Study HZA106827: Efficacy/Safety Study of Fluticasone Furoate/Vilanterol (GW642444) in Adult and Adolescent Asthmatics: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study HZA106827: Efficacy/Safety Study of Fluticasone Furoate/Vilanterol (GW642444) in Adult and Adolescent Asthmatics (NCT01165138), a randomized phase 3 study. The primary outcome is Mean Change From Baseline in Clinic Visit Trough (Pre-bronchodilator and Pre-dose) Forced Expiratory Volume in One Second (FEV1) at Week 12.

2. Clinical Question

The central statistical contrast is change from Baseline to Week 12 in pre-bronchodilator, pre-dose FEV1. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. Trough measurements were taken at clinic visits while participants remained on treatment. The trial was randomized, double-blind, and parallel-group, with 612 participants enrolled. The registry describes a 12-week treatment period and lists asthma as the condition.

The trial’s question is about comparative average change in lung-function measurement, not about an individual participant’s experience or a guarantee of benefit. The posted results report adjusted analyses as well as recalculated, unadjusted comparisons. Those approaches should not be treated as interchangeable: the registry’s own ANCOVA results are the sponsor’s reported analysis, while the recalculations are descriptive checks based on the posted summary statistics. The registry record does not report the original sample-size justification or a complete statistical analysis plan.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled, parallel-group, multicentre study. Its official title describes placebo with rescue medication. Participants received once-daily fluticasone furoate/vilanterol, fluticasone furoate alone, or placebo inhalation powder for 12 weeks. The brief summary identifies the intended population as adults and adolescents 12 years of age and older with persistent bronchial asthma.

The registry records enrollment of 612 and status as completed. The start date is 2010-08-20 and the primary completion date is 2011-10-01. These dates describe the registry record; they do not by themselves establish when each participant began or completed treatment. The registry record does not report additional details about site distribution, allocation ratios, or the method used to generate the randomization sequence.

The primary outcome was mean change from Baseline in clinic-visit trough FEV1 at Week 12. The endpoint description specifies electronic spirometry, with the highest of 3 technically acceptable measurements recorded. Baseline was the pre-dose value obtained at Visit 3, and change was defined as the Week 12 value minus the Baseline value. The registry describes an ANCOVA model with Baseline trough FEV1, region, sex, age, and treatment group as covariates.

The primary endpoint population is described as randomized participants who received at least one dose, with only those who had non-missing covariates and post-Baseline FEV1 data included in the analysis. Missing data were handled using last observation carried forward, as described in the endpoint record. Further details about the analysis set, missing-data assumptions, or the original design calculations 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: Participants meeting eligibility criteria at the Screening visit completed a 4-week Run-in Period for Baseline safety evaluations and measures of asthma status. Participants were then randomized to a 12-week Treatment Period. 1110 participants were screened, 610 were randomized, and 609 received \>=1 dose of study treatment.

Overall Study

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 one dose of the study medication. Only those participants with non-missing covariates and post-Baseline FEV1 data were analyzed.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Mean Change From Baseline in Clinic Visit Trough (Pre-bronchodilator and Pre-dose) Forced Expiratory Volume in One Second (FEV1) at Week 12, measured over Baseline and Week 12.

The primary endpoint was mean change from Baseline in clinic-visit trough FEV1 at Week 12, measured in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. It is a continuous measure of pulmonary function, so the reported treatment values represent adjusted group means rather than counts of participants with a particular outcome.

“Trough” refers to the clinic-visit FEV1 measurement taken before bronchodilator and before the next study dose, while participants were still on treatment. The registry says measurements were made electronically by spirometry in the evening at Baseline through Week 12 clinic visits, and that the highest of 3 technically acceptable measurements was retained. Baseline was the pre-dose value from Visit 3; change from Baseline was calculated as the Week 12 value minus that Baseline value.

Using change from Baseline places the comparison on a common reference point: it describes how the measured lung-function value changed during the treatment period, rather than only comparing the Week 12 values. The registry’s ANCOVA model also included Baseline trough FEV1 and specified region, sex, age, and treatment group as covariates. This adjustment is intended, in general, to account for specified baseline and participant characteristics when estimating group differences. It does not turn the endpoint into a measure of symptoms, rescue-medication use, or quality of life; those appear as separate outcomes. The endpoint is a group-level statistical measure and does not directly describe the outcome for every participant.

7. Results Posted in the Registry

• FF 100 µg OD: mean 0.33 versus 0.20 on control; difference 0.14 (95% CI 0.05 to 0.22), standardized effect d = 0.32; z-test p = 0.002.
• FF/VI 100/25 µg OD: mean 0.37 versus 0.20 on control; difference 0.17 (95% CI 0.09 to 0.26), standardized effect d = 0.40; 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.

Mean Change From Baseline in the Percentage of Rescue-free 24-hour (hr) Periods During the 12-week Treatment Period

• 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 26.50 versus 17.80 on control; difference 8.70 (95% CI 2.45 to 14.95), standardized effect d = 0.27; z-test p = 0.006.
  • FF/VI 100/25 µg OD: mean 37.10 versus 17.80 on control; difference 19.30 (95% CI 13.04 to 25.56), standardized effect d = 0.60; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF 100 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF/VI 100/25 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Percentage of Symptom-free 24-hour (hr) Periods During the 12-week Treatment Period

• 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 20.40 versus 14.60 on control; difference 5.80 (95% CI -0.13 to 11.73), standardized effect d = 0.19; z-test p = 0.055.
  • FF/VI 100/25 µg OD: mean 32.50 versus 14.60 on control; difference 17.90 (95% CI 11.95 to 23.85), standardized effect d = 0.59; 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 FF/VI 100/25 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Number of Participants Who Withdrew Due to Lack of Efficacy During the 12-week Treatment Period

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • FF 100 µg OD: 2.9% (6/205) versus 15.8% (32/203) on control; risk difference -12.8 percentage points (95% CI -18.4 to -7.3), risk ratio 0.19 (0.08–0.43); unadjusted two-proportion z-test p = <0.001.
  • FF/VI 100/25 µg OD: 3.5% (7/201) versus 15.8% (32/203) on control; risk difference -12.3 percentage points (95% CI -17.9 to -6.7), risk ratio 0.22 (0.10–0.49); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for FF 100 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for FF/VI 100/25 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results cover rescue-free periods, symptom-free periods, and withdrawal due to lack of efficacy. Across these outcomes, the overall pattern is that both active-treatment arms have estimates in a more favorable direction than placebo for the listed measures, although the strength and precision of comparisons vary. The registry also lists quality of life and serial post-dose FEV1 outcomes among the secondary outcomes, but numerical results for those outcomes are not reported in the registry record.

At a broad level, the secondary pattern is compatible with the primary endpoint’s reported comparisons against placebo: the reported lung-function estimates and several secondary estimates favor active treatment in their direction. These endpoints measure different aspects of the trial, however. FEV1 is a spirometry measure; rescue-free and symptom-free periods concern daily experience, while withdrawal for lack of efficacy is a participant count. Agreement in direction does not make the outcomes interchangeable or establish that a change in one caused a change in another.

Unadjusted secondary comparisons carry less weight than a primary analysis designated in advance because multiple outcomes and contrasts create more opportunities for chance findings. In general, multiplicity procedures can control the overall false-positive risk when many hypotheses are tested, but the registry record does not report whether such a procedure was used. The unadjusted results are therefore best viewed as supportive or exploratory evidence, not as a set of independent confirmations. The record also does not report a complete analysis plan establishing the order in which secondary hypotheses were tested.

Only outcomes with posted numerical estimates can be evaluated quantitatively. For the other listed secondary outcomes, the registry record does not report numerical results. That absence limits any overall assessment of the full secondary-outcome pattern and should not be filled by assuming that unreported results were positive, negative, or similar to the posted outcomes.

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

• Mean Change From Baseline in the Percentage of Rescue-free 24-hour (hr) Periods During the 12-week Treatment Period
• Change From Baseline in the Percentage of Symptom-free 24-hour (hr) Periods During the 12-week Treatment Period
• Change From Baseline in the Total Asthma Quality of Life Questionnaire (AQLQ) (+12) Score at Week 12/Early Withdrawal
• Number of Participants Who Withdrew Due to Lack of Efficacy During the 12-week Treatment Period
• Serial FEV1 Over 0-1 Hour Post-dose at Randomization

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant has a measured change in FEV1, expressed in liters, and the trial reports group-level estimates of mean change. A mean provides a summary of the central value across analyzed participants. It does not show how each participant’s value was distributed, and it can conceal variation in individual responses. The arm estimates are least-squares means, which are model-based adjusted means rather than simple arithmetic averages.

What does ANCOVA do?

The registry says the primary analysis used analysis of covariance (ANCOVA), including Baseline trough FEV1, region, sex, age, and treatment group as covariates. In general, ANCOVA estimates treatment-group differences while adjusting for the covariates specified in the model. Including Baseline measurement can account statistically for variation in starting values. The adjusted estimate is conditional on the model and analysis population; it is not the same calculation as subtracting two unadjusted arm means. The registry record does not report further model details, such as diagnostics or the precise coding of covariates.

The registry labels the primary endpoint as a least-squares mean with standard error. A standard error describes the estimated uncertainty of a group estimate, rather than the spread of individual participants’ measurements. In general, smaller standard errors indicate more precise estimates, though they do not measure whether an effect is clinically important. The arm-level standard errors are 0.031 for placebo, 0.030 for FF 100 µg OD, and 0.030 for FF/VI 100/25 µg OD.

How should the recalculations be read?

The recalculated comparisons are simple, unadjusted comparisons derived from the posted summary statistics. They estimate mean differences and confidence intervals for each active arm versus placebo. The recalculations use an approximate pooled standard deviation derived from the arm standard errors; that approximation is not the same as re-running the trial’s ANCOVA on participant-level data. For that reason, the recalculated results are a check on the reported summaries, not a replacement for the registry’s own analysis. The record flags a discrepancy, and the sponsor’s analysis takes precedence.

A confidence interval gives a range of values reasonably compatible with the data under the analysis assumptions. It reflects sampling uncertainty, not a range containing a specified proportion of individual participants. A p-value measures how surprising data at least as extreme would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, nor does it describe clinical importance. These general interpretations apply to both adjusted and unadjusted analyses, but their estimates and uncertainty can differ because their methods differ.

What does the analysis population imply?

The endpoint record defines the Intent-to-Treat population as all randomized participants who received at least one dose of study medication. It then states that only participants with non-missing covariates and post-Baseline FEV1 data were analyzed. Thus, the analysis description does not mean that every randomized participant necessarily contributed to the primary endpoint estimate. The registry record does not report the number excluded from this endpoint analysis or the reasons for missing covariates or FEV1 data.

For missing primary endpoint data, the registry describes last observation carried forward (LOCF): the last non-missing post-Baseline on-treatment measurement at a scheduled clinic visit was used to impute a missing measurement. In general, imputation fills in a value under an assumption about what an unobserved measurement would be. LOCF assumes that carrying forward the last observed value is an acceptable representation of the missing value. That assumption may not hold in every clinical course, and the method does not remove uncertainty about missing outcomes. The provided endpoint description is truncated after the LOCF explanation, so additional details about the method are not reported in the registry record.

Why can over-dispersion matter?

Over-dispersion is a general concern for count or binary outcomes when observed variability exceeds what a simple model assumes. It can make standard errors and confidence intervals too small if the model does not account for the extra variability. The primary FEV1 endpoint is continuous, and the posted primary analysis description is ANCOVA; the registry record does not report an over-dispersion adjustment for this endpoint. This general concept is more relevant to outcomes modeled as counts or event rates and should not be assumed to have been part of this trial’s primary analysis.

Finally, several outcomes and comparisons are reported. In general, evaluating many hypotheses can increase the chance of at least one apparently unusual result, so interpretation depends on whether and how multiplicity was planned for. The registry record does not report a multiplicity adjustment or enough detail to reconstruct the full prespecified testing sequence. The posted p-values should therefore be understood in the context of the individual analyses reported, rather than as proof that all trial-wide statistical uncertainty has been addressed.

11. Confidence Intervals and Precision

The sponsor-reported 95% confidence interval for FF 100 µg OD versus placebo extends from 0.051 to 0.222 liters. For FF/VI 100/25 µg OD versus placebo, it extends from 0.087 to 0.258 liters. Both reported intervals lie above zero, indicating that the reported ANCOVA estimates are compatible with positive differences under that analysis. The direct comparison between the active arms has a 95% confidence interval from -0.048 to 0.120 liters, which includes zero. The registry reports p = 0.405 for that direct comparison.

In general, a confidence interval expresses the precision of an estimate by showing a range of values compatible with the data and the analysis assumptions. A narrower interval indicates greater statistical precision than a wider interval, but precision alone does not determine whether a difference matters clinically. The FEV1 endpoint is measured in liters, so the interval limits describe uncertainty in the group difference on that scale. The intervals are not predictions of the range of responses among individual participants.

The recalculated, unadjusted intervals are 0.051 to 0.221 liters for FF 100 µg OD versus placebo and 0.087 to 0.257 liters for FF/VI 100/25 µg OD versus placebo. They are close to, but not identical with, the sponsor-reported intervals. The recalculations use summary statistics and an approximate standard deviation; the registry’s reported estimates come from ANCOVA. Since the registry record flags a discrepancy, the sponsor’s own analysis takes precedence.

Intervals and p-values should be read together with the analysis population, the imputation method, and the number of outcomes considered. The registry record does not report a prespecified threshold for a clinically important FEV1 difference, so statistical precision alone cannot determine clinical importance. It also does not report whether interval estimates were adjusted for multiple comparisons.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect in the posted results, not the trial’s original design calculations. For these continuous and binary outcomes, the figures are participants per arm. The 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 set at the stated fraction of the observed effect. The original trial’s sample-size assumptions and justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions were true. The 90% power column makes the same kind of planning estimate for a 90% chance of detecting the specified effect. These are design-planning quantities, not guarantees about what a future study would find.

Each planning scenario uses a fraction of the observed effect: the full observed effect, 75% of the observed effect, or 50% of the observed effect. Smaller effects are harder to distinguish from random variation at a fixed level of precision, so the planning illustration calls for more participants per arm when the target effect is smaller. This relationship is general; the specific figures depend on the observed estimates and the listed assumptions.

These figures are not observed power. Observed power is not a useful substitute for reading the effect estimate and its confidence interval; the planning counts instead illustrate how assumed effect size relates to a future study’s planned enrollment. They should not be read as evidence that the current trial was adequately or inadequately designed, because the registry record does not report the original design justification.

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 = 0.136; pooled standard deviation σ = 0.430.
2. n = 2 × (1.96 + 0.842)² × 0.430² / 0.136² = 157.3, rounded up to 158 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 <- 0.136                      # observed difference in means
sigma <- 0.430469959922802                     # 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(1165138)
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 = 158 (80% power), 211 (90% power)
 75% of observed effect: n per arm = 280 (80% power), 375 (90% power)
 50% of observed effect: n per arm = 630 (80% power), 843 (90% power)
power.t.test: 158.2 
Simulated power at n = 158 per arm: 0.802 (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 reports the sponsor’s primary endpoint analyses using ANCOVA. The reported treatment differences versus placebo are 0.136 liters for FF 100 µg OD and 0.172 liters for FF/VI 100/25 µg OD. Their respective 95% confidence intervals are 0.051 to 0.222 and 0.087 to 0.258, with p = 0.002 and p < 0.001. The direct comparison between the active arms is 0.036 liters, with a 95% confidence interval from -0.048 to 0.120 and p = 0.405.

The recalculated comparisons use posted arm-level summary statistics and are unadjusted. They produce estimates close to the sponsor-reported values, but the confidence intervals differ slightly. The sponsor-reported analysis is the analysis to prioritize because it is the trial’s own ANCOVA result. The recalculations cannot reproduce every feature of that model or use the participant-level data.

The registry record flags a discrepancy between the reported analysis and the recalculation. In that circumstance, the sponsor’s own analysis takes precedence; the recalculation is best treated as a transparent, approximate check. The record labels the reported parameter “Median Difference (Final Values)” even though the primary outcome is described as a least-squares mean change. The registry record does not explain this labeling, so it should not be silently resolved by assuming a different estimator. Further clarification of the reported parameter is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint, multiple secondary outcomes, and several treatment contrasts. In general, when many hypotheses are tested, the chance of at least one small p-value can increase even if no underlying effect exists. A prespecified testing hierarchy or multiplicity adjustment can address that issue, but the registry record does not report whether either was used. The reported p-values therefore describe their individual comparisons and should not be interpreted as multiplicity-adjusted unless the record says so.

The primary endpoint analysis description identifies an ANCOVA model and its covariates, along with an LOCF approach to missing measurements. The registry record does not report the original statistical analysis plan, the original sample-size justification, interim analyses, or further details of the imputation procedure. The endpoint description says the last non-missing post-Baseline on-treatment measurement at scheduled clinic visits was used for a missing value. The assumption that this carried-forward value adequately represents an unobserved Week 12 value cannot be verified from the summary results alone.

The analysis population is described as randomized participants who received at least one dose, but only those with non-missing covariates and post-Baseline FEV1 data were analyzed. This distinction matters: an intention-to-treat label does not by itself show that every randomized participant contributed to the reported endpoint estimate. The number with missing primary data, the reasons for missingness, and the analysis exclusions are not reported in the registry record.

In general, missing-data methods rely on assumptions about why values are missing and what those values might have been. LOCF is one method, but a single imputed value does not capture all uncertainty about an unobserved outcome. The registry record does not report sensitivity analyses using alternative missing-data assumptions. Consequently, the robustness of the primary result to different assumptions about missing measurements cannot be assessed from the posted record.

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: pancreatitis (0.5%).

For serious adverse events, the registry lists 0 participants affected in the placebo group, 1 in the FF 100 µg OD group, and 0 in the FF/VI 100/25 µg OD group. The corresponding numbers at risk are 203, 205, and 201. These are descriptive counts within the registry’s listed groups. They do not establish that a treatment caused or prevented an event, and small counts cannot characterize uncommon harms precisely.

The registry identifies pancreatitis as a top serious-event term at 0.5%. It does not provide enough detail in this record to interpret that term as an arm-specific comparison. Death counts are null for the listed groups; deaths are therefore not reported in the registry record. The groups at risk for safety outcomes are not identical to the primary endpoint analysis counts, so the two sets of figures should not be treated as the same analysis population.

Serious adverse event counts are only one part of safety assessment. They do not convey timing, duration, severity beyond the serious classification, or a causal assessment. The registry record’s other adverse-event counts are separate from the serious-event counts and should not be combined with them. Safety interpretation also requires context about exposure and follow-up, which is not fully detailed in the posted results. These figures alone cannot establish overall safety or rule out uncommon events.

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

The reported primary endpoint analyses show positive adjusted mean differences in Week 12 change in trough FEV1 for each active-treatment arm compared with placebo. The sponsor-reported confidence intervals for those comparisons are above zero, and their reported p-values are below 0.05. The reported direct comparison between the two active arms has a confidence interval that includes zero and p = 0.405. Those are statements about the analyses and outcomes in the registry record, not guarantees about an individual participant’s response.

The endpoint is a spirometry measure in liters. It does not by itself describe symptoms, daily functioning, quality of life, rescue medication use, or every dimension of asthma control. The secondary outcomes address some other aspects, but their interpretation is limited by the absence of a reported multiplicity plan and by numerical results not being available for every listed outcome. The record also does not report a threshold for a clinically important FEV1 difference, so statistical evidence should not be equated with clinical importance.

The trial’s results apply to the study population, treatment regimens, and 12-week period described in the registry. They do not establish what would occur with different populations, doses, or durations. The registry describes adults and adolescents 12 years of age and older with persistent asthma, but the result summaries do not provide detailed subgroup estimates. Any subgroup-specific interpretation would therefore go beyond the posted results.

The analyses also depend on the specified model, the endpoint population, and the LOCF method for missing measurements. The record does not report the original design assumptions, multiplicity handling, or sensitivity analyses that would help assess these issues. The numerical results are informative about the posted comparisons, but the record does not support broader conclusions about all possible outcomes or all sources of uncertainty.

18. Why This Trial Matters Statistically

This trial illustrates why the treatment contrast, endpoint, and analysis method all matter when reading a clinical result. The primary measure is a change in a continuous lung-function outcome, and the registry reports adjusted ANCOVA estimates alongside arm-level summaries. A treatment difference is not simply a count of participants who improved; it is a model-based estimate on the FEV1 scale, with uncertainty represented by a confidence interval.

It also demonstrates the distinction between the sponsor’s own analysis and a summary-statistic recalculation. The recalculated comparisons are close to the reported estimates, but they are unadjusted and rely on an approximate standard deviation. The registry flags a discrepancy, which is a reason to prioritize the sponsor-reported ANCOVA rather than treat the recalculation as an independent replication. This distinction is especially important when a record uses different labels for the reported parameter and the endpoint description.

The secondary outcomes show why a clinical trial cannot be reduced to one p-value. Measures of lung function, symptoms, rescue-free periods, and withdrawal address different questions. Multiple outcomes also raise multiplicity concerns, and the registry record does not state whether those concerns were handled in the analysis plan. Results are more useful when read alongside their confidence intervals, analysis population, missing-data approach, and the scope of the outcomes actually reported.

Finally, the sample-size illustrations make explicit that planning depends on the effect a future study aims to detect. Smaller assumed effects require more participants per arm under the stated planning assumptions. Those illustrations do not reveal the trial’s original design rationale. Keeping those two uses of sample-size calculations separate helps prevent a retrospective planning exercise from being mistaken for evidence about the trial’s design or success.

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 does not report the original sample-size justification, so the posted planning illustrations cannot establish whether the enrolled sample was chosen to detect a particular effect. It also does not report a full statistical analysis plan, interim analyses, or a multiplicity procedure. Those omissions limit assessment of whether the reported comparisons followed a prespecified testing strategy.

The primary endpoint analysis used LOCF for missing measurements, according to the registry description. The number of missing FEV1 values, reasons for missingness, and sensitivity analyses under alternative assumptions are not reported in the registry record. Because the endpoint analysis also required non-missing covariates and post-Baseline FEV1 data, the record does not show how many randomized participants contributed to that estimate or how exclusions may have affected it.

The sponsor-reported analysis labels its parameter “Median Difference (Final Values),” while the primary endpoint description identifies least-squares mean change. The registry record does not explain this difference in terminology. The recalculations are based on posted summaries rather than participant-level data and use an approximate pooled standard deviation; they cannot resolve the ambiguity or reproduce the sponsor’s full ANCOVA.

Numerical results are not reported for all outcomes listed in the registry. The record also does not report a clinically important difference threshold for FEV1 or detailed subgroup results. Safety summaries include small serious-event counts, and death counts are not reported in the registry record. These limitations mean that the posted record supports interpretation of its specified comparisons, but not a complete evaluation of every outcome, missing-data scenario, or safety question.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study HZA106827: Efficacy/Safety Study of Fluticasone Furoate/Vilanterol (GW642444) in Adult and Adolescent Asthmatics — NCT01165138.
• Registry record last updated 2018-02-14; status last verified 2018-01.
• 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 asthma study with 612 participants enrolled. Participants received once-daily fluticasone furoate/vilanterol, fluticasone furoate, or placebo inhalation powder for 12 weeks.

The primary endpoint was change from Baseline in clinic-visit trough FEV1 at Week 12. The sponsor-reported ANCOVA comparisons versus placebo had positive estimates and confidence intervals above zero; the direct comparison between active arms had a confidence interval that included zero. Recalculated unadjusted estimates are similar but not identical, and the registry flags a discrepancy. The sponsor’s own analysis takes precedence.

The registry describes an LOCF approach for missing primary measurements and an analysis population requiring non-missing covariates and post-Baseline FEV1 data. The original sample-size justification, multiplicity handling, and several other analysis details are not reported in the registry record. Secondary and safety results should be interpreted within those limits.