A 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 Study to Evaluate the Efficacy and Safety of Fluticasone Furoate (FF)/GW642444 Inhalation Powder in Subjects With Chronic Obstructive Pulmonary Disease (COPD) (NCT01009463), a randomized phase 3 study. The primary outcome is Annual Rate of Moderate and Severe COPD Exacerbations Expressed as Least Square Mean.

2. Clinical Question

The clinical question concerns exacerbation frequency over follow-up, rather than simply whether a participant ever experienced an exacerbation. The registry defines moderate and severe events according to the treatment or care required: moderate events required oral corticosteroids and/or antibiotics, while severe events required inpatient hospitalization. It also describes symptom-based criteria for identifying an exacerbation. Those definitions make the endpoint a measure of clinically categorized worsening over time, rather than an unrestricted count of respiratory symptoms.

3. Trial Design

This was a randomized, double-blind, parallel-group phase 3 study sponsored by GlaxoSmithKline. The registry lists enrollment of 1626 participants and describes four treatment groups: GW642444 25 µg once daily, and fluticasone furoate/GW642444 at 50/25 µg, 100/25 µg, or 200/25 µg once daily. The record labels the combination as an inhaled corticosteroid/long-acting beta agonist and the comparator as a long-acting beta agonist. The groups were followed for the primary outcome during the double-blind study medication period.

The primary endpoint timeframe is described as from the start of double-blind study medication until Visit 11 (Week 52) or early withdrawal. The study title also describes a 52-week efficacy and safety comparison. The registry lists the study as completed. Start and primary completion dates are recorded, but they are not needed to interpret the outcome estimates.

The endpoint analysis population is described as the Intent-to-Treat population, defined in the record as all randomized participants who received at least one dose of study drug and had available data for analysis. This definition does not establish that every randomized participant contributed data to every endpoint; the available endpoint denominators differ. For the primary outcome, the reported group denominators were 409 for GW642444, 408 for FF/VI 50/25 µg, 403 for FF/VI 100/25 µg, and 402 for FF/VI 200/25 µg.

The record identifies randomization, double masking, and a parallel design. Further details about how randomization was generated or concealed, the practical masking procedures, or the original design assumptions are not reported in the registry record. The record also does not state how many participants were assigned to each group before analysis or explain why the endpoint-specific analysis denominators differ.

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 (V) 1, eligible participants (par.) entered a 4-week, open-label Run-In Period (RIP) to establish a stable Baseline. At V 2, eligible par. were randomized to a 52 week, double-blind Treatment Period. 2631 par. were screened, 2071 par. entered the RIP, and 1626 par. were randomized, out of which 1622 received at \>= 1 study treatment dose.

4-week, Open-label Run-In Period

Reasons for not completing this period:

52-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 par. randomized who received at least 1 dose of study drug and with available data for analysis. Analysis used a negative binomial regression model with covariates of trt, smoking status at Screening, Baseline pre-dose Day 1 % predicted FEV1 and region and with logarithm of time on trt as an offset variable.

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 Annual Rate of Moderate and Severe COPD Exacerbations Expressed as Least Square Mean, measured over From the start of the double blinded study medication until Visit 11 (Week 52)/Early Withdrawal.

The primary endpoint is the annual rate of moderate and severe COPD exacerbations, expressed as a least-squares mean in exacerbations per participant per year. The record defines an exacerbation through worsening of specified major or minor symptoms for at least two consecutive days. An investigator categorized events as mild, moderate, or severe. Moderate events required treatment with oral corticosteroids and/or antibiotics; severe events required inpatient hospitalization. The primary measure combines the moderate and severe categories.

A rate endpoint describes the frequency of events relative to participants’ time under observation. It is therefore suited to a question about how often exacerbations occurred during a treatment period, rather than only whether an exacerbation occurred at least once. Annualizing the rate expresses frequency on a common time scale, while the least-squares mean represents a model-based estimate rather than a simple raw count divided by participants.

The record says the primary analysis used negative binomial regression, with treatment, smoking status at screening, baseline pre-dose Day 1 percent predicted FEV1, and region among the listed covariates. The description ends before fully specifying the model. The rate outcome is relevant to the study question because repeated events can contribute information about exacerbation burden. However, it does not, by itself, describe event severity within each category, the timing of every event, or a participant’s overall experience of COPD.

7. Results Posted in the Registry

• FF/VI 50/25 µg QD: 0.92 versus 1.05 (Exacerbations per participant per year) on control; rate ratio 0.88 (95% CI 0.72–1.07, derived from the posted confidence limits); p ≈ 0.187.
• FF/VI 100/25 µg QD: 0.70 versus 1.05 (Exacerbations per participant per year) on control; rate ratio 0.67 (95% CI 0.54–0.82, derived from the posted confidence limits); p ≈ <0.001.
• FF/VI 200/25 µg QD: 0.90 versus 1.05 (Exacerbations per participant per year) on control; rate ratio 0.86 (95% CI 0.70–1.05, derived from the posted confidence limits); p ≈ 0.128.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Time to First Occurrence of Moderate or Severe COPD Exacerbation

• 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/VI 50/25 µg QD: 46.6% (190/408) versus 49.4% (202/409) on control; risk difference -2.8 percentage points (95% CI -9.7 to 4.0), risk ratio 0.94 (0.82–1.09); unadjusted two-proportion z-test p = 0.420.
  • FF/VI 100/25 µg QD: 39.7% (160/403) versus 49.4% (202/409) on control; risk difference -9.7 percentage points (95% CI -16.5 to -2.9), risk ratio 0.80 (0.69–0.94); unadjusted two-proportion z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FF/VI 50/25 µg QD 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 proportion with the event is statistically lower for FF/VI 100/25 µg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Annual Rate of Exacerbations Requiring Systemic/Oral Corticosteroids Expressed as Least Square Mean

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • FF/VI 50/25 µg QD: 0.71 versus 0.84 (Exacerbations per participant per year) on control; rate ratio 0.85 (95% CI 0.68–1.06, derived from the posted confidence limits); p ≈ 0.141.
  • FF/VI 100/25 µg QD: 0.52 versus 0.84 (Exacerbations per participant per year) on control; rate ratio 0.62 (95% CI 0.49–0.78, derived from the posted confidence limits); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference (a ratio of 1), so these data do not show a statistically significant difference between FF/VI 50/25 µg QD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for FF/VI 100/25 µg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Trough FEV1 at Week 52 (Visit 11)

• 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 50/25 µg QD: mean 0.00 versus -0.04 on control; difference 0.04 (95% CI 0.01 to 0.07), standardized effect d = 0.20; z-test p = 0.012.
  • FF/VI 100/25 µg QD: mean 0.02 versus -0.04 on control; difference 0.06 (95% CI 0.03 to 0.09), standardized effect d = 0.30; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF/VI 50/25 µg QD 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 QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes cover complementary aspects of exacerbation experience and lung function. They include time to the first moderate or severe exacerbation, annual rates of exacerbations requiring systemic/oral corticosteroids, and change from baseline in trough FEV1. The first is a time-to-event measure, the second is a recurrent-event rate with a narrower treatment-related event definition, and the third is a continuous lung-function measure. These outcomes are related to the primary endpoint but answer different questions.

Across the posted secondary analyses, the 100/25 µg group has comparisons with the comparator that are reported as statistically distinguishable for the time-to-first outcome and corticosteroid-requiring event rate, and the reported FEV1 comparison also has a p-value below 0.001. The registry lists fewer sponsor-reported comparisons than there are possible treatment-group contrasts for some secondary outcomes. It does not give a complete set of sponsor analyses for each outcome and dose. The broad pattern is compatible with the primary result in that the 100/25 µg group is the dose with the clearest reported contrast against the comparator, but secondary endpoints should not be treated as independent confirmation of the primary finding.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for chance findings. The registry record does not report whether a multiplicity adjustment or a hierarchy of confirmatory endpoints was used. Secondary outcomes can help describe consistency, differences in endpoint definition, and additional dimensions of the trial, but they do not erase uncertainty in the primary analysis. Their interpretation also depends on analysis populations, missing data, and model choices, which are not fully documented in the registry record.

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

• Time to First Occurrence of Moderate or Severe COPD Exacerbation
• Annual Rate of Exacerbations Requiring Systemic/Oral Corticosteroids Expressed as Least Square Mean
• Change From Baseline in Trough FEV1 at Week 52 (Visit 11)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a count rate: exacerbations can recur, and the reported quantity is an estimated annual frequency per participant. A rate differs from a binary outcome, which records whether an event occurred or did not occur, and from a time-to-event outcome, which focuses on the elapsed time until an event. The registry also reports these other endpoint types as secondary outcomes, but the primary analysis targets recurrent moderate and severe exacerbations.

Why model a rate?

General statistical explanation: count outcomes often have more variability than a simple model assuming equal mean and variance would accommodate. This extra variability is called over-dispersion. Negative binomial regression is one approach for modeling count rates when variability is greater than a basic Poisson model allows. The registry identifies negative binomial regression for the primary analysis. That model choice is consistent with analyzing an event rate, but the record does not give enough detail to reconstruct the complete fitted model or all assumptions used.

The record lists treatment, smoking status at screening, baseline pre-dose Day 1 percent predicted FEV1, and region as covariates. Including covariates can account for specified participant characteristics or study factors in a model-based comparison. It does not mean that every possible source of imbalance or confounding is controlled. The population and model description is truncated after the word “with,” so additional model details are not reported in the registry record. The record also does not state whether an exposure offset or any particular approach to missing observations was used in the primary model.

Rates, ratios, and uncertainty

The least-squares mean rates give an estimated event frequency for each group. A rate ratio compares two rates on a relative scale; a value of 1 is the null value, representing equal rates. A ratio below 1 indicates that the numerator group’s estimated rate is lower than the comparator’s, while a ratio above 1 indicates a higher estimated rate. A rate ratio does not state the absolute number of events avoided or the experience of every participant.

A confidence interval describes the range of estimates reasonably compatible with the data and the statistical model under repeated use of the method. A narrow interval indicates greater precision than a wide interval, though precision is not the same as clinical importance or freedom from bias. Whether the interval includes the null value is one element of inference, not a complete interpretation. The registry reports 95% confidence intervals for the primary arm estimates and for sponsor-reported comparisons.

The posted sponsor analyses identify a Generalized Linear Model and report risk ratios for primary comparisons. They are not identical in every detail to the simple unadjusted recalculations. The recalculated estimates use posted summary statistics and do not reproduce the sponsor’s fitted model. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence. A simple recalculation is useful as a check on the direction and approximate scale of the reported contrast, but not as a substitute for the original analysis.

Different secondary outcome methods

Time to first moderate or severe exacerbation is a time-to-event question: it considers when the first qualifying event occurs and can account for differing follow-up times through a survival model. The sponsor reports Cox regression hazard ratios for two comparisons. A hazard ratio concerns the relative event rate over follow-up under the model; it is not the same as a risk ratio or a difference in annual event rates.

The annual rate of exacerbations requiring systemic/oral corticosteroids is another recurrent-event rate. The registry reports least-squares mean rates, sponsor risk ratios, and a negative-binomial-based recalculation for the two listed comparisons. Change in trough FEV1 is a continuous outcome. It is reported as a least-squares mean change, and its comparisons use mean differences. These measures have different units and meanings, so their estimates should not be ranked or pooled as if they were the same outcome.

General statistical explanation: the estimated standard error reflects sampling uncertainty for an estimate. Larger standard errors usually correspond to less precise estimates, while confidence intervals communicate uncertainty on the outcome’s scale. For continuous outcomes, a mean difference expresses the contrast in original units. For rates and time-to-event outcomes, ratios express relative contrasts. Statistical significance alone does not indicate whether a contrast is meaningful to patients, and the registry record does not provide a threshold for clinical importance.

11. Confidence Intervals and Precision

Precision is conveyed by the width of the confidence interval as well as by the point estimate. For the primary outcome, the sponsor-reported comparison for FF/VI 100/25 µg has a risk ratio of 0.66 and a 95% confidence interval of 0.54 to 0.81. Its interval lies below the null ratio of 1. The 50/25 µg comparison has a reported risk ratio of 0.87 and interval 0.72 to 1.06, while the 200/25 µg comparison has a reported risk ratio of 0.85 and interval 0.70 to 1.04; both intervals include 1. These statements describe the reported estimates and their uncertainty, not the clinical value of any difference.

The arm-level confidence intervals also show uncertainty around each estimated annual rate. For GW642444, the interval is 0.92 to 1.21; for FF/VI 50/25 µg it is 0.8 to 1.06; for FF/VI 100/25 µg it is 0.6 to 0.81; and for FF/VI 200/25 µg it is 0.78 to 1.04. The interval for an individual arm rate is not the same as a confidence interval for the contrast between arms. A direct comparison interval is the relevant interval for assessing the relative effect.

Confidence intervals are conditional on the analysis method and assumptions. They do not account automatically for incomplete outcome data, multiplicity, model misspecification, or other possible biases. The record flags a discrepancy between recalculations and sponsor results, so the sponsor’s reported comparison intervals take precedence. The registry record does not report a prespecified threshold for a clinically important difference, and statistical precision alone cannot establish whether an estimate is large enough to matter in practice.

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 illustrations describe hypothetical future planning using the observed effect as a starting point. For the time-to-event outcome, the values are total events; for the other outcomes, the values are participants per arm. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The trial’s own original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated participants per arm, or total events for time-to-event planning, needed under those assumptions for an 80% chance of detecting the chosen effect if that effect is the true one. The 90% power column gives the corresponding planning quantity for a 90% chance. Higher target power generally requires more information under otherwise similar assumptions. Planning for 75% or 50% of the observed effect uses a smaller target contrast than planning for 100% of the observed effect, and smaller effects need more participants or events to detect reliably.

These figures are planning illustrations, not a reconstruction of the trial’s actual design and not observed power. They are based on the posted effect estimates and the stated simplified assumptions. Real study planning may depend on additional features, such as the exact endpoint model, expected follow-up, event accrual, loss to follow-up, and multiplicity strategy; those assumptions are not reported in the registry record. The illustrations should therefore be read as conditional comparisons of hypothetical sample sizes, not as claims about what the original investigators planned or about the probability that the completed study was adequately powered.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 1.0500; treatment rate λ₁ = 0.9200 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/1.0500 + 1/0.9200) / (1.00 × [ln(0.876)]²) = 919.4, rounded up to 920 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
lambda0 <- 1.05                      # control rate, events per patient-year
lambda1 <- 0.92                      # treatment rate
tt      <- 0.996550402453047                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(1009463)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 920 (80% power), 1,231 (90% power)
 75% of observed effect: n per arm = 1,607 (80% power), 2,151 (90% power)
 50% of observed effect: n per arm = 3,553 (80% power), 4,756 (90% power)
Simulated power, Poisson counts, n = 920 per arm: 0.803
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.629

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary comparisons using a Generalized Linear Model and gives risk ratios, 95% confidence intervals, and p-values. For FF/VI 50/25 µg, the sponsor reports a risk ratio of 0.87, a 95% confidence interval of 0.72 to 1.06, and p = 0.181. For FF/VI 100/25 µg, the corresponding values are 0.66, 0.54 to 0.81, and p < 0.001. For FF/VI 200/25 µg, they are 0.85, 0.70 to 1.04, and p = 0.109.

The simple recalculations use posted summary statistics and are not reproductions of the sponsor’s adjusted model. Their estimates and p-values are close in some cases but differ in others. The record marks a discrepancy, so the sponsor’s own analysis takes precedence. The recalculations can serve as an approximate check on the contrast, but they should not be used to overwrite or reinterpret the sponsor’s reported results. The registry does not provide enough detail to determine the specific source of every difference.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists a primary endpoint and several secondary outcomes, with multiple treatment comparisons. Testing many outcomes and contrasts can increase the chance that at least one result appears statistically notable by chance. A prespecified hierarchy, family-wise error procedure, or other multiplicity strategy can address that issue, but the registry record does not report whether such an approach was planned or used. The reported secondary p-values should therefore be read as unadjusted unless the registry explicitly identifies an adjustment; no such adjustment is described in the record.

The primary analysis population is described as randomized participants who received at least one dose and had available data for analysis. This is the registry’s stated definition, but it does not provide a participant flow for each outcome or explain exactly how missing measurements were handled. Endpoint group denominators are not identical across outcomes. For example, the primary rates use group denominators of 409, 408, 403, and 402, while the trough FEV1 analysis uses 291, 308, 310, and 289. The registry does not explain these differences in the record excerpt.

Missing data can affect estimates if the availability of outcomes is related to participants’ health, treatment, or likelihood of an event. General statistical explanation: an analysis that uses only available measurements may be unbiased under some conditions but can be biased under others. The registry record does not report a missing-data assumption, imputation procedure, sensitivity analysis, or a detailed account of withdrawals. It also does not report interim analyses or stopping rules. None should be inferred from the completed status or the reported endpoint results.

The primary model description names several covariates but is truncated, and the record does not fully specify the analysis plan. These omissions limit independent assessment of the model, missing-data handling, and the family of statistical tests. They do not change what the posted estimates say, but they constrain how confidently the results can be interpreted beyond the reported analyses.

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 (7.5%), pneumonia (3.0%), cellulitis (1.0%), cerebrovascular accident (0.7%), acute respiratory failure (0.7%).

The safety record lists participants with serious adverse events and participants with other adverse events in each group. Serious adverse events were reported for 60 of 409 participants receiving GW642444 25 µg, 65 of 408 receiving FF/VI 50/25 µg, 56 of 403 receiving FF/VI 100/25 µg, and 63 of 402 receiving FF/VI 200/25 µg. The corresponding counts for other adverse events were 197 of 409, 227 of 408, 221 of 403, and 225 of 402. These are counts of participants, not event rates per participant-year.

The most frequently listed serious-event terms include chronic obstructive pulmonary disease at 7.5%, pneumonia at 3.0%, cellulitis at 1.0%, cerebrovascular accident at 0.7%, acute respiratory failure at 0.7%, and renal failure acute at 0.7%. The registry does not report deaths in the record. These summaries do not establish whether an event was caused by a study treatment, and group-level counts alone do not describe event timing, duration, severity beyond the serious classification, or individual circumstances. Safety comparisons require the full context of event definitions, follow-up, and attribution, which is not fully in the registry record.

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

The results describe estimated exacerbation rates and comparisons among the four randomized groups during the treatment period. The sponsor-reported primary analysis gives the clearest statistical distinction for FF/VI 100/25 µg versus GW642444 alone; the reported confidence interval for that risk ratio lies below 1. The intervals for the 50/25 µg and 200/25 µg comparisons include 1. This is a statistical description of the posted model-based comparisons, not a clinical recommendation or a conclusion that any treatment works or does not work.

A group average cannot describe the response of every participant. Annual event rates summarize frequency across follow-up and do not show each participant’s event pattern, the severity of every episode, or how the result relates to an individual’s priorities. The registry does not state a threshold for a clinically important rate difference. It is therefore not possible to infer clinical importance from statistical significance alone.

The study also reports secondary outcomes that address time to a first event, a more specific exacerbation rate, and lung-function change. They can add context but should not be collapsed into one conclusion: event rates, hazard ratios, and mean differences use different scales and answer different questions. Unadjusted secondary comparisons have additional uncertainty when multiple outcomes and groups are examined.

Finally, interpretation is bounded by what the registry record documents. The original sample-size rationale, full statistical plan, multiplicity approach, detailed missing-data methods, and some model details are not reported. The sponsor’s analysis takes precedence over the simple recalculations because the record flags a discrepancy. These results are best understood as the reported group-level estimates and their uncertainty, with the unreported analysis details and limitations kept in view.

18. Why This Trial Matters Statistically

This trial is statistically instructive because its primary outcome is a recurrent event rate rather than a single yes-or-no event. A rate uses information about repeated exacerbations and follow-up time, while the secondary time-to-first endpoint discards later events by design. The two outcomes can therefore give complementary but not interchangeable descriptions of exacerbation experience.

The registry also makes visible the distinction between a model-based sponsor analysis and an unadjusted recalculation from summary statistics. The sponsor reports adjusted generalized linear model comparisons, while the recalculations are approximate checks based on posted summaries. Their differences illustrate why analysis details matter, particularly when the record identifies a discrepancy and the sponsor’s own results take precedence.

The study compares three combination doses with a shared comparator and reports several secondary outcomes. This creates a multiplicity question: a pattern across endpoints can be informative, but it needs to be interpreted alongside the planned testing strategy. Since that strategy is not reported, secondary findings cannot be treated as if they arose from a single isolated test.

Finally, the confidence intervals help distinguish the precision of estimates from their p-values. A point estimate alone does not show how uncertain a result is, and statistical significance is not the same as clinical importance. Considering the endpoint definition, the model, the comparison interval, the sample-size assumptions, and what remains undocumented gives a more complete statistical reading than focusing on a single result.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

Several trial-specific limitations affect interpretation. The registry’s primary model description is incomplete: it identifies negative binomial regression and lists treatment, smoking status at screening, baseline pre-dose Day 1 percent predicted FEV1, and region as covariates, but the description ends before the full model is specified. The record does not report the original sample-size justification, the complete analysis plan, or whether multiplicity was controlled across endpoints and comparisons.

The primary endpoint is based on investigator categorization of COPD exacerbations, with moderate and severe events combined. The registry provides symptom and treatment criteria, but the posted summary does not give the adjudication process or group-specific breakdowns by severity. The annual rate is a useful recurrent-event summary, but it does not expose the timing or distribution of events among participants.

Outcome denominators vary across analyses, particularly for trough FEV1, and the registry does not explain the differences or detail missing-data procedures. It does not report a missing-data sensitivity analysis. The record also contains incomplete sponsor comparisons for some secondary outcomes, so an all-dose pattern cannot be assessed consistently from the reported analyses alone.

The record flags a discrepancy between recalculations and sponsor analyses. The sponsor’s analyses take precedence, but the record does not explain the specific source of the discrepancy. Safety summaries list counts and selected serious-event terms, but do not establish causality, provide a detailed comparison model, or report deaths. These limits do not negate the reported estimates, but they restrict independent evaluation of robustness and clinical meaning.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Efficacy and Safety of Fluticasone Furoate (FF)/GW642444 Inhalation Powder in Subjects With Chronic Obstructive Pulmonary Disease (COPD) — NCT01009463.
• Registry record last updated 2017-11-09; status last verified 2017-10.
• Results first posted 2013-08-19.
• 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 record describes a completed randomized, double-blind, parallel-group phase 3 study in COPD, with enrollment of 1626. It compares GW642444 25 µg once daily with three once-daily fluticasone furoate/GW642444 doses: 50/25 µg, 100/25 µg, and 200/25 µg. The primary endpoint is the annual rate of moderate and severe COPD exacerbations during treatment, reported as least-squares means with 95% confidence intervals.

The sponsor-reported primary comparison for FF/VI 100/25 µg has a risk ratio of 0.66, a 95% confidence interval of 0.54 to 0.81, and p < 0.001; the other two sponsor-reported primary comparisons have confidence intervals that include 1. The record flags a discrepancy with simple recalculations, so the sponsor’s results take precedence. Secondary endpoints and safety summaries provide additional context, while the full multiplicity, missing-data, and original sample-size plans are not reported in the registry record.