A 6-month Study to Evaluate the Efficacy and Safety of Fluticasone Furoate (FF)/GW642444 Inhalation Powder in Subjects With Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A 6-month Study to Evaluate the Efficacy and Safety of Fluticasone Furoate (FF)/GW642444 Inhalation Powder in Subjects With Chronic Obstructive Pulmonary Disease (COPD) (NCT01053988), a randomized phase 3 study. The primary outcome is Change From Baseline in Weighted Mean FEV1 Over 0-4 Hours Post-dose at Day 168.

2. Clinical Question

The trial addressed pulmonary function in people with COPD. The registry identifies the endpoint as a co-primary endpoint and describes FEV1 as the maximal amount of air that can be forcefully exhaled from the lungs in one second. For this outcome, the comparison concerns the average change from baseline in a weighted mean of serial FEV1 measurements, rather than a single reading at one moment.

The study also included secondary outcomes for respiratory-disease-related dyspnea, peak post-dose FEV1 on Day 1, and time to onset of an increase in FEV1. These outcomes provide additional kinds of information, but they do not replace the primary endpoint. Their interpretation depends on their own estimates, uncertainty, and analysis methods, and the registry record does not report a multiplicity strategy for the set of outcomes.

3. Trial Design

The registry describes a Phase 3, randomized, double-masked, parallel-group study with enrollment of 1031. Its official title describes a 24-week comparison of FF/VI, its individual components, and placebo in people with COPD. The study status is completed. The registry lists the start as 2009-10-05 and primary completion as 2011-02-01.

Five arms appear in the primary outcome results: placebo, FF 100 µg OD, VI 25 µg OD, FF/VI 50/25 µg OD, and FF/VI 100/25 µg OD. The intervention descriptions identify FF as an inhaled corticosteroid and GW642444 as a long-acting beta agonist; the arm labels use VI for the single-agent and combination doses. The registry also lists placebo as an intervention. The study title describes inhalation powder delivered once daily in the morning via a dry powder inhaler.

The primary endpoint timeframe is baseline to Day 168. The registry’s primary endpoint description says FEV1 was measured by electronic spirometry at baseline and serial visits. The weighted mean used pre-dose and post-dose readings over the 0–4-hour period. A repeated-measures model was used, with treatment, smoking status at screening, baseline FEV1, centre grouping, day, and specified interactions among day, baseline, and treatment as covariates.

Endpoint-specific analysis counts are lower than the overall enrollment and differ across arms. The registry says the numbers presented reflect data available at the relevant time point. It defines the primary analysis population as randomized participants who received at least one dose, while the full handling of missing observations and covariate information is 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: Eligible participants (par.) completed a 2-week single-blind (placebo) Run-in Period (RIP) to assess Baseline rescue use, symptoms, disease stability. Par. were then randomized to a 24-week Treatment Period. A total of 1804 par. were screened, 1390 entered the RIP, of whom 1031 were randomized, 1030 received at least one dose of study medication.

2-week, Single-blind Run-In Period

Reasons for not completing this period:

24-week, 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 randomized par. who received at least one dose of study medication. Number of par. presented represent those with data available at the time point being presented; however, all par. in the ITT population without missing covariate information and with at least one post BL measurement are included in the analysis

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 in Weighted Mean FEV1 Over 0-4 Hours Post-dose at Day 168, measured over Baseline (BL) to Day 168.

The primary endpoint is change from baseline in weighted mean FEV1 over 0–4 hours after dosing at Day 168, measured in liters. FEV1 is the maximal amount of air forcefully exhaled from the lungs in one second. It is a measure of pulmonary function, and the registry designates this endpoint as co-primary.

The weighted mean combines serial FEV1 readings taken before and after dosing during the specified period. The registry description includes pre-dose measurements and post-dose measurements at 5, 15, and 30 minutes and 1, 2, and 4 hours. The baseline value is the mean of two pre-dose assessments on Day 1. Change from baseline is defined as the Day 168 weighted mean minus that baseline value.

Using repeated readings can characterize the measured response across the post-dose interval instead of relying on one isolated observation. The repeated-measures model also uses data across scheduled visits, with treatment and other listed covariates included in the analysis. In general, an endpoint should be interpreted in its stated units and timeframe: a change in liters describes the measured difference in lung-function volume, not by itself a complete account of symptoms, daily functioning, or other outcomes important to participants.

The registry reports least-squares means with standard errors for the arms. Least-squares means are model-based adjusted means, so they are not simply the raw averages of all enrolled participants. The available results describe the endpoint and statistical contrasts; the registry does not report a threshold for judging whether a given change is clinically important.

7. Results Posted in the Registry

• FF 100 µg OD: mean 0.08 versus 0.03 on control; difference 0.05 (95% CI 0.00 to 0.10), standardized effect d = 0.25; z-test p = 0.037.
• VI 25 µg OD: mean 0.13 versus 0.03 on control; difference 0.10 (95% CI 0.05 to 0.15), standardized effect d = 0.47; z-test p = <0.001.
• FF/VI 50/25 µg OD: mean 0.22 versus 0.03 on control; difference 0.19 (95% CI 0.14 to 0.24), standardized effect d = 0.88; z-test p = <0.001.
• FF/VI 100/25 µg OD: mean 0.20 versus 0.03 on control; difference 0.17 (95% CI 0.12 to 0.22), standardized effect d = 0.80; z-test p = <0.001.

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 Chronic Respiratory Disease Questionnaire Self-administered Standardized (CRQ-SAS) Dyspnea Score at Day 168

• 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 100 µg OD: mean 0.29 versus 0.23 on control; difference 0.06 (95% CI -0.18 to 0.30), standardized effect d = 0.06; z-test p = 0.626.
  • VI 25 µg OD: mean 0.37 versus 0.23 on control; difference 0.14 (95% CI -0.10 to 0.38), standardized effect d = 0.14; z-test p = 0.255.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FF 100 µg OD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VI 25 µg OD and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Peak Post-dose FEV1 (0-4 Hour) on Day 1

• 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 100 µg OD: mean 0.12 versus 0.11 on control; difference 0.01 (95% CI -0.02 to 0.04), standardized effect d = 0.08; z-test p = 0.389.
  • VI 25 µg OD: mean 0.25 versus 0.11 on control; difference 0.14 (95% CI 0.11 to 0.17), standardized effect d = 1.00; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FF 100 µg OD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for VI 25 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary pulmonary-function assessment to dyspnea, early post-dose lung function, and time to onset. Across the posted numerical summaries, the general pattern is not uniform across outcome types: arm estimates differ in their separation from placebo, and the apparent amount of uncertainty varies. The CRQ-SAS dyspnea estimates are accompanied by unadjusted recalculations with intervals that include zero for the listed placebo comparisons. The Day 1 peak FEV1 summaries show a different pattern, with the VI and combination arm estimates higher than the placebo estimate. These summaries provide context, but they are not a substitute for the primary Day 168 endpoint.

The registry lists time to onset as a secondary outcome, but numerical results for that outcome are not reported in the registry record. The posted secondary results also do not include sponsor-reported analyses in the information available for these outcomes. Accordingly, the numerical contrasts and intervals in the secondary summaries are unadjusted recalculations rather than the registry’s reported mixed-model results for the primary endpoint.

Secondary outcomes can help describe whether the primary finding aligns with other measured aspects of function, but each outcome addresses a different question and may have a different measurement scale or timeframe. A Day 1 peak FEV1 measure is not interchangeable with a weighted mean over the post-dose interval at Day 168. Likewise, a dyspnea questionnaire score reflects a different domain from spirometric lung function.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for apparently notable findings by chance. The registry record does not report whether or how multiplicity was controlled, so the secondary p values from recalculations should be treated as exploratory evidence rather than as confirmatory conclusions. The broad pattern can be noted, but it does not resolve the uncertainty about clinical importance or replace the sponsor-reported primary analysis.

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

• Change From Baseline in Chronic Respiratory Disease Questionnaire Self-administered Standardized (CRQ-SAS) Dyspnea Score at Day 168
• Change From Baseline in Peak Post-dose FEV1 (0-4 Hour) on Day 1
• Time to Onset (Increase of 100 Milliliter [mL] From Baseline in 0-4 Hours Post-dose FEV1) on Treatment Day 1

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is measured in liters and expressed as change from baseline. The registry reports least-squares means and standard errors for each arm, then reports least-squares mean differences from mixed models. A mean summarizes the central level of a continuous measurement. A standard error describes the precision of an estimated mean; it is not the same quantity as the spread of individual participants’ measurements.

What does the repeated-measures model do?

In general, a repeated-measures model analyzes measurements collected from the same participants at multiple times while accounting for the fact that observations from one participant are related. The registry says its model included treatment, smoking status at screening, baseline FEV1, centre grouping, day, and interactions of day with baseline and treatment. This adjustment means the reported least-squares means and contrasts are model-based, rather than simple differences between unadjusted group averages.

The model description identifies the covariates, but it does not give a full account of the model specification. For example, the covariance structure, estimation details, and the complete handling of missing observations are not reported in the registry record. Those details can affect how repeated observations contribute to estimates and how uncertainty is calculated, so the listed covariates alone are not a complete statistical analysis plan.

How should the contrasts be read?

A least-squares mean difference is a contrast between two model-adjusted arm estimates. In this trial, the registry reports the contrast in liters for selected arm pairs. A positive contrast against placebo means the adjusted estimate for the named active arm is higher than the adjusted placebo estimate. It does not mean every participant in that arm had a higher measurement, and it does not describe the range of individual responses.

The sponsor’s analyses use a mixed-model method, while the simple recalculations use the posted arm summaries and are unadjusted. The recalculations use approximate standard deviations inferred from the reported standard errors, as identified in the statistical outputs. This distinction matters: the sponsor’s model uses the stated repeated-measures framework and covariate adjustment, whereas an unadjusted two-arm calculation cannot reproduce all features of that analysis.

Where the recalculated and sponsor-reported estimates differ, the sponsor’s own analysis takes precedence. The differences are small in the displayed estimates, but the relevant point is methodological: calculations based on summary values are checks, not replacements for the trial’s reported model. The registry’s reported estimates, confidence intervals, and p values should therefore anchor interpretation of the primary comparisons.

What do confidence intervals and p values describe?

In general, a confidence interval gives a range of values compatible with the data and the assumptions of the analysis, at the stated confidence level. A narrower interval indicates greater precision than a wider interval, all else equal. For a contrast, an interval that includes zero does not rule out no difference under the model at that confidence level; an interval wholly on one side of zero indicates that the reported range excludes zero. These statements concern statistical uncertainty, not clinical importance.

A p value describes how incompatible the observed data are with a specified null hypothesis under the analysis assumptions. It does not measure the size or importance of a difference, and it is not the probability that the null hypothesis is true. The registry’s p values are reported for its mixed-model comparisons, but the record does not say whether the tests were adjusted for the number of comparisons or outcomes.

Why can dispersion and sample size affect precision?

In general, variability among individual measurements and the number of observations contribute to the precision of a mean or contrast. Greater variability tends to make estimates less precise, while more observations can improve precision when the analysis assumptions hold. In repeated-measures settings, the association among measurements within participants also matters; it is not captured by looking only at one standard error per arm.

The primary arm summaries report standard errors, not standard deviations. A standard error reflects uncertainty in an estimated mean, while a standard deviation describes variability among observations. The unadjusted recalculations approximate a pooled standard deviation from the arm standard errors and sample sizes; they are consequently not equivalent to a reanalysis of individual participant data. The displayed confidence intervals from the registry’s mixed models are the more relevant uncertainty summaries for the sponsor-reported comparisons.

What is not established by these methods?

The registry record does not report the original sample-size justification, an interim-analysis plan, a complete statistical analysis plan, or a multiplicity procedure. It also does not report enough detail to evaluate all modeling choices or the missing-data assumptions. These absences do not invalidate the displayed estimates, but they limit how completely the analysis can be audited from the registry entry alone. Statistical evidence about a measured endpoint should be read alongside its confidence interval, analysis population, model description, and the limits of the record.

11. Confidence Intervals and Precision

The registry reports 95% confidence intervals for its mixed-model primary comparisons. For FF 100 µg OD versus placebo, the reported difference is 0.053 liters and the interval is 0.003 to 0.104. For VI 25 µg OD versus placebo, the difference is 0.103 liters and the interval is 0.052 to 0.153. For FF/VI 50/25 µg OD versus placebo, the difference is 0.192 liters and the interval is 0.141 to 0.243. For FF/VI 100/25 µg OD versus placebo, the difference is 0.173 liters and the interval is 0.123 to 0.224.

In general, a confidence interval expresses uncertainty about an estimated contrast under the analysis model. It is not a range containing a specified proportion of individual participants’ outcomes, and it does not show the probability that a particular value is true. The intervals describe precision in the estimated mean differences, not how much participants vary from one another.

Each reported primary interval lies above zero, while the interval for FF 100 µg OD is closer to zero than the intervals for the other active-versus-placebo comparisons. This describes the estimates’ statistical position and uncertainty. It does not establish whether any difference crosses a threshold that matters clinically; such a threshold is not reported in the registry record.

The arm-level standard errors are similar in the posted primary results, but they should not be substituted for the confidence intervals on treatment contrasts. A contrast’s uncertainty depends on the model and the information used to estimate both arms. The sponsor’s intervals come from the mixed-model analyses described in the record. The separate recalculated intervals are unadjusted approximations based on summary statistics, and the discrepancy flag means the sponsor’s analysis takes precedence.

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 figures are planning illustrations based on the observed effect, not the trial’s original design calculation. For the continuous outcomes, the figures mean participants per arm. The stated planning 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. For time-to-event outcomes, the convention would instead be total events, but the primary endpoint is continuous.

The 80% power column gives the illustrative number of participants per arm for a planned study to have an 80% chance of detecting the selected effect under those assumptions, if the effect and assumptions are correct. The 90% power column gives the corresponding planning figure for a 90% chance. Higher planned power generally requires more participants, all else equal. The figures are not observed power.

Rows for planning for 75% or 50% of the observed effect consider smaller target differences than planning for 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants under the same assumptions. These calculations are therefore sensitive to the effect chosen for planning. They should not be read as evidence that the observed effect will recur or as a justification used by the investigators.

The original trial’s sample-size justification and design assumptions are not reported in the registry record. The planning figures are separate illustrations and should not be used to infer that the trial was designed around the observed result.

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 = 0.054; pooled standard deviation σ = 0.218.
2. n = 2 × (1.96 + 0.842)² × 0.218² / 0.054² = 256.0, rounded up to 257 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 <- 0.054                      # observed difference in means
sigma <- 0.218071407395386                     # 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(1053988)
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 = 257 (80% power), 343 (90% power)
 75% of observed effect: n per arm = 456 (80% power), 610 (90% power)
 50% of observed effect: n per arm = 1,025 (80% power), 1,371 (90% power)
power.t.test: 257 
Simulated power at n = 257 per arm: 0.800 (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’s own primary analyses use mixed models and report least-squares mean differences with 95% confidence intervals and p values. The recalculations use posted arm-level summaries and are simple, unadjusted checks. They do not reproduce the repeated-measures model or its covariate adjustment.

The recalculated estimates are close to the sponsor’s estimates, but the record flags a discrepancy. For example, the unadjusted recalculation for FF/VI 100/25 µg OD versus placebo is 0.174 liters, while the sponsor-reported mixed-model difference is 0.173 liters. Other small differences also occur in the displayed comparisons. The sponsor’s own analysis takes precedence where the results differ.

This preference is not a claim that the sponsor analysis is free of assumptions. It reflects that the registry’s reported analysis is the trial’s model-based result, while the recalculation is derived from summary statistics and approximate dispersion. The sponsor’s confidence intervals and p values should be used when describing the registered primary comparisons. The recalculations can provide a rough independent check, but they cannot establish what an individual-level reanalysis would show.

The registry also reports comparisons between selected active arms. Those are distinct model-based contrasts, not recalculated versions of every possible pairwise comparison. The record does not report a complete multiplicity plan, so p values across this set should not be interpreted as though the family of tests and any adjustment were fully documented.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a co-primary endpoint and several secondary outcomes, and the reported analyses include multiple comparisons among study arms. The record does not report a multiplicity procedure, such as an adjustment to account for testing several outcomes or contrasts. Without that information, the p values should be read as reported for their individual analyses, not as proof that the overall chance of a false-positive conclusion across all tests was controlled.

The registry describes the primary analysis as a repeated-measures model and identifies its covariates. It does not report a full statistical analysis plan, a detailed hierarchy among co-primary endpoints, or an interim-analysis plan. These elements are important for understanding which tests were planned as confirmatory and how the investigators intended to handle several potential findings. They are not reported in the registry record.

The primary analysis population is described as all randomized participants who received at least one dose of study medication. The record says the numbers presented represent those with data available at the time point, and it refers to an additional restriction involving missing covariate information in the model description. The available description is truncated and does not fully specify the analysis set or missing-data procedure. Details such as imputation, assumptions about why data are missing, and sensitivity analyses are not reported in the registry record.

For that reason, the posted endpoint-specific counts should be kept distinct from overall enrollment. The primary outcome counts reflect participants with available data at the relevant time point, while the adverse-event counts use their own at-risk group sizes. These sets of counts describe different analysis contexts and should not be treated as interchangeable.

These reporting gaps limit a complete assessment of how the analysis was prespecified and how robust it is to missing observations or multiple testing. They do not change the values reported by the registry, but they do qualify the strength of broader conclusions drawn from the set of outcomes.

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: chronic obstructive pulmonary disease (2.9%), pneumonia (1.5%), carotid artery stenosis (1.0%), ischaemic stroke (1.0%), multiple fractures (0.5%).

The registry reports serious adverse events by arm as the number affected and the number at risk. The figures are 11 of 207 for placebo, 16 of 206 for FF 100 µg OD, 15 of 205 for VI 25 µg OD, 6 of 206 for FF/VI 50/25 µg OD, and 11 of 206 for FF/VI 100/25 µg OD. These are counts in the registry’s safety results, not the primary endpoint analysis counts.

The listed top serious-event terms include chronic obstructive pulmonary disease, pneumonia, carotid artery stenosis, ischaemic stroke, multiple fractures, and road traffic accident, with percentages reported for those terms. The registry does not provide enough context in the record to interpret these term percentages as comparative risks across arms. A term listed among serious events is a reported event, not by itself evidence that study medication caused it.

Deaths are not reported in the registry record for these arm summaries. Serious adverse-event counts alone do not describe all adverse events, their timing, duration, severity distribution, or causal assessment. They also do not establish a comparative safety conclusion. The figures should be read as recorded counts in the stated at-risk groups, alongside the limits of the safety information reported.

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

The posted primary results describe differences in a specific measure: change from baseline in weighted mean FEV1 over the 0–4-hour post-dose interval at Day 168. The registry’s mixed-model estimates and confidence intervals quantify those contrasts for the study arms. They do not describe every dimension of COPD, and they do not show how each individual participant’s lung function changed.

A statistically distinguishable contrast is not automatically a clinically important contrast. The registry record does not give a clinical-importance threshold for the FEV1 endpoint. It also does not supply enough information to translate the liter-based differences into expected changes in symptoms, daily activities, exacerbations, or other outcomes. Those outcomes should not be inferred from a spirometric result alone.

The findings apply to the enrolled study population, the regimens, and the endpoint timeframe described in the registry. They do not establish results for people or settings not represented in the record, and they do not answer every comparison among the five arms. The posted active-arm comparisons are model-based estimates, and their interpretation depends on the model and available data.

The secondary outcomes offer additional measurements, but they are not all reported with sponsor analyses, and a time-to-onset result is not reported in the registry record. The lack of a reported multiplicity plan also means that secondary findings should be interpreted cautiously. Safety counts are similarly descriptive and do not establish causation or a complete comparison of harms.

In general, clinical interpretation combines the estimated size of a difference, its uncertainty, the outcome’s relevance, and the quality and completeness of the evidence. The registry results support a description of the measured statistical contrasts. They do not, on their own, establish a treatment recommendation or a definitive overall balance of benefits and risks.

18. Why This Trial Matters Statistically

This trial illustrates why clinical trial results need to be read at more than one statistical level. The arm-level least-squares means describe estimated changes, while the mixed-model contrasts answer the direct comparison question. Confidence intervals add information about precision, and p values address compatibility with a null hypothesis under the analysis model. None of these measures alone establishes clinical importance.

It also shows why the analysis method matters. The primary outcome was measured repeatedly, and the registry reports a repeated-measures model with covariates and interactions. A simple calculation from arm summaries cannot reproduce that model. The small differences between unadjusted recalculations and sponsor estimates make the distinction concrete: summary-statistic checks can orient the reader, but the sponsor’s analysis is the appropriate reference for the registered model-based result.

The endpoint-specific counts and overall enrollment also demonstrate why denominators must be attached to the relevant analysis. The number enrolled is not the same as the number contributing data to a particular endpoint or safety summary. Reading the outcome, population, and denominator together prevents an apparent mismatch from being mistaken for a contradiction.

Finally, registry reporting has limits. The record gives useful estimates and some method details, yet it does not report the original sample-size justification, a complete multiplicity plan, or a full missing-data strategy. Recognizing what is and is not documented is part of statistical interpretation. It helps distinguish a clear numerical result from a broader conclusion that the record cannot fully support.

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 entry does not report the original sample-size justification or the assumptions used in designing the trial. The sample-size figures accompanying the results are planning illustrations based on observed effects, not evidence of the original design rationale. They should not be used to infer what the investigators planned before observing the outcomes.

The primary endpoint description identifies the repeated-measures model and lists covariates, but important implementation details are not reported in the registry record. The full analysis population description is incomplete, and the handling of missing data, model covariance structure, and sensitivity analyses is not specified. Endpoint counts therefore need to be understood as available-data counts rather than assumed to represent every randomized participant.

The record indicates a discrepancy between simple unadjusted recalculations and sponsor-reported analyses. The sponsor’s own model-based analyses take precedence, but the recalculations cannot independently validate all model assumptions. The registry also does not report a multiplicity strategy for the co-primary and secondary outcomes or for the several arm comparisons.

Some secondary numerical results are available as arm summaries and recalculations, but sponsor-reported analyses are not listed for those outcomes in the record. The time-to-onset outcome is named, but its numerical results are not reported in the registry record. These gaps make the secondary evidence less complete than the primary comparison results.

For safety, the record gives serious adverse-event counts and selected terms, but deaths are not reported in the registry record and the summaries do not establish causation. The registry information also does not provide a clinical-importance threshold for the primary FEV1 endpoint. These limitations constrain conclusions about clinical meaning, missing-data robustness, multiplicity, and comparative safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A 6-month Study to Evaluate the Efficacy and Safety of Fluticasone Furoate (FF)/GW642444 Inhalation Powder in Subjects With Chronic Obstructive Pulmonary Disease (COPD) — NCT01053988.
• Registry record last updated 2018-07-12; status last verified 2018-06.
• Results first posted 2013-08-15.
• 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

NCT01053988 is a completed Phase 3 randomized, double-masked, parallel-group study of inhaled FF, VI, FF/VI combinations, and placebo in people with COPD. The registry reports enrollment of 1031 and describes a 24-week study with once-daily morning dosing in the official title.

The primary outcome was change from baseline in weighted mean FEV1 over 0–4 hours post-dose at Day 168. The registry reports mixed-model least-squares mean differences, 95% confidence intervals, and p values for comparisons against placebo and selected active arms. Simple unadjusted recalculations differ slightly from some sponsor results; the sponsor’s analyses take precedence.

The registry also lists dyspnea, Day 1 peak FEV1, and time to onset as secondary outcomes. The original sample-size rationale, full multiplicity approach, complete missing-data method, and numerical time-to-onset results are not reported in the registry record. Serious adverse-event counts are reported by arm, while deaths are not reported in the registry record.