A Study to Evaluate the Effect of Umeclidinium (UMEC) as Combination Therapy 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 Effect of Umeclidinium (UMEC) as Combination Therapy in Subjects With Chronic Obstructive Pulmonary Disease (COPD) (NCT02257372), a randomized phase 4 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in One Second (FEV1) on Day 85.

2. Clinical Question

The comparison concerns the additional effect associated with assignment to UMEC within a treatment regimen that already included ICS/LABA. It is not a comparison of UMEC alone against no treatment, and the registry describes both groups as receiving background therapy. Albuterol/salbutamol was also issued for use as needed during the study.

The primary outcome is a measure of lung function rather than a direct measure of symptoms, daily functioning, or long-term disease course. The registry also lists a post-dose FEV1 outcome as secondary. These related measures help describe lung-function changes at different measurement times, but they do not by themselves answer every clinical question about the treatment regimen or its effects beyond the study period.

3. Trial Design

This was a randomized, double-blind, parallel-group Phase 4 study in participants with COPD. The registry lists an enrollment of 236 and describes equal allocation between the blinded UMEC and placebo regimens. The study was completed. Its recorded start date was 2014-09-30, and its primary completion date was 2015-03-24.

Participants assigned to the UMEC group took UMEC 62.5 mcg once daily by dry powder inhaler and continued open-label ICS/LABA medication. Participants assigned to the comparator group took blinded placebo once daily by dry powder inhaler and also continued open-label ICS/LABA medication. The treatment period was 12 weeks; the brief summary describes the total duration for each participant as approximately 14 weeks. Albuterol/salbutamol metered-dose inhaler or nebules were issued for use as needed.

The registry describes the primary analysis population as randomized participants who received at least one dose of randomized study medication. It also says that only participants with data available at a specific timepoint were analyzed. The primary endpoint is change from baseline in trough FEV1 on Day 85, measured using spirometry. The recorded analysis used a mixed model repeated measures approach.

The registry’s planned sample description is approximately 230 participants randomized, with 115 participants per treatment, to complete at least 206 evaluable participants. This is a design description, not a statement that every randomized participant contributed to every outcome analysis. For the primary endpoint, the posted group counts are 110 for placebo plus ICS/LABA and 109 for UMEC plus ICS/LABA. Reasons for the difference between enrollment, the planned evaluable count, and outcome-specific counts are not reported in the registry record.

Details such as the locations of participating centers, the original statistical analysis plan, and the original sample-size justification are not reported in the registry record. The available design description therefore supports interpretation of the randomized comparison, but not reconstruction of every operational or planning decision.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: Participants who met eligibility criteria at screening completed an approximately one week run-in period and participants who met the randomisation criteria were entered a 12-week treatment period. A total of 266 participants with chronic obstructive pulmonary disease (COPD) were screened; 236 participants randomized and entered into the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat (ITT) population: all participants randomized to treatment who received at least one dose of randomized study medication in the treatment period. Only participants with data available at specific timepoint were analyzed.

5. Baseline Characteristics

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

6. Primary Endpoint

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

The primary endpoint is change from baseline in trough forced expiratory volume in one second (FEV1) on Day 85, reported in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. The registry defines the Day 85 trough value as the mean of FEV1 measurements taken 23 and 24 hours after dosing on Day 84, at Week 12. Baseline FEV1 is the mean of measurements taken 30 and 5 minutes before dosing on Day 1. Change is defined as the Day 85 trough value minus baseline.

FEV1 is used as a quantitative measure of lung function. Measuring change from baseline expresses the outcome relative to each participant’s starting measurement, while the trough timing is intended to capture lung function near the end of the dosing interval. The registry says FEV1 was measured by spirometry. The endpoint is therefore a specific, timed physiological measure; it should not be treated as a complete measure of symptoms, quality of life, or longer-term outcomes, which are not described by this primary measure.

The reported group estimates are least-squares means from the repeated-measures analysis. Such adjusted means are model-based estimates that account for the listed covariates, rather than simple arithmetic averages of every observed change. Their comparison estimates the difference between randomized groups on this endpoint while participants in both groups received background ICS/LABA therapy.

7. Results Posted in the Registry

• Umeclidinium 62.5 mcg+ICS/LABA: mean 0.09 versus -0.03 on control; difference 0.12 (95% CI 0.07 to 0.17), standardized effect d = 0.64; 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 0-6 Hour FEV1 Obtained Post-dose on 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:
  • Umeclidinium 62.5 mcg+ICS/LABA: mean 0.18 versus 0.04 on control; difference 0.15 (95% CI 0.10 to 0.20), standardized effect d = 0.82; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Umeclidinium 62.5 mcg+ICS/LABA than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint: change from baseline in weighted mean 0-6 hour FEV1 obtained after dosing on Day 84. Its reported analysis estimates a positive mean difference favoring the UMEC group in the sense that the group estimate is higher than the placebo group estimate. The interval is reported as 0.099 to 0.197 liters, with p <0.001. The unadjusted recalculation is also positive and close to the sponsor’s reported estimate.

At the broad level, the secondary outcome’s direction is consistent with the primary outcome: both posted FEV1 comparisons show a higher model-estimated change in the UMEC plus ICS/LABA group than in the placebo plus ICS/LABA group. This consistency can add context because the outcomes measure lung function at different timing relative to dosing. The secondary measure should not, however, be treated as an independent confirmation of every aspect of the primary result; the outcomes are related and arise from the same trial.

The registry reports two outcome measures in total, including the primary outcome, and one posted secondary outcome. Whether the analysis plan adjusted for multiple comparisons, defined a hierarchy, or controlled a family-wise error rate is not reported in the registry record. Without that information, secondary p-values should be read as unadjusted evidence and given less weight than the prespecified primary analysis. Considering multiple outcomes can increase the chance of a nominally small p-value arising by chance, especially if many comparisons are made.

The secondary finding is therefore best viewed as supporting descriptive context for the primary lung-function result, not as a separate basis for broad claims. Other secondary outcomes, patient-reported measures, or longer-term endpoints are not reported in the registry record. The available secondary information does not establish whether the observed pattern extends to outcomes beyond the one listed.

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

• Change From Baseline in Weighted Mean 0-6 Hour FEV1 Obtained Post-dose on Day 84

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s outcome is a change in FEV1 measured in liters. The registry reports least-squares means and standard errors for the groups, then reports a mean difference from a mixed model repeated measures analysis. In general, a mean summarizes the central level of a continuous measure, while its standard error describes the uncertainty in estimating that mean. A standard error is not the spread of individual participant outcomes.

What does the repeated-measures model do?

The registry states that the primary analysis used a mixed model repeated measures method. In general, repeated-measures models are designed for outcomes measured at more than one timepoint and can estimate group patterns over time while accounting for the relationship among measurements from the same participant. The registry lists treatment, baseline FEV1, type of ICS/LABA, smoking status, Day, the Day-by-baseline interaction, and the Day-by-treatment interaction as covariates or model terms. Day is described as nominal. The registry does not report the full model specification, covariance structure, estimation details, or diagnostic checks, so those aspects cannot be evaluated from the record.

The reported primary comparison is the mean difference in final values from this model. The registry describes the parameter as “Mean Difference (Final Values).” Least-squares means are adjusted model estimates, not necessarily the observed arithmetic means. Adjustment can account for the listed variables when estimating the group contrast, but it does not remove uncertainty or guarantee that every possible source of bias has been addressed. How the covariates were selected and whether other prespecified analyses were planned are not reported in the registry record.

How should the interval and p-value be read?

The sponsor reports a 95% confidence interval for the primary mean difference from 0.071 to 0.174 liters. In general, a confidence interval expresses the uncertainty around an estimated effect under the assumptions of the analysis. The interval is compatible with a range of positive mean differences; it does not mean that 95% of individual participant results fall within that range. The p-value is reported as <0.001. In general, a p-value measures how unusual data at least as incompatible with a null comparison would be if that null and the statistical assumptions held. It does not measure the size or clinical importance of the effect.

The posted recalculation uses summary statistics and is explicitly unadjusted. It estimates a mean difference of 0.123 liters, with an interval from 0.072 to 0.174 liters. The recalculation’s pooled standard deviation is marked approximate. In general, an unadjusted calculation based on summary statistics need not reproduce a model that adjusts for baseline and other covariates or handles repeated measurements. It is useful as a check on the reported contrast, not as the trial’s definitive analysis.

Why can dispersion affect planning?

The group summaries report standard errors, while planning calculations use an approximate pooled standard deviation. In general, standard deviation describes how much individual outcomes vary around their mean. Standard error describes uncertainty in a group mean and depends both on variation and the number of observations. When outcomes vary more widely, a study generally needs more participants to estimate a group difference precisely or to detect a given difference. The pooled standard deviation in the recalculation is approximate, so planning figures derived from it are illustrations rather than exact reconstructions of the trial’s design.

Over-dispersion is a general concern when a statistical model assumes less variability than the data actually contain. If variability is underestimated, standard errors can be too small and intervals can be too narrow. The registry does not identify over-dispersion as a problem in this trial, and the record does not provide diagnostics that would establish whether it occurred. It should therefore be understood as a general statistical consideration, not a reported finding about this study.

What do the group counts represent?

The primary endpoint lists 110 participants in the placebo group and 109 in the UMEC group. The adverse-event at-risk counts are 117 and 119, respectively. These counts refer to different posted summaries and should not be assumed to represent the same analysis set. The registry defines the primary population as randomized participants who received at least one dose, with only participants having data at the specific timepoint analyzed. The exact reasons for outcome-specific counts and the handling of missing measurements are not reported in the registry record.

In general, the interpretation of a repeated-measures analysis depends in part on how incomplete measurements are handled and on the assumptions made about missingness. The registry identifies the model but does not state the missing-data assumptions, imputation approach, or sensitivity analyses. No conclusion about those choices should be inferred from the model label alone.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is 0.123 liters, with a 95% confidence interval from 0.071 to 0.174 liters. The interval indicates that the estimated difference is not a single exact value: under the model and its assumptions, values across the stated range are compatible with the data. The interval is entirely above zero, consistent with the reported p-value of <0.001 for the group comparison. The interval does not express the range of individual participant responses.

The registry’s unadjusted recalculation gives a 95% interval from 0.072 to 0.174 liters around the same rounded mean difference of 0.123 liters. The recalculated limits are close to the sponsor’s reported limits. They differ in their calculation basis: the sponsor’s interval comes from the repeated-measures analysis, while the recalculated interval is based on posted summary statistics. The sponsor’s model-based result is therefore the relevant primary analysis.

In general, a narrower confidence interval indicates greater precision in estimating an average effect, whereas a wider interval indicates more uncertainty. Precision is distinct from clinical importance: even a precisely estimated difference requires context to judge its practical meaning, and a clinical-importance threshold is not reported in the registry record. Likewise, an interval for a group mean difference does not show how variable the outcome was among individuals.

The secondary endpoint’s reported interval is 0.099 to 0.197 liters, but it is a separate outcome and should not be used to infer the precision of the primary endpoint. The registry does not report confidence intervals for every possible analysis or explain how uncertainty would change under alternative model specifications. As with any model-based interval, interpretation depends on the design, analysis population, and assumptions used.

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 events. They are illustrations based on the observed effect and the posted summary statistics, rather than the original trial’s sample-size justification. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each scenario, the effect to detect is set to the stated fraction of the observed effect.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the assumed effect under those planning assumptions, if the effect and model assumptions used in the calculation were true. The 90% power column gives the corresponding per-arm number for a design with a 90% chance. These are planning concepts, not observed features of the completed trial. This is not observed power.

The rows that use 100%, 75%, and 50% of the observed effect illustrate how the required sample size changes when the target effect is set smaller. Smaller effects need more participants to detect, all else equal. For example, the primary-endpoint planning figures increase across the listed effect scenarios as the assumed target becomes smaller. These figures do not show how many participants actually had outcomes, and they do not establish the trial’s original planning rationale.

Read any visual curve as a display of the relationship between the assumed effect and the illustrative participant requirement, not as a record of recruitment or trial conduct. The trial’s own original design assumptions and sample-size justification are not reported in the registry record. The planning results should therefore be treated as hypothetical design illustrations rather than evidence about the power achieved in this study.

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 = 0.192.
2. n = 2 × (1.96 + 0.842)² × 0.192² / 0.123² = 38.3, rounded up to 39 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 <- 0.19202605765957                     # 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(2257372)
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 = 39 (80% power), 52 (90% power)
 75% of observed effect: n per arm = 69 (80% power), 92 (90% power)
 50% of observed effect: n per arm = 154 (80% power), 205 (90% power)
power.t.test: 39.2 
Simulated power at n = 39 per arm: 0.794 (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’s primary analysis reports a mean difference of 0.123 liters, a 95% confidence interval from 0.071 to 0.174 liters, and p <0.001. The simple unadjusted recalculation from the posted summary statistics also gives a mean difference of 0.123 liters, with a 95% interval from 0.072 to 0.174 liters and p <0.001. The registry does not flag a discrepancy between the analyses.

The estimates are closely aligned, but they do not arise from identical methods. The sponsor used a mixed model repeated measures analysis with the covariates listed for the primary endpoint. The recalculation is an unadjusted summary-statistic calculation and its pooled standard deviation is approximate. Small differences in interval limits are consistent with these differing calculation approaches and the displayed precision of the reported values.

When a discrepancy is flagged, the sponsor’s own analysis takes precedence as the trial’s reported analysis. No such discrepancy is flagged for this result, and the sponsor’s model remains the primary result because it is the analysis reported for the trial. The recalculation serves as a secondary check on the posted summary, not as an alternative adjusted analysis or an independent replication.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and one secondary endpoint. It does not report whether the analysis plan used a hierarchy of tests, adjusted p-values for multiple outcomes, or specified a family-wise error procedure. The reported p-values should therefore be understood as presented in the registry, without assuming that multiplicity was controlled. In general, testing several outcomes can increase the chance of at least one apparently notable result under a collection of null effects. This concern is one reason secondary findings usually carry less confirmatory weight when adjustment procedures are not described.

The primary analysis population is defined as randomized participants who received at least one dose of randomized study medication. The registry further states that only participants with data available at the specific timepoint were analyzed. This definition is narrower than simply describing all enrolled participants, and it does not mean that every randomized participant contributed to every endpoint. The posted primary endpoint group counts are 110 and 109; the adverse-event counts use different at-risk totals, 117 and 119. Reasons for the differing counts are not reported in the registry record.

The registry identifies a mixed model repeated measures analysis but does not describe its missing-data assumptions, any imputation, sensitivity analyses, or how participants with incomplete records were handled in detail. In general, missing outcome data can affect estimates if the probability of missingness is related to outcomes or treatment response. A model label alone is not enough to determine whether the assumptions are appropriate or how robust the findings are to departures from them.

The registry also does not report the full statistical analysis plan, the timing of any plan finalization, or whether interim analyses were conducted. Those matters cannot be inferred from the posted endpoint results. The information available supports a description of the reported comparisons, but leaves uncertainty about multiplicity control, missing-data procedures, and the full set of analyses that may have been planned or performed.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chronic obstructive pulmonary disease (2.6%), motor neuron disease (0.9%), road traffic accident (0.9%), cerebrovascular accident (0.8%), myocardial infarction (0.8%).

The serious adverse event summaries report 5 affected participants among 117 at risk in the placebo plus ICS/LABA group and 6 among 119 at risk in the UMEC plus ICS/LABA group. These are participant counts in the posted safety summary. The registry also reports other adverse events affecting 35 participants in the placebo group and 25 in the UMEC group, with the same respective at-risk counts. The summaries should be read as descriptive counts, not as proof that a study medication caused an event or that differences between groups are attributable to treatment.

The listed serious-event terms and percentages include chronic obstructive pulmonary disease (2.6%), motor neuron disease (0.9%), and road traffic accident (0.9%), as well as cerebrovascular accident (0.8%), myocardial infarction (0.8%), and pseudomembranous colitis (0.8%). The registry does not provide enough detail in this summary to assign each listed term to a particular group or to determine causality. Death counts are not reported in the registry record.

These figures do not establish comparative safety on their own. The registry summary does not provide event-level timing, duration, severity details beyond the serious-event classification, or a causal assessment for each event. Differences in counts should not be interpreted as evidence of a treatment effect without the study’s complete safety analyses and context.

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

The primary result describes an average difference in change from baseline in trough FEV1 on Day 85 between participants assigned to UMEC plus ICS/LABA and participants assigned to placebo plus ICS/LABA. The sponsor’s estimated difference is 0.123 liters, with a 95% confidence interval from 0.071 to 0.174 liters. The reported p-value is <0.001. The estimate and interval describe the statistical result for this measured lung-function endpoint in the study population and time period.

The result does not establish what any particular participant would experience. Group averages do not indicate that all participants changed in the same way, and the registry does not report the individual outcome distribution or the proportion of participants who reached a specific degree of change. Nor does statistical evidence of a difference establish that the magnitude is clinically important. A threshold for clinical importance is not reported in the registry record.

The comparison was an add-on design: both groups received ICS/LABA background medication, and the randomized difference was UMEC versus placebo. The findings therefore do not describe UMEC used without background therapy or compare the background regimens themselves. The treatment period was 12 weeks, so the posted result does not establish longer-term effects.

The primary endpoint is a physiological measure. It does not by itself demonstrate differences in symptoms, daily functioning, quality of life, exacerbations, hospitalization, or survival. The registry lists one secondary FEV1 endpoint, but outcomes not posted in the record cannot be inferred from the primary result. Similarly, the safety counts are descriptive and do not establish causal attribution.

In general, clinical interpretation combines the estimated effect and its precision with the outcome’s practical importance, study design, population, and other relevant evidence. The registry result contributes information about a defined comparison and measurement; it is not a complete account of the benefits and risks of a treatment regimen or a basis for individual treatment decisions.

18. Why This Trial Matters Statistically

This trial is statistically useful as an example of an add-on randomized comparison. Both groups continued ICS/LABA, while assignment to UMEC or placebo created a contrast focused on the additional medication within that background-treatment setting. The double-blind, parallel-group design and reported model-based comparison provide a framework for interpreting that contrast, while the endpoint and treatment duration define its scope.

The result also illustrates why the estimate, interval, and p-value answer different questions. The mean difference describes the average contrast on the FEV1 scale; the confidence interval communicates uncertainty around that estimate; and the p-value measures compatibility with a null comparison under the analysis assumptions. None alone establishes clinical importance. In this record, the sponsor’s estimate and the simple recalculation are closely aligned, but their methods differ, making the distinction between adjusted analysis and unadjusted recalculation important.

The study further shows why analysis populations and outcome-specific counts matter. The primary endpoint counts and safety at-risk counts are not identical summaries, and the record says that only participants with data at a given timepoint were analyzed. Reporting the model name is informative, but incomplete reporting of missing-data assumptions and multiplicity procedures limits evaluation of those aspects.

Finally, the sample-size illustrations connect observed effects with planning concepts without describing the trial’s original justification or achieved power. Their assumptions are explicitly illustrative. Keeping that distinction clear helps prevent planning calculations from being mistaken for trial results. Together, these features make the record a case study in reading a model-based clinical comparison with attention to effect size, precision, population, and limits of reporting.

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 reported primary outcome is a specific lung-function measure at a defined timepoint after 12 weeks of treatment. The registry does not report a clinical-importance threshold for the change, so the statistical estimate cannot by itself establish how meaningful its magnitude is in practice. Individual response distributions are also not reported, limiting interpretation of how outcomes varied among participants.

The comparison concerns UMEC added to ICS/LABA, not UMEC alone or a comparison of different background regimens. The study description names several background ICS/LABA options, but the registry does not provide subgroup results by background medication. The results therefore do not establish whether the estimated contrast varied across those regimens. The registry also does not report geographic or site-level details that would help characterize representativeness.

The reported primary group counts are 110 and 109, while the safety at-risk counts are 117 and 119. The registry does not explain the differences among enrollment, planned evaluable participants, and endpoint-specific counts. It states that only participants with data at the relevant timepoint were analyzed, but does not describe missing-data assumptions or sensitivity analyses. This limits assessment of how incomplete outcome data might affect the estimates.

The record does not report whether multiplicity was controlled, provide a complete statistical analysis plan, or describe interim analyses. It also does not provide full model specifications or diagnostics. The primary estimate remains interpretable as the sponsor-reported result, but these omissions constrain independent evaluation of analysis choices and robustness.

Finally, the posted treatment period is 12 weeks, and the listed outcomes are FEV1 measures. The registry record does not establish longer-term effects or results for outcomes not reported. Safety counts are summarized without sufficient detail to determine causality or characterize event timing and duration.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Evaluate the Effect of Umeclidinium (UMEC) as Combination Therapy in Subjects With Chronic Obstructive Pulmonary Disease (COPD) — NCT02257372.
• Registry record last updated 2017-08-17; status last verified 2017-07.
• Results first posted 2015-11-24.
• 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

NCT02257372 is a completed randomized, double-blind, parallel-group Phase 4 study of UMEC added to ICS/LABA compared with placebo added to ICS/LABA in participants with COPD. The registry lists enrollment of 236 and a 12-week treatment period. The primary endpoint was change from baseline in trough FEV1 on Day 85.

The sponsor’s mixed model repeated measures analysis reports a mean difference of 0.123 liters, with a 95% confidence interval from 0.071 to 0.174 liters and p <0.001. The posted unadjusted recalculation is close to the sponsor’s result. One secondary FEV1 endpoint is also reported, with a direction consistent with the primary result. The record reports serious and other adverse-event counts but does not provide enough information to establish causality.

Multiplicity procedures, detailed missing-data methods, the full analysis plan, and the trial’s original sample-size justification are not reported in the registry record. Interpretation is limited to the posted outcomes, analysis population, treatment context, and study period.