The Effect of Indacaterol on Exercise Endurance in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The Effect of Indacaterol on Exercise Endurance in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (NCT00620022), a randomized phase 3 study. The primary outcome is Exercise Duration Time Assessed by Constant-load Cycle Ergometry at the End of Each Treatment Period.

2. Clinical Question

The study was a Phase III trial with randomized allocation and a crossover model. Its registered enrollment was 90. The clinical question is therefore about a short-term, within-trial comparison of exercise endurance under the two treatment conditions in the enrolled COPD population. It is not a comparison of long-term outcomes, nor does the posted endpoint directly measure every aspect of daily function or disease burden. The registry record does not report a broader claim about how the result should guide care.

3. Trial Design

The registry describes a Phase III, randomized, quadruple-masked, placebo-controlled, multicenter crossover study of indacaterol 300 μg once daily. The study status is completed. The recorded start was 2008-04, and primary completion was 2009-01. Registered enrollment was 90. These details describe the trial as recorded; they do not establish how many participants contributed data to every outcome analysis.

Participants were assigned to treatment sequences. One sequence received indacaterol for 3 weeks, followed by a 3-week washout, then placebo for 3 weeks. The other sequence received placebo first and indacaterol after the washout. Both treatments were delivered in the morning using a single dose dry powder inhaler. The record also notes daily inhaled corticosteroid treatment if applicable, but the available arm descriptions end mid-sentence, so additional details about that treatment are not reported in the registry record.

The primary measure was assessed at the end of each 3-week treatment period, on the last day of Weeks 3 and 9. In this crossover arrangement, each participant could contribute measurements under both treatments, subject to availability and the analysis-population definition. The registry says the reported outcome analysis used a mixed model, but detailed model specifications—including how treatment sequence, period, or within-participant correlation were handled—are not reported in the registry record.

The registry also lists inspiratory capacity at rest as a secondary outcome and includes adverse-event summaries. These outcomes have different measurements and analysis counts, so their denominators should not be assumed to match the primary endpoint. The record does not report the original design assumptions used to determine enrollment, nor does it provide a detailed protocol-level account of allocation procedures or masking implementation.

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.

Treatment Period 1

Reasons for not completing this period:

Treatment Period 2

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Modified intent-to-treat (modified ITT) population: All randomized patients who received at least 1 dose of study drug. The number of patients analyzed for each treatment group was the number with non-missing values for the dependent and independent variables in the mixed model.

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 Exercise Duration Time Assessed by Constant-load Cycle Ergometry at the End of Each Treatment Period, measured over End of each 3 week treatment period (last day of Weeks 3 and 9).

The primary endpoint is exercise duration time, measured in seconds by constant-load cycle ergometry at the end of each treatment period. At screening, each participant’s Wmax was determined; the exercise test then used a work-rate of 75% of that value. The workload was maintained until symptom limitation caused the participant to stop. Duration was measured from the start of loaded pedaling to stopping.

This endpoint captures how long a participant can continue a standardized exercise test at the specified workload. It is a continuous measure, so the registry reports least-squares means for the treatment groups and a mean difference for the comparison. A longer recorded duration represents more time completed on this particular test; it should not be treated as a direct measurement of every kind of exercise in daily life.

Measuring at the end of each treatment period allows the posted comparison to relate exercise duration to each treatment condition in the crossover study. The registry’s stated timeframe is the last day of Weeks 3 and 9. The measure is therefore tied to the end of the treatment periods, rather than a long-term follow-up outcome. The registry record does not report a threshold that would define a clinically important change in exercise duration, so the statistical estimate alone does not establish how meaningful a difference would be to an individual patient.

7. Results Posted in the Registry

• Indacaterol 300 μg: mean 586.00 versus 475.00 on control; difference 111.00 (95% CI 25.62 to 196.38), standardized effect d = 0.41; z-test p = 0.011.

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.

Inspiratory Capacity (IC) Assessed at Rest With Spirometry at the End of Each Treatment Period 60 Minutes Pre-dose

• 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:
  • Indacaterol 300 μg: mean 2.39 versus 2.25 on control; difference 0.14 (95% CI 0.05 to 0.23), standardized effect d = 0.47; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Indacaterol 300 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists inspiratory capacity at rest, assessed by spirometry at the end of each treatment period, as a secondary endpoint. Its posted estimated contrast is positive for indacaterol relative to placebo, in the same general direction as the primary exercise-duration estimate. The two measures capture different aspects of lung function and exercise performance, so agreement in direction is contextual rather than proof that they measure the same effect.

The secondary finding can add descriptive context to the primary result, but it should not be treated as a separate, definitive confirmation. Multiple outcomes create multiple opportunities to observe apparently notable results by chance. In general, a prespecified multiplicity strategy can control how such results are interpreted; the registry record does not report an adjustment, a testing hierarchy, or another multiplicity procedure. The secondary comparison’s p-value is therefore unadjusted, and its evidential weight is more limited than it would be under a clearly stated confirmatory plan.

The analysis counts for the secondary outcome do not exactly match the primary outcome counts for each treatment. That can arise because outcome availability and model-variable completeness differ by endpoint, but the registry does not report the reasons for the observed counts or how missing values were handled. The counts should be read as analysis-specific rather than assumed to represent the same set of measurements for every outcome.

The registry lists two outcome measures and reports no separate analysis records. This does not mean that no statistical comparisons are posted: estimates and unadjusted p-values are available for the primary and secondary results. It means the record does not provide a fuller inventory of analysis plans or reported analyses from which to establish whether the posted secondary analysis was prespecified, exploratory, or selected after examining the data. That uncertainty is another reason to treat the secondary result as supportive description, not as a stand-alone conclusion.

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

• Inspiratory Capacity (IC) Assessed at Rest With Spirometry at the End of Each Treatment Period 60 Minutes Pre-dose

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes as least-squares means with standard errors. The primary endpoint, exercise duration, is a continuous measure in seconds. A least-squares mean is a model-based estimate of a group mean; it can differ from a simple arithmetic average when the analysis model accounts for design features or other variables. The record names a mixed model for the primary analysis, but does not provide enough detail to identify every term or assumption in that model.

What does the mean difference represent?

The reported mean difference compares the estimated treatment means, with the contrast defined as indacaterol relative to placebo. For the primary endpoint, the reported estimate is 111.0 seconds. A positive contrast means the estimated exercise duration is higher under indacaterol in the posted comparison. The estimate is a summary of the modeled treatment contrast, not a statement that every participant experienced the same change. In a crossover trial, treatment observations can be linked within a participant; the registry does not report the covariance information or full model output needed to independently reproduce that contrast.

How should the standard errors be read?

The standard errors reported alongside the treatment means describe the estimated sampling uncertainty of those means under the model. They are not standard deviations of individual participants’ exercise durations. A standard deviation describes variation among observations, while a standard error describes uncertainty in an estimate. The primary treatment means have reported standard errors of 30.3 seconds for indacaterol and 31.3 seconds for placebo. The registry does not provide raw observations or the full variance structure, so these summaries cannot show the distribution of individual responses.

What does the confidence interval add?

A confidence interval expresses uncertainty around an estimated contrast by giving a range of values compatible with the data and analysis under its statistical assumptions. For the primary mean difference, the reported interval runs from 25.62 to 196.4 seconds. It conveys more about precision than the point estimate alone: values across that range are not equally likely, but the interval shows that the precise magnitude is uncertain. The registry record does not state the confidence level, so it should not be inferred from convention.

What does the p-value tell the reader?

The unadjusted p-value for the primary comparison is 0.011. In general, a p-value describes how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is correct, and it does not measure clinical importance. It also does not account for multiple testing unless an adjustment is made. The record does not report whether the primary test was adjusted or how it fit into any prespecified testing sequence; the posted value is identified as unadjusted.

Why does the crossover structure matter?

In general, crossover designs compare treatments within participants, which can reduce the influence of stable differences between participants when the analysis appropriately models the design. They also require attention to treatment sequence, period, and possible carryover effects. The washout period is part of the recorded design, but its presence alone does not demonstrate that carryover was absent. The registry says a mixed model was used, yet the exact model terms, assumptions, and diagnostic checks are not reported in the registry record. No claim about how these issues were resolved should be inferred from the summary statistics alone.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation is greater than a model assumes. When a model underestimates variability, standard errors can be too small and intervals too narrow; when variability is represented adequately, uncertainty estimates are more credible. The posted outcomes are continuous, and the registry does not report an over-dispersion assessment. This concept is relevant as a general reminder to check whether the model’s variance assumptions fit the data, not as a finding that over-dispersion occurred in this trial.

The primary outcome description defines the modified intent-to-treat population as randomized patients who received at least one dose. It further says that the number analyzed for each treatment was based on non-missing dependent and independent variables in the mixed model. This clarifies why analysis counts can differ by treatment and from enrollment, but it does not describe the missingness mechanism, imputation, or sensitivity analyses. Those details are not reported in the registry record.

11. Confidence Intervals and Precision

The primary estimated mean difference is 111.0 seconds, and its reported confidence interval extends from 25.62 to 196.4 seconds. Because the interval does not include zero, the reported range is in the positive direction. The width of the interval also shows that the point estimate should not be treated as exact: the result remains compatible with a span of possible mean differences under the analysis. The confidence level is not reported in the registry record, so the interval should not be labeled with a confidence percentage that the record does not state.

Precision is different from clinical importance. A narrow interval would indicate less statistical uncertainty about the estimated contrast, but would not by itself establish that the effect matters to patients. A wide interval signals greater uncertainty in the magnitude, but does not necessarily mean that the underlying measure is uninformative. The registry does not report a minimally important difference or another threshold for interpreting the size of the exercise-duration contrast.

The reported standard errors for the least-squares means are 30.3 seconds for indacaterol and 31.3 seconds for placebo. These quantify uncertainty in the estimated means under the analysis, rather than the spread of individual exercise times. The mixed-model approach and crossover structure may affect how uncertainty is estimated, but the detailed model specification and covariance assumptions are not reported in the registry record.

The secondary inspiratory-capacity comparison also has a reported interval, from 0.046 to 0.234 liters around a mean difference of 0.14 liters. Its precision and inferential interpretation should be considered in light of its secondary status and the absence of a reported multiplicity plan. Neither interval should be read as a guarantee that future estimates will fall inside its bounds; it describes uncertainty for the estimate in this study under the analysis assumptions.

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 figures are planning illustrations based on the observed effect, not the trial’s original enrollment calculation. They are expressed as participants per arm for 80% power and participants per arm for 90% power; they are not total event counts. The registry’s planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect.

For example, the row planning for 75% of the observed effect gives the per-arm requirements under the 80% and 90% power columns. The 80% power column represents the number of participants per arm in the planning calculation when the assumed effect and other listed assumptions apply; the 90% column uses a higher target probability of detecting that effect under those assumptions. These are design-planning quantities, not estimates of what happened during the completed trial.

The table and curve should be read as illustrating how requirements change when the target effect changes. Smaller effects need more participants to distinguish them from random variation at a given power target and significance level. The listed calculations are based on the observed effect and fractions of it, rather than a clinical threshold reported in the registry. This is not observed power: it does not measure the probability that the completed trial detected its actual effect, and it does not replace the confidence interval for interpreting the observed estimate.

These illustrations use an equal-allocation, two-arm planning setup. The trial itself is described as a crossover study, and the original design assumptions, including any assumptions used to select enrollment, are not reported in the registry record. Therefore, the planning figures should not be treated as a reconstruction of the trial’s own sample-size rationale or as a direct restatement of its crossover design.

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 = 111.000; pooled standard deviation σ = 267.518.
2. n = 2 × (1.96 + 0.842)² × 267.518² / 111.000² = 91.2, rounded up to 92 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 <- 111                      # observed difference in means
sigma <- 267.517786901591                     # 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(620022)
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 = 92 (80% power), 123 (90% power)
 75% of observed effect: n per arm = 163 (80% power), 218 (90% power)
 50% of observed effect: n per arm = 365 (80% power), 489 (90% power)
power.t.test: 92.1 
Simulated power at n = 92 per arm: 0.802 (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 more than one outcome, comparison, time point, or analysis is tested. In general, testing several hypotheses without a plan can increase the chance that at least one result appears unusual by chance. A prespecified hierarchy, adjusted significance procedure, or clear distinction between confirmatory and exploratory outcomes can help readers understand how to weigh multiple results. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a detailed statistical plan for interpreting the primary and secondary outcomes.

The primary result is reported with an unadjusted p-value, and the secondary comparison also has an unadjusted p-value. The presence of both results does not establish whether the study’s original protocol treated the secondary endpoint as confirmatory or exploratory. The registry record does not report the trial’s prespecified analysis plan, interim analyses, or sample-size justification. No assumptions about these elements should be inferred from the outcome summaries.

The primary analysis population is defined as randomized patients who received at least one dose of study drug. For each treatment, the number analyzed was the number with non-missing values for the dependent and independent variables in the mixed model. This definition gives useful information about eligibility for the analysis, but it does not explain why values were missing, whether missingness differed by treatment or period, or whether any imputation or sensitivity analysis was used. Those details are not reported in the registry record.

Different endpoints have different analysis counts: the primary exercise-duration outcome and the secondary inspiratory-capacity outcome do not have identical treatment-specific counts. That variation makes it especially important not to assume a common analysis population across outcomes. The record does not provide participant flow by sequence, reasons for exclusion, or a comparison of included and excluded participants. These omissions limit assessment of the potential effects of missing outcome data.

The crossover structure also raises design-specific questions about period effects, sequence effects, and carryover. A washout period is recorded, but the registry does not report model terms, tests, or sensitivity analyses addressing those issues. The use of a mixed model is stated for the primary outcome, yet its full specification is not available. These missing details do not establish that the analysis was inappropriate; they define what cannot be evaluated from the registry record.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: femur fracture (1.2%), road traffic accident (1.2%), breast cancer (1.2%), chronic obstructive pulmonary disease (1.2%), angina pectoris (1.2%).

The serious adverse-event summary reports 3 affected participants among 83 at risk in the indacaterol group and 1 among 84 at risk in the placebo group. These are group-specific registry counts. They should be read alongside the stated at-risk denominators, not as estimates of an overall risk difference or as a complete account of event severity, timing, or relatedness. The registry record does not report deaths for these groups.

The other, non-serious adverse-event summary reports 6 affected participants among 83 at risk with indacaterol and 10 among 84 at risk with placebo. These counts are separate from the serious-event counts and should not be combined. The record lists Femur fracture, Road traffic accident, Breast cancer, Chronic obstructive pulmonary disease, and Angina pectoris among the top serious-event terms, each at 1.2%. The posted term percentages do not, by themselves, establish which treatment group each event occurred in or whether an event was judged related to treatment.

Safety summaries are descriptive. Differences in counts do not establish a cause, and the registry information does not provide enough detail to assess event timing, exposure-adjusted rates, or statistical uncertainty. The at-risk groups for safety also differ from the primary outcome analysis counts, reflecting that these are separate summaries with their own denominators.

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

The result describes a short-term comparison of exercise duration under indacaterol and placebo in a randomized crossover trial among patients with moderate to severe COPD. The posted primary estimate favors longer exercise duration during the indacaterol condition, with a mean difference of 111.0 seconds and a confidence interval from 25.62 to 196.4 seconds. It is evidence about the measured cycle-ergometry outcome under the trial’s recorded conditions, not a direct measure of every activity or outcome that may matter to patients.

The point estimate is not the same as a uniform response. Group-level least-squares means do not show how individual participants varied, how many improved or worsened, or how the contrast differed across patient characteristics. The registry does not provide participant-level results or subgroup analyses for this outcome. The interval conveys uncertainty in the estimated mean contrast, while the absent confidence level and incomplete model detail limit how fully its statistical properties can be assessed.

The posted result does not establish a clinically important difference because the registry record does not state a threshold for interpreting exercise-duration changes. Nor does it establish durability beyond the short treatment periods, effects on outcomes not measured in the registry, or applicability to populations not described in the study. A secondary measure may offer additional context, but the missing multiplicity plan means its unadjusted result should not be treated as equivalent to a separately confirmed primary finding.

The result also does not settle questions about safety. The adverse-event counts are descriptive, and the registry does not report deaths for the treatment groups. It does not provide the event-level detail needed to determine timing, relatedness, or comparative risk with precision. Statistical results should be kept separate from medical advice: this record presents trial estimates and limitations, not an individual treatment recommendation.

17. Why This Trial Matters Statistically

This trial illustrates how a crossover design changes the interpretation of a treatment comparison. Participants were assigned to sequences and received both indacaterol and placebo, separated by a washout period. Such a design can make within-participant comparisons informative, but understanding the estimate depends on the model’s treatment of period, sequence, and correlation between measurements. The registry identifies a mixed model but does not report its full specification, leaving important analytical details unresolved.

The endpoint also shows the distinction between an outcome definition and its broader meaning. Exercise duration was measured under a standardized cycle-ergometry workload and recorded in seconds. That offers a concrete continuous measure, but it is not interchangeable with everyday function or an overall assessment of COPD. The estimated mean difference and interval therefore need to be interpreted in relation to the task measured, rather than generalized automatically.

The record highlights how treatment-specific counts can differ across analyses. The modified intent-to-treat definition requires treatment exposure and non-missing model variables, and the primary and secondary outcomes have different analysis counts. Registered enrollment cannot substitute for the number contributing to a particular result. Without a detailed participant flow or missing-data analysis, readers cannot determine why those counts vary.

Finally, the posted unadjusted comparisons illustrate why statistical interpretation requires more than a point estimate or p-value. Confidence intervals express uncertainty in magnitude; p-values do not quantify clinical importance; and multiple outcomes complicate the interpretation of unadjusted tests. The registry does not report the original analysis plan, multiplicity strategy, or design assumptions for enrollment. Those omissions are not evidence that the study lacked such plans, but they limit what can be verified from the record.

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 leaves several trial-specific details unavailable. It identifies a mixed model for the primary outcome but does not report its full specification, including how the crossover structure, period, sequence, or within-participant dependence were modeled. The washout period is described, but the record does not report an assessment of possible carryover or related sensitivity analyses. These gaps prevent a full evaluation of the modeling choices from the posted summary alone.

The confidence level for the reported confidence intervals is not stated. The registry also does not report the original sample-size justification or the assumptions used to plan the trial. The planning illustrations based on the observed effect do not fill that gap; they are not a reconstruction of the original design process. No conclusion about the trial’s intended power or analysis assumptions can be drawn from those illustrations.

Missing-data handling is another limitation. The primary population definition requires non-missing values for model variables, but the record does not describe the amount or pattern of missingness, its reasons, any imputation, or sensitivity analyses. The outcome-specific analysis counts differ, and no participant flow by treatment sequence is reported. Consequently, the extent to which missing data may have influenced the estimates cannot be assessed from the registry record.

The record does not describe multiplicity control, a hierarchy of endpoints, or whether the secondary result was confirmatory. It also does not state a clinically important threshold for the primary measure. The safety summary lacks event timing and relatedness details, and the deaths field is not populated with a count. Finally, the available arm descriptions are truncated after mentioning daily inhaled corticosteroid treatment if applicable, so further details about that aspect of the treatment context are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: The Effect of Indacaterol on Exercise Endurance in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease — NCT00620022.
• Registry record last updated 2011-08-17; status last verified 2011-07.
• Results first posted 2011-08-17.
• 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

NCT00620022 is a completed Phase III randomized, quadruple-masked, placebo-controlled crossover study sponsored by Novartis. It enrolled 90 patients with moderate to severe COPD and compared indacaterol 300 μg once daily with placebo in treatment sequences separated by a 3-week washout.

The primary endpoint was exercise duration on constant-load cycle ergometry at the end of each treatment period. The registry reports a positive mean difference for indacaterol relative to placebo, with a confidence interval and an unadjusted p-value. Inspiratory capacity is listed as a secondary outcome, and adverse events are summarized separately.

The record does not report the full mixed-model specification, original sample-size justification, multiplicity plan, or detailed missing-data analyses. These omissions limit assessment of the posted results beyond the outcome definitions and summary statistics recorded.