Theme

The thread: One run is an anecdote

A figure showing a single simulation is showing one draw from a distribution of figures. Where the claim is about behaviour rather than about one dataset, the figure runs across many seeds and reports what held for all of them — and where it shows one run, it shows twenty of them side by side.

What each rule leaves behind, at 120 patients. Four allocation rules over the same cohorts and the same seeds, each scored on three imbalances: the number of patients in each arm, the worst of the nine factor levels, and the worst of the 24 cells of the cross-classification. No rule holds all three. Permuted blocks hold the totals exactly and leave the margins near a coin's. Blocks inside every cell hold the cells and let the totals drift, because 24 part-filled blocks do not have to end level. Minimisation holds the margins and the totals and is at 83% of a coin's cell imbalance. Each of the three columns is somebody's definition of a balanced trial.

Balancing on what was recorded first

Balancing what is known in advance

Four allocation rules, three definitions of balance, and no rule that holds more than one of them. Minimisation keeps the worst factor margin near three patients whether the trial has forty or six hundred and forty — and lets the imbalance in the cross-classified cells climb to 86% of a coin's, because the cells are not what it is watching.

A block length chosen from the data

The length nobody has

Every comparison of block windows in this collection is made at each window's own best block length. That length has a standard deviation of sixteen across draws and averages twenty-five. No rule is aimed at it.

Twenty series with a lag-one correlation of 0.8. Every series has a true mean of zero and 60 observations. The marks on the right are the twenty sample means. The variance of that mean is 8.3 times what 60 independent observations would give, so the series is worth about 7 of them.

When the observations repeat each other

The observations that repeat each other

Almost every standard error divides by √n, which claims the observations carry independent information. At a lag-one correlation of 0.8 a fifty-point series is worth about six independent observations, and its 95% interval covers 47%.

Twenty samples of 40, every one of them genuinely normal. Each panel is a quantile-quantile plot of 40 draws from a normal distribution. The worst point in the worst panel sits 0.87 standard deviations off the line. Anything a reader would reject here would be a false alarm.

What makes it checkable

The seed is part of the figure

Every other site in this fleet draws from a deterministic rule, so a figure either is or is not what it claims. Here the figures are samples, and a sample can be right by luck. That changes what a figure has to carry.

One forecast, and the band the arithmetic puts round it. An AR(1) with φ = 0.75, 60 observations, fitted by least squares and forecast 14 steps ahead. The point forecast decays towards the fitted mean at φ̂^h; the band is ±1.96 standard errors from σ̂²Σψ̂², which grows with the horizon and stops at the unconditional spread 1.72. The dashed pair is the same band computed at the true parameters, which nobody has. The marks past zero are what actually arrived: 12 of 14 inside the band this once, which is one draw and settles nothing.

The observation that has not happened

What the model says next

The usual account of a time series stops at estimation. A forecast asks the other question — not what the parameter is but what the next observation will be — and the band round it is a closed form that grows with the horizon and then stops growing, at a value the series was going to reach anyway.

8 exponential draws, standardised, against the normal. The source is one-sided and skewed. At n = 8 the standardised sum has skew 0.695, and the theory says 2/sqrt(n) = 0.707 — so the convergence is visible AND its rate is predicted.

The distribution itself

Sums of almost anything

The theorem says sums converge on one shape whatever they are sums of, which is remarkable and true. Watching it happen from a one-sided skewed source, with the rate of convergence predicted in advance, is more convincing than watching the shape appear.

Two 95% bands for a quantile plot of 40 points. The outer band is left by 5% of genuinely normal samples — which is what a reader is using a band for. The inner one holds each point separately at 95%, which is what software draws, and 45.0% of genuinely normal samples step outside it. The outer is the inner widened by a factor of 1.502.

What a diagnostic plot is showing

The band the eye was standing in for

The confidence band software draws on a quantile plot holds each point at 95%, and a genuinely normal sample of forty has forty chances to leave it — so 45.0% of them do. The band a reader is actually using is that one widened by a factor of 1.502, and nothing draws it.

Where a replication's estimate lands against a 95% interval, replication the same size. The chance that a 95% interval contains a replication's estimate is 95.00% when the original landed on the truth, 82.99% one standard error away and 48.40% two away. Averaged over where originals land it is 83.42%, and 5.00% of originals capture a replication less than half the time.

An interval read beside something else

Five times in six

A 95% interval is read as a 95% chance that a replication's estimate will land inside it. With the spread known and a replication of the same size, the chance is 83.42% — five times in six — because both estimates are uncertain. An original that landed two standard errors from the truth captures a replication 48.40% of the time; a replication a tenth the size lands inside 44.54% of the time; and among significant originals from studies with 17% power, 66.94%.

Two instruments, two block lengths. The block length that would actually have been best on each draw, for each of the two error readings, averaged over 400 samples of 120 rows. For the rectangular window the implied long-run variance wants 18.92 and the 95% point wants 16.05; for the tapered window, 21.82 against 17.74. The quantile wants a shorter block under both windows — a ratio of 0.848 and 0.813. That is the mechanism the whole field turns on: a rule for choosing a block length is a way of guessing a target, and the two instruments do not have the same target. A rule tuned to one is systematically long for the other, and the two windows do not pay the same price for being long.

The block length read on a quantile

A length for each instrument

The block length that is best for an implied variance is 18.92; the one best for the 95% point of the same resamples is 16.05. A rule is a way of guessing a target, and there are two targets.

How far apart the two components are, on each probe. The median separation between the two components of the admissible set — the difference in their mean probe values, over the spread inside a component — over the 100 of 200 designs whose set is enumerated and found split. The separating direction carries 10.565 and needs the enumeration. The fourth power as the earlier fields use it carries 1.543; projected off the span the rule balances, 5.080. The design's own leverage, which uses no dictionary and no outcome, carries 3.836. A random direction in the same subspace carries 0.942, and a direction chosen by looking for concentrated structure carries 0.543 — below random, and the one heuristic here that is worse than not choosing at all.

A probe chosen rather than picked

A probe chosen from the design

The design's own leverage aligns with the separating direction four times better than a random direction in the same subspace. The concentrated direction the argument invites is worse than random.

The probe a trial has is the probe a trial got. What the two-chain test says when it is run on the trial's own difference in arm means, over 24 outcomes on one fourteen-unit set. The set is in 2 mirror components — that is enumerated, not inferred — so every quiet reading is a miss. 29% of them are quiet. The reason is in the enumerated set rather than in the run: how far the two components are apart on a given probe ranges from 0.001 to 4.938 of a within-component spread across these outcomes, a factor of several thousand. Both covariate probes — chosen before any outcome existed, and replaceable if they had been quiet — report the split. An outcome cannot be chosen and cannot be replaced.

The diagnostic after the trial

A probe nobody chose

On a set that is definitively in two pieces, seven of twenty-four outcomes report nothing at all. Every covariate probe reports it. What separates them is not accuracy — it is that one of them can be chosen and the other is what happened.

Four datasets, slope 0.50, R² 0.67. Every one of these fits reports the same slope to two decimals and the same R². Only the first is a linear relationship with noise: the second is a curve, the third is a line with one outlier, and the fourth has its slope set by a single point.

Regression, and what the summary hides

Four datasets, one summary

Four datasets agree on slope, intercept and R² to two decimals. One is a linear relationship, one is a curve, one is a line with an outlier, and one has its slope set by a single point. The summary cannot tell them apart and neither can any other summary.

Designs that change while they run

Randomising towards the winner

Allocating more patients to the arm that is doing better is the humane thing to want and it buys nothing statistically: at a fixed total it costs thirty points of power. And because the allocation is a function of the outcomes, the ordinary test on it rejects a true null 7.8% of the time before any time trend is applied — and 58% after one.

Most of the rise is the optimiser's, and under one law it is not. The rise in log-likelihood from the tapered plug-in to the maximum over the same eight-lag band, beside what the same optimiser produces on a sample generated from the plug-in's own covariance — where the family is correctly specified by construction and there is nothing to find. Under AR(1) at 0.8 the raw rise is 5.72 and the manufactured baseline is 4.79, leaving 0.93 at 1.8 standard errors; under long memory the excess is 0.14, at 0.2. Under the moving average it is 11.87 at 19.4 standard errors, on every draw. The taper is a shrinkage, and it costs nothing where the sequence decays smoothly and a great deal where it stops dead.

A covariance with no parameter

The plug-in and the maximum

A tapered covariance estimate sits five and a half log-likelihood units below the maximum of the likelihood it is substituted into. Four fifths of that is what the optimiser would have found if nothing were missing.

Two rates, not a factor. The standard deviation of the covariate imbalance under three rules, at five trial sizes, 260 trials each, on log axes. The upper line is a coin: its slope is -0.489, against a closed form of exactly −½. The middle line is minimisation on a median split; its slope is -0.519 — the same rate — because inside a category the assignment is still a coin, and what it buys is the constant, 0.654 of a coin's at n = 200. The lower line is the rule that reads x and maximises the information about the treatment effect: slope -0.987, nearly twice as steep. Its advantage is therefore not a number that can be quoted — it is 0.258 of a coin's at n = 50 and 0.065 at n = 800, and it keeps going.

Balancing what has no levels

The rule that reads the number

Stop categorising and let the rule read the covariate itself. What it should minimise is not an invented distance but the variance of the effect being estimated — and what comes back is not a better constant but a different rate.

Twenty walks up the same hill, σ = 2. Each walk fits a plane to the same four-corner factorial, takes its gradient as a direction, and steps along it until a run comes in below the one before. The true optimum is the cross. 80% of the walks stop before the best point on their own path — not because the direction was wrong, but because one noisy run is enough to stop them, and the direction error costs only 3.9% of the available gain.

The surface between the corners

Walking up the gradient

The fitted gradient is wrong by an angle with a closed form, σ/(|β|√N), and what that angle costs is its squared cosine — twelve per cent at twenty degrees. What costs a third of the gain is not the direction at all. It is deciding where to stop.

A weak instrument gives back the problem it was hired for. The counted mean bias of two-stage least squares at 4 instruments and 200 rows, over 2000 draws a setting, against the standard approximation and against the least-squares inconsistency the instrument was brought in to remove. At π = 0.02 the counted bias is 0.3220 ± 0.0142 where least squares is out by 0.3594 — 89.6% of the way back. At π = 0.3 it is 0.0118 against 0.2647. The approximation, the inconsistency over the population first-stage F, tracks the count at the weak end and sits above it in the middle: 0.968, 0.971, 0.918, 0.810, 0.740, 0.722, 0.846 as the ratio of counted to approximated bias.

A variable that moves one thing only

Weak, and back where it started

A consistent instrumental estimate at two hundred rows and a concentration parameter of 0.32 is biased by 0.3220 ± 0.0142 against a least-squares inconsistency of 0.3594 — 89.6% of the way back to the problem it was hired to solve. Just identified, it has no mean at all, and that is measured as a rate rather than assumed.

$Three answers to how much sample is left. What a set of inverse-probability weights leaves of the treated arm, by three routes, at six settings of the assignment rule. The integral 1/(π∫φ/e) reads the whole covariate space and falls from 0.9392 to 2.655e-3. Kish's effective size counted in samples of 600 falls only to 0.2861, because almost all of the integral's fall is in a region a sample of six hundred never draws from. And the fraction the variance of the weighted mean actually delivers is lower again — 0.1155 — because the variance is the average of one over the effective size and the effective size averaged is not the same number. At the widest overlap all three agree to 0.05%.$ Weighting one sample into another

How many observations a weight leaves

Kish's effective sample size is exact — for an outcome whose mean does not move with the covariates the weights are built from, the studentised variance reads 1.0680 where the formula says one. For the population's own outcome the same reading is 6.769, rising to 52.497.

The quantity that does not depend on the list. The probability that letting each candidate choose its own tuning parameter changes which candidate the table selects — the product of the two moving shares — against the length of the list, over 1200 draws apiece. It is 14.2%, 11.9%, 12.3%: a spread of 2.2% across a list length that moves the disagreement rate by a factor of 1.52. This is the invariant the whole field turns on. Everything downstream of the winner — the coefficients, the regret, whatever a reader is going to quote — is a function of whether the winner changed, and how often that happens is not something the list controls. A longer list changes how often the candidates quarrel and not how often the quarrel matters.

The rate and the size of a disagreement

How often it matters

The disagreement rate rises by half across the list and the share of disagreements that decide anything falls by nearly the same factor. Their product — how often the tuning list changes which candidate wins — sits at an eighth and does not move.

Two measurements of the same thing, correlated 0.60. Pick the worst 15% on the first measurement and their average rises by 0.78 on the second. Pick the best and theirs falls by 0.48. No treatment was given to anybody.

Reversals that are not errors

Regression to the mean

Select the worst performers, measure them again, and they improve. Select the best and they decline. No intervention is required for either, the size of the apparent effect is predictable from the correlation alone, and it is the reason so many things appear to work.

One experiment finding out where to look. A single run of the fully sequential design: 40 runs, the first 8 placed at the guess K = 1, then the model refitted and the design revised after every 2. The marks are the settings the runs were made at. The horizontal lines are where a design built at the truth K = 3 would have put them — 1.875 and 10.00 — and the rule walks onto them without being told: its estimate of K after the first eight runs was 2.694, and by the end 2.765 against a truth of 3. The whole experiment is 96.5% as efficient as the design that knew the answer, where running all 40 at the guess would have been 81.1%.

A design that assumes less

The design that stops guessing

Every repair so far protects a guess. The alternative is to run part of the experiment, estimate the parameter from it, and design the rest at the estimate — which recovers most of what a threefold wrong guess costs, and has a best moment to stop guessing that is earlier than anyone expects.

Whichever dial made the set thin, the crossing is at the same thinness. Each curve is one dictionary, swept over eight tolerances at two hundred units; a point above the line is a set thin enough that walking beats hunting. The curves lie nearly on top of one another, which is the answer to whether the crossing is a fact about the tolerance or about the thinness it produces: the crossings sit between one admissible assignment in 176 and one in 268 for dictionaries of 3 to 6 functions. The mechanism is that a hunt costs exactly 1/p and a walk costs almost the same everywhere — between 82 and 394 evaluations per usable draw across the whole table — so the crossing is wherever 1/p reaches a number that does not move.

What a dictionary buys and what it costs

The set a dictionary leaves

A rule constrained on six functions at a loose tolerance leaves a set as thin as one constrained on three at a tight one. Both sampling methods cross over at the same thinness, and the tolerance where that happens moves by a factor of three.

Two constructions on one triangle, and a third that is not. Three resamplings that all keep runs of neighbours, on the same residuals at a block length of 5, with the lags running past ℓ so that the tapers separate. A blocked multiplier never moves a residual; a fixed-length moving block moves every one; and they attenuate identically, worst gap 1.4 standard errors, both sitting on γ_resid(k)(1 − k/ℓ)⁺ and both exactly zero past ℓ — so the attenuation is the block boundary rather than the multiplier. The third is the stationary bootstrap, whose runs are geometric rather than fixed: its taper is γ_resid(k)(1 − 1/ℓ)^k, it agrees with the other two at the first lag and at no other, and at lag 6 it still carries 0.0081 where they carry -0.0005.

Estimating the dependence, not naming it

The triangle that was not the multiplier's

A resampling that leaves each residual on its own row can keep only what the residuals have, times a triangle. A construction that moves every one of them has the same triangle — and the one in this collection's own table has a different taper entirely.

Searching among fitted models

The weight that is a vector

Two forecasts have a best combination and one number describes it. Eight have a best combination too, and the vector describing it puts nothing at all on the forecast with the smallest mean squared error.

Twenty 95% intervals for a proportion that really is 0.35. 2 of the twenty miss the true value. The 95% is a property of the procedure across repetitions — no single interval has a 95% chance of anything, because it either contains 0.35 or it does not.

Intervals, counted

Twenty intervals and one expected miss

The 95% belongs to the procedure, not to the interval in front of you. Twenty intervals from twenty samples make that visible in a way no definition does, and the one that misses is not a mistake.

A probe chosen rather than picked

What a chosen probe finds

On a chain of eight hundred draws the probe the earlier fields use misses 44% of the sets that are split. Its own residual off the rule's span misses 12%, for one least-squares fit.

The distribution itself

What normal actually looks like

A single quantile plot of forty normal points wanders enough to look suspicious. Twenty of them, all genuinely normal, show what the noise looks like — and any single panel a reader would have rejected is in there.

The crossing barely moves. Both methods' costs in one unit — assignments evaluated per usable draw — as the tolerance tightens. A hunt costs 1/p and rises without limit: from 2.22 at a tolerance of 1.2 to 357.14 at 0.18. A walk costs its autocorrelation time and barely moves. The two cross at a tolerance of 0.190 at one swap and 0.195 at eight — the whole family of proposal sizes crosses inside a band of about two hundredths, because where the crossing is, the large proposal has already lost its advantage. A multi-swap proposal is worth a factor of 5.65 in the regime where the walk should not be used at all.

What a block may vary

Where the gain is, and where the decision is

A bigger proposal is worth a factor of six at a loose tolerance and nothing at a tight one. The tolerances where it helps are the ones where a hunt costs two evaluations a draw, and the crossing barely moves.

Twenty cells of an interval that is exactly 95%, 1,000 replications each. The t interval covers exactly 95% in every cell. Estimated at 1,000 replications its cells read 93.9% to 96.5%, and 2 of the twenty are flagged by their own ±1.96 standard errors.

What makes it checkable

A coverage table with its own error

Twenty cells estimating the coverage of an interval that is exactly 95%, at a thousand replications each, read from 93.9% to 96.5% — and a table like that flags at least one of its correct cells on 69.9% of honest runs. Ten times the replications does not repair it: at ten thousand the same table still flags one 63.3% of the time.

What a fixed-width interval covers, by the number of blocks the trial ran before it stopped. Two thousand runs of each rule, the modelled weighting, a promise of 0.34. Reading its report: 4–8 blocks, 22.3% of runs, 78.2%; 9–12 blocks, 16.6% of runs, 90.4%; 13–16 blocks, 18.4% of runs, 96.2%; 17–20 blocks, 17.4% of runs, 96.0%; 21–28 blocks, 17.9% of runs, 96.4%; 29–36 blocks, 7.4% of runs, 99.3% — 91.45% overall. Reading the arms: 4–8 blocks, 0.0%, none; 9–12 blocks, 0.9%, 94.4%; 13–16 blocks, 30.4%, 95.6%; 17–20 blocks, 50.0%, 93.9%; 21–28 blocks, 18.0%, 94.4%; 29–36 blocks, 0.7%, 92.3% — 94.50% overall.

When a fixed width is reached

The trials that stopped early

A fixed-width trial that stops when its own interval is short enough covers 91.45% — an average of 78.2% among the 22.3% of runs that stop within eight blocks and 96% to 99% among those that run longer. Widening every interval by 17.1% brings the average to 95% and leaves the early stops at 85.6%, while 92.8% of runs now report an interval wider than the width they promised. Even doubling every interval leaves the early stops short.

How many of a league table's top ten are small groups, ranked four ways. A hundred groups with sizes from 4 to 400, of which 36% have twenty units or fewer. Small groups make up 36.3% of the true top ten, 62.1% of the top ten by raw means, 13.4% by posterior means and 22.9% by the posterior chance of being in the top ten. The three rankings recover 4.43, 5.38 and 5.47 of the true top ten.

What partial pooling does to one group, to the set, and to a ranking

A league table of a hundred

A hundred groups with sizes from 4 to 400, and a top ten to publish. Ranked by their own means, small groups fill 62.1% of the top ten against their 36.3% share of the true top ten. Ranked by posterior means they fill 13.4%. The ranking built from each group's chance of being in the top ten recovers 5.47 of the true ten, the best of three and barely half; and the group ranked first could hold any rank from 1 to 31.

What a pilot buys, σ = 1 against 3. Each point is 6,000 two-stage experiments of 100 units: a pilot of m per arm, then the rest split by the pilot's own estimate of the two spreads. Above the line the pilot has made the experiment worse than not bothering. The best pilot here is 8 per arm at 0.809, against 0.800 for a designer who knew the spreads — so the rule recovers 96% of what knowing them is worth. A larger pilot estimates the ratio better and has less left to apply it to, which is why the curve turns.

Splitting the units

Allocating on a guess

Every allocation rule in this field is a function of quantities the experiment is being run to find out. Fed a pilot's estimate of them, the rule that minimises the variance makes the experiment worse than not bothering — until the arms differ by about a factor of two, which is further than anyone would guess.

Balancing what has no levels

Balancing more than one number

The criterion generalises to several covariates without a word changing, which makes the question what it is worth rather than whether it can be done. Each one added takes a share of the assignment's freedom, and the imbalance left in every one of them rises.

Where a walk is cheaper than a hunt. Both costs in the same unit. A rejection sampler evaluates 1/p assignments per independent draw and does not care how large the trial is; a walk evaluates one per step and yields an effective draw every τ steps, and τ is a property of the constraint and the statistic together. They cross at a tolerance of 0.194 standard deviations, where about one assignment in 396 is admissible — far tighter than any trial is designed at. And the walk does not remove the acceptance cost; it pays it once, hunting for somewhere to start.

When the two are not independent

Draws that repeat each other

A hunt costs 1/p evaluations per independent draw. A walk costs one per step and yields an effective draw every τ steps. Both are counted in the same unit, and the walk is dearer at every tolerance a trial is designed at.

An AR(1) at φ = 0.5, 200 observations. The bars are the measured correlations; the curve is φᵏ, which is what an AR(1) must have. The band is ±1.96/√n, where an independent series would stay. The first bar is 0.53 against a band of ±0.14.

When the observations repeat each other

The check before the standard error

One number decides whether every interval in an analysis is trustworthy, and the check for it flags a lag-one correlation of 0.5 nine times in ten — and one of 0.2 only one time in five, where the interval already covers 88.6% instead of 95%.

What the long-run relation is worth, at α = -0.2. Root mean squared one-step forecast error of the error-correction model divided by that of the model fitted on differences alone; below one means the levels helped. With the equilibrium known the ratio is 0.929 at 100 observations and settles on 0.905 by 3,200, against a closed form of 0.905 that mentions no sample size at all; the excess at short series is the cost of fitting three coefficients on fifty observations. With the equilibrium estimated as well it is 1.127 at 100 — worse than differencing — and 0.914 at 3,200. The gap between the two curves is the cost of not knowing β.

Series that move together

The cost of differencing a pair

Differencing two cointegrated series makes every standard error honest and throws away the one thing known about where they are going. The error-correction model forecasts better by exactly what a closed form says — and at four hundred observations it is better on four series in five and worse on average.

A fit takes the low frequencies out of what it leaves behind. The autocorrelation of the errors, of the residuals of a fitted benchmark, and of those residuals rescaled by their own leverage. (I − H) removes the component of the errors lying in a column space that is itself slow-moving, so the residuals are less persistent at every lag — by 5.9% at the first and 26.6% by the fourth. The leverage correction is the standard repair for what a fit does to a residual's size; drawn here against what it does to a residual's dependence, it does nothing.

Counting what is independent

The residuals are not the errors

A fit removes the part of the errors lying in its own column space, and a persistent design's column space is itself slow — so what is left behind is smoother than what went in, at every lag, by an amount that grows with the lag.

Regression, and what the summary hides

Twenty residual plots

Judging whether a residual plot looks wrong requires knowing what a correct one looks like, and almost nobody has seen twenty of those. Here they are, from a model that is exactly right, at the sample size that matters.

The block length read on a quantile

What the interval covers

Eight rules and windows, and not one of them reaches its promised 95%. The range is 80.8% to 91.0%, and the choice between two block windows is a choice inside a shortfall that is four times larger.

The false discovery rate of twenty correlated tests, against the correlation. BH, every null true: 5.08% at 0, 4.86% at 0.3, 3.70% at 0.6, 2.34% at 0.9. BH, 10 of 20 real: 2.55% at 0, 2.53% at 0.3, 2.26% at 0.6, 1.66% at 0.9. BY, every null true: 1.46% at 0, 1.31% at 0.3, 1.03% at 0.6, 0.69% at 0.9. BY, 10 of 20 real: 0.72% at 0, 0.75% at 0.3, 0.64% at 0.6, 0.50% at 0.9. 20,000 families at each correlation.

Corrections, and what each controls

False discoveries that arrive together

Correlate twenty tests and Benjamini–Hochberg still holds its false discovery rate — 1.66% at a correlation of 0.9 with ten real effects, against 2.55% when the tests are independent. What changes is how the errors come. A family of true nulls reports anything 2.34% of the time instead of 5.08%, and when it does, it reports 16.56 false findings out of twenty.

How long an honest forecaster looks broken for. The calibration error shown by a forecaster with no miscalibration in it at all, at five record lengths, drawn against one over the square root of the length so that the closed form is a straight line through the origin. It is 0.1252 at fifty forecasts and 0.0090 at ten thousand, against a closed form of √(2K/πn) times the mean root bin variance which gives 0.1257 and 0.0089. The threshold drawn across it is 0.02, a figure routinely read as evidence that something is wrong; the mean falls under it at 1976 forecasts and the 95th percentile at about 4111. Below that, an honest forecaster and a miscalibrated one are being told apart by a statistic that is mostly the sample size.

A forecast that is a probability

The miscalibration a perfect forecaster shows

A forecaster whose true reliability is exactly zero shows a calibration error of 0.1252 on fifty forecasts and 0.0090 on ten thousand. Every one of 1,200 blameless hundred-forecast records exceeds the 0.02 routinely read as evidence of a problem, and the mean does not fall under it until 1,976 forecasts.

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