Normal Distribution
nothing is called 95% until it has been counted
The collection

Every essay — page 10

Essays 217 to 240 of 436, in the same order.

More arms than two

Minimisation balances a trial by making the arms' counts even inside every factor level. 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 — while the ratio a trial was designed to deliver quietly disappears unless the score was told about 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.

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.

8 figures · Assignment, part 6 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.

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.

9 figures · Assignment, part 7

The best of a set, and what the search costs

Comparing two forecasters is a test. Comparing eight 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 about two independent comparisons and eight separate problems carry eight, so a correction that charges for the number of models is wrong in both directions. The reference distribution has to be over the whole set — and once it is, the models nobody would have run turn out to cost more than the ones that were close.

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.

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.

9 figures · Forecast, part 5 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.

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.

9 figures · Multiplicity, part 5 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 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.

9 figures · Multiplicity, part 6 The distribution the table does not have. 599 series simulated from the smaller model fitted to one comparison's own data, the whole rolling comparison re-run on each, and the ordinary statistic recorded. Under this null the two forecasts are the same forecast in population, so what is left in a sample is the larger model's estimation error and the statistic is centred at -1.134 rather than at zero. Its 95% point is 0.264; the standard normal drawn behind it puts that point at 1.645. Reading this statistic against that curve is not a poor approximation, it is a different distribution: the share of this one above 1.645 is 0.2%.

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.

6 figures · Bootstrap, part 4

What the design is asked to guarantee

Two halves of one question that were never separated: which parameters a design is for, and how much precision is enough. Protecting one parameter of a non-linear model over a range of its own values is a worst case of a ratio of determinants, and it is not a special case of either problem it is made of. Letting the experiment stop when it is precise enough is the adaptation with a theorem against it — the rule stops when its own noise estimate is low, so the interval it produces is short.

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.

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.

9 figures · Criterion, part 6 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.

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.

9 figures · Local design, part 7 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.

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.

8 figures · Stopping, part 5 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.

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%.

8 figures · Stopping, part 6

Balancing what has no levels

Every balancing rule in the two fields before this one reads a level. Age, blood pressure and a baseline score have none, and the first thing that happens to them is that somebody invents some — a choice with a cost available in closed form before any data exists: a median split can see exactly 2/π of a normal covariate, so a rule that balances its two halves perfectly still leaves three fifths of a coin's imbalance. A rule that reads the number instead does not beat that by a factor; it beats it by a rate.

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.

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.

8 figures · Assignment, part 8 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.

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.

9 figures · Assignment, part 9 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.

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.

8 figures · Randomisation, part 3 What balancing several numbers at once costs each of them. The criterion generalises without a word changing — the covariate imbalance becomes a vector and the correction a quadratic form — so the question is what it is worth rather than whether it can be done. At n = 200 with 200 trials per point, a rule balancing one covariate leaves 12.7% of a coin's imbalance in it; balancing eight leaves 23.2% in each. The assignment has a fixed amount of freedom and every covariate added takes a share of it. The rule degrades rather than failing: at eight covariates it is still four times better balanced than a coin, and the eight are being held simultaneously rather than in turn.

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.

8 figures · Blocking, part 2

The set field compares forecasts nobody estimated. A specification search compares a benchmark with a table of variants that all contain it, and two things change at once: every variant is behind before the search begins, by an amount with a closed form in the shape of the table, and the reference distribution for the winner can no longer be resampled from the data — it has to be generated from a model. The repair the nested case asks for, applied row by row, takes a table from its nominal level to a quarter.

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.

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.

8 figures · Forecast, part 6 The distribution of the largest statistic in the table. Fit the benchmark to the whole series, resample its residuals, simulate 199 series in which the null is true by construction, re-run the entire eight-variant search on each, and keep the largest statistic. That is the distribution drawn here, and it is the distribution of the thing a specification search actually reports. It is centred at 1.045 — the maximum of eight statistics is not centred at zero however well each of them behaves — and its 5% point is 2.536. A table read against 1.671 is reading the distribution of one statistic; a Bonferroni correction reads it against 2.577 and is nearly right here, because eight variants that each add a different lag are nearly eight separate chances.

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.

8 figures · Bootstrap, part 5 The ranking on the left, the weights on the right. Eight moving-average forecasts of an AR(1) at φ = 0.4895, the persistence at which the best of them exactly ties the 60-observation benchmark. On the left, each candidate's expected squared error in units of the series' own variance: the smallest belongs to L = 2, at 1.0156. On the right, the weight each carries in the variance-minimising combination of all eight — and the best of them carries 0.00000. The two ends of the family carry 1.0172 of the weight between them, and the combination they make is worth 0.7817, which is 23.0% below the best single forecast. Both columns are closed forms in φ. Which forecast to keep and which forecasts to use are different questions, and this is a set where the answers share nothing.

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.

8 figures · Rank, part 4 Eight encompassing nulls, all of them true at once. The forecast under test is the variance-minimising combination of the eight candidates, and the first-order condition that defines its weights is cov(e_c, e_j) = var(e_c) for every j — so every one of the eight nulls is exactly true simultaneously and every rejection counted here is false. 800 draws of 60 origins. The largest of the eight statistics rejects 25.0% of the time at a nominal 5% and one comparison stated in advance rejects 3.1%, which makes the set worth about 9.1 independent comparisons — nearly the eight it has. Bonferroni, which is far inside its level on a search over accuracy comparisons of the same eight forecasters, is at 4.8% here.

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.

8 figures · Multiplicity, part 7

What the procedure may not read

Two restrictions that were cheap until now. A design for a non-linear model may not read the parameter values, and where the model has two of them the guess is a point in a rectangle: the weights that were exactly 1/√2 become a function, and a design robust in one coordinate turns out to guarantee no more than one built at a single point. A stopping rule may not read the mean it will report — and there is an exact way to obey that, at a price in the width of the interval rather than in the number of observations.

One curve, three designs, and the disagreement is the weights. The compartmental response exp(−θ₁t) − exp(−θ₂t) at the guess θ = (0.2, 1.2), with three designs underneath it. Each mark is a setting and its height is the share of the experiment spent there. The D-optimal design splits the runs equally between two settings — that is the determinant's answer and it is equal for every model of this kind. The design for the first parameter alone puts 1.9% of the experiment at its early setting and the rest at its late one, because the early runs are there to identify the nuisance and nothing more. The design that protects a 4-fold rectangle needs 3 settings and spends 9.1% at the earliest of them.

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.

9 figures · Local design, part 8 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.

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.

9 figures · Criterion, part 7 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.

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.

8 figures · Stopping, part 7 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 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.

8 figures · Nuisance, part 2

The shape the covariate enters by

Every balancing rule in the two fields before this one optimises one over the variance of the treatment estimate in a model where the covariate enters linearly — which is not an assumption about the analysis, it is what the criterion is. Balancing the mean of a covariate removes exactly 2/π of the imbalance in a median split of it, a quarter of a threshold in the tail, and nothing at all from a quadratic. The ranking of the rules reverses between shapes, and against one of them every rule here is worse than a coin.

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.

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.

8 figures · Blocking, part 3 A threshold in the tail is a threshold nothing balances. The share of a coin's imbalance in an indicator 1{x > c} that survives a rule which balances the covariate itself. The smooth curve is 1 − ρ² with ρ = φ(c)/√(p(1−p)), a closed form with no trial in it; the points are counted over 500 trials of 200 units at each threshold. At the median the two agree that about a third survives — the removed share is exactly 2/π — and by two standard deviations 86.9% survives. The closed form is exact in the limit and optimistic by a few points at this many units, because the rule balances the sample's mean rather than the population's.

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.

8 figures · Blocking, part 4

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