A Study to Evaluate the 24 Hour Spirometric Effect (FEV1) of Fluticasone Furoate/Vilanterol Inhalation Powder (100mcg Fluticasone Furoate (FF)/25mcg Vilanterol (VI)) Compared With Salmeterol/Fluticasone Propionate Inhalation Powder (50mcg Salmeterol/500mcg Fluticasone Propionate (FP)): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate the 24 Hour Spirometric Effect (FEV1) of Fluticasone Furoate/Vilanterol Inhalation Powder (100mcg Fluticasone Furoate (FF)/25mcg Vilanterol (VI)) Compared With Salmeterol/Fluticasone Propionate Inhalation Powder (50mcg Salmeterol/500mcg Fluticasone Propionate (FP)) (NCT01342913), a randomized phase 3 study. The primary outcome is Change From Baseline Trough in 24-hour Weighted-mean FEV1 on Treatment Day 84.

2. Clinical Question

3. Trial Design

This was a Phase 3 randomized, double-blind, parallel-group study in people with COPD. The registry lists an enrollment of 528 and a completed study. The recorded start date was 2011-02-01, and the primary completion date was 2011-10-01. The stated treatment period was 12 weeks.

One group received FF/VI 100/25 µg once daily; the other received salmeterol/FP 50/500 µg twice daily. Both combinations were described as an inhaled corticosteroid and long-acting beta agonist. The trial therefore compared two active combination regimens with different dosing schedules. The registry record does not identify a placebo group.

Randomization helps make the groups comparable at the start of a trial, while double masking is intended to limit influences from knowledge of assigned treatment on participant experience and outcome assessment. A parallel-group design means that participants were assigned to one regimen rather than crossing over between both. These are general features of the listed design; further details about the randomization sequence, concealment, masking procedures, or study conduct are not reported in the registry record.

The primary endpoint compared change from baseline in 24-hour weighted-mean FEV1 on Treatment Day 84. The registered timeframe was baseline and Day 84. The primary analysis lists an ITT population defined as randomized participants who received at least one dose of double-blind medication, with randomized participants treated as having received a dose unless definitive evidence showed otherwise. Outcome-specific analysis counts differ from the overall enrollment, and the registry record does not explain the participant flow or all reasons for unavailable measurements.

The trial also lists time to onset on Treatment Day 1 and change from baseline in trough FEV1 on Treatment Day 85 as secondary outcomes. Outcome results are not posted for every listed outcome. The original sample-size assumptions, detailed statistical analysis plan, and planned handling of missing observations 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: At Visit 1, participants entered a 2-week, single-blind (placebo) Run-in Period to obtain Baseline assessments of salbutamol use and to evaluate adherence with study treatment and procedures, diary card completion, and assessment of disease stability. At Visit 2, participants were randomized to a 12-week, double-blind Treatment Period.

2-week Run-in Period

Reasons for not completing this period:

Double-Blind Treatment Period

Reasons for not completing this period:

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 1 dose of double-blind medication. Randomized participants were assumed to have received double-blind medication unless definitive evidence to the contrary existed. Only participants available at the indicated time point were assessed.

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 Change From Baseline Trough in 24-hour Weighted-mean FEV1 on Treatment Day 84, measured over Baseline and Day 84.

The primary endpoint was change from baseline in 24-hour weighted-mean FEV1 on Treatment Day 84, measured in liters. FEV1 is the volume of air a person can forcefully exhale in one second and is a measure of pulmonary function. The registry describes the weighted mean as combining pre-dose and post-dose measurements taken at specified times over the 24-hour period on Day 84.

Baseline trough FEV1 was defined as the mean of two assessments made 30 and 5 minutes before the dose on Treatment Day 1. Change from baseline was calculated by taking the Day 84 average and subtracting the baseline value. This endpoint therefore describes change over the treatment period, rather than the Day 84 level alone.

Using measurements across the dosing interval can characterize pulmonary function over the full period between doses. That is relevant to the study’s stated comparison of once-daily and twice-daily regimens. This is a general explanation of the endpoint’s rationale; the registry record does not give a separate justification for selecting it as the primary endpoint.

7. Results Posted in the Registry

• FF/VI 100/25 µg QD: mean 0.13 versus 0.11 on control; difference 0.02 (95% CI -0.02 to 0.06), standardized effect d = 0.10; z-test p = 0.288.

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.

Change From Baseline in Trough FEV1 on Treatment Day 85

• 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 errors.
• Result:
  • FF/VI 100/25 µg QD: mean 0.11 versus 0.09 on control; difference 0.02 (95% CI -0.02 to 0.07), standardized effect d = 0.10; z-test p = 0.293.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FF/VI 100/25 µg QD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists time to onset on Treatment Day 1 and change from baseline in trough FEV1 on Treatment Day 85 as secondary outcomes. Posted results are available for the Day 85 trough FEV1 outcome. The registry record does not report a result for time to onset on Treatment Day 1. For the posted secondary endpoint, the estimated group contrast is close in direction and scale to the primary endpoint estimate, and its interval includes zero. This broad pattern does not provide a clearly separated secondary signal from the primary comparison.

The Day 85 trough measurement and the Day 84 weighted mean address related but distinct aspects of pulmonary function. Trough FEV1 focuses on a measurement before dosing, whereas the primary endpoint combines readings across a 24-hour period. Similar directions across related measures can add context, but they do not make the endpoints interchangeable or independently confirm the same claim.

Secondary results generally carry less inferential weight than a prespecified primary result. They may involve multiple outcomes, measurement times, or analyses, increasing the chance of apparently notable findings arising by chance if many comparisons are considered. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcomes. Accordingly, the secondary findings are best treated as supportive descriptive context rather than as standalone confirmatory evidence.

The registry lists three outcome measures, but only two secondary outcomes are named in the outcome information. It also records a single analysis. Details about the analysis plan for the unreported secondary outcome, reasons results are absent, and any planned adjustment across outcomes are not reported in the registry record. The overall secondary evidence is therefore limited by both the number of posted results and the lack of multiplicity information.

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

• Time to Onset on Treatment Day 1
• Change From Baseline in Trough FEV1 on Treatment Day 85

9. Statistical Interpretation

10. Statistical Methods Explained

The primary comparison is a comparison of group means for a continuous outcome. FEV1 is measured on a numeric scale, and the endpoint is the mean change from baseline in liters. A mean summarizes the central value of the measurements, while the standard error describes the estimated uncertainty in that mean. The registry identifies the arm values as least-squares means and their dispersion as standard errors.

What does ANCOVA contribute?

ANCOVA is a statistical method that compares groups while accounting for one or more covariates. In a clinical trial, adjustment can improve precision when the covariates are relevant to the outcome and are incorporated as specified in the analysis plan. The sponsor’s registered primary analysis is described as ANCOVA and reports a least-squares mean difference. A least-squares mean is a model-based group estimate, rather than simply the raw arithmetic average. The registry record does not describe the covariates in the model, the model specification, or how assumptions were assessed.

Randomization supports a comparison of treatment groups by helping balance baseline characteristics on average. Statistical adjustment is not a substitute for randomization, but it can account for selected variables in the analysis. Since the registry does not report which variables were included in ANCOVA, the adjusted result cannot be independently reconstructed from the posted arm summaries alone.

How should the difference and p-value be understood?

The mean difference is the estimated contrast between FF/VI and salmeterol/FP for the endpoint. Its sign depends on the comparison order; the registered estimate is positive for FF/VI relative to salmeterol/FP. A p-value describes how unusual data at least as incompatible with a specified null hypothesis would be under the assumptions of the test. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect.

The sponsor reports p = 0.282 for the ANCOVA comparison. The recalculation reports p = 0.288 using a simple unadjusted method. These values arise from different analyses: one is the registered adjusted analysis, and the other uses posted summary statistics for a basic unadjusted comparison. Small differences between them are expected when methods or rounding differ. The registry record does not report a full statistical analysis plan or additional model diagnostics.

Why do standard errors matter?

A standard error measures the precision of an estimated mean, not the spread of individual participants’ measurements. Smaller standard errors generally indicate a more precisely estimated group mean under the analysis assumptions. The arm-level standard errors are 0.015 for salmeterol/FP and 0.015 for FF/VI for the primary outcome. These values alone do not describe the full distribution of participant-level FEV1 changes.

The recalculated comparison uses an approximate pooled standard deviation derived from the posted standard errors and group sizes. This is a simple unadjusted calculation and does not account for covariate adjustment or any features of the sponsor’s ANCOVA. Its purpose is to provide a transparent comparison from the summary statistics, not to replace the registered analysis.

What assumptions underlie a mean-based comparison?

Mean-based methods summarize the numerical scale directly. Their interpretation depends on the analysis being appropriate for the outcome and study design. General considerations include whether observations are sufficiently independent, whether the model captures important features of the data, and whether residual behavior is adequate for the inference. The registry record does not report diagnostics, distributional summaries, or detailed information about dependence or departures from model assumptions.

Over-dispersion is a general concern when observed variability exceeds what a model assumes; it can make standard errors too small if not addressed. It is commonly discussed for count outcomes, rather than as a defining feature of a continuous FEV1 mean comparison. No over-dispersion assessment is reported for this endpoint. More broadly, the registry’s summary values cannot reveal the shape of individual participant measurements or the influence of outliers.

The endpoint uses repeated spirometric readings during a 24-hour period to form a weighted mean for each participant. The registry describes the scheduled measurement times, but does not report the weighting formula, rules for incomplete measurement profiles, or any sensitivity analyses. Those details matter for reproducing the endpoint and evaluating the impact of missing readings.

11. Confidence Intervals and Precision

The sponsor’s primary estimate was a least-squares mean difference of 0.022 liters, with a 95% confidence interval from -0.018 to 0.063. A confidence interval gives a range of values compatible with the observed data under the analysis and its assumptions. In repeated use, intervals constructed in this way would cover the underlying parameter at the stated rate if the assumptions and method were appropriate. It is not a probability statement that the particular interval has a 95% chance of containing the true difference.

The interval crosses zero, so the data do not rule out no difference between the regimens at the stated confidence level. The negative endpoint permits a small difference in the opposite direction to the point estimate, while the positive endpoint permits a larger difference in the estimated direction. The interval therefore communicates uncertainty more fully than the point estimate alone.

The unadjusted recalculation gives a 95% interval from -0.019 to 0.063. Its endpoints are close to the sponsor’s rounded interval, but it is based on summary statistics and a different method. The recalculated interval should not be treated as an exact reproduction of the adjusted ANCOVA result. The registry identifies no clinically important difference threshold, so the interval cannot be classified against such a threshold.

Precision is also shaped by the amount of observed information and the variability of the outcome. The primary endpoint counts were 233 for salmeterol/FP and 224 for FF/VI. These counts give context for the uncertainty but do not by themselves determine it; measurement variability and analysis choices also matter. The interval should be read as a statement about the estimated group contrast, not about the range of individual participant responses.

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 sample-size display gives planning illustrations in participants per arm for this continuous outcome; it does not give total event counts. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario sets the effect to detect as a stated fraction of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column means the illustrated number of participants per arm for a design that would have an 80% probability of detecting the specified effect under the stated assumptions, if that effect and assumptions were correct. The 90% power column gives the corresponding planning target for a 90% probability. These are design concepts, not probabilities that the observed trial result is correct or that a treatment effect exists.

The rows consider planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to reach the same target power under the same assumptions. The display is a planning illustration based on the observed effect, not observed power. It should not be interpreted as evidence that the original trial was designed around these targets or assumptions.

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 = 0.022; pooled standard deviation σ = 0.221.
2. n = 2 × (1.96 + 0.842)² × 0.221² / 0.022² = 1,590.1, rounded up to 1,591 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 <- 0.022                      # observed difference in means
sigma <- 0.221417809422978                     # 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(1342913)
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 = 1,591 (80% power), 2,129 (90% power)
 75% of observed effect: n per arm = 2,827 (80% power), 3,785 (90% power)
 50% of observed effect: n per arm = 6,361 (80% power), 8,515 (90% power)
power.t.test: 1591 
Simulated power at n = 1,591 per arm: 0.799 (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 own registered analysis is the ANCOVA comparison, with a least-squares mean difference of 0.022 liters, a 95% confidence interval from -0.018 to 0.063, and p = 0.282. It is the direct result reported for the primary endpoint. The registry’s analysis does not show a statistically significant difference between the groups.

The simple recalculation from the posted arm summaries gives a mean difference of 0.022, a 95% interval from -0.019 to 0.063, and p = 0.288. It is an unadjusted calculation and cannot reproduce the covariate adjustment used by ANCOVA. Its close estimate provides a basic consistency check, but it should not be substituted for the sponsor’s model-based result.

The sponsor and recalculated estimates are presented at different precision, and their confidence intervals and p-values are not identical. The registry record does not indicate a discrepancy requiring the sponsor’s analysis to be set aside. The appropriate reading is therefore to treat the registered ANCOVA as the main inferential analysis and the recalculation as a secondary check using the available summaries.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several hypotheses are tested in the same study. With more tests, the chance of at least one apparently unusual result can increase, even if there are no underlying effects. This is a general statistical concern and is relevant when a trial reports primary and secondary outcomes or multiple time points.

The registry identifies one primary endpoint and lists secondary outcomes concerning time to onset on Treatment Day 1 and trough FEV1 on Treatment Day 85. It does not report whether the secondary tests were adjusted for multiplicity, whether they followed a prespecified hierarchy, or whether only selected results were intended to be confirmatory. The original statistical analysis plan is not reported in the registry record. The posted primary p-value can be interpreted as the result of its reported ANCOVA analysis, but the multiplicity context for the wider set of outcomes is unclear.

Information about missing data is also limited. The primary population definition specifies randomized participants who received at least one dose of double-blind medication, with randomized participants assumed to have received a dose unless definitive evidence showed otherwise. The primary outcome analysis counts are smaller than the overall enrollment. The registry record does not explain the reasons that some participants are absent from endpoint counts, how missing FEV1 measurements were handled, or whether sensitivity analyses tested alternative assumptions.

The endpoint requires measurements across a 24-hour period, and incomplete profiles could affect calculation of a weighted mean. The registry describes the measurement schedule but does not state how incomplete profiles were treated or how the weighting was applied. These details limit independent assessment of missing-data assumptions and reproducibility.

The record also does not specify the covariates in the ANCOVA, the model diagnostics, or the planned handling of protocol deviations. Those omissions do not invalidate the reported result, but they constrain how fully its assumptions and robustness can be evaluated from the registry information alone.

16. 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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (0.8%), atrial fibrillation (0.8%), sialoadenitis (0.4%), infective exacerbation of chronic obstructive airways diseas (0.4%), angina pectoris (0.4%).

The registry reports serious adverse events in 3 of 262 participants at risk in the salmeterol/FP group and 6 of 266 participants at risk in the FF/VI group. It reports other adverse events affecting 30 of 262 and 32 of 266 participants, respectively. These are counts of participants reported as affected and the corresponding groups at risk; they should not be confused with the primary endpoint analysis counts.

The listed serious adverse event terms include pneumonia and atrial fibrillation at 0.8% each, and sialoadenitis, infective exacerbation of chronic obstructive airways disease, angina pectoris, and coronary artery disease at 0.4% each. These registry entries describe reported events, not an assessment of whether treatment caused them. The deaths field is not reported in the registry record.

Adverse-event counts are descriptive. They do not by themselves establish a comparative safety difference, especially without further details about event definitions, follow-up, severity, attribution, or statistical testing. The registry record does not provide enough information to infer causation or to characterize risks beyond the listed data.

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

The primary result is an estimate of the average difference between the two groups in change from baseline in 24-hour weighted-mean FEV1 on Treatment Day 84. The registered ANCOVA estimate is 0.022 liters in the direction of a larger change for FF/VI, with a 95% confidence interval from -0.018 to 0.063 and p = 0.282. The interval includes zero, and the analysis does not provide statistically significant evidence of a difference.

This does not prove that the treatments have identical effects. The confidence interval remains compatible with a range of differences, including values in either direction. Nor does the result prove that an effect of clinical importance is absent: the registry record does not state a threshold for clinical importance, and the interval cannot be judged against a threshold that is not reported.

The result applies to the specific regimens, outcome definition, population, and assessment time in this trial. It concerns spirometric change over the specified treatment period, not every aspect of COPD or every outcome that might matter to participants. The registry record lists secondary outcomes, but results are not posted for all of them. It also does not provide enough detail to assess all analysis assumptions, missing-data choices, or the wider multiplicity context.

Randomization and masking are features of the trial design, but their presence does not remove uncertainty in the estimate. The trial’s reported endpoint counts and confidence interval describe the available information for this comparison. Generalization to different populations, durations, or clinical settings requires evidence beyond this registered result. These statistics should be understood as a summary of the observed trial comparison, not as medical advice or a recommendation about treatment choice.

18. Why This Trial Matters Statistically

This trial illustrates why an estimated difference should be interpreted together with its confidence interval. The point estimate alone gives a direction and scale, but the interval communicates that the data are compatible with both a small difference in the opposite direction and a larger difference in the estimated direction. That uncertainty is central to understanding the primary comparison.

It also distinguishes a registered adjusted analysis from a simple recalculation. ANCOVA produces a model-based least-squares mean difference, while a recalculation from arm summaries is unadjusted. Their estimates are close, but they answer the comparison using different methods. Reporting both makes clear why an independent arithmetic check is informative without replacing the trial’s stated analysis.

The secondary outcomes, multiplicity, and missing-data details matter to interpretation even when the primary outcome is clear. A result for one endpoint does not resolve questions about other measures, and unavailable outcome information cannot be treated as a negative result. Likewise, planning illustrations derived from the observed effect are not evidence about the trial’s original design or its power after the fact.

Finally, the registry’s adverse-event counts illustrate the distinction between descriptive safety reporting and causal inference. Counts and listed event terms convey what was recorded, but do not by themselves establish attribution or a treatment-related difference. Together, these points show how study design, analysis method, precision, and reporting completeness shape what can responsibly be concluded from a clinical trial record.

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 registry record leaves several trial-specific details unreported. It does not give the original sample-size justification or the assumptions used to design the trial. The planning illustrations based on the observed effect cannot fill that gap and should not be read as the trial’s original design calculation.

The primary ANCOVA is named, but its covariates, model specification, and diagnostic checks are not described. The registry also does not report how incomplete 24-hour spirometry profiles were handled, how missing endpoint data were addressed, or whether sensitivity analyses were performed. The primary population definition is available, but the record does not provide a complete explanation of participant flow into the endpoint analysis counts.

Multiplicity procedures and the statistical status of secondary outcomes are not reported. Results are not posted for time to onset on Treatment Day 1, and the registry does not explain why. The significance and interpretation of secondary findings therefore cannot be fully assessed within a prespecified testing framework.

The registry reports the primary estimate and confidence interval but does not state a clinically important difference threshold. As a result, statistical uncertainty can be described, but clinical importance cannot be evaluated against a stated benchmark. The safety information is also limited to reported counts and listed terms; attribution, event detail, and deaths are not reported in the registry record.

These limits concern the information available in the registry record. They do not demonstrate that particular analyses or procedures were not conducted; they mean those details cannot be assessed from the registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the 24 Hour Spirometric Effect (FEV1) of Fluticasone Furoate/Vilanterol Inhalation Powder (100mcg Fluticasone Furoate (FF)/25mcg Vilanterol (VI)) Compared With Salmeterol/Fluticasone Propionate Inhalation Powder (50mcg Salmeterol/500mcg Fluticasone Propionate (FP)) — NCT01342913.
• Registry record last updated 2018-08-31; status last verified 2018-08.
• Results first posted 2013-07-30.
• 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 registry describes a completed Phase 3 randomized, double-blind, parallel-group study of FF/VI 100/25 µg once daily versus salmeterol/FP 50/500 µg twice daily in COPD. Enrollment was 528, and the stated treatment period was 12 weeks.

The primary endpoint was change from baseline in 24-hour weighted-mean FEV1 on Treatment Day 84. The sponsor’s ANCOVA reported a least-squares mean difference of 0.022 liters, with a 95% confidence interval from -0.018 to 0.063 and p = 0.282. The interval includes zero, and the result does not establish a difference between the groups.

The registry also lists secondary outcomes and adverse-event counts, but not all outcome results or detailed analysis and missing-data methods. The registered estimate should be read with its uncertainty and reporting limitations.