Track record

Being watched: under-rested home teams

When the home team has had 4 days or less since its last match, the model used to systematically underrate it. In the latest measurement that bias is gone: we said 44.4%, the actual figure was 44.6% (3,129 matches).

The flaw was neither invented nor buried: it was genuinely measured on 8 August 2026 across 719 matches in 6 leagues (z=+3.14) and has been stated on this page ever since. As coverage grew and the sample multiplied, the gap dissolved statistically — meaning the original finding was largely small-sample noise. This box updates itself after every audit run; if the bias returns it will show up here as a warning again.

Why double chance adds up to 200%

1X, 12 and X2 always sum to exactly 200%. This is not an error, it follows from the definition: the options are not mutually exclusive, they overlap — every outcome is counted in two of the three, so the 100% of 1X2 is doubled. For the same reason 1X plus X2 exceeds 100% by exactly the probability of a draw. This is an invariant, verified by a unit test on every build.

The main culprit behind our losses: the draw

The model said “draw” in only 0.0% of 133 matches. Yet 26.3% of matches ended level.

This is not an error, it's what the maths gives: a draw is almost never the single most likely outcome — with probability spread across three results, one side usually stands out. But when draws do happen they are recorded as losses, and they make up half of ours. That is exactly why double chance performs so much better than 1X2: it covers the draw instead of losing to it.

Is there a parameter to be extracted from the losses

Factors knowable BEFORE the match were scanned: days of rest, fixture congestion, missing players, stage of the season, expected goals. Result: no usable parameter emerged.

One factor looked significant in the raw scan (“accuracy is 8.6 points higher in matches expected to be high-scoring”). Controlled for within the same confidence band, the sign reversed (−6.9 points) — high-scoring matches were already concentrated in the high-confidence bands, and those bands are naturally more accurate. The raw finding was an artefact of the distribution, not of the factor. Without that control we would have drawn a wrong parameter out of it and damaged the model.

Our ceiling: 85% of losses are decided by a single goal. That is football's natural variance; chasing it makes the model fit noise. The share attributable to red cards and in-match events will be measured separately once event data is ingested — that data can't be known before kick-off so it can't be a parameter, but it shows our ceiling.

Head-to-head history (the “bogey team” effect)

The intuition that “team X has a bogey team in Y” was tested. Result: no signal.

• The correlation between the bias in past meetings and the bias in the current match is r = −0.05 — indistinguishable from chance.
• Of the 165 pairings with at least 4 matches, 52 look “dominant”. But even in a world with no pairing effect at all, simulation produces 46.3 of them. The excess of +5.7 sits inside the noise band.
• When a correction was applied to expected goals, the best coefficient came out as zero — that is, applying no correction. Every positive coefficient made the prediction worse.

The honest limit: across the 3 seasons we hold, there are at most 6 matches per pairing. That is enough to say “this data can't show it”, not enough to say “there is no effect”. The test will be repeated when more seasons are available.

An attempt to correct the known bias (sharpening)

To fix the “not confident enough” flaw described above, the probability distribution was sharpened with a correction that preserves the ranking. Result: it didn't work and wasn't applied.

• With the coefficient chosen on the first 75%, the holdout Brier went 0.6020 → 0.6031 (worse).log loss de bozuldu.
• It improved only three of the six leagues and hurt three. A correction that doesn't work everywhere isn't a correction, it's overfitting.
• The calibration error (ECE) got worse at the very thing we were trying to fix.

The bias itself turned out to be fragile: the +3.2 point gap seen for very strong away teams across all the data becomes −0.8 in the most recent 25%. So it isn't a stable enough flaw to correct. Another method will be tried; if that fails too, the flaw will keep standing here as it is.

Pulling the draw probability toward the base rate

Since half our losses are caught out by draws, this was tried: pull each match's draw probability toward the league's long-run draw rate. Result: no gain, it makes things worse.

The measurement showed why: the model's average draw probability is 25.6%, while the actual draw rate is 23.3%. So the model doesn't under-call draws — it slightly OVER-calls them. The impression that “the model doesn't see draws” is wrong — it gives each match the right probability, but among three outcomes a draw is almost never the highest (in 3 of 943 matches; the highest value seen was 37.8%). That is what the maths gives, not a flaw to be corrected. The right answer was not to force the model but to bring double chance forward.

Number of missing players (injuries)

Tested on 859 matches against real per-match injury records. Result: no measurable contribution.

• The correlation between the difference in missing players and the bias in the result is r = −0.04. The direction is right — the depleted team scores less — but the magnitude doesn't separate from noise (p = 0.28).
• Added to the model as a correction, the best coefficient again came out as zero.

Why this isn't surprising: we have no player-quality data, so a missing star and a missing substitute count the same. On top of that, the effect of ongoing injuries is already reflected in the team's recent results and therefore in its rating. This is not a “never”, it's a “not like this”.

Team-specific home advantage

League-wide home advantage is already in the model (home teams score 1.63 goals per match, away teams 1.28). What was tested is whether the advantage varies from team to team. Result: no contribution.

The team factors looked meaningful (highest 1.25, lowest 0.79) but adding them to the model made the prediction worse at every coefficient. There are only ~17 home matches per team per season; most of the “fortress at home” label that comes out of that little data is noise.

An independent strength measure (ClubElo)

Because squad-value data could not be obtained from a source with clean licensing, an independent team-strength measure was tried. Result: the effect is real but small (+0.46%).

What shows this isn't noise: when the coefficient was chosen on the first 75%, the best value came out as 0.12 — and the holdout's own optimum was also at 0.12. Under overfitting those two points diverge. Even so, for a gain of that size we don't take on a dependency with unclear licensing; if the terms become clear and it's confirmed across more seasons, it will be added.