Study to Evaluate the 24-Hour Pulmonary Function Profile of Fluticasone Furoate/Vilanterol (FF/VI) Inhalation Powder 100/25mcg Once Daily Compared With Tiotropium Bromide Inhalation Powder 18mcg Once Daily in Subjects With COPD Who Have or Are At Risk for Co-morbid Cardiovascular Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Evaluate the 24-Hour Pulmonary Function Profile of Fluticasone Furoate/Vilanterol (FF/VI) Inhalation Powder 100/25mcg Once Daily Compared With Tiotropium Bromide Inhalation Powder 18mcg Once Daily in Subjects With COPD Who Have or Are At Risk for Co-morbid Cardiovascular Disease (NCT01627327), a randomized phase 3 study. The primary outcome is Change From Baseline Trough in 24-hour Weighted Mean FEV1 on Treatment Day 84.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-masked, parallel-group study. The registry lists an enrollment of 623 participants and a completed status. The study start date is 2012-04-01, and the primary completion date is 2012-12-01. Its stated purpose was to assess the 24-hour spirometry effect of once-daily FF/VI compared with once-daily tiotropium during a 12-week treatment period in people with COPD who had or were at risk for co-morbid cardiovascular disease.

The two treatment groups were FF/VI 100/25 µg once daily and tiotropium 18 µg once daily. The official description identifies a novel dry powder inhaler for FF/VI and the HandiHaler for tiotropium. Further details about how randomization was generated, how allocation was concealed, and which parties were masked are not reported in the registry record. The original sample-size justification and the assumptions used to plan the trial are also not reported in the registry record.

The primary outcome was change from baseline in 24-hour weighted mean FEV1 on Treatment Day 84. The registry also lists time to onset on Treatment Day 1 and change from baseline in trough FEV1 at Treatment Day 84 as secondary outcomes. The posted numerical secondary results include the trough FEV1 outcome; numerical results for time to onset are not reported in the registry record.

The primary outcome description specifies an ANCOVA model, adjusted for baseline FEV1, exacerbation history and reversibility stratum, smoking status at screening, country, and treatment group. The registry record does not report additional details of the full statistical analysis plan, such as handling of multiplicity or planned interim analyses.

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 Run-in Period (RIP) to obtain baseline assessments of rescue use, COPD symptom scores and disease stability. Par. were then randomized to a 12-week Treatment Period. A total of 890 par. were screened, of whom 623 were randomized and received at least one dose of study medication.

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 who were randomized and received at least one dose of study medication. Only participants with data available at the indicated time point were assessed.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline Trough in 24-hour Weighted Mean FEV1 on Treatment Day 84, measured over Baseline and Day 84.

The primary endpoint was change from baseline in 24-hour weighted mean FEV1 on Treatment Day 84, measured in liters. FEV1 is the maximal amount of air forcefully exhaled from the lungs in one second. It is a continuous measure of pulmonary function, so the reported group results are least-squares means rather than counts of participants with a particular event.

The Day 84 weighted mean was calculated from pre-dose and post-dose FEV1 measurements collected at 5, 15, and 30 minutes and at 1, 2, 4, 6, 8, 12, 13, 14, 16, 20, and 24 hours. Baseline trough FEV1 was the mean of the assessments 30 and 5 minutes before dosing on Treatment Day 1. Change from baseline was calculated as the average of the Day 84 values minus the baseline value.

Using measurements across the day makes the endpoint a summary of pulmonary function over the stated 24-hour profile rather than a single post-dose reading. That is the general rationale for a weighted mean endpoint. The registry’s analysis adjusted for baseline FEV1 and specified clinical and study factors; the registry record does not provide further detail on the weighting procedure.

7. Results Posted in the Registry

• TIO 18 µg OD: mean 0.10 versus 0.12 on control; difference -0.02 (95% CI -0.06 to 0.02), standardized effect d = -0.11; z-test p = 0.246.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Trough FEV1 at Treatment Day 84

• 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:
  • TIO 18 µg OD: mean 0.09 versus 0.10 on control; difference -0.01 (95% CI -0.04 to 0.03), standardized effect d = -0.02; z-test p = 0.796.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between TIO 18 µg OD and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists time to onset on Treatment Day 1 and change from baseline in trough FEV1 at Treatment Day 84 as secondary outcomes. Numerical group results are posted for trough FEV1; numerical results for time to onset are not reported in the registry record. The available secondary result follows the same broad pattern as the primary comparison in that the posted unadjusted interval includes zero. This provides context but does not resolve the uncertainty in the primary analysis.

For trough FEV1, the posted group estimates are 0.098 liters for FF/VI and 0.093 liters for tiotropium. The unadjusted mean difference is -0.005 liters when expressed as tiotropium minus FF/VI, with a 95% confidence interval from -0.043 to 0.033 and p = 0.796. The planning figures associated with this outcome are highly sensitive to the small observed difference; they are illustrative calculations and not a design rationale for the trial.

Secondary outcomes can help describe whether the primary finding is accompanied by a similar pattern in related measures. They are usually less decisive when many outcomes are examined, because the chance of at least one apparently unusual result can rise as more comparisons are made. General statistical practice may address this through prespecification or multiplicity procedures. Whether such procedures were used, and how the secondary outcomes were prioritized, are not reported in the registry record. Accordingly, secondary results should be treated as supporting context rather than as independent confirmation or a substitute for the primary analysis.

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

• Time to Onset on Treatment Day 1
• Change From Baseline in Trough FEV1 at Treatment Day 84

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes the primary analysis as ANCOVA, or analysis of covariance. In general, ANCOVA estimates a treatment-group contrast while accounting for selected participant or study characteristics. The specified covariates were baseline FEV1, exacerbation history and reversibility stratum, smoking status at screening, country, and treatment group. Adjustment can improve comparability of the estimate when these factors are associated with the outcome, but it does not remove the need to examine the analysis definition, missing data, or the uncertainty around the estimate.

What does an adjusted estimate represent?

The registry reports least-squares means for each group. In general, a least-squares mean is a model-based group estimate after accounting for the covariates included in the analysis. It is not necessarily the raw arithmetic mean among participants in that group. The posted adjusted values are 0.117 liters for FF/VI and 0.095 liters for tiotropium. The reported comparison is a median difference (net) of 0.022 liters. Because the registry’s comparison is described as a median difference (net) and the group estimates are least-squares means, readers should retain the registry’s stated labels rather than infer that every displayed quantity is the same kind of summary.

What does the unadjusted recalculation add?

The recalculated comparison uses the posted group summaries to form an unadjusted mean difference. It is expressed as tiotropium minus FF/VI, yielding -0.022 liters, with a confidence interval from -0.059 to 0.015 and p = 0.246. In general, an unadjusted comparison does not account for the covariates in the ANCOVA model. It is useful as a transparent check based on the displayed summaries, but it does not replace the registry’s own adjusted analysis. The recalculation uses an approximate pooled standard deviation derived from the reported standard errors, as indicated in the posted analysis details. That approximation is another reason to distinguish it from the sponsor’s model-based result.

What do standard errors and confidence intervals describe?

A standard error describes the uncertainty in an estimated quantity under the statistical model and sampling process. It is not the spread of individual participant outcomes. The primary group estimates have standard errors of 0.013 and 0.014 liters. In general, a confidence interval gives a range of values compatible with the observed data and the method used to calculate the interval. It expresses uncertainty about an estimate; it does not guarantee that the true value lies in the interval, nor does it assign a probability to each value in the interval.

The registry’s adjusted 95% confidence interval is -0.012 to 0.055 liters. The recalculated unadjusted 95% interval is -0.059 to 0.015 liters. Both include zero. The two intervals belong to different analyses and should be interpreted separately. A p-value, likewise, is a measure of how unusual the data would be under a specified null model and its assumptions. It is not the probability that the null hypothesis is true, nor a measure of clinical importance.

Why can adjustment and summary choice matter?

ANCOVA and a simple comparison of group summaries may differ because the former adjusts for covariates and the latter does not. Differences may also reflect the exact outcome summary and the method used for the contrast. General statistical practice is to prioritize the prespecified, appropriately reported trial analysis when its plan is available, while treating simple recalculations as complementary checks. The registry record does not report enough detail to assess all aspects of the original plan, including the precise rationale for the reported median-difference summary.

Over-dispersion is a general issue when outcomes vary more than a simple model assumes: standard errors can be understated if the model fails to account for that extra variability. The primary endpoint is continuous, and the registry reports standard errors and an ANCOVA analysis. Whether diagnostics for model fit, residual behavior, or variance assumptions were conducted is not reported in the registry record. No claim about those diagnostics can therefore be made.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a treatment-group contrast. The sponsor’s reported adjusted primary comparison is 0.022 liters, with a 95% confidence interval from -0.012 to 0.055. This interval spans zero and includes both negative and positive differences. It therefore does not isolate the estimate to one side of no difference. The registry reports p = 0.201 for this analysis.

The unadjusted recalculation is -0.022 liters, with a 95% confidence interval from -0.059 to 0.015 and p = 0.246. That interval also spans zero. The estimates have opposite signs because the recalculated contrast is expressed as tiotropium minus FF/VI, while the registry reports its own adjusted median difference (net). These contrasts differ in method and summary, so sign alone should not be used to characterize them as conflicting findings.

In general, a wide confidence interval indicates that the data are compatible with a broader range of effects than a narrow interval would. A confidence interval that crosses zero does not prove there is no difference; it indicates that the analysis does not rule out zero at the stated confidence level. Whether the interval rules out effects that would matter clinically cannot be determined without a clinically important difference threshold, which is not reported in the registry record.

The primary group standard errors are 0.013 and 0.014 liters. They describe uncertainty around the group estimates, not the participant-to-participant variation in FEV1. The primary comparison’s confidence interval is the more direct summary of uncertainty about the contrast. The registry does not report confidence limits for each individual group estimate.

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 participants per arm, not total participants and not total events. The primary outcome is continuous, so the figures use participants per arm. A time-to-event planning display, if present, would instead give total events; that convention does not apply to this continuous endpoint.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects equal to the stated fraction of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding number per arm for a 90% chance. These are planning targets, not guarantees about what a future trial will find. They are not observed power: they do not measure the probability that the completed trial detected an effect after its results were known.

The rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. Smaller effects need more participants to detect, all else held constant. For example, the primary outcome planning figures rise from 1,424 participants per arm at 80% power when planning for 100% of the observed effect to 5,696 per arm when planning for 50% of the observed effect. At 90% power, the corresponding figures are 1,906 and 7,624. These calculations are illustrations derived from the observed estimate, not evidence that the trial was designed around those effects.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.022; pooled standard deviation σ = 0.210.
2. n = 2 × (1.96 + 0.842)² × 0.210² / -0.022² = 1,423.8, rounded up to 1,424 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.022                      # observed difference in means
sigma <- 0.209517793367783                     # 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(1627327)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 1,424 (80% power), 1,906 (90% power)
 75% of observed effect: n per arm = 2,532 (80% power), 3,389 (90% power)
 50% of observed effect: n per arm = 5,696 (80% power), 7,624 (90% power)
power.t.test: 1424.7 
Simulated power at n = 1,424 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 reports the sponsor’s primary comparison as an ANCOVA analysis with a median difference (net) of 0.022 liters, a 95% confidence interval from -0.012 to 0.055, and p = 0.201. It also reports adjusted least-squares means of 0.117 liters for FF/VI and 0.095 liters for tiotropium. Those are the results from the sponsor’s reported analysis.

The simple recalculation from the posted summary statistics gives an unadjusted mean difference of -0.022 liters for tiotropium minus FF/VI, with a 95% confidence interval from -0.059 to 0.015 and p = 0.246. It is a check based on summary values, not a reconstruction of the ANCOVA model. The analyses differ in adjustment and in the type and direction of the reported contrast, so their estimates are not directly interchangeable.

The registry record does not flag a discrepancy between the reported analysis and recalculation. The sponsor’s analysis remains the relevant posted model-based result; the recalculation is supplementary context. Neither analysis supports a definitive conclusion from the interval alone, and the clinical importance of the estimated range cannot be judged without a threshold that is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, time points, subgroups, or treatment comparisons are tested. In general, making many statistical tests without an appropriate plan can increase the chance of a nominally significant result occurring by chance. A study may address this by identifying a primary endpoint in advance, ordering tests hierarchically, or adjusting the significance threshold. Which approach is appropriate depends on the trial’s aims and analysis plan.

The registry identifies a primary endpoint and lists secondary outcomes, but multiplicity procedures are not reported in the registry record. It is therefore not possible to determine whether the reported p-values were adjusted for multiple testing, whether a hierarchy was prespecified, or whether secondary findings were intended to support formal claims. The registry also does not report interim analyses or stopping rules. Their presence or absence should not be inferred from the posted results.

The primary population is defined as randomized participants who received at least one dose of study medication. The registry states that only participants with data available at the indicated time point were assessed. This clarifies the stated analysis population, but additional details on missing measurements, exclusions after randomization, imputation, sensitivity analyses, or the assumptions used for incomplete data are not reported in the registry record.

Missing data can affect a comparison if the participants with observed outcomes differ systematically from those without them. General statistical assessment therefore considers how much data are missing, why they are missing, and whether conclusions change under reasonable alternative assumptions. Those details are not reported in the registry record, so the impact of missing outcome data cannot be evaluated from the posted information alone.

The registry describes the primary model and its covariates, but the complete statistical analysis plan is not reported in the registry record. The choice of covariates, outcome summary, handling of protocol deviations, and any subgroup analyses beyond the stated description cannot be assessed. These reporting gaps limit appraisal of prespecification and robustness; they do not, by themselves, show that the analysis was inappropriate.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (1.0%), urinary tract infection (0.6%), chronic obstructive pulmonary disease (0.6%), cardio-respiratory arrest (0.6%), post procedural infection (0.3%).

The registry reports 10 participants with serious adverse events in each treatment group. The serious-event risk sets are 310 for FF/VI and 313 for tiotropium. These figures describe the counts and the respective groups at risk as recorded; they do not establish that the treatments caused the events. The registry’s serious-event terms include pneumonia at 1.0%, urinary tract infection at 0.6%, chronic obstructive pulmonary disease at 0.6%, cardio-respiratory arrest at 0.6%, post procedural infection at 0.3%, and anaemia postoperative at 0.3%.

The record also reports 31 participants with other adverse events in the FF/VI group and 32 in the tiotropium group, with 310 and 313 at risk, respectively. These counts are a separate category from serious adverse events. The listed serious-event terms should not be interpreted as a complete description of every event or as a comparison of event severity between groups. Death counts are not reported in the registry record. The posted safety figures alone do not establish causation, comparative safety, or the clinical importance of an individual event.

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

The central result is an uncertain estimated difference in change in 24-hour weighted mean FEV1 at Treatment Day 84. The sponsor’s adjusted comparison has a 95% confidence interval that includes zero, and the unadjusted recalculation also has an interval that includes zero. The data therefore do not provide a precise estimate confined to one side of no difference under either reported summary.

This is not proof that the treatments have exactly the same effect. In general, absence of a statistically significant result does not demonstrate equivalence or non-inferiority. Those conclusions require appropriate prespecified margins and analyses. Such margins and a non-inferiority or equivalence objective are not reported in the registry record.

Nor does the result establish that a difference of any particular size is clinically unimportant. The registry reports the outcome in liters, but a threshold for a clinically meaningful FEV1 change is not reported in the registry record. Interpretation should therefore separate statistical uncertainty from clinical importance. The interval describes a range of values compatible with the analysis; clinical context is needed to judge which values within that range would matter.

The result concerns a defined population with COPD who had or were at risk for co-morbid cardiovascular disease, a specified inhaled treatment comparison, and the Day 84 pulmonary-function outcome. It does not by itself answer questions about other populations, longer-term outcomes, exacerbations, quality of life, or outcomes not posted in the registry. The registry lists a 12-week treatment period, so conclusions should remain tied to that study setting and follow-up.

Safety counts are descriptive registry results and should not be read as proof of causation. Likewise, the planning calculations are hypothetical sample-size illustrations based on the observed effect, not evidence about the probability that the completed trial found an effect. Taken together, the posted data support a cautious statistical description, not medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This trial is statistically informative because it combines a continuous pulmonary-function endpoint, repeated measurements across a 24-hour period, and an adjusted comparison between randomized parallel groups. The primary endpoint summarizes multiple time-specific measurements rather than relying on a single reading. The registry’s ANCOVA description also makes clear that baseline FEV1 and several other factors were included in the reported model.

The results illustrate why an estimate should be read together with its confidence interval. The adjusted estimate is positive, while the recalculated contrast is expressed in the opposite direction; both intervals include zero. Looking only at the sign or at one group estimate could give an incomplete impression. The distinction between adjusted and unadjusted analyses, and between the registry’s median-difference summary and a recalculated mean difference, is important for a fair reading.

The record also shows the limits of registry reporting. It identifies the population, treatment groups, endpoint, and model covariates, but does not report the original sample-size justification, multiplicity procedures, missing-data methods, or complete analysis plan. Those omissions constrain assessment of prespecification and robustness. The planning illustration can help readers understand how assumptions about the effect to detect influence required sample sizes, but it cannot reconstruct the trial’s own design rationale.

These features make the study a useful example of the difference between a numerical estimate, the uncertainty around it, and the claims justified by the record. Statistical interpretation requires attention to all three, as well as to the limits of the posted information.

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.

Several trial-specific limitations follow from the registry record. The original sample-size justification and design assumptions are not reported, so the planned effect size and basis for the enrollment target cannot be assessed. The planning figures linked to the observed effects are retrospective illustrations and should not be mistaken for the study’s original design calculations.

The record describes the primary analysis as ANCOVA and names its covariates, but it does not report the complete analysis plan, multiplicity procedures, interim analyses, or stopping rules. It also does not report how missing outcome measurements were handled beyond stating that only participants with data at the indicated time point were assessed. Reasons for missing data and sensitivity analyses are not reported.

The primary outcome group sizes differ from the overall enrollment, and the registry specifies that only participants with data available at the indicated time point were assessed. This means the posted primary result is not based on every randomized participant. The reason for unavailable data and its possible effect on the estimates cannot be evaluated from the registry record.

The simple recalculation uses an approximate pooled standard deviation based on the posted standard errors. It is unadjusted and does not reproduce the sponsor’s ANCOVA. The sponsor’s reported adjusted summary and the recalculation are therefore not interchangeable. The registry also does not report a clinically important difference threshold, limiting interpretation of whether the estimated range would matter clinically.

Finally, numerical results for the listed time-to-onset secondary outcome are not reported in the registry record, and the safety information is limited to the posted event counts and terms. These reporting limits restrict broader conclusions about outcomes beyond the primary pulmonary-function measure and the available safety summaries.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Evaluate the 24-Hour Pulmonary Function Profile of Fluticasone Furoate/Vilanterol (FF/VI) Inhalation Powder 100/25mcg Once Daily Compared With Tiotropium Bromide Inhalation Powder 18mcg Once Daily in Subjects With COPD Who Have or Are At Risk for Co-morbid Cardiovascular Disease — NCT01627327.
• Registry record last updated 2017-11-09; status last verified 2017-10.
• Results first posted 2013-11-01.
• 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

NCT01627327 is a completed Phase 3 randomized, double-masked, parallel-group study comparing once-daily FF/VI 100/25 µg with once-daily tiotropium 18 µg in participants with COPD who had or were at risk for co-morbid cardiovascular disease. The registry lists an enrollment of 623 and a 12-week treatment period.

The primary outcome was change from baseline in 24-hour weighted mean FEV1 on Treatment Day 84. The sponsor’s adjusted analysis reports a median difference (net) of 0.022 liters, with a 95% confidence interval from -0.012 to 0.055 and p = 0.201. A simple unadjusted recalculation gives a mean difference of -0.022 liters for tiotropium minus FF/VI, with a 95% confidence interval from -0.059 to 0.015 and p = 0.246. Both intervals include zero, and the analyses differ in method and summary.

The registry also posts trough FEV1 results and serious and other adverse-event counts. Details about the original sample-size justification, multiplicity, and missing-data methods are not reported in the registry record.