A Study to Compare the Efficacy and Safety of Umeclidinium/Vilanterol and Fluticasone Propionate/Salmeterol 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 Compare the Efficacy and Safety of Umeclidinium/Vilanterol and Fluticasone Propionate/Salmeterol in Subjects With Chronic Obstructive Pulmonary Disease (COPD) (NCT01817764), a randomized phase 3 study. The primary outcome is Change From Baseline in 24-hour Weighted-mean Serial FEV1 on Treatment Day 84.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, multicenter, double-blind, double-dummy, parallel-group study sponsored by GlaxoSmithKline. Its official title describes evaluation of efficacy and safety over 12 weeks in subjects with COPD. The registry lists the study as completed and records enrollment of 707 participants. The start date is 2013-03-01 and the primary completion date is 2013-10-01.

Before treatment, eligible subjects completed a 7 to 14 day run-in period. The study description says approximately 710 eligible subjects were expected to be equally randomized, with at least 568 evaluable subjects targeted. The registry’s enrollment field records 707; those planning statements should not be mistaken for the number with data in every analysis. The primary outcome has 315 participants in the UMEC/VI arm and 310 in the FSC arm. The secondary outcome has 317 and 312, respectively. Safety summaries list 353 participants at risk in each group.

Participants were assigned to one of two treatment groups for 12 weeks. The UMEC/VI group received 62.5/25 micrograms once each morning through the Novel dry powder inhaler and placebo morning and evening through ACCUHALER/DISKUS. The FSC group received 250/50 micrograms morning and evening through ACCUHALER/DISKUS and placebo once each morning through the Novel dry powder inhaler. The matching placebo schedules and devices are part of the double-dummy design.

The brief description says a safety follow-up assessment was planned approximately 7 days after the end of study treatment, including early withdrawal where applicable. Total participation was expected to last approximately 15 weeks. The registry record does not report further details of the randomization sequence or allocation concealment.

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 707 participants, representing the enrolled participants, were randomized to study treatment. Of these, 706 comprised the Intent-to-Treat 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: Intent-to-Treat (ITT) Population: all par. randomized to treatment who received \>=1 dose of randomized study medication in the treatment period. Only par. with analyzable data at the indicated time point were assessed, but all par. without missing covariate information and with \>=1 post-Baseline measurement were 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 in 24-hour Weighted-mean Serial FEV1 on Treatment Day 84, measured over Baseline and Day 84.

The primary endpoint is change from baseline in 24-hour weighted-mean serial FEV1 on Treatment Day 84, measured in liters. FEV1 is defined in the registry as the maximal amount of air that can be forcefully exhaled in one second. A change score compares the Day 84 value with the baseline value; the registry specifies Day 84 minus baseline.

The weighted mean combines pre-dose FEV1 with measurements collected after the morning dose at 5 and 15 minutes, and at 1, 3, 6, 9, 12 (before the evening dose), 13, 15, 18, 23, and 24 hours. This repeated-measure schedule is intended to describe lung function across the dosing interval rather than at a single moment. As a general statistical point, a weighted mean can capture the overall profile across specified time points, but its interpretation depends on the timing and weighting defined for the measure.

The registry reports least-squares means and standard errors for the endpoint, with an analysis of covariance adjusting for treatment, baseline FEV1, and smoking status. This adjusted comparison addresses the prespecified outcome as recorded, rather than simply comparing unadjusted raw changes. The endpoint is a lung-function measure; it does not by itself describe symptoms, daily functioning, or all aspects of safety.

7. Results Posted in the Registry

• FSC 250/50 µg BID: mean 0.09 versus 0.17 on control; difference -0.07 (95% CI -0.11 to -0.04), standardized effect d = -0.32; 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 Trough FEV1 on Day 85

• 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:
  • FSC 250/50 µg BID: mean 0.07 versus 0.15 on control; difference -0.08 (95% CI -0.12 to -0.04), standardized effect d = -0.35; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FSC 250/50 µg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry posts one secondary outcome: change from baseline in trough FEV1 on Day 85. Its arm-level estimates follow the same broad direction as the primary outcome, with a positive change in both groups and a higher estimate in the UMEC/VI group. This is a different measure and time point from the primary 24-hour weighted-mean FEV1 endpoint on Day 84. Its general pattern is consistent with, but does not independently establish, the primary finding.

The registry lists a recalculated comparison for the secondary measure but no sponsor-reported analysis for it. That makes the secondary result less direct as evidence about the trial’s own inferential analysis. The secondary endpoint should be read as additional descriptive information, rather than as an equal-status confirmation of the primary result.

Multiplicity is another reason to interpret secondary findings cautiously. When several outcomes or comparisons are tested, the chance of at least one apparently notable result can increase. Statistical approaches can control or otherwise address that issue, but the registry record does not report whether a multiplicity adjustment or hierarchical testing plan was used. The number of outcome measures is listed as 2, with one secondary outcome posted, but that information alone does not establish how testing was organized.

The secondary data do not change the identity of the primary endpoint or its reported analysis. They add context about another FEV1 measure, while leaving unanswered questions about multiplicity, missing data, and the sponsor’s inferential method for this secondary result. No additional secondary outcomes or sponsor analyses are reported in the registry record.

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

• Change From Baseline in Trough FEV1 on Day 85

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, meaning that it is measured on a numerical scale rather than classified into a small set of categories. In this case, change in FEV1 is measured in liters. The registry reports a least-squares mean for each group. As a general statistical concept, a least-squares mean is a model-based group estimate adjusted for the covariates included in the model; it need not equal the unadjusted average among participants with observed values.

What does the ANCOVA do?

The registry states that the primary analysis used analysis of covariance (ANCOVA), with treatment, baseline FEV1, and smoking status in the model. In general, ANCOVA estimates a group contrast while accounting for selected baseline characteristics. Baseline adjustment can improve precision when baseline measurement is associated with the follow-up outcome, and it makes the analysis conditional on the model’s included covariates. The record identifies those covariates but does not report additional modeling details, such as coding choices, diagnostics, or sensitivity analyses.

The baseline value was the mean of two assessments made 30 minutes and 5 minutes before dosing on Day 1. The change score was calculated as the Day 84 value minus the baseline value. Using two pre-dose assessments to define baseline is part of the registry’s endpoint description; it should not be confused with the later serial measurements that contribute to the 24-hour weighted mean.

How should the arm estimates be read?

The posted primary least-squares mean changes are 0.165 liters for UMEC/VI and 0.091 liters for FSC. Each estimate is accompanied by a standard error in the record. A standard error describes the sampling uncertainty of an estimated quantity under the analysis; it is not the spread of individual participants’ measurements. General statistical reasoning distinguishes that uncertainty from a standard deviation, which describes variation among observations. The registry reports standard errors, not standard deviations, for these arm estimates.

The sponsor’s ANCOVA reports a mean difference (net) of 0.074 liters and a 95% confidence interval from 0.038 to 0.110. The recalculated contrast uses FSC relative to UMEC/VI, so its sign is reversed. A contrast depends on the order in which groups are subtracted; reversing the order changes the sign but not the underlying separation. The registry’s own adjusted analysis is the appropriate reference for the primary inference.

What does the p-value convey?

The reported p-value is p < 0.001. In general, a p-value is calculated under a null hypothesis and the assumptions of the statistical model. It measures how incompatible the observed data are with that null model, not the probability that a treatment is effective or that the null is true. Statistical evidence and effect magnitude are different ideas: the estimate describes the observed contrast, while the p-value summarizes evidence against a specified null model.

A confidence interval gives a range of values compatible with the data and model at its stated confidence level. In repeated use under the model, intervals constructed in the same way would contain the target parameter at the stated rate. It is not correct to interpret a particular 95% interval as assigning a 95% probability to the fixed parameter. The interval’s width also matters: it communicates precision in a way the p-value does not.

What is the role of recalculation?

The simple recalculation is an unadjusted comparison based on posted summary statistics, whereas the registry’s sponsor analysis is an ANCOVA. General statistical principles explain why those need not match exactly: adjustment for baseline and other covariates, the analysis population, and the model all affect an estimate and its uncertainty. In this record, the sponsor’s reported analysis is available and there is no flagged discrepancy. The recalculation is best understood as a transparent summary-statistic check, not as a competing primary analysis.

The posted arm sizes for the primary outcome are 315 and 310. Those are the numbers attached to the endpoint’s reported group estimates, not the safety counts or the study’s total enrollment. Different outcomes can have different analysis counts because the registry reports outcome-specific data. The record says only participants with analyzable data at the indicated time point were assessed, while describing the ITT population as randomized participants who received at least one dose. Further details about the disposition of missing values are not reported in the registry record.

For planning illustrations, the record uses a normal approximation, equal allocation between two arms, a two-sided significance level of 0.05, and specified fractions of the observed effect. General statistical concepts explain why a smaller target effect requires more participants to distinguish it from random variation at the same assumed significance level and power. These calculations are illustrations based on the observed contrast, not the trial’s original design rationale.

11. Confidence Intervals and Precision

The sponsor’s primary estimate is a mean difference of 0.074 liters, with a 95% confidence interval from 0.038 to 0.110. The interval lies on the positive side under the registry’s reported group ordering. It gives a range of effect sizes compatible with the primary analysis and its assumptions, rather than a single certain value. The interval’s lower and upper endpoints show that the estimate is not infinitely precise, even though the reported p-value is below 0.001.

As a general explanation, a confidence interval reflects both the estimated effect and its uncertainty. A narrower interval indicates greater precision for the parameter under the model; a wider interval leaves more uncertainty about its magnitude. The interval does not capture every source of uncertainty, such as unreported analysis choices or limitations in generalizing beyond the study population. Nor does it determine whether a difference is clinically important: the registry record does not report a threshold for clinical importance.

The sponsor’s interval is based on the ANCOVA analysis. The simple recalculation is unadjusted and uses the posted summary statistics; it is not an equivalent substitute for the model-based confidence interval. The two estimates also use opposite contrast directions, so signs must be interpreted according to which group is subtracted from which. The sponsor’s own reported analysis is the reference for the primary result.

For the secondary endpoint, the registry posts arm-level standard errors and a recalculated interval, but no sponsor-reported analysis. That distinction matters when assessing how directly an interval reflects the trial’s own analysis. The primary interval and the secondary summaries should not be treated as identical in evidentiary status.

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 primary effect and use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set in turn to 100%, 75%, or 50% of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

For planning for 100% of the observed effect, the figures are 153 participants per arm for 80% power and 205 participants per arm for 90% power. For planning for 75% of the observed effect, they are 272 participants per arm for 80% power and 364 participants per arm for 90% power. For planning for 50% of the observed effect, they are 611 participants per arm for 80% power and 817 participants per arm for 90% power.

In plain language, 80% power means that, under the stated assumptions and if the target effect were the true effect, the design would have an 80% chance of meeting the specified statistical criterion. The 90% column expresses the corresponding planning target at a higher chance of detecting that effect. These are prospective planning interpretations, not measures of what happened in this completed trial.

Smaller effects are harder to distinguish from random variation, so they require more participants under otherwise unchanged assumptions. The estimates are sensitive to the assumed effect and model; they are not guarantees of a result. This is not observed power.

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 = -0.074; pooled standard deviation σ = 0.231.
2. n = 2 × (1.96 + 0.842)² × 0.231² / -0.074² = 152.6, rounded up to 153 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 <- -0.074                      # observed difference in means
sigma <- 0.230688521736551                     # 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(1817764)
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 = 153 (80% power), 205 (90% power)
 75% of observed effect: n per arm = 272 (80% power), 364 (90% power)
 50% of observed effect: n per arm = 611 (80% power), 817 (90% power)
power.t.test: 153.5 
Simulated power at n = 153 per arm: 0.796 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports the sponsor’s primary analysis as an ANCOVA mean difference (net) of 0.074 liters, with a 95% confidence interval from 0.038 to 0.110 and p < 0.001. The arm estimates are 0.165 liters for UMEC/VI and 0.091 liters for FSC. The sponsor’s analysis is adjusted for treatment, baseline FEV1, and smoking status, as described in the outcome record.

The recalculated comparison is a simple unadjusted calculation from posted summary statistics. It expresses FSC relative to UMEC/VI, so its estimate has the opposite sign from the sponsor’s reported difference. This is a contrast-direction issue, not evidence that the analyses point in different directions. The recalculation does not reproduce the ANCOVA adjustment and should not be used to replace the registry’s reported model-based result.

The record does not flag a discrepancy between the posted summaries and the sponsor analysis. In interpreting the primary result, the sponsor’s own adjusted analysis takes precedence over the unadjusted recalculation. The recalculation can still help readers understand how the summary-statistic contrast relates to the arm-level estimates, while recognizing that the registry’s ANCOVA is the analysis reported for the primary comparison.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity concerns arise when a study makes more than one statistical comparison. As a general concept, carrying out many tests can increase the chance of at least one result appearing statistically notable by chance. A prespecified testing hierarchy or adjustment can address this concern, but neither the presence nor the absence of such a plan is reported in the registry record. The record identifies the primary outcome and one posted secondary outcome; it does not describe how the full testing family was defined or controlled.

The primary outcome description says the analysis used an ITT population, defined as all participants randomized to treatment who received at least one dose of randomized study medication during the treatment period. It also says only participants with analyzable data at the indicated time point were assessed. These statements describe the population framework and the availability of outcome data, but they do not fully specify how missing values were handled.

Specific methods for missing data, including any imputation, assumptions about why observations were missing, or sensitivity analyses, are not reported in the registry record. Further details about withdrawals, exclusions from the endpoint analysis, and the impact of missing outcome data are also not reported. Therefore, the posted analysis counts should be read as outcome-specific counts rather than as evidence that every randomized participant contributed to every measure.

The ANCOVA description names treatment, baseline FEV1, and smoking status. It does not report additional model diagnostics, covariate coding, or robustness analyses. This limits independent assessment of how sensitive the estimate is to modeling choices. The registry record also does not report interim analyses or stopping rules. Their absence from the record should be understood as unreported information, not as proof that a particular procedure was or was not used.

16. Safety Results

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

Other (non-serious) adverse events

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

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (0.8%), chronic obstructive pulmonary disease (0.8%), ischaemic stroke (0.6%), bronchitis (0.3%), burn infection (0.3%).

The safety summaries list 353 participants at risk in each group. The UMEC/VI group has 6 participants recorded as affected by a serious adverse event, and the FSC group has 10. The summaries also list 38 participants affected by other adverse events in the UMEC/VI group and 25 in the FSC group. These are counts in the registry’s safety fields; they are not the primary efficacy outcome and should be considered separately from the FEV1 comparison.

The serious-event terms listed include pneumonia and chronic obstructive pulmonary disease at 0.8% each, ischaemic stroke at 0.6%, and bronchitis, burn infection, and viral gastroenteritis at 0.3% each. The term list does not provide arm-specific counts for each event in the information recorded here, so it should not be used to attribute an individual term to one group. Deaths are not reported in the registry record.

Safety counts describe events recorded during the study and do not by themselves establish causation. The study description includes a safety follow-up assessment planned approximately 7 days after treatment ended. Detailed event narratives, severity distributions, and additional follow-up information are not reported in the registry record.

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

The primary result describes a between-group difference in change from baseline in 24-hour weighted-mean FEV1 on Treatment Day 84. The sponsor’s ANCOVA estimate is 0.074 liters, with a 95% confidence interval from 0.038 to 0.110 and p < 0.001. The posted least-squares mean changes are 0.165 liters for UMEC/VI and 0.091 liters for FSC. Together, these figures describe the estimated group contrast and its statistical uncertainty for the registry’s specified endpoint.

The result does not mean that every participant had the group-average change, or that the estimate predicts an individual person’s outcome. Group means can coexist with substantial variation in individual measurements. The registry’s reported standard errors concern the precision of estimated means, not the range of responses among participants.

The result also does not answer every question about COPD. The primary endpoint is a lung-function measure, not a complete assessment of symptoms, quality of life, exacerbations, or long-term outcomes. The record includes one secondary FEV1 measure, but it does not report a full range of clinical outcomes or longer-term follow-up. The trial’s treatment period is described as 12 weeks, so the primary endpoint should be interpreted at that study time point.

A statistically significant result is not, by itself, a determination of clinical importance. The registry record does not give a threshold for a clinically important difference. It also does not provide sufficient detail about missing-data methods or multiplicity handling to resolve all uncertainty about the analysis. The findings are therefore best understood as the posted estimate for the studied population, outcome, and time point, with the stated limitations, rather than as a blanket conclusion about treatment or care.

18. Why This Trial Matters Statistically

This trial illustrates several issues that matter when reading clinical comparisons. First, treatment schedules and devices differed, so the registry describes a double-dummy design: each group received active treatment through one device and placebo through the other. This is a design feature intended to preserve masking while accommodating different dosing schedules. The record identifies the study as randomized, double-blind, and parallel-group.

Second, the primary outcome is a model-adjusted continuous measure. Readers need to distinguish the least-squares means and the ANCOVA contrast from an unadjusted comparison of raw participant values. The sponsor’s analysis accounts for treatment, baseline FEV1, and smoking status; a summary-statistic recalculation cannot reproduce every feature of that model.

Third, the result is more informative when its magnitude and precision are considered together. The reported mean difference and confidence interval describe the estimated contrast and its uncertainty, while the p-value addresses evidence against a null model. None of these quantities alone establishes clinical importance or applies automatically to other outcomes and populations.

Finally, the record provides limited detail on several elements needed for a fuller statistical audit, including missing-data handling, multiplicity, and the trial’s own sample-size rationale. The planning illustrations based on the observed effect are distinct from the original study design. Recognizing these differences helps keep the interpretation tied to what the registry actually reports.

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 primary analysis is described as ANCOVA adjusted for treatment, baseline FEV1, and smoking status, but additional model specifications and diagnostics are not reported in the registry record. The missing-data method and sensitivity analyses are also not reported. The outcome description states that participants needed analyzable data at the indicated time point, so the endpoint counts should not be assumed to include every person enrolled or randomized.

The registry record does not report a multiplicity plan for the primary and secondary outcomes. It also does not provide a sponsor-reported analysis for the posted secondary endpoint. The secondary pattern can add context, but it cannot resolve the uncertainty about the testing strategy or substitute for the primary analysis.

The study’s original sample-size justification and design assumptions are not reported. The planning illustrations use the observed effect and stated assumptions; they do not explain how the trial’s enrollment target was originally selected. Enrollment is recorded as 707, while the brief description gives an approximate target of 710 and says at least 568 evaluable subjects were to be completed. These are distinct record entries and should not be conflated with the endpoint-specific analysis counts.

The primary outcome is a Day 84 lung-function measure during a 12-week treatment period. Long-term outcomes, clinical-importance thresholds, detailed participant-level response distributions, and further safety follow-up are not reported in the registry record. Safety event counts and listed terms offer a limited summary and do not establish causality. These constraints bound what can be concluded from the posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Compare the Efficacy and Safety of Umeclidinium/Vilanterol and Fluticasone Propionate/Salmeterol in Subjects With Chronic Obstructive Pulmonary Disease (COPD) — NCT01817764.
• Registry record last updated 2017-11-08; status last verified 2017-10.
• Results first posted 2014-05-29.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed Phase 3 randomized, double-blind, double-dummy, parallel-group study sponsored by GlaxoSmithKline, comparing UMEC/VI with FSC in subjects with COPD. Enrollment is recorded as 707. The primary outcome is change from baseline in 24-hour weighted-mean serial FEV1 on Treatment Day 84.

The sponsor’s ANCOVA reports a mean difference (net) of 0.074 liters, with a 95% confidence interval from 0.038 to 0.110 and p < 0.001. The analysis description identifies treatment, baseline FEV1, and smoking status as model terms. One secondary FEV1 outcome is posted, along with safety counts. Details on multiplicity, missing-data handling, and the trial’s original sample-size assumptions are not reported in the registry record.