Phase IIb Study of Umeclidinium (UMEC) Bromide Versus Placebo in Subjects With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase IIb Study of Umeclidinium (UMEC) Bromide Versus Placebo in Subjects With Asthma (NCT03012061), a randomized phase 2 study. The primary outcome is Mean Change From Baseline in Clinic Trough Forced Expiratory Volume in 1 Second (FEV1) at Week 24.

2. Clinical Question

The trial was designed to compare the efficacy, safety and tolerability of the two umeclidinium doses with placebo in participants with asthma. Its primary lung-function question concerns the difference in mean change from baseline, not whether every participant experienced an improvement or whether the observed group contrast predicts an individual response. The registry record describes the study as randomized, double-blind and parallel-group, and reports three treatment arms.

The clinical question is specifically about adding umeclidinium to background fluticasone furoate, rather than comparing umeclidinium with no asthma treatment. The placebo group also received fluticasone furoate. The contrast therefore concerns the study regimens as assigned, under the conditions and follow-up represented in the record. The primary endpoint is a lung-function measure; the registry also lists other lung-function, safety and tolerability outcomes.

3. Trial Design

This was a Phase IIb, randomized, double-blind, placebo-controlled, three-arm, parallel-group study in participants with asthma. The registry reports enrollment of 425. Participants were assigned to once-daily UMEC 31.25 mcg, UMEC 62.5 mcg or placebo for 24 weeks. Each arm also received fluticasone furoate 100 mcg once daily. The record describes administration by dry powder inhaler.

The brief summary describes a maximum participation period of approximately 31 weeks, including pre-screening, screening/run-in, randomization/treatment and safety follow-up. The stated planned number of randomized participants was approximately 384, with 128 participants randomized to each of the three arms. Those are planning figures in the study description; the registry separately reports enrollment of 425. The record does not explain the difference between the planned and reported enrollment figures.

The study began on 2017-01-25, had primary completion on 2018-05-30 and is listed as completed. The primary endpoint compares mean change in clinic trough FEV1 from baseline to Week 24. The primary analysis description states that the Intent-to-Treat Population included randomized participants, excluding those randomized in error who did not receive study drug, and that participants with baseline data and at least one post-baseline measurement were analyzed. Different participants could contribute at different time points.

These design features define the context for interpreting the treatment contrasts. Randomization and masking are reported, but further details about the randomization procedure, allocation concealment, masking assessment, or the trial’s original statistical planning assumptions are not reported in the registry record. The posted results include sponsor analyses using mixed-model repeated measures for the primary endpoint and ANCOVA for the reported secondary lung-function endpoint.

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: Total 421 participants were included in the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat Population. Participants with available data at Baseline and at least one time point post-Baseline were analyzed. All on- and post-treatment data was included. Different participants may have been analyzed at different time points.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Mean Change From Baseline in Clinic Trough Forced Expiratory Volume in 1 Second (FEV1) at Week 24, measured over Baseline (Day 1 pre-dose) and Week 24.

The primary endpoint is mean change from baseline in clinic trough forced expiratory volume in one second (FEV1) at Week 24, measured in liters. FEV1 is defined in the registry as the maximal amount of air that can be forcefully exhaled in one second. The highest of three technically acceptable measurements was recorded at each visit. Baseline was the last acceptable or borderline acceptable pre-dose clinic FEV1 value before randomized treatment began. Change was defined as the Week 24 value minus baseline.

FEV1 is used as a measure of lung function. A trough measurement concerns the clinic value at the specified point in the dosing schedule, rather than the separate secondary measure taken three hours after dosing. Considering change from baseline places the Week 24 measurement in relation to each participant’s starting value. Comparing group means then describes the average difference in change between assigned regimens; it does not describe the range of individual responses.

The reported arm estimates are least-squares means with standard errors. The registry says that the primary treatment-policy estimand included all on- and post-treatment data. The stated analysis population required baseline and at least one post-baseline measurement, and different participants could contribute at different time points. These details matter because the estimate represents the analyzed data under those rules, rather than a complete set of Week 24 measurements from every randomized participant.

The registry record identifies the endpoint and its measurement procedure, but does not report a clinically important difference threshold for interpreting the magnitude of a change. Statistical separation from placebo and clinical importance are distinct questions.

7. Results Posted in the Registry

• UMEC 31.25 mcg QD: mean 0.30 versus 0.13 on control; difference 0.18 (95% CI 0.09 to 0.26), standardized effect d = 0.50; z-test p = <0.001.
• UMEC 62.5 mcg QD: mean 0.31 versus 0.13 on control; difference 0.18 (95% CI 0.10 to 0.27), standardized effect d = 0.52; z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Mean Change From Baseline in Clinic FEV1 at 3 Hours Post Dose at Week 24

• 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:
  • UMEC 31.25 mcg QD: mean 0.37 versus 0.18 on control; difference 0.19 (95% CI 0.10 to 0.28), standardized effect d = 0.52; z-test p = <0.001.
  • UMEC 62.5 mcg QD: mean 0.37 versus 0.18 on control; difference 0.20 (95% CI 0.11 to 0.29), standardized effect d = 0.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for UMEC 31.25 mcg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for UMEC 62.5 mcg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists five secondary outcomes, spanning lung function and safety-related measures. The detailed quantitative secondary results available in the record concern mean change in clinic FEV1 three hours after dosing at Week 24. For that measure, the sponsor reports ANCOVA comparisons against placebo for both UMEC doses, each with a positive mean difference and p < 0.001. The posted group means and recalculated contrasts point in the same direction as the sponsor’s secondary analyses.

This secondary lung-function finding is directionally consistent with the primary endpoint, which also concerns FEV1 at Week 24 but measures clinic trough values rather than the three-hours-post-dose measure. The outcomes address related but distinct measurement times. Consistency across these lung-function measures can add context, but it does not make them interchangeable or constitute independent confirmation: they are from the same trial and participants may contribute to more than one analysis.

The record lists additional secondary outcomes concerning adverse events, electrocardiogram findings, blood pressure and pulse rate, but detailed quantitative results for those outcomes are not present in the available endpoint results. Their results are not reported in the registry record in the registry record used for this interpretation. Therefore, the overall secondary pattern cannot be characterized across all listed outcome families from the lung-function results alone.

Secondary analyses generally carry less evidential weight than the prespecified primary question, particularly when many outcomes or comparisons are examined. Multiple testing can increase the chance of at least one nominally significant result. Whether the trial adjusted for multiplicity, established a testing hierarchy, or designated secondary outcomes as confirmatory is not reported in the registry record. The secondary p-values should therefore be read as reported evidence for those specific comparisons, not as a substitute for the primary analysis or as definitive evidence across all secondary outcomes.

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

• Mean Change From Baseline in Clinic FEV1 at 3 Hours Post Dose at Week 24
• Number of Participants With On-treatment Adverse Events (AE), Non-serious Adverse Events (Non-SAE)
• Number of Participants With On-treatment Abnormal Electrocardiograms (ECG) Findings
• Mean Change From Baseline in On-treatment Systolic Blood Pressure (SBP) and Diastolic Blood Pressure (DBP)
• Mean Change From Baseline in On-treatment Pulse Rate

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change in FEV1 measured in liters. For a continuous outcome, a treatment contrast can be expressed as the difference between group means. Here, the registry reports least-squares means and standard errors, and the sponsor’s primary comparison is a mean difference adjusted through a mixed-model repeated-measures analysis.

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group mean. It is not necessarily the same as a simple arithmetic average of all observed changes, because the model can account for specified features of the data. The registry reports the estimate and standard error, but does not report the complete model formula, all included covariates, covariance structure, or other implementation details. Therefore, the reported least-squares means should be read as the sponsor’s modeled group estimates, not reconstructed as raw averages.

Why use repeated-measures modeling?

Mixed-model repeated measures (MMRM) is a general approach for analyzing measurements collected repeatedly over time. It can model the association among a participant’s repeated measurements rather than treating each measurement as unrelated. In general, repeated-measures models can use available outcome data at different visits while accounting for the structure specified in the model. The registry says that different participants may have been analyzed at different time points and that the primary treatment-policy estimand included on- and post-treatment data. The full model details and missing-data assumptions are not reported in the registry record, so the specific behavior of this MMRM cannot be fully assessed from the posted information.

The primary outcome description also states that the analysis population consisted of randomized participants, with an exclusion for participants randomized in error who did not receive study drug, and required baseline and at least one post-baseline measurement. This is the population definition reported for the endpoint, not a guarantee that every randomized participant contributed a Week 24 value. A treatment-policy estimand is intended to address the effect of assignment while including the specified on- and post-treatment data; the registry does not provide enough detail to evaluate all estimand components or intercurrent-event handling.

How should the confidence interval and p-value be read?

A confidence interval gives a range of effect estimates compatible with the data and the analysis procedure at the stated confidence level. The sponsor reports 95% confidence intervals for both primary treatment contrasts. Their intervals lie above zero, in the direction of a greater mean change for each UMEC group than for placebo. The accompanying p-values are p < 0.001. In general, a p-value evaluates how unusual the observed data, or more extreme data, would be under a specified null hypothesis and model. It is not a measure of effect size or clinical relevance.

The recalculated comparisons are simple, unadjusted comparisons derived from posted summary statistics. They are not a recreation of the sponsor’s repeated-measures model. The recalculated standard deviations are approximated from the reported standard errors and group sizes, so those calculations rely on less information than the sponsor’s model-based analysis. The posted record reports no discrepancy, and the sponsor’s analyses are the appropriate source for the trial’s reported inference.

What does an unadjusted recalculation add?

A simple recalculation can act as a consistency check on the direction and approximate size of a reported contrast. It can show whether the posted group summaries produce a similar unadjusted estimate. It cannot reproduce adjustment for repeated observations, model covariates, or the sponsor’s full analysis choices when those details are not available. Agreement between the recalculation and sponsor estimate supports numerical consistency, but does not independently validate the model assumptions or remove uncertainty about the analysis specification.

The record also lists ANCOVA for the reported secondary lung-function endpoint. In general, analysis of covariance compares outcome means while accounting for specified covariates. The registry does not report the full ANCOVA specification. The secondary model and its results should therefore be interpreted as reported, without assuming details that are not in the record.

Why do variance and over-dispersion matter in general?

For continuous outcomes, the spread of individual observations affects the precision of an estimated mean difference. More variable outcomes generally produce less precise estimates when other conditions are held constant. The posted summary statistics give standard errors for arm estimates, while the recalculation uses an approximate pooled standard deviation. This conversion is a calculation aid, not a separately reported trial statistic.

Over-dispersion is most directly relevant to count outcomes, where the observed variability exceeds what a simple count model assumes. It is not the central model issue for this continuous FEV1 endpoint. General statistical practice would consider whether the chosen model represents the data adequately, but model diagnostics and assumptions are not reported in the registry record.

Finally, the analysis involves more than one dose comparison and the record lists additional outcomes. Testing multiple hypotheses raises a general multiplicity concern: when many tests are considered, the chance of at least one apparently significant finding can increase. Whether and how the study controlled multiplicity is not reported in the registry record. The primary endpoint should consequently be distinguished from secondary and exploratory findings, and the significance of secondary results should not be interpreted as though multiplicity had been addressed unless that is documented.

11. Confidence Intervals and Precision

The sponsor’s primary estimates have 95% confidence intervals that provide information about statistical precision as well as direction. For UMEC 31.25 mcg versus placebo, the reported mean difference is 0.176 liters, with a 95% confidence interval from 0.092 to 0.260. For UMEC 62.5 mcg versus placebo, the reported mean difference is 0.184 liters, with a 95% confidence interval from 0.101 to 0.268. Both intervals are entirely above zero, indicating that the model-based estimates are compatible with a positive mean difference under the reported analysis.

A confidence interval is not a range containing every participant’s response, nor does it express the probability that the true effect lies within the particular interval. In general, it is a range produced by a procedure that would cover the underlying parameter at the stated rate over repeated applications under its assumptions. Its width reflects sampling uncertainty and the analysis method; it does not account automatically for every potential source of bias or model misspecification.

The intervals allow a more informative reading than the p-values alone. They convey a range of effect sizes compatible with the data, while the p-values provide evidence against a null difference under the model. The registry does not report a clinically important threshold for FEV1 change, so the intervals cannot be classified against such a threshold from this record. Statistical precision should not be equated with clinical importance.

The unadjusted recalculated intervals are close to the sponsor’s intervals: 0.092 to 0.259 for UMEC 31.25 mcg and 0.101 to 0.267 for UMEC 62.5 mcg. Their similarity is a consistency observation, not evidence that the two methods are interchangeable. The recalculations use posted summaries and approximate variability; the sponsor used MMRM. The sponsor’s estimates and intervals take precedence as the reported trial analysis.

12. Planning a Similar Trial: Sample Size

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

The sample-size display is a planning illustration based on the observed effect, not the original trial’s sample-size justification. Its rows represent planning for 100%, 75% or 50% of the observed effect. The figures are participants per arm, not total participants or total events. The two power columns describe the approximate number of participants per arm associated with 80% power and 90% power under the stated illustration assumptions.

Power is the probability that a specified analysis would detect an effect of a particular size at the chosen significance level if that effect were the true one, assuming the planning model applies. The 80% and 90% columns therefore describe design targets for hypothetical future studies, not a retrospective rating of this trial. This is not observed power.

The listed 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 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.

Smaller effects are harder to distinguish from random variation, so the planning illustration requires more participants per arm when the assumed effect is reduced. The rows for planning for 75% or 50% of the observed effect thus represent more demanding targets than planning for the full observed effect. These calculations are illustrations based on the observed contrast and should not be read as evidence that the observed effect will recur in another study. They also do not account for design features that are not specified in the illustration assumptions.

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 = 0.176; pooled standard deviation σ = 0.354.
2. n = 2 × (1.96 + 0.842)² × 0.354² / 0.176² = 63.8, rounded up to 64 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 <- 0.1757                      # observed difference in means
sigma <- 0.354182732498353                     # 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(3012061)
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 = 64 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 114 (80% power), 152 (90% power)
 50% of observed effect: n per arm = 256 (80% power), 342 (90% power)
power.t.test: 64.8 
Simulated power at n = 64 per arm: 0.793 (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 used mixed-model repeated measures and reported a mean difference of 0.176 liters for UMEC 31.25 mcg versus placebo, with a 95% confidence interval from 0.092 to 0.260 and p < 0.001. For UMEC 62.5 mcg versus placebo, it reported 0.184 liters, with a 95% confidence interval from 0.101 to 0.268 and p < 0.001.

The recalculated estimates from posted arm summaries are 0.176 liters and 0.184 liters, respectively. Their confidence intervals and p-values are also close to the reported analyses. These recalculations are simple and unadjusted; they do not reproduce the sponsor’s MMRM or account for its full model specification. The record indicates no discrepancy. Accordingly, the sponsor’s analysis is the primary basis for interpreting the trial results, while the recalculation serves as a numerical cross-check rather than a replacement analysis.

The sponsor’s reported results also label both comparisons as superiority analyses. That label describes the stated direction of the statistical test; it does not by itself establish clinical importance, individual benefit, or a difference between the two UMEC doses. A direct comparison of doses is not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The record reports two primary treatment comparisons against placebo and lists several secondary outcomes. It does not report whether the trial used a multiplicity adjustment, a hierarchical testing strategy, or another procedure to control the overall type I error across comparisons. Without that information, the reported p-values should be interpreted as comparison-specific results rather than assumed to have family-wise error control. This matters most when drawing conclusions across multiple doses and outcomes, since the opportunity for chance-positive findings increases as more hypotheses are tested.

For the primary endpoint, the sponsor reports an MMRM analysis. The registry describes the analysis population and states that all on- and post-treatment data were included under the treatment policy estimand. It also notes that different participants may have been analyzed at different time points and that the primary analysis required baseline data plus at least one post-baseline measurement. The record does not report the complete missing-data strategy, model assumptions concerning missing observations, sensitivity analyses, or the extent and pattern of missing endpoint data. Those details are important for judging how robust the estimate is to incomplete follow-up.

The Intent-to-Treat Population description excludes participants randomized in error who did not receive study drug, and requires available baseline and post-baseline data for the primary endpoint analysis. This is the registry’s stated analysis definition. The number analyzed differs by arm in the posted primary results, but the record does not provide enough detail to explain each participant’s contribution or missingness. It would be inappropriate to infer reasons for missing data or to assume that the model eliminates all potential bias from missing outcomes.

The registry record also does not report the full statistical analysis plan, interim-analysis procedures, or the original sample-size justification. These omissions limit assessment of prespecification and the relationship between the posted analyses and the planned analysis. They do not change the reported estimates, but they constrain how fully the analysis process can be independently evaluated.

16. Safety Results

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

Deaths

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: asthma (1.4%), hypertension (1.4%), pulmonary embolism (0.7%), pulmonary infarction (0.7%), thrombophlebitis superficial (0.7%).

The safety figures count participants with serious adverse events among those at risk in each arm. The registry reports 5 of 143 for placebo, 4 of 139 for UMEC 31.25 mcg and 3 of 139 for UMEC 62.5 mcg. These are participant counts, not event totals; one participant could potentially experience more than one event, and the posted figures do not describe event timing or duration.

The record reports zero deaths in each arm. Serious adverse event terms listed across the study include Asthma and Hypertension, each reported as 1.4%, and Pulmonary embolism, Pulmonary infarction, Thrombophlebitis superficial and Diverticulitis, each reported as 0.7%. The registry figures do not establish that treatment caused any particular event, nor do they provide enough information to compare risks reliably or assess rare harms.

These data are descriptive and should be read alongside the trial’s duration, population and follow-up. The registry record does not provide a detailed causal assessment or all event-level clinical context. No safety conclusion beyond the posted counts and terms is warranted.

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

The posted primary results show that mean change from baseline in clinic trough FEV1 at Week 24 was higher in each UMEC group than in the placebo group receiving the same background fluticasone furoate regimen. The sponsor’s reported mean differences are 0.176 liters for UMEC 31.25 mcg and 0.184 liters for UMEC 62.5 mcg, with 95% confidence intervals above zero and p < 0.001 for both comparisons. These estimates describe group averages under the reported analysis.

They do not show how every participant responded, whether the changes were noticeable to participants, or whether the treatment effect persists beyond the study period. The registry record does not report a threshold for a clinically important FEV1 difference. Statistical evidence against a null difference is not the same as evidence that a difference is clinically important, and neither is a substitute for considering the full balance of benefits and harms.

The study compares each UMEC dose with placebo, not one UMEC dose directly with the other. Similar estimates versus placebo do not prove that the doses are equivalent, nor do they establish that one dose is superior. The record does not report a direct dose comparison or an equivalence or non-inferiority analysis.

Interpretation is limited to the enrolled asthma population, the study regimens, the 24-week treatment period, the measured endpoints and the analysis described in the registry. The results do not automatically generalize to populations, treatment combinations or settings not represented in the trial. Missing-data assumptions, multiplicity procedures and the original sample-size rationale are not reported in the registry record, which limits further evaluation of the analysis and its broader implications.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result should be read through several statistical layers. The primary outcome is a change in a continuous lung-function measure, and the central effect estimate is a between-group mean difference. Looking at the arm means alone gives context, while the contrast and its confidence interval quantify the estimated separation and its precision. The p-value adds evidence relative to a null-difference model but cannot answer questions about clinical importance or individual response.

The record also makes the distinction between a sponsor’s prespecified-style model analysis and a simple recalculation visible. The MMRM estimates are close to the unadjusted calculations from posted summaries, but those calculations do not reproduce the model or establish its assumptions. Numerical agreement can be reassuring as a consistency check while leaving the sponsor’s analysis as the main inferential result.

Other issues are equally consequential. Participants could contribute measurements at different time points, and the analysis population required baseline and at least one post-baseline observation. The full missing-data approach is not reported. Multiple outcomes and treatment comparisons raise questions about multiplicity, but the registry does not state whether an adjustment was used. These omissions do not erase the observed result; they define the limits of what can be concluded from the posted record.

Finally, the planning illustration based on the observed effect is not a retrospective measure of power. It shows how assumed effect size and target power relate to a hypothetical number of participants per arm under stated assumptions. Separating those planning calculations from observed trial evidence helps prevent a common interpretive error. Together, these distinctions support a more transparent reading of the estimated effect, its uncertainty and the limits of the available record.

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 complete statistical analysis plan, the trial’s original sample-size justification, or interim-analysis procedures. It also does not provide the full MMRM or ANCOVA specifications, including all covariates and model structure. These omissions limit independent assessment of prespecification and model implementation.

Although the primary outcome description states that on- and post-treatment data were included and describes the analysis population, the detailed missing-data strategy and sensitivity analyses are not reported in the registry record. Different participants may have contributed at different time points. The posted results therefore cannot, by themselves, show how robust the estimates are to missing observations or explain each arm’s analysis count.

The registry lists multiple secondary outcomes and reports results for a secondary lung-function measure, but detailed results for the other listed secondary outcomes are not present in the registry record for interpretation. Multiplicity adjustment or a testing hierarchy is not reported. This limits the strength of conclusions across outcomes beyond the primary endpoint.

The primary outcome is a surrogate measure of lung function, and the record does not report a clinically important difference threshold. The trial’s 24-week treatment period also bounds what can be inferred about longer-term outcomes. Finally, no direct comparison between the two UMEC doses is reported. Similar placebo contrasts should not be taken as evidence of equivalence between doses.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Phase IIb Study of Umeclidinium (UMEC) Bromide Versus Placebo in Subjects With Asthma — NCT03012061.
• Registry record last updated 2020-10-28; status last verified 2020-10.
• Results first posted 2019-06-19.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT03012061 is a completed Phase IIb, randomized, double-blind, parallel-group study of umeclidinium versus placebo in participants with asthma. The registry reports enrollment of 425 and a 24-week treatment period. Both UMEC groups and the placebo group received background fluticasone furoate 100 mcg once daily.

The primary endpoint was mean change from baseline in clinic trough FEV1 at Week 24. The sponsor reported positive mean differences versus placebo for UMEC 31.25 mcg and UMEC 62.5 mcg, with 95% confidence intervals above zero and p < 0.001 for each comparison. Recalculations from posted summaries were close to the sponsor estimates, and the record indicates no discrepancy.

The registry also lists secondary lung-function and safety outcomes. Safety summaries report serious adverse event counts and zero deaths in each arm. Details about multiplicity, missing-data sensitivity analyses, full model specifications and the original sample-size rationale are not reported in the registry record.