The thread: Count it, do not claim it

Choosing what the rule reads

A basis is a subspace

A balancing rule cannot tell one basis from another with the same span, so choosing what to hand it is choosing a subspace — and then what it removes of any outcome shape is a projection, computable exactly, with no trial anywhere in it.

One experiment, with the blocks getting smaller as the target comes into range. A single run at a requirement of 0.25, with the block sizes 5, 5, 11, 25, 11, 8, 3, 2 and a total of 70 observations in 8 blocks. The rule stops when the observations in hand reach z²σ̂²/d², with σ̂² pooled from the within-block contrasts — an estimate that moves as the run goes on, so the target moves too. Early blocks are large because the target is far away and cannot be overshot; late ones are small because a block is the granularity of the answer. The interval afterwards is built from the 8 block means and from nothing the rule looked at, and it has 7 degrees of freedom against the rule's 62.

The block size as a schedule

A block size that changes

The blinded rule's exactness never needed the blocks to be the same size. Letting the size be chosen from the contrasts as the run goes on leaves the coverage exactly where it was — and runs straight into an identity that says what a schedule can and cannot buy.

Four blocks, and only the ends matter. The weights a block carries, normalised so that the resample keeps the residuals' variance and only their covariances are attenuated. What separates these shapes, for everything that follows, is the value at the two ends and nothing about the middle: the first-order attenuation is −(w(0)² + w(1)²)/(2∫w²), which is -1.0000 for the rectangle, -0.3896 for the trapezoid cut off at half height, and exactly zero for both windows that reach the axis. The half-height trapezoid is in the table to be the case that separates a shape from a boundary value: it is smooth, it is tapered, and it buys none of the order the other two buy.

A block, weighted inside itself

A block weighted inside itself

The triangle every block resample attenuates by is not a fact about blocks. It is the self-convolution of a rectangle, and a block weighted down towards its own ends has a different one — whose leading term is the squared value at the two ends and nothing else about the shape.

Paying for a search

A break that was looked for

A two-regime whitening finds its change point by maximising a profile, and then reads a criterion that counts parameters. Under no break there is no parameter to count, because every position describes the same model.

The price of each thing the rule is not told. What each rule gives up against the best model available, at a persistence of 0.85 on a fifteen-candidate table, over 400 draws. Reading down: least squares with the ordinary penalty; the whitening at the true ρ; the same at a ρ̂ estimated per candidate; that rule with the term the Gaussian likelihood carries and it omits; a Bartlett-tapered Ω̂ estimated once from the fullest candidate at L = 8; the same estimated per candidate; and the truncated Ω̂, which exists on only 45.0% of draws and is averaged over those. Knowing ρ recovers 89.9% of what counting rows gives up, estimating it 83.4%, and estimating a whole covariance 75.6%.

Estimating the dependence, not naming it

A covariance with no parameter in it

The whitening that repairs a criterion is told the dependence is a first-order autoregression and left to find one number. A real dependence is not one number, and the obvious estimate of it is not a covariance matrix.

What a median split can see. A standard normal covariate with its median marked, and the mean of each category as a vertical rule: -0.7979, 0.7979. A rule that balances the categories is balancing those numbers and nothing else, so the part of the covariate it can act on is the variance between them — 0.6366 of the total, which at two categories is exactly 2/π because the two half-normal means are ±√(2/π). The rest, 0.3634, is variation inside the categories that the rule cannot see and does not touch: the assignment within a category is still a coin. Everything the next figure measures is a consequence of this one, and it is available before any unit has arrived.

Balancing what has no levels

A covariate with no levels

Every balancing rule on this site reads a level. Age and blood pressure have none, so somebody cuts them into categories — and a median split can see exactly 2/π of a normal covariate, whatever the rule does with the halves.

What each rule gives up against an oracle that is arithmetic. Expected squared error of the candidate each rule selects, minus the expected squared error of the best candidate in the table, over 500 draws of 120 rows. Both quantities are closed forms — σ_S²(1 + q/(n − q − 1)) — so the only Monte Carlo here is over which candidate got picked. The hold-out spends half its rows measuring what the criterion computes, and pays 1.8 times as much for it. Schwarz's criterion is worst because it is answering a different question: which candidate contains the truth, rather than which one forecasts best.

Scoring a search without spending data

A criterion is a prediction of the hold-out

A rolling hold-out spends half the sample measuring what a criterion computes from all of it. Against an oracle that is arithmetic rather than an estimate, the criterion gives up 0.01701 and the hold-out 0.03200 — and the number the hold-out reports for its own winner is optimistic by more than either.

The expansion that never terminates. The Hermite coefficients of a median split, in magnitude, against the reference j to the power −3/4, anchored at the first one. Every even order is exactly zero because sign is an odd function, and every odd order is not, so no truncation is exact — where a polynomial of degree d is exact at any order past d. Summed, the tail past J falls like 1/√J: sixty orders still leave 6.6% of the variance outside. That statement is what made a cut dictionary's geometry unavailable in closed form, and it is a statement about the function against itself. What it is not is the accuracy of an inner product between two correlated variables, where every term past J carries a factor of ρ^m as well.

A cut point, at a correlation

A cut is not a polynomial, and it does not have to be

A threshold's expansion never terminates, which is why a balancing dictionary's geometry was closed for powers and taken to draws for cut points. Conditioning on the second variable closes it for both.

Fitted together, or fitted after

A dependence fitted with the line

Every whitening in this collection reads the dependence off a set of residuals, and residuals are not errors. Fitting the two together recovers most of what that costs, and changes almost nothing about the decision it feeds.

Four dependences a single parameter cannot tell apart. Every law here is standardised to a lag-one autocorrelation of 0.8, so a rule told the errors are a first-order autoregression finds the same number in all four and has no way of seeing what separates them. The geometric decay is the world in which estimating a covariance rather than naming it was priced, and found to cost. The five-period moving average has 0.200 at the fourth lag and exactly nothing past it, where the geometric law says 0.328 at the fifth. Long memory at d = 4/9 is still at 0.576 by the twentieth lag, where the geometric law has reached 0.012. The break has no autocorrelation function at all: what is drawn for it is the average over the pairs at each gap, which is what a stationary estimate converges to.

The shape a dependence has

A dependence with a shape

Four ways for errors to repeat, all with the same first lag and nothing else in common. A rule told the errors are a first-order autoregression finds the same number in all four, and is right about one of them.

Two covariates make the dictionary an outer product. Four functions of each covariate, and everything a balancing rule may be handed. The margins are the 8 main effects and the block between them is the 16 interactions, which are 66.7% of the dictionary. Every inner product in it is closed form — ⟨f₁g₁, f₂g₂⟩ = ⟨f₁,f₂⟩⟨g₁,g₂⟩ when the covariates are independent — so nothing about the geometry gets harder. What gets harder is the counting: choosing k of 24 is C(24, k), which is 10,626 at four and 735,471 at eight.

When the set is too large to walk

A dictionary that is a product

Two covariates make what a balancing rule may read an outer product — eight main effects and sixteen interactions — and every inner product in it is still closed form. What a rule holding all eight main effects removes of a pure interaction is not small. It is zero.

The rule is parity, and it runs both ways. At a correlation of 0.5, four combinations of a dictionary and an outcome shape. The joint sign flip (X, Y) → (−X, −Y) leaves the bivariate normal alone at every correlation, so a function that changes sign under it is orthogonal to one that does not. A product of two odd functions is even; a product of an odd and an even one is odd. So an odd dictionary removes exactly none of the first and something of the second, and an even dictionary does the reverse — which it does, to machine precision, in both of the two rows that should be zero. This is one rule where there had been two: that a median split's square is constant, and that a polynomial dictionary contains the products a correlation generates.

What a dictionary buys and what it costs

A dictionary that is neither

A rule handed two median splits removes none of their interaction; a rule handed two covariates removes none of their product. Those were two results with two explanations, and they are one result with one — and finding it corrected the number underneath both.

A covariance with no parameter

A family before a fit

A regression's coefficients and one correlation can be maximised together. Replace the correlation with an estimated covariance and there is nothing left for "jointly" to mean — until a set of covariances is named, and the set turns out not to contain the truth.

One margin rises; the other turns over. The two halves of the table's margin across the sweep: a lower-tail copula's own leak with a symmetric covariate, and a covariate skewed at 0.95 under a Gaussian copula. The marginal's leak rises at every step, from 3.727% to 36.056%. The copula's does not: it rises to 9.064% at a Spearman of 0.6 and falls to 8.219% by 0.7. It has to turn over, because at a rank correlation of one the two variables are a deterministic function of each other and there is no interaction left for a split to leak. So the margin of the table turns over before any cell in it does.

The same table at seven correlations

A margin that turns over

A skewed covariate's leak grows without limit as the dependence strengthens. A copula's own leak does not — it peaks at a rank correlation of 0.6 and falls. The margin of the table turns over before any cell in it does.

The correction is not a property of the sample. tr(HΩ)/q for each of fifteen candidates, at ρ = 0.7. Two candidates that fit the same number of coefficients need corrections that differ by as much as 1.49, because one of them is fitting the persistent predictors and the other is not — so no single number can be right for both, and the scalar n/n_eff = 5.537 is above every one of them. The four predictors carry persistences 0.9, 0.6, 0.3, 0; at one persistence for every column the whole spread collapses and a scalar looks exactly as good as the trace.

Counting what is independent

A penalty is a trace

Akaike's 2q is not a count of coefficients. It is the answer a trace collapses to when the rows are independent — and once they are not, the trace is still the right object and is no longer the count.

A proposal that moves more, refused more often. The two halves of the trade, both exact, on the 410 admissible assignments of twelve units. The integrated autocorrelation time of an imbalance the rule was never handed falls from 7.30 at one swap to 3.97 at three, and the acceptance rate falls with it, from 58.8% to 40.8%. A rejected proposal costs one evaluation and leaves the chain where it was, so acceptance is not the price of anything and the ranking by acceptance is the reverse of the ranking by cost. Past three the family folds: exchanging k of six from each arm is the complement of exchanging six − k, so k = 5 has the same 36 proposals as k = 1 and k = 6 has 1.

What a block may vary

A proposal that moves more than two units

The walk's autocorrelation is a fact about its step size and not about its acceptance rate. Exchanging three units from each arm mixes nearly twice as fast as exchanging one, and is refused a third more often.

The rate and the size of a disagreement

A rate times a size

A sweep reported what it costs to let every candidate choose its own tuning parameter and found it flat across the list. It was reporting a product, and the two things multiplied together do not behave the same way at all.

What each variant loses before anything has been searched for. The mean loss differential of each of the eight variants against the benchmark, over 600 tables of 60 origins, with every fit given 71 rows. The series is an AR(1) and every variant adds a lag whose coefficient is zero, so in population the two forecasts are the same forecast and the difference drawn here is estimation noise and nothing else. The marked line is σ²(q₁ − q₀)/n = -0.01408, which is an expression in how many coefficients each model has and how many rows it was fitted on — it knows nothing about the series, the persistence or which lag the variant added, and every bar is within a fifth of it. This is the amount a reference distribution recentred at each column's own sample mean believes the candidates are already behind by.

Searching among fitted models

A table of nested models

A benchmark and eight variants of it, each adding one thing. Every variant is behind before the search begins, by an amount that can be written down before the data exists — and the two most natural ways of reading the table are wrong in opposite directions.

The test, checked where the answer is known. A fourteen-unit trial at eight tolerances. At each one the admissible set is enumerated — 1534, 886, 304, 158, 126, 116, 102, 84 assignments — and its components counted, which is only possible because 3432 equal splits of fourteen units can be walked. The dots are the test, which walks none of them: two chains, one started at an assignment and one at its complement, compared on a statistic the rule was not handed. Filled marks are tolerances the enumeration says leave the set in more than one piece. The test fires on every one of them and on none of the others, 0 misses and 0 false alarms.

What a chain cannot report

A test rather than a survey

A thin admissible set falls into an arrangement and its mirror image, and the walk that samples it is uniform on half the reference distribution for ever. That was found by enumerating fourteen units, and enumeration stops at twenty-four.

The construction survives a difference of two weighted means. Coverage of δ̂ ± t√(S_D²/H) on b − 1 degrees of freedom, over 900 runs at a requirement of 0.3, where δ̂ is the block differences weighted by h_b = (1/m_A + 1/m_B)⁻¹ and H is their total. The theorem the one-mean field rests on goes through with h_b in place of the block size, and the reason is that the weights a weighted least squares decomposition needs are the inverse variances — which is exactly what h_b is. The stopping rule reads only within-arm within-block contrasts, so it is a function of nothing the interval reports, whatever it does with the block sizes. Each bar is within 2.9% of the level it claims.

A promise about two arms

A width promised for a difference

The exact fixed-width interval was built for one mean. Two arms make the target 42.7 units of effective size and each unit costs four observations, so the same promise about a difference costs 169.4 rather than 42.7 — and the theorem survives untouched with the harmonic size in place of the block size.

The stopping rule costs more than the weighting does. Coverage over 2000 runs of a trial whose variance ratio drifts by a factor of twenty, at three ways of deciding when to stop. Twelve blocks fixed in advance is the top line and reproduces what a trial of fixed length delivers. Stopping when the reported interval is short enough is the bottom line, and it costs between 3.0% and 5.5% of coverage — including for the rule that is told every block's true ratio, which is what says the shortfall belongs to the stopping and not to the weights. Stopping on a width predicted from the within-arm sums of squares is the middle line, and it is back at the fixed-length values. The standard error on each point is 0.49%.

When a fixed width is reached

A width the trial has to stop for

The weighting that covers at 94.9% on twelve blocks covers at 91.5% when the trial stops as soon as its interval is short enough — and so does the rule that is told every block's true variance ratio. The shortfall is the stopping, not the weights.

One zero is arithmetic and one is a symmetry. What two balancing rules remove of the interaction they are aimed at, on five joint laws of the ranks matched at a Spearman correlation of 0.4, with a normal covariate throughout. A rule holding a median split of each covariate removes exactly nothing of the product of the splits under every one of them, including the two that are not symmetric under reflection — and the reason is not a symmetry at all: a centred median split takes the values ±½, so its square is a quarter identically, and the interaction is orthogonal to both main effects whatever the joint law is. A rule holding the mean of each removes exactly nothing under the three radially symmetric copulas and 7.71% under the two that are not. Bars at the floor are exact zeros; the axis cannot draw 9e-32.

The other half of the dependence

A zero that is arithmetic

A median split's exact zero was explained by a symmetry of the latent normal. It holds under a Clayton copula, which has no such symmetry, because a centred median split squares to a quarter identically.

One zero holds and one does not. Three rules, at a correlation of 0.5, against the skewness of the covariate. A rule balancing the mean of each covariate removes exactly nothing of their product when the marginal is symmetric — including the heavy-tailed symmetric one at skewness zero, which is what says the guarantee needs symmetry rather than normality — and removes up to 29.7% when it is not. A rule balancing a median split of each removes exactly nothing of the product of the splits under every marginal here, to 1e-30: both sides are functions of the sign of the latent normal, and a monotone transformation moves neither. A rule balancing a threshold at a value on the covariate's own scale removes between 4.9% and 22.5% — it never had a zero to lose, under any marginal at all.

A guarantee that needed a symmetry

A zero that rests on a symmetry

A balancing rule removes exactly none of an interaction between two odd functions, at every correlation. The argument needs the joint sign flip to preserve the law, and no real covariate is symmetric about anything.

Two designs for one model, and the weights are not equal. Where the runs go, for the same two-parameter model at K = 1 and a ceiling of T = 10. The D-optimal design for both parameters is the familiar one: half the runs at 0.8333 and half at the ceiling. The design for the half-saturation constant alone moves the lower setting down to 0.6040 — where the response curve is still bending, which is where K is visible — and, unlike every design in the two fields before this one, it does not split the runs evenly: the weights are exactly 1/√2 and 1 − 1/√2, 0.7071 and 0.2929, at every K, V and T. The equal weights of D-optimality were a consequence of asking about both parameters at once, and nobody had to notice while that was the only question being asked.

What the design is asked to guarantee

An efficiency that is a ratio

A design chosen for a model is not a design chosen for the parameter somebody wanted. Asking for one of two parameters moves the runs, unbalances the weights, and costs the other question exactly 15.07% — at every setting, because it is algebra.

Three intervals, one shortfall. What each of three intervals actually covers, at four rules and two block windows, over 300 samples of 120 rows. All three are built from the same resamples on the same draws, so a difference between them is a difference in what is done with the resampled series. Not one of the twenty-four cells reaches the ninety-five per cent it promises. The studentised interval runs from 75.7% to 92.3%, the percentile interval — the earlier field's — from 80.0% to 89.7%, and a normal interval on the same scale from 81.7% to 89.0%. The standard repair for a percentile interval's shortfall does not repair it.

The interval, studentised

An interval that carries its scale

A percentile interval inherits the resampled distribution's skewness and its scale error together. The standard repair is one extra variance per resample. It was named and not run, so this runs it.

$Four rules, three shapes, and no ordering that survives. The variance of the unadjusted treatment estimate under each rule, as a fraction of the variance a coin gives, over 450 trials of 200 units each. Against a covariate that enters linearly the rule that reads the number nearly halves it. Against a threshold at 1 it removes about a fifth. Against a quadratic every rule here is at or worse than a coin — they are all optimising a criterion that is one over the variance of an estimate in a model this outcome does not obey, and a constraint that helps nothing still costs something. Nothing in a trial says which column it is in.$ The shape the covariate enters by

Balanced on the wrong function

A rule that reads a covariate's numbers halves the variance of the treatment estimate, if the covariate enters the outcome as a straight line. If it enters as a threshold the rule is worth a fifth of that, and if it enters as a curve every rule here is worse than a coin.

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.

Eight groups, τ = 1 against a within-group spread of 3. Each row is a group. The hollow circle is the group's own mean, the filled one is the estimate after pooling, and the small mark is the truth the data was generated from. The group of 3 moves 75% of the way to the population mean of 0.10; the group of 40 moves 18%.

Groups that borrow

Eight groups, one population

Eight hospitals are neither one hospital nor eight unrelated problems. The two obvious answers cost 2.23 and 1.15 in squared error; the estimate between them costs 0.88, and the weight it uses is not a matter of taste.

Every split of 100 units, σ = 1 against 3. Each point is one integer split, with its variance computed exactly rather than simulated. The minimum is at 25:75, which is the ratio of the spreads 25:75, and equal allocation costs 25% more variance — the same as throwing away 20 of the 100 units. The shaded band is every split within 5% of the best, and it runs from 17% to 35%: sharp to state, flat to sit on.

Splitting the units

Not half and half

The same units, the same measurements, the same analysis — and a different variance, decided before anything is measured. When the two arms have different spreads the best split is σ₁ : σ₂, equal allocation costs 2(σ₁²+σ₂²)/(σ₁+σ₂)², and at three to one that is a quarter of the experiment.

Which allocations reverse the overall comparison. The per-group success rates are held fixed; only the split of each group between treatment and control changes. 32% of the allocations reverse, and the worst reverses by 13.1 percentage points.

Reversals that are not errors

Simpson's reversal is a region, not a table

The treatment wins in both groups and loses overall. That is normally shown with one famous table, which cannot answer the two questions a reader has — how often, and how large. Swept, it turns out to occupy 31% of the allocation space.

A charge for a covariance's own dimension

The charge nobody derived

A band of lags is charged one log-likelihood unit apiece, because that is what a regression coefficient costs. A band's numbers are not regression coefficients, and measuring what they actually cost puts the convention out by a factor of nearly three.

The number the comparison was missing. What it costs to choose the tuning parameter for every candidate separately rather than once for the table, under AR(1) at 0.8, paired on the draw. The window's figure is the one the earlier field reported; the order's is the one it named and did not make. They are the same size — 0.00401 against 0.00360, at 2.30 and 1.72 paired standard errors — and matching the lists at eight values leaves them the same size again. The prediction that the longer list would make the order's cost the larger of the two is not what happens; what happens is that the two rules cost the same once they are scored by the same criterion, which took a missing term to arrange.

How long the list is

The comparison that was not made

Choosing a whitening's window separately for every candidate costs 0.00401 of regret. The same question about an order was named and left, because the two lists are different lengths. The order's answer is 0.00360, and matching the lists changes almost nothing.

The same study read three ways. At time 2 the truth is 0.497. Kaplan–Meier gives 0.532; dropping the censored subjects gives 0.180; treating the censoring time as the event time gives 0.392. Both naive readings understate survival, because the subjects they mishandle are the ones doing well.

When the data stops early

The data that stops early

A subject still event-free when a study ends is not missing and not observed. It is known to exceed something, which is a third state most tools have no slot for — and the two obvious ways of forcing it into one are wrong by 31 and 13 percentage points.

A design that is right once, and one that is never wrong by much. Three designs for the Michaelis–Menten model, scored at every true value of K across a 16-fold range. The peaked curve is the two-point local design built at K = 1: 100% there and 66.7% at the worst point of the range. The curve just under it is the design that averages the criterion over a uniform prior on the same range, which is barely different — 67.9% at worst — because averaging is dominated by the middle of the range where the local design is already good. The flat line is the maximin design: 3 settings, never above 80.8% and never below 78.8%. Its worst case is 12.0 points better, and what it gives up is the 21.2 points at the one value the local design was built for.

A design that assumes less

The design for the worst case

A design for a non-linear model is optimal at a guess about the answer. Averaging over a prior repairs that on average; protecting the worst value in a range is a different problem, with a different answer, and it needs a third setting to reach it.

Four runs, and the term they cannot reach. Every run sits at a corner, so x₁² and x₂² are 1 at every run and both columns are copies of the intercept. The normal matrix is singular: the design has no information about curvature at all, and no analysis can recover it.

The surface between the corners

The design that cannot see a curve

A two-level factorial has every run at a corner, where every squared term equals one — so the column that would estimate curvature is a copy of the intercept, and the design has no information about it at all. A few runs at the centre buy one number back, and only one.

The eighth was not a constant. The probability that a per-candidate tuning list changes which candidate the table selects, at each of 5 separations between the candidates, over 800 draws apiece. The earlier field reports this flat at about an eighth across list length, on a table and a world it never varies. Vary how much the omitted coefficients are worth — one multiplier, with the table, the list, the law and the sample size all held — and it runs from 17.6% to 1.5%, a factor of 11.75. The world in which every candidate is true is the world in which the tuning list decides most; the world in which one candidate dominates is the world in which it decides nothing.

What decides whether a tuning list decides

The eighth that was not a constant

How often a per-candidate tuning list changes which candidate wins is reported flat at about an eighth across list length. Vary how far apart the candidates are instead and it runs from 17.6% to 1.5%.

The allocations the rule could have made, from these exact patients. One 200-patient trial allocated by response-adaptive randomisation, re-randomised 999 times. No outcome is redrawn anywhere in this figure: each re-randomisation runs the same rule over the same patients in the same order, so what is drawn is the set of experiments that could have happened rather than a sampling distribution. The observed |z| is 1.417, 258 of the 999 re-randomisations reach it, and the p-value is (1 + 258)/(1 + 999) = 0.2590. The curve is the half-normal the ordinary analysis reads the same statistic against; its 5% point is 1.96 and this distribution's is 2.101.

The reference distribution the design supplies

The experiments that could have happened

An adaptive trial's allocation is a function of the outcomes it will later be compared against, so the ordinary analysis rejects a true null 9.2% of the time. Hold the outcomes fixed, re-run the rule that assigned them, and count — the same statistic against a reference distribution the trial could actually have drawn from is back at 4.0%.

The fourth-order expectation, by two routes. Every inner product in an eight-term slice of the dictionary at ρ = 0.5, computed from the linearisation and Mehler's formula and counted from two hundred thousand draws of a correlated pair. The entries that matter are the ones off the main effects: ⟨f(X)u(Y), g(X)v(Y)⟩ is a fourth-order expectation, which the independent-covariate field could not write down. The worst departure is 1.99 standard errors over 36 pairs, measured in each pair's own error because the entries differ in size by two orders of magnitude.

When the two are not independent

The fourth moment that was missing

Mehler's formula makes the main effects exact at any correlation and stops there, because the interactions need an expectation of four Hermite functions rather than two. A linearisation turns the four into two, and the whole geometry becomes closed again.

Where a taper's case begins

The gap a sample shows

The exact difference between two block windows at a block length of twenty is three tenths of a point. What a hundred and twenty rows report is four and a third, because the autocovariances the window is applied to are attenuated too.

What the procedure may not read

The guess with two numbers in it

Every optimal design for a non-linear model is optimal at a guess. Where the model has one parameter that moves the settings, that guess is a number and everything about it comes out in closed form; where it has two, three constants become functions and one of them becomes zero.

A quantile is the dearer reading, everywhere. The error each rule and window delivers on the two error readings, over 400 draws. The lower pair of lines is the implied long-run variance — the instrument the earlier field uses — and the upper pair is the 95% point of the standardised resampled mean, read against the finite-sample truth of 3.889 found by simulating the law directly. The quantile costs more at every one of the eight cells: at the plug-in rule it is 59.1% against 45.3% for the taper. That is not a defect in the bootstrap; a quantile is a statement about the shape of a distribution as well as its scale, and a fixed number of resamples estimates a tail worse than a variance. What matters for the comparison is that the two orderings between the windows are not the same, which the margins figure is about.

The block length read on a quantile

The instrument and the reading

Every comparison between two block windows in this collection is an error in an implied long-run variance. Nobody reads a long-run variance. Read on the 95% point a test uses, the same bootstrap costs half as much again.

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%.

A probe chosen rather than picked

The part the rule already took

A diagnostic that reports on what a balancing rule was not handed is run through a column that is 92% inside the span the rule balanced — because orthogonality in the population is not orthogonality on fourteen units.

Two diagnostics, one answer, two different moments. The two-chain statistic on a covariate probe and on the trial's own difference in arm means, at seven tolerances of a fourteen-unit rule, against the enumerated truth. Both are quiet wherever the set is one set and both fire wherever it is not, at every tolerance — which is what says the outcome probe is the same test rather than a resemblance of it. The difference between them is not accuracy and it is not power. It is when: the covariate probe can be run before a single outcome exists, when a practitioner can still loosen the rule or change the sampler, and it can be run again on a different function if it comes back quiet. The outcome probe runs after the trial, on the one column the trial produced, and what it can do with a positive verdict is repair the p-value rather than the design.

The diagnostic after the trial

The statistic the p-value is about

The test for whether a balanced-assignment walk reaches its whole set is run on a covariate function chosen before the trial. Run on the difference in arm means it is the same test, and it is about the number the trial publishes.

The same 40 units, arranged two ways. Both designs estimate the same effect of 0.5 and both are unbiased — 0.488 and 0.497. The blocked design's estimate has standard deviation 0.318 against 0.692, a variance ratio of 0.21 where the model predicts 0.20.

Decided before the data

The variance removed before the data

Arranging forty units in pairs rather than assigning them at random cuts the variance of the estimated effect to a fifth — and the fifth is knowable in advance, because it is exactly the share of the variance the pairs do not carry.

The curvature is in the denominator. The optimism a Bartlett band of each width actually costs, divided by that width, on two ways of measuring the width, over 2000 draws at 120 rows. Measured in the weights the band spends — Σ w(k), which is what the earlier field levies its charges on — the reading falls from 0.9528 at two lags to 0.7486 at thirty, so a charge proportional to the summed weights is too dear at one end and too cheap at the other. Measured in the pairs the band uses — Σ w(k)(1 − k/n), because a lag of k is an average over n − k products — the same readings are flat from 4 lags up, at 0.0084 of χ² per width against 0.2359. The correction has no fitted parameter in it: it is a function of the window, the width and the sample size.

A charge that is not a straight line

The width a band is measured in

A tapered covariance band spends 84% of its own weights at two lags and 74% at thirty. Every charge in the collection is a straight line through the origin in those weights, so it is too dear at one end and too cheap at the other.

Where one rule becomes three. Every arrival in 200 simulated trials is put to all three scores, and the picture is how often they would send that patient to different arms. The range and the pairwise sum are the same rule at two arms and at three — for sorted counts the pairwise sum is twice the range, so the arm that minimises one minimises the other — and they part company at four, where the pairwise sum is 3(d − a) + (c − b) and the range still sees only d − a. The variance disagrees with both from two arms onwards, on 5.4% of arrivals at two and 27.0% at five, because the scores are summed over 3 factors and a sum of squares does not order the candidates the way a sum of absolute values does. All three are called minimisation.

More arms than two

Three arms and three scores

Minimisation balances a trial by keeping the arms' counts even inside every prognostic factor. With two arms there is one way to measure how uneven two counts are. With three there are several, they are all called minimisation, and they send different patients to different arms.

Overlap and complementarity, separated

Two effects in one number

How much two searches over one sample share is measured as the net of two things — ground both of them find, and configurations only the joint search reaches. One extra supremum per draw separates them exactly.

Both halves of the dependence at once

Two failures that cancel

A mildly skewed covariate under a lower-tail copula leaks 0.002% of an interaction where each failure alone leaks eight and seven per cent. Turn the copula over and the same pair compounds.

Two searches over one sample

Two searches, one sample

A searched break in a regression manufactures 34.7 of likelihood ratio where a count of coefficients says 11.1. A searched window manufactures 84.0. The two together manufacture 99.4, not 118.7.

Two searches over different features

Two searches that share nothing

Two searches over independent columns remove shares of the residual sum that add exactly. On the scale a chi-square point is quoted on they look super-additive by a fifth of a unit, and none of it is overlap.

Exact in the corner, where nothing was. Coverage of a nominal 95% interval on five designs, at a required half-width of 0.3. The first four are the two-arm field's own and the fifth is its corner — two variances, block sizes that swing by eight, and an allocation that alternates between five to one and one to five — where neither of that field's two conditions holds. The effective-size weights over-cover there at 98.40%; the weights h_b(λ) = (1/m_A + λ/m_B)⁻¹ cover at 94.84%, and at 94.84% when λ is estimated from the within-arm contrasts rather than known. Nothing here is supposed to move.

The weights the corner needs

Weights that need only a ratio

A fixed-width interval about a difference is exact under either of two conditions and under neither in the corner. It is exact there too, and the only thing it needs is how much larger one arm's variance is than the other's.

Coverage of four nominal 95% intervals, n = 20. Computed exactly by summing over all 21 possible counts, not simulated. The Wald interval drops to 18.2% and is jagged everywhere; Clopper–Pearson never falls below 95% and pays for it in width.

Intervals, counted

What the 95% refers to

An interval that claims 95% is making a checkable statement about a procedure, not about the interval in front of you. Build every possible sample and count, and the interval taught first turns out to cover 87.6% of the time.

The familywise error rate with no correction, α = 0.05. Two routes: the curve is 1 − (1 − α)^m and the points are counted over 6,000 simulated families of true nulls. With twenty tests the chance of at least one false positive is 64.1%.

Corrections, and what each controls

What the correction corrects

Twenty tests of true nulls produce at least one false positive 64% of the time, and the closed form and the count agree. Bonferroni holds it at 5% and Holm holds it at 5% while finding more. Nobody should still be using Bonferroni.

Three quantities, and only one of them crosses zero. Two forecasts of an AR(1) — the last value carried forward and the mean of the last 60 observations — at 1 step ahead. The curve through zero is σ₁² − σ₂², the difference in expected squared error that a comparison of accuracy tests; it changes sign at φ = 0.4922. The two curves above it are σ₁² − σ₁₂ and σ₂² − σ₁₂, the quantities the two encompassing tests are about, and neither of them comes near zero anywhere: the smallest value either takes across the range is 0.008 times the variance of the series. All three are closed forms in φ, R and h with no simulation in them. Equal accuracy is one hypothesis about this picture and encompassing is another, and a set of numbers can satisfy either without the other.

The best of a set, and what the search costs

What the other forecast adds

Two forecasters, one series, and two different questions about them. Which is more accurate has an answer that changes with the persistence of the series; whether either is redundant has an answer that never changes at all.

What eight groups say about τ, when the truth is 1. The posterior density for the population spread after eight groups whose standard errors run from 0.5 to 2.1. The shaded band is the central 95% interval, from 1.02 to 4.44; the posterior median is 1.99 and the mean 2.18. The vertical mark at 1.07 is the moment estimate that empirical Bayes substitutes and then treats as known.

The spread, and its own uncertainty

What the plug-in forgets

The shrinkage weight needs a population spread, and the population spread has to be estimated from eight numbers. Empirical Bayes estimates it, substitutes it, and proceeds as though it were known — and the interval that comes out covers 79% rather than the 95% it claims.

A probe from what the rule blocks

What the rule blocks

A balancing rule breaks the admissible set into pieces by refusing exchanges. Which exchanges it refuses is computable from the design and the tolerance alone, before any assignment exists — and it makes a probe.

A search with no fixed point

When the benchmark is a candidate

A specification search with a benchmark nailed down is the case with a closed form. Take the nail out — let the model that would have been reported be one of sixteen, chosen by the same data as its rivals — and the same true null is read three ways, at 2.0%, 7.8% and 76.2%.

One comparison, and the two error bars it can be given. 60 rolling origins, a window of 60 observations, forecasts 4 steps ahead, at the persistence φ = 0.8256 where the two benchmarks have exactly equal population mean squared error. Each mark is one origin's difference in squared error; the horizontal line is their mean, 0.6522. The two vertical bars at the right are ±1.96 standard errors round that mean computed two ways — 0.5337 treating the differences as independent, 0.6880 allowing for the overlap between neighbouring forecasts. The null is true here by construction, so an interval that excludes zero is a mistake, and the narrow one does it far more often than the wide one.

Comparing two forecasters

Which forecast is better

Two forecasters, one series, and a difference in mean squared error. Whether that difference is real is a hypothesis test, its terms are not independent, and the standard error it needs is not the one a t-test computes.

The tail past the last observation

Three shapes, one limit

A normalised sum has one limit and a normalised maximum has three, indexed by a single number. Twenty blocks put the sign of that number right 97.3% of the time — and naming the family from a light-tailed record gets worse as the record grows, from 83.0% at twenty blocks to 4.8% at five hundred.

The first stage an instrument needs is set by the violation nobody can see. The error each estimator converges on when the instrument has a direct effect of 0.05 on the outcome — a path the exclusion restriction asserts is zero and no sample can check. The instrument's error is δ/π exactly, so it is the reciprocal of the very quantity that made the method work: 1.0000 at a first stage of 0.05 and 0.0833 at 0.60. Least squares carries the confounding instead, at 0.3440 at a first stage of 0.30. The two cross at π = 0.1389, and the crossing is exactly δ times 2.7778 — the first stage an instrument needs is proportional to the violation it is assumed not to have, and below that line the method being corrected is the better estimator.

A variable that moves one thing only

The assumption nothing tests

An instrument buys a causal effect with an assumption no sample can check, and the price is set by the same quantity that made the method work. The first stage it needs is 2.7778 times the violation it is assumed not to have, so a direct effect of 0.05 demands a first stage of 0.1389 and least squares wins below it.

One wrong model, four designs, four slopes. The slope a straight line converges to when the truth is a quadratic, under four covariate distributions, by two routes: the population projection in closed form, and the mean of 2500 fitted slopes at 200 rows apiece. The even spread over [0, 2] gives 1.6000 and the same spread moved to [1, 3] gives 2.6000, while widening it to [0, 4] gives 2.6000 — the same number as the shifted one, because a symmetric design's target is the truth's tangent slope at the design's own mean and does not read the spread at all. An exponential spread with the SAME mean as the first gives 2.6000. So two studies of one world, each fitting the same wrong model, honestly report slopes 1.0000 apart, and neither is making an error.

A standard error for a model that is wrong

What a wrong model estimates

A straight line fitted to a curved truth converges on the tangent at its own design's mean. Two honest studies of one world, fitting the same wrong model, report 2.600000 and 1.600000, and neither is in error.

The coverage is exact and it is not the nominal rate. ⌈(m+1)(1−α)⌉/(m+1) against m, the number of calibration points, at α = 0.05. It is a closed form and needs no data. It never falls below 95.0% and never reaches 1−α+1/(m+1), the two bounds the rank argument gives. It equals 95.0% exactly at 10 of the 182 sizes drawn — the sizes where (m+1)α is a whole number, which are 20 apart — and sits above it everywhere else, worst at 38 points where it is 97.4359%, or 2.4359% of coverage nobody asked for. Below 19 points there is no such order statistic and the interval is the whole line, which is where the curve starts.

Coverage without a distribution

Coverage from exchangeability alone

A conformal interval's coverage is a fact about the ranks of m+1 numbers, so it can be enumerated before any data arrive — all 40,320 orderings of eight values, agreeing with the closed form to machine precision. What that exactness delivers is not 95%.

What each forecaster says, and what is true. The true probability of the event given a forecaster's signal, and what three forecasters report. The truth is Φ(-0.5 + 1.2w) and the honest forecaster reports it, so its curve and the truth are the same line. The loud forecaster pushes every probability towards the ends and the hedged one pulls every probability towards the middle; both have their mean report held at the base rate of 0.3744, so each crosses the truth exactly once and neither can be caught by checking its average. Their reliability terms are 0.008500 and 0.013025 against the honest forecaster's zero, and all three have the same area under the ROC curve, 0.868312.

A forecast that is a probability

An identity in three terms

Reliability minus resolution plus uncertainty is quoted as a rewriting of a probability score. It is an identity to 2.6·10⁻¹⁵ on the one grouping where reliability is the whole score and resolution exactly cancels uncertainty, and it is out by 0.004125 on the coarsest grouping anybody would actually draw.

A weight that balances, and one that unbalances. The standardised difference between the arms on each covariate, integrated over the population rather than counted in a sample. Unweighted, the arms differ by 0.8310 on the first covariate and 0.6015 on the second, which is what makes the raw difference of arm means 2.7102 against a true average effect of 1.0000. Weighting each unit by one over its own assignment probability removes both differences exactly — -2.78e-17 and -5.69e-19, which is machine precision and not a small number — because the weighted density of the treated arm is the population's own whatever the propensity is. Weighting by a score fitted without the second covariate balances the first to 0.0035 and pushes the second out to 0.7057, further apart than doing nothing.

Weighting one sample into another

A score that balances

Weighting each unit by one over its own assignment probability drives the standardised difference between the arms from 0.8310 to 2.8×10⁻¹⁷ — exactly, not nearly. A score fitted without the second covariate leaves that covariate at 0.7057, further apart than doing nothing at all.

The value that is not there

Three mechanisms and one dataset

Four rules for which outcomes go missing, each calibrated to lose the same 35% of the rows and each leaning on what it reads with the same coefficient. Three leave the fitted slope exactly where it was, and the one that reads the outcome moves it by 0.163531.

20,000 p-values from a true null, n = 12. Flat, as it must be: under the null a p-value is uniform on (0,1). The Kolmogorov–Smirnov distance from uniform is 0.0090 (p = 0.81). That flatness is the check that catches an error a single rejection rate would miss.

Tests, and the second number

A p-value that is not flat is not a p-value

Under a true null, p-values are uniform. That is stronger than saying the test rejects 5% of the time, it constrains the whole distribution rather than one point of it, and it catches implementation errors that a rejection rate sails past.

Twenty points and one more, at leverage 0.74. Without the distant point the slope is 0.495; with it the slope is -0.389. Its leverage is 0.737 and its Cook's distance is 24.1, against a conventional threshold of 1.

Regression, and what the summary hides

The line that one point drew

A single observation among twenty-one reverses the sign of a fitted relationship. Its leverage is known from its x value before the outcome is looked at, so this is a property of the design rather than a surprise in the data.

What x-bar plus or minus 2 sample standard deviations holds, at n = 10. The content of the band is a random variable. Across 20,000 normal samples of 10 it averages 91.1%, its fifth percentile is 74.7%, and it falls short of 95% on 59.9% of samples. The band that is drawn to show where 95% of the data lies.

The interval that holds observations, not a mean

Two standard deviations of what

The 95.45% inside two standard deviations is a fact about a curve whose centre and width are given. Drawn from ten observations, the same band holds 91.1% on average and less than 95% on 59.9% of samples — and the average is the reading that hides it.

How often a randomised trial reports the reversal, advantage 6 points. Simple randomisation against randomisation stratified by group, 4,000 trials at each size. The simple design reverses on 3.40% of trials at its worst size and 0.50% at 1280 units; the stratified design reverses on none of them, at any size.

When the stratified answer and the pooled one disagree

The reversal a coin cannot prevent

Randomisation removes Simpson's reversal in expectation, which is not the same as removing it. A correctly randomised trial of eighty units, on a population where the treatment helps in both groups, reports it losing overall on 3.40% of trials — and stratifying the randomisation takes that to zero at every size.

What 20 analyses of one dataset are worth. The threshold giving a 5% family-wise error rate, read back as a number of independent analyses. At no correlation it is 20.05; at 0.6 it is 11.37; at 0.95 it is 2.58. Bonferroni divides by 20 throughout.

The analyses that were available and not run

How many analyses there really were

Bonferroni divides by twenty because twenty analyses were run. Twenty analyses of one dataset are worth 11.37 independent ones at a correlation of 0.6 and 2.58 at 0.95, and the threshold that controls exactly the same error rate is measurable rather than assumed.

One relationship at five designs, residual spread 1.00. Every panel has the same slope of 1, the same intercept of 0 and the same residual standard deviation of 1.00. Only the range of x differs. R-squared runs from 0.021 to 0.849, and the estimated residual spread is 0.9932 in all five.

What a summary of a scatter is a property of

R² is a property of the design

One line, one residual spread, five studies that differ only in how far apart they placed their x values. R² runs from 0.021 to 0.849 and the estimated residual spread is 0.993 in every one of them. Nothing about the relationship changed.

Which side a 95% t interval misses on, exponential source. Both tails should be 2.5%. At 8 observations the interval falls short of the mean on 9.75% of samples and overshoots on 0.31%. At 500 they are 3.31% and 2.05%, and the total is 5.36% — which a coverage table reports as very nearly right.

Shape, and what it does to a two-sample test

Where the two tails disagree

A 95% t interval on an exponential source at 120 observations covers 94.81%, which reads as very nearly right. It misses below the mean on 4.08% of samples and above on 1.11% — one tail 63% too heavy and the other 56% too light, and the total is the statistic that hides it.

The normal approximation's error on a sum of 100 exponential draws, under its Berry–Esseen bound. The distance between the exact distribution function and the normal one peaks at 0.0133, at z = -0.01. The Berry–Esseen bound is 0.1146, 8.62 times the real worst error, and larger than the whole 2.5% tail a two-sided test reads.

Past the first term of the normal approximation

A bound written for a coin

The Berry–Esseen theorem guarantees how far a standardised sum can be from the normal, and the guarantee is true. On an exponential source it is 8.62 times the real worst error at every sample size, the worst error sits at the centre rather than in a tail, and at a hundred draws the bound is larger than the 2.5% tail it would be asked to vouch for.

Coverage of the Wilson interval against the expected count, at 10, 30, 100 and 1,000 trials. Read against the expected number of successes the four sample sizes draw the same curve near the boundary. The worst coverage is 83.50% at n = 10, 83.71% at n = 30, 83.79% at n = 100, 83.81% at n = 1000, each at an expected count near 0.177, and the limiting depth is e^(−0.1765) = 83.82%.

A proportion's interval near the boundary, and the coin

A hole no sample size fills

Wilson's interval is the recommended repair for a proportion, and away from the boundary it wobbles a point or two around 95%. Near zero it has a hole: at an expected count of 0.1765 its coverage is 83.50% at ten trials, 83.79% at a hundred and 83.81% at a thousand, and it never climbs past e to the minus 0.1765, which is 83.82%. The hole is where the interval built on one success stops containing the truth, and it belongs to the count rather than to the sample size.

The power trials actually have when sized for 80% from a pilot of 10. Four thousand pilots of 10 observations, each sizing a trial for 80% power at half a standard deviation from its own standard deviation. 55.9% of the trials have less than 80% power and 11.1% less than 50%; the median trial has 76.8%.

What a sample-size calculation was given

The spread a pilot supplies

A trial sized for 80% power from a pilot's standard deviation is sized from an estimate that is too small more often than not. With a pilot of ten, 55.9% of the trials it sizes have less than 80% power and 11.1% less than 50%, although the planned sample is right on average. Sizing from the pilot's 80% upper confidence limit instead leaves 19.8% short, at 1.65 times the sample; from its 90% limit, 10.0% short at 2.12 times.

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%.

A charge that is not a straight line

A lag the sample has less of

A sample autocovariance at lag k is an average over n − k products, not n. Count a band's width in the pairs it actually has and the curvature in its charge goes away, on a correction with nothing fitted in it.

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.

A probe from what the rule blocks

A model and a count

The share of a unit's exchanges a tolerance box refuses can be modelled from the design or counted over the admissible set. They order the units the same way at a correlation of 0.81 and disagree about the level by 0.027.

Searching among fitted models

A null with a model in it

The distribution to read the winner of a table against cannot be resampled from the data, because the data does not contain the null. It has to be generated from a model — which is the assumption the resampling was chosen to avoid.

Three priors on the spread, at a true τ of 0.5. The posterior for τ under a flat prior (mean 1.66), a half-Cauchy of scale 1 (1.32) and one of scale 0.25 (1.15). The three answers differ by 30% of the widest. The prior does visible work when eight groups cannot separate a small spread from none, and almost none when they can.

The spread, and its own uncertainty

A prior on the spread

Integrating over the population spread means putting a prior on it, which sounds like the objection rather than the repair. The prior's effect is measurable, it is invisible where the groups are clearly different, and the reflex choice for a scale parameter turns out not to have a posterior at all.

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.

Two searches over different features

A search that is already the other

A break search shifts every coefficient after a row, so a step column is one of the directions it can move in. Paired with a dictionary of them it reads exactly one, on every draw, and that fixes the top of the scale.

Where the two kinds of cut sit. Six covariates, each a monotone transformation of the same latent normal. The vertical line at zero is where every median split sits, on every one of them, because a monotone map preserves order: the median of the covariate is the image of the median of the latent normal. The marks on the curves are where a threshold at 1 on the covariate's scale falls — 1.000, 0.881, 0.875, 0.783, 0.713, 0.337 — and none of them is at zero. That is the whole of the difference. A function of the sign of the latent normal is odd, and a rule made of odd functions removes exactly nothing of an interaction between two of them; a threshold anywhere else is neither odd nor even and removes something.

A guarantee that needed a symmetry

A split survives what a mean does not

The two things every trial balances come apart on a skewed covariate. A median split is a function of the sign of the latent normal whatever the marginal is; a mean is not, and its exact zero is gone at a skewness of one.

The same copula, turned over. A Clayton copula and its reflection, at the same Spearman correlation of 0.40 and the same Kendall tau of 0.275, against the covariate's marginal. With a symmetric covariate the two are the same number to nine decimals — 7.707% apiece — because the leak then depends on how much asymmetry the copula has and not on which way it points. Skew the covariate and they come apart: at a skewness of 2.26 the lower-tail copula leaves 3.431% and the upper-tail one 36.213%, a factor of 10.6. Both halves of the dependence are asymmetries and an asymmetry has a direction; a lower-tail copula concentrates the dependence where a right-skewed marginal is compressed and the two distortions partly undo each other, and an upper-tail one concentrates it where the marginal is stretched.

Both halves of the dependence at once

A symmetry that was not enough

A heavy-tailed symmetric covariate has a skewness of zero and leaks exactly nothing under three copulas. Under the two asymmetric ones it doubles the leak, from 7.707% to 14.229%.

How far each reference distribution's 95% point falls short. Seven constructions on rows that repeat each other, at a block length of 5 and 200 draws, against the statistic's own 95% point of 3.0224 computed from three thousand draws of the same world. Reading down: a multiplier on every row keeps no dependence at all and is 44% short; a multiplier shared along a block keeps the triangle; a fixed block keeps the same triangle and is 8% closer, which is the pair that says a taper is not what decides this; the stationary bootstrap; the two tapered blocks, both further short than the untapered one at this block length; and errors generated from a fitted model, which is the only construction here not bounded by what the residuals report.

A block, weighted inside itself

A taper and a critical value

Two constructions whose tapers visibly differ give the same critical value, and two that share a taper exactly do not. Adding a construction whose taper is a decision rather than an accident says which half of that is true.

The shape the covariate enters by

A threshold in the tail

How much of a threshold's imbalance a balanced covariate removes is a correlation, and the correlation is a closed form. At the median it is exactly 2/π — the same 2/π a median split throws away — and two standard deviations out it is an eighth.

The zero was a fact about independence. What a balancing rule handed every main effect of both covariates removes of a pure interaction, as the covariates are allowed to move together. At ρ = 0 it is exactly nothing — at machine precision, at any number of main effects — which is the independent-covariate result and is correct. It is not small anywhere else: the product of the two covariates loses 64.0% of itself by ρ = 0.5, because h₁h₁ = h₀ + √2·h₂ and Mehler pairs h₂ with h₂ at ρ². Four interactions are drawn and none of them keeps the zero.

When the two are not independent

A zero that was an assumption

A rule handed every main effect of both covariates removes exactly none of a pure interaction. That is true at machine precision, it is a fact about independence, and it dies as the square of the correlation.

A block length chosen from the data

An ordering that depends on the rule

The tapered block beats the rectangular one at the best available block length and at one estimated from the data. At a length written into a protocol, and at the rule of thumb, the rectangle wins — at every sample size measured.

More arms than two

Balancing towards unequal targets

A three-arm trial allocating two to one to one is the ordinary case, and a balancing rule built from raw counts does not know it. It balances the arms towards equality inside every factor level, delivers a third to each arm, and reports that it minimised imbalance.

What a longer block buys and what it costs. A trapezoidal block at 120 rows, with the error split into the two things it is made of. The bias falls with the block length, because a longer block attenuates less, and it flattens at 23.2% because the sample's own autocovariances are short whatever window is applied to them. The spread rises with it, because a longer block means fewer of them. Their sum in quadrature has a minimum at ℓ = 16, which is not where either of the two has one. The faint line is the rectangle's total error, for scale: it is above the trapezoid's from ℓ = 12 onwards.

Where a taper's case begins

Bias is not the whole of it

A window that reaches zero at its ends attenuates less and uses less of each block. The block length that minimises its bias is not the one that minimises its error, and comparing two windows at one length compares one of them mis-tuned.

How wrong the ratio is allowed to be. λ enters only through the weights, so misstating it leaves the estimate unbiased and moves two things — the interval's calibration and its efficiency — both of which are closed forms of the design. Coverage stays at its level over a factor of two in either direction (94.93% at half the truth, 94.27% at twice it) and starts to go at a factor of five. An estimate on hundreds of within-arm degrees of freedom is never wrong by anything like that, which is what makes the feasible rule usable rather than merely definable.

The weights the corner needs

Blinded, and still exact

The one number the exact interval needs is a ratio of within-arm spreads, which is a contrast and contains no mean — so a rule forbidden to look at the effect may compute it, on more degrees of freedom than the interval itself has.

Eight candidates, one of them exactly as good as the benchmark. The candidate set: moving averages of the last 1, 2, 3, 5, 8, 13, 21 and 34 observations, each drawn as its expected squared error divided by the benchmark's — the mean of all 60. The persistence is not chosen, it is solved for: at φ = 0.4895 the best candidate in the set, the average of 2, has exactly the benchmark's expected squared error, and every other candidate is worse by between 0.5% and 5.1%. So the null that no candidate beats the benchmark is true, with one candidate on its boundary. Everything a set comparison claims about its own error rate has to be measured here, because anywhere further inside the null every procedure flatters itself.

The best of a set, and what the search costs

Eight forecasters and one benchmark

A set of forecasters is a multiplicity problem on top of a dependence problem, and the two do not separate. Eight windows of one series carry the multiplicity of two and a half independent comparisons; eight separate problems carry eight.

Coverage against sample size, true proportion 0.15. Coverage does not improve monotonically. n = 19 covers 93.8% while the larger n = 20 covers 81.9%. The sample space is discrete, so the endpoints jump as n changes.

Intervals, counted

More data is not monotonically better

Coverage of an interval for a proportion does not improve smoothly as the sample grows. It oscillates, and there are larger samples that cover materially worse than smaller ones — a sample of twenty covers twelve points worse than a sample of nineteen.

The one candidate an effective sample size is right about. n/n_eff with the finite-sample inflation Σ(1 − |k|/n)ρ^|k| is not an approximation to tr(HΩ) for a fit with only an intercept — it is that trace, to machine precision, because the hat matrix of a constant column is 1/n everywhere and its trace against Ω is the mean of Ω. The quoted limit form n(1 − ρ)/(1 + ρ) is not even right about that one. And the average correction the table's fifteen candidates actually need is 3.318 per parameter, well below the scalar, so applying it to all of them over-charges every one.

Counting what is independent

One number for a table of candidates

An effective sample size is a real quantity, it is exactly right about one thing, and that thing is a mean. Substituted into Akaike's criterion it changes nothing at all, because the penalty it is meant to fix has no sample size in it.

Ten groups of 10, pooled on the log-odds scale. Each row is a group. The hollow circle is its own proportion, the filled one is the estimate after pooling, and the vertical rule is the pooled population proportion of 31.3%. One group saw no events at all, and its raw proportion of zero becomes 21.2% — an estimate the group's own data cannot produce and the population's can. The arrows are not the same length, and none of the groups differs in size.

Hierarchy past one number

Pooling a proportion

A proportion cannot be shrunk on its own scale — an estimate would leave the interval, and how much information a count carries depends on where it sits. Move to log-odds and the approximation works, at the price of a group that saw nothing having no estimate at all until the correction supplies one.

Four designs, scored on the one parameter that was wanted. Every design scored by its Ds-efficiency for K at 13 true values across a 16-fold range. The peaked curve is the subset design built at the guess K = 1: 100% there and 42.1% at the worst point of the range. The flat curve is the maximin-Ds design, never above 64.8% and never below 61.2%. Between them is the maximin design for the pair — a robust design, protecting something else, and worth 41.9% at worst here. The lowest curve is the D-optimal design at the guess, which is what an experimenter who wanted K and looked up a design for the model would actually run: 29.1% at the worst point, against 61.2% available.

What the design is asked to guarantee

Protecting one parameter over a range

A design for a non-linear model is optimal at a guess. A design for one of its parameters over a range of guesses is a worst case of a ratio of two determinants, and it is not a special case of either problem it is made of.

Every way of splitting 16 units into two halves. All 12,870 assignments, enumerated. The spread of the standardised imbalance is exactly 2/√n = 0.500, whatever the covariate's own distribution, and 33.3% of assignments differ by more than 0.5 standard deviations. Randomisation does not deliver balance; it delivers a known distribution of imbalance.

Decided before the data

Randomisation is not balance

A third of all ways to split sixteen units leave the two halves more than half a standard deviation apart on a covariate. What randomisation delivers is not balance but a known reference distribution — and it makes a test exact with no assumption about the data's shape at all.

Stationary is not the same as convergent. How far each k-swap walk is from uniform after t steps, started at the least balanced admissible assignment of 410. Every one of these chains has a symmetric proposal and rejects by standing still, so every one of them is doubly stochastic and every one preserves the uniform distribution exactly. Only five of the six get there. Exchanging all six units of each arm is a single proposal — the complement — and the admissible set is closed under complement, so the walk takes it every time and oscillates between two assignments for ever: after 160 steps it has visited 1 state and sits 0.9976 from uniform. Its stationary distribution is a fact about the matrix; its limit does not exist.

What a block may vary

Stationary is not convergent

A walk that exchanges every unit in each arm preserves the uniform distribution exactly and never gets near it. Every doubly stochastic matrix has the same stationary distribution; only some of them have a limit.

Two promises, and no rule here keeps both. A fixed-width procedure promises two things: that the interval covers at its nominal rate, and that it is no wider than the width asked for. Over 1500 runs of the modelled weighting, a rule that stops when the interval it will report is short enough keeps the width — only 2.0% of runs come out wider than 0.34 — and covers at 91.13% against a nominal 95%. A rule that stops on a width predicted from the within-arm sums of squares covers at 94.80% and comes out wider than promised on 42.3% of runs. The two promises are in conflict because keeping the second one exactly requires conditioning on the very quantity that has to be independent of the stopping time for the first.

When a fixed width is reached

Stopping on the arms

The width a trial will report is predictable from quantities the interval is not about. A rule that stops on the prediction covers at 94.5% where one that stops on the interval covers at 91.5, and it costs two blocks and half of the width promise.

Sheppard's arcsine, by two routes. Corr(sign X, sign Y) as the covariates' correlation runs from zero to one, drawn twice. One route is a sixty-four-node quadrature of the orthant probability over the correlation — the general construction, which works at any pair of cut points; the other is (2/π) arcsin ρ, which is elementary and works only at the median. They agree to 3.3e-16 at every one of 81 correlations, which is what licenses the quadrature everywhere else. The curve is above the diagonal at small ρ and below it at large: two signs agree with probability ½ + arcsin(ρ)/π, so a correlation of 0.5 gives exactly ⅓ and a correlation of 0.8 gives 0.5903.

A cut point, at a correlation

The arcsine that closes it, and the error that was overstated

Two median splits of a correlated pair agree with probability ½ + arcsin(ρ)/π, exactly. And the truncation the field was avoiding falls geometrically in the correlation, not algebraically in the order.

Two searches over one sample

The charge that is not a sum

Charging two searches what each costs on its own is conservative, and conservative here means the test never fires. At the largest break measured it declares nothing, on every draw, while a calibrated threshold reaches 29%.

A budget of 4,000, at 1 and 20 a unit. Every affordable pair, enumerated. The best is 280 cheap units and 186 expensive ones — a ratio of 1.51, against the σᵢ/√cᵢ rule's 1.49. The unit rule, which says buy in the ratio of the spreads, lands at 66:197 and costs 17% more variance for the same money. Both rules are right about their own constraint; only one of them was asked.

Splitting the units

The cost of a unit

Change the constraint from units to money and the allocation rule changes with it — from σᵢ to σᵢ/√cᵢ, which can point the other way. An arm that is noisy and expensive gets fewer units than the same arm would if the money were not the thing running out.

A search with no fixed point

The displacement is a parameter count

A nested variant is behind its benchmark out of sample before anything is searched for. The closed form for how far turns out to have nothing about nesting in it — only two integers and a window length — and it prices a table where no candidate contains any other.

How much memory a fit takes out, candidate by candidate. Under AR(1) at 0.8, the lag-one autocorrelation a candidate's residuals report, computed exactly for each candidate on 200 draws. The upper line is the law at 0.8000. A candidate that is an intercept alone reports 0.7773 — which is exactly what a sample of 120 errors reports, because an intercept annihilates the sample mean and nothing else, and the two arithmetics agree to the last bit. Every predictor after that takes more out, down to 0.7341 at the fullest candidate. That is the collision this field is about: the rule every whitening here uses estimates its nuisance once, from the fullest candidate, so that the criteria stay comparable — and the fullest candidate is the one whose residuals report the least.

Fitted together, or fitted after

The fit that takes the memory out

A candidate's residuals report less dependence than its errors do, and how much less is arithmetic rather than noise. The rule used for a good reason reads the series that has lost the most.

What a 95% forecast interval covers, counted. 1200 series of 25 observations from an AR(1) with φ = 0.7, at each horizon, on one set of seeds. The upper line is the interval computed at the true parameters — it covers 95.3% on average, which is the check that σ²Σψ² is the right formula rather than a claim about anything a forecaster can do. The lower line is the same formula fed σ̂² and φ̂: 92.8% at one step and 87.3% at 6. The interval that would cover what it claims is 6.9% wider at one step.

The observation that has not happened

The interval that forgets it estimated

The forecast band is derived for a model whose parameters are known, and then computed by putting estimates into it. Counted, the 95% interval covers 87.3% six steps ahead on twenty-five observations, and the point forecast inside it returns to the mean a third faster than the series does.

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.

The rate and the size of a disagreement

The quarrel that changes the winner

A disagreement about the tuning parameter costs 0.031 when it changes which candidate the table selects and −0.0007 when it does not. The distance between the values disagreed about has nothing to do with it.

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.

Three readings, one verdict. Every tolerance of a fourteen-unit trial, with three comparisons on each. The first is between a chain started at an assignment and a chain started at its complement, which is what a mirror split separates. The second is between two chains started at the same assignment on different streams, which nothing about the set can separate — so a large reading there says the run is too short and not that the set is in pieces. The third is the same comparison on the statistic's absolute value, which is symmetric under the complement and therefore blind to the split by construction. The verdict is the pattern rather than any one line: the split is called only where the first fires and the other two do not, which happens at exactly the tolerances the enumeration calls disconnected — 0.8, 0.75, 0.7.

What a chain cannot report

The statistic that changes sign

A test for an unreachable half needs a quantity that tells one half from the other. Every symmetric reading of a mirror pair is identical, and a magnitude is the natural thing to reach for.

The mean's zero is the copula's symmetry. Five copulas, each at a Spearman rank correlation of 0.4, with a normal covariate throughout — so nothing here is about the marginal, which is the whole of the earlier field. Horizontally: how far the copula's density is from its own reflection through the centre of the unit square, measured rather than read off the family's name. Vertically: what a rule balancing the mean of each covariate removes of their product. The three copulas at zero on the horizontal axis remove exactly nothing, to thirty decimal places. The two that are not symmetric remove 7.71%. A guarantee that held for six marginals turns out to have needed something the marginals could not have told anybody about.

The other half of the dependence

The symmetry the marginals could not show

A mean's interaction zero needs the covariate to be symmetric and the copula to be symmetric under reflection. Six marginals could only ever test one of those, and the other is broken by the commonest kind of dependence there is.

The reference distribution the design supplies

The test that needs the rule

A randomisation test assumes almost nothing about the data and one thing about the experiment. Tell it a fair coin produced an allocation that an adaptive rule produced — which is what every off-the-shelf permutation routine does — and it rejects 8.0% of true nulls where knowing the rule gives 4.0%.

Where the residual test's statistic actually falls, at n = 200. Four thousand pairs of unrelated random walks, each regressed on the other and each residual tested for a unit root. The statistic is computed as a t and its distribution is not a t: five per cent of it falls below -3.38, where the ordinary one-sided 5% point of a t on 198 degrees of freedom is -1.65. Everything left of -1.65 — 70.2% of the whole distribution — is a pair of unrelated walks that a t table calls cointegrated.

Series that move together

The test with no table

The statistic that separates a real long-run relation from a spurious one is computed as a t and is not a t. At two hundred observations its 5% point is −3.38 where the t table says −1.65, and reading it against the table calls two unrelated random walks cointegrated 70.5% of the time.

The variance touches p and never crosses it. d(x) = f(x)′M⁻¹f(x) along the diagonal of a square region, for the D-optimal measure. The line at 6 is the number of parameters in the model. Kiefer and Wolfowitz's theorem says a design is D-optimal exactly when the largest d anywhere in the region is p — not approximately, equals — so the optimal curve is tangent to that line at its support points and below it everywhere else. Here the largest value anywhere on a 41×41 grid is 6.000000000.

A design chosen rather than looked up

The theorem that says when to stop

A search that maximises the volume of the information has no way of knowing it has finished, because nothing tells it what the maximum is. Kiefer and Wolfowitz's equality does — a design is D-optimal exactly when the worst prediction anywhere in the region equals the number of parameters, which is 6.000000000059 here, gated at machine precision.

The term that cancels, and the term that does not. The volume each candidate's whitening moves — log|Ω̂| — for a sieve of order 4 on one sample of 120 rows. Estimated once from the fullest candidate and used for the whole table, it is the same number for every candidate, so it drops out of every difference the criterion reads: that is why nothing in this collection has ever needed to carry it. Estimated from each candidate's own residuals it ranges over 23.87, which is more than a parameter is worth, and the criteria being compared are then fits made under different error models with no term saying so. The window's rule has carried this term since the estimated-covariance field and the sieve's never had it.

How long the list is

The volume a whitening moves

A sieve's whitening has a determinant and this collection's criterion for it never carried one. Shared across a table the term cancels exactly, which is why nothing ever noticed; used per candidate it is worth more than a parameter and the whole comparison turns on it.

The weight on the population, σ = 3. Each curve is one population spread τ. A group's estimate moves B = se²/(se² + τ²) of the way to the population mean, where se = σ/√n is what the group's own mean does not know. At τ = 1 a group of 9 observations sits halfway.

Groups that borrow

The weight that decides

B = se²/(se² + τ²) is not a compromise between two answers. It is exactly the posterior mean's weight, it agrees with a numerical integration to ten digits, and an argument that mentions no population at all arrives at almost the same estimator.

A window with two wrong ends. The regret of a rule whitened by a Bartlett-tapered Ω̂, as the window widens, against three rules that need no window at all. At L = 0 the estimate is the identity and the rule is exactly least squares — 0.08556, the same number to five places. It falls to 0.01754 at L = 20 and rises again by L = 30, because a quarter of the sample's lags are then being estimated from it. The automatic bandwidth a practitioner would reach for, 4(n/100) to the power 2/9, which at this sample size is 4, gives 0.02963 — 69% above the best available window. The rule told the dependence is an AR(1) sits at 0.01440 throughout, which is the price of not knowing the form.

Estimating the dependence, not naming it

The window that has to be chosen, and the term that was dropped

An estimated covariance has a bandwidth in it, and both ends of the dial are wrong for different reasons. The rule a practitioner would reach for is two thirds worse than the best window there is.

Four designs, and what each of them guarantees. The worst Ds-efficiency each design achieves anywhere in a rectangle of parameter values 4 times wide in each coordinate. The design built at the guess guarantees 7.3%: it is perfect where it was built and nearly useless at one corner. The D-optimal design at the same guess guarantees 25.6% — it answers the wrong question everywhere and is therefore not concentrated on being right anywhere. The third is the one this field exists to measure: maximin over the first parameter's whole range, with the second held at its guess. It guarantees 7.0%, which is no better than the design that protects nothing. Protecting both is worth 45.9%, and it needs 3 settings to do it.

What the procedure may not read

The worst case in two directions

A design that protects a range of one parameter is robust. Protect the range of one parameter while holding the other at a guess and the design is still robust, still has a guarantee, and guarantees no more than a design that protects nothing at all.

No block size is best at both things the procedure claims. Two claims and one dial. The honest interval's half-width falls as the blocks get smaller, because the interval's degrees of freedom are the number of blocks: 0.2602 at blocks of two against 0.2933 at blocks of sixteen. The fixed-width claim — that the mean is within 0.25 of the truth — gets more reliable as they get larger, because the sample size is less variable: 92.40% against 95.00%. Both are computed from the same runs, and the second is reproduced to within a tenth of a point by E[2Φ(d√N/σ) − 1], which needs the sample-size distribution and nothing else. The schedules sit at the bottom left: as narrow as the smallest fixed block and as few observations, with the rule's spread estimate on half as many degrees of freedom again.

The block size as a schedule

Two degrees of freedom, one total

The block size is a dial, and the two things a fixed-width procedure claims move in opposite directions along it. Divide the width by the square root of the sample size and one of them turns out to depend on the number of blocks and on nothing else.

Twenty tests, 10 of them real — what each procedure holds. no correction: familywise 40.8%, false discovery 5.3%, power 85%. Bonferroni: familywise 2.8%, false discovery 0.5%, power 49%. Holm: familywise 3.6%, false discovery 0.6%, power 53%. Benjamini–Hochberg: familywise 20.0%, false discovery 2.6%, power 75%.

Corrections, and what each controls

Two different promises

Bonferroni bounds the chance of any false positive. Benjamini–Hochberg bounds the share of the findings that are false. Both are called correcting for multiple comparisons, and one of them lets the familywise rate reach 20%.

What decides whether a tuning list decides

Two factors pointing opposite ways

As the candidates on a table are pulled apart, they quarrel about the tuning parameter three times as often and the quarrel decides the winner thirty times less often. A sweep that reads the first factor has read the one pointing the wrong way.

Coverage of four nominal 95% intervals, n = 30. Computed exactly by summing over all 31 possible counts, not simulated. The Wald interval drops to 26.0% and is jagged everywhere; Clopper–Pearson never falls below 95% and pays for it in width.

What makes it checkable

Two routes to every number

A site about probability that only simulates has one route to each answer and no way to tell a right one from a plausible one. Every important number here is computed twice, by arithmetic that shares nothing, and the two are required to agree.

Two independent random walks, 100 steps. Nothing connects these two series: each is generated from its own independent draws. Regressing one on the other gives a slope with t = -10.9, R² = 0.55 and p = 0.0e+0 — a result that would be reported as a finding by any standard output.

When the observations repeat each other

Two walks and a finding

Regress one random walk on another, independently generated, and the slope is significant 76.7% of the time with a median R² of 0.17. Nothing connects the two series, nothing in the output says so, and more data makes it worse.

The prior, doing visible work

What a credible interval covers

A credible interval makes the statement everyone wants and does not claim to have a coverage. It has one anyway, it can be summed over the sample space exactly, and on a reasonable prior it beats the interval taught first.

Power at an effect of 0.5 standard deviations. The curve is the non-central t on 2n − 2 degrees of freedom with δ = d√(n/2); the dots are 4,000 experiments run at each size. Reaching 80% power needs 64 per arm.

Tests, and the second number

What a p-value does not say

The same p of 0.04 corresponds to a large effect in ten observations and a negligible one in two thousand. A p-value alone cannot be interpreted, and the number that makes it interpretable is almost never printed beside it.

Paying for a search

What a search costs in parameters

An information criterion's penalty is an estimate of the optimism a fit carries. For a break point the optimism can be measured and cannot be counted, and it comes to about two and a half parameters.

Four windows, one line, and one that is off it. The optimism measured for each window at a band of 30 lags, against what that window's weights sum to, on 2000 pairs of independent samples of 120 rows. The diagonal is where a window that spent exactly its summed weights would sit. Three of the points are one shape at three levels — the Bartlett window, its square and its cube, whose sums stand in the ratio 6 : 4 : 3 — and they lie on a line through the origin at 0.767 of the diagonal, with 0.033 between the highest and the lowest. Scaling the weights scales the charge by the factor the weights predict, which is what makes the weights the mechanism. The Parzen window has a comparable sum and a different shape, and it sits at 0.871: its weights stay near one over the first few lags, and the first few lags are where the information is. A weight sum treats every lag as equally informative and no sample does.

A charge for a covariance's own dimension

What a window leaves free

A Bartlett window's weights sum to exactly half its width, which is a candidate for what the band costs. Varying the weights without varying anything else says the weights are the mechanism; varying the shape at the same weight says they are not the arithmetic.

Overlap and complementarity, separated

What a zero is made of

Two disjoint dictionaries of independent columns read an excess of 0.000116 and are made of an overlap of 0.000583 and an interaction of 0.000467. The control the whole scale is anchored on reads zero because two effects cancel.

The interval, studentised

What studentising costs

Averaged over eight cells the studentised interval is 2.09 times as wide as the percentile one and covers 0.46 points better. At the block lengths the rules choose, the scale it divides by rests on two or three numbers.

What a dictionary buys and what it costs

What the extra function buys

A rule balancing the mean of each covariate has a worst case of exactly zero. Adding the median split — the other thing every trial balances — leaves it at exactly zero, and one square moves it.

A test between nested models, under a null that is true. 1000 comparisons: an AR(1) truth, forecast by a fitted AR(1) and by a fitted AR4 whose extra coefficients are zero. In population the two forecasts are identical, so every rejection is false. The larger model's mean squared error is 1.1663 against 1.0583 — worse, by exactly the noise in estimating coefficients that are not there — and the ordinary test therefore declares the smaller model significantly better 67.2% of the time. Read one-sided in the direction anybody asks about, it finds the larger model better 0.0% of the time. Adding the squared difference between the two forecasts back into the loss differential puts the level at 4.9%.

Comparing two forecasters

When one model contains the other

The comparison a forecaster most often wants is between a model and the same model with one more term. That is exactly the comparison the standard test cannot make — and it fails by declaring the smaller model significantly better, more confidently the more data it is given.

One curve is a binomial coefficient and the other is a line. The number of subsets a maximin over this dictionary would have to score, against the number the exchange algorithm actually scores. At three functions the walk is 2,024 subsets and is the honest answer; at eight it is 735,471 and the exchange algorithm has looked at 421. The warrant for the second curve is the four sizes where both exist and agree, which is a weak warrant — it says the algorithm has not yet been wrong, not that it cannot be — and it is the only one available past the point the first curve leaves the page.

When the set is too large to walk

Where the enumeration stops

A maximin over an eight-function dictionary is a walk over seventy subsets. Over twenty-four it is 735,471 at eight functions, and the exchange algorithm that replaces the walk scores 421. What licenses the second curve is four sizes where both exist and agree, which is a weaker warrant than it looks.

Generality in the wrong direction buys nothing. Regret on a sample whose persistence changes from 0.95 to 0.65 at row 60, over 200 draws. The three stationary rules — told one number, told a window, told an order — are within 0.4 standard errors of each other, and all three stop in the same place: they are general in the lag direction, and the departure is in the other one. Letting the model change once, at a point estimated from the same residuals, is worth 0.05021 more at 4.5 paired standard errors — about as much again as the whole of the first repair. Being told where the break is adds 0.01926, and being told the entire covariance adds 0.02465.

The shape a dependence has

Where the generality runs out

A covariance that changes half way through a sample is not one a window can estimate. One number, a window and an order are worth the same as each other on it — and letting the model change once, at a point nobody can locate, is worth as much again as all three.

A design that assumes less

Where the minimum is attained

A design that protects a range is finished when its worst case is a tie. That is a checkable property rather than a description, it is why the search cannot climb a derivative, and it is the same corner the criteria field found at the end of the Φₚ family.

The crossing is in the dependence, not in the split. Regret of each rule as the design and the errors are made persistent at the same coefficient, scored on fresh rows because the closed form assumes exactly what is being taken away. An optimism theorem counts rows; when the rows repeat each other there are fewer of them than there are rows, the penalty is too small for the fit it is correcting, and the criterion starts buying coefficients it should not — its average winner grows from 3.31 coefficients to 3.90. The hold-out never used the theorem and overtakes at ρ ≈ 0.81. Schwarz's criterion, worst of the three on independent rows, is best on repeating ones — its heavier penalty is right for the wrong reason.

Scoring a search without spending data

Where the two searches cross

The obvious dial between a criterion and a hold-out is how much of the sample to hold out, and moving it never changes the answer. The dial that does is one nobody chooses — how much each row repeats the one before it — and the two rules change places at about 0.81.

The guarantee, as the basis is allowed more functions. The lower line is the best worst case over the six named shapes for a basis of each size, found by scoring every subset of the dictionary — an exact answer, since the problem is finite. One function guarantees 2.3%, which is nearly nothing; three guarantee 59.0% and the basis that does it is the covariate, its square and its cube, with no indicator in it. The upper line is the same problem with the basis drawn rather than fixed, which is worth 2.09 times as much at two functions and 1.32 at three. The two lines converge because a basis large enough to protect everything has nothing left to randomise over.

Choosing what the rule reads

Which shapes are worth protecting

Choosing a basis by its worst case is a finite problem with an exact answer. The answer has no tie in it, which a maximin optimum is supposed to have — and the tie comes back, along with twice the guarantee, when the basis is drawn rather than chosen.

A promise about two arms

Which weights are the inverse variances

There is an exact estimator when the two arms share a variance and another when every block has the same two counts, and between them they cover every trial anybody designs on purpose. In the corner where neither holds, both cover 98.45% instead of 95%, and the only estimator at its level is the one with no theorem behind it.

One tail arrives; the other is still on its way at a million. The Kolmogorov distance between the exact law of a normalised maximum and its Gumbel limit, at six block sizes, for two parents that both have that same limit. Both are closed form: the exact law of a maximum is F(x)^n and no simulation is involved. The exponential parent's distance falls from 0.0280 to 2.707e-7 — a factor of a hundred thousand, which is exactly one over n. The normal parent's falls from 0.0522 only to 0.0091, a factor of 5.74, because its rate is one over log n. At a million readings a block the two differ by a factor of 33556.3.

The tail past the last observation

The maximum converges slowly

The rate at which a normalised maximum reaches its limit law is computable rather than simulable, because the exact law of a maximum is always available. For a normal parent the distance falls like one over the logarithm of the block and is still 0.0091 at a million readings; for an exponential parent, with the same limit, it is 2.707×10⁻⁷.

Unrepresentative in every respect but the one that matters. Three properties of the complete cases as the chance of being observed leans harder on the regressor, in closed form, at 35.0% of outcomes missing throughout. The mean of the regressor among the rows kept climbs from 0.0000 to 0.5528 against a population mean of zero, and the mean of the outcome from 0.0000 to 0.3980 above its own. The bias in the fitted slope is exactly zero at every one of the ten settings, because selection acting on the regressor alone leaves the conditional law of the outcome given the regressor untouched and least squares conditions on exactly that. The sample is wrong about almost everything and right about the one quantity being estimated.

The value that is not there

Dropping the incomplete rows

Push the missingness until the rows that survive have a covariate mean of 0.543905 against a population zero and a variance of 0.5041 against one, and the fitted slope is still exactly right. Where the rule reads the outcome instead, the same sweep takes coverage to 2.42% at eight hundred rows.

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.

Coverage without a distribution

What the split costs

Splitting a sample between fitting and calibrating looks like a trade against the guarantee, and it is not: coverage moves 0.63 points across nine splits and every reading sits on its own promise. The whole cost is 1.38% of width — and at sixty observations the width falls, rises and falls again.

A standard error for a model that is wrong

The bread and the filling

The robust standard error is not a safety margin. At one setting of the error variance it is 1.2806 times the model-based one and at another it is 0.8246 times it, and the sign of a single dial decides which.

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

Kaplan–Meier from 120 subjects, 59 of them censored. The step curve is the estimate, the smooth curve is the truth it is trying to recover. 59 of 120 subjects were still event-free when observation stopped; they are not dropped, and they are not counted as events — they leave the risk set at the time they were last seen.

When the data stops early

The curve that survives censoring

Kaplan–Meier recovers the true survival curve to within a fraction of a point at every censoring level from 37% to 71%, where dropping the censored subjects is off by 28 and then by 43. The estimator is a running product and the reason it works is in its denominator.

Three bands called 95%, at n = 20. Half-widths in sample standard deviations: 0.468 for the mean, 2.14 for one future observation, 2.75 to hold 95% of the population. The first two differ by exactly the square root of n + 1, which is 4.58 here.

The interval that holds observations, not a mean

A tenth as wide, and both of them right

The interval for a mean and the interval for one future observation are both labelled 95%, and at a hundred observations one is 10.05 times the other — exactly the square root of n + 1. Read the narrow one as the wide one and it covers a new value 15.7% of the time.

Naming the analysis in advance, against correcting for all 20 of them. The prespecified analysis detects an effect that is in it 52% of the time at two standard errors and an effect elsewhere 5% of the time. The corrected slate detects it 23% of the time wherever it is. The two are worth the same when the chance of having named the right analysis is 38% — and that figure rises to 91% at four standard errors.

The analyses that were available and not run

What naming it in advance costs

Preregistration is argued for as free. Against an effect of two standard errors hiding in one of twenty analyses, naming the right one detects it 51.5% of the time and naming the wrong one detects it 4.7% of the time; correcting all twenty detects it 22.5% wherever it is. The two are worth the same when the chance of having named correctly is 38%.

The pooled two-sample test's size, with a true null everywhere. Forty units split between two groups, with the second group's variance a stated multiple of the first's, and the two population means equal. A 5% test should reject 5% of the time. The pooled test runs from 0.55% to 18.91% across this region; Welch's runs from 4.63% to 5.51%.

Shape, and what it does to a two-sample test

A degrees of freedom that is not a count

The pooled two-sample test's size runs from 0.55% to 18.91% across forty units split five ways against five variance ratios, with a true null in every cell. Welch's runs from 4.63% to 5.51% — bought with a degrees of freedom that is a function of the data, not an integer, and not a count of anything.

The operating characteristic, and the point that minimises harm at 0.10% prevalence. The published pair — 90% sensitive, 95% specific — is the open mark. With a miss costing 100 times a false alarm and a prevalence of 0.10%, the threshold that minimises expected cost sits at 74.7% sensitivity and 98.81% specificity, with a predictive value of 5.9%.

Two tests, a threshold, and the rate they are read against

The test is a point somebody chose

A test reported as 90% sensitive and 95% specific is not two properties of a test. It is one property read at a threshold, and the threshold that minimises harm runs from 3.05 standard deviations of the score at a prevalence of one in ten thousand to −0.12 at one in two — 45% of cases detected at one end and 99.9% at the other.

What the plot says, and what the interval does, at n = 40. For each source: how often a quantile plot of the data leaves its pointwise band, and how often the 95% t interval for the mean misses. The two-lump source leaves the band on 100% of samples and its interval covers 94.80%; the t on three degrees of freedom leaves it on 57% and covers 95.73%, the best of the five.

What a diagnostic plot is showing

The plot is about the wrong quantity

A t interval needs the sampling distribution of the mean to be normal, not the data. A two-lump source leaves its quantile band on 100% of samples of forty and its interval covers 94.80%; a t on three degrees of freedom leaves it on 57% and covers 95.73%, the best of five sources.

Worst and average coverage of six 95% intervals for a proportion, 30 trials. The worst coverage over every proportion beside the average over a uniform one, with the average expected width. Clopper–Pearson: worst 95.05%, average 97.34%, width 0.299. Blaker: worst 95.00%, average 96.31%, width 0.283. Wilson: worst 83.71%, average 95.24%, width 0.271.

A proportion's interval near the boundary, and the coin

What a guaranteed minimum costs

Clopper–Pearson's interval never covers less than 95%, and at thirty trials it averages 97.34% and is 10.4% wider than Wilson's. Blaker's interval keeps the same guarantee, averages 96.31% and is 4.6% wider. The difference is not waste: Clopper–Pearson guarantees each side separately, holding both below 2.5%, and Blaker guarantees only their sum — so at ten trials and a proportion of 0.15 it misses on one side 5.00% of the time.

Two 95% intervals 2.772 standard errors of the difference apart, standard errors in the ratio 1. The intervals are separated, and the test of the difference gives p = 0.0056. Two 95% intervals with equal standard errors just touch at p = 0.0056.

An interval read beside something else

Two intervals that overlap

Two 95% intervals that just touch are read as a difference at the edge of significance. With equal standard errors their difference has p = 0.0056, not 0.05; two intervals can overlap by 58.6% of an arm and still differ at exactly 5%; standard-error bars that just touch mark p = 0.157; and when the two estimates are correlated at 0.8, touching intervals conceal a difference of 6.2 standard errors. Read as a test, non-overlap needs 1.66 times the sample for the same power.

How the truth, the raw means, the posterior means and the constrained estimates spread, standard error 1. Beyond two population widths above the centre lie 2.28% of the true values, 7.86% of the raw means, 0.234% of the posterior means, and 2.28% of the constrained estimates.

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

Estimates that are too alike

Posterior means give each group its least-error estimate, and as a set they are too alike: with each group's standard error equal to the population's spread, they spread 0.707 as widely as the truth. Beyond two population widths lie 2.28% of the true effects, 7.86% of the groups' own means, and 0.234% of the posterior means — a tenth of the truth. Rescaling the estimates to the right spread counts the tail exactly and costs 17% more squared error; summing each group's posterior chance of being beyond the line counts it without changing any estimate.

A near-perfect cancellation, at one correlation. A covariate skewed at 0.75 under a lower-tail copula, at each of 7 rank correlations. The earlier field measures this cell at a Spearman of 0.4 and reads 0.002% where adding the two halves' own leaks gives 16.579% — a cancellation so near exact that it is that field's headline. Across the sweep the same cell reads 0.0084%, 0.0182%, 0.0097%, 0.0015%, 0.0864%, 0.4693%, 1.5327%. Its smallest value is at 0.4, in the interior, and by 0.7 it is 1007.40 times larger. The near-zero is where two curves cross, and they cross beside the one correlation that was measured.

The same table at seven correlations

The zero that was a crossing

A cell that leaks 0.002% where adding its two halves gives 16.6% is a field's headline. On a finer grid it passes through zero at a rank correlation of 0.38 — two hundredths from where it was measured.

Two searches over one sample

A charge that depends on the rule

The break search's charge is 34.7 on its own and 15.4 once a window has been chosen from the same sample. Most of what a break search finds under correlated errors is the correlation, and a whitening has taken it already.

Three copulas that break nothing, and a factor of two between them. The three radially symmetric copulas, at a matched Spearman correlation of 0.40, against the covariate's marginal. All three leave exactly nothing with a symmetric covariate — that is the guarantee, and it holds to twenty decimal places. What they do to a skewed covariate is not the same at all: at a skewness of 2.26 a Frank copula leaves 12.118% where a Gaussian leaves 21.539% and a t on four degrees of freedom leaves 23.640%. A factor of 2.0 between two copulas that are both symmetric, both matched on rank correlation, and both harmless on their own. So the copula matters to the marginal's leak without breaking any symmetry of its own, which is a milder version of the same finding and applies to every trial rather than to the asymmetric ones.

Both halves of the dependence at once

A copula that halves a marginal

Three copulas break nothing on their own and put a factor of two between the same skewed covariate's leaks — 12.118% under a Frank against 23.640% under a t, at the same rank correlation.

When the set is too large to walk

A count that has to be estimated

At sixteen units the admissible assignments can be counted by walking all 12,870 of them. At four hundred there are about 2^393.70, and the share admitted is 0.31885 against a closed form of 0.31818 that has no trial size in it at all. The exhaustion a small trial runs into is a fact about small trials.

What a chain cannot report

A defect that is about size

The admitted share of a rerandomisation barely moves with the number of units. The number of admissible neighbours grows like the square of it, and that is what decides whether the walk can go everywhere.

A line in the right width beats two curves. How far each candidate charge sits from the measured optimism across the plateau, in units of each width's own standard error, over 2000 draws. The straight line through the origin in the band's summed weights — which is what the earlier field levies — misses by 0.2382 per width. The same straight line in the pairs the band actually uses, Σ w(k)(1 − k/n), misses by 0.0095. A fitted power law misses by 0.0293 and a fitted decaying rate by 0.0172, both on one fitted constant more. The deferral this field answers asked for a curve; the answer is a line, in a variable with nothing fitted in it.

A charge that is not a straight line

A line that beats two curves

A deferral asked for a curve. Fitted against the same measurements, a straight line in a variable nobody had to fit describes the plateau better than either curve does with a constant more — and for three windows out of four it does not.

What a longer list actually changes. How often the fifteen candidates choose different tuning parameters, at a true null where every one of them contains the truth, so a disagreement is manufactured rather than discovered. The order's list is an interval of integers, and thinning it moves the rate smoothly from 0% at two values to 39% at thirteen. The window's is not an interval — it runs 0, 1, 2, 4, 8, 12, 20, 30 — so a thinned window list jumps depending on whether it happens to keep the width the criterion wants, between 0% and 42% with no order to it. So "the same length" was never quite the same thing for the two rules, and it is a smaller effect than the field it was invoked to explain.

How long the list is

A list is not a rule

How often fifteen candidates disagree about a tuning parameter runs from nothing at two values on the list to two draws in five at thirteen. What the disagreement costs does not move at all.

What each probe can see. How far apart the two components of the admissible set are on each probe, over the spread inside a component, on 100 designs whose set is enumerated and split. It is the population quantity a chain is trying to report. The separating direction itself reads 10.5646; the projected fourth power 5.0800, the design's own leverage 3.8362, the modelled active set 1.9529, the counted active set 2.0170 and a random direction in the same subspace 0.9422. The two active-set probes beat the random direction and lose to both of the earlier field's, which is the field's answer to the question that opened it.

A probe from what the rule blocks

A quantity that loses to a heuristic

Leverage is a heuristic about which units a balancing rule has most to say about. The constraint's active set is the thing the rule actually does. As a probe, the heuristic wins by 4.4 paired standard errors.

Flat along a row, apart between them. The probability that a per-candidate tuning list changes the winner, at three list lengths on three candidate tables, over 800 draws in each of the nine cells. Along a row — the reading the earlier field takes — it moves by a factor of at most 1.21, so that field's invariant survives on every table. Down a column it moves by up to 1.98. The list length is the dial that does not move this number and the table is one that does, and the earlier field varied only the first.

What decides whether a tuning list decides

A table and a list

A nested ladder of candidates differing by one coefficient was predicted to turn over more often at every list length. It turns over less at every one, and its list changes the winner half as often.

Cut the charge and the width follows it. The band width each charge picks, averaged over 400 draws of 120 rows under AR(1) at 0.8, with the standard deviation across draws beside it. Schwarz's charge — half a log n a lag, which is 2.39 here — picks 3.67. Akaike's picks 6.02. Charging the numbers the window actually leaves free, which is half the width, picks 10.12; charging what the optimism measures, 0.767 of that, picks 14.15. A charge and the width it buys are very nearly reciprocal, which is what a likelihood rising at a fixed rate a lag implies and is why the four answers span a factor of 3.86. The width that was actually best on the draw averages 13.90 and moves by 10.30 from draw to draw — three times as much as any rule's answer does.

A charge for a covariance's own dimension

A width that moves and an error that does not

Four charges give four widths a factor of four apart and four errors half a per cent apart. The derived charge wins, significantly, by a quarter of what was on offer — and none of the four is an estimate of anything.

Four cells change their answer. The four cells of the twenty whose excess changes sign as the dependence strengthens, over 7 recalibrations. Above the line the two failures compound — the cell leaks more than adding the copula's own leak and the marginal's — and below it they cancel. All four start above and end below, and all four are at the two most skewed covariates: skew 0.90 under heavy-tailed, skew 0.95 under heavy-tailed, skew 0.90 under upper tail, skew 0.95 under upper tail. Whether two failures of a dependence compound or cancel is therefore not a property of the pair. It is a property of the pair at a strength of dependence, and a fifth of the table changes its answer inside the range measured here.

The same table at seven correlations

An answer that changes

Eleven of twenty cells cancel and nine compound, at one rank correlation. Sweep the correlation and four of the twenty change sides — all four from compounding to cancelling, all four at the most skewed covariates.

16 groups shrunk towards a fitted line, at γ = 1.2. Hollow circles are the groups' own values, filled ones the estimates after pooling, and the diagonal is the line fitted through them with each group weighted by how well it is measured — slope 1.21, intercept 0.20. The horizontal rule is where the same 16 groups would have been shrunk to with no covariate. The spread left to borrow against is 0.64 with the covariate against 1.28 without, so every group is pulled further in than it would otherwise have been.

Hierarchy past one number

Borrowing towards a line

A group shrunk towards the average of all groups is being compared with groups it has nothing in common with. Fit a group-level predictor and it is shrunk towards what the predictor says a group like it should be — which halves the spread left to borrow against and takes a quarter off the squared error.

What each criterion selects, at 50 observations. 700 series from an AR(2) with coefficients 0.6 and -0.3, every order from 0 to 8 fitted to the same 42 responses so the log-likelihoods are comparable. AIC finds the true order 55.1% of the time and lands above it 25.7%; BIC finds it 54.1% and lands above it 4.0%. The closed form for one extra lag is P(χ²₁ > 2) = 15.73% for AIC, which does not depend on n at all, and P(χ²₁ > ln n) = 4.79% for BIC at this size, which falls to zero. Under the true order is the other failure and it is BIC's: 41.9% against 19.1%.

The observation that has not happened

Choosing the order

One criterion is consistent and one is not, which is the whole of what gets said about them. At two hundred observations the consistent one is right 95% of the time and the other 70%; at fifty they are both right 54% of the time and wrong in opposite directions, and consistency has not started to mean anything yet.

Paying for a search

Choosing whether to break

Charging what the search manufactures takes a rule from splitting a stationary sample on 99% of draws to 16%. It also costs regret, because the two mistakes a rule can make are not the same size.

Least squares estimates persistence low, by an amount with a formula. 3000 series of 50 observations at each persistence. The lower curve is the counted bias of the least-squares estimate of φ, and the open marks on it are −(1 + 3φ)/n, computed rather than fitted. The upper curve is the bias left after adding that quantity back, evaluated at the estimate rather than at the truth nobody has: -0.0020 at φ = 0.3, -0.0023 at φ = 0.5, -0.0039 at φ = 0.7, -0.0059 at φ = 0.8, -0.0108 at φ = 0.9, -0.0165 at φ = 0.95. The formula is a leading-order expression and it understates the bias where the persistence is nearest one — -0.0882 counted against -0.0770 predicted at φ = 0.95, which is the corner of the parameter space every one of these approximations is worst in.

Comparing two forecasters

Correcting the persistence

Least squares estimates how much a series remembers of itself as smaller than it is, at every value it can take, by an amount with a closed form. Subtracting that amount back is one line of arithmetic, and what the line costs is variance.

The trace statistic under the null, and the 5% point it needs. 600 systems of 3 unrelated random walks, each put through the reduced-rank regression, with the statistic for "rank ≤ 0" collected. The 5% point is 31.91. There is no standard table to look that up in: the distribution depends on the number of common trends under the null and is not a chi-square, so the value is simulated on one set of seeds and applied on another — exactly the position the pair's residual test was in one field ago.

Three series, and a count

Counting what is still wandering

The statistic that turns a spectrum into an integer has one name and three distributions. Its 5% point is 8.12, 18.64 or 31.74 depending only on how many series are left wandering under the null being tested — and read against the wrong one of those three, it calls unrelated random walks cointegrated most of the time.

The one thing a trial always reports is the one thing that survives. How wrong three p-values are when they are computed over the half of the admissible set a single walk can reach, rather than over all of it, at a fourteen-unit trial where the whole set can be enumerated. The two-sided p-value on the difference in arm means — the number a trial publishes — is wrong by exactly nothing, at every row, to machine precision. That is not luck: the two components are complement pairs and the difference in arm means is exactly negated by the complement, so the distribution of its absolute value is the same on both. A one-sided p-value on the same statistic is out by as much as 0.112, and the largest response observed in the treated arm — a safety reading rather than an effect, and the one statistic here that is not odd under the complement — by as much as 0.172. The defect survived because the commonest thing anybody computes is the one quantity it cannot touch.

The diagnostic after the trial

Half a reference distribution

A walk that reaches half its admissible set reports the two-sided p-value exactly right, to the last digit, for ever. A one-sided one it puts on the wrong side of five per cent about once in thirty.

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.

One likelihood, three answers. The concentrated Gaussian log-likelihood of one sample of 120 rows under AR(1) at 0.8, as a function of the correlation the errors are whitened at. Three rules put three different numbers on this curve. The two-step rule reads the least-squares residuals and lands at 0.7616, giving up 0.304 of log-likelihood. Iterating moves it to 0.8080 and gives up 0.002. The maximum is at 0.8044. The curve is not flat between them: what a fixed point of the residual update finds is a solution of a different equation, and the difference is the Jacobian term ½log(1 − ρ²), which grows as the correlation does.

Fitted together, or fitted after

Iterating is not maximising

Re-reading a correlation from the generalised residuals and refitting converges in seven steps. What it converges to solves the first-order condition of a sum of squares, and the likelihood has one term more than that.

What each instrument costs to read. The number of draws each instrument needs to separate a rectangular block from a trapezoidal one at two standard errors, at a block length of 20 and 120 rows — measured from each instrument's own spread on the same draws. The implied variance needs 7.0 and the 95% point needs 20.2, a factor of 2.90 at this block length. There is a closed form beside it and it does not depend on either the scale or the size of the gap: the standard error of a p-quantile is √(p(1−p))/f(q) over √B where a standard deviation's is σ/√(2B), which at the 95% point of a nearly normal reference distribution is 3.30 times as many draws for the same statement. And the quantile route needs every one of those draws resampled, where the variance route needs none.

Where a taper's case begins

Measuring a variance rather than a quantile

A resample's implied long-run variance can be computed from the sample with no resampling in it at all. A critical value cannot, and the difference is a factor of three in the draws before any of the resampling is counted.

A wider band is always a better fit. The likelihood maximised over the band, at five widths, averaged over 30 samples. A band at L lags is a band at L + 1 with the last entry held at zero, so the families are nested and the maximised likelihood cannot fall — it does not, on any draw. What it does is rise at 0.984 of log-likelihood a lag. A parameter that is doing nothing buys half a unit in expectation and Akaike's criterion charges one, so this is a criterion very nearly indifferent between every width on offer. The dashed line is what a charge of one unit a lag would exactly cancel. Nothing in the fit chooses a width, and what does choose one is a charge somebody has to pick.

A covariance with no parameter

Nothing in the fit picks the width

A wider band is always a better fit, and it is better by about one unit of log-likelihood a lag — which is the order of what a criterion charges for a parameter. Three defensible rules choose widths a factor of three apart.

3 arms against one control, 360 units in all. Every control size, enumerated. The best is 132 on the control and 76 on each arm — a ratio of 1.74, against √3 = 1.73. Splitting the units evenly over all 4 groups costs 7.2%, which is small; what the larger control also does is lower the correlation between the comparisons, from 0.50 to 0.37, and that changes which multiplicity correction is right.

Splitting the units

One control, many arms

The control appears in every comparison, so it is worth √k treatment arms — and the same sharing makes the k tests correlated at n/(n+n₀), which is the quantity Bonferroni ignores. Both facts come out of one design decision, and it is the size of the control.

R² against the number of useless predictors, n = 30. The response is pure noise and so is every predictor, so the true relationship is nothing at all. R² rises from 0.000 to 0.648 anyway, following k/(n − 1) — which is what a criterion that rewards higher R² is actually rewarding.

Regression, and what the summary hides

R² is not a measure of fit

Adding a predictor with no relationship to anything cannot reduce R², and in expectation raises it by 1/(n − 1). Twenty useless predictors on thirty points give an R² of 0.69 from pure noise.

One rule keeps its promise and the other keeps its budget. Both stopping rules at five requirements, 1,500 experiments each, with a first stage of 5. The upper curve is the two-stage rule: 97.1%, 96.2%, 95.9%, 96.1%, 96.0% — at or above 95% at every point, which is a theorem rather than a tendency, because its interval is built from a spread estimated before the stopping point was chosen. It pays 2.06×, 2.01×, 2.00×, 1.99×, 1.99× the observations that knowing σ would need. The lower curve is the rule that re-estimates after every observation: 94.5%, 89.3%, 91.0%, 91.5%, 94.3%, on 0.98×, 0.87×, 0.88×, 0.93×, 0.96×. The second rule is the one anybody would run and the first is the one whose claim is true.

What the design is asked to guarantee

Stopping when it is precise enough

An experiment that runs until its estimate is precise enough is the natural design and the one with a theorem against it. Its two-stage cousin keeps its promise exactly, for every unknown spread, and pays twice the observations for it.

Four analyses of the same 3-arm trials, under a true null. 250 trials of 150 patients, 3 arms, minimisation with p = 0.85, 99 re-randomisations for each exact test. Two statistics — an F on the arms alone and an F on the arms after the balanced factors — against two reference distributions: the table the statistic is named for, and the distribution the allocation rule itself generates when the outcomes are held fixed and the rule is re-run. Only the first cell is wrong, and it is wrong in the direction that costs power rather than the one that manufactures findings: 0.0% where 5% is claimed. Either repair works — adjusting for what the rule balanced, or asking the rule what it would have done.

More arms than two

The analysis after three arms

An unadjusted analysis after a two-arm balancing rule rejects 0.6% of true nulls where it claims 5%. With three arms and a deterministic rule it rejects none at all — and the repair is the same repair, which is a sentence and a column in the model.

Four analyses of the same trials, with no treatment effect at all. 700 trials of 120 patients allocated by minimisation at p = 0.8, with the prognostic factors carrying a real effect on the outcome and no treatment effect — every rejection below is a false one. Two statistics, the plain difference and the same after adjusting for the balanced factors, each read against two reference distributions: a t table, and the set of allocations the rule could have produced from these covariates. The unadjusted comparison rejects 0.6% where it claims 5% — conservative, which is a loss of power rather than an error, and nothing on the output says so. Adjusting puts it back at 5.4%. Both re-randomised versions are at their nominal level by construction, whatever statistic goes into them.

Balancing on what was recorded first

The analysis has to know the rule

A trial balanced by minimisation and analysed by comparing the two arms' means rejects a true null 0.6% of the time where it claims 5%, and at full determinism 0.0%. That is not an error anybody complains about — it is a test that has stopped working, paid for by a balance the analysis then refused to use.

The weights may not read the block they weight. A weighted least squares decomposition needs weights that are constants, or at least independent of the differences they multiply. One λ̂ pooled across the trial is estimated on hundreds of degrees of freedom and is effectively a constant; a λ̂ estimated inside each block is estimated on that block's own two or three, and is correlated with the difference it weights. Coverage falls from 94.68% to 82.76% — and the interval gets wider while doing it, 0.5163 against 0.3024, which is the signature of weights that are noise.

The weights the corner needs

The condition that cannot be dropped

The weights may not read the block they weight. Estimate the variance ratio inside each block rather than across the trial and the coverage falls to 83% — on an interval that is at the same time seventy per cent wider.

A cut at a quantile, and a cut at a value. Two rules that read identically in a protocol. One splits each covariate at its median; the other splits it at 1 on the covariate's own scale — a dose, a temperature, a clinical threshold. At a correlation of 0.5 the first removes exactly nothing of the interaction between its own two splits, under every marginal here, because a median split is a function of the sign of the latent normal whatever the marginal is. The second removes what the bars show, and it does so on a normal covariate too: the threshold sits at 1.000 on the latent scale rather than at zero, so it is 59.4% odd and 40.6% even. The exact zero was never about the cut; it was about the cut being at the median.

A guarantee that needed a symmetry

The cut that is not a quantile

A protocol that says split the covariate at a threshold and one that says split it at the median read the same and are different rules. One has an exact guarantee under every marginal and the other has none under any.

Two arms leave one degree of freedom per block unaccounted for. Each point is one run. The one-mean field's identity is (b − 1) + (N − b) = N − 1, and every schedule moves along that line rather than off it. Two arms give the rule N − 2b and the interval b − 1, which come to N − b − 1 — short of the N − 2 two arms leave by exactly one per block, since a block's arm counts absorb one degree of freedom each and only one of the two directions carries the difference. The hollow points add what the block sums are worth, b − 1 more, and land on the total. The missing degrees of freedom are not lost; they are in a place the interval has to be shown it may read.

A promise about two arms

The degrees of freedom in the sums

One arm partitions N − 1 exactly. Two arms give the rule N − 2b and the interval b − 1, which is short by one per block — and the missing ones are in the block sums, which are correlated with the differences at −0.79 and are usable anyway.

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.

Sixteen candidates nobody would have run, and what they cost. At φ = 0.65 one candidate in the original set is genuinely better than the benchmark, and the question is how often each procedure finds it. The added candidates are stale copies of the last value — read two, four, six … steps late — every one of them worse than the benchmark by at least 43%, and not one of them is ever the best candidate in a sample. The reality check goes from 35.5% to 0.0% as they are added, because its reference distribution has to assume every candidate is exactly as good as the benchmark and sixteen such assumptions is a critical value nothing reaches. The recentred version, which drops from the recentring the candidates the data has already ruled out — 15.1 of 24 of them — goes from 25.5% to 24.5%. The top line never moves: reporting the winner's own p-value cannot notice a change to a set it never looks at.

The best of a set, and what the search costs

The models that were never in the running

A reference distribution for a set has to assume something about every candidate in it. Assuming that all of them are as good as the benchmark is what makes the reality check honest, and it is what sixteen hopeless candidates use to destroy it.

Four rules of four change sign. The margin between the two block windows in points of coverage, under each of four rules, on each of three intervals built from the same resamples, over 300 draws. Positive is the tapered window covering better. On the percentile interval the taper wins at all four rules, by 5.33, 1.67, 5.00 and 4.00 points, which is the earlier field's own reading. On the studentised interval the rectangle wins at all four, by 4.33, 7.00, 4.33 and 2.67. And a normal interval, which uses no resampling at all, puts the two within a third of a point at every rule — so the disagreement is manufactured entirely by what is done with the resamples.

The interval, studentised

The ordering reverses again

One field found two of four rules changing sign between two readings of one resampling. Turn the same resamples into a studentised interval instead of a percentile one and all four change sign.

Where the +1 matters, and why nobody has noticed that it does. The true size of the two rules at every B, computed rather than simulated: under the null the count of re-randomisations reaching the observed statistic is uniform over {0 … B}, so both sizes are integer arithmetic. With the +1 the size is (⌊α(B+1)⌋)/(B+1), which never exceeds 5%. Without it the size is (⌊αB⌋+1)/(B+1), which is larger except at B = 19, 39, 59 — the values with B + 1 a multiple of 1/α, and the values everybody uses. At B = 19 the two rules are the same rule; at B = 20 the uncorrected one is a 9.5% test. The marks are simulated on 500 trials of 120 patients, as the second route to the same numbers.

The reference distribution the design supplies

The plus one and the round number

A sampled randomisation test counts the observed allocation as one of its own reference draws, and the correction is invisible at B = 19, 39, 59 and 999 — every value anybody uses. At B = 20 the version without it is an 8.00% test where the corrected one is 3.80%, and the convention protecting everybody is a preference for round numbers minus one.

τ̂ across 2,000 datasets of 12 groups, true τ = 1.5. The population spread is not supplied to a hierarchical model — it is estimated from how far apart the group means are, after subtracting the noise that would separate them anyway. It averages 1.41 here against a true 1.5, and comes out exactly zero on 5% of datasets.

Groups that borrow

The prior the data estimates

A hierarchical model needs a population spread, and it does not ask for one. It reads τ off the distance between the group means — biased six per cent low, exactly zero on 53% of datasets where the groups are identical — and the prior stops being a belief.

The row count entered twice, and a penalty is one place. Regret against the best available model as the errors are made persistent. Counting rows more than quadruples; both penalty repairs — the trace, and the scalar effective sample size — are worse than it at every persistence measured; and whitening the sample and keeping the ordinary penalty falls, recovering 86.9% of what counting rows gives up at ρ = 0.85. Doing it at an estimated ρ recovers 80.6%, so having to estimate the dependence from the rows being selected on costs 7.3% of what knowing it is worth. Mallows' forms are drawn beside the logarithmic ones and behave the same, which is what rules the linearisation out.

Counting what is independent

The repair that was exact and made it worse

A penalty computed from the trace is exactly the optimism it estimates, and selecting with it gives up a fifth more than not correcting anything. The row count entered the criterion twice, and a penalty is the second place.

The block length read on a quantile

The reversal that was the instrument's

On an implied variance the rectangle wins at a protocol length and at the rule of thumb. On the 95% point a test reads, and on the coverage an interval delivers, the taper wins at all four rules.

Exact coverage, at every block size. Coverage of the interval each rule reports, at a nominal 95%, over 2,500 runs each with a standard error of 0.44 points. The blinded rule stops on the within-block contrasts and reports an interval built from the block means, and those two are independent whatever the rule does — so the interval is an ordinary t interval on b − 1 degrees of freedom and its coverage is exact. It is exact at every block size drawn. The interval a practitioner writes at the purely sequential rule's stopping time covers 91.72%, and Stein's two-stage rule is exact for the same reason as the blinded rule and spends 2.10 times the observations to be so. The bars are truncated at 86% so the differences can be seen.

What the procedure may not read

The rule that cannot see the mean

A sequential rule stops when its own estimate of the spread is small, which is more often on the samples whose spread came out low — so the interval afterwards is short. There is a way to keep updating the estimate and stop being able to see the mean at all.

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.

The shape a dependence has

The window a whitening wants

Every law here is best whitened by a window several times longer than its own memory, including the one whose memory ends at the fourth lag. The three ways of choosing it from the sample all land in the same place, and it is the wrong one.

The guarantee that survives a correlation, and the one that does not. What a balancing rule handed both main effects removes of the pure interaction between them, as the covariates become dependent. For median splits it is exactly zero at every correlation, because sign(x)² = 1: the interaction sign(X)sign(Y) is orthogonal to sign(X) and to sign(Y) whatever ρ is. For the product of the raw covariates it is 4ρ²/(1+ρ²)² — 64.00% by ρ = 0.5, rising to all of it at perfect correlation. A cut away from the median sits between them and is not small: 23.01% at a cut of one. The zero is not a fact about interactions. It is a fact about a dictionary whose functions square to a constant, which a polynomial one does not.

A cut point, at a correlation

The zero that survives a cut

A rule holding both main effects removes half of a pure interaction between correlated powers and exactly none between correlated median splits. The guarantee that a correlation destroyed was never about interactions.

What a rule reads, against what the outcome uses. The variance of the treatment estimate relative to a coin's, for four things a rule might balance against three shapes the outcome might have, over 350 trials of 200 units. The diagonal is the easy part — a rule that reads the function the outcome uses removes about half the variance. What the table is for is the off-diagonal: reading the covariate alone is worth nothing against a quadratic (0.755), and reading all three is worth nearly as much against every shape as the matching rule is against its own (0.532, 0.493, 0.514).

The shape the covariate enters by

Three functions of one number

A rule that balances the covariate is exposed to every shape the outcome might have. A rule that balances three functions of it costs two points of variance against the shape the first was built for and takes the worst case from a coin's to about half of it.

A central composite design, 13 runs. Adding 4 axial runs at ±√2 gives every factor three levels, which is the least that can estimate a squared term. The normal matrix now inverts, so each βᵢᵢ has an estimate of its own — and at exactly this axial distance the design is rotatable, which the next figure measures.

The surface between the corners

Three levels, and the ring where the design says the same thing

A central composite design puts its axial runs at ±α, and α is not a matter of taste. At F to the quarter the prediction variance depends only on how far a point is from the centre and not at all on which direction it lies in — a property with no simulation in it, exact or absent.

Two searches over different features

Three quarters of the way to one search

The pair that started this reads 0.762 on a scale whose one is containment. And the pair that shares nothing but its response reads −0.306, so the sign the earlier field found does not transport at all.

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.

Scoring a search without spending data

Two defects and one resampling

Four resamplings, each the repair for one defect and wrong about the other. Put both defects in the same world and the statistic's 5% point is 3.8028, where the best of the four reaches 2.8326 — until a multiplier that stays on its own row and shares a sign with its neighbours reaches 2.9988.

How long a walk has to be given. Every equal split of twelve units is enumerated, the 410 admissible ones are found, the transition matrix is built, and the distance from uniform is computed exactly at each step — no simulation anywhere. The walk is started at the least balanced admissible assignment, which is the state a rejection sampler is least likely to have handed it and the one a burn-in has to cover. It is 0.0849 away after twenty steps and 0.00008 after ninety. A real cost, and a small one, and naming it is what stops it being assumed to be zero.

When the two are not independent

Walking the admissible set

A rerandomisation test hunts for admissible assignments and throws away the rest. A walk visits them instead — and it is exactly uniform only because it stands still when a proposal fails, which is the step that looks like waste.

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 overshoot is the last block size and nothing else. A run stops at a multiple of its own block sizes and cannot land between them, so it ends past its own target by about half a block. Fixed sizes overshoot by 1.5, 2.2, 3.1, 4.7, 8.5 observations as the size goes 2, 3, 5, 8, 16. Every schedule here ends in blocks of two and every one of them lands where blocks of two land — 1.62, 1.32, 1.37 against 1.48 — while having spent most of the run inside blocks four and eight times larger. That is the one thing on this page a schedule genuinely takes from both ends.

The block size as a schedule

What a schedule actually buys

Big blocks early and small blocks late is the right instinct and it does not take both ends of the trade, because there are not two ends to take. What it does take is the overshoot — about four per cent of the observations — and a steadier stopping point.

A block length chosen from the data

What choosing the length costs

The gap between two block windows at the best available length is 2.12 points. What the best rule a practitioner could run gives up against that same length is 7.26. The argument is a third of the size of the thing it is inside.

What differencing fixes, and what it costs, 100 steps. The first pair is the false-positive rate for two independent random walks: 77% on the levels, 4.9% on the differences. The second pair is how much of a real relationship survives: R² falls from 0.91 to 0.33. The same operation does both.

When the observations repeat each other

What differencing costs

Differencing takes the false-positive rate between two unrelated walks from 76.7% to 4.9%, and takes a genuine relationship's R² from 0.91 to 0.33. Applied to a series that did not need it, it doubles the variance and installs a correlation of −0.5 that the data never had.

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.

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.

Three analyses of the same trials, none of them wrong about the data. 320 trials at n = 60 with no treatment effect at all, so every rejection counted is a false one, and a covariate that drives the outcome with coefficient 1. The unadjusted comparison is at 5.94% after a coin — its level — and at 0.00% after the rule that reads the covariate: the design removed the imbalance and the analysis is still pricing it. Adjusting for the covariate gives 4.06%, and the rule's own reference distribution — hold the outcomes, re-run the rule 199 times, count — gives 3.13% against the 4.5% that 199 draws can deliver. The last of the three has to be told the assignment rule and nothing else, which is the one thing the experimenter certainly knows.

Balancing what has no levels

What the balanced trial is worth

A rule that reads the covariate removes three quarters of the imbalance. An analysis that does not know it happened prices the imbalance anyway, rejects one true null in two hundred instead of one in twenty, and finds a real effect less often than a coin-tossed trial does.

How often "there is no spread between the groups" is reported about data that has one. Every dataset here was generated with a real population spread of 1. The moment estimator is the difference between the observed spread and what noise alone would produce, clamped at zero, and the difference comes out negative often: at eight groups it reports exactly zero on 32.6% of datasets, which is an instruction to pool completely and give all eight groups the same estimate. The rate falls to 4.2% at 48 groups.

The spread, and its own uncertainty

When the spread estimates to zero

The usual estimate of a population spread is a difference of two positive quantities, clamped at zero. On a third of eight-group datasets with a real spread in them the difference comes out negative, the estimate is exactly zero, and every group is pooled completely on data that said no such thing.

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.

A class that is a subspace has no guarantee below its own dimension. Each cell is the worst case over every unit-variance function in a class of dimension m, for a rule reading k functions: the smallest squared principal-angle cosine between the two subspaces. Wherever k is less than m the number is zero to machine precision, and that is not a weak guarantee but the absence of one — some direction of the class is orthogonal to the entire basis, and against an outcome in that direction the rule does exactly what a coin does. An experimenter who declines to name the shapes and asks instead to be protected against everything smooth is asking for the cells above the diagonal.

Choosing what the rule reads

Where the guarantee is exactly zero

An experimenter who declines to name the shapes, and asks instead to be protected against anything in a class, is asking for a number that is not small but zero. Bounding the class is unavoidable, and the two ways of doing it choose different bases.

Which tail the threshold is in. What a rule balancing a threshold at 1 on each covariate's own scale removes of the interaction between the two thresholds, on five copulas matched at a Spearman rank correlation of 0.4 with a normal covariate throughout. This rule never had a zero to lose — the earlier field establishes that under every marginal — so what is left is a size, and the size depends on where the dependence lives. A Clayton copula, whose density piles up in the lower tail, leaves 5.33%; the same copula turned over, so that it piles up in the upper tail where the threshold is, leaves 33.36%. Same rank correlation, same Kendall tau, same marginal, same threshold: 6.26 times the leak, decided by which end of the distribution the dependence and the cut are both in.

The other half of the dependence

Which tail the cut sits in

The same copula and its reflection have the same rank correlation, the same Kendall tau and the same marginals. A balancing rule holding a threshold at a dose leaves 5.33% under one and 33.36% under the other.

What conditioning on a variable does

Adjusting for everything

"Control for every covariate that was measured" leaves a larger bias than controlling for nothing on 65.5% of four thousand randomly drawn structures and a smaller one on 33.8%. Its squared error is 4.110 times that of using no covariate at all, and half of it sits in its worst tenth of structures.

The threshold buys accuracy and spends exceedances. The mean squared error of the estimated shape against the threshold, split into the square of its bias and its spread, over 600 records of 2000 readings from a a normal parent. At the 0.9 quantile 199 exceedances are left, the bias is -0.1708, the spread is 0.0701 and the total error is 0.0341. The bias falls as the threshold rises because the exceedances get closer to being generalised Pareto; the spread rises because there are fewer of them. The sum is smallest at the 0.925 quantile, at 0.0340, of which 80.6% is still bias — so even the best threshold on this grid is one where accuracy, not spread, is the binding constraint.

The tail past the last observation

The threshold is a dial

A peaks-over-threshold analysis has one knob, and raising it buys accuracy with exceedances. For a normal parent the error is smallest at the 0.925 quantile and 80.6% of it is still bias there — and both diagnostics practitioners use to set the knob lose to a fixed 0.90 rule, one by a factor of 1.590 and one by 11.881.

A filled value is not an observation. What a 95% interval for the slope actually covers after each way of handling 35.0% missing outcomes, counted over 4000 studies of 200 rows. Dropping the incomplete rows covers 95.93%. Filling with the observed mean covers 13.85%, because the estimate itself has moved. Filling with a fitted value covers 80.85% against a closed prediction of 79.73%: the estimate is right and the reported standard error is short by a factor of 0.6567 against a predicted 0.6500, because the residual sum of squares is divided by the whole sample's degrees of freedom. Adding residual noise recovers the spread and covers 85.78% against a predicted 84.62%, since the interval still ignores the variance of having imputed at all.

The value that is not there

One imputation is not an observation

Three ways of filling a missing outcome, under a mechanism that makes dropping the rows beyond reproach. Filling with the observed mean covers 13.85%, filling with a fitted value covers 80.85%, adding noise covers 85.78%, and the thing all three were meant to improve on covers 95.93%.

Robust, at the sample sizes it is reached for. Counted coverage of five 95% intervals for a slope, at six sample sizes, under an error variance leaning towards the edges of the design (γ = 0.8), over 20000 draws at the small end. The model-based interval sits at about 87.06% everywhere and does not improve with the sample, because it is a claim about a variance it is not estimating. The robust ones do improve: HC0 covers 88.73% at 20 rows, 92.70% at 50 and 94.93% at 1,000. Its promise is asymptotic and its use is not, and the gap between those two facts is this picture. The leave-one-out correction read against a t on n − 2 is the only line that is near its promise at the small end: 94.55% at 20 rows.

A standard error for a model that is wrong

Robust is not free

A robust standard error's promise is asymptotic and its use is not. Its 95% interval covers 88.73% at twenty rows, and under mild heteroskedasticity it is the worse of the two intervals until a hundred.

Six forecasters, all calibrated, not equally useful. The resolution of six forecasters that are all perfectly calibrated, each reporting the true probability of the event given a signal that carries more or less of the latent state. The largest reliability anywhere in the family is 2.0e-33, so a calibration check passes every one of them. They are not equally good: resolution runs from exactly 0.00 for the forecaster that issues the base rate every time to 0.092758 for the one that sees everything, and their Brier scores run from 0.234237 — which is the world's own uncertainty, and the score of a table of base rates — to 0.141479. Calibration is a necessary condition that a constant forecast satisfies exactly.

A forecast that is a probability

Calibrated and useless

Six forecasters that are calibrated to 2·10⁻³³ run from resolution exactly 0 to 0.092758, and three forecasters with reliabilities from 0 to 0.013025 have areas under the ROC curve identical to every bit a double carries. Each measure is exactly blind to what the other one sees.

Weighting one sample into another

The region with no comparison

A trimmed interval covers the average effect over everybody 90.8% of the time at six hundred rows and 41.0% at nine thousand six hundred, while covering the average effect over the units it kept 94.3% and 96.0% throughout. An interval that gets worse as the sample grows is an interval about something else.

One cohort of 40, and two intervals around the end of its curve. A single simulated study of 40 subjects with exponential survival at rate 0.35, dropout at rate 0.15 and follow-up to 6 — the first seed from 8811 upward whose plain band reaches below −0.05, chosen to show the failure rather than its frequency. The step curve is Kaplan–Meier and the smooth curve the truth. The plain band, the estimate plus and minus 1.96 Greenwood standard errors, first dips below zero at t = 3.78 and reaches −0.052; early on it also rises to 1.023, above one. At t = 5 the estimate is 0.069 with 1 subject still under observation, the plain interval runs from −0.052 to 0.191 and the log-log interval from 0.006 to 0.251, against a truth of 0.174. The log-log band is built on a scale that cannot leave [0, 1], and it bends away from the edge rather than through it.

When the data stops early

The interval at the end of the curve

The interval most software prints around a survival curve covers 89.7% at five years, where 3.3 of forty subjects are still being watched and where the curve is actually read. The same variance carried on a log–log scale covers 94.8% there — and the failure was never the width.

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.

The interval that over-covers when the instrument fails. Counted coverage of two nominal 95.0% intervals for the same causal effect, read off the same 2000 draws of 200 rows at each first stage. The exact Anderson–Rubin set covers 95.3% at every setting — flat, because the statistic it inverts is built from y − tβ, which contains no π at all, and is therefore the same number on the same draw whatever the instrument is worth. The conventional interval covers 99.1% at π = 0.02 and 95.6% at π = 0.6: it goes wrong at the weak end by covering too MUCH, at a median width of 7.320, because its standard error is computed from residuals taken at an estimate that has itself gone wrong. A weak instrument does not make this interval lie about its coverage; it makes it useless while telling the truth.

A variable that moves one thing only

What the first stage does not know

A single weak instrument does not make the conventional interval undercover — it makes it cover 99.1% at a width of 7.320. Where the promise actually breaks is many instruments — coverage falls from 97.2% to 51.5% while the median width falls from 1.454 to 0.583.

Forty O'Brien–Fleming trials at a true effect of 0.16, with the boundary written as an effect. The dashed line is the smallest effect a trial can report and still stop at each look: 0.510 at 80 observations, 0.255 at 160 observations, 0.170 at 240 observations, 0.128 at 320 observations, 0.102 at 400 observations. The true effect is 0.16, so at 3 of the five looks a trial cannot stop without reporting more than it. 29 of these forty trials stop before the last look, each marked where it stopped.

Stopping rules

The effect a stopped trial reports

An O'Brien–Fleming trial at 88.45% power holds its error rate exactly and reports an effect 9.6% too large on average. The 11.39% of trials that stop at the second look report 1.83 times the truth, the ones that cross at the last look report 0.80 times it, and pooling every trial by its size gives the truth back to the last digit.

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 far apart four summaries put the quartet. Each bar is the largest value minus the smallest across the four datasets. Pearson spans 0.0018, which is the construction working. Distance correlation — the measure that is zero if and only if the variables are independent — spans 0.101, and Spearman spans 0.491.

What a summary of a scatter is a property of

The summary that was meant to work

Distance correlation is zero if and only if two variables are independent, which is exactly the guarantee a correlation coefficient lacks. Run on the four datasets that share a correlation, it spreads them by 0.10 — and Spearman, which guarantees nothing, spreads them by 0.49.

Estimating a prevalence of 0.10% from 1,000 tests. The positive rate reads 5.09%, which is 50.9 times the truth. The Rogan-Gladen correction averages 0.100% — unbiased — with a standard deviation of 0.820 points against the positive rate's 0.695, and it comes out negative on 48.6% of samples.

Two tests, a threshold, and the rate they are read against

The prevalence the test has to estimate

Every predictive value takes a prevalence as given, and the prevalence is usually estimated from the same test's positive rate. At a true prevalence of one in a thousand that rate reads 5.09% — fifty times the truth — and the correction that inverts it is unbiased, 18% more variable, and negative on 48.6% of samples of a thousand.

How many observations the smallest and largest of them need. The interval between the extremes of n draws holds at least 95% of the population with probability 1 - n p^(n-1) + (n-1) p^n, whatever the population is. Reaching 95% confidence takes 93 observations.

The interval that holds observations, not a mean

Ninety-three observations, and nothing assumed

The interval between the smallest and largest of a sample holds a share of the population whose distribution does not depend on the population — Beta(n − 1, 2), for anything continuous. Buying the 95/95 that normality buys at ten observations costs 93 of them, and that number is the exchange rate between an assumption and data.

Welch's test on skewed groups: the low and high rejection rates in every cell, with equal means throughout. Each cell should read 2.5 / 2.5. Two identical exponentials at 20 and 20 read 2.04 / 2.22; the worst cell, a wide exponential against a normal at 8 and 32, reads 9.79 / 0.47.

Shape, and what it does to a two-sample test

The skewness of a difference

Welch's test holds its size to within half a point when both groups are normal. Give both groups the same skewed population and it still balances at twenty and twenty — and at eight and thirty-two it rejects low on 7.16% of samples and high on 0.66%. One number decides which: the skewness of the difference of the two means, which ranks twenty-five cells by their imbalance with a correlation of 0.997.

Clopper–Pearson, mid-p and the randomised interval: coverage across the proportion, 20 trials. Clopper–Pearson never falls below 95% and runs up to 99.80%. The mid-p interval, which is the randomised interval with its coin fixed at one half, runs from 92.94% to 99.80%. The randomised interval covers 95% at every proportion, to within the 0.043% of the numerical integration over the coin.

A proportion's interval near the boundary, and the coin

The coin that makes it exact

Every interval for a proportion either covers less than 95% somewhere or more than 95% on average, because a count is discrete. One construction covers exactly 95% at every proportion: it adds a uniform random draw to the count. At thirty trials it is 0.9% wider than Wilson's interval and narrower than both exact ones — and two analysts with the same data report different intervals, and one study in forty that sees nothing reports an empty one.

How much of a normal outcome's information survives cutting it into two, by where the cut is. For a small shift, a cut at the mean keeps 63.7% of the information, so the trial needs 1.57 times the sample. A cut at the top tenth keeps 34.2% and needs 2.92 times; a cut two standard deviations out keeps 13.1%.

What a sample-size calculation was given

An outcome cut in two

Replacing a measured outcome with whether it crossed a threshold keeps 63.7% of the information when the cut is at the mean, 34.2% at the top tenth and 13.1% two standard deviations out. A trial that needs 63 patients per arm on the measured outcome needs 102 cut at the mean and 185 cut at one and a half standard deviations. The responder rates that result read as a share of patients who respond — 50.0% against 69.1% — when every patient moved by the same amount; and a cut chosen after looking turns a 5% test into a 17.7% one.

One t interval with its scale read three ways, 120 rows in blocks of 32. What a 95% t interval for the mean of a first-order autoregression at 0.7 covers, and how wide it is, when its block-means scale is read from the 3 disjoint blocks of 32 rows, from a block at every one of the 89 starting rows, and from those overlapping blocks tapered — over 8,000 draws. Disjoint: 94.4% at a width of 1.560, with a multiplier of 4.30. Every starting row: 94.8% at 1.054, multiplier 2.74. Tapered: 95.0% at 1.020, multiplier 2.57.

A block, weighted inside itself

A block at every starting row

The t interval on the block count reads its scale from the disjoint blocks, three of them when 120 rows are cut into blocks of thirty-two, and throws away the other eighty-six blocks the series contains. Reading a block at every starting row leaves the scale's attenuation where it was — the two expectations agree to within a hundredth at every cell — and nearly doubles the degrees of freedom it realises, so the interval loses a third of its width at the same coverage. Where the interval falls short, at short blocks, it falls short by the same amount however the blocks are read.

The best of a set, and what the search costs

A distribution drawn from the null

Between nested models the ordinary comparison statistic has a null distribution centred at minus one and a 95% point of a quarter. A correction to its mean repairs the centre and leaves the shape; simulating the null repairs both.

A wrong weight costs width; a random weight costs level. Five weightings on a trial whose variance ratio drifts by a factor of 20.1 between the first block and the last, over 4000 runs. The rule that knows every λ_b covers at 95.1% and sets the width. One ratio for the whole trial is wrong for every block and costs nothing in level — 94.8% — while being 20% wider; equal weights are calibrated by an identity and 22% wider. The ratio estimated inside each block is the only rule aimed at the quantity that actually varies, and it is the only one that misses the level, at 92.0%: a weight computed from a handful of degrees of freedom is mostly noise, and noise in a weight is not a wrong weight. Modelling the drift across blocks recovers the oracle's width at 94.8%.

What a block may vary

A ratio that changes between blocks

A wrong weight costs width and a random weight costs level. The rule aimed at the quantity that actually varies is the only one that misses its own coverage, and the rule that models it across blocks recovers the whole of what knowing it is worth.

What a schedule is allowed to read, and what happens when it reads more. The construction allows the block sizes to be anything at all as long as they are functions of the within-block contrasts, which are independent of every block mean. A schedule that shrinks the block whenever the between-block spread is running above what the contrasts say is a direct attempt to hold down the quantity the interval will be built from, and it succeeds: the estimate lands at 0.8373σ² against the honest 0.9831, and the coverage goes with it. Growing the block on the same spread instead pushes the other way and over-covers — which is not a repair, it is the same violation with the sign reversed, and the level is no longer a property of the procedure at all.

The block size as a schedule

A schedule that reads the mean

The block sizes may be anything at all provided they are functions of the contrasts. Two natural schedules break that, in opposite directions — and the most natural mistake of the three is not a schedule at all but a stopping rule, at 86.87% coverage and fewer observations.

Paying for a search

A second break on a flat profile

Searching a hundred and twenty rows for one change point manufactures five units of likelihood. Searching for a second manufactures four more, on a series that has at most one — and on a profile whose whole range is under seven.

One window for the table, or one each. The regret of the same fifteen-candidate table under AR(1) at 0.8 over 150 draws, with the window attached three ways. Chosen once from the fullest candidate's residuals it gives up 0.02518. Chosen from each candidate's own residuals, with the covariance estimate still shared, it gives up 0.02799 — a paired cost of 0.00281 at 2.0 standard errors for the tuning parameter alone. Estimating the covariance per candidate as well costs 0.01087, so the objection already on record is about 3.9 times the size of the one that was not.

Fitted together, or fitted after

A window for every candidate

The window and the order a whitening needs are chosen once, from the fullest candidate, on an argument that was made about an estimated covariance. A tuning parameter is not a covariance, and the two cost different amounts.

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.

A guarantee that stops being a number. The worst case of each dictionary over six outcome shapes, at a correlation of 0.5, against the skewness of the covariate. Under a symmetric marginal every rule made of odd functions has a worst case of exactly zero, and the rule holding a mean and a median split of each covariate — the two things every trial balances — is one of them. Under skew that zero becomes 0.74%, 1.83%, 2.24%, 2.49%: small numbers, each of which depends on a marginal nobody stated. The guarantee has not improved by becoming positive. It has stopped being a guarantee, because it can no longer be written down without the covariate's distribution in it.

A guarantee that needed a symmetry

Balancing a skewed covariate

The worst case of the rule every trial runs goes from exactly zero to somewhere between a quarter of a per cent and two and a half. Which is small, and is a number that cannot be stated without the covariate's distribution in it.

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 the set stops being one set. How many of the 3,432 equal splits of fourteen units a balancing rule admits, as the tolerance tightens, with the number of components single swaps leave it in. The set falls from 886 to 84 assignments, and somewhere in that fall it stops being connected: at 0.8 it is in 2 pieces and every assignment's complement is in the other one. Nothing about the rule changes at that point and nothing a chain reports changes either, which is the whole difficulty — the acceptance rate, the stationary distribution and the detailed balance are all in order on both sides of it.

The diagnostic after the trial

Before the trial and after

The same diagnostic run at two moments answers two different questions. Before, a positive verdict changes the design. After, it changes which number gets reported — and only for the numbers the defect can reach.

One of them is mostly leverage. How much of the design's own leverage direction each active-set probe carries, once both are standardised and projected off the rule's span — which is what a probe is, so it is the comparison that matters. Over 189 designs the modelled active set agrees with leverage at |r| = 0.8359 ± 0.0114 and the counted one at 0.4239 ± 0.0216. So the modelled probe is largely leverage under another name and the counted one is genuinely a different direction — and the counted one is the worse probe, at 0.3854 of alignment against 0.4272. What the active set contains beyond leverage points away from where the set splits.

A probe from what the rule blocks

Counting it exactly does not help

If a modelled active set lost because the model was crude, the exact one would win. It is computed at a cost no trial can pay, and it is worse — so the approximation was never what was costing the probe.

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.

What each construction carries, against what there was. The autocorrelation of a resampled error series at five lags, averaged over 60 samples of 40 resamples each. Three facts are in the picture. The residuals lie below the errors at every lag, which is the ceiling a multiplier cannot exceed. The blocked multiplier and the fixed-length block lie on top of each other below it — they attenuate identically, because the attenuation is the join — while the stationary bootstrap, whose runs are geometric rather than fixed, sits above them both. And the sieve is the exception in kind rather than in degree: at lag six it carries 0.0638 where the residuals have 0.0300 and the multiplier has -0.0011, because a fitted model extrapolates past the lags it was told about and a truncated sample sequence cannot.

Estimating the dependence, not naming it

Errors generated from a fitted model

The one construction that is not bounded by the residuals, because a model extrapolates past the lags it was told about and a truncated sample sequence cannot. It is nearly exact where the only defect is dependence, and it pays for it where there are two.

What a guesser gets, and what a guesser gets for nothing. 600 trials of 150 patients under a fully deterministic rule, with an investigator who knows the rule, the factors and every assignment so far. The guess rate falls with the number of arms — 87.8% at 2, 86.2% at 3, 81.0% at 4 — which reads like a trial getting safer and is not: what a guesser can trade on is the excess over the 50%, 33%, 25% they would get by naming an arm at random, and that goes the other way, from 1.76× chance at two arms to 3.24× at 4. The gap a guesser manufactures between the best and worst arm under a true null is 0.759, 0.733, 0.711 standard deviations — nearly unchanged.

More arms than two

Guessing one arm in three

A balancing rule is guessable because it is balancing. With three arms the next assignment is worked out less often than with two — and by more, relative to what a guesser gets for nothing, and the damage they can do is almost unchanged.

A bias against a variance, with the answer in between. How wrong one sample's reference distribution is, split into the two things it is wrong by. Sharing the multiplier over more rows keeps more of the dependence and closes the bias from 1.688 to 0.835; every row it is shared over also removes an independent sign from the 101 the sample started with, and the spread of the resulting quantile rises from 1.307 to 2.172. The distance a practitioner with one sample is actually exposed to is the two together, and it is smallest at ℓ = 5.

Scoring a search without spending data

How long a block a multiplier shares

Sharing a sign over more rows keeps more of the dependence and leaves fewer independent signs to build a distribution from. The bias falls from 1.6885 to 0.8479 and the spread rises from 1.3073 to 2.1716, and the rejection rate walks straight through its nominal level on the way from 11.3% to 1.3%.

What each analysis does at a true null, by shape. Four analyses of the same trials — 500 of them at each shape, 120 units, assigned by the rule that reads the covariate. Every rejection is false. The unadjusted analysis is the one that moves: 1.60% against a linear outcome, where the design removed a great deal that the standard error still prices, and 5.20% against a quadratic, where it removed nothing and the standard error is right. Adjusting holds the level in all three columns, and so does the design's own reference distribution, which needs to be told the rule and nothing else.

The shape the covariate enters by

The analysis and the shape

An unadjusted analysis after a rule that read the covariate is too cautious — by a third against a linear outcome, by nothing at all against a quadratic. And an adjustment for the wrong function recovers almost none of the precision the right one would.

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 corner costs when the table is full of hopeless candidates. The benchmark holds two predictors, one of which is worth 1; a third predictor, worth the amount on the horizontal axis, is held only by candidates the benchmark does not contain. At the left the null is true and both procedures hold their level. To the right there is a genuinely better candidate, and the uncorrected reality check finds it 2.7% of the time while the same test with the clearly bad columns recentred finds it 51.0% of the time. The columns doing the damage are the ones nobody would have looked at twice: they are so far behind that they cannot win, and calibrating as though they might is what makes the test blind.

A search with no fixed point

The corner the test is calibrated at

"No candidate is better than the benchmark" is not a null but a face of a region, and a reality check is calibrated at one corner of it. Fill the table with candidates that are hopeless rather than equal and the test finds a genuine improvement 0.0% of the time.

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.

Adding a run can make the design worse. The D-efficiency of the best N-run design at each size, against the optimal measure. It is not a rising curve. 13 runs reaches 99.77% and 14 falls to 99.44%, because the optimal weights are real numbers and N runs is an integer approximation to them, so how good a design can be depends on how well N divides. A Wald interval behaves the same way: a larger sample sometimes makes its coverage worse, for exactly this reason.

A design chosen rather than looked up

The design that has to be integers

The optimal design is a set of real weights and an experiment is a set of runs, so the theory's answer is never available. Thirteen runs reach 99.77% of it and fourteen reach 99.44% — adding a run makes the design worse per run, and the search that finds it does not always find the same one.

A design that is right once, against one that is never wrong by much. Two designs for the same two-parameter model, scored at every true value of K across a range of 16-fold. The local design is the two-point optimum for a guess of K = 1: it reaches 100% there and 66.7% at the worst point of the range. The hedged design maximises the average of log|M| over a prior spanning a factor of 4 either side, uses 3 settings rather than two, and is never below 75.4%. What it costs is 10.4 points at the one value the local design was built for — which is the whole trade, and it is only available to somebody willing to say how wrong the guess might be.

The criterion, and what it assumes

The design that hedges

A locally optimal design is right at one value of the unknown and 23.9% efficient at the edge of a sixteenfold range. Averaging the criterion over a prior instead buys the worst case back to 56.3% — and buys it by adding support points, at spreads the arithmetic decides rather than the experimenter — a third setting at a factor of 3.36 and a fourth at 8.86.

What the diagnostic says at two hundred units. The same test run 8 times on independent streams, at five tolerances of a two-hundred-unit trial, 40,000 steps each. At the loosest tolerance every run says the same thing — the walk reaches the whole set — and it keeps saying it as the set is thinned. Past a point the runs stop agreeing with each other: at the tightest tolerance here 6 of 8 report that the chains have not mixed and 2 report a split, which is a diagnostic disagreeing with itself rather than a property of the set. That disagreement is the honest answer at this size, and it is one nothing in this collection could give before: an enumeration stops at about twenty-four units.

What a chain cannot report

The diagnostic at two hundred

Pointed at a trial size no enumeration reaches, the test gives three answers rather than one — and past a certain thinness it stops agreeing with itself, which is the honest reading and the one nothing could give before.

Where the taper's case begins, and it is not where the algebra says. The block length at which a trapezoidal block's implied variance stops being more biased than a rectangular one's, against the length of the sample. Computed exactly — from the law's own autocovariances, with no sampling in it — the answer is 19.2 and does not depend on the sample at all. What a sample of 120 rows reports is 13.3, and the reported crossing walks out towards the exact one as the sample grows: 13.3, 15.0, 16.4, 18.0. The mechanism is that the autocovariances the window is applied to are themselves attenuated, worst at the longest lags, and the window that discards those lags loses less of them.

Where a taper's case begins

The error no window repairs

Every block window's best estimate of a long-run variance is wrong by about forty per cent at a hundred and twenty rows, and the largest part of that is not a bias at all. Choosing the window moves a twentieth of it.

Designs that change while they run

The estimate after the choice

An arm chosen for being ahead is ahead by more than it should be, and the trial then publishes the average of the stage that chose it and the stage that did not. The unbiased estimate is the one built from a third of the data — and it is the least accurate of the three.

Four intervals at one stopping time. 3,500 experiments under the sequential rule with a first stage of 5 and a required half-width of 0.4, which is a demand that knowing σ would meet with 24.0 observations and which the rule meets with 20.8. The rule's own interval covers 90.3%. Replacing the fixed width by a t interval on the same data gives 92.0%. Keeping the rule's own random sample size and drawing a fresh sample of that size gives 89.8% at the fixed width and 95.5% for a t interval — so the sample size being random costs nothing, and the sample size being chosen by the data the interval is built from costs the rest. The spread estimated at the stopping moment is 17.1% below the truth, which is the same fact one level down.

What the design is asked to guarantee

The interval after a stop it chose

A rule that stops when the estimated precision is good enough stops on the samples whose estimate was small. Its interval covers 90% and claims 95%, and a fresh sample of the same random size covers 95.4%.

What the interval covers once the order is chosen as well. 1200 series of 40 observations from an AR(1) with φ = 0.7, at each horizon, on one set of seeds. The upper line is the interval computed at the true parameters — it covers 95.5% on average, which is the check that σ²Σψ² is the right formula rather than a claim about anything a forecaster can do. The lower line is the same formula fed σ̂² and φ̂: 93.6% at one step and 90.8% at 6. The third line chooses the order by AIC from the same data before computing the interval, which costs a further 0.8 points at h = 6.

The observation that has not happened

The interval after the choice

Estimating the coefficients of a known model costs a 95% forecast interval about two points of coverage. Choosing which coefficients to estimate, from the same forty observations, costs another four and a half — so the step nobody records in the output is the more expensive of the two.

Counted coverage of two 95% intervals, over 2,000 datasets. Each point is one of the eight groups, at its own standard error. The integrated interval covers 95.2% overall against its stated 95%; the plug-in covers 78.8%, and its shortfall grows with the group's standard error — from 86.1% at se 0.5 to 77.0% at se 2.1. The mean widths are 3.48 and 2.66.

The spread, and its own uncertainty

The interval that integrates

A credible interval for one group in a hierarchy has to average over every value the population spread might take. That averaging is what makes it cover — 95.2% against the plug-in's 78.8% — and it costs 31% more width, a heavier tail, and a mixture rather than a normal.

Where the maximum is, from 15 runs. One dataset, one fitted quadratic, and two answers to "where is the best setting". The delta method reports 0.80 ± 0.46, a finite interval it will report whatever the data does. Fieller's set is 0.49 to 1.76, because the curvature here has t = -4.04. The true optimum is at 0.75.

The surface between the corners

The optimum is a ratio, and its interval is sometimes the whole line

The best setting is −b₁/2b₂: a ratio of two estimates whose denominator is a curvature the design can often barely see. The delta method reports a finite interval every time and covers 68.8% where the curvature is weak; Fieller's set covers 95% and says so by being unbounded.

Four sequences, and the rule only ever sees the last one. Under long memory at d = 4/9, four things that are all called the dependence. The law itself is the top line. What a sample of 120 rows reports on average is the second, computed exactly: subtracting a sample mean takes the first lag from 0.800 to 0.538. What a candidate's residuals report is the third, lower again at 0.472, because a fit removes dependence along with signal. The autoregressions are fitted to that third sequence and reproduce it exactly out to their own order — the Yule–Walker equations are solved to make it so — so everything they say past that is extrapolation. At the twentieth lag the law has 0.576, the residuals report 0.006, and an AR(8) extrapolates 0.028.

The shape a dependence has

The order the tail is drawn at

A fitted autoregression reproduces the sample exactly at the lags it was fitted on, so everything it says past them is extrapolation — and the order is the dial that decides how much of it there is.

The correction does not arrive at the truth, it passes it. The average decay factor a forecast applies to the last observation, at φ = 0.85 and 50 observations, 3000 series per horizon. The middle curve is φʰ, what the model actually does. Below it is the uncorrected forecast, which uses φ̂ʰ and reverts too fast — 24.8% short at h = 4, 30.0% short at h = 6, 32.7% short at h = 8. Above it is the forecast built on the corrected estimate, which overshoots, and the reason is arithmetic rather than a bad correction: raising an unbiased estimate to a power does not give an unbiased estimate of the power, and the higher the power the more the spread of φ̂ is converted into overshoot.

Comparing two forecasters

The repair that moves the wrong number

Correcting the bias in a persistence parameter is one line of arithmetic that works. Feeding the corrected estimate into a forecast repairs the number everybody looks at, makes the forecast worse by squared error at moderate persistence, and improves the interval for a reason that has nothing to do with bias.

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.

Expected width against coverage, n = 30, p = 0.15. The Wald interval is the shortest and covers 94.2%. Clopper–Pearson covers 98.3% and is 13% wider. Shortness is not a virtue on its own — an interval of zero width is the shortest of all.

Intervals, counted

The shortest interval is the one that misses

Four intervals for the same data, with their widths and their coverage measured together. The narrowest is the one that fails its stated level, which is exactly why it looks the most appealing.

A thin enough set is not one set. Every admissible set of 14 units this table can enumerate, by how much of the assignment space it admits and how many pieces it falls into under single swaps. A walk is uniform on the piece it starts in and never leaves it. The pieces are not fragments: at 522 admissible assignments the set splits into 3 halves of exactly 520 each, and every assignment's complement is in the other half — no sequence of admissible single swaps takes an assignment to its own mirror image. Two-swap proposals reconnect four of the six disconnected sets here — the two they do not are the thinnest, where a two-unit move rarely lands anywhere admissible either — which makes a bigger proposal a correctness repair rather than the speed dial it was measured as.

What a dictionary buys and what it costs

The walk that cannot cross

A thin enough admissible set is not one set. It splits into an assignment and its mirror image, no sequence of admissible single swaps joins them, and the walk that samples it is uniform on half the reference distribution for ever.

The one zero neither half of the dependence can touch. A median split's interaction leak at all 30 combinations of copula and marginal, on a log scale. Every one is under 10⁻¹⁶ and the largest is 1.74e-20, which is the quadrature's own noise rather than a leak. The reason is arithmetic and it is short: a centred median split takes the values ±½, so its square is a quarter identically — for every unit, on every draw, whatever the covariate's scale is and whatever joint law the ranks have. The interaction is then orthogonal to both main effects by construction, and there is nothing for either half of the dependence to break. Both of the fields this one joins report this zero holding under their own variation; running both variations at once is what establishes that it is not two coincidences.

Both halves of the dependence at once

The zero that survives both

A median split's interaction leak is under 10⁻¹⁶ at all thirty combinations of copula and marginal. It is the only guarantee in the collection that neither half of the dependence can touch.

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.

What 20 clusters of 20 correlated observations do to a 95% interval. Each study has 400 observations arranged as 20 clusters of 20. The lower points are the counted coverage of the usual interval, which treats them as 400 independent observations; the curve through them is 2Φ(1.96/√deff) − 1 with deff = 1 + 19ρ, computed before any data was drawn. At ρ = 0.81 the interval covers 36% rather than 95%. The upper points treat the cluster as the unit and need no variance components at all.

Hierarchy past one number

Two levels at once

A third level of grouping adds no new arithmetic and produces one number — the design effect — that decides how many independent observations a clustered study is worth. It is the same quantity the time-series field computes for autocorrelated data, arrived at from a completely different picture.

The scale moves the width; the curve does not. The band width each charge picks, averaged over 150 draws of 120 rows. The two conventions — a unit a lag and half a log n a lag — pick 6.08 and 3.65 lags. The four charges derived from the measured optimism pick 15.05, 15.60, 15.47 and 15.44, against a best width on the draw of 14.13. So the scale a charge is levied on moves the width by a factor of 4.27 and the shape of the charge moves it by 3.6%. None of the six is an estimate of the draw's own best width: the correlations are -0.006, -0.003, 0.017, -0.001, 0.016, -0.004.

A charge that is not a straight line

What a better charge buys

Four charges derived from the same measurements pick band widths within six per cent of each other and deliver errors within two per cent of the gap any of them leaves. The scale a charge is levied on decides the width; the shape of the charge decides nothing.

A design that assumes less

What a design chosen from the data costs

Two earlier measurements found what happens when a rule reads the data, and the error rate broke both times. A design that reads the data to decide where to put its runs breaks nothing — and the control that proves it also finds what the real shortfall is.

When the set is too large to walk

What a reference distribution costs to sample

A randomisation test on a trial too large to enumerate has to sample its reference distribution, at 1/p attempts per draw and a p-value resolved to 1/(B + 1). Six constraints cost 9,878 attempts per thousand draws, and a thousand draws resolve p to 9.99·10⁻⁴ and not one digit finer.

Free until the sums stop seeing what the differences see. Coverage with and without the block sums pooled into the interval's variance estimate. With one effect and one level they are free. With an effect that varies between blocks they are still free, because a block's sum picks that variation up exactly as its difference does. With a level that varies they make the interval 37% wider and conservative. And where the effect falls as the level rises — a ceiling, and not an exotic thing to suppose — the sums carry none of the between-block variation while the differences carry all of it, the pooled estimate is short, and the interval that uses it covers 88.75% on a width 20% narrower than the honest one.

A promise about two arms

What a two-arm rule may not pool

A spread computed "within the block" without the arm label carries a share of the effect, so the trial runs 173 observations at a null and 282 at an effect of 1.5. The stopping rule is reading the thing it exists to measure, and the phrase that produced it is one word long.

Fitting them together is worth something under one law. Four fits of the same regression under four dependences: least squares, the two-step plug-in every whitened rule in this collection runs, the coefficients and the band maximised together, and a whitening at the law's own covariance that nobody has. Under the moving average — the one law the band family contains — the joint fit beats the two-step by 0.0077 at 3.3 paired standard errors. Under the autoregression, long memory and the break it is a tie: 0.4, 1.0, 0.3 standard errors. That is the same ordering the likelihood gap gave, arrived at through the coefficients rather than through the objective.

A covariance with no parameter

What fitting them together buys

Maximising over the coefficients and the covariance together beats the two-step under one of four dependences and ties under the other three. It is the one the band family contains, and the likelihood said so before any coefficient was compared.

What the exactness costs, and the dial it is bought with. The median half-width of the interval each rule reports, at a requirement of 0.4 and a first look after 5 observations. The flat line is the interval a practitioner writes at the purely sequential rule's stopping time, which covers 91.72% rather than 95%. The curve is the blinded rule, which covers its nominal level at every block size: it reads b − 1 degrees of freedom where the other reads n − 1, and pays for the exactness in width. The best block size is 3, at 0.4712. Larger blocks give the stopping rule a better estimate and the interval a worse one, and the two costs go opposite ways, which is what puts the minimum in the middle.

What the procedure may not read

What the blindfold costs

The exactly-covering rule pays for it in the width of the interval, and the block size is a dial between two costs that run in opposite directions. And on an interval whose width was fixed in advance, the same repair buys nothing at all.

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.

One group 6 population widths from the rest. Squared error for each group under partial pooling, with each group's own mean beside it. Seven of the eight are estimated better by pooling. The eighth, which was never from the population, is estimated 6.1 times worse — 13.9 against 2.3.

Groups that borrow

When borrowing goes wrong

Partial pooling wins on the total and can lose badly on one group. Placed six population widths out, the group that was never from the population is estimated six times worse than by its own mean — and nothing in the output says so.

Searching among fitted models

When every null is true

A reality check assumes that every candidate in the set is exactly as good as the benchmark, which is a configuration nobody's data is ever in. Test a combination against its own parts and that configuration is not assumed — it is what the arithmetic makes true.

Where the constraints exhaust the randomisation. At 16 units there are 12,870 equal splits, so the ones meeting a stated tolerance can be counted rather than estimated. With each of the first k standardised imbalances required to be within 0.4 of a coin's own spread, the admissible count runs 3874 → 1006 → 314 → 0 → 0 → 0 — and at 4 functions there is no admissible assignment at all. The count is the number of distinct answers a randomisation test can give: at 3 functions its finest attainable p-value is 1 in 314. Balance improves with every constraint and the reference distribution shrinks with it, and the two run out at different rates.

Choosing what the rule reads

When the constraints run out

Every function added to a basis is a constraint the assignment has to satisfy with the same units. At sixteen units and a stated tolerance the admissible assignments run 3,874, then 1,006, then 314, then none — and the count is exact, because the assignment space is finite.

Every equation's adjustment speed, and the one number they make together. Each series gets its own equation, each is regressed on the same lagged disequilibrium, and what comes back is the whole vector α. Averaged over 400 systems at n = 300: α₁ = -0.154 against -0.15 generated, α₂ = 0.104 against 0.1 generated. The gap closes at the combination of them rather than at any one entry — 25% of any disagreement per step, a half-life of 2.41 steps, where the single equation that fits only the first series reports 4.27.

Three series, and a count

Which series does the moving

“y adjusts towards x” and “x adjusts towards y” are different mechanisms with identical long-run relations, and a single-equation model cannot tell them apart because it only writes one equation. Writing all of them recovers a vector — and a gap that closes at 25% a step where one equation alone reports 15%.

One penalty, read along two dials. How much wider the studentised interval is than the percentile one, at every sample size and every block length on the grid, with the number of whole blocks each cell leaves written beneath. Read across a row and the block length changes; read down a column and the sample size does. The penalty is nearly a function of the block count alone: the cells at 15 blocks read 1.16, 1.20, 1.17, 1.15, 1.13, 1.10 across three sample sizes and three block lengths, while the cells at one block length read anything from 1.10 to 3.95. The largest penalty on the grid is 3.95, at the cell with 3 whole blocks in it.

The interval, studentised

The count or the length

A block length and a block count are one number read two ways at one sample size. Read at three, the studentised interval's width penalty tracks the count — with an R² of 0.9911 against a closed form that has no length in it — and its coverage tracks the length.

The same dial, on a list that steps by one. The probability that a per-candidate tuning list changes which candidate the table selects, at each of 5 separations, for both tuning parameters at a matched list length of 8, with errors from a first-order autoregression. The sieve order runs from 13.1% to 2.6%, a factor of 5.00; the whitening window, from 16.4% to 1.5%, a factor of 11.75. What is held is the number of options, the table, the law, the sample size and the seeds; what cannot be held is the size of a step, since an integer step and a geometric step are different amounts of change. The dial moves both, and it moves them by 2.35 times as much on one as on the other.

What decides whether a tuning list decides

A step that is not a ratio

Run the separation sweep on a tuning list of integers rather than a geometric ladder and the two factors still point opposite ways. The invariant does not survive: along a row of integers the probability moves by 2.163 where along the geometric ladder it moves by 1.208.

The record stops here, and the curve does not. The level exceeded once in T blocks, against T, for a normal parent at 365 readings a block. The truth is closed form — the block maximum's own distribution function is Φ(x) raised to the 365, so the T-block level is Φ⁻¹ of the 365-th root of (1 − 1/T), with nothing fitted in it — and the fitted mean over 800 records of 50 blocks sits on top of it, 4.0186 against 4.0330 at 100 blocks. What moves is not the level but its error, which grows from 0.0956 at 10 blocks to 0.6383 at a thousand while the level itself moves only from 3.4421 to 4.5454. The rule marks the largest reading an average record contains, 4.0062: everything to the right of where it crosses is read from a fit rather than from data.

The tail past the last observation

A level with no data in it

The largest of fifty block maxima is a 51-block event by its own plotting position, so a hundred-block level is read 1.96 times past the longest event the record contains — and it lands above the largest reading on 52.4% of records. The estimate stays nearly unbiased out there; what grows is its error, sixfold from ten blocks to a thousand.

The extra 1/m, and the correction nobody quotes. What a pooled 95% interval covers against the number of imputations, counted over 2000 studies of 200 rows at 35.0% of outcomes missing. Rubin's rules — total variance W̄ + (1 + 1/m)B, read against a t distribution on (m − 1)(1 + W̄/((1 + 1/m)B))² degrees of freedom — cover 94.10% at two imputations and reach their promise by 5, at 95.25%. Dropping the (1 + 1/m) factor takes two imputations to 93.10%; using a normal quantile instead of the degrees-of-freedom correction takes it to 92.55%; dropping both takes it to 91.45%. The median degrees of freedom at two imputations is 12.95, which is why the second correction is the larger.

The value that is not there

The variance between imputations

Pooling several filled datasets covers 94.10% at two imputations and reaches its promise at five, where a single fill covered 85.78%. The correction everybody quotes is the smaller of the two doing the work — 1.00 ± 0.22 points against 1.55 ± 0.28.

Four numbers, and only one of them is the question. Four quantities in a population where the effect is not the same for everybody: 40.0% compliers, 25.0% always-takers and 35.0% never-takers, with the compliers carrying an effect 1.0000 larger than everybody else's. The population average effect is 0.5000. The compliers' average effect is 1.1000. A valid instrument converges on 1.1000 — the second of those, not the first, and the two differ by 0.6000. Comparing the treated with the untreated as they stand gives 1.4182, wrong by 0.9182 in the same direction, because always-takers start 1.5000 above never-takers before any treatment happens. The instrument removes the selection and changes the question at the same time, and only one of those is reported.

A variable that moves one thing only

Whose effect it is

With a perfectly valid instrument and no violation of anything, the estimate converges on 1.1000 where the population average effect is 0.5000. The gap is exactly θ(1 − p_c), the always-takers and never-takers cancel out of both halves of the ratio, and five per cent defiers move the answer to 1.2667.

A standard error for a model that is wrong

Three corrections and a leverage

On an even design of twenty rows the four robust corrections read 0.8603, 0.9559, 1.0000 and 1.1647 of the truth and the choice barely matters. Add one point at x = 8 and they read 0.3191, 0.3419, 1.0000 and 5.1127.

Either model is enough; neither is not. The bias of three estimators of an average effect of 1.0000, over 600 samples of 600 units with the assignment rule at strength 1, in each of the four cells made by getting each nuisance model right or wrong. The wrong model in both cases is one that omits the second covariate, which the outcome and the assignment both depend on. The outcome model alone is off by 0.8064 whenever it is the wrong one; weighting alone is off by 0.8190 whenever the propensity model is. The augmented estimator built from both is off by -0.0085, -0.0083 and -0.0016 in the three cells where at least one of them is right, and by 0.8118 in the fourth — which is between its two components rather than better than either.

Weighting one sample into another

Either model, but not neither

The augmented estimator's bias is −0.0085, −0.0083 and −0.0016 wherever one nuisance model is right, against components off by 0.8064 and 0.8190. One step past the overlap sweep it is the least biased estimator on the table at 0.0857 and the worst on it at 1.9265.

Which samples Wilson and Clopper–Pearson each cover, n = 50, p = 0.2. Each bar is the probability of one count, shaded by which interval built on that count contains 0.2. Both cover 95.1% of samples, only Wilson 0.0%, only Clopper–Pearson 1.6%, neither 3.3%. The correlation between their hits is 0.810, so on shared draws the variance of their difference is 4.891 times smaller than on independent ones.

What makes it checkable

The same draws for both methods

Two intervals computed on the same simulated datasets give a difference in coverage whose variance can be 4.891 times smaller than on separate datasets — or, for a pair that covers different samples, 1.164 times larger. Which one a comparison gets is an exact sum over the counts each interval covers, and a standard error that ignores the sharing covers 100.00% for one pair and 93.07% for the other.

A forecast that is a probability

A score that rewards lying

An absolute-error score pays a forecaster exactly ⅛ of a point to replace a true quarter with a zero, and over two hundred records a liar beats a truthful forecaster on 200 of 200. A skill score against the forecaster's own average buys 0.012633 of reported skill for 0.002035 of real score.

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.

What a sample-size calculation was given

A baseline cut in two

Adjusting a trial's result for a baseline measurement that predicts the outcome shrinks the sample it needs to 1 − ρ² of the unadjusted one. Adjusting for whether that measurement was above its median shrinks it only to 1 − (2/π)ρ² — the cut keeps 63.7% of what the covariate could remove, exactly the fraction a cut outcome keeps. In patients the loss grows with the covariate's strength: a cut costs 12% more patients at a correlation of 0.5, 35% at 0.7 and 2.55 times as many at 0.9, where a simple change from baseline would have done better than the cut adjustment.

How much naming more analyses in advance is worth, at an effect of 2 standard errors, for four analysts' beliefs. Twenty analyses correlated at 0.6, one of which holds the effect. Each curve is an analyst whose belief falls by a fixed ratio from one choice to the next: 0.2, 0.5, 0.7, 0.9. The best number to name is 1, 3, 5, 15 respectively, and each best set holds between 80% and 90% of the analyst's belief. Every curve ends at 22.7%, the power of correcting for all twenty.

The analyses that were available and not run

Naming a handful in advance

A preregistration that names three of twenty analyses sits between naming one and naming none, and whether it beats both depends on one thing: how much of the analyst's belief the three hold. An analyst who is 50% sure of a first choice, and whose belief halves down the list, gets 34.8% expected power from naming three, 28.3% from naming one and 22.7% from exploring all twenty. Spread the same 50% evenly over the rest and naming three is the worst of the three plans. The rule for adding one more to the list needs no belief at all: the next analysis must be at least 20.8% as likely as the first to be worth naming.

Coverage across the proportion of the randomised interval with the arrangement of the successes as its coin, 20 trials. Between proportions of 0.2 and 0.8 the arrangement coin's coverage stays within 0.121% of 95%, where mid-p's strays by 2.76%. Its worst coverage is 92.60%, at a proportion of 0.140, near the ends of the range where the count leaves few arrangements; mid-p's is 92.94%. Averaged over the proportion, 95.63% against mid-p's 96.11% and Clopper–Pearson's 97.71%.

A proportion's interval near the boundary, and the coin

The coin that is already there

The randomised interval covers exactly 95% at every proportion because it adds a drawn coin to the count, and a drawn coin is why nobody reports it. A sequence of trials already holds one: given the count, the order the successes arrived in is equally likely to be any of its arrangements whatever the proportion is. Used as the coin, it keeps twenty trials' coverage within 0.12 points of 95% from proportions of 0.2 to 0.8, where mid-p strays by 2.8, and it gives the same interval to every analyst. It fails where the count has few arrangements — a count of none has one — and it holds only while the order is read as recorded: an analyst choosing among sixteen orders lifts a 5% test on sixteen trials to 7.68%.

Coverage against block length, 120 rows. The coverage of the t interval for the mean of a first-order autoregression at 0.7 on 120 rows, at every block length on a fine grid, with its scale read from the disjoint blocks and from a block at every starting row, over 8,000 draws. The squared-error length for disjoint blocks at the true persistence is 13.9 rows, and the same algebra for the overlapping scale gives 16.0, marked. The overlapping interval first reaches 95% — to within a tenth of a point — at blocks of 32 rows, where it covers 94.9% at a width of 1.056; at the overlapping squared-error length it covers about 92.5%.

A block, weighted inside itself

A length chosen for the interval

The squared-error rule for a block length weighs the scale's bias against its variance. Rebuilt for a block at every starting row, whose variance is two thirds as large, it asks for blocks fourteen per cent longer and buys four tenths of a point of coverage. A t interval has already paid for the scale's variance in its multiplier, so its own coverage is predicted by the bias alone — within seven tenths of a point up to blocks of twenty-eight rows — and a rule that chooses the shortest length that prediction says will cover asks for blocks two and a half to three times longer and lands within about a point of 95% at 120, 240 and 480 rows. The price is width, and it is paid where the series is short.

A cut walked from the median into each tail. What a rule balancing a threshold on each of two normal covariates removes of the interaction between the two thresholds, with the cut moved from the 1st percentile to the 99th, on five copulas at a Spearman rank correlation of 0.4. Every copula reads exactly zero at the median. The three radially symmetric copulas are mirror images about it: the Gaussian peaks at 19.49% near the 95th percentile and is down to 13.44% at the 99th; the Frank peaks at 13.22% near the 85th and falls to 2.06%; the t is still near its highest, 37.45%, at the 99th. The Clayton climbs to 56.37% at the 1st percentile, in the tail its dependence is in, and never passes 5.39% in the other; its reflection is the same curve turned round.

The other half of the dependence

A cut walked into the tail

Move a balancing rule's threshold off the median and the interaction it leaks rises from exactly zero — and then either turns back to nothing or climbs to a ceiling, depending on one property of the dependence. With both covariates cut, the whole regression collapses to two probabilities, and far out it settles on 2λ/(1 + λ) of the tail-dependence coefficient: 57.25% under a Clayton, 35.57% under a t, and zero under a Gaussian or a Frank however strongly the covariates are related.

One pooled ratio, two periods. The calibration factor of weights built from one variance ratio pooled across the trial — the factor by which the interval's own scale estimate overstates the estimate's variance — when arm B's ratio is F times higher in one kind of period than the other, closed form on the corner's block compositions. With the small A-heavy blocks the noisier, the factor rises: 1.00 at F = 1, 1.50 at F = 1.5, 2.07 at F = 2, 3.12 at F = 3, 3.91 at F = 4, 4.86 at F = 6, 5.44 at F = 8. With the large B-heavy blocks the noisier, it falls: 1.00 at F = 1, 0.74 at F = 1.5, 0.65 at F = 2, 0.58 at F = 3, 0.55 at F = 4, 0.53 at F = 6, 0.53 at F = 8. A ratio estimated per period gives weights that are the inverse variances again, and its factor is exactly 1 at every F.

The weights the corner needs

A ratio that changes with the period

The corner's exact interval needs one variance ratio, and the corner's own alternating allocation makes two kinds of period that need not share one. When they differ the pooled ratio is precise and wrong: at a fourfold difference the interval covers 100.0% one way round and 85.1% the other. A ratio estimated per period is exact again, blind to the effect, and costs under a tenth of the width — and a ratio that merely wanders at random costs width and no coverage at all.

A premium that shrinks and a payout that grows. The relative error of the trapezoid's implied variance with the block length read off the whole autocovariance sequence, minus its error with the length from the lag-one correlation alone, in points, at four sample sizes and 400 draws each. Under the first-order autoregression the plug-in's algebra was written for, reading the sequence costs 3.87 at 120, 2.37 at 240, 2.48 at 480, 1.15 at 960. Under the five-period moving average, which the plug-in reads as an autoregression at 0.8, it is 0.43 at 120, -1.72 at 240, -3.01 at 480, -3.77 at 960 — a tie at 120 rows and a gain that grows with the sample.

A block length chosen from the data

A length read off the whole sequence

The automatic block length reads one number off the sample — the lag-one correlation — and assumes the rest of the dependence is geometric. Reading the whole autocovariance sequence instead removes the assumption and puts the length where the law wants it. At a hundred and twenty rows it buys nothing, even where the assumption is wrong; it costs 3.87 points where the assumption is right, and by 960 rows that premium is 1.15 and the payout under a law the plug-in misreads is 3.77. Under long memory neither rule, nor the best length on each draw, gets within ninety per cent.

Every pair of sieve orders. Each cell is a tuning list of exactly two sieve orders, the row's and the column's, and its shade is how often fifteen candidate regressions choose different values from it, at a true null over 240 draws. Every pair holding order zero disagrees on no draw at all, because the criterion never picks zero under this law. Every adjacent pair of positive orders disagrees on between 17% and 25% of draws — 22.1% for one and two, 25.0% for eleven and twelve — and the rate falls as the two orders move apart, to 5.0% for one and twelve. The largest cell is 25.0%.

How long the list is

Two values the criterion cannot tell apart

Fifteen candidates disagree about a whitening's order on two draws in five when the list holds all thirteen orders — and on more than one in five when it holds only one and two. Every adjacent pair of positive orders disagrees about as often as that pair does, and every pair holding an order the criterion never picks disagrees on none. A list's disagreement is set by the pairs of values on it that the criterion cannot tell apart, not by how many values it has, and one candidate's own doubt about its pick predicts all fifteen candidates' disagreement with a rank correlation of 0.96.

Two searches over different features

The overlap at the critical value

Two searches over independent noise columns are additive on average: the joint search finds what the two find separately, to within a fortieth of the smaller. At the point a test actually uses — the joint statistic's 95% quantile — the same pair overlaps by 0.320, and a rule that adds the two searches' own critical values rejects 1.4% of true nulls instead of 5%. Nothing about the searches causes it. Quantiles of a sum do not add, and on every pair in the field the overlap at the critical value is larger than the overlap the field measured.

Two searches over one sample

A break that is there

Put a real break in the regression at row 60 and the profile's two-unit set still misses it on most draws — it contains the true row on 12% of draws at a small break and 69% at a large one, without whitening; with the window searched as well, 23% to 75%. A set that would contain it on 95% of draws needs a threshold of about 19 units without whitening and about 8.5 with it, and either honest set holds most of the sample: fifty-seven of the seventy-three candidate rows at a break of one standard deviation. Searching the window does not move where the break is found.

$Projection as a dial. Each probe projected a fraction λ of the way off the span of the rule's balanced columns, over the 100 designs of 200 whose admissible set is enumerated to be split; the median separation — the two components' difference in mean probe value over the spread inside a component. the separating direction: 10.565 at 0, 11.500 at 0.25, 11.456 at 0.4, 11.424 at 0.5, 11.240 at 0.6, 10.664 at 0.75, 10.427 at 0.9, 10.273 at 1; the design's leverage: 4.537 at 0, 4.845 at 0.25, 4.924 at 0.4, 4.849 at 0.5, 4.678 at 0.6, 4.417 at 0.75, 4.205 at 0.9, 3.836 at 1; the fourth power: 1.543 at 0, 1.846 at 0.25, 2.094 at 0.4, 2.570 at 0.5, 2.870 at 0.6, 3.686 at 0.75, 4.579 at 0.9, 5.080 at 1.$ A probe chosen rather than picked

How far to project

The field's repair for a probe is to project it off the span the balancing rule already pinned. Treated as a dial rather than a switch, that repair is right all the way for the fourth power — its separation rises from 1.543 unprojected to 5.080 fully projected — and wrong for the design's own leverage, which carries 4.537 unprojected, 4.924 at four tenths of the way and only 3.836 projected fully. The leverage probe the field recommended was a third of the way past its best. Even the separating direction itself gains a little from a partial projection and loses a little from a full one.

The rate and the size of a disagreement

What a longer sample settles

At a hundred and twenty rows, letting each candidate choose its own whitening changes which of fifteen candidates wins on about an eighth of draws, whatever the list, the table or the law. At four hundred and eighty rows it changes the winner on 1.0% of draws for a window and 2.3% for an order, and at nine hundred and sixty on a quarter of one per cent. The sample settles it through one factor only: how often the candidates disagree about the tuning value hardly moves, and the share of their disagreements that change the winner collapses.

What a lag of band costs, as the sample grows. The optimism one more lag of a Bartlett band adds, measured by fitting on one sample and scoring on an independent one, 2,400 pairs at each size, with two standard errors: 0.3745 ± 0.0176 at 120 rows, 0.3842 ± 0.0266 at 240 rows, 0.4523 ± 0.0392 at 480 rows, 0.4022 ± 0.0563 at 960 rows. The window's summed weights give one half a lag and the convention charges one.

A charge for a covariance's own dimension

The charge at four times the sample

A band of lags is charged a full unit apiece and is worth about three eighths of one at a hundred and twenty rows. The field's last essay said the error in that convention was harmless only because the error surface is flat, and that a steeper surface would give it a cost. A longer sample was the obvious place for one. It is not there: from 120 rows to 480 the error's spread across band widths falls by three quarters, and the derived charge's advantage over the convention falls from 5.5 standard errors to 1.7. What the sample does move is the charge itself, from 0.37 of a unit a lag towards the half a unit the window's weights predict.

The table swept along the covariate instead. What a rule holding a mean of each covariate fails to remove of their interaction, at each of 4 copulas, as the covariate is skewed further and the rank correlation is held at 0.4. The sweep runs from a symmetric covariate at g = 0 to a skewness of 11.16, and the three settings the earlier table names — g = 0.3, 0.6 and 0.9 — are on it, where this sweep reproduces that table to the last digit. Every row rises and then falls: the lower-tail copula from 7.707% through 0.0015% and back to 5.587%, the upper-tail one to a maximum of 36.213%. So the quantity a trial is exposed to is not monotone in how skewed its covariate is.

The same table at seven correlations

The other dial

The table is swept along the strength of the dependence and never along the shape of the covariate. Swept along the shape at a fixed correlation, the same two copulas cross, the same way — and the near-zero cell turns out to be a minimum in both directions at once.

Where the bias lands. The drift in the log variance ratio, fitted across 12 blocks over 4000 trials. E[log λ̂_b] is log λ_b plus ψ(k_B/2) − log(k_B/2) − ψ(k_A/2) + log(k_A/2), which depends on nothing but the degrees of freedom — so the tempting sentence is that it goes into the intercept and leaves the slope alone. It does not, because the blocks alternate between allocations and the alternation is correlated with the covariate being fitted: the lopsided blocks carry 0.5383 of bias and the even ones carry none. Uncorrected the slope reads 1.5597 against a truth of 1.5, which is 8.0 standard errors. Subtracting the two digammas block by block leaves 1.4976.

What a block may vary

The bias that lands in the slope

The bias in a log variance estimate depends on nothing but its degrees of freedom, so it goes into the intercept — unless the degrees of freedom alternate with the design, which is exactly what a block-randomised trial makes them do.

The ceiling a multiplier cannot reach past. A wild-type resampling forms e*_t = e_t·w_t with the multiplier independent of the residual, so what comes out has autocovariance γ_resid(k)·γ_w(k) — the residuals' own, multiplied by the multiplier's. Since |γ_w| ≤ 1 the reference distribution's dependence is bounded above by the residuals', and the residuals' is already below the errors'. The two shortfalls compose. For a block of ℓ the multiplier's autocorrelation is exactly the triangle (1 − k/ℓ)⁺, drawn here as the dashed prediction against the realised resamples at ℓ = 5; the bound is attained only at ℓ = n, where the reference distribution is built from one sign.

Counting what is independent

What a multiplier cannot keep

Two reasons were named for the quarter a blocked resampling falls short, and taking either away makes the gap larger. What is left is a bound — a multiplier can only take dependence out, and the residuals' own is already below the errors'.

Where the bootstrap works and where it does not. Uniform data on [0, 1]. For the mean the percentile bootstrap covers 93.5%. For the maximum it covers 0.0%, because a resample can never contain a value larger than the largest one observed, so the interval cannot reach above it.

Intervals, counted

Where the bootstrap lies

Resampling is the most generally useful trick in the subject and it has a failure mode that is easy to state: it cannot see past the data. For a statistic that lives at the edge of the sample, coverage collapses from 95% to almost nothing.

A probe from what the rule blocks

A set of pairs, not a vector

The active set is a graph on the units, and every probe built from it so far has been its degree. Read as a graph it recovers 0.1326 of the alignment the summary lost — and draws level with leverage rather than passing it.

A charge that is not a straight line

What the correction assumes

A correction with nothing fitted in it repairs one window of four. The reason is that its size is set by where a window puts its weight and the curvature it must repair is set by something else — and for one window at one sample size the two happen to agree.

The tail past the last observation

Two intervals for one return level

Two 95% intervals read off the same fits of the same records, against a level known in closed form. The symmetric one covers 80.3% at twenty-five blocks and reaches only 89.0% at two hundred — and 99.24% of its misses are the interval sitting entirely below the truth, which is not the endpoint anybody expects to fail.

$The damage does not stay in the term that was left out. Where each coefficient lands when the model that fills the missing outcomes and the model that analyses them disagree, over 1500 studies of 200 rows at 35.0% missing and 20 imputations. An imputer that omits a covariate the analysis fits attenuates that covariate's coefficient by exactly the missing fraction — -0.1405 counted against a closed -0.1400 — and pushes the coefficient it did impute on the other way by exactly the product of the omitted coefficient, the covariates' correlation and the missing fraction: 0.0402 counted against 0.0420. Both closed forms come out of the same two-by-two solve. Matching models leave both alone, and so does an imputer that knows more than the analysis.$ The value that is not there

An imputation model the analysis does not contain

A model that fills the gaps without a covariate the analysis fits attenuates that covariate's coefficient by exactly the missing share, 0.4 to 0.26, and moves the one it did carry by exactly γρf, 0.6 to 0.642. The reverse case is supposed to inflate the interval, and at four strengths of the extra knowledge it does not.

The same error, caught or invisible, by how it is arranged. The overidentification test's rejection rate against the error the violation actually puts into the estimate, so the two rows are the same estimate being equally wrong. With the whole violation on one instrument the test keeps its size at 5.0% under the null and reaches 86.4% by an error of 0.800. With both instruments violating in the same ratio as their first stages the two Wald ratios are identical, the test has nothing to compare, and it rejects at 5.8% at that same error — its own size. Over 1000 draws of 300 rows at each setting, at a nominal 5.0%. The test is a comparison between instruments and it was never a check on either.

A variable that moves one thing only

Two instruments that disagree

The overidentification test keeps its size at 5.0% and reaches 86.4% power against a violation carried by one instrument. Against the same error carried by both in proportion to their first stages it rejects on 4.6% of draws — its own size — while the estimate is wrong by 0.3000, which is 94.2% of the confounding the instruments were brought in to remove.

What a scale that grows across the sample costs. What the interval covers when the noise scale grows across the sample, against how far the departure has gone, over 1500 draws at each setting. The coverage runs from 94.47% at no departure to 83.93% at the end of the sweep, a loss of 11.07%. The rank argument needs the 200 calibration scores and the test score to be exchangeable, and this is one of the three ways that fails. A test built for it reaches 80% power at 4.054, where the coverage is 85.13% — so 9.87% of the loss is inside the region such a test would have missed.

Coverage without a distribution

When the order matters

Three ways of breaking exchangeability cost 4.93, 11.07 and 1.07 points of coverage, and the ordering by cost is the reverse of the ordering by how soon a test would have caught them. The departure practitioners check for is the cheapest one.

The price of insurance is noise, not coverage. What a robust standard error costs under a constant error variance — the case where the model-based one is exactly right — at five sample sizes over 20000 draws at the small end. It is not coverage: the leave-one-out interval read against a t on n − 2 covers 95.52% at 20 rows against the model-based 95.06%. It is a wider interval, by a factor of 1.0689 at 20 rows falling to 1.0049 at 250, and it is a variance estimate 2.57 times as variable at 20 rows and 1.85 times at 250 — against a denominator that is exactly V²·2/(n − 2), so only the numerator is counted. The uncorrected estimate is the cheaper of the two at small samples and the dearer at large: 1.31 against 1.76.

A standard error for a model that is wrong

Right for the wrong reason

A robust standard error costs no coverage where the risk is absent — 95.52% against 95.06% at twenty rows. It costs a 6.89% wider interval and a variance estimate 2.572 times as variable, and the pre-test that would avoid paying recovers 15.9% of what the insurance is worth.

Tests, and the second number

The p-value a replication gets

Under a true null a p-value is flat. Under a real effect its distribution is closed form and wide — a study with 80% power returns anything from 4.4×10⁻⁵ to 0.13 in eight runs of ten — and the chance that an exact replication of a p = 0.05 result is significant again is exactly one half, under both of the models people use without naming them.

Two far rows, and the line with one of them deleted. Twenty clean points and two rows near x = 9. The slope is −0.511 with every row, −0.376 with one far row deleted, and 0.495 with both deleted. Deleting one of them barely moves the line, because the other is still there.

Regression, and what the summary hides

Two points that hide each other

One far observation among twenty-one has a Cook's distance of 24.1. Put a second beside it and the two read 0.966 and 0.772, neither crossing 1, while together they reverse the slope and deleting both moves the fit by 53.3.

A cohort screened once, the top tenth enrolled, and followed up with nothing given — correlation 0.6. 2000 people read once at screening and once at follow-up, with a test–retest correlation of 0.6 and no treatment. The 215 above a cut at the top ten per cent of one reading (1.282 standard deviations) are enrolled. Their mean screening reading is 1.744 and their mean follow-up reading 0.982, a fall of 0.762 ± 0.055 with nothing done to anyone. The closed form for the fall is (1 − ρ) times the truncated-normal mean, (1 − 0.6) × 1.755 = 0.702.

Reversals that are not errors

The measurement that got them enrolled

Enrol the top tenth of one screening reading and give them nothing, and they fall by 0.702 standard deviations at follow-up. Measured from a fresh reading taken after enrolment they fall by nothing. Averaging ten screening readings still leaves 0.101, and it takes twenty-one to get under 0.05.

The risk of one cause, estimated two ways. Two causes of an ending event with constant hazards 0.2 (the one of interest) and 0.3 (the competitor), random dropout at 0.1 and follow-up to 6. The lower line is the cumulative incidence, (0.2/0.5)(1 − e^(−0.5t)), the chance of actually having had this event by t; the dots on it are the Aalen–Johansen estimate over 2000 studies of 300, 0.3670 at t = 5 against 0.3672. The upper line is 1 − e^(−0.2t), and the dots on it are one minus Kaplan–Meier with the competing event treated as censoring: 0.6318 at t = 5 against 0.6321. The second is larger by a factor of 1.722 at t = 5, and it is not an error of estimation. It estimates, correctly, the risk in a population where the competing cause does not exist.

When the data stops early

One minus Kaplan–Meier is not a risk

With two ways for observation to end, one minus Kaplan–Meier for one cause reads 0.6318 at t = 5 where the chance of actually having had that event is 0.3670. Added across the two causes, the complements reach 1.4088 — more than the whole cohort. Nothing is estimated badly: the complement estimates, correctly, the risk in a world where the other cause does not exist.

Estimating a weight you already know is worth doing. The variance of an inverse-probability estimate weighted by a propensity fitted from the sample, over the variance of the same estimate weighted by the true propensity, paired on the same 500 samples of 600 units at each of five settings. Every reading is below one: the stabilised estimator keeps 27.8% of its true-weight variance where the assignment is nearly a coin toss and 72.0% where it is nearly decidable, and the unstabilised one 30.0% and 49.3%. Neither estimator is materially biased, so this is a variance rather than a trade. The true weights are right about the population and know nothing about the draw; the fitted weights are the value that sets this draw's own imbalance to zero, and that imbalance was what the variance was made of.

Weighting one sample into another

The estimated weight is the better one

The propensity is known exactly here, so it can be weighted by — and estimating it from the same data and weighting by that gives a variance ratio of 0.4769 on paired draws. The reason is a projection: the draw's own imbalance explains 56.33% of the true-weight variance and 0.05% of the estimated-weight one.

The squared estimate 1 standard errors from the flat point, exact and linearised. At δ = √n·μ/σ = 1 the exact law of the squared estimate has mean 2.00, variance 6.00 and skewness 2.177; the delta method's normal has mean 1.00, variance 4.00, no skewness, and 30.85% of its mass below zero, where a square cannot go. The Kolmogorov distance between them is 0.3085.

The distribution itself

Where the derivative is zero

The delta method reads a standard error off a tangent line, and at a flat point the tangent says the spread is zero. The interval built on it for a squared mean covers 99.991% there and 85.978% one and a half standard errors away, with nearly every miss on the same side — and the law it should have used is a χ², not a normal.

Corrections, and what each controls

Estimating how many nulls are true

Benjamini–Hochberg at 5% delivers 2.55% when half of twenty nulls are false, because it cannot tell how many are. Storey's estimate of that share, read off the p-values above one half, spends the rest and finds 81.93% of the real effects instead of 74.70% on independent tests. Correlated at 0.9, the same procedure reports a finding in 19.29% of families in which every null is true.

Four intervals at 3 blocks of 32 rows. What four 95% intervals for the mean of a first-order autoregression at 0.7 cover, and how wide they are on average, at 120 rows cut into 3 whole blocks of 32, over 240 draws with 200 resamples each under the rectangle. The normal interval, the block-means variance with 1.96, covers 82.1% at a width of 0.708. The percentile interval covers 82.1% at 0.632 and the studentised one 90.4% at 2.495. The fourth resamples nothing: it is the normal interval with 1.96 replaced by Student's t on 2 degrees of freedom, and it covers 94.2% at 1.555, 0.62 times the studentised interval's width.

The interval, studentised

The interval with no resampling in it

Replace 1.96 in a normal interval on the block-means variance with Student's t on one fewer degrees of freedom than there are whole blocks, and resample nothing. Across twenty-four cells it covers at least as often as the studentised bootstrap interval at every one, by 0.42 to 10.42 points; it is narrower wherever seven blocks or fewer are left; and at fifteen blocks of 32 it covers 95.0%, which no resampled interval on the grid reaches.

Two 95% intervals for 2 of 20, under Jeffreys — Beta(½, ½). The equal-tailed interval runs from 0.0214 to 0.2839 and is 0.2625 wide; the shortest interval runs from 0.0093 to 0.2540 and is 0.2447 wide. Both hold 95% of the posterior, and the shorter one buys its 6.8% by moving its lower endpoint towards the denser side.

The prior, doing visible work

The shortest interval, and the one that does not move

Two 95% intervals come out of every posterior and they are not the same set. The shorter one is shorter by 4.86% on average and 22.41% at its best, it covers 86.72% where the other covers 95.68%, and it is not even the shortest once the parameter is written a different way.

What each estimator costs, against how many groups there are. Each point is 4,000 datasets, with the population spread estimated from the data rather than supplied. Partial pooling first beats BOTH of the estimators it sits between at 5 groups; below that, complete pooling — which estimates nothing at all — is the better answer. Its own cost falls from 1.751 at 2 groups to 0.795 at 40.

Groups that borrow

The fewest groups that can borrow

At three groups the estimator that shrinks towards its own data's mean returns the group means untouched, on every dataset, because its constant is J − 3. At two it expands instead of shrinking. And the number of groups at which partial pooling starts to be worth doing is five, or two, or never — it depends on how far apart the groups are.

The average decay factor each route produces, φ = 0.85, 6 steps ahead. The truth is φ^6 = 0.3771. no correction averages 0.2616 with a spread of 0.1646 and a squared forecast error of 3.2516; the formula, on the persistence averages 0.4213 with a spread of 0.2528 and a squared forecast error of 3.4827; the bootstrap, on the persistence averages 0.4355 with a spread of 0.2655 and a squared forecast error of 3.5120; the bootstrap, on the decay factor averages 0.3375 with a spread of 0.2278 and a squared forecast error of 3.4132. 800 series, 100 bootstrap refits each.

Comparing two forecasters

Correcting the forecast instead

The complaint against the usual repair is that a correction aimed at the persistence lands on the wrong quantity. Aiming it at the decay factor the forecast actually uses fixes exactly that — the error stops compounding with the horizon, 69.7% becomes 9.5% at twelve steps — and the forecast still gets worse.

What visiting fewer settings costs, 6 parameters. Carathéodory's bound puts the support of an optimal measure between 6 and 21. 6 settings: D-efficiency 88.90%, G-efficiency 57.18%, 0 degrees of freedom for lack of fit; 7 settings: D-efficiency 94.54%, G-efficiency 61.22%, 1 degrees of freedom for lack of fit; 8 settings: D-efficiency 95.99%, G-efficiency 64.60%, 2 degrees of freedom for lack of fit; 9 settings: D-efficiency 97.40%, G-efficiency 82.76%, 3 degrees of freedom for lack of fit. The saturated design has none, and buying the first one costs about five points of efficiency to get back.

A design chosen rather than looked up

How many places a design goes

Carathéodory's bound puts an optimal design's support between six and twenty-one settings, and every design in this field that can fit the model visits exactly nine. The count is not a choice anybody makes, it decides how many degrees of freedom are left to check the model with, and the first spare setting costs six points of efficiency to get back.

What the fit calls the shape, against what it is. One eigenvalue held at −3 and the other swept from −2 to 2, so the truth is a maximum on the left and a saddle on the right and the change happens at exactly zero. At an eigenvalue of −0.25 — a genuine maximum — the fit reports a saddle on 26.4% of studies; at +0.25 — a genuine saddle — it reports a maximum on 25.1%. The standard error of a squared coefficient under this design is 0.3791, and the region of confusion is about that wide either side of zero.

The surface between the corners

The sign the curvature has

A fitted surface reports a maximum, a minimum or a saddle, and the report is a comparison of two estimated eigenvalues against zero. At a true second eigenvalue of −0.25 the fit calls a genuine maximum a saddle on 26.4% of studies, and at +0.25 it calls a genuine saddle a maximum on 25.1%.

What 240 observations are worth, by which question is asked. 8 rows and 10 columns with 3 observations in each cell — 240 in all, each belonging to one row and one column, neither nested in the other. the overall mean: variance 0.1703 against a naive 0.0060, a design effect of 28.4 and 8.5 effective observations; a difference between two rows: variance 2.0682 against a naive 0.0960, a design effect of 21.5 and 11.1 effective observations; a difference between two columns: variance 1.0845 against a naive 0.1200, a design effect of 9.0 and 26.6 effective observations.

Hierarchy past one number

Two groupings that cross

Pupils belong to a school and to a neighbourhood, and neither is nested in the other. There is then no design effect: the overall mean is worth 8.5 independent observations out of 240, a row difference 11.1 and a column difference 26.6, and which grouping matters depends on the question rather than on the study.

What the guess is worth, when it is worth anything. The variance cost of an even split relative to the variance-minimising one for a risk difference, against the first arm's proportion, with the second at 0.3. The cost is a pure number: it does not depend on the trial's size. It is exactly zero at 0.3 and at 0.70, where the two arms have the same p(1 − p); it is 0.19% at a half and 4.36% at a tenth. Across the whole range from a tenth to nine tenths it never exceeds 4.36%, which is what the variance-minimising rule is worth here — and what it is worth is the reason it is safe to use with a guess.

Splitting the units

The arm whose variance is its answer

With a binary outcome the allocation rule is a function of the proportions the trial exists to estimate. It costs at most 4.36% of variance to ignore it anywhere between a tenth and nine tenths, because √(p(1−p)) stays within a factor of two of its peak across 98% of the unit interval.

The damage and the warning, against the same dial. Two readings at each persistence. In the darker colour, how often a regression between two independent series of 200 steps is called significant at 5%: 4.9% at φ = 0, 34.2% at 0.8, 52.4% at 0.9, 83.4% at a unit root. In the lighter, how often the standard unit-root test refuses a unit root on one of those series — the chance the analyst is told the series is stationary and may be regressed: 87.2% at φ = 0.9 and 31.9% at 0.95. At φ = 0.9 both are high at once, which is a correct diagnostic licensing a regression that is wrong half the time.

When the observations repeat each other

The cliff that is a slope

A regression between two independent series is called significant 4.9% of the time at no persistence, 52.4% at a lag-one correlation of 0.9, and 83.4% at a unit root. The rule the field offers asks whether the last of those holds, and at 0.9 the unit-root test correctly refuses one 87.2% of the time.

The bounded error and the unbounded one. How the sequential trace procedure's answer is distributed, against the sample length, for a three-series system with 2 genuine relations. Over-counting — claiming a stationary combination that is a random walk — reads 4.9%, 7.2%, 5.7%, 6.2%, 5.9%, 4.2% across the six lengths, never far from the 5% of a single test. Under-counting reads 69.5%, 40.2%, 14.0%, 0.5%, 0.0%, 0.0%. The procedure is described as a 5% rule and the 5% applies to one of those columns.

Three series, and a count

The rank is a decision

The sequential procedure's 5% bounds one of its two errors. Over-counting reads between 4.2% and 7.2% at every sample length from fifty observations to three hundred; under-counting reads 69.5% at fifty and 0.0% at three hundred, and nothing in the procedure bounds it.

An interval read beside something else

A subgroup inside its own trial

A trial with 80% power, significant overall and not in the fifth of it that is women, has told the reader almost nothing about women: that pattern turns up 57.45% of the time when women have the full effect and 58.26% when they have none. The subgroup is part of the whole, so the two verdicts are correlated, and the one test that answers the question — the subgroup against everyone else — can be recovered from the two printed intervals and nothing more.

How often a randomised trial of eighty shows a Simpson reversal on some baseline variable, against how many were tabulated. The treatment helps every patient equally. On one nominated, strongly prognostic variable the reversal appears in 4.1% of trials. Tabulating 2, 5, 10, 20, 50, 100 variables of mixed prognostic value, some variable reverses in 4.1%, 6.5%, 10.8%, 16.1%, 26.1%, 34.1% of trials; stratifying the randomisation on the most prognostic one gives 0.2%, 2.9%, 7.7%, 12.2%, 23.4%, 31.9%.

When the stratified answer and the pooled one disagree

Twenty variables nobody stratified on

A randomised trial of eighty patients in which the treatment helps every patient by the same six points shows Simpson's reversal on one nominated, strongly prognostic baseline variable in 4.07% of trials. Tabulate twenty baseline variables of mixed prognostic value and some variable reverses in 16.07% of trials; a hundred, in 34.13%. Stratifying the randomisation on the strongest variable removes its reversal and leaves 12.17% and 31.93%: the protection is exactly as wide as the list it was given.

The band that allows at most r of the next m observations outside it, 95% of the time, from a sample of ten. At a hundred future observations the band that holds all of them has factor 4.942; allowing one outside, 4.289; two, 3.948; five, 3.378. The tolerance factors for 99% and 95% content are 4.445 and 3.382.

The interval that holds observations, not a mean

A band allowed a few misses

From ten observations, a band holding every one of the next hundred with 95% probability reaches 4.942 sample standard deviations either side of the mean. Allowing one of the hundred outside brings it to 4.289; allowing five, to 3.378 — the 95%-content tolerance factor, 3.382, to within half a hundredth. The tolerance interval turns out to be the limit of a promise about a share of failures. And the misses arrive together: when this band misses once, it misses again 45.4% of the time, where independent misses at the same rate would do so 12.5%.

What four adjusted analyses report about their own precision and what they have, 50 patients an arm, baseline correlated 0.7. Reported against actual variance of the treatment estimate, as shares of the unadjusted analysis's, over 20,000 trials of 50 patients an arm. Adjusted for the baseline as measured: 0.529 reported, 0.518 actual. Median cut fixed in advance: 0.716 and 0.700. The decile cut with the best fit: 0.671 and 0.736. The decile cut with the smallest p-value: 0.762 and 1.615.

What a sample-size calculation was given

The cut that fitted best

A trial that adjusts for its baseline cut at whichever of the sample's nine deciles fits the outcomes best — without ever looking at the treatment difference — reports a variance 0.671 of the unadjusted analysis's where its estimates actually have 0.736, which is worse than the 0.700 a median fixed in advance delivers. The sample says the chosen cut kept 72.4% of what the baseline could remove; the population says it kept less than a median. A true null is rejected 5.87% of the time at fifty patients an arm and 9.31% at ten, and a cut chosen for its p-value rejects 14.22%.

How slow a return each test can see at 200 observations: the relation estimated against the relation supplied. The estimated relation's test reaches 80% power up to a half-life of 5.05 steps and the supplied relation's up to 6.88. At a half-life of 8 the two find the pair 36.3% and 71.9% of the time; at 12, 16.9% and 39.3%. Their 5% points are −3.38 and −2.89.

Series that move together

A relation supplied in advance

When theory supplies the long-run coefficient, the gap between two series can be tested directly and the search the Engle–Granger test pays for disappears: its 5% point moves from −3.38 to −2.89, and at two hundred observations the slowest return found four times in five goes from a half-life of 5.05 steps to 6.88. The price is in what a rejection means. With a gap that halves in three steps, a coefficient a fifth too large is confirmed 99.1% of the time and one half again too large 81.9%, though every such gap contains a random walk — and at a thousand observations the second is confirmed more often, not less.

How often a trial that borrows its control from an earlier one declares a treatment with no effect a success, by the earlier control's drift. Fifty patients an arm, an earlier control of two hundred, a one-sided 2.5% threshold. Without borrowing the rate is 2.5% at every drift. Pooling outright reaches 73.1% at a drift of half a standard deviation. A half-normal prior of scale 0.05 on the between-trial spread peaks at 35.2% and is still at 31.8% at a drift of 1.5; a half-Cauchy of the same scale peaks at 11.0% near a drift of 0.4 and falls back to 3.4%.

The spread, and its own uncertainty

A control borrowed from the last trial

A trial of fifty patients an arm can borrow its control group from an earlier trial of two hundred by treating the two control means as draws from one population with a spread between trials. With two trials there is one difference to learn that spread from, so the prior on it decides how much is borrowed — and its tail decides whether the borrowing stops when the two trials disagree. A half-normal prior of scale 0.05 buys 17.4 points of power and, at a drift of 1.5 standard deviations, still declares a treatment with no effect a success 31.8% of the time. A half-Cauchy of the same scale buys 13.6 points, peaks at 11.0% and falls back to 3.4%.

What a summary of a scatter is a property of

The points a slope rests on

Before any outcome is measured, a regression's design already says how many of its points the slope will rest on: n divided by the covariate's kurtosis, exactly. A hundred points of a normal covariate carry a slope on about 35 of them; a hundred of a lognormal one, on 7.6. The largest leverage follows the same tail — above one half in 15.7% of lognormal designs of a hundred and in none of the normal ones — and on a correct straight line, deleting the single highest-leverage point moves the slope by more than its standard error in 16.3% of lognormal datasets of a hundred and 0.1% of normal ones.

How far each estimate of the small groups sits from their truth, when the size relation is flattening below the median size. The small groups' average true effect is −0.259. Their estimates are off on average by −0.012 (own means), +0.276 (one fitted centre), −0.173 (fitted line in log size), −0.025 (fitted quadratic in log size), −0.003 (the true relation).

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

The relation the table has to estimate

Pooling a league table's groups towards a centre that rises with size repaired the small groups' bias — when the size relation was known. Fitted from the table itself, a straight line in log size loses almost nothing: the small groups' error is 0.750 against 0.719 with the true relation. When the relation bends below the median size, the fitted line extrapolates the large groups' slope into the region where it is barely observed and misplaces the small groups by −0.173 if the relation flattens and +0.264 if it steepens — smaller than one centre's error, of either sign. A quadratic in log size removes nearly all of it, −0.025 and +0.014, and costs 0.025 in error when the relation was straight.

How far three estimates of the chosen arm sit from its true effect, with all eight alike. Eight arms of sixty, the best carried forward with thirty more. Average error: both stages, as published +0.123; stage two alone −0.001; stage one shrunk, then both +0.020. The arms' spread estimates to zero on 57.1% of trials.

Designs that change while they run

Shrinking the arm that was chosen

A trial that carries the best of eight arms forward reports it as better than it is — by +0.123 when the eight arms are alike — and its second stage alone is unbiased but the least accurate of the estimates. Pulling the chosen arm's first stage back towards the eight arms' mean before combining removes most of the bias when the arms are alike (+0.020) and gives the smallest error of any estimate, 0.133 against the published 0.182. When one arm really is ahead by half a standard deviation, the same shrinkage pulls the true winner back towards the losers and understates it by 0.103, with more error than the published estimate. The weight is estimated from eight numbers, and it is right when the selection was noise and wrong when the selection was right.

Coverage against the expected count of the interval whose coin is read from the arrival times. The randomised interval for a Poisson mean, with its coin read from where in the window the events fell, covers exactly 97.5% at every expected count between 0.025 and ln 40 = 3.689 and exactly 95% past it, when a count of zero is given the exact interval's [0, ln 40]; its worst is 95.00%. Given mid-p's [0, ln 20] instead, it falls to 92.50% just past 3.00. Mid-p itself reaches 91.66% at 3.03; the exact interval never falls below 95.62% and averages well above 95%.

A proportion's interval near the boundary, and the coin

The coin a clock supplies

A count observed over a window comes with the times its events arrived, and given the count those times are uniform whatever the rate is — so they are a coin with a continuum of faces at every count from one up. Used to randomise the interval for a Poisson mean, they leave exactly one count without a coin, the count of zero, and what that count is given decides everything: mid-p's limit of ln 20 leaves a hole at 92.5%, and the exact interval's ln 40 is the shortest limit that leaves none, after which the interval covers exactly 97.5% below an expected count of 3.69 and exactly 95% above it.

Both halves of the dependence at once

A median with ties

The median split's interaction zero survives every marginal and every copula, because a split that is on for exactly half the units squares to a constant. A covariate measured on a few levels cannot be split exactly in half: on a five-point scale three in eight units sit on the median, and a rule balancing 'above the median' removes 6.39% of the interaction under a Gaussian copula and 10.06% under one of the two Claytons. The size is set by the share of units on the median, which is the formula's own factor. And a fair coin for the tied units restores the zero exactly, on every copula.

A threshold read along the skew. What a rule balancing a threshold at the value 1 on each covariate's own scale removes of the interaction between the thresholds, against the covariate's skewness, on five copulas at a Spearman rank correlation of 0.4. Gaussian: 16.41% with no skew, 10.07% at a skewness of 11.16; t on four: 22.18% with no skew, 12.11% at a skewness of 11.16; Frank: 13.19% with no skew, 10.14% at a skewness of 11.16; Clayton: 5.33% with no skew, 4.82% at a skewness of 11.16; Clayton turned over: 33.34% with no skew, 17.61% at a skewness of 11.16. Every leak falls, because the value moves towards the median.

The same table at seven correlations

Where the skew puts a threshold

The field read the mean-balancing rule along a sequence of skewness and left the threshold rule — a cut at a fixed value on the covariate's own scale — unread. Read, it turns out to be no new curve. Skewing the scale moves the value 1 from the 84th percentile of the latent covariate to the 74th, and the rule's leak is the copula field's cut sweep read at that quantile: it falls on every copula, from 16.41% to 10.07% under a Gaussian. Whether skew and dependence compound or cancel is then a fact about the slope of each copula's curve, and unlike the mean rule's, no cell changes its answer along the sequence.

Balancing what has no levels

A number read with error

A rule that balances the recorded covariate balances the true one only as far as the recording reaches. At a reliability of 0.8 it leaves 45% of a coin's imbalance in the covariate that drives the outcome, back on the coin's 1/√n rate — and a median split turns out to be a recording with reliability 2/π.

What a guesser gets from less than everything. 1,000 three-arm trials of 150 patients under minimisation on three factors with the preferred arm taken with probability 1, and five investigators guessing each next assignment from different information. Knowing the rule, the factors and every assignment so far: 86.3%. Knowing everything about the patients at their own centre and nothing about the others, and applying the rule's own score to that: 52.8%. Knowing only how many of their own centre's patients went to each arm: 55.5%. Knowing only the trial's arm totals, which a drug-supply system shows anyone who reorders: 54.5%. A guess at random gets 33.3%. The cruder the information, the less the guesser gets — except that the rule's own score, applied to a partial record, does worse than simply counting.

More arms than two

A guesser who sees the totals

The bound on how guessable a three-arm minimisation is assumes an investigator who sees everything. One who sees only the arm totals — what a drug-supply screen shows — names the next arm 54.5% of the time against a chance 33.3%, and manufactures 45% of the full guesser's bias.

The block size as a schedule

How much of the forbidden spread a rule may read

A stopping rule that reads the spread its interval will report breaks the interval. Blend that spread into what the rule reads, a share at a time, and the cost is not proportional to the share — at a tight requirement a rule can read four fifths of it before anything is lost, and the last fifth costs nearly four points.

Choosing what the rule reads

What the ellipse spends its assignments on

Rerandomising on Mahalanobis distance never runs out of assignments, where a box of per-function tolerances does at four functions. But at the same number of admissible assignments it holds the worst named function half as tightly, because it spends its constraint on a combination of the basis nobody named.

A third stage, between the two rules. Four rules for one requirement: a half-width of 0.4 at 95%, which knowing σ would meet with 24.0 observations, after a first stage of 5. Each bar is the mean number of observations as a multiple of that, and the note beside it is the coverage. The two-stage rule spends 2.03× and covers 95.42%, computed exactly. The three-stage rule — a second stage to half of what the first spread asks for, the spread re-read on everything, a third stage to the rest — spends 0.86× and covers 88.42%; given 8.50 more observations in every experiment's last stage it covers 95.00% on 1.20×. The rule that re-estimates after every observation spends 0.88× and covers 90.5% over 4,000 drawn experiments; it is the only row that has to be drawn, because it is the only one whose stopping point shares observations with the mean.

What the design is asked to guarantee

The fifth a third stage never reaches

A three-stage stopping rule keeps the two-stage rule's independence and the sequential rule's budget. With a first stage of five it covers 88.4% — worse than the rule it was meant to repair — because in a fifth of experiments the second stage buys nothing.

The sums, pooled as they are and made independent. Coverage on four designs at a requirement of 0.9, 20,000 runs each, about 3.0, 3.6, 3.4, 3.0 blocks. Refusing the sums: 94.91%, 95.06%, 94.96%, 94.86%. Pooling them as they are: 94.98%, 93.67%, 96.17%, 94.93% — exact at balance, short when the allocation is unbalanced and the same in every block, long when it alternates. Pooling the residualised sums, each block's sum less the part of it its own difference predicts: 94.98%, 95.16%, 95.06%, 94.70%, on every design. Each bar is ±0.31%.

A promise about two arms

The sums made independent

The block sums are a free second copy of a two-arm trial's variance only at balance. With ten and two in every block, pooling them covers 93.67% on four blocks; swap the arms each block and it covers 96.17%. Take from each sum the part its own difference predicts and the copy is independent at every allocation.

What a dictionary buys and what it costs

Two functions a covariate

Every constraint costs admissible assignments at the same rate, so the decision a trial faces is a budget: which two functions of each covariate. Over twenty-eight pairs the worst case never picks the mean. At a correlation of a half it picks the square with a cut at one, beating the mean and the square by sixteen hundredths of a point on a floor held by a shape no pair removes a tenth of — and giving up 41% of a linear outcome to do it. Over the 127 lists of shapes a designer could write, twenty-three different pairs are best somewhere.

The shape the covariate enters by

How many functions a trial can hold

A rule that reads more functions of one covariate protects more shapes, and every function it reads costs the shapes it already held: the imbalance it leaves in a linear outcome falls like one over the trial size, with a constant that runs from about 3 for one function to about 16 for six. At fifty units that cost eats the protection, and the worst case over four shapes sits between 37% and 42% of a coin's from two functions to six. At four hundred it falls from 42% to 6%. By six functions the worst shape, at every size, is one the rule is reading.

A block, weighted inside itself

A share read off the sample

A block length chosen for an interval's coverage needs the share of the mean's variance the scale will find, and the published rule reads it from a first-order autoregression at the sample's lag-one value. Reading it from the sample's own autocovariances instead was supposed to survive series nobody had modelled. At 120 rows it covers 92.5% to 93.5% on all four laws — worse than the wrong shape on every one — because a centred series' autocovariances sum to exactly zero and the share they imply is too generous; read to lag forty it covers 84%. The assumed shape costs width, not coverage: 17% too wide where dependence stops at lag four, and nothing visible under a break, where the interval covers for a reason the share knows nothing about.

Searching among fitted models

One test for eight nulls

A combination of eight forecasts can be tested against its parts one comparison at a time or all at once. All at once is a Wald test on the vector of eight encompassing means — which has seven degrees of freedom, not eight, because the means sum to zero on every origin when weighted by the combination. On sixty origins it rejects a true null 26.6% of the time, Hotelling's correction brings that to 15.1%, and handed its own true critical value it is less powerful than Bonferroni over the largest of the eight against both wrong combinations measured: 12% against 18%, and 47% against 96%.

Four intervals for the effect, minimisation at p = 0.8, 120 patients. Under minimisation at p = 0.8, 120 patients, over 600 trials with an additive effect of 0.45 and 199 re-run allocations per trial, the average width of four 95% intervals for the effect, and how often each covers it: unadjusted t interval 1.229 wide, covering 99.7%; unadjusted, test inverted 0.816 wide, covering 95.3%; adjusted t interval 0.723 wide, covering 96.0%; adjusted, test inverted 0.722 wide, covering 96.2%.

Balancing on what was recorded first

The interval the test inverts to

A randomisation test of no effect becomes an interval for the effect by testing every value at once: subtract the hypothesised effect from the treated outcomes and ask the same question again. Because the rule reads only covariates, one set of re-run allocations answers every value. Under minimisation the unadjusted t interval covers 99.7% at a width of 1.229; the inverted test of the same unadjusted difference covers 95.3% at 0.816, a third narrower, with no model of the outcome. Under complete randomisation the two are the same interval — which is what says the third was the rule's.

A search with no fixed point

The displacement on a heavy tail

A correct candidate with one more parameter is behind out of sample by a closed-form amount, and the closed form rests on one Gaussian fact: the expected leverage of a fresh row is q/(R − q − 1). On predictors that are not Gaussian it becomes whatever the leverage is, and two routes that share no arithmetic agree on what that is. With a finite fourth moment it barely moves — 1.5% more per parameter at eight degrees of freedom, 4.5% at five, 7.3% on an exponential. At three degrees of freedom it is 28% more, and the estimate of it will not settle: four batches of twenty thousand draws disagree by more than a quarter.

What the two-regime residue was made of, persistent first. Under a break in the persistence at row 60 of 120 (0.95 then 0.65), the selection regret of six whitenings over 200 draws: restart, unscaled, residual persistences 0.04043; restart, unscaled, persistences given 0.03488; restart, unscaled, fitted with the line 0.03466; the law's recursion, residual persistences 0.03856; the law's recursion, fitted with the line 0.01640; the law's own covariance 0.01579. The whitening that restarts at the break and does not rescale its two regimes gives up 0.01910 against the oracle even when it is given the true persistences; the law's recursion, which divides each row by its regime's innovation scale and continues across the break, is the oracle when given them and within 0.00061 of it when they are fitted with the regression.

The shape a dependence has

The residue was the weights

A regression whose errors change persistence at a known row was whitened as two autoregressions and still gave up 0.0246 against the law's own covariance. That residue was put down to estimating the two persistences from residuals, and the repair named was to fit them with the line. Fitting them with the line moves the persistent regime's estimate from 0.81 to 0.89 and recovers a fifth of the residue — exactly what being told the true persistences recovers. The rest was the transform: it never divided the two regimes by their own innovation scales, which differ sixfold. The law's own recursion, told the persistences, is the oracle to machine precision; fitted with the line, it estimates the persistent one at 0.945 and comes within 0.0006 of the oracle.

Where a taper's case begins

A model against a window

A block resample's long-run variance is attenuated by its window, and the construction that escapes the window is a model: fit an autoregression and sum its dependence to every lag in closed form. Measured on both halves of the answer, the escape is narrower than it looks. Correctly specified, on 120 rows of a first-order autoregression, the model's error is 45.5% of the truth against the trapezoid block's 42.4% — it removes the bias and buys a spread larger than the bias was — and it pulls ahead only from about 480 rows. Wrongly specified, on a five-period moving average, it is off by 84% to 105% at every length, and even an order chosen by the criterion trails the window throughout.

What the procedure may not read

A variance that follows the response

Every design for the two-rate compartmental model assumed the same noise at every sampling time. Let the noise grow with the response, as a combined additive and proportional error does, and the design for the slow rate runs to the tail of the curve, where the response and so the noise are smallest: at three additive standard deviations of proportional error at the peak, the constant-noise design is worth two thirds of the right one. The earlier essay expected a weight function to break the model's scale invariance. A variance that follows the response leaves it exact to six decimals; only one that follows the clock breaks it. And tailoring the design to the noise makes it more fragile to the rates: its worst case over the rectangle falls from 9.2% to 3.3%.

The observation that has not happened

Shocks that are not normal

Every forecast interval in this field reads a normal quantile, and every series it was scored on had normal shocks. Give a first-order autoregression shocks with heavy tails and the 95% interval still covers about 95%; its 99% interval covers 98.2%. Give it skewed shocks and the 95% interval covers 94.8% one step ahead with every miss on one side — 0.0% below, 5.2% above — and the horizon does not repair it: twelve steps ahead the misses are still 0.0% below and 4.9% above, because a persistence of 0.7 keeps the error's skewness at 1.11 however far out the forecast goes. A two-sided coverage count cannot see any of this.

When the two are not independent

The share a sample removes

A rule balancing eight main effects of two independent covariates removes exactly none of their interaction — in the population. A trial is a sample, and in a sample of a hundred units exact balance on the same eight functions removes 24% of the interaction's variance on average, between 10% and 42% from one trial to the next. At twenty-five units it removes 62%. The zero is the centre of nothing: it is the limit the in-sample share falls towards, by about two fifths with every doubling of the trial, carried there by an interaction whose spread grows with the very functions it is regressed on. At a correlation of a half the closed form says 64%; a trial of a hundred gets 69% on average and anything from 53% to 83%.

Six intervals for the white predictor, a five-period moving average. Under a five-period moving average, over 200 regressions of 120 rows with an eight-lag band, how often each 95% interval for the white predictor's coefficient covers it: two-step band, as reported 95.5%; joint fit, as reported 72.0%; joint fit, White's sandwich 71.0%; joint fit, four-lag sandwich 71.0%; joint fit, band maximised again 85.5%; the law's own covariance 92.0%. The bootstrap redraws each regression 24 times from its fitted coefficients and fitted band, maximising the band afresh on every redraw.

A covariance with no parameter

An interval that knows the band was maximised

A regression whose coefficients and eight-lag error band are maximised together prints an interval that covers 72% to 83% where 95% was promised, because it reports nearly the precision of a known covariance and delivers less. Two repairs were named. A sandwich standard error read off the whitened residuals repairs nothing — 71% to 83% — because the maximisation has already made those residuals look independent. A parametric bootstrap that redraws from the fitted band and maximises the band again on every redraw repairs about half the gap, to 85.5% to 89%, by pricing the maximisation through repeating it. What it cannot price is that the band it redraws from is the maximised one.

What decides whether a tuning list decides

The same dial under a second law

On a first-order autoregression, separating the candidates moved the chance that a tuning list changes the winner 2.35 times as far on a whitening window as on a sieve order, and the difference was put down to the step: an integer step is worth a third of a geometric one. Rerun the whole sweep with errors from a five-period moving average and the difference is gone — the probability spans a factor of 5.53 on the window and 5.13 on the order, a ratio of 1.08 — and near the null both lists leave about five and a half candidates within reach, where the autoregression left 3.6 and 1.9. The two factors still point opposite ways under both laws. The step's size was a property of the law the lists were tuned on.

A guarantee that needed a symmetry

A share at a hundred units

On a skewed covariate the closed form credits a rule that balances the means with removing 26% of the covariates' product and 52% of a square, shares that rest on symmetry having failed. A trial does not collect them. At a hundred units the rule removes 12% of the product and 37% of the square on the clearly skewed covariate, and at four hundred units barely more, because the shares live in the long tail and the tail is a handful of units. On the most skewed covariate the rule removes a fifth of the median split at a hundred units and nothing of it at four hundred: balancing the mean of such a covariate is balancing its largest few values.

Scoring a search without spending data

A penalty that counts independent rows

Akaike's penalty charges a fit two error variances a coefficient because each coefficient is fitted from n independent rows. When the design and the errors both persist, a row is worth less than a row, and the honest charge is twice the coefficient's variance inflation. On a hundred and twenty rows at persistence 0.7 that charge is 34.7 against an optimism counted at 34.5, where Akaike's charges 10. Charged it, the criterion's regret at 0.95 falls from 0.128 to 0.032 with the persistences given and to 0.065 when they are read off the sample — and at 0.5, where the charge is right and Akaike's is half of it, Akaike's still selects better.

Power as the recentring's threshold moves. The recentred set test's power at a persistence of 0.65, where one forecaster genuinely beats the benchmark, over 300 draws of 100 origins, as its threshold runs from zero to three times Hansen's. With the eight windows alone: 30.3%, 28.3%, 26.0%, 26.0%, 26.0%, 26.0%. With sixteen stale candidates added: 30.3%, 28.3%, 24.3%, 21.0%, 19.3%, 17.7%. The studentised reality check, which sets nothing aside, has 26.0% and 17.7%.

The best of a set, and what the search costs

The threshold the recentring reads

A recentred set test keeps a candidate at its own mean when the sample has placed it far enough below the benchmark, and how far is a threshold — Hansen's, about 1.75 on a hundred origins, chosen as a rate rather than tuned. Swept from zero to three times that, it is a dial with one side that costs almost nothing. At zero the test finds a genuinely better forecaster 30.3% of the time with or without sixteen stale candidates in the set; at Hansen's threshold it finds it 24.3% of the time with them, and at three times it 17.7%. Its size never passes 3.0%, even where every candidate sits exactly on the boundary.

Paying for a search

The break a shared scale hid

The break searches in this field all maximised a likelihood with one innovation variance for the whole series, and on a break from 0.95 to 0.65 they found it badly: an average of 74.8 where the truth is 60, within twelve rows on 47% of draws, from a profile everyone called flat. Give each regime its own innovation variance — one more parameter, and the one the law actually has — and the same search lands at 61.8 with a spread of 5.8, within twelve rows on 94% of draws, reporting four times the likelihood. The break was never barely there; the likelihood was blind to the half of its evidence that is in the scale. Under no break the extra parameter costs about one and a half units of manufactured likelihood.

A design that assumes less

A bootstrap that repeats the design

After a design that chose its settings from the data, a parametric bootstrap can keep the settings the experiment ran or repeat the whole procedure from the start. On twelve runs repeating it changes coverage by a point at most, because the adaptivity was nearly free. What matters is the interval's shape: the percentile bootstrap covers 90.6%, no better than the Wald interval's 91.3%; the studentised one 93.0%; the profile interval 94.9%. And after a design stuck at a twelvefold wrong guess, the studentised bootstrap — the textbook repair — covers 77.8%, with intervals averaging 54.5 wide for a parameter of 3.

A probe chosen rather than picked

A ceiling that is one unit

The benchmark every probe of a split admissible set was measured against maximised the wrong thing, so the obvious next step was the direction that maximises the separation itself. On 88 of 100 split designs that direction has no finite value: some combination of units reads the same on every assignment of a component. On 83 of them it is a single unit, sitting in one arm across one component and the other arm across the other — and a chain can see a unit that never moves without enumerating anything.

Past the cap, long memory's surface is flat. The prediction error at every band width from four lags to eighty, above the lowest on the extended list, under long memory at d = 4/9 at three sample sizes, 600 draws each. At 120 rows the floor is at 12 lags and eighty is 0.0039 above it. At 480 the floor is at 30 lags and every width from twenty-four to eighty is within 0.0003 of it. At 960 it is at 48 and thirty to eighty lags are within 0.0000. The dashed line is the list's cap: the surface does not rise behind it, it levels off.

A charge for a covariance's own dimension

A cap that decides nothing

Every band-width list this field priced stopped at thirty lags, and long memory at a large sample is the one dependence whose best band wants to be wider. At 960 rows it does: the draw's own best width lies past the cap on 48.7% of draws. Lift the cap to eighty and the measured charge follows, from 28 lags to 46 — and the error moves by two ten-thousandths, in the wrong direction and inside its standard error, because the surface behind the cap is flat. The field's last conditional fails where it had its best chance.

Five length rules, read on two intervals. The coverage of a 95% interval for the mean at the block length each of five rules picks, on the percentile interval and the studentised one built from the same resamples, under a five-period moving average and a first-order autoregression at 120 and 480 rows, 2,000 draws each. moving average at 120: percentile 88.5%, 85.3%, 86.4%, 86.3%, 88.8%; studentised 92.5%, 87.9%, 94.9%, 92.6%, 95.0%. moving average at 480: percentile 90.5%, 90.5%, 90.4%, 91.6%, 91.9%; studentised 91.2%, 91.2%, 94.5%, 93.3%, 95.0%. autoregression at 120: percentile 84.7%, 80.2%, 85.8%, 85.4%, 85.9%; studentised 90.3%, 83.0%, 92.0%, 90.9%, 94.3%. autoregression at 480: percentile 87.0%, 87.0%, 90.0%, 90.5%, 90.9%; studentised 88.6%, 88.6%, 93.0%, 93.0%, 94.2% (in the order eight, from the protocol, n to the one third, the plug-in, the whole sequence, the best on the draw). The rules spread over at most 5.6% on the percentile interval; the interval moves the same rule by up to 8.5%.

A block length chosen from the data

A ranking that belongs to the interval

Five ways of choosing a block length, read on the coverage of the interval each length builds rather than on the variance it implies. On the percentile interval the variance's verdict mostly survives: under a five-period moving average the plug-in and the whole-sequence rule tie at 120 rows and the sequence rule leads at 480. Build a studentised interval from the same resamples and the lead reverses — the plug-in's longer blocks cover 94.5% against 93.3% — because an interval that widens for its own uncertainty is paid for a long block where a percentile interval is punished for one. Under long memory no length and no interval covers two times in three.

When a longer sample settles the tuning list. How often the tuning list changes which candidate the table selects, against the sample size, for the whitening window (solid) and the sieve order (dashed), on three tables of candidates, twelve hundred draws at each size. Every subset of four predictors: window 12.33% at 120, 2.58% at 240, 1.00% at 480, 0.25% at 960; order 10.58% at 120, 6.25% at 240, 2.33% at 480. The nested sequence of four: window 5.83% at 120, 1.25% at 240, 0.67% at 480, 0.25% at 960; order 5.83% at 120, 4.00% at 240, 2.25% at 480. Six subsets of two predictors each: window 11.75% at 120, 3.75% at 240, 5.75% at 480, 2.33% at 960; order 9.42% at 120, 6.67% at 240, 4.42% at 480. The nested table starts at half the full table's rate and reaches a small one a sample size sooner; the table whose candidates all have the same dimension is still changing its winner on one draw in forty-three at 960 rows.

The rate and the size of a disagreement

The table decides when the sample settles it

Letting each candidate regression choose its own whitening changes which candidate wins on about an eighth of draws at 120 rows, and a longer sample settles it — for fifteen nested-and-crossed subsets, at 0.25% by 960 rows. A nested sequence of four candidates gets there a sample size sooner, from half the rate. Six candidates that all hold two predictors never get there: at 960 rows their tuning list still changes the winner on 2.3% of draws, nine times the full table's, because a disagreement among candidates of one size goes on deciding the winner as often at 960 rows as at 240.

Four rules for a break and a column. How often each of four rules says something is there, for the pair of searches over a break and a column, under four truths, 400 draws each under a first-order autoregression at 0.8 with every threshold simulated on 1200 null draws. nothing there: joint, calibrated 6.3%, summed thresholds 6.3%, Bonferroni 6.3%, either, uncorrected 12.0%. a shift from row 60: joint, calibrated 65.3%, summed thresholds 64.0%, Bonferroni 55.0%, either, uncorrected 69.3%. a column enters: joint, calibrated 11.8%, summed thresholds 10.8%, Bonferroni 73.0%, either, uncorrected 82.5%. both: joint, calibrated 70.5%, summed thresholds 69.0%, Bonferroni 75.8%, either, uncorrected 84.8%. The first block is each rule's size.

Two searches over different features

The power a calibration buys

Charging two searches separately makes a joint test conservative, and calibrating the joint statistic on its own null repairs that. Against a real break, on the pair of a break search and a window search, the repair is worth 47 points of power — 62.0% against 14.5%. On the pair of a break search and a column search it is worth nothing, and worse: a real column is found by the calibrated joint test on 11.8% of samples and by a plain Bonferroni split on 73.0%, because a joint statistic takes its threshold from the noisier of its two searches.

What each stopping rule spends. The average number of observations the corner design takes before it stops, with the stopping rule reading pooled within-arm spreads (the upper bar) and each kind of period's own spreads (the lower), at a promised half-width of 0.3, 3,000 trials each. one ratio: 1,656 and 1,649; 2-fold, small blocks noisier: 1,020 and 1,015; 2-fold, large blocks noisier: 2,976 and 2,614; 4-fold, small blocks noisier: 751 and 669; 4-fold, large blocks noisier: 5,642 and 3,368; 8-fold, small blocks noisier: 711 and 490; 8-fold, large blocks noisier: 10,989 and 3,019. With one ratio the two rules are the same rule. With the large blocks noisier the pooled rule over-spends by a factor that grows with the difference, to 3.6 times at eightfold; with the small blocks noisier it over-spends less.

The weights the corner needs

A stopping rule that reads the periods

A fixed-width trial in the corner stops when its estimated precision reaches the promise, and it estimated that precision from spreads pooled across a trial whose two kinds of period need not share a variance ratio. Read each kind of period's own spreads instead and the trial stops on 3,019 observations where it took 10,989, at an eightfold difference, with the interval it reports still covering 95.1%. The stopping time reads nothing but within-arm spreads, per period now as well as pooled, and that is all the exactness needed.

How often each set holds the break. For a shift added to the response from row 60 of 120 on first-order errors at 0.8, 300 samples at each of five sizes and 120 simulations per sample, the coverage of sets for the break row built at a threshold each method supplies. simulated at the truth: 95.0%, 93.7%, 93.7%, 95.0%, 94.0%; estimated break, true persistence: 90.0%, 88.3%, 88.3%, 89.3%, 90.3%; estimated break, persistence matched: 81.0%, 83.3%, 81.3%, 81.3%, 82.3%; estimated break and persistence: 64.0%, 66.0%, 67.7%, 70.7%, 75.7%; a fixed threshold of 21 units: 96.0%, 94.0%, 96.0%, 97.3%, 98.3%; the two-unit set: 12.3%, 19.7%, 35.0%, 49.0%, 66.7%, at shifts of 0.3, 0.6, 1, 1.5, 2. Simulated at the truth the construction is exact; simulated at what one sample can estimate it misses the true row a quarter to a third of the time.

Two searches over one sample

A set calibrated at the estimate

A confidence set for where a regression breaks needs a threshold on the profile likelihood, and no fixed one works: the honest threshold falls as the break grows. Simulating the profile's deficit at the true break, shift and persistence gives a set that covers 93.7% to 95.0% at every break size and narrows from 67 rows to 23. Simulating it at what one sample can estimate gives a set that covers 64% to 76%, and most of the shortfall is one number: a split regression's residuals report a persistence of 0.62 where the errors have 0.8.

A leak read off a cohort, at two cuts. The threshold rule's leak as a cohort of 1,000 units estimates it from its own two-by-two table: the bar is the middle eighty per cent of 600 cohorts' plug-in estimates, the open circle their median and the stroke the true leak, for five copulas at a Spearman rank correlation of 0.4. At the 90th percentile the estimate is centred on the truth and its middle eighty per cent spans about fourteen points: Gaussian 12.8% to 26.4% around 19.2%, t on four 21.5% to 35.7% around 28.9%, Frank 5.4% to 18.7% around 12.2%, Clayton 0.8% to 9.6% around 4.4%, Clayton turned over 35.9% to 49.5% around 43.1%. At the 99th it is not centred on anything: Gaussian 13.1% to 100.0% around 13.7%, t on four 17.5% to 72.9% around 37.4%, Frank 14.4% to 100.0% around 2.2%, Clayton 16.1% to 100.0% around 0.6%, Clayton turned over 37.0% to 75.7% around 56.3%, because on three of the five copulas between two cohorts in five and four in five have nobody past both cuts.

The other half of the dependence

A leak read off a two-by-two table

The share of an interaction a threshold-balancing rule leaves alone needs one number from the data: how often a unit past the cut on one covariate is past it on the other. A cohort of a thousand estimates it to within a dozen points at the 90th percentile. At the 99th most cohorts have an empty cell in their table, and every one of those reads a leak of exactly one hundred per cent — a reading the bootstrap then confirms with an interval of zero width.

When each unit first changed arm. One design of two hundred units, the rule balancing the covariate, its square and a median cut, and a swap-one-pair chain run for 1.6 million steps from a random admissible start, at six tolerances: for each unit, the step at which its arm first differed from the start, the two hundred sorted from first to last. At 1: half the units had moved by step 79, nine in ten by 269, all by 1,073; At 0.6: half the units had moved by step 79, nine in ten by 362, all by 1,073; At 0.4: half the units had moved by step 106, nine in ten by 429, all by 1,593; At 0.3: half the units had moved by step 153, nine in ten by 645, all by 3,878; At 0.22: half the units had moved by step 194, nine in ten by 747, all by 1.1 million; At 0.16: half the units had moved by step 237, nine in ten by 1270, and 1 never moved. The last units to move set the run length a diagnostic built on them needs, and at the tightest tolerance one never does.

What a chain cannot report

A unit that has not moved

At two hundred units the two-chain diagnostic could not settle its own verdict, because its standard error needed a relaxation time the run was too short to estimate. Reading which units moved needs no standard error. Run for 1.6 million steps on five designs, it finds a unit in place in both chains on three designs at the tightest tolerance and one at the next — and every one of them is a unit no swap can move from any admissible assignment, by arithmetic. The admissible set does split at two hundred units, and the split is one extreme unit.

What iterating the band is worth. How much lower the prediction error is when the Bartlett band is iterated to its fixed point than when it is read once off the least-squares residuals, paired on the draw, with two standard errors, 300 draws at 120 rows for each law and window. First-order autoregression: 4 lags 2.84 ± 0.36, 8 lags 3.43 ± 0.58, 20 lags 4.16 ± 0.80; five-period moving average: 4 lags 2.04 ± 0.28, 8 lags 2.69 ± 0.42, 20 lags 4.32 ± 0.68; long memory: 4 lags 0.83 ± 0.14, 8 lags 1.13 ± 0.25, 20 lags 1.33 ± 0.44 thousandths. Every one is below zero by more than two and a half standard errors; the gain is largest at the widest band under the two short-memory laws.

Fitted together, or fitted after

A fixed point with no likelihood under it

A tapered band of autocovariances has no likelihood to maximise, so the one rule that can fit its dependence together with the regression is to iterate: read the band off the residuals, refit, read it again. It converges on every draw, in seven to eleven fits at the median, gives back about half the memory the first fit took out of the residuals under a short-memory law, and lowers prediction error by two to four thousandths — five to eight paired standard errors. Under the law a first-order likelihood describes, its maximum still wins; under the two it does not, the band's fixed point beats it.

How many starts it takes to land in two pieces. Averaged over the split designs at each of three tolerances, the chance that k starting assignments drawn uniformly from the admissible set — what hunting for a start by rejection gives — do not all fall in one component, which is the most any diagnostic built on comparing chains from those starts can detect. At 0.6: 28% with 2, 47% with 4, 63% with 8, 77% with 16, 88% with 32, 95% with 64, 99% with 128. At 0.8: 12% with 2, 21% with 4, 32% with 8, 46% with 16, 62% with 32, 77% with 64, 90% with 128. At 1.0: 4% with 2, 8% with 4, 13% with 8, 21% with 16, 33% with 32, 47% with 64, 64% with 128. The median split design needs 21, 109 and 439 starts at the three tolerances to expose its split with probability 95%. With an even allocation the mirror makes two starts enough whenever the split is a unit.

The diagnostic after the trial

After the mirror is gone

The two-chain diagnostic starts its second chain at the complement of the first's start, which exists only when the arms are equal. At five treated against ten, enumerated on two hundred designs, a split admissible set is one big piece and some crumbs — the median puts 97.3% of its assignments in one component — so two random starts see the split on 12% of split designs and 95% needs a median of 109 starts. Worse, the rule fixes units in a connected set all the time, so a unit that never moves stops being evidence. A hunt that forces such a unit into the other arm finds 41 of 70 splits; 29 carry no unit that marks them.

What a quarrel between two orders costs. Every two-value list of autoregressive orders from one to twelve, read on the same 2400 draws of a first-order autoregression at a hundred and twenty rows: each cell is the average regret of choosing the order per candidate rather than once for the table, on the draws where the fifteen candidates disagree about it. The cost grows away from the diagonal and stays level along it. Next to the diagonal, a quarrel between neighbouring orders costs 0.00126 for one and two and 0.00088 for eleven and twelve; four orders apart it costs 0.00803 and 0.00802; eleven apart, 0.02436. Every list holding order zero is left off because the candidates never disagree about one.

How long the list is

A quarrel's cost is its width

When fifteen candidate regressions disagree about a whitening's autoregressive order, the disagreement costs in proportion to how far apart the two orders are — 0.0027 of regret for every order of distance, a line that explains 96% of the cost across sixty-six pairs — and not at all by which orders they are: a quarrel between eleven and twelve costs what one between one and two costs, though one of those holds the truth. Fitted on pairs, the line predicts every longer list's cost. The window's quarrels follow no such line.

The floor a repair has to choose. Regret of the truncated covariance repaired by flooring its eigenvalues, at a persistence of 0.85 on 120 rows, 120 draws, by floor, on a log scale. Window 4: 1.5649 at 0.001, 0.0945 at 0.01, 0.0385 at 0.05, 0.0285 at 0.1, 0.0226 at 0.2, 0.0235 at 0.4, 0.0292 at 0.7; the taper at the same window 0.0275. Window 8: 1.1919 at 0.001, 0.0980 at 0.01, 0.0334 at 0.05, 0.0258 at 0.1, 0.0197 at 0.2, 0.0209 at 0.4, 0.0249 at 0.7; the taper at the same window 0.0178. Window 12: 0.8692 at 0.001, 0.0621 at 0.01, 0.0239 at 0.05, 0.0209 at 0.1, 0.0212 at 0.2, 0.0239 at 0.4, 0.0282 at 0.7; the taper at the same window 0.0150. Window 20: 1.7110 at 0.001, 0.2495 at 0.01, 0.0399 at 0.05, 0.0238 at 0.1, 0.0202 at 0.2, 0.0219 at 0.4, 0.0259 at 0.7; the taper at the same window 0.0135. Least squares gives up 0.0890 and the whitening told the truth 0.0075.

Estimating the dependence, not naming it

A covariance repaired

A truncated autocovariance sequence fails to be a covariance matrix on most draws of a persistent series, and this line of essays has always scored it on the draws where it survives. The textbook repair is to floor its eigenvalues. At a floor of 0.001 that moves the matrix by four per cent and gives up 1.56 of regret, seventeen times what least squares gives up, because a whitening reads an inverse and an inverse reads the smallest eigenvalues. At a floor of 0.2 it beats the taper at the shortest windows. So the repair is not a repair: it is a second dial.

Student's t on 5 degrees of freedom, against the normal. The two-sided 95% critical value is 2.571 for t(5) and 1.960 for the normal — 31% wider. Using the normal at this sample size makes every interval too short by that much.

Intervals, counted

The correction for not knowing the spread

The t distribution exists because the standard deviation is estimated rather than known. At eight observations, using the normal instead makes every interval 12% too short — and the coverage that follows can be measured rather than argued about.

Reading the draw changes what is charged, not what is tracked. The correlation between the band width each rule picks and the best band width on the same draw, over 400 draws. The three fixed charges read -0.069, -0.066, 0.012. The three that read the sample read -0.012, -0.019, -0.041. None of the six is distinguishable from nothing. The statistic the first plug-in reads does vary — the draw's own summed squared autocorrelation runs from 2.06 to 10.19 with a mean of 4.36 — so the failure is not that the charge stopped moving. It is that what it moves with carries no information about which width this draw wanted.

A charge that is not a straight line

A charge that reads the draw

Three charges built to read the sample track the best band width on their own draw at −0.012, −0.019 and −0.041, deliver more error than the fixed rule they are calibrated to, and pick a width half again as variable. The statistic moves; the answer does not.

The exceedances arrive together. 300 steps of a max-autoregression with dependence 0.75, drawn on a logarithmic scale because its marginal has no variance. The rule marks the 0.9 quantile: 30 of the 300 readings are above it and they fall into 5 clusters, the largest holding 11. The mean cluster holds 6.000, and its reciprocal — 0.167 — is the runs estimator of the extremal index, whose true value for this process is exactly 1 − 0.75 = 0.25. Every threshold method in the collection assumes exceedances are independent pieces of information; here 30 of them are 5.

The tail past the last observation

The clustering the tail has

Every threshold method counts exceedances as though they were independent pieces of information, and in a dependent series they arrive in clusters. Ignoring that overstates a return level by the reciprocal of the extremal index — ×3.527 counted where the mean cluster holds four — and leaves a reported standard error 2.151 times too small.

The rows are held fixed; only the clusters move. Counted coverage of four 95% intervals for a slope, at five cluster counts with the row count held at 300 throughout and a within-cluster correlation of 0.1, over 6000 draws apiece, with the sizes equal. The interval that counts rows covers 53.42% at 5 clusters — a second closed form says 2Φ(z/√D) − 1 = 54.44% for a design effect of 6.900, and reads nothing about clusters at all. The cluster-robust interval read against a normal covers 74.43% there and 94.20% at 100 clusters; read against a t on G − 1 it covers 85.08% and 94.47%. The number of independent things is the cluster count, and every quantity here is blind to how many rows were typed.

A standard error for a model that is wrong

The count that is not the rows

Three hundred rows in five clusters of sixty carry 6.9000 times the variance an independent-rows calculation reports, and the interval that counts rows covers 53.42%. The same five unequal sizes laid out two ways give design effects of 9.3158 and 5.4652.

The two standardised means, and the shape of Fieller's set for their ratio at a = 3, d = 1. Each dot is one pair (zx, zy) drawn around (3, 1). Outside the horizontal band |zy| > 1.96 Fieller's set is a bounded interval, with probability 17.01%; inside the band and outside the disc of radius 1.96 it is everything outside an interval, 75.03%; inside the disc it is the whole line, 7.96%. On 40,000 counted draws Fieller covers ρ = 3.00 95.21% of the time and the delta interval 82.48%.

The distribution itself

A ratio whose interval has to be the whole line

The delta interval for a ratio of two means covers 95.61% when the denominator is eight standard errors from zero and 1.10% at a ten-thousandth of one, and ten times as wide it still covers only 3.48%. Linearising is not the fault. Gleser and Hwang proved that every interval that is always finite fails the same way, so an interval that keeps its promise has to be the whole line some of the time.

One row at x = 9 on a wrong line, fitted three ways. Least squares gives slope −0.389, Huber 0.171 with the extra row at weight 0.115, and least trimmed squares 0.420, fitted to the 12 rows it keeps. The twenty clean rows alone give 0.495. Open circles are the rows the trimmed fit leaves out.

Regression, and what the summary hides

A robust loss and a far x

One far row drags least squares to a slope of −0.389. Huber's loss, the standard robust line, reaches only 0.171, and carried further out the same row gets its full weight back. Least trimmed squares reads 0.420 at every distance, and at the normal model keeps 7.13% of least squares' efficiency to do it.

Three intervals as one strength is spread thinner, at a concentration of 8. Coverage of three nominal 95.0% intervals on the same 1000 draws of 200 rows at each count, when a total concentration parameter of 8 is spread over 1 to 32 instruments. Two-stage least squares covers 97.2%, 96.4%, 94.0%, 86.7%, 73.2%, 51.5%. Building each row's fitted treatment from a first stage that never saw that row covers 97.1%, 97.2%, 98.3%, 97.8%, 97.9%, 98.7%. Limited-information maximum likelihood with its conventional standard error covers 97.2%, 96.7%, 95.7%, 90.9%, 85.2%, 79.0%. At one instrument the likelihood estimator is two-stage least squares exactly, which is why the first readings of those two agree to the last draw.

A variable that moves one thing only

Leaving each row out of its own first stage

Spread a fixed first-stage strength over thirty-two instruments and two-stage least squares covers 51.5%. Build each row's fitted treatment from a first stage that never saw that row and the same draws cover 98.7% — through an interval 5.99 times as wide, around an estimate that misses by more than the whole effect on 34.7% of draws. At eight times the strength the same repair covers 95.3% and costs a width factor of 1.66.

One curve, and two forecasters that are each a single point. The ROC curve of an honest forecaster whose signal has correlation 1 with the latent state — every threshold on its probability, from the bivariate normal — and two forecasters that only ever say 0 or 1. The one an absolute-error score pays for says 1 wherever the honest probability exceeds a half: it has a true-positive rate of 0.6742 and a false-positive rate of 0.1375, and its "curve" is the two straight segments through that point, with area (TPR + TNR)/2 = 0.7684. The honest curve's area is 0.8683. Thresholding at the base rate of 0.3744 instead of at a half gives the largest area any two-valued forecaster can have here, 0.7818, and it is still 0.0866 short.

A forecast that is a probability

The liar with two answers

The forecaster an absolute-error score pays for says only 0 or 1, and on the ROC square it is a single point: its area is (TPR + TNR)/2 = 0.7684, against the honest forecaster's 0.8683, and it falls below the honest one on 200 of 200 counted records. No relabelling of its two answers returns what it threw away — the best recovers a Brier score short of the honest one by exactly the 0.022154 of resolution lost — and below a signal correlation of 0.7332 the same score prefers saying no every time to an honest forecast.

Three ways to reject with two studies, drawn where the two z statistics live. Two one-sided studies, each summarised by its z statistic. Fisher's combination rejects outside a curve that runs parallel to both axes, so one study past z = 2.378 decides it alone; Stouffer's rejects above the straight line z₁ + z₂ = 2.326; Tippett's rejects when either z passes 1.955. Each region holds exactly 5% of the standard bivariate normal — Fisher's in closed form, e^(−c/2)(1 + c/2) at c = 9.488 — and of 100,000 counted null pairs they catch 4.95%, 4.88% and 5.04%. Two alternatives carry the same Stouffer evidence: one study at 2.326 and the other at nothing, where the powers are 62.7%, 50.0% and 65.4%; and both at 1.163, where they are 47.7%, 50.0% and 38.3%.

Tests, and the second number

Two ways to combine p-values

Fisher's and Stouffer's combinations are both exactly right when every null is true, for the single reason that each p-value is flat. Under a real effect they disagree about which evidence counts: with Stouffer held at 50% power across ten studies, Fisher is the more powerful while the signal sits in six or fewer of them and the less powerful from seven.

What each group gains from being pooled, τ = 1. Eight groups whose sizes span a factor of 13.3. The smallest gains 2.076 of squared error, which is 36.8% of the total reduction; the largest gains 0.030, which is 0.5%. 2 of the eight account for half of everything pooling buys.

Groups that borrow

Where the borrowing goes

Pooling cuts the total squared error across eight groups by 56%. Two of the eight take 61% of that reduction, the four best-measured groups share 11% between them, and the largest group gets 1.5% of what the smallest does. The headline is a fact about the groups nobody was asking about.

The Box–Behnken design in three factors: 15 runs, none at a corner. Twelve runs at the midpoints of the cube's edges and 3 at its centre. Every run holds one factor at zero, so no run puts all three factors at an extreme — which is what makes it runnable where a corner is not. The three panels are the design's coordinate projections, with repeated positions marked.

Decided before the data

The design that refuses the corners

Box–Behnken runs three factors in fifteen runs and puts none of them at a corner, which is what makes it usable where a corner cannot be run. It predicts the corner 1.84 times worse than the seventeen-run design that goes there, and 1.31 times worse at the middle of a face, and all three numbers are matrix computations with no simulation in them.

A design chosen rather than looked up

Augmenting a design that has already run

The equivalence theorem still certifies when some runs are already spent, and one number in it changes: the bound is no longer p but (p − λ·tr(M⁻¹M_fixed))/(1 − λ). It equals p again exactly when the runs already made can still be absorbed into the design that would have been chosen — so the certificate says whether the experiment is still recoverable.

The ridge, when the fitted optimum is outside the region. One fitted surface. Its stationary point is at a radius of 2.289 and the fit calls the shape a maximum. The ridge is the best setting at each radius, found by the Lagrange condition (B̂ − μI)x = −ĝ/2; the fitted response rises along it from 59.93 at the centre to 62.10 at the edge. The true optimum is at (0.4, 0.3).

The surface between the corners

When the best setting is outside the region

On a flat surface at twice the noise the fitted optimum lands outside the experimental region on 24.9% of studies and more than three coded units out on 11.8%. The answer is a ridge — the best setting at each radius, with a closed form — and the two obvious rules for using it turn out to be within four per cent of each other.

What a variance estimated from K units is worth. The between-unit mean square is a scaled chi-square on K − 1 degrees of freedom, so the estimator's whole distribution is decided by the number of units. At two units its interquartile range spans a factor of 13.03 and its ten-to-ninety range a factor of 171.3, and it comes out exactly zero on 26.7% of studies. The closed form and 3,000 simulated studies agree to 0.051 at every quantile.

Hierarchy past one number

A level with two units

A variance estimated from two units is a scaled chi-square on one degree of freedom. Its interquartile range spans a factor of thirteen, its ten-to-ninety range a factor of a hundred and seventy-one, and it comes out exactly zero on 26.7% of studies — so the design effect it decides runs from 1.00 to 7.01 against a truth of 4.69.

Four 95% intervals for the odds after 2 of 20. credible, transformed: 0.0218 to 0.3964. Wald, transformed: -0.0305 to 0.3012. delta method on the odds: -0.0512 to 0.2734. delta method on the log-odds: 0.0258 to 0.4789. The first two are the same intervals for the proportion with their endpoints put through the odds; the last two are fresh approximations made on the new scale.

The prior, doing visible work

An interval for something else

An interval for the odds is free — put the endpoints through the odds and the coverage does not move, exactly, for any interval at all. The method everyone uses instead computes a new standard error on the new scale, and at twenty trials that costs four points of coverage, produces negative odds, and has no value at all when nothing was observed.

Six cells, and 5% is the right answer in all of them. How often a regression between two independently generated series is called significant at the 5% level, for two worlds and three treatments, at 200 observations. Every pair is independent by construction, so 5% is correct everywhere and every other reading is a failure. Untreated: 82.9% and 100.0%. With a fitted line removed: 74.2% and 33.5%. Differenced: 5.0% and 5.2%. The treatment that controls the rate in both worlds is the one that discards the level and the trend, which is the quantity a study of trending series was about.

When the observations repeat each other

The repair that keeps the question

A regression between two independent trending series is significant 82.9% of the time on random walks and 100.0% on trend-stationary ones. Subtracting a fitted line leaves 74.2% and 33.5%; differencing leaves 5.0% and 5.2% and throws away the trend the study was about.

Too small breaks it and too large does not. Coverage of the weighted interval against the factor the true likelihood ratio is multiplied by, at a test population 80.0% drawn from the noisier group and 200 calibration points. The exact weight is the factor of 1 and covers 95.70%. Overstating it costs nothing: 96.13% at sixteen times too large. Understating it costs, and costs steeply below about a half — 94.93% at half, 88.37% at an eighth and 67.90% at a thirtieth. The question this answers was whether a wrong weight degrades smoothly or falls off a cliff, and the answer is that it does neither symmetrically: the curve is smooth and one-sided.

Coverage without a distribution

The weight that has to be estimated

A likelihood ratio sixteen times too large costs 5.5% of interval width and no coverage at all; one a thirtieth of the right size covers 67.90%. The estimate from a batch of five unlabelled covariates covers 95.10% against an exact repair's 95.30%, and the binomial says why.

One statistic that is right under both hypotheses. Rejection rates for both statistics under both nulls, at 25% of 150 units treated, with the weak-null readings taken at an effect spread of 3. The difference in means is exact under the sharp null and rejects 22.93% of true weak nulls. The studentised difference is exact under the sharp null — 4.07% — and reads 6.27% under the weak one. The repair is a change of statistic inside the same construction: the same re-randomisations, the same fixed outcomes, a different number compared across them.

The reference distribution the design supplies

A statistic that is exact twice

Dividing the difference in means by its own separate-variance standard error before permuting takes the rejection rate under a true weak null from 20.47% to 6.07%, keeps the exactness under the sharp null at 4.07%, and costs 0.8 points of power against a real effect. At an even split it changes nothing at all, in every draw.

The variance of the baseline-adjusted estimate for four arrangements of visits, against the correlation between visits. At a correlation of 0.5 between visits, the adjusted analysis has 0.750 of the unadjusted variance with one visit before treatment and one after, 0.667 with two before, 0.500 with two after and 0.417 with two of each.

What a sample-size calculation was given

A visit before or a visit after

A trial that can afford one more measurement per patient can take it before treatment, to sharpen the baseline adjustment, or after it, to average the outcome. With every pair of visits correlated 0.5, the second visit after treatment removes a quarter of the variance and the second visit before it removes a twelfth, and it is never the other way round: the baseline's contribution is ρ²(1 − ρ)/(1 + ρ), which peaks at ρ⁵ = 0.090 when ρ is the golden ratio's reciprocal. Below a correlation of one half, a single extra follow-up beats any number of baselines. When the correlation fades with the time between visits, averaging an earlier baseline into the adjustment makes the trial less precise, not more.

How slow a shared return a panel of pairs can see at 200 observations each. The average of the pairs' Engle–Granger statistics, against its own 5% point. One pair reaches 80% power up to a half-life of 5.1 steps, four pairs 9.2, sixteen 15.0. At a half-life of 12 the three find the relation 20.0%, 54.2% and 99.8% of the time.

Series that move together

A slow return across many pairs

One pair of two hundred observations is found tied four times in five only if its gap halves within 5.1 steps. Sixteen independent pairs sharing the same half-life, tested by the average of their Engle–Granger statistics, are found four times in five up to a half-life of 15.0 — and at a half-life of twelve, 99.8% of the time against one pair's 20.0%. What the widened test rejects is a statement about the panel: with half the pairs tied it rejects 55.4% of the time, with a quarter 21.2%, and a pair-by-pair reading of a panel in which all sixteen are tied finds 2.65 of them, against 0.78 when none are.

How often a trial borrowing from 16 earlier trials that agree declares a treatment with no effect a success, by its own control's drift. Fifty patients an arm, each earlier control of two hundred, a one-sided 2.5% threshold. With 16 earlier trials, the half-normal prior peaks at 88.1%, the half-Cauchy at 80.7% near a drift of 0.6, and the half-Cauchy with a fifth of the prior on a vague component at 16.9%. At a drift of 1.5 the three read 73.3%, 25.5% and 3.7%.

The spread, and its own uncertainty

A history that agrees with itself

Borrowing a control from sixteen earlier trials that agree with each other should be safer than borrowing from one, and it is the opposite. Sixteen agreeing trials estimate the spread between trials as small, and a small spread estimated confidently is a licence to pool: under a half-Cauchy prior that let go of a single disagreeing trial, a current control 0.6 standard deviations from a sixteen-trial history turns a treatment with no effect into a success 80.7% of the time, against 10.5% at worst with one earlier trial. Moving a fifth of the prior onto a vague component brings the worst case to 16.9% and keeps power at 91.0%, against 70.5% without borrowing.

Where a thousand validation studies of 100 diseased and 300 healthy put the threshold, at a prevalence of 26%. The best threshold flags 100.0% of healthy people. Reading the study's own operating curve, 7.7% of studies recommend flagging nearly everyone, and the recommended thresholds cost 15.4% more than the best on average; fitting a normal curve to each group's scores first, 47.4% do, at an average excess of 2.5%.

Two tests, a threshold, and the rate they are read against

The threshold a validation study can see

When diseased scores are twice as spread as healthy ones, the harm-minimising threshold jumps near a prevalence of 26% from an interior cut to flagging everyone, because the true operating curve keeps climbing in a tail where few diseased people score. A validation study of a hundred diseased and three hundred healthy cannot see that tail: its own curve reaches 100% sensitivity at its lowest diseased score and goes flat. Just past the jump, only 7.7% of such studies recommend flagging everyone, and their recommended thresholds cause 15.4% more harm than the best on average. Fitting a normal curve to each group first sees the tail: 47.4% of studies then recommend flagging everyone and the excess harm falls to 2.5%. More healthy people in the study change nothing; more diseased people do.

How often a trial of 80 shows a Simpson reversal on its strongest baseline variable, against how many cut points are tried. The treatment helps every patient equally. Cut at its median, the variable's table reverses in 4.4% of trials; trying 2, 3, 5, 9 cuts, in 6.4%, 8.7%, 10.8%, 13.2%. Independent chances would give 33.3% at nine.

When the stratified answer and the pooled one disagree

Five places to cut one variable

A continuous baseline variable has to be cut before it makes a subgroup table, and the cut is chosen. In a randomised trial of eighty where the treatment helps every patient equally, the strongest baseline variable cut at its median shows a Simpson reversal in 4.4% of trials; tried at five candidate cuts, some cut reverses in 10.8%, and at nine, 13.2%. Nine correlated cuts are worth about five independent chances, not nine. Across twenty continuous variables cut at five points each, some table reverses in 32.2% of trials — twice the rate with each variable cut once, and about thirty-one independent chances where the table holds a hundred.

How often a trial whose effect is the same for everyone shows a significant subgroup interaction, by the size of its subgroup table. Four hundred patients, 80% power overall, characteristics whose latents correlate 0 (their split indicators 0.000). Some interaction test reaches 5% in 5.10% at 1, 9.13% at 2, 17.43% at 4, 34.63% at 8, 47.13% at 12, 56.23% at 16; the equicorrelated-normal integral gives 5.00%, 9.75%, 18.55%, 33.66%, 45.96%, 55.99%. A Bonferroni reading of the eight holds 5.57%.

An interval read beside something else

Sixteen subgroups and one effect

A trial of four hundred with 80% power tabulates its result by eight binary characteristics — sixteen subgroups — and the treatment's effect is the same for every patient. Among trials significant overall, 93.5% report at least one subgroup where it is not, and the median one reports seven. Some subgroup-against-the-rest interaction reaches 5% in 34.6% of trials — eight independent chances — and when the characteristics overlap as two age thresholds do, 18.6%, about four. The effective count is set by the correlation between the characteristics' split indicators, (2/π) arcsin of their latent correlation, and a Bonferroni reading of the eight holds the rate at 5% whatever the overlap.

How often a quantile plot's shape test sees a skewed error distribution, on the errors and on residuals of fits of more columns. On the forty errors themselves the test flags 82.9%. On the residuals of fits with 2, 5, 10, 20 columns: 79.1%, 71.4%, 51.2%, 23.0%. On 40 − p errors, which is what losing the fitted columns' worth of observations alone would give: 80.6%, 76.1%, 69.1%, 49.5%.

What a diagnostic plot is showing

Residuals that look too normal

The quantile plot most often read is of a regression's residuals, and residuals look more normal than the errors behind them. Each residual is a mix of all the errors, and the mix moves towards a bell as the fit takes more columns. On forty rows with skewed errors, the straightness test flags 82.9% of samples of the errors themselves, 79.1% of the residuals of a line, 71.4% with five columns, 51.2% with ten and 23.0% with twenty — far below the 49.5% that twenty errors would give, so the fit costs more than the observations it uses. Light tails vanish faster: 73.0% on the errors, 4.7% on twenty-column residuals. The band's level holds at every design, and one point with leverage 0.73 costs almost nothing; what costs is the number of columns.

How many observations a band from a sample's extremes needs to let at most r of the next 100 outside, 95% of the time, for any population. From the sample's smallest and largest: none of the next 100 outside needs 3,850 observations, at most one 637, at most five 107 and at most ten 50. From the second smallest and second largest, 7,750, 1,204, 187 and 85.

The interval that holds observations, not a mean

A range allowed a few misses

Without assuming a shape, the band a sample can offer is its own smallest and largest values, and the number of future draws falling outside it is beta-binomial for every continuous population. A promise that at most one of the next hundred lands outside, with 95% probability, then needs 637 observations; none of the hundred, 3,850; at most five, 107. The normal-theory band keeps the one-in-a-hundred promise from ten. On normal data, at the sizes the range needs, it is only 6% wider than the normal band at the same size — the price of dropping the assumption is paid in observations, not in width — and its misses cluster far less than a band from ten: a second follows a first 19.7% of the time, against 45.4%.

What a summary of a scatter is a property of

A point ordinary on every axis

In a multiple regression each coefficient rests on its own number of points, n divided by the kurtosis of that covariate's residual after the others, exactly. Correlation between normal covariates inflates a coefficient's variance fivefold and leaves it resting on the same third of the points. What correlation does instead is hide the point that decides the coefficient: at a correlation of 0.9 it stands out on no single covariate's plot in 77.3% of designs of a hundred, and the largest leverage a normal design reaches depends on the number of points and covariates and on nothing else.

How far four estimates of the chosen arm sit from its true effect, with one arm ahead by 0.5. Eight arms of sixty, the best carried forward with thirty more, 20,000 trials. Average error: both stages, as published +0.006; shrunk under a normal prior −0.103; shrunk under a t prior, 3 df −0.101; normal prior with a fifth vague −0.073. Root-mean-square error: 0.151, 0.189, 0.192, 0.176.

Designs that change while they run

A prior that lets one arm stand out

Shrinking the chosen arm of eight under a normal prior understates a genuine winner by 0.103. A t prior on three degrees of freedom with the same spread understates it by 0.101 — the tail is too far out to reach a lead of three and a half standard errors. A prior with a fifth of its weight on a vague component understates it by 0.073, costs 0.010 of bias when the arms are alike, and still has more error than the unshrunk estimate. With sixteen arms the same mixture recovers three fifths of the loss, because a bell of fifteen shows its outlier; with eight, the arms put more than half their posterior weight on 'one stands out' in 0.4% of trials where one does.

How often seven 95% intervals cover the small groups of a league table whose size relation is steepening below the median size. Groups of twenty patients or fewer, 600 tables of a hundred groups. Coverage: one centre, plugged in 58.0% (average width 2.81); one centre, its uncertainty added 58.5% (average width 2.83); a fitted line, plugged in 83.1% (average width 1.58); a fitted line, its uncertainty added 88.4% (average width 1.77); a fitted quadratic, plugged in 85.5% (average width 1.53); a fitted quadratic, its uncertainty added 93.7% (average width 1.92); the true relation and spread 94.8% (average width 1.55).

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

The interval a small group is given

A league table's 95% interval for a small group, pooled towards a size relation fitted from the table, covers 92.8% of the time when the relation is straight and 83.1% when it steepens below the median — and 77.4% for the groups of eight patients or fewer. Adding the fitted centre's own uncertainty, weighted by how much the group borrows from it, brings the line to 88.4% and a fitted quadratic to 93.7%, and the quadratic's interval covers 94.6% of the smallest groups at every shape tried. One centre, plugged in, covers the smallest groups 35.2% of the time when the relation steepens, and no added variance repairs a centre in the wrong place.

Coverage of an interval for a ratio of two rates against the expected total. The unconditional coverage of three intervals for the ratio of two Poisson rates, each built conditionally on the total and each reporting the whole of (0, ∞) when the total is zero, at the conditional proportion 0.5, against the expected total count. With the arrival times in both windows as the coin the interval covers exactly 95% plus a twentieth of e raised to minus the expected total: 96.84% at an expected total of one, 95.25% at three, 95.00% from about ten. The exact conditional interval covers 100.00%, 99.79%, 97.82% and 96.55% at forty; mid-p 99.11% at three and 95.89% at ten.

A proportion's interval near the boundary, and the coin

Two windows and a ratio

Two counts from two windows give an interval for the ratio of their rates through the conditional binomial: given the total, the first window's count is binomial with a proportion that depends only on the ratio. The arrival times in both windows supply that binomial with a continuous coin at every total from one up, and the interval then covers exactly 95% plus a twentieth of the chance of no events at all. A total of zero can only report the whole of (0, ∞). And the exact conditional test's familiar conservatism is not the zero total's: the zero is the larger cause only while the expected total is below ln 2, and at an expected total of ten the exact interval still covers 97.8% for reasons that have nothing to do with it.

A probe from what the rule blocks

How far, not whether

The blocking matrix records whether a tolerance box refuses an exchange. Dropping the pairs it refuses for certain changes nothing. Recording instead how far each exchange moves the balance vector turns the pairing into its degree plus a part that lies inside the rule's own span — and the degree is the design's leverage, exactly. The heuristic that beat every reading of what the rule blocks was the unclamped pairing's degree all along.

Seven products of three splits. The correlation of every product of three centred median splits with every other, at a Spearman rank correlation of 0.4 between each pair of covariates. Under a Gaussian copula a main effect correlates with the other mains and with the triple (0.273), and with no pair at all, because the third moment is 0.000. Under a Frank copula, whose pairs are radially symmetric, the third moment is 0.078 and every other cell fills in: a main correlates 0.082 with the pair it is not in. In both panels a main is exactly uncorrelated with a pair it belongs to, which is the known zero.

Both halves of the dependence at once

The zero that needed two

A rule balancing two median splits removes nothing of their interaction, on every copula, because a centred split squares to a constant. Add a third covariate and the same arithmetic stops protecting the thing it looked as if it protected. The product of three splits is not orthogonal to the mains: at a rank correlation of 0.4 a rule on the mains removes 14.47% of it under a Gaussian copula. And the symmetry that decides the rest belongs to the triple rather than the pair, so Frank's copula, whose pairs are radially symmetric, leaks where Clayton's, whose pairs are not, barely does.

The same table at seven correlations

A cut on each side

Every table of the threshold's leak put one quantile on both covariates, which is the diagonal of a surface nobody had drawn. Off the diagonal the copulas swap places: a cut at the 5th percentile on one covariate and the 95th on the other removes 54.8% of the interaction under a Gaussian copula and 1.1% under a t copula, the reverse of their order at the near corner. Walked further out, the far corner has two opposite limits, and which one a Gaussian reaches is decided by whether its correlation is above or below exactly one third.

The shape the covariate enters by

The list it was chosen on

Six functions of one covariate looked like 720 designs, one per order of addition. The rule reads a span and not a sequence, so they are 63, and at a hundred units the best four leave 12.1% of a coin's imbalance against the designer's first four at 31.5%. Those best four contain no cube and are, function for function, the four shapes the worst case was scored on. Read on six shapes it was not told about, the same design leaves the cube 77.0% of a coin's imbalance, and the designer's four, which lost by a factor of two and a half, leave it 28.1%.

$Three repairs at one requirement. Coverage against spend at a half-width of 0.4 and a first stage of 5, all exact. A floor on the second stage at 5, 8, 10, 12, 15, 18, 21, 24 observations covers 88.4%, 91.4%, 92.4%, 93.1%, 93.9%, 94.6%, 95.3%, 96.0% at 0.86, 0.94, 0.97, 1.00, 1.02, 1.05, 1.09, 1.14 times the oracle's spend. The second stage reading with t, with its fraction dialled from 0.2 to 1, covers 88.1%, 89.0%, 90.6%, 92.1%, 93.4%, 94.4%, 95.2%, 95.9%, 96.4% at 0.84, 0.91, 1.02, 1.17, 1.34, 1.52, 1.70, 1.89, 2.08 times. A constant at the end covers 88.4%, 89.4%, 90.4%, 91.3%, 92.1%, 92.9%, 93.6%, 94.2%, 95.0%, 95.7% at 0.86, 0.90, 0.94, 0.98, 1.02, 1.06, 1.10, 1.14, 1.20, 1.26 times.$ What the design is asked to guarantee

A floor that reads the first stage

A three-stage stopping rule fails at a first stage of five because a low first reading asks for nothing more, and the only floors that repair it were set near the answer, by somebody who already knew roughly what the spread was. Inflating the first reading by Stein's own factor needs no such knowledge, and it does cut the experiments left stuck from a fifth to a fifteenth. But those still stuck cover less than before, the rule needs a different dial at every requirement, and a floor of 26 observations covers 96.5% at the spend where the rule covers 92.1%, even met by a spread it was not set for.

Which side the misses fall on. Misses of a nominal 95% forecast interval 1 step ahead on 60 observations of a first-order autoregression at 0.7, split by side. normal shocks: the interval as printed 3.1% below and 3.1% above, shocks from the residuals 3.8% below and 4.2% above, the same, coefficient re-estimated 3.3% below and 4.4% above. Student's t on five: the interval as printed 3.3% below and 3.0% above, shocks from the residuals 3.9% below and 3.0% above, the same, coefficient re-estimated 3.6% below and 3.1% above. skewed shocks: the interval as printed 0.0% below and 6.5% above, shocks from the residuals 4.3% below and 4.1% above, the same, coefficient re-estimated 1.8% below and 4.3% above.

The observation that has not happened

A tail sixty residuals have barely seen

A forecast interval that reads a normal quantile has every one of its misses on one side when the shocks are skewed, and the natural repair is to draw future shocks from the model's own residuals. It works on the side: 0.0% below and 6.5% above becomes 4.3% and 4.1%. It pays for that with coverage, 93.5% to 91.6%, and on sixty observations it does this under normal shocks too. And a nominal 99% interval has a ceiling nothing in the resampling can lift, because one new shock beats all of sixty old ones in either direction with probability 3.3%.

Coverage as the effect moves with the level. Coverage on ten and two in every block, with the level between blocks moving at a spread of 0.5 and the effect moving with it at each slope, 4000 runs each. At -3: refusing the sums 94.4%, pooling them 88.8%, residualised 97.0%; At -2.5: refusing the sums 94.3%, pooling them 88.9%, residualised 95.6%; At -2: refusing the sums 94.9%, pooling them 90.0%, residualised 93.8%; At -1.5: refusing the sums 95.1%, pooling them 91.7%, residualised 92.7%; At -1: refusing the sums 95.1%, pooling them 94.8%, residualised 94.0%; At -0.5: refusing the sums 95.1%, pooling them 97.2%, residualised 97.7%; At 0: refusing the sums 95.0%, pooling them 98.8%, residualised 99.6%; At 0.5: refusing the sums 95.0%, pooling them 99.4%, residualised 99.9%; At 1: refusing the sums 95.0%, pooling them 99.4%, residualised 99.9%.

A promise about two arms

The sums under a moving level

A trial's block sums are a free second estimate of its variance only while they see what the differences see, and a level that moves between blocks with an effect moving against it breaks that: pooled raw at a ceiling they cover 87.6% to 90.0%. Residualising the sums on an unbalanced design does not make them safe. It moves the failure. On ten and two, 90.0% at the ceiling becomes 93.8%, the trough leaves for a slope of about −1.5, and over the rest of the range the same estimate over-covers, at 99.9% on an interval half as wide again as it needs to be.

Coverage lost against the honest rule. Coverage lost in points against the rule that reads only within-block spreads, on the same observations, blocks of 2, 6000 runs, at half-widths 0.5, 0.35, 0.25, 0.15. the reported spread in full: 0.32 ± 0.27, 2.53 ± 0.37, 5.33 ± 0.41, 3.75 ± 0.35. a fixed half: 0.72 ± 0.26, 2.43 ± 0.29, 0.98 ± 0.26, -0.25 ± 0.20. κ = (b − 1)/(N − 1): 0.37 ± 0.21, 1.18 ± 0.25, 0.58 ± 0.23, -0.18 ± 0.19. the same, phased in as b/(b + 20): 0.22 ± 0.10, 0.35 ± 0.16, 0.23 ± 0.18, -0.10 ± 0.19. the same, read in only after twenty blocks: 0.00 ± 0.00, -0.02 ± 0.04, 0.17 ± 0.19, -0.17 ± 0.19.

The block size as a schedule

A rule that sets its own κ

A stopping rule may read the spread inside its blocks and may not read the spread between them, and the dial between the two costs nothing for a long stretch and then a lot. The share an efficiency argument recommends is each estimate's share of the degrees of freedom, and on blocks of two at a half-width of 0.15 that loses nothing and steadies the experiment by 30%. At 0.35 it loses 1.18 points. Deferring the forbidden reading until twenty blocks costs nothing measurable at any requirement, and it keeps most of the steadiness where steadiness can be had.

Balancing what has no levels

A second reading or a second covariate

A rule that balances a recording balances the truth only as far as the recording reaches, and a second reading of the covariate raises that reach. So does a first reading of something else. At a reliability of 0.8 the first reading of a second covariate does more once that covariate matters a third as much as the first, and the threshold is exact: the square root of (1 − λ)/(1 + λ), with no trial size in it. A protocol's list of measurements turns out to be a small knapsack, and it is rarely filled by reading anything twice.

The guess rate through a trial. Guess rates in each tenth of a trial of 150 patients on three arms with the rule taking its preferred arm with probability 0.8, over 1500 trials. knowing everything: 65.9%, 72.2%, 72.0%, 72.8%, 72.4%, 72.2%, 72.5%, 72.7%, 72.7%, 72.4%. a joint table learned in earlier trials: 53.4%, 55.4%, 54.8%, 55.1%, 54.3%, 53.8%, 54.9%, 54.8%, 54.1%, 54.8%. the centre's totals: 45.4%, 50.3%, 50.2%, 50.8%, 49.8%, 50.2%, 50.9%, 50.6%, 50.4%, 50.7%. following whichever has been right: 46.5%, 50.2%, 49.3%, 49.6%, 48.9%, 48.7%, 49.3%, 49.0%, 49.0%, 48.7%. a joint table learned in this trial: 36.4%, 43.8%, 45.0%, 46.2%, 46.7%, 46.8%, 48.1%, 48.5%, 47.9%, 48.9%. the centre's own factors, scored: 46.8%, 51.4%, 49.7%, 49.9%, 48.4%, 48.6%, 48.5%, 47.7%, 47.6%, 46.7%. Chance is 33.3%.

More arms than two

The guesser who learns

An investigator who watches a three-arm minimisation can tally which of several partial readings has been right so far and follow the leader. It does not help. Following the leader names 48.9% of assignments where the best single reading names 49.9%, and a table of what the three readings say together, learned inside the trial, starts at 36% and has not caught up by a hundred and fifty patients. Learned over earlier trials, that table reaches 54.5%. The full guesser's 71.8% stays out of reach of all of them, because the gap to it is information rather than practice.

When the set is too large to walk

A floor for the draw

A basis drawn at random guarantees more on average than any fixed one, at the price of leaving some shape wholly untouched in a large share of trials. Requiring every basis in the draw to keep a floor looks like a smooth trade between the two. It is a staircase, and the first step does nearly all the work. No basis has a floor between zero and 31.83%, so there is nothing to give up until a floor of that size is asked for. And at four functions, seven bases tie at the fixed basis's own 63.66%: a mixture of them keeps that floor exactly and adds thirteen points to the guarantee.

Choosing what the rule reads

A box with a count

The ellipse never runs out of assignments and holds the named functions loosely; the box holds them tightly and can come up empty. Dropping the ellipse's thin directions was meant to give both, and it does not: no cutoff comes within a third of the box. But the box's emptiness was never a property of the box. It belongs to a tolerance fixed in advance. Set the tolerance by a count instead, and at that count the region is the box, on every set of units, with nothing left to run out.

A guarantee that needed a symmetry

The covariate on its ranks

A skewed covariate spoils every parity argument a balancing rule relies on, and a rule that balances ranks instead of values looks like the way out, since a rank has the same uniform law on any marginal. The measurement says the skew really does belong to the scale for one kind of shape: a rank holds a median split at exactly a quarter of a coin's imbalance whatever the covariate. But it pays with a cap on any shape linear in the value, at nearly half a coin's imbalance on the strongest skew. And a rule holding values and median splits together holds both, beating the rank on the shape a rank gives up and matching it on the one it gains.

The excess over the Gaussian displacement, by window. By how much the expected leverage per parameter exceeds the Gaussian closed form, with the fresh row integrated out, at windows 20, 40, 80, 160, 320, 640. normal: -0.90%, -0.61%, -0.04%, -0.06%, -0.02%, 0.00%. t on eight: 4.14%, 2.78%, 1.79%, 0.73%, 0.28%, 0.18%. t on five: 10.70%, 7.50%, 3.93%, 2.01%, 1.26%, 0.70%. t on three: 44.44%, 32.67%, 22.62%, 16.43%, 11.70%, 7.63%. exponential: 27.91%, 14.01%, 7.21%, 3.53%, 1.93%, 0.85%. On normal predictors the closed form is exact from a window of 80.

A search with no fixed point

An excess and its window

The parameter-count displacement is a Gaussian fact, and on heavy-tailed predictors it runs a few per cent over. Swept across windows from 20 to 640 rows, the excess is about the predictors' excess kurtosis divided by the window: a law with a fourth moment of nine on 80 rows is 7.5% over, and on 640 rows under one. At three degrees of freedom it falls only as the root of the window, from 44% to 7.6%. And the instability once blamed on that law was not there: with the fresh row integrated out, the batches agree to a point and a half, and the mean exists.

What a stated power leaves of the main effects. The main-effect efficiency of the best design reaching a power of 0.8 at level 0.05, as N|δ|² rises through 50, 60, 70, 80, 100, 130, 170, 220, 300, 400, 600, 1000. a saddle, two-degree test, the compound path: out of reach, out of reach, 0.806, 0.841, 0.881, 0.914, 0.937, 0.952, 0.966, 0.975, 0.984, 0.990. a bowl, two-degree test, the compound path: 0.782, 0.823, 0.851, 0.871, 0.898, 0.923, 0.941, 0.955, 0.967, 0.976, 0.984, 0.990. a bowl, its own one-degree contrast, the compound path: 0.827, 0.859, 0.880, 0.896, 0.918, 0.937, 0.952, 0.964, 0.973, 0.980, 0.987, 0.992. a bowl, a factorial with centre points: 0.914, 0.930, 0.940, 0.948, 0.959, 0.969, 0.976, 0.982, 0.987, 0.990, 0.993, 0.996.

The criterion, and what it assumes

A design chosen for a test

A screening experiment that wants its main effects and a check on curvature has been told to trade them with a weight nobody can state. It can state a power. Read against a power of 80%, the frontier collapses to one curve in runs times the squared size of the curvature, and a large enough trial pays almost nothing. But the curve belongs to a test. A factorial with a few centre points beats the entire frontier on a bowl, spending 4% of its main-effect information where the frontier spends 10%, and against a saddle of the same size it has exactly its 5% level.

What Hansen's threshold costs, by the number of origins. The power a threshold of zero keeps over Hansen's, on the same draws. with sixteen stale candidates: 7.5%, 7.3%, 6.8%, 5.3%, 3.7%, 6.0%. the eight windows alone: 2.7%, 3.8%, 4.7%, 5.3%, 3.7%, 6.0%, at 25, 50, 100, 200, 400, 800 origins. The price does not fall as the sample grows.

The best of a set, and what the search costs

A threshold against its sample

A recentred test's threshold exists so that the test is right in the limit, and at a hundred origins it costs a fifth of the power against a stale set. The natural defence is that the price falls as the sample grows and the guarantee starts to earn it. Across twenty-five to eight hundred origins it does not: a threshold of zero keeps four to seven points more power at every size, and its size at the corner stays at the level from fifty origins on. What does change with the sample is the stale set, which stops costing anything by two hundred origins under Hansen's rule and by eight hundred under the most cautious.

A block, weighted inside itself

A sequence that knows it was centred

A block length read off a sample's own autocovariances gets worse the further out it reads, because a centred series' autocovariances sum to exactly zero. To first order every lag loses the same amount, about the long-run variance over the sample size, and that can be added back. Corrected, a reading to lag forty goes from 84.5% to 89.2%, and to lag twelve from 93.3% to 94.5%. But the correction overshoots on the long lags, and on the rule that picks its own cut-off, which is short, it moves coverage by three tenths of a point. The identity was the reason the lag mattered. It was not the reason the rule falls short.

Every finding Benjamini–Hochberg made in thirty families, with its interval, at real effects of 2. 85 findings, sorted by their estimate. 12 of their ordinary 95% intervals miss the true effect, every one of them on the far side; 6 of the wider false-coverage-rate intervals miss.

Corrections, and what each controls

Intervals for the findings

Benjamini–Hochberg's findings usually go out each with its ordinary 95% interval. With ten real effects of two standard errors among twenty tests, 11.59% of those intervals miss their effect, every miss on the far side, and the interval around the most prominent finding covers 72.36% of the time — 2.38% when the effects are one standard error. Intervals widened for the number of findings hold the share that miss under 5%.

How often each combination, and each union of them, rejects ten studies of nothing. Each combination alone rejects exactly 5% of null sets. Counted on 1,000,000 sets of ten null studies: Fisher or Stouffer 6.63%, Fisher or Tippett 8.05%, Stouffer or Tippett 8.96%, any of the three 9.66% — enclosed on a two-dimensional lattice between 9.18% and 10.09% — and all three together 1.05%. The three sizes add to 15%.

Tests, and the second number

The smallest of three combinations

Reporting whichever of Fisher's, Stouffer's and Tippett's combinations is smallest is a test of its own, and on ten studies of nothing it rejects 9.66% of the time — not 5%, and nowhere near the 15% the three sizes add to, because the statistics are correlated at up to 0.903. Read at 2.448% each it is exact, and then it trails the best single combination by at most 7.45 points and leads the worst by at least 10.30.

The honest curve, and the same forecaster in three coarse vocabularies. The ROC curve of the honest probability at full signal, area 0.8683, beside the same forecaster rounded to the nearest whole number, area 0.7684 — the two-valued liar — to the nearest half, area 0.8205, and to the nearest tenth, area 0.8650. A vocabulary of v values is v points on the square joined by straight segments, and tied reports count half.

A forecast that is a probability

A forecaster that rounds

An honest probability issued in tenths loses 0.0033 of ROC area and 0.000708 of resolution — the variance its bands average away, and 89.5% of the 0.000792 it adds to the Brier score. Two hundred records of two thousand forecasts show that loss on 189; it takes about 3,300 forecasts to put it two standard errors from zero. And 3.207 in every thousand forecasts in tenths are a 0% on an event that happened, which a logarithmic score charges without limit.

The difference in restricted mean survival at every horizon, in three worlds. Treatment minus control, in closed form, with dropout irrelevant to the truth. The proportional treatment's difference grows to 0.4766 at τ = 3 and the waning treatment's to 0.2675. The crossing treatment's rises to 0.1776 at τ = 2, near where the two survival curves cross, and falls back to 0.1366 at τ = 3. The ticks along the bottom are the eleven horizons, from 0.5 to 3 in quarters, at which a trial below reads its differences.

When the data stops early

A horizon chosen after looking

A difference in restricted mean survival read at whichever of eleven horizons looks most convincing rejects 11.24% of trials in which the treatment does nothing, against 4.70% at a horizon fixed in advance. The correlation of the differences across horizons is closed, and the Gaussian process it defines prices the choice at a critical value of 2.317 — which brings the counted size back to 4.99% and keeps 96.92% of the power that a horizon nobody could have known to fix would have had.

Regression, and what the summary hides

The start an efficient robust line inherits

The MM-estimator carries a trimmed fit on through a redescending loss, and it does what it promises on one far row: slope 0.479 at every distance, the row at weight exactly zero, and 87.2% of least squares' efficiency at twenty rows. What it cannot do is choose. At eight far rows of twenty the exact trimmed fit picks the wrong half on 111 datasets; the efficient step repairs none of them, spoils none of the other 89, and ends nearer the wrong line than the start did.

Three intervals as one strength is spread thinner, at a concentration of 8. Coverage of four nominal 95.0% intervals on the same 1000 draws of 200 rows at each count, when a total concentration parameter of 8 is spread over 1 to 32 instruments. Two-stage least squares covers 97.2%, 96.4%, 94.0%, 86.7%, 73.2%, 51.5%. Building each row's fitted treatment from a first stage that never saw that row covers 97.1%, 97.2%, 98.3%, 97.8%, 97.9%, 98.7%. Limited-information maximum likelihood with its conventional standard error covers 97.2%, 96.7%, 95.7%, 90.9%, 85.2%, 79.0%. The same estimate with Bekker's many-instrument standard error covers 97.2%, 97.2%, 97.2%, 95.0%, 94.3%, 93.8%. At one instrument the likelihood estimator is two-stage least squares exactly, which is why the first readings of those two agree to the last draw.

A variable that moves one thing only

A standard error that knows about the instruments

Limited-information maximum likelihood came out least biased when a concentration parameter of 8 was spread over thirty-two instruments, and its conventional interval covered 79.0%. Bekker's many-instrument standard error covers 93.8% on the same draws, at 63% of the jackknife's width — and it gets there with a median standard error of 0.561 against a true spread of 0.797, because it is large on the draws that need it. At eight times the strength it covers 94.9% at 91% of the jackknife's width, and nothing measured here beats it.

Reversals that are not errors

The slope of a density nobody can see

Tweedie's formula corrects a reading by the slope of the readings' own log-density, and a study has its readings. Estimated from a thousand of them, the correction for the top one per cent beats the correlation's linear rule on 84.0% to 98.0% of studies from heavy-tailed populations and on 75.0% to 81.5% from a bounded one — and costs an error of 0.09 to 0.12 where the population is normal and the rule was already exact. At 250 readings the log-spline loses to the rule it replaces, and at 16,000 the same log-spline gets worse on a power tail.

A run length of 4 makes every exceedance its own cluster. 200 steps of a max-moving-maximum, X(t) = max(0.4·Z(t), 0.3·Z(t−6), 0.3·Z(t−12)) with unit Fréchet innovations Z, whose extremal index is exactly 0.40: one large innovation can put three readings above a threshold, 6 steps apart. The rule marks the 0.9 quantile and 19 readings clear it; 12 of the gaps between consecutive exceedances are exactly 6 steps. With a run length of 4, so that two exceedances 4 or more steps apart start separate clusters, they form 19 clusters, shaded, the largest holding 1. The runs estimator reads 1.000 against 0.40.

The tail past the last observation

The run length a declustering chooses

The runs estimator of an extremal index carries a constant nobody derives. Where a cluster is a run of neighbouring exceedances the constant barely matters; where a cluster's members fall six steps apart, the estimate is 0.9069 at a run length of six and 0.3649 at seven against an index of 0.40, and a run length of four removes under a tenth of the overstatement declustering exists to remove. A rule that reads the run length off the data has the smallest worst error of the three.

A prior worth 35 observations, moved across the range — truth 0.1, n = 20. The same prior weight centred at each of 33 places. Its interval covers 100.0% where the centre is near the truth and 0.0% at its worst, while the mean width where it covers least is 0.221 against a flat prior's 0.263 on the same data.

The prior, doing visible work

When the prior is confident and wrong

A prior worth thirty-five observations, centred in the wrong place, produces a 95% interval that covers nothing at all — and reports a width 5% narrower than an honest one. It takes seventeen thousand observations to repair, not thirty-five, and the worst study to run is the one whose sample size equals the prior's weight, exactly.

Twelve groups from two clusters, τ = 1. Every group's truth is in one of two clusters, and the population's total spread is exactly τ = 1, so the analysis recovers τ̂ = 1.515 and every shrinkage weight is what it would be for a single normal population. The estimates are pulled towards the grand mean, which is the middle of the gap — a place 0 of the 12 truths are and 6 of the estimates end up.

Groups that borrow

One population, or two

Group effects from two clusters rather than one bell, with the same total spread. The analysis recovers the same population spread, uses the same weight for every group, and reports nothing unusual — while 46% of its estimates land in a region holding 6.6% of the truths.

What the forecast interval is short by, φ = 0.85, 6 steps ahead. The plug-in interval covers 88.42% against a claimed 95%. Correcting the variance recovers 0.56 points, propagating the persistence's own standard error recovers 0.40, correcting the persistence recovers 2.66, and all three together recover 4.20 — leaving 2.38 points unaccounted for.

Comparing two forecasters

What the interval is short by

The forecast interval covers 88.42% where it claims 95%. Correcting the persistence recovers 2.66 points, correcting the innovation variance 0.56, propagating the persistence's own standard error 0.40 — and all three together recover 4.20 of the 6.58, leaving a residual none of the standard repairs reaches.

What a confirmation run at the chosen setting would find. The true optimum is worth 62.348. At σ = 2 the fit predicts 62.679 at the setting it recommends and the truth there is 61.821 — a gap of 0.858, which is 0.72 of the prediction's own standard error. The setting itself gives up 0.527 against the best available.

The surface between the corners

The run that confirms it

The setting a response-surface analysis recommends was chosen because the fitted surface was highest there, so the height the fit predicts at it is a maximum over a random field. At twice the noise the fit predicts 0.858 more than is there — 0.72 of the prediction's own standard error — and the gap is not noise, it is the selection.

When the observations repeat each other

How slow a return a sample can see

At two hundred observations the test finds a gap that halves in five steps four times in five, one that halves in eight 37.3% of the time, and one that halves in fifty 4.95% of the time — which is the rate at which it finds pairs with no mechanism at all. The boundary moves with the sample, not with its square root.

Three promises, and no procedure keeps all three. Average coverage and worst-case coverage for four 95% intervals for a proportion at n = 40, computed exactly. Their expected widths are 0.2418, 0.2417, 0.2472, 0.2641 in the same order. The textbook interval and the score interval have the same expected width to four digits — 0.2418 and 0.2417 — and worst-case coverages of 55.31% and 92.21%. The exact interval never breaks its promise and is 9.3% wider than the score interval to do it. Each of the three columns orders the four procedures differently.

Intervals, counted

An interval that covers and says nothing

A procedure returning the whole line 95% of the time and the empty set otherwise has coverage exactly 95% at every parameter value. Two real intervals at forty observations have expected widths of 0.2418 and 0.2417 and worst-case coverages of 55.31% and 92.21%.

Each interval covers one question and not the other. Coverage of each interval for the overall mean, scored against both estimands, over 20,000 two-site studies of 10 observations apiece. The fixed-effect interval covers the mean of the two sites in hand 96.37% of the time and the population mean 54.77%. The random-effects interval covers the population mean 94.96% — exactly its level, from one degree of freedom — and over-covers the two sites in hand at 98.25%. Both are correct; they are answers to different questions printed in the same place.

Hierarchy past one number

What a two-unit study should report

The fixed-effect interval covers the mean of the two sites in hand 96.37% of the time and the population mean 54.77%. The random-effects interval covers the population mean 94.96% — exactly its level, from one degree of freedom — and is 11.6 times wider.

The interval that holds observations, not a mean

A range that grows with the lot

A band set from the range of everything seen so far flags a unit only when it sets a new record, and for any continuous population those flags are independent, with the k-th unit flagged with probability 2/(n + k). That makes a few-misses promise far cheaper than the fixed range's — at most five of the next hundred from 36 starting observations rather than 107 — and exactly as expensive when no miss is allowed, because a lot with no flag never moves the band. The saving is bought by believing every flag. After a two-standard-deviation step in the mean, the fixed range flags 25.03 of the eighty units that follow and the learning range 3.62; by the last twenty units it sees a unit outside in 25.5% of lots, against 18.4% with no step at all.

Series that move together

A shock every pair shares

Sixteen pairs of series whose shocks are half common are worth 5.37 independent pairs to the panel's average statistic, and sixteen that share nine tenths are worth 1.44. Read against the 5% point computed for independent pairs, the pooled test then calls a panel with no relation tied 15.5% and 31.6% of the time; read against its own point, it finds a relation shared by every pair 22.3% of the time at nine tenths common, against one pair's 20.0%. Removing each date's cross-sectional average gives back the level and all sixteen pairs when every pair feels the shock equally, and leaves 13.3% false alarms when the loadings run from a half to one and a half.

How often a trial borrowing from 8 earlier trials on a trend declares a treatment with no effect a success. Fifty patients an arm, each earlier control of two hundred, the current trial one step after the last. At slopes 0, 0.01, 0.02, 0.03, 0.05, 0.075, 0.1: exchangeable 2.7%, 4.4%, 6.6%, 8.3%, 9.9%, 8.3%, 6.7%; with a fifth of the prior vague 2.4%, 3.6%, 5.5%, 6.9%, 7.6%, 6.5%, 5.7%; with a line in time 2.9% at every slope.

The spread, and its own uncertainty

A history that has been moving

Earlier control arms borrowed as exchangeable draws are pooled towards the history's middle, and when the control mean has been rising the current trial sits at its end. A drift of 0.02 standard deviations a trial — a step between neighbouring trials of under a third of either one's standard error — turns a treatment with no effect into a success 9.9% of the time from sixteen earlier trials, and a drift of 0.05 overstates the effect by 0.130 standard deviations from eight. A line in time removes the bias exactly, at every slope, and pays for it in borrowing: from eight earlier trials it borrows 175 control patients where the exchangeable model borrows 439.

How often one genuine interaction in a table of eight is found, by its size, at latent correlation 0. A trial of 400 with 80% power for its main effect, eight characteristics, the first modifying the effect. At h = 0, 0.25, 0.5, 0.75, 1 the real interaction crosses 5% in 4.2%, 10.3%, 29.2%, 56.6%, 81.0% of trials; Bonferroni's 2.734 in 0.4%, 1.8%, 8.7%, 26.6%, 53.6%; the exact threshold for this overlap, 2.727, in 0.4%, 1.9%, 8.8%, 27.0%, 53.8%.

An interval read beside something else

One characteristic that really matters

A trial of four hundred tabulates eight characteristics and one of them genuinely changes the treatment's effect — the whole effect on one side, none on the other. Tested alone at 5% the real interaction is found 81.0% of the time; at the Bonferroni threshold that protects the table, 53.6%. It is the table's largest interaction in 82.4% of trials when the characteristics are independent and in 54.4% when they overlap like nested age bands, and in that case another characteristic crosses the Bonferroni line in half of all trials and is the top finding in a quarter. A family-wise threshold counts false rows; it cannot say which of two overlapping rows is the cause.

How often a Simpson reversal appears on the strongest baseline variable when its cut is slid along it, by the trial's size. The treatment helps every patient by the same six points. At 40, 80, 160, 320, 640 patients: some cut in the middle 80% reverses in 18.8%, 23.4%, 24.3%, 19.2%, 10.6% of trials; some decile in 12.2%, 13.2%, 14.1%, 11.0%, 6.2%; the median in 3.9%, 4.4%, 4.2%, 3.1%, 1.7%.

When the stratified answer and the pooled one disagree

A cut that slides

Slide the cut on a trial's strongest baseline variable along every gap between observed values in its middle eighty per cent, and a trial of eighty whose treatment helps everyone equally shows a Simpson reversal somewhere in 23.4% of trials — against 13.2% for the nine deciles and 4.4% for the median. Sixty-five cut positions are worth about 9.5 independent cuts, and at 640 patients, with 513 positions, about 7.2: a table that moves one patient at a time is a continuous scan, and its count is set by the range scanned rather than by the number of cuts. The reversing cuts spread along the whole range, in 2.62 separate runs at eighty patients and 8.36 at 640.

Whether residuals built to be independent see a skewed error better than ordinary ones. The straightness test, each version read at its own 5% point. On all forty errors: 82.9%. At 2, 5, 10, 20 columns: ordinary residuals 79.1%, 71.4%, 51.2%, 23.0%; BLUS residuals 76.4%, 64.9%, 38.3%, 16.2%; recursive residuals 64.4%, 49.5%, 25.9%, 9.1%; 40 − p errors 80.6%, 76.1%, 69.1%, 49.5%.

What a diagnostic plot is showing

Residuals made independent

Recursive residuals — each row predicted from the fit to the rows before it — are exactly independent normals under the null for any design, so a quantile plot of them has an exact band. They see a skewed error worse than the ordinary residuals do, not better: 25.9% against 51.2% at ten columns on forty rows, 9.1% against 23.0% at twenty. BLUS residuals, the independent set closest to the errors, reach 38.3% and 16.2%. Every such set is a rotation of the ordinary residuals, so none holds information they lack, and independence is bought by mixing some residuals almost entirely out of other rows' errors — the least pure recursive residual at twenty columns is 0.4% its own.

Two tests, a threshold, and the rate they are read against

A test whose tail is not normal

A validation study that fits a normal curve to each group saw the tail where a threshold jumps — when the diseased scores really were normal. Give the same published test a diseased group with no lower tail at all, and the binormal fit invents one: 89.7% of studies recommend flagging everyone, adding 67.08 false alarms' worth of harm per hundred people to a best threshold that costs 5.61. Give it a lump of mild cases instead, and the binormal fit misses the tail that is there and does worse than the study's own curve. A normality test on the hundred diseased scores sees the missing tail every time and the lump 60.4% of the time, and a study that fits the binormal model only when normality is not rejected is never the worst of the four.

What a sample-size calculation was given

The correlation a pilot can see

Two models of repeated visits agree that adjacent visits correlate 0.7 and disagree about how many follow-ups a trial should buy: three under equal correlation, one when the correlation fades. Planning on the wrong one costs 28.0% or 9.9%. Two follow-ups cost at most 3.2% more than the best under either, and at most 11.1% under any curve with that adjacent correlation. A pilot of twenty patients at four visits chooses worse on average than that rule when the correlation fades; it takes about forty to draw level with it, and at an effect of half a standard deviation those forty patients' extra visits cost fifty times what the better schedule saves.

What a summary of a scatter is a property of

A term built from the others

A regression's squared terms and interactions are columns built from its covariates, and each coefficient on one rests on the number of points divided by the kurtosis of what the built column adds — fifteen for the square of a normal covariate, nine for the product of two uncorrelated ones, three for a treatment's interaction with a normal covariate, which is the same as the covariate's own coefficient. A design of a hundred rests on more than the population says, 12.2 points behind a square against 6.7, because a hundred draws rarely hold the tail that sets the kurtosis. Centring changes nothing about the square's coefficient, to the last digit. And correlation between two covariates hides the point that decides each one's own coefficient while it reveals the point that decides their interaction.

The error of the chosen arm's estimate against a fixed second stage's size, and a second stage sized by the interim, 8 arms, one ahead by half a standard deviation. Fixed second stages of 10, 25, 40, 55, 70 patients: both stages combined err by 0.172, 0.155, 0.143, 0.133, 0.126; the mixture-shrunk estimate by 0.208, 0.183, 0.164, 0.151, 0.140. The rule that sizes the second stage by the interim spends 41.4 on average and errs by 0.142 and 0.159; its second stage alone errs by 0.225.

Designs that change while they run

A second stage sized by the first

A drop-the-losers trial can size its second stage by what the first stage says about the arms' shape — more patients when the chosen arm's lead looks like luck, fewer when it looks real. The rule does what it was built to do: at sixteen arms with a genuine winner it spends 51.0 patients a group when the interim chose the wrong arm and 24.2 when it chose the right one. And it buys nothing. Against a fixed second stage of the same average size, every estimate of the chosen arm errs by the same to within a few thousandths; the published combination's bias rises from 0.014 to 0.022, and the second stage alone, still unbiased, errs by 0.319 against 0.281.

Every group's 90% rank interval in one league table whose size relation is steepening below the median size, with its true rank. A hundred groups from four to four hundred patients, ranked from their posterior under a fitted quadratic size relation whose uncertainty is drawn once per table. The groups of twenty patients or fewer have rank intervals 30.1 places wide on average, and 34 of their 36 true ranks fall inside; the groups of over a hundred, 32.1 places, with 27 of 30 inside.

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

A ranking with its uncertainty

A league table's reader wants a rank, and a rank interval inherits a fitted size relation's errors differently from an effect interval. When the relation steepens below the median size, a fitted line's 95% interval for a small group's effect covers 83.1% of the time; its 90% interval for the same group's rank covers 95.6%, because the line's error lifts the small groups into the crowded middle of the table, where rank intervals are wide. The error surfaces instead in the large groups' ranks, 87.6%, and in width: 36.9 places against the 27.3 the true relation needs. A quadratic's uncertainty has to be drawn once per table, since it moves every small group together — added group by group it over-covers at 92.8%.

How often four permutation tests of a covariate-adjusted effect reject a true weak null, effect varying with the outcome, 25% of 150 treated. At an effect spread of 0, 0.5, 1, 1.5, 2: the adjusted coefficient's permutation test rejects 5.9%, 10.8%, 13.2%, 16.6%, 14.8%; over its sandwich standard error, 5.7%, 5.0%, 3.4%, 3.4%, 3.0%; the coefficient with a treatment-by-covariate interaction, 5.1%, 10.2%, 12.8%, 14.7%, 14.0%; the same over its sandwich standard error, 5.7%, 5.2%, 5.2%, 5.1%, 3.9%.

The reference distribution the design supplies

The repair, with a covariate in it

Studentising a permutation test's statistic made the difference in means exact under the sharp null and nearly right under the weak one. Carried to the covariate-adjusted estimate a trial actually reports, the repair works only if the adjustment includes the treatment-by-covariate interaction. With a quarter of 150 units treated and effects that vary with the outcome, the adjusted estimate's permutation test rejects 14.8% of true weak nulls; over its sandwich standard error, 3.0%; the interacted estimate over its sandwich, 3.9%. When the effect varies with the covariate itself, even an even split does not protect: the adjusted test rejects none of a thousand true weak nulls, and at an average effect of 0.2 its power is 5.2% against the interacted, studentised test's 40.7%.

How often reporting whichever contrast is most significant rejects when the arms do not differ, by the split. 20,000 trials a point. With both arms at 0.05, 0.1, 0.3: at shares 0.3, 0.35, 0.4, 0.45, 0.5, 0.55, 0.6, 0.65, 0.7 the chosen contrast rejects 6.5%, 5.6%, 5.0%, 5.0%, 5.1%, 5.1%, 5.2%, 5.2%, 6.3%; 6.0%, 5.4%, 5.3%, 4.9%, 4.8%, 4.9%, 5.2%, 5.4%, 5.8%; 5.8%, 5.6%, 5.2%, 5.1%, 5.2%, 5.1%, 5.3%, 5.4%, 5.7%.

Splitting the units

A contrast chosen after the data

A two-arm trial with a binary outcome that reports whichever of the risk difference, the log risk ratio and the log odds ratio comes out most significant has tested three statistics that ask one question. At an equal split the choice is no choice at all: the difference has the largest z in every one of twenty thousand trials, so the selected test is the difference's, at its 5%. At a 30–70 split the choice is real and costs a point and a half of false positives, 6.5% at the rarest outcome. Pre-registering the difference and the odds ratio as a pair with Bonferroni's correction — the cautious alternative — costs eight to twelve points of power at every split.

Four laws, one flat floor. The error a band of each fixed width delivers, averaged over 400 draws of 120 rows under each law, drawn above that law's own best single width. From one lag to the best width the error falls by 0.02763 under AR(1) at 0.8, 0.02517 under a five-period moving average, 0.01122 under long memory at d = 4/9, 0.03507 under a break in the persistence; from six lags to thirty the whole surface spans only 0.00269, 0.00445, 0.00255, 0.00521. The best single width is 12, 24, 24, 16 lags. The flattest surface end to end is the one under long memory at d = 4/9, which is the law a steeper surface was expected from.

A charge that is not a straight line

The surface under every law

A draw-reading charge for a covariance band failed on one law, and the failure was deferred to a law with a steeper error surface. Run under all four laws in the collection, the surface is flat from six lags to thirty under every one, no draw-reading charge tracks anything, and long memory — the law expected to be steepest — is the flattest end to end. What the law moves is the level of the charge, not whether a draw can be read.

The weight each of a hundred outcomes carries in the fitted value at the 97.5th percentile of a lognormal covariate. One design of a hundred lognormal covariate values. The fitted value at a covariate value of 7.10 is a weighted sum of the outcomes, with weights fixed by the design. Under a line and its square it rests on 10.7 effective points, the largest carrying 19.1% of its variance. Under a natural spline with knots at 0.17, 0.57, 1.18, 3.95 it rests on 3.8, the largest carrying 41.1%.

What a summary of a scatter is a property of

A value read off a curve

No coefficient of a spline is read; what is read is the fitted curve's value at a covariate value of interest, and that value is a weighted sum of the outcomes with weights the design fixes before any outcome is seen. In the tail of a lognormal covariate a natural spline's value rests on 4.8 of a hundred points, fewer than the squared term's coefficient's 6.9, and the squared term's own value there rests on 10.2 — yet it is three times further from the truth, because its extra points are borrowed from where the curve has a different shape and buy no precision at all. At four hundred points, moving the last knot past the value raises its count threefold and halves its error; doubling the data does neither.

How often an adjusted permutation test rejects a true sharp null when the covariate is chosen after randomisation, held fixed or re-chosen inside every shuffle. 150 units, half treated, six baseline covariates of which three are prognostic; 2,000 experiments and 99 re-randomisations each, read on the adjusted coefficient over its sandwich standard error. Choosing the covariate most correlated with the outcome: 5.0% held fixed, 5.0% re-chosen. Choosing the covariate with the smallest residual variance: 5.5% held fixed, 5.3% re-chosen. Choosing the covariate most imbalanced between the arms: 3.0% held fixed, 4.8% re-chosen. Choosing the covariate with the smallest adjusted p-value: 10.4% held fixed, 5.1% re-chosen. Naming the most prognostic covariate in advance: 5.5%.

The reference distribution the design supplies

The covariate chosen afterwards

A trial that chooses which baseline covariate to adjust for after randomisation has two ways to run its permutation test: hold the chosen covariate fixed across the shuffles, which is what an analysis that reports adjusting for it actually does, or re-make the choice inside every shuffle, which is exact by construction. Holding it fixed, a choice made on significance rejects 10.4% of true sharp nulls, a choice made on imbalance only 3.0% — and pays seven and a half points of power for it — while a choice that never reads the arm labels is the same test either way. The interacted, studentised statistic keeps its weak-null behaviour only when the covariate chosen is the one the effect varies with.

How often two orders of selection report a winner from twenty analyses, no effect anywhere. Twenty analyses correlated 0.6, each with a diagnostic correlated γ with its own statistic, over 20,000 families a point. Clean then significant — the best diagnostic, reported if it clears 1.96 — reports a winner in 2.55%, 4.25%, 6.91%, 13.15% of families at γ = 0, 0.3, 0.6, 0.9. Significant then clean — the best diagnostic among those that cleared 1.96 — reports one in 18.04%, 18.04%, 18.04%, 18.05%: in every family where any analysis cleared 1.96, whatever γ is.

The analyses that were available and not run

The cleanest of the significant

An analyst with twenty correlated analyses can choose in two orders: take the one whose diagnostics look cleanest and report it if it clears 1.96, or take the analyses that cleared 1.96 and report the cleanest of them. The second is the one described as prudent, because it never reports an analysis whose diagnostics look poor — and with no effect anywhere it reports a significant analysis in about 18% of families whatever the diagnostic is, against 2.55% to 13.15% for the first. The diagnostic decides which significant analysis is shown and never whether one is. Each report's own interval can still be made exact, by conditioning on a selection set that is a union of pieces rather than a half-line; the family's claim count cannot.

What it costs to set the t limit at one level without knowing which skewed source the 15 observations came from. For the t limit on 15 observations, charged twenty per standard deviation of shortfall plus its margin, the loss at each nominal level as an excess over the best level for each source. The best levels are 97% for the exponential, 96.25% for the gamma, shape 2, 97.75% for the gamma, shape ½, 98.25% for the lognormal. The minimax level, 97.25%, costs at most 0.8% on any of them: 0.1% on the exponential, 0.6% on the gamma, shape 2, 0.2% on the gamma, shape ½, 0.8% on the lognormal. The conventional 97.5% costs up to 1.0%.

Shape, and what it does to a two-sample test

A level set before the source is known

Every best level for an upper limit on skewed data was found knowing the source, and the fifteen observations that would tell the sources apart are the ones being used to set the limit. Chosen instead to protect the worst of four skewed sources, the t limit's level is 97.25% when a failure is charged by the size of its shortfall, and it costs at most 0.8% more than each source's own best — the sources disagree about the best level and agree that missing it a little is cheap. The fitted gamma family, the construction meant to adapt to the source, is the one that needs it: its best levels run from 90% to 96.5% and its minimax level costs 3.4%. Charged a fixed amount per failure, the t limit's minimax level is 99.97% and costs 6.5%; the conventional 97.5% costs up to 119.9%.

How far the published estimate of the chosen arm sits from the best arm's effect, by how six hundred patients are split between choosing and estimating. Eight arms and a control, six hundred patients: a stated number an arm in the first stage and the rest split equally between the chosen arm and the control in the second. Root mean squared error of the published estimate about the best arm's true effect, over 5,000 trials a split. All eight alike: best at 16 an arm (0.092), 0.183 at the familiar sixty; One modestly ahead: best at 56 an arm (0.151), 0.153 at the familiar sixty; One clearly ahead: best at 48 an arm (0.146), 0.154 at the familiar sixty; Two clearly ahead: best at 40 an arm (0.128), 0.151 at the familiar sixty; Spread evenly: best at 40 an arm (0.131), 0.146 at the familiar sixty. The split that guards every world puts 32 an arm before the choice and costs at most 21.3% over each world's best.

Designs that change while they run

Patients spent before the choice

A trial that picks the best of eight arms and then confirms it splits its patients between choosing and estimating, and the familiar shape — sixty an arm before the choice, thirty after — spends ninety per cent of a six-hundred-patient budget on the choice. Measured against the effect a reader is told about, the best arm's, that split is nearly right when one arm is modestly ahead and twice as wrong as it needs to be when the arms are alike. A split of thirty-two an arm before the choice is never more than 21.3% worse than the best split for whichever world holds; sixty an arm can be 98.8% worse. The two targets an estimate could serve — the chosen arm's effect and the best arm's — pull the split in opposite directions, and only one of them is what gets published.

What a trial's own first patients buy when they choose the follow-up schedule for the rest, powered for an effect of 0.2. Internal pilots measured on two follow-ups, the schedule that needs no pilot, whose correlation curve chooses the schedule for every later patient. Extra cost over the cheapest schedule at stable shares 0, 0.1, 0.2, 0.3, 0.4, 0.5, 0.6, 0.7: no pilot, two follow-ups throughout, 11.1%, 9.8%, 8.1%, 5.9%, 2.9%, 0.0%, 0.0%, 3.2%; an internal pilot of 20, 10.5%, 9.8%, 9.3%, 7.9%, 5.9%, 3.7%, 4.2%, 5.2%; an internal pilot of 40, 5.9%, 5.7%, 5.6%, 4.7%, 3.4%, 2.0%, 2.4%, 2.5%; an internal pilot of 80, 3.6%, 3.4%, 3.2%, 2.8%, 1.9%, 1.0%, 1.6%, 1.6%. Worst cases: no pilot 11.1%, 20 patients 10.5%, 40 patients 5.9%, 80 patients 3.6%.

What a sample-size calculation was given

A schedule the trial chooses for itself

A separate pilot cannot pay for itself in choosing a trial's follow-up schedule, because its patients are recruited, measured and discarded. A trial can instead measure its own first patients on the schedule that needs no pilot — two follow-ups — fit the correlation curve to them, and give everyone after them the schedule that curve makes cheapest. Those first patients are counted in the analysis and cost no extra visit. Forty of them cut the trial's worst-case excess cost across every curve with adjacent correlation 0.7 from 11.1% to 5.9% in a trial of two hundred an arm, and eighty cut it to 3.6%; twenty buy almost nothing. And because the curve is read from within-arm deviations, the choice cannot see the effect: the pilot's effect estimate is the same whichever schedule it chose.

The textbook (Wald) interval's coverage among studies whose count of 40 lands in the tails. Coverage of the nominal 95% textbook (Wald) interval at 40 trials, conditional on the count being at most k or at least 40 − k, computed exactly over the counts for every true proportion. With k = 2 its highest value anywhere is 88.96%; With k = 5 its highest value anywhere is 94.90%; With k = 8 its highest value anywhere is 95.57%. A set whose highest value stays below 95% is a set of counts on which the label is wrong whatever the proportion is.

Intervals, counted

A count that bets against its interval

A reader who sees only the count can bet against an interval's 95%, and win whatever the proportion is, exactly when some set of counts carries less than 95% at every proportion. Out of forty trials the textbook interval has one — a count of five or fewer, or thirty-five or more, covers at most 94.90% — and the score interval has none: a prior exists under which every one of its forty-one intervals is 96.46% credible, and that prior is the proof that no bet can be found.

The E-optimality certificate along the axis x₂ = 0. The certificate — a fifth of the squared distance of the point's squared radius from one, plus a fifth of the squared difference of its two squared coordinates — along the axis x₂ = 0, with its two pieces drawn alone at full weight: the radial piece, a third of the squared distance from the unit circle in squared radius, which reaches 0.333 here, and the cross piece, half the squared difference of the squared coordinates, which reaches 0.500. The certificate's largest value on the cut is 0.2000, reached at x = -1.0, 0.0, 1.0; the smallest eigenvalue of the nine-point design is 0.2.

A design chosen rather than looked up

A certificate for the worst direction

E-optimality was the one design criterion here whose answer was claimed rather than proved. It has a certificate after all, and on the square it fits on one line — (1⁄5)(1 − x₁² − x₂²)² + (1⁄5)(x₁² − x₂²)², which never exceeds 1⁄5 and touches it at exactly the nine points of the 3² grid. That proves the design with 2⁄5 of its weight at the centre, 1⁄10 at each edge midpoint and 1⁄20 at each corner is E-optimal on the whole square, and it is built from two directions mixed three to two, either of which alone fails.

Two halves of one dataset with 8 far rows of twenty: the trimmed fit's winner and the best half with the other sign. Twenty rows, 8 of them near x = 9 on a line with a reversed slope. The exact trimmed fit keeps the eleven rows whose own line has the smallest residual sum: 5 far rows and 6 clean ones, slope -0.629, residual sum 0.587. The best eleven rows whose line slopes the other way are all clean, slope 0.398, residual sum 0.657 — 1.12 times the winner's.

Regression, and what the summary hides

The other half a trimmed fit rejected

The exact trimmed fit visits every half of the data, so it can report more than its winner: the best half whose line slopes the other way. Whenever the winner is reversed by a far cluster, that other half is the clean line. Printed beside the winner when its residual sum is within 1.70 times — a rule that raises five per cent of clean datasets — it flags 65% of the reversed fits at seven far rows of twenty, 55% at eight and 30% at nine, and no rule built on fit can do better at nine, where the far cluster has become the tighter half by every measure the data hold.

Ten studies every study shares the control: the three combinations read as though independent, by the correlation. Counted on 400,000 null sets of ten one-sided studies at each correlation, every study shares the control. Fisher: 5.00%, 9.54%, 12.83%, 15.01%, 16.63%, 17.88%, 18.80%. Stouffer: 5.00%, 11.51%, 16.29%, 19.54%, 22.20%, 24.23%, 25.86%. Tippett: 4.98%, 4.86%, 4.68%, 4.45%, 4.17%, 3.72%, 3.27%. Smallest of three: 9.66%, 14.44%, 17.94%, 20.41%, 22.55%, 24.34%, 25.88% — at correlations 0, 0.1, 0.2, 0.3, 0.4, 0.5, 0.6. Each combination is read at its critical value for independent studies.

Tests, and the second number

Studies that share a control

Ten comparisons against one control arm of the same size are correlated at exactly one half, and combined as though they were independent, Stouffer's sum rejects 24.23% of sets in which nothing works, Fisher's 17.88%, while Tippett's smallest p-value falls to 3.72%. Repaired with the correlation the design states, each is exact again — and the smallest of the three is then inflated less than for independent studies, 7.05% against 9.66%, because sharing makes the three combinations agree. The two inflations the dependence was expected to stack do not stack.

A cross-entropy fit of a normal proposal to P(Z > 5), stage by stage, fitting mean and spread or the mean alone. Each stage draws a thousand points from the current proposal, keeps the top tenth, and refits the normal to them, each weighted by the target density over the proposal's. Fitting the mean alone, the levels are 1.24, 2.99, 4.59, 5.00 and the fit reaches 5 at stage 4, ending at N(5.199, 1). Fitting mean and spread from the same seed, the spread goes 1.000, 0.456, 0.244, 0.096, 0.054, 0.043 over the first six stages, roughly halving each time, and after 30 stages the level has stalled at 3.728 with a spread of 1.0e-6, never reaching 5.

What makes it checkable

A proposal fitted to its own draws

The cross-entropy method fits an importance-sampling proposal from its own pilot draws, and asked to fit a normal's mean and spread to P(Z > 5) it fails before the question of variance arises: the spread halves at every stage, the level stalls near 3.7, and 95% of runs never reach the threshold, so the interval covers 1.1% of the time. Its ideal end point, the normal closest to Z conditioned past 5, is N(5.187, 0.181²), which has an infinite variance inside its own draws' reach and covers 93.7% at a thousand draws and 90.8% at ten thousand. Fitting the mean alone lands within a tenth of the best shift and covers 94.5%.

The bias each model puts into the treatment effect when sixteen earlier controls stepped once. Sixteen earlier trials of two hundred, the first eight a step below the last eight, which sit at the current control's level; the current trial has fifty patients an arm and no treatment effect; 1,500 trials at each step. Exchangeable trials: -0.003, 0.020, 0.041, 0.056, 0.063, 0.065, 0.054. A line in time: -0.003, -0.016, -0.029, -0.041, -0.052, -0.067, -0.075. A change point: -0.003, 0.003, 0.003, -0.001, -0.002, -0.003, -0.003 — at steps of 0, 0.05, 0.1, 0.15, 0.2, 0.3, 0.5.

The spread, and its own uncertainty

A history that stepped

When sixteen earlier control arms stepped once — the first eight a fifth of a standard deviation below the last — borrowing them as exchangeable flatters a treatment with no effect by 0.063 and stops borrowing, and fitting a line through them penalises it by 0.052. A model with a change point is unbiased at every step size, borrows more the larger the step, 512 patients at a fifth, and puts two thirds of its belief on the right place for the change. Against a steady drift it is the one that fails, so each of the three is safe only against the shape of history it assumes.

What the sixteen-run factorial's surviving runs estimate when about 1.3 runs are lost, by why they were lost. A 2⁴ factorial fitting eleven coefficients; true A = 1, B = 0.5, AB = 0.5, everything else 0, noise 1; 20,000 datasets. Runs are lost when the response exceeds 2.5, or at random at the high corner of A and B, or at random anywhere, each losing 1.26 runs on average. Bias of the fit on the surviving runs — lost at random: A 0.001, B 0.003, AB 0.000, C -0.002; lost at the high corner: A 0.003, B 0.001, AB 0.000, C -0.000; lost when the response passes the threshold: A -0.131, B -0.120, AB -0.117, C -0.000.

Decided before the data

A run lost for a reason

A sixteen-run factorial that loses a run at random loses precision and nothing else. One that loses a run because the process failed — the response passed a threshold — loses about the same number of runs and biases exactly the effects that pushed the response there: an interaction of 0.5 reads 0.383, a main effect of 1 reads 0.869, and the interval around each still covers about 94%. Treating the lost runs as censored above the threshold overshoots with eleven coefficients and works with six, because a run's own leverage decides how much a censored observation pulls its own estimate.

Seven ways to report the height at the setting a response-surface analysis recommends, at noise 2. Bias and root mean squared error of the reported height about the true height at the chosen setting, over 2,000 studies with a central composite design of thirteen runs, or the same design run twice. 13 runs, the fit's own height: bias 0.884, error 1.537. 13 runs, optimism bootstrapped away: bias 0.183, error 1.396. One confirmation run alone: bias -0.005, error 2.005. Corrected fit and one confirmation run: bias 0.056, error 1.121. 26 runs, the fit's own height: bias 0.475, error 0.998. 26 runs, optimism bootstrapped away: bias 0.050, error 0.924. 26 runs split: choose on 13, estimate on 13: bias -0.014, error 1.213.

The surface between the corners

The height at the chosen setting

The height a response-surface fit predicts at the setting it recommends reads high, because the setting was chosen where the fit was highest. The obvious repair — choose on some runs, estimate on the rest — is impossible in the usual thirteen-run design, which has nine distinct settings where two separate fits need twelve. A parametric bootstrap of the optimism removes four fifths of it at no cost in runs, 0.884 down to 0.183 at twice the noise. With the design run twice, correcting the full fit beats splitting it: an error of 0.924 against 1.213, at a better setting.

Where three vocabularies of 5 values put their cuts, under the honest forecasts they divide. The density of the honest probability at full signal, piled toward small values because the event happens 37.4% of the time, and below it three ways of cutting it into 5 groups, each printing its group's event rate. 5 equal-width bins: cuts at 0.200, 0.400, 0.600, 0.800, printed values 0.075, 0.295, 0.497, 0.698, 0.904, resolution lost 0.003454. 5 equal-mass groups: cuts at 0.066, 0.211, 0.422, 0.695, printed values 0.025, 0.132, 0.311, 0.554, 0.850, resolution lost 0.004046. the best 5: cuts at 0.145, 0.339, 0.552, 0.777, printed values 0.054, 0.236, 0.441, 0.662, 0.892, resolution lost 0.003193. The density is cut off at 3.2 near zero, where it grows without bound. The best vocabulary's cuts sit halfway between neighbouring printed values, and its printed values sit at their groups' event rates; no other partition into 5 groups loses less.

A forecast that is a probability

Five values chosen by the forecasts

The vocabulary of five calibrated values that loses least on the Brier score puts its cuts at 0.145, 0.339, 0.552 and 0.777, and gives up 0.003193 of resolution against 0.003454 for equal-width bins and 0.004046 for equal-mass groups. Eleven such values beat tenths by 18.5% — but only once someone knows where to cut. Fitted on a record of two thousand forecasts the same eleven add 0.001547, about twice what tenths add with nothing fitted, and they draw level only near twelve thousand. For users acting at chances near one in ten, a vocabulary cut for them lowers their regret by a factor of 7.5 and costs the Brier score nearly nine times as much.

Coverage under a drifting scale, with the quantile taken over fewer and more recent scores. The noise scale grows linearly across the sample to 1 + v times its starting value; 4,000 draws at each v. Worst coverage over the sweep: all 199 scores 85.63%, the last 99 90.88%, the last 39 93.42%, the last 19 93.53%. At v = 2.12, where the best of three detectors first fires 80% of the time, they cover 88.11%, 91.86%, 94.02%, 94.45%. Every window covers 95% when nothing drifts.

Coverage without a distribution

A quantile over the recent scores

A noise scale that grows across the sample takes a split conformal interval from 95% to 85.63%, and the best detector cannot see most of that loss. Take the quantile over the last thirty-nine calibration scores instead of all 199 and the worst coverage across the whole sweep is 93.42%, for 3.7% more width when nothing has drifted. The same window covers 91.30% where all 199 cover 93.53% under strongly correlated errors — and switching to it only when the detector fires is worse than either, because the detector fires on correlation too.

Coverage of the cluster-robust slope interval at six, ten and twenty clusters of unequal size, by reference. 5,000 studies of 300 rows at each setting, within-cluster correlation 0.2. 6 clusters, equal sizes: 89.1%, 92.6%, 96.0%; 6 clusters, 5:1, big at the edges: 80.1%, 88.1%, 95.2%; 6 clusters, 5:1, big at the centre: 93.8%, 95.4%, 96.8%; 6 clusters, 15:1, big at the edges: 76.2%, 86.8%, 94.5%; 10 clusters, equal sizes: 91.1%, 93.0%, 95.8%; 10 clusters, 5:1, big at the edges: 86.3%, 90.3%, 94.7%; 10 clusters, 5:1, big at the centre: 94.5%, 95.7%, 96.4%; 10 clusters, 15:1, big at the edges: 84.9%, 89.6%, 94.8%; 20 clusters, equal sizes: 92.9%, 93.8%, 95.1%; 20 clusters, 5:1, big at the edges: 90.9%, 92.7%, 94.8%; 20 clusters, 5:1, big at the centre: 94.5%, 95.0%, 95.6%; 20 clusters, 15:1, big at the edges: 90.6%, 92.4%, 94.7% — for the usual variance on G − 2, the bias-reduced variance on G − 2, and the bias-reduced variance on its effective count.

A standard error for a model that is wrong

An effective number of clusters

Ten clusters of thirty rows, a covariate spread evenly across them, and a cluster-robust interval for the slope read against a t on G − 2 = 8 covers 91.1%. The slope needed about five degrees of freedom, not eight, because the two outermost clusters carry 49% of its variance and the middle two 0.6%. A count computed from the sizes and positions before any outcome is seen — 4.45 here, 3.32 when the big clusters sit at the edges — with the bias-reduced variance covers between 94.5% and 96.8% in all twelve layouts measured, where the usual interval on G − 2 covers between 76.2% and 94.5%.

Power of four tests of two survival curves, in three shapes of treatment effect, at 50, 100 and 200 a side. 6,000 trials at each setting, dropout 0.1 a year, follow-up to three years. hazard halved throughout, 50 a side: log-rank 64.9%, best of eleven horizons 51.7%, restricted mean at 3 61.1%, one test for all twelve 56.6%; hazard halved throughout, 100 a side: log-rank 91.8%, best of eleven horizons 81.0%, restricted mean at 3 88.4%, one test for all twelve 86.0%; hazard halved throughout, 200 a side: log-rank 99.7%, best of eleven horizons 98.4%, restricted mean at 3 99.4%, one test for all twelve 99.3%; halved for a year, then nothing, 50 a side: log-rank 18.5%, best of eleven horizons 32.1%, restricted mean at 3 26.6%, one test for all twelve 30.8%; halved for a year, then nothing, 100 a side: log-rank 29.3%, best of eleven horizons 51.7%, restricted mean at 3 42.5%, one test for all twelve 50.2%; halved for a year, then nothing, 200 a side: log-rank 51.4%, best of eleven horizons 81.4%, restricted mean at 3 70.3%, one test for all twelve 80.2%; curves that cross, 50 a side: log-rank 5.1%, best of eleven horizons 45.7%, restricted mean at 3 10.4%, one test for all twelve 44.0%; curves that cross, 100 a side: log-rank 5.2%, best of eleven horizons 76.7%, restricted mean at 3 16.4%, one test for all twelve 75.5%; curves that cross, 200 a side: log-rank 5.2%, best of eleven horizons 96.7%, restricted mean at 3 26.5%, one test for all twelve 96.6%.

When the data stops early

One test for a curve that might cross

The log-rank statistic and the differences in restricted mean survival at eleven horizons are one Gaussian vector under no effect, and its correlations are closed — from −0.461 at half a year to −0.949 at three, where the log-rank statistic is nearly the restricted mean itself. So one critical value, 2.374, prices the largest of all twelve. At 100 a side it keeps 93.6% of the log-rank test's power when the hazard is halved throughout and 98.5% of the best horizon's when the curves cross, where the log-rank test has none. Running both tests and keeping either rejection rejects 8.67% of trials with no effect.

The value that is not there

A variable that moves recording

A selection model fitted to a skewed outcome that is missing at random reports selection that is not there on three studies in four. Give it a variable that shifts who is recorded and has no place in the outcome — strong enough to carry 29% of the recording index's variance — and the false reports fall to 7.5%, the slope from 1.034 to 0.613 against a truth of 0.6. Leave the same variable out of the model and it does harm instead: false reports reach 100%, and where the outcome really does decide recording, the estimated pull falls from 1.18 to 0.78.

Sixteen groups from two clusters: the true effects, the observed means and the pooled estimates, with the kurtosis of each. One dataset of 16 groups of four observations each, effects drawn from two clusters with total spread 2, noise 3. The fitted spread is 1.701, so every estimate is pulled 43.7% of the way to the centre -0.213. Kurtosis: true effects 1.203, observed means 2.348, pooled estimates 2.348 — the last two identical, because one is an affine image of the other.

Groups that borrow

The shape the estimates keep

Partial pooling was suspected of destroying the evidence of its own misfit: compressing a two-cluster population of group effects towards one centre before any test could see the clusters. With groups of equal size it destroys nothing, because every estimate moves the same fraction of the way to the same place and the estimates keep the means' shape exactly — except when the fit pools completely, as it does on 29.9% of eight-group datasets at a spread of one. The evidence was never there: a shape check has 6.5% power at eight groups. With groups of unequal size the pooled estimates see the clusters better than the raw means do.

Five 95% intervals for an AR(1) forecast 6 steps ahead at φ = 0.85, fifty observations. Coverage on 4,000 series, the same series for every interval, each simulated interval built from 499 simulated futures. The plug-in formula: 88.48%. The formula, all three repairs: 92.80%. Simulated: parameters drawn: 92.55%. Simulated: residual bootstrap: 88.25%. Simulated: bootstrap, bias removed: 93.47%.

Comparing two forecasters

An interval built from simulated futures

A forecast interval read off simulated futures needs no delta method and no normal multiplier, and was expected to close the residual the three repairs to the formula leave. It does not close it on its own: the plain residual bootstrap covers 88.25% six steps ahead at φ = 0.85, the plug-in formula's 88.48% to within the count, because it simulates around the same biased persistence. With that bias removed inside the bootstrap it covers 93.47%, the best of five intervals, and its shortfall stops growing with the horizon — 93.80% at twelve steps, where the repaired formula covers 91.85%.

Testing for flatness at 5% before choosing the interval for a squared mean. Coverage of four nominal 95% intervals for μ², exact, against the true mean's distance δ from the flat point in standard errors. The tangent interval Z² ± 2z|Z| has its worst, 85.98%, at δ = 1.45. The second-order interval read off χ²₁ is right only at δ = 0 and falls to 34.22% at δ = 2. The two-stage rule, which uses the second-order interval when a 5% test does not reject flatness, has its worst, 49.72%, at δ = 1.96. The squared exact interval never falls below 95%.

The distribution itself

Testing for a flat point first

Test whether the gradient is zero, and if the test does not reject, read the interval off the second-order law that holds at a stationary point. For a squared mean that two-stage rule covers about 50% at its worst whatever the pretest's level — 49.72% with a 5% test, where the tangent interval it was meant to rescue never falls below 85.98% — because its worst sits exactly where the true distance equals the test's critical value, half the samples are declared flat there, and the second-order interval cannot reach the truth from any of them.

Reversals that are not errors

A correction built on a retest

Tweedie's correction for regression to the mean needs the error variance, and a study gets it from a few people measured twice. Twenty of them are enough: with normal errors the estimated correction then beats the correlation's rule on 73% to 77% of studies of a thousand readings from a heavy-tailed population, though its variance is uncertain by a third. What twenty cannot reveal is the error's shape. Laplace errors of the same variance make the correction overstate the lead a top group keeps by about 0.17, the plain rule then wins on most studies, and a study needs about two hundred retest pairs before a check on its own differences notices.

The prior, doing visible work

A prior wrong about its own spread

A prior can be centred exactly where the truths lie and still be wrong about how far they spread. Ten times too confident — worth a hundred observations about proportions whose population is worth ten — its 95% credible intervals cover 48.2% of the population's studies at twenty trials, and nothing in the interval shows it: it is 0.456 of a flat prior's width, against 0.436 for a prior whose hundred observations' confidence is earned. A prior with tails too thin misses the one study in ten that comes from somewhere unusual a third of the time, and a flat component of two per cent brings that study's coverage from 65.6% to 84.0%.

Coverage of the population mean from two units, by the true spread between units. 4,000 two-unit studies at each true spread, ten observations a unit, within-unit standard deviation 1.2. exact, on one degree of freedom: 94.97%, 95.50%, 94.95%, 94.83%, 95.15%, 95.20%, 94.67%. spread supplied as 1: 100.00%, 100.00%, 99.92%, 95.53%, 81.85%, 70.03%, 51.55%. half-normal, scale 1: 100.00%, 100.00%, 99.78%, 94.63%, 86.25%, 79.70%, 68.38%. half-Cauchy, scale 1: 100.00%, 100.00%, 100.00%, 98.98%, 95.50%, 92.38%, 88.00%. inverse-gamma(0.001, 0.001) on the variance: 100.00%, 100.00%, 100.00%, 99.15%, 97.05%, 95.28%, 92.65% — at spreads 0, 0.25, 0.5, 1, 1.5, 2, 3. The exact interval holds 95% at every spread; every integrated one over-covers when the spread is small and under-covers when it is large, and where it crosses 95% is set by the prior's tail.

Hierarchy past one number

A prior on the spread between two sites

Integrate the between-site spread of a two-site study under a half-normal prior of scale 1 and the interval for the overall mean is 3.01 wide and covers 94.63% when the true spread is 1 — the supplied interval again, under another name. At a true spread of 3 it covers 68.38%. Every prior tried covers 95% averaged over its own draws and none covers it at every spread; each holds up to about its own scale, because two sites move the posterior median of the spread by less than a third of what the truth moves.

The shape one real modifier leaves on a table of eight characteristics, and one trial's table. Expected interaction z when characteristic 1 modifies the effect at h = 1: 2.80, 2.00, 2.00, 2.00, 0.00, 0.00, 0.00, 0.00 — the real row 2.80, its three nested neighbours 0.713 of that, the four unrelated characteristics nothing. One seeded trial of 400 reads 1.91, 1.90, 2.06, 1.95, 0.14, 0.33, 0.39, 2.08.

An interval read beside something else

The pattern a cause leaves on its neighbours

A characteristic that modifies a treatment's effect raises every characteristic that overlaps it, in proportion to the overlap, and fitting that pattern was supposed to say which one is the cause. Fitted with the noise's own correlation it names the largest row on every trial, because the noise draws the same pattern — so the 54.4% at which the largest row is right among nested characteristics is the most any reading of the table can manage, and the honest answer is a set of about five.

How often a league table's own data choose a bent centre over a straight one. Over 400 tables of a hundred groups each. The quadratic's curvature coefficient is significant at 5% on 5.3% of tables whose relation is straight, 14.5% of tables whose relation is flattening below the median, 29.3% of tables whose relation is steepening below the median; its average AIC weight is 0.374, 0.456, 0.558.

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

A centre chosen by its own table

A league table that picks its centre's shape from its own data — a line unless a curvature test says otherwise — picks the line on 85.5% of tables whose relation flattens below the median, because the bend lives where the groups are smallest and noisiest. Its bottom ten then flags like the line's: 2.61 innocent small groups a table against 2.19 for a quadratic told the shape. Always fitting the quadratic costs 0.07 of a correctly flagged group when the relation is straight and matches the told answer when it bends, and a flag set by probability carries the choice through a mixture of the two.

Series that move together

A factor estimated from the panel

When sixteen pairs feel a common shock with loadings from a half to one and a half, removing the cross-sectional average leaves the pooled test rejecting an unrelated panel 13.3% of the time. Estimating the factor and each pair's loading instead brings that to 8.9% — and no further, because each loading comes from the same two hundred dates however many pairs there are — and it costs power against the average at the right critical value, 73.8% against 82.5%. Removing the shocks as observed restores 4.5% exactly and finds a shared relation 7.5% of the time: a series tied to its partner carries the partner's factor in its level, not its own shock.

The tail past the last observation

Where the extremal index matters to a return level

A return level from a declustered fit depends on how often clusters arrive, which is the extremal index estimated from the same record. For a level reached once in two periods of a twenty-period record the index's error is a quarter to four fifths of the level's variance, and an interval that leaves it out covers 59.0% when clusters are long; put in, 90.0%. For a level reached once in a hundred periods its share is under two and a half per cent and adding it changes no interval at all — what fails there is the shape, fitted from however many clusters the dependence left: 82.3% coverage from forty-six clusters, 65.7% from nineteen.

How many units a range needs to let at most r of the next hundred outside, fixed, learning or forgetting. 95% of the time, for any continuous population. At most 1: fixed 637, window 564, learning 512; At most 2: fixed 300, window 236, learning 197; At most 5: fixed 107, window 64, learning 36; At most 10: fixed 50, window 27, learning 4. The window counts are from 20,000 lots of uniform draws; the other two are exact.

The interval that holds observations, not a mean

A range that forgets

A band set from the range of the last sixty-four units flags each unit of a stable lot with probability exactly 2/65, for ever, and its flags arrive as if independent — so a promise of at most five outside in the next hundred costs sixty-four units, between the learning range's thirty-six and the fixed range's hundred and seven. What it was supposed to buy, a flag that lasts as long as a step and then stops, it cannot give: it absorbs a two-sigma step as fast as the learning range, 1.89 flags in ten units against 1.93, because it learns from what it flags. Refusing to learn from a flag makes it a fixed range that costs 141.

How far each estimator errs when instruments are cells of unequal size and the confounding moves with them, μ² = 8. Thirty-three cells of 2 to 15 units, thirty-two instruments, 1,000 draws a point. At η = 0, 1, 2: two-stage least squares 0.286, 0.387, 0.593; likelihood, Bekker's interval 0.049, 0.534, 0.830; jackknife instrumental 0.146, 0.325, 0.689; jackknife likelihood, robust interval 0.066, 0.066, 0.195.

A variable that moves one thing only

Cells of unequal size and an error that follows them

Thirty-two instruments that are the indicators of cells holding 2 to 15 units each, and confounding whose variance is larger in the small cells. Limited-information maximum likelihood, the estimator that came out least biased with many instruments, then errs by 0.534 at a concentration of 8 — further than two-stage least squares — and Bekker's interval covers 74.8%. The jackknife version of the likelihood, which never lets a row's own leverage reach its own fitted value, errs by 0.066 and its robust interval covers 90.6%; at eight times the strength, 94.8% against Bekker's 87.3%. On normal instruments the same unequal variance costs almost nothing, because their leverages are nearly equal.

What a diagnostic plot is showing

Residuals of a model the data chose

Five columns picked by a forward search from twenty candidates that have nothing to do with the outcome leave residuals that show a skewed error 36.8% of the time, where five columns fixed in advance show it 65.4% — the power of a fit of 13.4 fixed columns. Against light-tailed errors the chosen fit's plot is blind, 8.5% against 34.5%. Simulating the search on normal errors gives a band that holds 5%, which the ordinary band already nearly did; the level was never what broke. A reader told the final model has five columns is reading a plot with the power of thirteen.

The interval for a finding's effect given that it cleared its threshold, against where its estimate landed. Threshold c = 2.8. At z just past it the selective 95% interval runs from −0.58 to 0.95; at z = 3.8, from 0.18 to 5.73; at z = 6.3, from 4.31 to 8.26, against the ordinary z ± 1.96.

Corrections, and what each controls

An interval that knows its finding was found

An interval for one Benjamini–Hochberg finding can be read from the distribution of its estimate given that it cleared the threshold it had to clear. It covers the finding's effect 94.8% of the time with real effects of two standard errors, against the ordinary interval's 87.0%, and it covers the most prominent finding 91.3% of the time where the ordinary one covers 72.4%. The price is width — a median 5.06 standard errors against 3.92 — and something larger: for three findings in four at that effect size the interval reaches back past zero, so a finding that cleared the line is, once the line is accounted for, not distinguishable from nothing.

How often a trial with nothing to find shows a Simpson reversal somewhere, by how many variables are searched and how. Trials of eighty whose treatment helps every patient by six points, twenty baseline variables tracking the risk with correlations from 0.95 to 0.10; 4,000 trials. Searching the strongest 1, 2, 5, 10, 20: every cut, 23.4%, 30.7%, 41.0%, 46.9%, 49.0%; the deciles, 13.2%, 19.4%, 27.9%, 33.3%, 36.4%; the median, 4.4%, 6.9%, 11.3%, 14.4%, 16.2%.

When the stratified answer and the pooled one disagree

Every variable, every cut

Slide the cut along every one of twenty baseline variables in a randomised trial of eighty whose treatment helps every patient equally, and some variable shows a Simpson reversal at some cut in 49.0% of trials — a coin toss with nothing to find. The twenty scans do not add like independent chances: if they did they would reverse 92.4% of the time. They read one patient risk between them, and the weak variables seldom reverse at all, so the strongest five supply 41.0 of the 49.0 points. A trial that shows one reversal usually shows several: 4.8 variables on average.

Two tests, a threshold, and the rate they are read against

A threshold reported with its interval

Resample a validation study of a hundred diseased and three hundred healthy people, refit the binormal model each time, and read off the threshold each resample recommends. Far from the prevalence at which the best threshold jumps to flagging everyone, the interval is tight — flagging 12% to 24% of healthy people at a prevalence of 5%. Near the jump, the median study's interval runs from flagging under half of the healthy to flagging everyone, and 91% of intervals cross the jump. The two ends differ by fifteen false alarms' worth of harm per hundred people, and no rule for choosing inside the interval beats the study's own choice at every prevalence.

How often a test of a supplied cointegrating relation rejects it, by how wrong it is and how long the sample is. 800 systems a point. At 100, 200, 400, 800 observations the right relation is rejected 9.4%, 5.4%, 5.4%, 6.4% of the time; one with c = 0.9, 19.9%, 37.8%, 78.5%, 98.5%; c = 1.1, 16.8%, 37.9%, 76.8%, 97.5%.

Three series, and a count

A restriction the data can check

A rank-two system of three series is identified by exactly two restrictions on its relations, and any two that describe the estimated plane fit it equally well — their forecasts agree with the unrestricted fit's to the last digit, so the data can neither confirm nor refuse them. Supply one relation in full instead, one restriction more than identification needs, and the surplus becomes a test: a relation a tenth wrong is rejected 37.8% of the time at two hundred observations and 98.5% at eight hundred, the error found half the time halving as the sample doubles. A right relation buys the forecast almost nothing; a fifth wrong costs 13% of it at two hundred observations and 25% at eight hundred.

The bias a tolerance on the second moments leaves where a square drives both the assignment and the outcome. 600 samples a point. Bias at δ = 0, 0.02, 0.05, 0.1, 0.2, 0.5: −0.0074, 0.0500, 0.1353, 0.2782, 0.5473, 0.6983; coverage 89.7%, 89.5%, 72.4%, 26.5%, 1.0%, 1.0%. The tolerance spent in full at the outcome's slope on the square would give 2·δ·√2: 0.0566, 0.1414, 0.2828, 0.5657 at the four smaller values; balancing the means alone gives 0.6973.

Weighting one sample into another

A balance allowed a tolerance

Weights that balance the means exactly and the second moments only to within a tenth of a standard deviation were supposed to keep the second-moment repair and recover the samples exact balance loses. Where a square drives both the assignment and the outcome they keep neither half of the repair: the bias is 0.2782 against −0.0074 with exact balance, and the interval covers 26.5%, because the weights spend the whole tolerance — every second-moment gap sits at the edge of its band — and the outcome converts a gap of a tenth into bias at its own slope, 2·δ·√2 = 0.283. At thin overlap the same tolerance does recover samples: 89.0% have weights at all, against 62.0% with exact balance.

Six intervals, one of them honest by right. How often each rule's reported 95% interval covers the true coefficient under a five-period moving average, over 1000 draws of 120 rows, for the most persistent predictor (its own lag-one correlation 0.9) and the white one. The law's own covariance covers 94.9% and 94.1%. Least squares covers 65.0% on the persistent predictor and 94.4% on the white one; a fitted ρ̂ 93.0% and 96.3%; the two-step band 86.5% and 97.3%. The joint fit covers 73.2% and 71.4% — short on both, and short on the white predictor where every other rule is honest — and counting its eight band coefficients gives 76.1% and 73.5%.

When the observations repeat each other

The interval the joint fit reports

Maximising a regression's coefficients and an eight-lag covariance band together gives a better estimate than plugging the band in. It also prints an interval that covers 71% to 85% of the time where 95% was promised — on the white predictor too, where every other rule is honest — because it reports almost the precision of the law's own covariance and delivers less than half of that advantage. Counting the eight lags it estimated buys one to two points.