Presatovir in Hematopoietic Cell Transplant Recipients With Respiratory Syncytial Virus (RSV) Infection of the Lower Respiratory Tract: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Presatovir in Hematopoietic Cell Transplant Recipients With Respiratory Syncytial Virus (RSV) Infection of the Lower Respiratory Tract (NCT02254421), a randomized phase 2 study. The primary outcome is Time-weighted Average Change in Nasal Respiratory Syncytial Viral (RSV) Load From Baseline to Day 9.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-blind, placebo-controlled, parallel-group study with quadruple masking. It lists the phase as phase 2 and gives a recorded enrollment of 60. The study was sponsored by Gilead Sciences and its official title identifies it as a multicenter study. The registry lists the status as completed, a start date of 2015-01-31, and a primary completion date of 2017-04-17.

Participants were assigned to presatovir or matching placebo. Both groups had scheduled study-drug administrations on Days 1, 5, 9, 13, and 17, with follow-up through Day 28. The arm descriptions also allowed optional extended monitoring with visits through Day 56. These descriptions establish the planned schedule but do not give details about adherence, discontinuations, or the number who entered extended monitoring; those details are not reported in the registry record.

The primary outcome analysis used the Full Analysis Set, defined in the record as randomized participants who received at least 1 full dose and had a quantifiable Day 1 nasal RSV viral load by central-laboratory RT-qPCR. The reported group sizes for this primary endpoint were 29 for presatovir and 28 for placebo. Those outcome denominators are not the same as the recorded enrollment figure, and the registry’s definition indicates that eligibility for this analysis depended on dosing and baseline assay criteria.

The record names three secondary outcomes: supplemental oxygen-free days through Day 28, respiratory failure requiring mechanical ventilation through Day 28, and all-cause mortality through Day 28. Results are posted for the latter two; results for supplemental oxygen-free days are not reported in the registry record. The original sample-size justification, randomization details, stratification-factor identities, and complete statistical analysis plan are also not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 71 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: all randomized participants who received at least 1 full dose of study drug and had an RSV viral load greater than or equal to the lower limit of quantification of the RT-qPCR assay in the Day 1 nasal sample, as determined by RT-qPCR at the central lab.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Safety Analysis Set: participants who received at least 1 full dose of study drug.

6. Primary Endpoint

The registry lists the primary outcome as Time-weighted Average Change in Nasal Respiratory Syncytial Viral (RSV) Load From Baseline to Day 9, measured over Baseline to Day 9.

The primary endpoint was the time-weighted average change in nasal RSV viral load from baseline to Day 9, measured in log10 copies/mL. The registry calls this the DAVG and describes it as an average viral burden change across the measurement period. A time-weighted measure uses the pattern of measurements over time to represent the average change, rather than relying on a single value at Day 9. This can be useful when the scientific question concerns the course of viral burden across a period.

Viral load is a continuous laboratory measure. The registry reports adjusted mean values from an ANCOVA model, with adjustment for baseline value and stratification factors. The reported mean change was -1.0 in the presatovir group and -0.97 in the placebo group. Because both arm means are changes from baseline, negative values represent a decline from baseline on the log10 copies/mL scale. The comparison of interest is the between-group treatment difference, not whether either arm’s average changed from its own baseline in isolation.

The registry’s primary analysis population required a baseline nasal sample with viral load at or above the assay’s lower limit of quantification, as well as receipt of at least 1 full dose. Consequently, the endpoint’s interpretation applies to the defined Full Analysis Set and should not automatically be extended to participants who did not meet those criteria. The record does not provide individual trajectories or additional details about how measurements were handled when a scheduled sample was unavailable.

7. Results Posted in the Registry

• Presatovir: mean -1.00 versus -0.97 on control; difference -0.03 (95% CI -0.63 to 0.57), standardized effect d = -0.03; z-test p = 0.922.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Percentage of Participants Developing Respiratory Failure Requiring Mechanical Ventilation Through Day 28

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Presatovir: 10.3% (3/29) versus 10.7% (3/28) on control; risk difference -0.4 percentage points (95% CI -16.3 to 15.6), risk ratio 0.97 (0.21–4.39); unadjusted two-proportion z-test p = 0.964.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Presatovir and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of All-Cause Mortality Among Participants Through Day 28

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Presatovir: 0.0% (0/29) versus 7.1% (2/28) on control; risk difference -7.1 percentage points (95% CI -16.7 to 2.4); unadjusted two-proportion z-test p = 0.143.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Presatovir and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes add information about clinical events and supportive care but do not overturn the primary endpoint’s broad pattern: the registry does not show a clear separation between the treatment groups in its posted primary comparison. The available secondary results also have substantial uncertainty, and the record does not report every named secondary outcome. In particular, results for supplemental oxygen-free days through Day 28 are not reported in the registry record.

The respiratory failure and all-cause mortality outcomes are different from the primary viral-load measure. Viral load is a continuous laboratory outcome, whereas these secondary outcomes concern whether an event occurred during a specified period. Agreement or disagreement across such measures cannot be assumed: they capture distinct aspects of the study, and the registry does not establish that one necessarily predicts another. The small event counts also make the secondary estimates unstable and their intervals broad.

These outcomes are secondary, and the record does not report a multiplicity adjustment. When several outcomes are tested, the chance of at least one apparently unusual result can increase if each is interpreted as though it were the sole planned test. Without a reported adjustment or complete analysis plan, secondary p-values should be treated as exploratory rather than as independent confirmatory evidence. This does not make them irrelevant; it means that they should be weighed alongside their uncertainty, outcome status, and the missing details about how the analyses were planned.

For these reasons, the secondary findings provide context but do not support a definitive conclusion about differences in broader clinical outcomes. The registry does not report the result for every listed secondary outcome, and the available event-based estimates should not be generalized beyond the study’s defined population and follow-up period.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Number of Supplemental O2-Free Days Through Day 28
• Percentage of Participants Developing Respiratory Failure Requiring Mechanical Ventilation Through Day 28
• Percentage of All-Cause Mortality Among Participants Through Day 28

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is a mean time-weighted change in nasal viral load, measured in log10 copies/mL. A mean summarizes the center of a distribution, but does not show how individual participants’ values are spread around that center. The registry reports standard errors alongside the arm means. A standard error describes the uncertainty in an estimated mean; it is not the same as the spread of individual participant values.

What does the primary ANCOVA comparison represent?

The sponsor’s reported primary analysis used ANCOVA and estimated a treatment difference. In general, ANCOVA compares outcome means while adjusting for specified covariates. The registry says that the reported means were adjusted for baseline value and stratification factors. Adjusting for baseline can account for differences in starting values when estimating a comparison of follow-up change. The record does not identify the stratification factors or give further model details, so those aspects of the fitted analysis cannot be assessed from the registry record.

The sponsor reported a treatment difference of -0.02, a 95% confidence interval from -0.62 to 0.57, and p = 0.94. The arm means were -1.0 and -0.97. A treatment contrast is the between-group estimate; it answers a different question from whether each group’s own mean change is above or below zero. The p-value is associated with the sponsor’s reported superiority analysis and should be read together with the effect estimate and interval.

What is the role of the re-calculation?

The re-calculated comparison is a simple, unadjusted calculation from posted summary statistics. It gives a mean difference of -0.03, p = 0.922, and a standardized effect size of -0.026. The posted pooled standard deviation is 1.156. These are descriptive re-calculations, not a reproduction of the ANCOVA, because adjusted estimates cannot generally be recovered from arm means and standard errors alone. The sponsor’s model-based result is the relevant registry analysis for the adjusted primary comparison.

Standardizing a mean difference expresses it relative to a measure of variability, which can help describe the size of an observed contrast on a scale independent of the original measurement units. It does not replace the original log10 copies/mL scale, and the small estimated standardized contrast does not by itself establish that clinically important differences are absent. The uncertainty interval and study population remain central to interpretation.

How should the binary outcomes be understood?

The respiratory failure and mortality outcomes are binary: each participant either met the outcome definition during the stated period or did not. The posted arm results are percentages with 95% confidence intervals. A risk difference compares the proportions between groups on the percentage-point scale; a confidence interval around that difference represents uncertainty in the estimated contrast. For respiratory failure, the registry also reports a sponsor analysis using the Cochran-Mantel-Haenszel method and p = 0.98. In general, that method can compare groups while accounting for strata. The specific strata used are not reported in the registry record.

For mortality, the sponsor-reported Cochran-Mantel-Haenszel p-value is 0.19. The registry does not give a corresponding sponsor-reported effect estimate or confidence interval for that analysis. A separate unadjusted re-calculation is not the same as the sponsor’s stratified analysis. The number of events is small, so the observed percentages and their intervals should be read as uncertain estimates rather than stable descriptions of future outcomes.

What can the methods not establish?

Statistical methods quantify comparisons under model and data assumptions. They do not resolve missing-data concerns unless the missing-data process and handling methods are known, and they do not establish clinical importance on their own. The record does not report the full statistical analysis plan, treatment of missing measurements, model diagnostics, or multiplicity adjustment. The primary endpoint description identifies ANCOVA and its adjustment variables at a high level, but does not provide enough detail to reproduce the sponsor’s analysis independently.

Over-dispersion is a general concern for count or binary outcomes when observed variability exceeds what a simple model assumes; it can make standard uncertainty estimates unreliable if ignored. The outcomes posted are small-sample binary proportions, but the registry record does not report a specific over-dispersion assessment. This general issue is not evidence that the analyses were or were not affected. It illustrates why method details and uncertainty intervals matter alongside point estimates and p-values.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the data. The primary sponsor-reported treatment difference was -0.02, with a 95% confidence interval from -0.62 to 0.57. In general, a confidence interval is a range produced by a method that, under its assumptions, is designed to cover the underlying parameter at the stated confidence level in repeated use. It is not a range containing 95% of individual participant outcomes, and it does not assign a 95% probability to this particular interval after it has been calculated.

The primary interval includes zero and extends in both directions around the estimated difference. This means that the result is compatible with no between-group difference as well as with differences favoring either group. Its span also cautions against treating the point estimate alone as a precise measure of the underlying effect. The registry reports standard errors of 0.215 for the presatovir mean and 0.218 for the placebo mean; these describe uncertainty in each reported arm mean, not the full variability among participants.

The respiratory failure percentages were 10.3% and 10.7%, with arm-specific 95% confidence intervals of 2.2% to 27.4% and 2.3% to 28.2%. The mortality percentages were 0.0% and 7.1%, with intervals of 0.0% to 11.9% and 0.9% to 23.5%. These wide ranges reflect substantial uncertainty in the estimates, consistent with the small numbers of participants and events. A difference between point estimates should not be read as a precise difference when the supporting intervals are broad.

The registry does not report sponsor confidence intervals for the two secondary treatment contrasts. The arm-level intervals should not be mistaken for an interval around a between-group difference. Overall, precision is limited, particularly for the binary outcomes, and the estimates should be interpreted as uncertain rather than definitive.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning illustrations translate an assumed effect size into a hypothetical sample size under specified assumptions. For these outcomes, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. The original trial’s own sample-size justification and design assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would give an 80% chance of detecting the assumed effect under those assumptions, if that effect and model were appropriate. The 90% power column gives the corresponding hypothetical number for a 90% chance. These are design-planning quantities, not guarantees about what a future study will find. They depend on the assumed effect, variability, analysis, and other planning conditions.

The rows use 100%, 75%, and 50% of the observed effect. For the primary endpoint, the corresponding 80% power planning figures are 23,298, 41,417, and 93,189 participants per arm; the 90% power figures are 31,189, 55,446, and 124,753 participants per arm. For the respiratory failure endpoint, the 80% figures are 108,341, 193,352, and 436,718 participants per arm, and the 90% figures are 145,038, 258,843, and 584,640 participants per arm.

The illustrations are based on the observed effects in this study, which are uncertain estimates, especially for rare binary outcomes. A smaller effect requires more participants to distinguish it from random variation under the stated assumptions. These calculations are planning illustrations, not observed power; they do not describe the probability that this completed trial detected its true effect.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.030; pooled standard deviation σ = 1.156.
2. n = 2 × (1.96 + 0.842)² × 1.156² / -0.030² = 23,297.0, rounded up to 23,298 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.03                      # observed difference in means
sigma <- 1.1557197206621                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(2254421)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 23,298 (80% power), 31,189 (90% power)
 75% of observed effect: n per arm = 41,417 (80% power), 55,446 (90% power)
 50% of observed effect: n per arm = 93,189 (80% power), 124,753 (90% power)
power.t.test: 23298 
Simulated power at n = 23,298 per arm: 0.807 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis used ANCOVA and reported an adjusted treatment difference of -0.02, with a 95% confidence interval from -0.62 to 0.57 and p = 0.94. The re-calculation from the posted arm summaries is unadjusted and gives a mean difference of -0.03 and p = 0.922. The values are close, but they are not identical because the sponsor analysis adjusts for baseline value and stratification factors, whereas the re-calculation uses summary statistics.

The registry record does not flag a discrepancy between the reported analysis and the re-calculation. Even so, the methods answer slightly different statistical questions: the sponsor result is the stated adjusted analysis, while the re-calculation is a check based on unadjusted summaries. The adjusted sponsor analysis should be used when describing the trial’s reported primary comparison. The re-calculation is useful as a transparent reference point, but it cannot reproduce model adjustments that are not recoverable from the posted summaries.

For respiratory failure and mortality, the sponsor reports Cochran-Mantel-Haenszel analyses with p-values of 0.98 and 0.19, respectively. The re-calculations use unadjusted comparisons and therefore need not match the sponsor’s stratified procedures. The registry does not provide the adjustment strata or full analysis details. Those p-values should be attributed to the sponsor-reported analyses, not treated as results of the simple re-calculations.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and three secondary outcomes. It reports a primary ANCOVA comparison and sponsor analyses for respiratory failure and mortality. The original statistical analysis plan, the prespecified hierarchy of tests, and any multiplicity-control procedure are not reported in the registry record. It is therefore not possible to determine from the record whether the secondary outcomes were formally adjusted for multiple testing or how their inferential priority was defined.

Multiplicity matters because conducting several statistical tests creates more opportunities for an apparently notable result to arise by chance. A prespecified adjustment can control the overall error rate, while an ordered testing strategy can specify which conclusions depend on earlier results. These are general methods; the registry does not establish that either approach was used. Secondary p-values should consequently be interpreted with caution and in the context of the primary result, rather than as stand-alone confirmatory findings.

Missing-data handling is also not reported in the registry record. The primary analysis population definition specifies randomized participants who received at least 1 full dose and had a Day 1 nasal sample meeting the assay threshold, but it does not explain how unavailable post-baseline measurements were handled. The record does not state whether missing outcomes were imputed, excluded at particular visits, or addressed through another method. Nor does it report a sensitivity analysis for missing data.

The analysis population is important for interpretation. Although recorded enrollment was 60, the primary endpoint results include 29 participants receiving presatovir and 28 receiving placebo. The record defines the Full Analysis Set using dosing and baseline assay criteria, so the primary results apply to that defined set. The registry does not provide enough information to reconcile all enrollment and analysis-population counts or to assess the consequences of exclusions and missing measurements.

These omissions do not show that the analyses were inappropriate. They limit independent assessment of how the outcomes were selected, how missing information was treated, and how much inferential weight should be assigned to the secondary tests.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (10.0%), respiratory failure (6.9%), anaemia (3.4%), febrile neutropenia (3.4%), bacterial infection (3.4%).

The registry reports serious adverse events among 7 of 30 participants at risk in the presatovir group and 7 of 29 at risk in the placebo group. It reports other adverse events among 19 of 30 and 17 of 29, respectively. Deaths are listed for 0 participants in the presatovir group and 4 in the placebo group. These are descriptive counts from the safety results, with denominators that differ from the primary endpoint analysis population.

The most frequent serious adverse event terms listed include pneumonia at 10.0%, respiratory failure at 6.9%, anaemia at 3.4%, febrile neutropenia at 3.4%, bacterial infection at 3.4%, and Clostridium difficile colitis at 3.4%. The registry does not provide event-level detail about timing, recurrence, relationship to study treatment, or overlap among terms. The percentages and counts should not be read as evidence that a particular event was caused by a study drug.

Safety counts are not direct treatment-effect estimates. The registry excerpt does not give comparative confidence intervals or a detailed statistical analysis for these events. Differences in observed counts should therefore be described, not interpreted as proof of a safety difference. The study population and the listed denominators also matter when considering how broadly the descriptive results apply.

17. What the Result Does, and Does Not, Mean

The posted primary result is an adjusted comparison of average nasal RSV viral-load change from baseline to Day 9 in the defined Full Analysis Set. The group means were -1.0 for presatovir and -0.97 for placebo. The sponsor-reported difference was -0.02, with a 95% confidence interval from -0.62 to 0.57 and p = 0.94. These figures describe the estimated contrast and its uncertainty; they do not prove that the groups are identical.

The interval includes zero and allows for differences in either direction. Thus, the data do not provide a precise estimate that rules out a potentially meaningful difference, and the high p-value is not evidence that the probability of no effect is 94%. The trial’s reported result should be understood as an inconclusive comparison on this endpoint, not as a formal demonstration of equivalence. No equivalence or non-inferiority margin is reported in the registry record.

The endpoint is a laboratory measure of viral burden over a defined period. It is not itself a direct measure of every clinical outcome that may matter to participants. The registry also lists respiratory failure, mortality, and supplemental oxygen-free days, but results for the latter are not reported. The available secondary results are uncertain and do not supply a basis for broad conclusions about clinical outcomes.

The findings apply to the analyzed participants who met the study’s dosing and baseline viral-load criteria. They should not be generalized automatically to people outside that population, other forms of RSV infection, or different settings. The record does not provide enough detail about missing-data handling, multiplicity, or the original sample-size rationale to resolve all questions about the strength and scope of the evidence.

In short, the registry reports estimates that are compatible with a range of between-group effects. The statistics describe what was observed and how uncertain the estimates are; they do not establish that presatovir does or does not work, nor do they substitute for clinical judgment.

18. Why This Trial Matters Statistically

This trial illustrates why an endpoint estimate, its uncertainty interval, and the analysis method should be read together. The primary point estimate is close to zero, but the confidence interval is broad enough to include differences in either direction. Treating the point estimate alone as definitive would overstate what the data determine. Conversely, interpreting a non-small p-value as proof of no effect would also go beyond the evidence.

It also shows the distinction between a model-based sponsor analysis and an unadjusted re-calculation from summary statistics. The sponsor used ANCOVA adjusted for baseline value and stratification factors; the simple re-calculation does not reproduce those adjustments. Comparing them can help readers understand the role of the stated model, while keeping the sponsor’s reported analysis as the primary inferential result.

The binary secondary outcomes make precision especially visible. The event counts are limited, and the arm-level confidence intervals are wide. Such estimates can be useful for describing the observed data, but the uncertainty constrains how strongly they can support comparisons. The record’s omission of results for supplemental oxygen-free days also demonstrates that an outcome listed as secondary cannot be interpreted without a posted result.

Finally, the record exposes the importance of protocol and analysis details. The original sample-size justification, missing-data procedures, multiplicity strategy, and complete statistical analysis plan are not reported. Those details affect how readers assess design intent and the scope of valid inference. Recognizing what is and is not documented is part of sound statistical interpretation, not a judgment about the conduct of the study.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The primary comparison is based on 57 participants in the stated Full Analysis Set, with 29 in the presatovir arm and 28 in the placebo arm. The registry’s total recorded enrollment is 60. The primary population excludes participants who did not meet its dosing and baseline assay criteria, and the registry does not report enough information to evaluate the impact of those criteria or account for the difference in counts.

The primary estimate has a broad 95% confidence interval, so the data do not precisely determine the between-group effect. The secondary binary outcomes have few events and wide arm-level intervals. These features limit the strength of conclusions that can be drawn from the point estimates, especially for uncommon outcomes.

The record does not report the original sample-size justification, full statistical analysis plan, identity of the stratification factors, multiplicity procedure, missing-data methods, or sensitivity analyses. It also does not report the result for supplemental oxygen-free days. This absence limits independent evaluation of design assumptions, outcome prioritization, and robustness to missing information. It does not establish that these procedures were not performed; they are simply not reported in the registry record.

The registry describes follow-up through Day 28 and an optional extended monitoring phase through Day 56, but it does not give the number entering extended monitoring or detailed longer-term outcome results in the registry record. The posted primary endpoint addresses viral burden from baseline to Day 9, while selected secondary outcomes cover up to Day 28. Conclusions should therefore remain tied to those measures and periods.

Finally, these are registry results rather than a full account of individual participant data, protocol deviations, or model diagnostics. The available summaries support a bounded statistical interpretation, not a comprehensive assessment of every design or conduct issue.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Presatovir in Hematopoietic Cell Transplant Recipients With Respiratory Syncytial Virus (RSV) Infection of the Lower Respiratory Tract — NCT02254421.
• Registry record last updated 2018-09-24; status last verified 2018-05.
• Results first posted 2018-05-11.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The record describes a randomized, quadruple-masked, parallel-group phase 2 study of presatovir versus matching placebo in hematopoietic cell transplant recipients with lower respiratory tract RSV infection. Recorded enrollment was 60. The primary endpoint was the adjusted time-weighted average change in nasal RSV viral load from baseline to Day 9.

The sponsor-reported primary treatment difference was -0.02, with a 95% confidence interval from -0.62 to 0.57 and p = 0.94. The posted estimate is uncertain and does not establish equivalence or a definitive difference. Secondary results are available for respiratory failure and all-cause mortality; supplemental oxygen-free-day results are not reported in the registry record. The original sample-size rationale, missing-data procedures, and multiplicity strategy are also not reported.