Presatovir in Lung Transplant (LT) Recipients With Respiratory Syncytial Virus (RSV) Infection: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Presatovir in Lung Transplant (LT) Recipients With Respiratory Syncytial Virus (RSV) Infection (NCT02534350), a randomized phase 2 study. The primary outcome is Time-Weighted Average Change in Viral Load From Day 1/Baseline Through Day 7 in Participants in the Full Analysis Set.

2. Clinical Question

3. Trial Design

The registry describes a Phase 2b randomized, controlled trial of presatovir in lung transplant recipients with RSV infection. It used a parallel-group design and double masking, with placebo as the comparator. The registry lists enrollment as 61. The sponsor was Gilead Sciences, and the study status is completed. The start date is 2015-12-31, and the primary completion date is 2017-02-20.

The presatovir regimen was 200 mg on Day 1, then 100 mg from Day 2 to Day 14. The placebo group received placebo tablets for 14 days. The primary objective concerned nasal RSV viral load in participants with RSV infection and acute respiratory symptoms. The posted primary endpoint summarizes viral-load change over the period through Day 7 rather than a single measurement at the end of treatment.

The primary analysis population was the Full Analysis Set, defined in the registry as participants who received at least 1 full dose of study drug and had a Day 1 nasal sample with RSV viral load at or above the assay’s lower limit of quantification. The registry description ends mid-sentence, so the remainder of the population definition is not reported in the registry record. The observed endpoint group sizes were 35.0 for presatovir and 19.0 for placebo.

Two secondary outcomes are listed: change in FLU-PRO score through Day 7 and percent change from baseline in FEV1% predicted value. The registry lists four outcome measures and four analyses overall. Details such as the trial’s original sample-size justification, full eligibility criteria, and any interim analyses are 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: 111 participants were screened.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Participants in the Full Analysis Set (participants who received at least 1 full dose of study drug and had an RSV viral load ≥ lower limit of quantification (LLOQ) of the real-time quantitative polymerase chain reaction (RT-qPCR) assay in the Day 1 nasal sample, as determined by RT-qPCR at the central lab) with available data were analyzed .

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 Viral Load From Day 1/Baseline Through Day 7 in Participants in the Full Analysis Set, measured over Up to 7 days.

The primary endpoint is the time-weighted average change in nasal RSV viral load from Day 1/baseline through Day 7, measured in log10 copies/mL. Viral load quantifies the amount of viral material detected in the nasal sample using RT-qPCR. A change score expresses how the measurement moved from baseline over the stated period; the time-weighted average incorporates measurements over that period rather than treating a single observation as the whole trajectory.

The endpoint matches the stated primary objective, which was to evaluate the effect of presatovir on nasal RSV viral load in RSV-positive lung transplant recipients with acute respiratory symptoms. It gives a continuous measure of viral-load change that can be compared between randomized groups. The reported means were -0.73 for presatovir and -0.9 for placebo. Because these are changes, a negative value indicates a decrease relative to baseline in the units used; the group means alone do not establish whether the difference is distinguishable from sampling uncertainty.

The Full Analysis Set required receipt of at least 1 full dose and a Day 1 nasal viral-load result at or above the assay’s lower limit of quantification. Such a threshold defines which measurements can contribute to the analysis, but it also means the endpoint results apply to the registry-defined analysis population, not automatically to every person enrolled. Further detail about handling measurements below the quantification limit is not reported in the registry record.

7. Results Posted in the Registry

• Presatovir: mean -0.73 versus -0.90 on control; difference 0.17 (95% CI -0.31 to 0.65), standardized effect d = 0.19; z-test p = 0.488.

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.

Time-Weighted Average Change in FLU-PRO Score From Day 1/Baseline Through Day 7

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Presatovir: mean -0.27 versus -0.31 on control; difference 0.04 (95% CI -0.14 to 0.22), standardized effect d = 0.13; z-test p = 0.659.
• 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.

Percent Change From Study Baseline in FEV1% Predicted Value

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Presatovir: mean 22.69 versus 26.36 on control; difference -3.67 (95% CI -18.48 to 11.14), standardized effect d = -0.14; z-test p = 0.627.
• 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 broadly echo the primary result in that the reported sponsor analyses do not show a clear separation between groups, and their confidence intervals include no difference. The simple recalculations likewise have estimates with uncertainty that spans the null. This broad pattern is relevant as context, but the secondary endpoints do not replace the primary viral-load question or independently settle it.

The endpoints address different kinds of measurements: FLU-PRO score captures reported symptoms, while FEV1% predicted is a lung-function measure. Agreement in the general direction of uncertainty across distinct outcomes can be informative, but it should not be treated as confirmation of one underlying effect. These measures may differ in scale, variability, timing, and analysis population. The posted results also have different group sizes for each endpoint, so the precision is not identical across outcomes.

Unadjusted secondary findings carry less weight when several outcomes are tested because the chance of at least one apparently unusual result can increase as more tests are considered. General statistical practice may use a prespecified multiplicity strategy to address that issue, but whether such a strategy was planned or applied is not reported in the registry record. The registry lists two secondary outcomes and four analyses overall, but it does not describe a hierarchy, adjustment procedure, or confirmatory status for the secondary analyses.

Accordingly, the secondary results are best treated as exploratory or supportive unless the original protocol or statistical analysis plan establishes otherwise. The record does not report a threshold for clinical importance for these outcomes. The broad pattern is compatible with the primary result’s uncertainty, but it cannot establish absence of effects or equivalence across outcomes.

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

• Time-Weighted Average Change in FLU-PRO Score From Day 1/Baseline Through Day 7
• Percent Change From Study Baseline in FEV1% Predicted Value

9. Statistical Interpretation

10. Statistical Methods Explained

The posted primary outcome is continuous: it is a mean change in viral load, accompanied by a standard deviation for each group. The registry-reported comparison is an ANCOVA treatment difference. The recalculated comparison is a simple unadjusted mean difference based on the posted group summaries. These methods answer related questions, but they are not identical: ANCOVA can account for specified covariates, while the summary-based recalculation does not adjust for them.

What does a mean difference describe?

A mean difference is the estimated separation between the group averages on the endpoint’s measurement scale. For the primary endpoint, the recalculated difference is 0.17 log10 copies/mL, with the estimate formed as the presatovir mean minus the placebo mean. The sign depends on that ordering. A difference near zero means the observed group averages are close on the scale; it does not, by itself, show whether the estimate is precise or whether a clinically meaningful threshold has been crossed. No threshold for clinical importance is reported in the registry record.

The standard deviation describes how spread out participant measurements were around the group mean. It is not the uncertainty of the mean itself. The uncertainty in a group mean also depends on the number of observations contributing to it. The primary endpoint’s posted standard deviations are 0.938 for presatovir and 0.815 for placebo. The groups have different analysis sizes, listed as 35.0 and 19.0, respectively.

Why report an ANCOVA result?

In general, analysis of covariance estimates a group contrast while accounting for selected covariates. With an appropriate model and prespecified covariates, adjustment can improve precision or account for baseline variation. The sponsor’s primary ANCOVA result is a treatment difference of 0.10, with a 95% confidence interval from -0.43 to 0.63 and p = 0.72. The covariates, model specification, and assumptions used for that analysis are not reported in the registry record. The adjusted estimate should therefore be understood as the sponsor-reported analysis, not as a model that can be independently reconstructed from the posted group means.

The recalculation is deliberately unadjusted. It uses the posted means and standard deviations to describe a comparison that does not depend on unavailable model details. It is useful as a transparent check of the summary statistics, but it is not a replacement for the sponsor’s planned analysis. In this trial, the record does not identify a discrepancy flag, and the difference between the adjusted and unadjusted estimates does not itself establish an error.

What do the p-value and confidence interval convey?

In general, a p-value measures how incompatible the observed data are with a specified null model, under the assumptions of the statistical test. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The sponsor’s p-value is 0.72, while the simple recalculation gives an unadjusted p-value of 0.488. These values arise from different analyses and should not be treated as interchangeable.

In general, a confidence interval gives a range of estimates compatible with the data and analysis procedure at the stated confidence level. A broad interval signals uncertainty about the size and direction of the effect. For the sponsor’s primary analysis, the 95% interval crosses zero, so the results do not rule out no difference under that analysis. The interval also includes values on both sides of zero, so the estimate does not precisely identify the direction of any underlying difference.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when variability in observed data exceeds what a statistical model assumes. If that extra variability is ignored, standard errors may be too small and confidence intervals may be too narrow. The primary endpoint is analyzed as a continuous measure with standard deviations reported, and the registry does not report an over-dispersion model or diagnosis. Over-dispersion should not be assumed to have affected this analysis; the concept is relevant as a general reminder that uncertainty depends on whether model assumptions fit the data.

For continuous outcomes, a normal approximation is one common basis for simple planning calculations. The sample-size assumptions listed for the planning illustration use a normal approximation, equal allocation, and a two-sided significance level of 0.05. Those are assumptions for the illustration, not information about the trial’s original design. The trial’s own sample-size justification and original planning assumptions are not reported in the registry record.

Finally, the Full Analysis Set definition matters. Requiring a qualifying Day 1 nasal sample and receipt of at least 1 full dose defines the population represented in the primary endpoint analysis. The registry does not report the complete truncated definition, a detailed account of missing-data handling, or sensitivity analyses. Those omissions limit assessment of how robust the result is to alternative assumptions about missing observations or population membership.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the observed data. The sponsor-reported primary treatment difference is 0.10, with a 95% confidence interval from -0.43 to 0.63. The interval includes zero and extends in both directions, so the data do not pin down a single direction or a narrow range of plausible differences. The p-value of 0.72 is consistent with the interval’s inclusion of no difference, but it should not be read as proof that the groups are equivalent.

The simple recalculation from posted summary statistics estimates a mean difference of 0.17 and gives an unadjusted p-value of 0.488. Its recalculated interval also crosses zero, but its endpoints are omitted from this prose because they are given to more than three decimal places. The sponsor’s adjusted interval is the registry-reported primary analysis and should be distinguished from the unadjusted recalculation.

In general, a confidence interval represents uncertainty under a particular analysis and its assumptions; it does not guarantee that the true effect lies within the interval. Precision depends on the amount of information, variability, and the analysis method. The primary group sizes were 35.0 and 19.0, and the reported standard deviations were 0.938 and 0.815. These features help contextualize uncertainty, but they do not permit a new confidence interval to be inferred beyond the reported analyses.

The registry does not report a threshold defining a clinically important difference for this endpoint. Consequently, the interval cannot be classified against such a threshold from the record. It supports a cautious reading: the estimated contrast is uncertain, and the data do not establish either a precise benefit or equivalence.

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 estimates are participants per arm for 80% power and participants per arm for 90% power. They are based on the observed effect and then consider planning for 100%, 75%, or 50% of that observed effect. For the primary endpoint, the estimates rise as the assumed effect becomes smaller. The same general relationship appears in the secondary-outcome planning estimates. Smaller effects are harder to distinguish from random variation, so more participants are needed to achieve the same target power under the stated assumptions.

These are planning illustrations, not the trial’s own sample-size justification. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report the original design assumptions or sample-size rationale.

In general, 80% power means that, if the assumed effect and model conditions hold, repeated studies would identify a statistically significant result in 80% of such studies. The 90% column represents a higher probability of detecting the assumed effect under those same conditions, and therefore yields larger planning requirements. These percentages are properties of the planning scenario, not probabilities that the observed trial result is correct.

This is not observed power. The calculations are forward-looking illustrations based on an observed estimate and stated assumptions; they do not measure the probability that the completed trial detected an effect. The estimates should also be interpreted cautiously because a small observed effect can be imprecise and may not represent the effect a future study should target. No original sample-size justification is reported in the registry record.

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 = 0.170; pooled standard deviation σ = 0.897.
2. n = 2 × (1.96 + 0.842)² × 0.897² / 0.170² = 437.4, rounded up to 438 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 <- 0.17                      # observed difference in means
sigma <- 0.897333078542273                     # 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(2534350)
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 = 438 (80% power), 586 (90% power)
 75% of observed effect: n per arm = 778 (80% power), 1,041 (90% power)
 50% of observed effect: n per arm = 1,750 (80% power), 2,343 (90% power)
power.t.test: 438.3 
Simulated power at n = 438 per arm: 0.803 (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 registry-reported primary analysis is the sponsor’s ANCOVA comparison: a treatment difference of 0.10, a 95% confidence interval from -0.43 to 0.63, and p = 0.72. That is the result to prioritize when describing the sponsor’s own analysis. It accounts for the sponsor’s chosen adjustment model, although the covariates and full model specification are not reported in the registry record.

The simple recalculation uses only the posted group summaries. It estimates an unadjusted mean difference of 0.17 and gives p = 0.488. The adjusted and unadjusted estimates are not required to match, because they arise from different analyses. The recalculated result offers a transparent summary-based comparison, but it cannot reproduce the ANCOVA without the model details and individual-level data.

The registry record does not flag a discrepancy. Accordingly, there is no recorded conflict that would warrant treating the recalculation as a correction to the sponsor’s result. The two estimates should be described according to their methods rather than selected by which appears more favorable. Both are uncertain, and the sponsor-reported confidence interval includes no difference. Details of the prespecified statistical analysis plan are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when statistical conclusions are drawn from several tests, outcomes, time points, or analysis populations. In general, conducting more tests can increase the likelihood that at least one result appears statistically significant by chance, even when there is no underlying effect. Researchers may address this through a prespecified hierarchy, adjusted significance thresholds, or other strategies. Which approach is appropriate depends on the trial’s objectives and plan.

The registry lists the primary viral-load endpoint and two secondary outcomes, and reports four outcome measures and four analyses overall. It does not describe whether tests were hierarchically ordered, whether p-values were adjusted, or whether any secondary analyses were designated as confirmatory. Multiplicity handling is therefore not reported in the registry record. The unadjusted recalculated p-values should not be treated as if they account for the full set of analyses.

Missing-data handling is also not reported in sufficient detail. The registry’s Full Analysis Set definition requires at least 1 full dose and a qualifying Day 1 nasal sample, but the definition is truncated. The record does not explain how missing post-baseline viral-load values were handled, whether participants with incomplete follow-up contributed to the time-weighted average, or whether sensitivity analyses examined alternative assumptions. The same level of detail is not reported for the secondary endpoints.

The analysis population matters because estimates describe the people and measurements included in each analysis. The endpoint group sizes differ across the primary and secondary outcomes, but reasons for those differences are not reported in the registry record. Without a full account of exclusions, missingness, and analysis populations, it is difficult to assess whether the available measurements represent the randomized groups in the same way.

The registry record also does not report interim analyses, stopping rules, or the original statistical analysis plan. Their absence from the record is a reporting limitation, not evidence that such procedures were or were not used. These gaps limit independent assessment of selective reporting, multiplicity control, and the sensitivity of the estimates to missing-data assumptions.

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: hypoxia (10.0%), non-cardiac chest pain (5.0%), sepsis (5.0%), deep vein thrombosis (5.0%), hypotension (5.0%).

The registry lists serious adverse events among participants at risk: 2 affected in the presatovir group, with 40 at risk, and 4 affected in the placebo group, with 20 at risk. It reports no deaths in either group. These are counts, not adjusted comparisons, and the groups at risk differ. The counts alone do not establish whether any observed difference is attributable to treatment.

The listed serious-event terms include hypoxia at 10.0%, non-cardiac chest pain at 5.0%, sepsis at 5.0%, deep vein thrombosis at 5.0%, hypotension at 5.0%, and anaemia at 2.5%. The registry’s list does not link these term percentages to a specific treatment group in the information, so they should not be assigned to either group. These percentages describe the registry’s listed terms, not a risk comparison between groups.

The record also lists other adverse events affecting 24 participants among 40 at risk in the presatovir group and 17 among 20 at risk in the placebo group. Event definitions, severity breakdowns, and detailed causal assessments are not reported in the registry record. Safety counts should therefore be read descriptively and in light of the limited reporting, rather than as a definitive comparative safety analysis.

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

The primary result estimates the difference between presatovir and placebo in the time-weighted average change in nasal RSV viral load through Day 7 among participants meeting the registry’s Full Analysis Set definition. The sponsor’s ANCOVA estimate is 0.10, with a 95% confidence interval from -0.43 to 0.63 and p = 0.72. The interval includes no difference and does not tightly determine the direction or size of the group contrast.

The result does not establish that the groups are equivalent. Equivalence requires a prespecified margin and a design and analysis intended to assess whether the effect lies within that margin; such an objective or margin is not reported in the registry record. Nor does a p-value above a conventional threshold prove that there is no effect. It indicates that the observed result is not strong evidence against the null model under the specified analysis.

The endpoint is a nasal viral-load measure over a limited period. It should not be conflated with symptoms, lung function, longer-term outcomes, or other clinical effects. The registry lists secondary symptom and FEV1% predicted outcomes, but does not report a clinically important threshold for these measures. The findings therefore address the posted endpoints and populations, not every possible consequence of RSV infection or treatment.

The trial enrolled 61 participants, while the primary analysis included group sizes of 35.0 and 19.0. The distinction between enrollment and the endpoint analysis population is important: the primary estimate applies to the Full Analysis Set described in the record, not necessarily to everyone enrolled. The registry definition is truncated, and details of missing data and sensitivity analyses are not reported.

These data are a statistical record of one completed trial. They do not by themselves determine treatment decisions, establish a mechanism, or guarantee that results generalize to other populations or settings. Interpretation should retain the uncertainty, the stated analysis population, and the limits of the registry reporting.

18. Why This Trial Matters Statistically

This trial illustrates why the estimate, its uncertainty, and the analysis method should be considered together. The primary group means are close in the posted scale, but the key question is not only how far apart they are: it is also how much uncertainty surrounds that separation. The sponsor’s confidence interval crosses zero and covers effects in either direction, so the result is not a precise determination of the group difference.

It also illustrates the distinction between an adjusted sponsor analysis and an unadjusted summary-based recalculation. The ANCOVA treatment difference and the recalculated mean difference are not identical, but they answer related questions using different information. Transparent reporting of the model and its covariates would help readers understand the adjustment. Those details are not reported in the registry record.

The endpoint and analysis population are equally important. A viral-load measure through Day 7 is a specific biological outcome, and the primary analysis applies to participants meeting the Full Analysis Set criteria. It does not automatically describe every enrolled participant or every clinically relevant outcome. The truncated population definition and unreported missing-data methods leave uncertainty about the path from enrollment to analysis.

Finally, planning estimates can help readers understand how assumptions about effect size affect future study requirements, but they are not a retrospective verdict on the completed study. They rely on a stated normal approximation and equal allocation and use the observed effect as a planning reference. The trial’s own original design rationale is not reported. Taken together, these features show why careful interpretation distinguishes estimation from proof, adjusted from unadjusted analysis, and descriptive planning from observed evidence.

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.

Several trial-specific reporting limitations constrain interpretation. The registry’s Full Analysis Set definition is truncated after its description of the Day 1 nasal sample, so it is not possible to confirm the complete population rule from the record. The group sizes in the primary analysis differ, and the reasons for the analysis-population counts relative to the enrollment figure are not reported.

The sponsor’s ANCOVA result is reported, but its covariates, model specification, and missing-data approach are not. The registry does not report sensitivity analyses that would show how the primary estimate changes under alternative assumptions. It also does not report detailed handling of viral-load measurements below the assay’s lower limit of quantification beyond the stated eligibility threshold for the primary analysis set.

The registry does not describe multiplicity control across the primary and secondary analyses, the analysis hierarchy, or the status of secondary outcomes as confirmatory or exploratory. The trial’s original sample-size justification, interim analyses, stopping rules, and statistical analysis plan are also not reported in the registry record. These omissions limit assessment of prespecification and the possibility that analytical choices affected inference.

The primary endpoint measures nasal viral load through Day 7. The record does not establish how this measure relates to outcomes outside that endpoint, nor does it report a threshold for a clinically important viral-load difference. The secondary endpoints have their own analysis populations and measurement scales, and the registry does not provide a complete account of missing observations for them.

Safety information is presented as counts and selected term percentages. The registry does not provide detailed event-level timing, severity, causality, or group attribution for the listed serious-event terms in the information reported. These constraints mean the safety summary is descriptive and cannot support a finely adjusted comparison.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Presatovir in Lung Transplant (LT) Recipients With Respiratory Syncytial Virus (RSV) Infection — NCT02534350.
• Registry record last updated 2018-11-28; status last verified 2018-11.
• Results first posted 2018-11-28.
• 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

NCT02534350 is a completed Phase 2b randomized, double-blind, parallel-group trial comparing presatovir with placebo in lung transplant recipients with RSV infection. The registry lists enrollment as 61 and identifies Gilead Sciences as the sponsor. Presatovir was given as 200 mg on Day 1 and 100 mg from Day 2 to Day 14; placebo tablets were given for 14 days.

The primary endpoint was time-weighted average change in nasal RSV viral load through Day 7. The sponsor-reported ANCOVA treatment difference was 0.10, with a 95% confidence interval from -0.43 to 0.63 and p = 0.72. The interval includes no difference and leaves substantial uncertainty about the effect’s direction and size. Two secondary outcomes and descriptive adverse-event counts are also reported.

Important statistical details, including the original sample-size justification, full analysis-plan specifications, multiplicity handling, and missing-data methods, are not reported in the registry record. The findings should therefore be read as estimates for the posted populations and endpoints, with the stated uncertainty and reporting limitations.