buckets is worse than nothing, and you have to size the buckets well enough to tell that from noise.

On your specific candidate directions:

> Longer horizons: necessary, not sufficient, as above. Broader universes: the honest benefit is statistical, not economic. More names give you the n to establish whether an effect exists at all. They do not improve the ratio per trade. Less liquid instruments: bigger moves and bigger spreads usually arrive together, and the execution uncertainty grows faster than the edge. I would treat this as the last resort. Slower cross-sectional signals: this is the one I would spend time on, and it is close to what conditioning does for me.

Last thing, and it is about your rejected strategy rather than the next one. Before treating the 1 to 2 bps reversion as real and merely too small, check the MDE of the estimator that produced it. At three minute holds you almost certainly have strong within-day correlation, so the effective sample is closer to the number of trading days than the number of trades. It is common for an effect that size to sit well inside the interval, in which case the finding is not "too small to trade" but "not distinguishable from zero." Those two conclusions point at different next experiments.

## Answer by Chris (score 1)

https://quant.stackexchange.com/a/85744

I'm a lot smaller than you and my process is nowhere near as strict, so take this as one guy's numbers.

The thing that helped me most was just holding longer. Your 6.5 bps round trip kills a 3 minute trade. That same 6.5 bps on a 5 day hold is noise. I didn't find a better signal, I just stopped paying the toll as often.

Second thing, I stopped guessing my costs and went and measured them. I'd been assuming my paper fills were 5-10 bps optimistic. Then I pulled 125 actual filled orders and compared each one against that day's close. Median came out to -5.9 bps on my buy/market entries, and 43% of them filled better than the close. My guess was worse than the reality. One thing that tripped me up there: split it by order type. Stop and limit exits fill when the market is moving against you, that's the entire point of them, so leaving those in made my entries look terrible.

Third one nobody warned me about is broker minimums. On a small account the per order minimum matters more than the spread does. One broker's $1 minimum worked out to about 2.5% a year of drag at my size. That's bigger than most of the edges people argue about, and you won't see it at all if you're only thinking in bps.

On the overfitting side, I had a strategy show a profit factor of 2.25 across 2.2 years of backtest. Felt great. Turned out to be a fluke of the parameter grid I searched. Put it on paper, it lost money, I shut it off. The stuff that held up had fewer knobs and traded less.

One thing I'd add to your setup, which is already better than mine. Tag every trade with what the market was doing that day. I did it after the fact and found out 100% of my trades had happened in a risk-on market. Deepest drawdown I'd ever traded through was -4.5%. My costs were honest and my sample still wasn't telling me anything.

-Chris