Sales research library

Why this is thin and the Flat list is not. Flat has three times the moves and five times the reportable yards. The received picture — that the top of this leaderboard is jumps-heavy — was backwards: it looked that way because cross-code moves are overwhelmingly Flat-to-hurdle horses arriving at jumps yards, and the ruler bug handed every one of them a spurious +14.20 lb. Once pre and post ratings are measured on the same ruler, a Flat lot is the well-supported case and a jumps lot is the weak one.

What would change this. More seasons, or a code-specific rating column so that Flat→hurdle progressions can be recovered properly instead of discarded. Lowering the 15-move gate would not count: the gate exists because these are named people.

Chase and bumper are not published at all. Five chase yards and zero bumper yards clear the gate. A five-name list of chase trainers would be an invitation to read rank differences the standard errors do not support, so it is not here. That absence is deliberate, not an oversight.

Coverage. For a jumps lot, the origin-to-destination comparison is blank about 93% of the time — both ends clear the gate on only 7.2% of jumps moves.

Do the two codes agree? Six yards clear the gate in both, and none is a major yard. Their effects correlate r = +0.944, which sounds reassuring and is worth almost nothing on six points spanning a two pound range. Treat the lists as separate estimates: there is no evidence here that a yard's Flat effect transfers to its jumps horses or the reverse.

How the artefact was caught. The rider's mean residual correlated +0.887 with the rider's mean predicted value — the control had plainly failed. The underlying model under-predicted, and not by a constant: the shortfall ran from +£84 per ride in the cheapest decile to +£1,562 in the dearest. This even survives a naive within-horse test, because a stable's best rider takes the horse to its valuable engagements while others partner it in handicaps.

What survives, on the rebuilt control sweep. Recentring within predicted-value band, season, country and code, then comparing the same horse in races of similar value: the permutation p runs 0.000 recalibrated, 0.458 once you add the same horse, and 0.500 once you add the race value too — that is, by the time both controls are on, a permutation test can no longer distinguish the spread of rider effects from what shuffling the labels produces. Read that as a weak test failing to detect, not as proof there is nothing to detect. The permutation measures the overall spread and is low-powered against heavy tails, and heavy tails at low ride counts are exactly what breaks the variance decomposition described below — one cause plausibly explains both. It is also why the two tightest specifications swap places between data vintages: that is instability in a low-powered test, not a finding about which specification is right. Split-half agreement on that tightest money-scale specification is +0.129, and the between-rider spread falls to £522.6 a run. Shrinkage is severe throughout: at the current threshold a rider needs about 1,616 rides before even half of their raw estimate is retained. There is still more here than noise — individual bootstrap intervals separate about a hundred riders — but it is not a ranking and it will not be presented as one.

One row of that sweep is deliberately blank, and the reason is instructive. The uncontrolled population figure has no rebuilt value, because the code that produces the sweep only reports on the recalibrated residual. An earlier draft filled the gap with +0.346 — which is a different model's recalibrated split-half, a different quantity entirely. It was caught before publication. We record it because a blank cell is honest and a plausible number in a blank cell is not, and because this page's own worst error was the same shape.

The estimator behind the earlier version of this finding turned out to be unstable, and that is the strongest thing on this page against naming riders. Until 2026-08-15 we published "452 of 576 riders cannot be told apart", measured with a 100-ride floor. On the rebuilt spine that threshold returns a negative between-rider variance (-56,855) — meaning no signal at all, and no estimates that can legitimately exist. The cause is not the prize correction, which moves the figure about 10% and does not move its sign; it is heavy tails at low ride counts. 77 riders with 100–150 rides carry a within-rider variance around 119 million — one large prize on a rare good mount — and those terms alone swamp the noise estimate for the whole population. Seven more days of data flipped it.

What that would have produced if nobody had guarded it. Not an error and not an empty table: a full table of large, plausible, sign-flipped figures against named professionals. The estimator now refuses and prints why. This is the clearest illustration we have of why the ranking is not published — the failure mode is not "the numbers look wrong", it is "the numbers look right".

The current basis. A 200-ride floor, which is where the estimator is stable across thresholds and across both prize columns: 459 riders, 34 clear of zero above and 68 below. The older "38 above, 86 below, of 576" cannot be reproduced at the threshold that produced it, and the two sets of counts are not comparable — so they are not compared here, and no trend should be read between them.

The names, however, do compare — and they say the instability is all at the tail. Counts measured at two different thresholds cannot be set against each other, but asking which riders appear on both lists is well defined either way. 27 of the 38 survive; 11 drop and 7 are new. Of the 11 that drop, 4 fall below the new ride floor mechanically — all of them worth £20–30 a ride, which is to say nothing — and 7 are still in the data with an interval that no longer clears zero. Every one of the drops is from the bottom of the list. The head does not move: the seven largest estimates all remain clear of zero at similar magnitude, the top one going from £1,062 to £912 a ride.

So the honest reading is that the head is real and the tail is noise-dominated, rather than that the whole thing is mush. That is a narrower claim than "these estimates do not survive", and it is the true one. It is also why the conclusion does not soften: the marginal entries were never findings, and they are precisely the ones that evaporate when the estimator is put on firmer ground. A list whose bottom half rearranges itself between data vintages is not something to publish as a ranking, even when its top half holds. No rider is named on this page in either direction.

Two things we will not paper over. The permutation test and the bootstrap disagree, and on the rebuilt spine they disagree more: on the money scale the permutation p moved from 0.050 to 0.500, which is squarely at chance, while the individual bootstrap intervals still separate about a hundred riders. The permutation tests the overall spread and is low-powered against heavy tails; the bootstrap tests individual riders. We are not going to pretend that is resolved. And the surviving ordering matching expert consensus is reassuring rather than evidence — exactly the kind of face validity that makes a confounded result feel true.

A separate question with a cleaner answer. Asked whether a rider beats their own market price, the answer is that no rider persistently does. That is not a weak effect, it is no effect: the split-half agreement between an early and a late period is -0.002 across 449 riders — indistinguishable from zero. It is the expected result, because the Betfair price already prices the jockey.

This page said "the split-half is negative" until 2026-08-15, and that was wrong. The published figure was −0.243 and was read as riders being anti-predictive of their own market, with a regression-to-the-mean story built on top. Re-measured with the same estimator, it is -0.002. The cause was inside the script that produced it: a blanket "multiply Irish rows by 0.600" — the same era-blind correction this project's own errata condemns — still live there, injecting a distortion correlated with both jurisdiction and period, which is exactly the shape that manufactures early-versus-late structure. The conclusion is unchanged and cleaner; the anti-predictive reading is withdrawn. One residual is real and unexplained: British riders split-half at -0.159 against Irish riders at +0.273.

Why this reached the page at all is worth recording. The figure was never quoted here as a number, only as the phrase "the split-half is negative" — so a search of this page for the published value found nothing, and the claim survived a check designed to catch exactly this. A story can carry a withdrawn finding after its number has been dropped.

The standing rule this produced. Any comparison between two groups of riders is a comparison of their mounts until you condition on the horse. It cost 85% of the raw prize-money effect measured here, and then it reversed the sign of the claimer result. The size of that correction does not carry across models: on the win-probability work behind the booking grid above, adding a horse control moves the spread by about 11 to 14%, not by 85%. What generalises is the direction, not the magnitude — assume the rule applies to every new rider comparison until shown otherwise, and measure the cost separately each time.

The one thing that does look odd, and its answer. Of the 377 cells that clear zero, 319 are positive and only 58 negative. Pure noise would split them about evenly, so that asymmetry is real — but it is not a course specialism. It is the residual yard effect at riders' home tracks: a rider attached to a stable rides that stable's horses most often at the track nearest it, and whatever the model under-prices about those horses lands on that cell. The null being tested is whether the rate of significant cells exceeds chance, and at 4.99% against 5.0% it does not.

The tempting list is the noise. The strongest-looking cells are exactly the ones that would get published — a top rider at his home Irish track on 321 rides, another at Punchestown on 211, a third at Newmarket. The underlying data is retained so the null stays checkable, not so the table can be used.

Why we bothered. "Course specialist" is one of the oldest claims in the sport and it is cheap to appear to confirm: rank riders by strike rate at a track and the list looks authoritative. The test that matters is whether the edge repeats, and it does not. Split-half pearson +0.032, spearman +0.014.

These counts are not transcribed. They are recounted from course_specialists.parquet every time this page is built, and the build fails if they stop matching what the write-up claims. A number quoted from a sentence can be contradicted by a correction appended beneath that sentence; a number recomputed from the data cannot.

This is the null that most nearly became a product. Consignor reputation is exactly the kind of feature a sales page is expected to have, it is cheap to compute, and the first version of it looked excellent. See the R-squared trap below, which is the same investigation.

Why clearance survives when quality does not. Clearance rate is a fact about how a consignor operates — what they enter, what reserve they set, whether they let a horse go. It is a property of the business. "Quality" is a property of the horses, and the horses are drawn from wherever the breeder happens to be. Only the first of those is stable enough to reproduce on a split half.

On the two recorded figures. -0.05 and -0.024 are two separate recordings of the same reliability test, written down by different people in different documents. They are not two different findings and they are not averaged here into a third number that neither document contains. Either way the answer is the same: a split-half correlation at or slightly below zero, where a real property would be clearly positive.

Buyers too. The same test on buyer identity gives +0.08 (also recorded as +0.079). No buyer quality ranking either.

No sample size is attached to the clearance figure in any document that records it. It is published as the bare correlation it was recorded as, and a denominator has not been invented for it.

This is here as a worked example, not as an anecdote. It is the reason nulls are published on this page at all. The failure mode is general: a categorical feature with many levels will silently encode any grouping that correlates with the levels, and the more levels it has the better it will score before you check. Nothing about the 0.206 looked wrong. It was found because someone demeaned within the obvious confounder and watched the number collapse, which is a check that has to be run deliberately — it does not announce itself.

The related finding it produced. The price model turned out not to know which sale it was pricing at all. Within-sale R-squared was negative on all eight runnings of the biggest yearling catalogue — worse than simply quoting that sale's own average — with the median lot 37 to 65% too cheap. The error ran both ways: one catalogue was priced at £22,559 against a sale whose median lot makes £2,625, another at £36,413 against £8,748. Adding an explicit sale-series level moved within-sale R-squared from −0.406 to +0.216 and mean absolute median-price error from 48% to 14%. Those are the figures recorded in the repository and they are the ones to cite. A second measurement of the same fix, taken during the working session that found it, records it as 0.114 → 0.596 — a larger gain on a different cut. That harness was never committed, so it is noted here for completeness and not used: where the two disagree, the repository figure stands.

And what that fix does not cover. A sale being run for the first time gets nothing from it — the Irish August store sale has no history in this population, so it is unchanged and carries a warning on the page. The fix corrects the level of a sale and barely moves the ordering within one.

Why this is in the nulls section when the number is real. Because "we found a large effect and cannot explain it" is a finding about our own understanding, not about the market. Shipping it would put a strong signal on the page whose mechanism nobody has established, and the most likely mechanism — that Book 3 is ordered by something that correlates with quality — would make it a restatement of the catalogue rather than a discovery about it.

What would unblock it. Establishing how Book 3 is actually ordered. That is a question about the catalogue and answerable by asking, not a modelling question.

The history is worth recording. Lot position was first rejected on 11 sales (rank correlation −0.019, p = 0.0010, 0 of 11 sales improved), then a 27-sale test reversed the rejection, and then decomposing by sale family reversed the reversal for every family except this one. Three passes, three different answers, and only the decomposition is trustworthy — the pooled results were averaging one strong effect against three null ones.

And it does not generalise. The original rejection was on Newmarket Flat yearling catalogues, where lots are ordered alphabetically by dam and ring position carries little about quality. An earlier test on a differently ordered sale found a gain. Lot position is not shown to be absent everywhere — it is shown to depend entirely on how the particular catalogue was built.