• I.e., can you act like a physicist?
• Fully sequential trials are almost never used, and may be more useful than adaptive trials
• What keeps a researcher from collecting data until there is sufficient evidence in one direction, or until she runs out of time, money, or patience?

• Traditional frequentist statistics
• Fixed budgets
  • Government grant project budgets vs. portfolio budgets
    
    
• Wouldn’t it be more logical to
  • direct more resources to promising studies?
  • direct resources away from unpromising studies (high prob. of inefficacy or only trivial efficacy)?

• The probability of a positive result when there is nothing?
• The probability that a positive result turns out to be nothing?
  
  
• How surprising is our data if the treatment has no effect?
• The probability of all possible levels of efficacy?

• If you like the first, you like the frequentist status quo
  • p = P(data more impressive than ours if treatment is ignorable)
• If you like the second, you have Bayesian tendencies & like posterior probabilities
  • P(unknown effect > c | data, prior information)
  • E.g. P(BP reduction > 0 mmHg),
    P(BP reduction > 5 mmHg),
    P(similarity) = P(change in [-3, 3] mmHg)

• Insufficient patient recruitment
• Equivocal result
  • At planned sample size result not “significant”
  • Uncertainty intervals too wide to learn anything about efficacy
  • The money was spent

• Over-optimistic power calculation
  • using an effect size > clinically relevant
  • if effect is “only” clinically relevant, likely to miss it
• Fixed sample size
• Losing power in the belief that α is something that should be controlled when taking multiple data looks
• Insensitive outcome measure

• Little evidence the treatment works
• Usually the study could have been stopped much sooner

• Frequentist (traditional statistics): need a final sample size to know when α is “spent”
• Fixed budgeting also requires a maximum sample size
• Sample size calculations are voodoo
  • arbitrary α, β, effect to detect Δ
  • requires accurate σ or event incidence
• Physics approach: experiment until you have the answer

• Yes for budget, if fixed
• No sample size needed at all if using a Bayesian sequential design
• With Bayes, study extension is trivial and requires no α penalty
  • logical to recruit more patients if result is promising but not definitive
    0.7 < P(benefit) < 0.95
  • analysis of cumulative data after new data added merely supersedes analysis of previous dataset

• α = type I assertion probability = P(p < 0.05 | H₀) typically
• It is not the probability of making an error in acting as if a treatment works
• It is the probability of making an assertion of efficacy (rejecting H₀) when any assertion of efficacy would by definition be wrong (i.e., under H₀)
• α ⇑ when as # data looks ⇑

• α includes the probability of things that might have happened
  • even if we have very strong evidence of efficacy at a given time, our design had the possibility of showing an efficacy signal at other times had efficacy=0
  • Bayesian methods deal with what did happen and not what might have happened

• Asking one to compute α for a Bayesian design is like asking a poker player winning > $10M/year to justify his ranking by how seldom he places bets in games he didn’t win.

• Controlling α leads to conservatism when there are multiple data looks
  • Bayesian sequential designs: expected sample size at time of stopping study for efficacy/harm/inefficacy ⇓ as # looks ⇑

• The probability of being wrong in acting as if a treatment works
• This is one minus the Bayesian posterior probability of efficacy (probability of inefficacy or harm)
• Controlled by the prior distribution (+ data, statistical model, outcome measure, sample size)
• Example: P(HR < 1 | current data, prior) = 0.96
  ⇒ P(HR ≥ 1) = 0.04 (inefficacy or harm)

• It controls the reliability of evidence at the decision point
• Not the pre-study tendency for data extremes under an unknowable assumption
• Simulation examples: bit.ly/bayesOp

• Not having an α penalty
• Being directional (no penalty for possibility of making a claim for an increase in mortality)
• Allowing for infinitely many data looks
• Borrowing information when there is treatment effect modification (interaction)

• Because they use low information outcome: time to binary event
• Do not distinguish a small MI from death and completely ignore death after a nonfatal MI
• Need 462 events to estimate a hazard ratio to within a factor of 1.20 (from 0.95 CI)
• Need 384 patients to estimate a difference in means to within 0.2 SD (n = 96 for Xover design)
• Event incidence ⇓ (censoring ⇑) ⇒ power for time to event = power of binary outcome

• Timing and severity of outcomes
• Handle
  • terminal events (death)
  • non-terminal events (MI, stroke)
  • recurrent events (hospitalization)
• Break the ties; the more levels of Y the better
  fharrell.com/post/ordinal-info
• Maximum power when there is only one patient at each level (continuous Y)

• In a given week or day what is the severity of the worst thing that happened to the patient?
• Expert clinician consensus of outcome ranks
• Spacing of outcome categories irrelevant
• Avoids defining additive weights for multiple events on same week
• Events can be graded & can code common co-occurring events as worse event

• Can translate an ordinal longitudinal model to obtain a variety of estimates
  • time until a condition
  • expected time in state
  • probability of something bad or worse happening to the pt over time, by treatment
• Bayesian partial proportional odds model can compute the probability that the treatment affects mortality differently than it affects nonfatal outcomes

• Ordinal longitudinal model also elegantly handles partial information: at each day/week the ordinal Y can be left, right, or interval censored when a range of the scale was not measured

• 0=alive 1=dead
  • censored at 3w: 000
  • death at 2w: 01
  • longitudinal binary logistic model OR ≅ HR
• 0=at home 1=hospitalized 2=MI 3=dead
  • hospitalized at 3w, rehosp at 7w, MI at 8w & stays in hosp, f/u ends at 10w: 0010001211

• 0-6 QOL excellent–poor, 7=MI 8=stroke 9=dead
  • QOL varies, not assessed in 3w but pt event free, stroke at 8w, death 9w: 12[0-6]334589
  • MI status unknown at 7w: 12[0-6]334[5,7]89
• Can make first 200 levels be a continuous response variable and the remaining values represent clinical event overrides

• Proportional odds ordinal logistic model with covariate adjustment
• Handles intra-patient correlation with a Markov process or other longitudinal models
• Extension of binary logistic model
• Generalization of Wilcoxon-Mann-Whitney Two-Sample Test
• No assumption about Y distribution for a given patient type
• Does not use the numeric Y codes

• B:A odds ratio
• P(B > A)
  c-index; concordance probability ≅ OR^0.65/(1 + OR^0.65)
  fharrell.com/post/po – does not assume proportional odds!
• Probability that Y=y or worse as a function of time and treatment
  does assume PO but the partial PO model relaxes this
• Time gained in good states (difference in mean time unwell)
• Bayesian partial PO model: compute posterior P(treatment affects death differently)

• VIOLET (Petal Network, NEJM 381:2529, 2019)
• Early high-dose vitamin D\(_3\) for 1360 D\(_3\)-deficient critically ill adults
• Primary endpoint: mortality (slight evidence for increase with D\(_3\))
• Ordinal endpoint collected each day for 28 consecutive days

• Simulation of VIOLET-like studies

Details at hbiostat.org/R/Hmisc/markov/sim.html

• Increase power by breaking ties
• Get close to the raw data
• Relevant to patients
• Respect timing and severity of outcomes
• Can do automatic risk/benefit trade-offs by including safety events in an ordinal outcome scale

• Has almost nothing to do with baseline balance across treatments
• Has to do with outcome heterogeneity within a treatment group
• Adjustment for strong baseline prognostic factors increases Bayesian and frequentist power for free
• Does this by getting the outcome model more correct
  Example: older patients die sooner; pts with poor baseline 6m walk test have poor post-treatment 6m walk test

• Provides estimates of efficacy for individual patients by addressing the fundamental clinical question:
  • If I compared two patients who have the same baseline variables but were given different treatments, by how much better should I expect the outcome to be with treatment B instead of treatment A?

• Provides a correct basis for analysis of heterogeneity of treatment effect
  • subgroup analysis is very misleading and does not inherit proper covariate adjustment
  • subgroup analysis does not properly handle continuous variables
• Continuous Y with X explaining \(\frac{1}{2}\) of the variation in Y
  • sample size cut \(\times \frac{1}{2}\) in comparison to unadjusted analysis

• Change from baseline (post - pre) assumes
  • post is linearly related to pre
  • slope of post on pre is 1.0
• ANCOVA assumes neither so is more efficient and extends to ordinal outcomes
• post - pre is inconsistent with ∥ group design
• post - pre is manipulated by pt inclusion criteria and RTTM

• Don’t take sample sizes seriously; consider sequential designs with unlimited data looks and study extension
• α is not a relevant quantity to “control” or “spend” (unrelated to decision error)
• Choose high-resolution high-information Y
• Longitudinal ordinal Y is a general and flexible way to capture severity and timing of outcomes
• Always adjust for strong baseline prognostic factors; don’t stratify by treatment in Table 1

• datamethods.org
• fharrell.com
• hbiostat.org
• hbiostat.org/endpoint
• hbiostat.org/bayes
• hbiostat.org/bbr/md/alpha
• hbiostat.org/bayes/design \(\leftarrow\)
• fharrell.com/post/nfl