To Investigate the Effects of Altering the Time of Day of Dosing (Morning or Evening) With Fluticasone Furoate 100 Micrograms Once Daily Administered Via a Dry Powder Inhaler in Subjects With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for To Investigate the Effects of Altering the Time of Day of Dosing (Morning or Evening) With Fluticasone Furoate 100 Micrograms Once Daily Administered Via a Dry Powder Inhaler in Subjects With Asthma (NCT01808339), a randomized phase 2 study. The primary outcome is Weighted Mean Forced Expiratory Volume in 1 Second (FEV1) Measured Over 24 Hours at Day 14 of Each Treatment Period.

2. Clinical Question

3. Trial Design

This was a Phase 2, randomized, triple-masked, placebo-controlled, repeat-dose, three-way crossover study. Its title describes a double-dummy design. Rather than assigning each participant to just one treatment group, the study planned for participants to take part in three treatment periods and receive each of the treatments in a random manner: fluticasone furoate 100 µg in the morning with evening placebo, fluticasone furoate 100 µg in the evening with morning placebo, and placebo at both times.

The brief summary describes each treatment period as lasting 14 (+/-2) days, with a 14 day run-in and washout periods of 14 to 21 days. It gives an approximate total study duration of 13 to18 weeks for each subject. The registry records an enrollment of 28. The brief summary states that 24 subjects would be enrolled to ensure 20 evaluable subjects; the reason for the difference between that planning statement and recorded enrollment is not reported in the registry record.

The primary outcome was measured on Day 14 of each treatment period. The stated timeframe is 24 hours post-PM dose on Day 14 of each treatment period, up to Study Day 105. The record describes serial FEV1 readings at 3, 6, 9, 12, 15, 18, 21, and 24 hours post-dose. The highest of three technically acceptable measurements was recorded at each time point. The posted outcome Ns are 21 for morning active dosing, 22 for evening active dosing, and 22 for placebo. In a crossover trial, these treatment-specific counts should not be read as three independent groups of participants; participants were intended to contribute measurements under all three treatments.

The study is marked completed. Its start is recorded as 2013-03 and its primary completion as 2014-03. The registry record does not report the treatment sequence distribution or the number of participants who completed every period.

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: Participants meeting randomization criteria were enrolled in the study for 13-18 weeks: three 14-day treatment periods separated by a 14- to 21-day washout period, followed by a follow-up visit within 7-14 days of the last dose.

Treatment Period 1 (14 Days)

Reasons for not completing this period:

Washout Period 1 (14-21 Days)

Treatment Period 2 (14 Days)

Washout Period 2 (14-21 Days)

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all participants randomized to treatment who received at least one dose of study medication, and had at least one Baseline and post-dose FEV1 measurement performed. Only those participants with non-missing covariates and a post-Baseline FEV1 measurement 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.

6. Primary Endpoint

The registry lists the primary outcome as Weighted Mean Forced Expiratory Volume in 1 Second (FEV1) Measured Over 24 Hours at Day 14 of Each Treatment Period, measured over 24 hours post-PM dose on Day 14 of each treatment period (up to Study Day 105).

The primary endpoint was weighted mean Forced Expiratory Volume in 1 Second (FEV1), measured over 24 hours at Day 14 of each treatment period and reported in liters. FEV1 measures the maximal amount of air that can be forcefully exhaled in one second. It is used in this trial as a continuous measure of lung function, allowing the study to compare the average lung-function measurement across treatment conditions.

Measurements were collected serially after the evening dose, at the time points listed in the registry record. The endpoint combines these measurements into a weighted mean rather than treating a single reading as the entire 24-hour response. The posted arm results are least-squares means with standard errors. A least-squares mean is a model-based estimate adjusted for the covariates and design terms described in the record, rather than simply the arithmetic average of each treatment group’s raw observations.

The endpoint is relevant to the stated comparison because morning and evening dosing could be assessed against placebo using the same planned lung-function measure and assessment period. The record also reports pre-treatment AM and PM trough FEV1 and Peak Expiratory Flow as secondary outcomes, as well as participants with any adverse event. The registry record does not report the detailed results for all of those secondary measures in the information.

The endpoint describes a measured lung-function outcome during the study. It does not by itself establish how participants felt, how long any difference lasted beyond the assessment period, or how results would generalize beyond the enrolled study population.

7. Results Posted in the Registry

• FF 100 µg AM: mean 3.30 versus 3.23 on control; difference 0.08 (95% CI -0.09 to 0.24), standardized effect d = 0.28; z-test p = 0.360.
• FF 100 µg PM: mean 3.33 versus 3.23 on control; difference 0.10 (95% CI -0.06 to 0.27), standardized effect d = 0.38; z-test p = 0.204.

8. Statistical Interpretation

9. Statistical Methods Explained

The trial’s reported primary analysis and the unadjusted recalculations answer related but distinct statistical questions. Keeping those approaches separate matters when interpreting the estimates.

What does a least-squares mean represent?

The registry identifies the primary measure as a least-squares mean and states that it was analyzed using a mixed-effects analysis of covariance model. In general, a least-squares mean is an adjusted estimate from a statistical model. It can account for specified covariates and design features, rather than summarizing only the observed values without adjustment. The registry lists fixed effects for treatment and period, participant baseline, period baseline, gender, and age, with participant as a random effect.

In general, a mixed-effects model can represent both systematic differences associated with fixed terms and variation associated with participants. The participant random effect is relevant to a crossover design because observations from the same person are related rather than independent. The model can account for that within-participant structure. The record does not provide the model coefficients, a full model specification, or details on how the model was fitted.

Why are the recalculations called unadjusted?

The recalculated comparisons use the posted least-squares means and standard errors to form approximate mean differences and intervals. They are labelled unadjusted because they are simple comparisons of posted summary statistics rather than a reproduction of the sponsor’s full mixed-effects model. The pooled standard deviations used in the calculation are approximate. These recalculations do not preserve every feature of a crossover model, such as the participant-level covariance among measurements taken under different treatments.

For morning active dosing versus placebo, the recalculated mean difference is 0.076 liters, with an interval from -0.087 to 0.239 and p = 0.36. For evening active dosing versus placebo, the recalculated difference is 0.105 liters, with an interval from -0.057 to 0.267 and p = 0.204. These estimates are useful for a simple summary-statistics comparison, but they should not be presented as if they were the sponsor’s adjusted analysis.

Why does crossover structure matter?

In general, a crossover design compares treatments within participants, which can reduce the influence of stable differences between people. At the same time, observations within a participant are correlated, and the analysis must handle that relationship. Period and treatment sequence can also matter in crossover studies. The registry lists period as a model term but does not report a sequence term or details about carryover assessment. The washout periods are described, but the registry record does not report the rationale for their duration or the results of any carryover assessment.

The listed treatment-specific outcome counts are 21, 22, and 22. They do not show how many participants posted usable measurements for every treatment period, and the record does not provide participant-level data or a complete-case count for the primary outcome. The stated Intent-to-Treat population requires randomization, at least one dose, and baseline and post-dose FEV1 measurements; the record further notes that only participants with non-missing covariates and a post-baseline FEV1 measurement were analyzed. The wording of the population description is incomplete, so fuller details of analysis-population handling are not reported in the registry record.

How should the sponsor’s median comparisons be read?

The sponsor-reported analyses use median differences in final values, with 90% intervals. The record gives a morning-versus-placebo median difference of 0.077, an evening-versus-placebo median difference of 0.105, and an active-schedule difference of -0.028. The 90% intervals are reported as 0.001 to 0.152, 0.029 to 0.180, and -0.102 to 0.045, respectively. P-values are not reported for these analyses. A median difference is not the same estimand as a difference between means, so the sponsor’s results should not be expected to match the unadjusted mean-difference calculations exactly.

In general, a confidence interval represents a range of estimates compatible with the data and a specified method, under that method’s assumptions. The sponsor’s intervals are explicitly reported as 90%. The recalculated intervals are posted as unadjusted intervals, and their values should be read as an approximate summary-statistics calculation rather than as an exact reproduction of the trial model.

What can the p-values establish?

The recalculated p-values describe the compatibility of the unadjusted mean differences with a null difference, under the calculation’s assumptions. They are not the sponsor’s p-values; the sponsor’s p-values are not reported in the registry record. A p-value does not measure the size or importance of an effect, nor does it give the probability that a hypothesis is true. Interpretation should consider the estimated difference, its interval, the analysis method, and the limits of the recorded data together.

The planning calculations use a two-sided significance level of 0.05, but that assumption belongs to the planning illustration. The original trial’s sample-size justification and analysis-plan details are not reported in the registry record. The posted results do not identify whether interim analyses were planned or conducted, so that information is not reported in the registry record.

10. Confidence Intervals and Precision

The intervals around the unadjusted mean differences are wide enough to include zero. For morning dosing versus placebo, the recalculated estimate is 0.076 liters and the interval runs from -0.087 to 0.239. For evening dosing versus placebo, the estimate is 0.105 liters and the interval runs from -0.057 to 0.267. In general, an interval that includes zero indicates that the corresponding unadjusted calculation does not rule out a zero mean difference under its assumptions. It also includes values on either side of zero, so the estimate is not precise enough to distinguish those possibilities on its own.

The sponsor-reported 90% intervals address median differences rather than the mean differences used in the recalculations. The morning-versus-placebo interval is 0.001 to 0.152, the evening-versus-placebo interval is 0.029 to 0.180, and the morning-versus-evening interval is -0.102 to 0.045. The first two intervals are reported zero, while the interval for the active-schedule comparison includes zero. These statements describe the posted intervals; they do not establish clinical importance, and the registry does not report p-values for those sponsor comparisons.

Precision depends on both the estimated effect and the amount of uncertainty in the measurements. The standard errors for the posted least-squares means are 0.059, 0.058, and 0.059 liters. In general, standard errors quantify uncertainty in an estimate under the analysis method; they are not measures of how much individual participants vary. The record does not provide the raw distributions or participant-level data needed to examine that variation directly.

The recalculated intervals use approximate pooled variability and do not reproduce the full crossover model. Consequently, their apparent precision should not be treated as the precision of the sponsor’s adjusted analysis. The registry’s sponsor-reported 90% intervals are a separate set of results, based on median differences in final values. The record does not state a clinical threshold for interpreting either set of intervals.

11. 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 entries describe participants per arm for 80% power and participants per arm for 90% power. They are not total event counts. The underlying illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It uses the observed effect as a reference and considers planning for 100%, 75%, and 50% of that observed effect. These calculations are planning illustrations, not observed power.

In plain language, the 80% power column gives the estimated number of participants per arm for a design intended to have an 80% chance of detecting the specified effect, if the planning assumptions hold. The 90% power column gives the estimated number per arm for a design intended to have a 90% chance under the same assumptions. The calculations are given separately for the morning-versus-placebo and evening-versus-placebo comparisons, because their observed effects differ.

For morning dosing versus placebo, the entries range from 202 participants per arm when planning for 100% of the observed effect to 806 participants per arm when planning for 50% of that effect at 80% power. At 90% power, the corresponding entries range from 270 to 1,079 participants per arm. For evening dosing versus placebo, the 80% power entries range from 108 to 429 participants per arm, and the 90% power entries range from 144 to 574 participants per arm. The 75% effect entries fall between the 100% and 50% entries.

Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants under the same assumptions. These are illustrations based on the observed estimates, not the trial’s original design calculations. The trial’s own sample-size justification and assumptions are not reported in the registry record. The figures should not be interpreted as evidence about the study’s observed power.

12. 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 = 0.076; pooled standard deviation σ = 0.272.
2. n = 2 × (1.96 + 0.842)² × 0.272² / 0.076² = 201.4, rounded up to 202 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 <- 0.0760000000000001                      # observed difference in means
sigma <- 0.272215288723161                     # 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(1808339)
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 = 202 (80% power), 270 (90% power)
 75% of observed effect: n per arm = 359 (80% power), 480 (90% power)
 50% of observed effect: n per arm = 806 (80% power), 1,079 (90% power)
power.t.test: 202.4 
Simulated power at n = 202 per arm: 0.796 (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.

13. Analyses Reported by the Sponsor

The registry’s sponsor-reported comparisons are median differences in final values, with 90% intervals. The reported median difference is 0.077 for morning fluticasone furoate versus placebo, 0.105 for evening fluticasone furoate versus placebo, and -0.028 for morning versus evening fluticasone furoate. Their intervals are 0.001 to 0.152, 0.029 to 0.180, and -0.102 to 0.045, respectively. P-values are not reported for these sponsor analyses.

The unadjusted recalculations instead compare the posted least-squares means using mean differences and approximate pooled variability. They give differences of 0.076 for morning dosing versus placebo and 0.105 for evening dosing versus placebo. Their intervals include zero, and their p-values are 0.36 and 0.204, respectively. These recalculations do not replace the sponsor’s own model-based analysis and should not be read as the same estimand: a median difference and a mean difference are different summaries.

No discrepancy is flagged in the registry record. Where the two approaches appear to tell different stories, the distinction in measure and method is important. The sponsor’s reported analyses are the registry’s own trial analyses; the recalculations are simple checks from posted summary statistics and do not recreate the crossover model. Further details of the sponsor’s method are not reported in the registry record.

14. Multiplicity, Missing Data and Analysis Populations

The registry reports several outcome measures and three sponsor-reported analyses. The primary outcome is weighted mean FEV1 over 24 hours at Day 14 of each treatment period. Secondary outcomes listed include pre-treatment AM and PM trough FEV1 on Day 14 of each treatment period, number of participants with any adverse event, and Peak Expiratory Flow. The record notes four outcome measures and three analyses, but detailed results for all secondary measures are not included in the reported information.

When multiple outcomes or comparisons are assessed, the chance of at least one apparently unusual result can increase. In general, multiplicity methods can adjust interpretation or testing to address that issue. Whether a multiplicity adjustment was planned or used is not reported in the registry record. The sponsor’s comparisons have no p-values recorded, and the record does not state a testing hierarchy or identify which comparisons were formally confirmatory. The unadjusted recalculated p-values should therefore be read as individual comparisons, not as multiplicity-adjusted conclusions.

The registry describes a specific Intent-to-Treat population: randomized participants who received at least one dose and had baseline and post-dose FEV1 measurements. It further states that only participants with non-missing covariates and a post-baseline FEV1 measurement were analyzed, but the population description is truncated. The record does not provide a full account of exclusions, missing-data handling, or sensitivity analyses for missing measurements. The count of analyzed participants by treatment condition does not establish how many contributed complete data across all periods.

In general, missing measurements can affect an estimate if the reasons for missingness are related to the outcome or treatment. Statistical approaches to missing data rely on assumptions, and those assumptions should be described to assess how they affect interpretation. The specific missing-data assumptions and methods are not reported in the registry record.

The model description lists treatment and period as fixed effects, participant baseline, period baseline, gender, and age as covariates, and participant as a random effect. The record does not report the full model specification, details of treatment sequence handling, a carryover analysis, or interim-analysis information. The trial’s complete statistical analysis plan is not reported in the registry record.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures show zero serious events among 23 participants at risk during morning fluticasone furoate treatment, zero among 24 during evening treatment, and zero among 25 during placebo. These counts describe the reported serious adverse events for the listed treatment periods. They do not mean that no adverse events of any kind occurred: the registry separately reports 18 participants with any adverse event in the morning group, 18 in the evening group, and 16 in the placebo group.

These treatment-specific at-risk counts differ from the primary outcome counts. The registry’s adverse-event groups report the number at risk for safety outcomes, while the primary results give the numbers contributing to the FEV1 outcome. As this is a crossover study, the safety counts should not be interpreted as three independent groups of participants. The same participants could contribute to more than one treatment condition.

In general, a zero count in a study of this size does not establish that an event cannot occur; it describes what was recorded among the participants and exposure periods in the trial. The registry does not list serious adverse event terms, and deaths are not reported as numeric counts. The summary does not provide event timing, severity grades for non-serious events, or participant-level exposure details. These figures describe the registry record and are not a basis for medical advice.

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

The posted results compare weighted mean FEV1 during treatment periods for morning and evening fluticasone furoate dosing and placebo. The primary least-squares mean estimates were 3.303 liters, 3.332 liters, and 3.227 liters, respectively. The recalculated unadjusted mean differences versus placebo were 0.076 liters for morning dosing and 0.105 liters for evening dosing. Their intervals include zero, and their p-values were 0.36 and 0.204. This describes the uncertainty in those simple comparisons rather than proving that the treatments are equivalent or different.

The registry’s sponsor-reported median comparisons are a separate analysis. Their 90% intervals for morning dosing versus placebo and evening dosing versus placebo are reported zero, while the interval for the morning-versus-evening comparison includes zero. Because the sponsor’s measure is a median difference and the recalculations use means, the results should not be combined into a single estimate. The registry does not report sponsor p-values or enough methodological detail to reproduce those analyses.

A confidence interval is not a range containing every participant’s response. In general, it describes uncertainty around an estimate under a statistical method and its assumptions. Neither the point estimates nor their intervals establish whether a difference is large enough to matter clinically. A clinical-importance threshold is not reported in the registry record.

The crossover design means participants were intended to receive all three conditions, so comparisons are informed by repeated treatment periods within participants. That design can make within-person comparisons informative, but correct interpretation depends on handling the repeated observations, period effects, and missing measurements. The record describes a mixed-effects analysis but does not provide all details needed to evaluate these features.

The results concern a specific lung-function endpoint, assessment schedule, and study population. They do not establish effects beyond the study’s observation period or for populations not represented in the trial. They also do not provide a basis for choosing a dosing time. The record should be read as a report of measured outcomes and their uncertainty, not as medical advice or a general claim about treatment.

17. Why This Trial Matters Statistically

This study presents a useful statistical example of why trial design and analysis method matter alongside the numerical estimate. The three-way crossover design planned for the same participants to experience morning active dosing, evening active dosing, and placebo. That differs from a parallel-group study in which each person receives only one assigned condition. Repeated measurements can support within-participant comparisons, but they also require an analysis that accounts for dependence among observations from the same participant.

The registry identifies a mixed-effects analysis of covariance model and lists treatment, period, baseline measurements, gender, and age among its terms, with participant as a random effect. This description signals that the primary results are adjusted model estimates. The simple recalculations from posted summaries do not reproduce that model, illustrating why summary-statistic checks can be informative without substituting for the sponsor’s analysis.

The record also highlights the importance of distinguishing means from medians and intervals from p-values. The recalculations use mean differences and approximate pooled variability; the sponsor reports median differences in final values with 90% intervals. Even when numerical estimates are close, those methods do not answer precisely the same question. Reporting the estimand and analysis method is essential to understanding what a contrast means.

Finally, the planning illustrations demonstrate how sample-size requirements depend on the effect size a future study aims to detect and the desired power. Those figures are not the original study’s sample-size justification and are not observed power. The registry’s limits on reporting—such as absent sponsor p-values, incomplete missing-data details, and unreported multiplicity procedures—also show why a result must be read together with the completeness of its statistical record.

18. 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 limitations affect interpretation. The primary outcome groups contain 21, 22, and 22 observations, but the registry does not provide participant-level data or the number of people with complete measurements for all three periods. The listed Ns therefore do not show how many within-participant comparisons were available. The description of the analysis population is incomplete, and detailed missing-data methods are not reported in the registry record.

The registry describes an adjusted mixed-effects analysis but does not provide the full model specification or all model diagnostics. It lists treatment and period terms and participant as a random effect, but details about treatment sequence, carryover assessment, or the handling of incomplete treatment periods are not reported in the registry record. These omissions limit independent assessment of how the crossover structure was handled.

The sponsor-reported median differences have 90% intervals but no reported p-values, and the specific method for those analyses is not identified. The unadjusted recalculations use approximate pooled standard deviations and do not reproduce the sponsor’s model. Their interval estimates should not be treated as a substitute for the adjusted analysis. The record does not report a clinical-importance threshold for FEV1 differences.

The brief summary’s enrollment plan describes 24 subjects to ensure 20 evaluable subjects, while recorded enrollment is 28. The reason for the difference is not reported in the registry record. The original sample-size justification, multiplicity plan, interim-analysis plan, and full statistical analysis plan are also not reported in the registry record. Although secondary outcomes are listed, detailed results for all of them are not included in the information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: To Investigate the Effects of Altering the Time of Day of Dosing (Morning or Evening) With Fluticasone Furoate 100 Micrograms Once Daily Administered Via a Dry Powder Inhaler in Subjects With Asthma — NCT01808339.
• Registry record last updated 2017-01-09; status last verified 2016-11.
• Results first posted 2014-09-04.
• 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.

22. Record Summary

This completed Phase 2 study examined morning and evening dosing of fluticasone furoate 100 µg against placebo in a randomized, triple-masked, three-way crossover design. The primary outcome was weighted mean FEV1 over 24 hours at Day 14 of each treatment period. The posted least-squares means were 3.303 liters for morning dosing, 3.332 liters for evening dosing, and 3.227 liters for placebo.

Unadjusted recalculations gave mean differences versus placebo of 0.076 liters for morning dosing and 0.105 liters for evening dosing; both recalculated intervals include zero. Sponsor-reported results use median differences with 90% intervals and are a distinct analysis. The record also reports zero serious adverse events in each treatment condition, alongside participants with any adverse event. Incomplete reporting of missing-data handling, multiplicity, and sponsor-analysis methods limits further assessment.