Statistical considerations for the Nipah virus treatment study

1. Statistical considerations for the Nipah virus treatment study Lori E Dodd, PhD Clinical Trials Research Section Division of Clinical Research/NIAID

2. Why randomize in outbreak setting? • Evaluating potential efficacy of experimental treatment requires a comparable control group • Ensuring a comparable control group is especially tricky in an emerging infectious disease: • Risk factors for death not well known • Supportive care may differ across sites & outbreaks • Randomization will tend to balance risk factors & supportive care differences • It is possible treatment may cause harm • Randomized control group an efficient way to identify this.

3. Ebola 2013-2016 treatment studies 8 studies reported evaluations of candidate treatments: • Amodiaquine, Convalescent Plasma, Convalescent Whole Blood, Favipiravir (2 studies), Interferon β-1⍺, TKM-13083, ZMappTM • Only ZMappTM used a randomized-controlled design • All other studies used historical controls What can we learn from comparing the control groups?

4. Mortality rates vary between 30% and 66%. Potential reasons for variability: Different amounts of virus at time of infection? Different time from onset of symptoms to treatment? Virus variants? Age differences? Gender differences? Genetics? Differences in supportive care? Mortality rates from 6 control groups: Adjustments for cycle threshold, age, and gender do not eliminate the between-study heterogeneity

5. Favipiravir Study Is this a reasonable estimate of the benefit of favipiravir?

6. Adjusting for baseline covariates does not resolve this predicament.* Randomization will tend to balance the differences in risk of death of baseline variables. Favipiravir Study This control group would suggest harm.

7. TKM-13083 Study Harm?

8. TKM-13083 Concern about TKM does not change even after adjusting for CT, age and gender.

9. Randomization will not A lead physician on ZMappTM regrets not having a placebo: ZMappTM was perceived to be a “magic serum.” Perception may have influenced patient management. Patients require continual monitoring during ZMappTM infusion. Potential differences in background care??? Balance post-baseline differences! Differences between groups related to treatment assignment AFTER randomization may still bias comparisons. Examples of unintended post-randomization bias: --Patients receiving experimental therapy are monitored more frequently, receiving improved background care, OR --Patients receiving control therapy are monitored more frequently, receiving improved background care Placebo-controlled trials address this potential bias.

10. Statistical analysis for this RCT Primary Endpoint: 28-day mortality Statistical test: test of lower mortality rate (using Boschloo’s test), two-sided type I error rate of 0.05 Sample size: 100 per arm Highly unlikely that one outbreak will provide sufficient statistical power for conclusive evidence

12. Randomization Stratified for statistical efficiency Limited to one stratification variable: Presence of neurologic symptoms (yes/no). Double-blinded design requires Process to ensure masking of treatment assignment Randomization via database with blinded treatment codes Pharmacist standardized operating procedure to preserve the blind Reporting of AEs to Data and Safety Monitoring Board who should be unblinded to treatment assignment

14. Interim monitoring considerations Early data are unreliable but ethical considerations demand that a trial stops for • Definitive early efficacy or • Definitive early harm Monitoring too frequently increases chances of a false positive finding Study likely to continue across multiple outbreaks Solution: group sequential monitoring

15. Definitive early efficacy Truncated O’Brien-Fleming boundary with 5 interim looks: Mortality boundaries for first (n=24) interim analysis: Flexibility to evaluate at the end of an outbreak

16. Definitive early harm Same frequency as for efficacy. Less evidence required to establish harm. p<0.05 for each look Mortality boundaries for first safety analysis (at n=24):

17. Conditional Power Method of calculating likelihood of concluding statistical significance given accumulated (but not complete) data Given the accumulated observed data (up to time of analysis), compute the probability of achieving statistical significance assuming the remaining data (up to total of 100/arm) follow assumed alternative: *e.g., 50% reduction in mortality Evaluated during interim analyses and/or accrual pauses (due to end of outbreak) —If conditional power < 20%, continuing study may be futile

18. Sample size reassessment After 100 participants have been accrued, sample size may be increased if: Conditional power is greater than 50%, or Pooled mortality rate is low

19. Continuing study across outbreaks Study continues (across outbreaks) without release of results until accrual completed or DSMB recommends early stopping. Procedures/agreements needed to ensure all sites/countries understand the importance of this. Early release of data without a definitive conclusion may make continued study of m102.4 impractical.

20. Prevail II example Randomized controlled trial comparing ZMappTM to standard-of-care during the 2013-16 Ebola outbreak Powered for a 50% reduction in mortality from 40% to 20% -200 subjects needed By January 2016, epidemic was clearly ending. Should study continue? West African Ebola outbreak was unprecedented. • No pattern of regional outbreaks • Unclearif and when another outbreak would occur

21. DSMB presented with the following data The PREVAIL II Writing Group. N Engl J Med 2016;375:1448-1456.

22. Recommendation DSMB recommended study closure and release of data Results published NEJM in 2016 ZMappTM was promising but results not definitive Ongoing debate about its efficacy Questions for thought: Should DSMB have kept study open? Suppose another outbreak was expected within a year, would DSMB have kept study going?