Exacerbation Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Exacerbation Study (NCT00845728), a randomized phase 3 study. The primary outcome is Trough Forced Expiratory Volume in 1 Second (FEV1)..

2. Clinical Question

3. Trial Design

This was a Phase IIIb, randomized, blinded, double-dummy, parallel-group study comparing two active inhaled treatments in people with COPD. The registry lists quadruple masking. Indacaterol was given as 150 µg once daily through a single-dose dry powder inhaler; tiotropium was given as 18 µg once daily through the HandiHaler. The planned treatment duration was 52 weeks. The study is marked completed, with a start date of 2009-03 and primary completion in 2012-07.

The registry lists 3439 participants enrolled overall. The outcome summaries use different analysis populations: the primary FEV1 results include 1450 participants in the indacaterol group and 1467 in the tiotropium group, while the exacerbation outcome uses 1675 participants in each group. The primary population is defined as the Per-Protocol Set for Spirometry, a subset of the Full Analysis Set excluding patients with major or other specified protocol deviations that could affect the efficacy analysis. The reason for the different denominators across outcomes is not reported in the registry record.

The primary endpoint was measured at 12 weeks, while the secondary exacerbation outcome covers 52 weeks. This difference matters when interpreting the results: the primary comparison addresses lung function at an earlier time point, whereas the secondary comparison summarizes exacerbation rates over the treatment period. The registry describes a mixed model for the primary endpoint and gives a rate comparison for exacerbations, but a full protocol, the original sample-size justification, and a detailed statistical analysis plan are not reported in the registry record.

The trial objective was framed as a non-inferiority question for trough FEV1. The numerical contrast and its statistical uncertainty are available, but the non-inferiority margin and other design criteria needed to assess the formal decision rule are not reported in the registry record. The study structure and observed results should therefore be distinguished from a complete account of the planned inferential framework.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-Protocol Set for Spirometry (PPS-S) This set included Full Analysis Set (FAS) patients without any major protocol deviations or non-protocol deviation criteria that could affect the respective analysis of efficacy.

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 Trough Forced Expiratory Volume in 1 Second (FEV1)., measured over 12 weeks.

The primary endpoint was trough forced expiratory volume in one second (FEV1), measured in liters at 12 weeks. FEV1 is the amount of air a person can forcibly exhale in the first second of an expiratory maneuver. In this study, trough FEV1 refers to lung function near the end of the dosing interval rather than soon after taking a dose. It was defined as the average of readings taken 23 hours 10 min and 23 hours 45 min after dosing.

The registry reports least-squares means. In general, a least-squares mean is a model-based estimate that adjusts for covariates included in the analysis; it is not necessarily the simple arithmetic average of the observed measurements. The primary model included treatment and specified baseline and reversibility measurements, as well as smoking history. The registry describes the analysis population as the Per-Protocol Set for Spirometry.

FEV1 is used as a measure of lung function, and measuring it near the end of a dosing interval makes the endpoint relevant to the stated comparison of sustained bronchodilation. The primary objective was non-inferiority, meaning the question was whether the indacaterol result met a prespecified standard for being no worse than the tiotropium result by more than an acceptable margin. That margin is not reported in the registry record, so the endpoint estimates can be described, but the formal non-inferiority criterion cannot be independently evaluated from the registry information.

7. Results Posted in the Registry

• Tiotropium: mean 1.15 versus 1.13 on control; difference 0.01 (95% CI 0.01 to 0.01), standardized effect d = 0.36; 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.

Rate of COPD Exacerbations

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, based on the estimated number of events and follow-up time.
• Result:
  • Tiotropium: 0.61 versus 0.79 (Exacerbations per patient per year) on control; rate ratio 0.77 (95% CI 0.71–0.84, approximate, Poisson model); p ≈ <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for Tiotropium than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint, the rate of COPD exacerbations over 52 weeks. Its reported comparison points in a different outcome domain from the primary FEV1 measure: it concerns event frequency over the treatment period, whereas the primary result concerns lung function at 12 weeks. The secondary estimate and its interval are posted with the results, and the reported p-value is <0.001.

This result can add context to the primary lung-function comparison, but it does not directly confirm or replace it. The endpoints measure different aspects of COPD and are analyzed on different scales. A difference in exacerbation rates does not determine the non-inferiority status of the FEV1 endpoint, particularly because the non-inferiority margin is not reported in the registry record. Nor should the outcomes be treated as interchangeable measures of a single effect.

The secondary comparison is reported with an unadjusted p-value. When multiple outcomes or analyses are examined, the chance of at least one apparently notable result can increase unless the analysis plan controls for multiplicity. This is a general statistical issue. The registry record does not report a multiplicity procedure, a hierarchy for interpreting secondary endpoints, or a complete statistical analysis plan. Accordingly, the secondary finding carries less confirmatory weight than a clearly prespecified primary analysis with a documented multiplicity strategy.

The registry’s analysis details for the rate outcome are limited. It identifies a Poisson-based comparison and gives the rates, event totals, and rate ratio, but further details on model checking and handling of over-dispersion are not reported in the registry record. The result is best read as the posted secondary association under the recorded comparison, with uncertainty and analysis-plan limitations kept in view. It is not a stand-alone basis for broad conclusions about all outcomes or all patients with COPD.

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

• Rate of COPD Exacerbations

9. Statistical Interpretation

10. Statistical Methods Explained

What does the primary model estimate?

The primary endpoint is continuous: each participant has a trough FEV1 measurement in liters, and the reported group estimates are least-squares means. In general, a least-squares mean is an adjusted estimate from a statistical model. The registry says the primary analysis used a mixed model for the Per-Protocol Set for Spirometry. Treatment was included as a fixed effect, along with baseline FEV1, specified reversibility measurements, and smoking history. The registry does not give the model formula in full or report additional details about its covariance structure or estimation procedure.

Adjustment can account for measured baseline or clinical characteristics included in a model. It does not automatically remove bias from unmeasured factors, and it does not make the model assumptions irrelevant. The trial was randomized, which supports a causal comparison in its intended setting, but the reported primary analysis was restricted to a per-protocol spirometry population. Such a population is defined by adherence to protocol criteria; it is not identical to an analysis of every randomized participant. How exclusions and missing measurements affected the estimates is not reported in the registry record.

How should the mean difference and p-value be read?

The posted mean difference is the tiotropium estimate minus the indacaterol estimate. A positive value therefore corresponds to a higher estimated trough FEV1 in the tiotropium group. The unadjusted p-value tests a null hypothesis of no difference under the comparison used to produce it. In general, a small p-value indicates that results at least this inconsistent with the null would be unusual if the null and the analysis assumptions were correct. It is not the probability that the null hypothesis is true, and it does not quantify clinical importance.

Because the study objective was non-inferiority, the usual question is not simply whether a difference is statistically distinguishable from zero. Non-inferiority requires a prespecified margin defining how large a disadvantage could be considered acceptable, followed by an interval-based assessment using the planned analysis. The margin is not reported in the registry record. The posted p-value alone is not a test of non-inferiority.

What does the exacerbation rate comparison represent?

The secondary outcome is the rate of COPD exacerbations per patient per year over 52 weeks. The registry reports rates for both groups and a rate ratio comparing tiotropium with indacaterol. In general, a rate ratio is a relative measure: a value of 1 represents equal rates, a value below 1 represents a lower rate in the numerator group relative to the comparison group, and a value above 1 represents a higher rate. The registry identifies the comparison as Poisson-based.

A Poisson model is commonly used for event counts or rates. It relies on assumptions about how the event counts vary around their expected rates. Over-dispersion occurs when the observed variation is greater than the model allows. If over-dispersion is present and not accounted for, standard errors and confidence intervals from a simple Poisson model can be too small, making uncertainty appear less than it is. This is a general statistical concern, not a finding that over-dispersion occurred in this trial. Diagnostics, model adjustments for over-dispersion, and detailed analysis specifications are not reported in the registry record.

The registry gives event totals of 1319 for indacaterol and 1018 for tiotropium, alongside 1675 participants in each group. Counts and rates answer related but distinct questions: counts are totals, while rates account for the stated time basis. The registry does not report further details on how individual follow-up time, recurrent events, or any variation in observation time was handled beyond identifying the rate comparison and its time frame.

What do standard errors and confidence intervals contribute?

In general, a standard error describes the estimated sampling variability of an estimate under a statistical model. It is not the same as the spread of individual participant measurements. A confidence interval combines an estimate and its estimated uncertainty to give a range of values compatible with the data under the method’s assumptions. The registry reports confidence intervals for the comparisons. A narrow interval indicates greater precision on the scale of the estimate than a wide interval, but precision does not establish clinical importance or protect against bias and model misspecification.

For the primary outcome, the registry reports a standard error alongside each group estimate and a confidence interval for the mean difference. For the secondary rate comparison, the interval is reported with the rate ratio. The registry does not describe all details of interval construction. The statistical interpretation should therefore remain tied to the methods actually recorded rather than assuming an unreported adjustment or diagnostic procedure.

Why does the analysis population matter?

The primary results use the Per-Protocol Set for Spirometry, described as patients from the Full Analysis Set without major protocol deviations or other specified deviations that could affect the efficacy analysis. The registry reports different participant counts for the primary and secondary endpoints. Differences in analysis sets can affect comparability and may reflect outcome availability or analysis-specific criteria, but the reasons are not reported in the registry record. Missing-data methods, sensitivity analyses, and the treatment of participants excluded from the primary analysis are also not reported.

These methods explain how the posted estimates should be understood, but they do not fill gaps in the registry’s statistical record. A full protocol and analysis plan would be needed to establish the planned handling of the non-inferiority margin, multiplicity, missing data, and analysis populations. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary estimate is a difference in mean trough FEV1, and its confidence interval is posted with the results. Both reported interval limits are positive. Under the model and analysis used, the interval therefore supports a positive estimated difference for tiotropium minus indacaterol rather than a difference on either side of zero. The interval is the relevant summary of uncertainty around the estimated contrast; the p-value alone does not show its range or practical size.

The secondary rate-ratio interval is also reported. Its limits are below 1, consistent with the posted estimate favoring a lower rate in the tiotropium group under this comparison. The interval conveys uncertainty in the relative rate, but does not address uncertainty arising from unreported aspects of the analysis, such as the handling of over-dispersion or missing follow-up.

In general, a confidence interval describes values that are reasonably compatible with the observed data and the statistical model. It is not a guarantee that the true effect is inside the interval, nor does it represent the range of individual participant outcomes. Interpretation depends on the model, analysis population, and assumptions used to calculate it. The registry does not report the non-inferiority margin, so the primary interval cannot be checked against the threshold required for a formal non-inferiority conclusion.

Precision and importance are separate. An estimate may be precise while the practical meaning remains uncertain, and an interval that excludes a null value does not by itself show whether an effect is consequential. The posted estimates, intervals, and p-values describe the statistical evidence for these outcomes; they do not settle questions about clinical importance or the completeness of the analysis plan.

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 illustrations based on the observed effects, not the trial’s original design calculations. For these continuous and rate outcomes, the figures are participants per arm, not total events. The illustrations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They show planning for 100%, 75%, and 50% of the observed effect. The registry’s original sample-size assumptions are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a design with an 80% chance of detecting the stated effect, if the planning assumptions and effect size are correct. The 90% power column gives the corresponding number for a 90% chance. These are design probabilities under assumptions, not guarantees for a future study. They do not describe the chance that the observed result is true, nor do they measure the success of this completed trial.

For the primary endpoint, the illustration ranges from 122 participants per arm for planning for 100% of the observed effect to 485 per arm for planning for 50% of that effect at 80% power. At 90% power, the corresponding figures are 163 and 649 participants per arm. For the secondary rate endpoint, the displayed figures likewise increase as the effect to detect becomes a smaller fraction of the observed effect: from 343 to 1,276 participants per arm at 80% power, and from 459 to 1,708 at 90% power.

Smaller effects are harder to distinguish from random variation, so planning for a smaller effect generally requires more participants. These illustrations use the observed effect as their starting point, which may not be the effect a future study should target. This is not observed power: the figures are planning calculations and do not add information about the probability that this trial detected its true effect.

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 = 0.011; pooled standard deviation σ = 0.031.
2. n = 2 × (1.96 + 0.842)² × 0.031² / 0.011² = 121.1, rounded up to 122 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 <- 0.0110000000000001                      # observed difference in means
sigma <- 0.0305527695235221                     # 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(845728)
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 = 122 (80% power), 163 (90% power)
 75% of observed effect: n per arm = 216 (80% power), 289 (90% power)
 50% of observed effect: n per arm = 485 (80% power), 649 (90% power)
power.t.test: 122.1 
Simulated power at n = 122 per arm: 0.795 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates more than one outcome, time point, population, or analysis and then interprets several statistical tests. In general, repeated testing can increase the chance of a result that appears statistically notable even when there is no corresponding effect. Trials may address this through prespecified outcome hierarchies, adjusted significance thresholds, or other procedures. A multiplicity strategy is not reported in the registry record. The primary endpoint and the secondary exacerbation outcome have different roles, but the registry does not explain whether or how their tests were jointly controlled.

The registry posts unadjusted p-values for the primary and secondary comparisons. Those values describe the individual comparisons as posted; they should not be assumed to account for testing across outcomes. No additional reported analyses are listed for the secondary outcome. A full statistical analysis plan, including any planned subgroup or sensitivity analyses and their relationship to the primary test, is not reported in the registry record.

Missing-data procedures are also not reported in the registry record. The registry gives the primary analysis population and endpoint-specific participant counts, but does not explain the reasons for differences in the denominators, the extent or pattern of missing measurements, or how missing data were handled. It does not report sensitivity analyses assessing how alternative assumptions about missing outcomes might affect the results.

The primary analysis population is the Per-Protocol Set for Spirometry, defined as Full Analysis Set patients without major protocol deviations or other specified deviations considered capable of affecting the efficacy analysis. That population is relevant to the stated primary objective, but the registry does not provide a parallel intention-to-treat estimate or explain the effect of exclusions. The secondary outcome has its own reported group sizes, and the criteria for inclusion in that analysis are not reported in the registry record.

These omissions limit independent assessment of the full inferential strategy. They do not change the numerical results that are posted, but they mean the record does not establish how missing data, multiple comparisons, or all analysis populations were handled in the original protocol and analysis plan.

15. 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 1.5% 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 (8.5%), pneumonia (1.7%), lower respiratory tract infection (1.6%), upper respiratory tract infection bacterial (1.0%), viral upper respiratory tract infection (0.7%).

The registry reports serious adverse events affecting 263 of 1721 participants at risk in the indacaterol group and 255 of 1718 at risk in the tiotropium group. It also reports other adverse events affecting 890 of 1721 and 793 of 1718, respectively. These are counts of participants with reported events and participants at risk, not event rates adjusted for exposure time. The registry does not provide a group-specific breakdown of the listed serious adverse-event terms in the information recorded.

The listed serious terms include chronic obstructive pulmonary disease at 8.5%, pneumonia at 1.7%, lower respiratory tract infection at 1.6%, upper respiratory tract infection bacterial at 1.0%, viral upper respiratory tract infection at 0.7%, and dyspnoea at 0.7%. The registry does not specify group assignments for these listed percentages in this summary. Death counts are not reported in the registry record.

These figures describe reported adverse events; they do not by themselves establish that a treatment caused an event or permit a full safety comparison. Definitions, event timing, exposure-adjusted analyses, and additional details on event severity and relatedness are not reported in the registry record. The counts should be interpreted in that limited context.

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

The posted results show a small estimated difference in trough FEV1 at 12 weeks, with the tiotropium group’s least-squares mean higher than the indacaterol group’s. The estimated mean difference is 0.011 liters, and the reported p-value is <0.001. The registry also reports a lower COPD exacerbation rate for tiotropium over 52 weeks than for indacaterol, with a rate ratio below 1 and a p-value of <0.001. These are descriptions of the analyses and outcomes recorded for this trial.

The primary objective was to demonstrate non-inferiority of indacaterol versus tiotropium for trough FEV1. The registry does not report the non-inferiority margin or the complete decision rule. Therefore, the numerical estimate and its statistical significance should not be treated as a complete demonstration that the formal non-inferiority criterion was met. A significant difference from zero and a non-inferiority conclusion answer different statistical questions.

The primary and secondary results also address different outcomes and time frames. FEV1 measures lung function at 12 weeks; the exacerbation endpoint summarizes event rates over 52 weeks. The secondary result does not determine the primary result, and neither outcome alone provides a complete account of benefit, risk, or patient experience. The registry’s adverse-event counts add safety context but are not a causal comparison by themselves.

More generally, a trial estimate is conditional on the population analyzed, the endpoint definition, the statistical model, and how missing observations and multiple outcomes were handled. The primary analysis was in a per-protocol spirometry population, and the registry does not report detailed missing-data or multiplicity methods. These limitations should remain part of the interpretation. The findings describe this randomized trial and its posted analyses; they do not, on their own, determine how results apply to people outside the study population or under other treatment conditions.

17. Why This Trial Matters Statistically

This trial illustrates why the statistical question must be matched to the design objective. The stated primary objective was non-inferiority, yet the registry reports a group difference and an unadjusted p-value without reporting the non-inferiority margin. A conventional test of no difference is not a substitute for evaluating a prespecified non-inferiority threshold. The distinction is central when interpreting trials designed to compare an active treatment with an active comparator.

The record also makes clear that endpoints may answer related but separate questions. Trough FEV1 is a continuous lung-function measure at 12 weeks, while exacerbations are events summarized as a rate over 52 weeks. A favorable-looking result on one scale cannot be assumed to establish the other, and differences in endpoint timing and analysis populations affect interpretation.

Precision is another key statistical issue. Confidence intervals communicate uncertainty more directly than a p-value alone, but they remain conditional on the model and its assumptions. The primary analysis uses a specified mixed model and a per-protocol spirometry population; the rate outcome is described as Poisson-based. The registry does not report enough detail to assess every modeling choice, possible over-dispersion, missing-data strategy, or multiplicity procedure.

Finally, planning illustrations based on observed effects are not evidence of the original design rationale or the trial’s achieved power. Distinguishing those planning calculations from trial-design assumptions prevents the observed results from being mistaken for prospective evidence. Together, these issues show why reading estimates alongside their endpoint definitions, analysis populations, uncertainty, and missing design details is essential to sound interpretation.

18. 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 non-inferiority margin, so the primary objective’s formal decision criterion cannot be independently assessed from the posted estimates alone. It also does not provide the complete protocol or statistical analysis plan. Details of the original sample-size justification, interim analyses, and any multiplicity strategy are not reported in the registry record.

The primary analysis is based on the Per-Protocol Set for Spirometry rather than an explicitly reported intention-to-treat analysis. The record does not describe missing measurements, reasons for the different analysis denominators, missing-data methods, or sensitivity analyses. This makes it difficult to judge how exclusions and incomplete outcome data may have affected the results.

The primary outcome is described as analyzed with a mixed model, including treatment and listed covariates, but further model details are not reported. The exacerbation comparison is described as Poisson-based, but diagnostics and any adjustment for over-dispersion are not reported in the registry record. The posted rate comparison should therefore be interpreted with these methodological details unresolved.

The secondary endpoint has an unadjusted p-value, and the registry does not report how multiplicity was handled. The adverse-event summary gives counts and selected serious-event terms, but does not provide the full context needed for a detailed comparative safety assessment, including death counts. These are limitations of the available registry information, not proof that the underlying trial did not address these issues.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Exacerbation Study — NCT00845728.
• Registry record last updated 2013-11-19; status last verified 2013-09.
• Results first posted 2013-11-19.
• 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.

22. Record Summary

The registry record describes NCT00845728, a completed Phase IIIb randomized, quadruple-masked, double-dummy, parallel-group trial comparing once-daily indacaterol 150 µg with once-daily tiotropium 18 µg in COPD. Overall enrollment was 3439, and treatment was planned for 52 weeks.

The primary endpoint was trough FEV1 at 12 weeks, analyzed in the Per-Protocol Set for Spirometry using a mixed model. The posted least-squares mean difference was 0.011 liters, with p < 0.001. The secondary outcome was COPD exacerbation rate over 52 weeks; the posted rate ratio was 0.772, with p < 0.001. Serious and other adverse-event counts are also reported.

The non-inferiority margin, full statistical analysis plan, multiplicity strategy, and missing-data methods are not reported in the registry record. These omissions limit assessment of the formal primary objective and of several aspects of the analyses.