Study to Compare the Addition of Umeclidinium Bromide (UMEC) to Fluticasone Furoate (FF)/Vilanterol (VI), With Placebo Plus FF/VI in Subjects With Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Compare the Addition of Umeclidinium Bromide (UMEC) to Fluticasone Furoate (FF)/Vilanterol (VI), With Placebo Plus FF/VI in Subjects With Chronic Obstructive Pulmonary Disease (COPD) (NCT01957163), a randomized phase 3 study. The primary outcome is Change From Baseline (BL) in Trough Forced Expiratory Volume in One Second (FEV1) at Day 85.

2. Clinical Question

The study asked whether adding umeclidinium bromide (UMEC) to fluticasone furoate/vilanterol (FF/VI) was associated with a different change in lung function than continuing FF/VI with matching placebo. The comparison used two UMEC doses and a placebo add-on, with trough forced expiratory volume in one second (FEV1) at Day 85 as the primary endpoint.

This is a comparison of assigned treatment groups under the study conditions. The registry record does not report a minimum clinically important difference for FEV1, so the statistical comparisons alone do not establish how large a change would be meaningful to an individual participant.

3. Trial Design

This was a randomized, double-blind, parallel-group phase 3 trial with an enrollment of 619. The registry record marks the study completed. It describes a four-week open-label run-in during which participants received FF/VI 100/25 mcg once daily. Participants were then randomized to continue FF/VI and receive one of two UMEC doses or matching placebo during a 12-week blinded treatment period.

The three assigned regimens were FF/VI 100/25 mcg plus UMEC 62.5 mcg, FF/VI 100/25 mcg plus UMEC 125 mcg, and FF/VI 100/25 mcg plus placebo. All were administered once daily by dry powder inhaler. The registry describes eight scheduled clinic visits, from pre-screening through Day 85, and a follow-up phone contact approximately seven days after the final clinic visit. Participation from screening through follow-up was described as approximately 17 weeks.

The primary outcome was change from baseline in trough FEV1 at Day 85. The record also lists change from baseline in weighted mean FEV1 over the 0–6 hours after dosing at Day 84 as a secondary outcome. The primary endpoint population is described as randomized participants who received at least one dose of randomized medication, with available data contributing at each time point. The exact analysis population counts at each time point are reported with the outcome results.

The registry record gives the trial’s randomized, double-blind, parallel design and the model used for the primary analysis. The original protocol’s sample-size justification and other design assumptions are not reported in the registry record. The record also does not report whether interim analyses were planned or conducted.

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: A total of 619 participants (pars.), representing the enrolled particpants, were randomized to study treatment and comprised the Intent-to-Treat (ITT) Population (participants randomized to treatment who received ≥ 1 dose of randomized study medication in the treatment period).

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population: all pars. randomized to treatment who received ≥ 1 dose of randomized study medication in the Treatment Period. Number of pars. presented represent those with data available at given time point; however, all pars. in the ITT population without missing covariate information, with ≥ 1 post BL measurement are included in the analysis.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline (BL) in Trough Forced Expiratory Volume in One Second (FEV1) at Day 85, measured over Day 85.

The primary endpoint was change from baseline in trough forced expiratory volume in one second (FEV1) at Day 85, measured in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. The record defines Day 85 trough FEV1 as the mean of the measurements taken 23 and 24 hours after dosing on Day 84. Baseline was the mean of measurements taken 30 and 5 minutes before dosing on Day 1. Change from baseline is the on-treatment value minus the baseline value.

Trough measurement is intended to characterize lung function near the end of the dosing interval, rather than shortly after a dose. That makes it relevant to a comparison of once-daily treatment regimens across the dosing interval. This is a general explanation of the endpoint, not a claim that the registry specifies a particular clinical threshold.

The endpoint is continuous: values can vary across a range rather than falling into only two categories. The posted group results are least-squares means from the stated repeated-measures model, with standard errors describing their estimated sampling uncertainty. The trial compared these adjusted group means through mean differences. The registry record does not report a threshold that would identify a change as clinically important, so the numerical result should be interpreted as a measured difference in lung function rather than as a stand-alone judgment about clinical importance.

7. Results Posted in the Registry

• FF/VI 100/25 µg + UMEC 62.5 µg: mean 0.10 versus -0.02 on control; difference 0.12 (95% CI 0.09 to 0.15), standardized effect d = 0.80; z-test p = <0.001.
• FF/VI 100/25 µg + UMEC 125 µg: mean 0.11 versus -0.02 on control; difference 0.13 (95% CI 0.10 to 0.16), standardized effect d = 0.84; z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Change From Baseline in Weighted Mean (WM), 0-6 Hour FEV1 Obtained Post-dose at 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:
  • FF/VI 100/25 µg + UMEC 62.5 µg: mean 0.19 versus 0.03 on control; difference 0.15 (95% CI 0.12 to 0.19), standardized effect d = 0.90; z-test p = <0.001.
  • FF/VI 100/25 µg + UMEC 125 µg: mean 0.17 versus 0.03 on control; difference 0.14 (95% CI 0.11 to 0.18), standardized effect d = 0.83; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF/VI 100/25 µg + UMEC 62.5 µg 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 + UMEC 125 µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record lists one secondary outcome: change from baseline in weighted mean FEV1 over the 0–6 hours after dosing at Day 84. Across the reported group means, both UMEC add-on groups are above the placebo add-on group. This overall direction is consistent with the primary outcome’s direction, which concerns trough FEV1 at Day 85. The endpoints capture different parts of the dosing interval, so agreement in direction is useful context but does not make them interchangeable measures.

The secondary results add evidence about lung function measured after dosing, alongside the primary endpoint measured near the end of the dosing interval. They do not establish effects on outcomes that are not listed in the registry, such as symptoms or longer-term clinical events. Nor does a broadly similar pattern prove that the treatments have equal effects across these distinct measurements.

The registry contains secondary repeated-measures analyses and unadjusted recalculations. The reported analysis labels include group identifiers that do not fully distinguish the two listed contrasts, so the record’s labeling does not support a more detailed interpretation of those specific sponsor comparisons. The overall direction can be described from the posted group means, but precise contrast claims should rely on clearly identified analysis results.

Multiple outcome comparisons increase the chance that at least one result appears statistically notable by chance. In general, multiplicity procedures account for that issue by adjusting the testing strategy or interpretation. The registry record does not report a multiplicity adjustment for the secondary endpoint. Its p-values should therefore carry less inferential weight than the primary result and should be treated as supportive rather than definitive evidence.

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

• Change From Baseline in Weighted Mean (WM), 0-6 Hour FEV1 Obtained Post-dose at Day 84

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome was analyzed with a mixed model for repeated measures (MMRM). The registry describes the model covariates as treatment, baseline FEV1, smoking status, Day, a Day-by-baseline interaction, and a Day-by-treatment interaction, with Day treated as nominal. In this description, “nominal” means that the time points are treated as distinct occasions rather than requiring a particular linear pattern over time. This is a general explanation of the term.

What does a repeated-measures model do?

Repeated-measures data arise when the same participant contributes measurements at multiple study visits. Those observations are related: a participant’s values over time are not generally independent of one another. An MMRM models the outcome across visits and uses the available repeated observations to estimate treatment-group patterns. The model can represent changes over time and whether those patterns differ by treatment. The registry record reports the model name and covariates but does not report all implementation details, such as the covariance structure, the estimation method, or the exact handling of every type of missing observation.

The primary result is reported as a least-squares mean difference. In general, a least-squares mean is a model-adjusted mean: it reflects the fitted model and its covariates, rather than only the raw arithmetic average of observed values. The estimated difference compares the adjusted change in one assigned group with the adjusted change in the placebo add-on group. This helps distinguish the reported model result from a direct subtraction of the group means printed in the outcome summary.

Why adjust for baseline and other covariates?

Baseline FEV1 is a pre-treatment measure used in the model to account for differences in starting lung function. Smoking status is also included, as are treatment and time terms. In general, adjustment can improve the precision of group comparisons and account for modeled differences in these characteristics. It does not guarantee that all sources of bias or imbalance have been removed. The record does not provide the full protocol or a detailed rationale for each covariate.

The Day-by-baseline interaction allows the relationship between baseline FEV1 and the outcome to vary across visits. The Day-by-treatment interaction allows treatment-group differences to vary over time. This is a general interpretation of interaction terms. The registry describes these terms but does not provide enough detail to reconstruct the complete fitted model.

How should the p-values be read?

A p-value evaluates how compatible the observed data are with a specified null hypothesis under the model and its assumptions. For the reported comparisons, the null hypothesis concerns no mean difference between the treatment group and placebo group. A small p-value indicates that results at least as discrepant from that null would be uncommon if the null and model assumptions held. It is not the probability that the null is true, and it does not indicate the size or importance of the difference. The posted primary comparisons report p-values below 0.001.

The sponsor’s primary estimates are from the MMRM. The unadjusted recalculations use posted summary statistics and are a separate, simpler calculation. They do not reproduce the sponsor’s adjusted repeated-measures analysis. The recalculation estimates for the primary comparisons are 0.123 liters and 0.128 liters; the sponsor-reported estimates are 0.124 liters and 0.128 liters. Since the methods differ, small differences between estimates should not be treated as an error in the sponsor’s model.

What do standard errors and confidence intervals convey?

A standard error describes the estimated variability of an estimate across hypothetical repetitions of the study under the model. A confidence interval gives a range of values compatible with the data and analysis at a stated confidence level. In general, narrower intervals indicate greater precision, while wider intervals indicate more uncertainty. The reported primary intervals are 95% confidence intervals. Their endpoints are above zero, which is consistent with the reported positive estimated differences. A confidence interval does not address all possible biases and does not establish clinical importance.

The registry reports standard errors for the group least-squares means, while the sponsor-reported contrasts include confidence intervals and p-values. The unadjusted recalculations are labeled as such because their uncertainty estimates are reconstructed from summary information, not from the trial’s full participant-level repeated-measures data. The recalculated standard deviations are approximate, so the reconstructed intervals should not be substituted for the sponsor’s model-based inference.

What can be inferred about the analysis plan?

The registry record identifies the primary outcome, the MMRM approach, and the listed covariates. It does not report the full statistical analysis plan, the trial’s original sample-size justification, the planned multiplicity strategy, or whether interim analyses were conducted. It also does not provide all details needed to independently reproduce the model. Those absences limit what can be concluded about the complete prespecified analysis strategy.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate for UMEC 62.5 mcg versus placebo was 0.124 liters, with a 95% confidence interval from 0.093 to 0.154. For UMEC 125 mcg versus placebo, the estimate was 0.128 liters, with a 95% confidence interval from 0.098 to 0.159. These intervals describe the uncertainty around the model-based mean differences under the reported analysis.

In general, a 95% confidence interval is constructed by a procedure that would cover the target value in 95% of repeated studies if the model and procedure were appropriate. It is not a statement that there is a 95% probability that this particular interval contains the true value. Both posted primary intervals lie above zero, so the estimated differences are positive and statistically distinguishable from zero by the reported analysis. The interval widths also show that the exact size of the difference remains uncertain.

The intervals do not include uncertainty from every possible source. They are conditional on the statistical model and its assumptions, and they do not resolve concerns about missing data, outcome selection, multiplicity, or generalizability. The registry record does not report a clinically important difference threshold for FEV1. Therefore, the intervals can describe statistical precision but cannot, by themselves, determine whether the differences matter clinically.

The recalculated unadjusted comparisons have intervals based on summary statistics and approximate standard deviations. The sponsor’s reported intervals come from the MMRM and are the more direct account of the trial’s stated primary analysis. The recalculated values are useful as a check on the direction and approximate size of the posted contrasts, not as a replacement for the sponsor’s model-based results.

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 across the trial. They are illustrations based on the observed effect, not the trial’s original design calculations. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original sample-size assumptions used to design the trial are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for an analysis to have an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions are correct. The 90% power column gives the corresponding number for a 90% chance. These are planning targets, not descriptions of what happened in the completed trial.

Rows for 100% of the observed effect use the full observed difference as the assumed target. Rows for 75% and 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so the planning figures require more participants per arm as the assumed effect gets smaller. The listed figures vary by comparison and outcome; they should be read in relation to the particular effect used for each illustration.

This is not observed power. It does not measure the probability that the completed trial produced a statistically significant result, and it should not be used to reinterpret the observed p-values. The registry record does not report the trial’s own original sample-size 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 = 0.123; pooled standard deviation σ = 0.153.
2. n = 2 × (1.96 + 0.842)² × 0.153² / 0.123² = 24.4, rounded up to 25 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 <- 0.123                      # observed difference in means
sigma <- 0.153309028516076                     # 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(1957163)
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 = 25 (80% power), 33 (90% power)
 75% of observed effect: n per arm = 44 (80% power), 59 (90% power)
 50% of observed effect: n per arm = 98 (80% power), 131 (90% power)
power.t.test: 25.4 
Simulated power at n = 25 per arm: 0.792 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor-reported primary comparisons use a mixed model for repeated measures and are reported as least-squares mean differences. For UMEC 62.5 mcg versus placebo, the sponsor estimate is 0.124 liters, with a 95% confidence interval from 0.093 to 0.154. For UMEC 125 mcg versus placebo, it is 0.128 liters, with a 95% confidence interval from 0.098 to 0.159. Both reported p-values are below 0.001.

The unadjusted recalculations from the posted summary statistics estimate mean differences of 0.123 liters and 0.128 liters, respectively. These are simple comparisons reconstructed from group summaries and do not reproduce the sponsor’s repeated-measures model, its covariate adjustment, or its use of observations over time. A small difference between the recalculated and sponsor estimates can arise because the estimands and methods are not identical.

The registry record does not flag a discrepancy between the posted results and the recalculations. The sponsor’s model-based estimates are the relevant results for the reported primary analysis; the recalculations are a supplementary check based on less detailed data. The recalculated uncertainty estimates rely on approximate standard deviations and should not be treated as equivalent to the sponsor’s model-based confidence intervals.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary outcome and one secondary outcome, with multiple treatment comparisons against the placebo add-on group. The primary endpoint results include two sponsor-reported comparisons. The secondary endpoint also has analyses for treatment groups, although the registry’s reported group labels do not fully distinguish the two listed sponsor contrasts.

When several hypotheses are tested, the chance of at least one apparently positive result can increase. General approaches to multiplicity include prioritizing a primary endpoint, specifying an order for testing, or adjusting significance thresholds. The registry record does not report whether any such strategy was prespecified or applied, so the multiplicity handling cannot be established from the record. In particular, secondary p-values should not be interpreted as though the full family of comparisons had necessarily been accounted for.

The primary analysis population is described as randomized participants who received at least one dose of randomized study medication in the treatment period. The record also says that the number presented represents participants with data available at the given time point, while mentioning an analysis population without missing covariate information and with at least one observation. The endpoint description is truncated, and the registry record does not fully specify how missing outcome measurements were handled, what assumptions were made about missingness, or whether sensitivity analyses were conducted.

MMRM can use observed repeated measurements without requiring every participant to have a value at every visit, under its modeling assumptions. This general feature does not show that missingness is harmless or establish which assumptions were used in this trial. The registry record does not report the amount or pattern of missing data or analyses testing the impact of missingness.

The trial’s original sample-size justification, complete statistical analysis plan, and any interim-analysis details are not reported in the registry record. Those gaps restrict assessment of whether the reported analysis matches every prespecified decision and how the family of outcomes was intended to be interpreted.

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 (1.9%), pneumonia (1.0%), cardio-respiratory arrest (0.5%), myocardial infarction (0.5%), lung neoplasm malignant (0.5%).

The registry reports serious adverse events for the treatment groups, using 206 participants at risk in the placebo add-on group, 206 in the UMEC 62.5 mcg group, and 207 in the UMEC 125 mcg group. Serious adverse events affected 6, 2, and 7 participants, respectively. These are counts of participants with serious adverse events, not a measure of treatment effect or a complete account of all safety outcomes.

The listed serious event terms include chronic obstructive pulmonary disease at 1.9%, pneumonia at 1.0%, cardio-respiratory arrest at 0.5%, myocardial infarction at 0.5%, lung neoplasm malignant at 0.5%, and rectal cancer at 0.5%. These percentages are the registry’s reported values. The record does not provide enough context in this summary to assign causality or assess how the events compare statistically across groups.

Deaths are not reported in the registry record. Other adverse events affected 15 participants in the placebo add-on group, 26 in the UMEC 62.5 mcg group, and 26 in the UMEC 125 mcg group. Serious and other adverse-event counts should be read as descriptive counts over the reported trial period; they do not, by themselves, establish comparative safety.

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

The primary result shows that, in this randomized trial, the modeled mean change in trough FEV1 was higher in each UMEC add-on group than in the FF/VI-plus-placebo group. The sponsor-reported mean differences were 0.124 liters for UMEC 62.5 mcg and 0.128 liters for UMEC 125 mcg, with confidence intervals above zero and p-values below 0.001. These estimates describe the study’s lung-function endpoint over the stated treatment period.

The results do not establish that the two UMEC doses differ from one another. The registry reports comparisons of each dose with placebo, not a direct dose-versus-dose test. Similar-looking estimates are not proof of equivalence. The record also does not provide a clinical importance threshold, so statistical evidence of a difference cannot on its own determine whether the size of the difference is meaningful to patients.

The findings apply to the participants and treatment conditions represented in this study, including the FF/VI run-in and the 12-week blinded treatment period. The registry record does not establish what would happen in other populations, with different background treatments, or over longer follow-up. It also does not report outcomes that would support conclusions about every aspect of COPD, such as symptoms or long-term disease events.

Statistical significance is not a guarantee that every participant experiences a change in the direction of the group average. The reported estimates are group-level averages, and individual responses may vary. The analysis also depends on the repeated-measures model and its assumptions; the registry record does not provide all details needed to evaluate every assumption or missing-data sensitivity.

The safety figures are descriptive and should be considered separately from the lung-function efficacy result. The counts do not prove that an event was caused by a study treatment, and the record does not provide a complete comparative safety analysis. Overall, the posted data support a statistical difference in the primary lung-function measure versus placebo in this trial, while leaving clinical importance, broader outcomes, and other treatment comparisons unresolved.

18. Why This Trial Matters Statistically

This trial illustrates why the estimand and analysis method matter when interpreting a clinical result. Its primary outcome is a change from baseline in trough FEV1, and its sponsor analysis uses a mixed model for repeated measures rather than a simple comparison of single visit averages. That model incorporates the time course and listed covariates, so its adjusted contrast is the appropriate starting point for understanding the registry’s primary result.

It also shows the distinction between the sponsor’s model-based estimate and an unadjusted recalculation using summary statistics. The recalculations are close in scale to the sponsor estimates, but they do not replicate the model or its use of repeated measurements. That distinction is important when reviewing registry results: a transparent recalculation can provide a check, but it cannot replace access to the full analysis data and specification.

The confidence intervals provide information beyond the p-values. They give a range of plausible values for the estimated average difference under the model, while leaving clinical interpretation dependent on context and a threshold that the registry does not report. The two dose-versus-placebo findings also do not answer a direct dose comparison question.

Finally, the record exposes limits of registry-based interpretation. It identifies the primary and secondary outcomes and the primary model, but does not report the full sample-size rationale, multiplicity strategy, complete missing-data handling, or interim-analysis information. These omissions matter because they affect how confidently readers can reconstruct the planned inferential framework. The trial is therefore a useful example of reading effect estimates, uncertainty, model specification, and reporting gaps together rather than treating a p-value as a complete summary.

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 relationship between the trial’s enrollment and its planned detectable effect cannot be evaluated from this information. The planning illustrations based on observed effects are not a substitute for the design rationale.

The primary analysis description names the MMRM and lists its covariates, but does not report all model details. The covariance structure, estimation details, and complete analysis specification are not reported in the registry record. The description of the analysis population is also incomplete, and the record does not fully explain the amount, pattern, or treatment of missing outcome data.

The registry record does not report a multiplicity strategy for the primary and secondary comparisons. This is particularly relevant to interpreting multiple comparisons and the secondary endpoint. It also does not report whether interim analyses were planned or conducted, or provide a clinical importance threshold for the FEV1 outcome.

The secondary outcome analysis labels do not fully distinguish the two listed sponsor contrasts, which limits interpretation of those particular reported comparisons. The registry provides group means and recalculated contrasts, but those recalculations are based on summary statistics and approximate standard deviations rather than participant-level data. They cannot reproduce the sponsor’s repeated-measures model.

The safety summary gives counts of participants with serious and other adverse events, but deaths are not reported in the registry record. The listed event counts and terms do not establish causality or provide a complete account of comparative safety. Follow-up described in the record is limited to the trial participation period, so the posted data do not establish longer-term outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Compare the Addition of Umeclidinium Bromide (UMEC) to Fluticasone Furoate (FF)/Vilanterol (VI), With Placebo Plus FF/VI in Subjects With Chronic Obstructive Pulmonary Disease (COPD) — NCT01957163.
• Registry record last updated 2017-11-09; status last verified 2017-10.
• Results first posted 2014-11-25.
• 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

This completed randomized, double-blind, parallel-group phase 3 trial enrolled 619 participants with COPD. After a four-week open-label FF/VI 100/25 mcg run-in, participants received FF/VI with UMEC 62.5 mcg, UMEC 125 mcg, or matching placebo during a 12-week treatment period.

The primary outcome was change from baseline in trough FEV1 at Day 85. The sponsor-reported mean differences versus placebo were 0.124 liters for UMEC 62.5 mcg and 0.128 liters for UMEC 125 mcg; both reported p-values were below 0.001, and both 95% confidence intervals were above zero. A secondary outcome measured weighted mean FEV1 over 0–6 hours after dosing at Day 84.

The registry record does not report the original sample-size rationale, a multiplicity strategy, complete missing-data methods, or deaths. The results describe the posted lung-function comparisons and do not by themselves establish clinical importance or a direct difference between the two UMEC doses.