Efficacy and Safety of Different Doses of Indacaterol in Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Different Doses of Indacaterol in Chronic Obstructive Pulmonary Disease (COPD) (NCT01089127), a randomized phase 3 study. The primary outcome is Trough Forced Expiratory Volume in 1 Second (FEV1) 24 Hours Post-dose at the End of the Study (Week 2 + 1 Day, Day 15).

2. Clinical Question

3. Trial Design

This was a Phase 3 randomized, quadruple-masked, parallel-group study in people with moderate to severe COPD. The official title describes a double-blind, double-dummy, placebo-controlled design and identifies salmeterol as an active control. The registry’s masking classification is quadruple. In a parallel-group design, participants are assigned to one treatment group and outcomes are compared across groups; participants do not switch among the listed treatments as part of the model described in the record.

The study enrolled 552 participants. The registry lists six arms: four once-daily morning indacaterol doses, salmeterol 50 μg twice daily, and placebo. The active treatments and corresponding placebos were delivered using the inhaler schedules described in the arm details. This double-dummy approach means that the treatment groups used matching placebo inhalations for the schedule or inhaler associated with the other treatment. It is intended to help preserve masking when the active regimens differ.

The study status is completed. The registry lists a start of 2010-03 and primary completion of 2010-07. Its brief summary describes comparison of 14-day bronchodilator efficacy for indacaterol against placebo and salmeterol. The primary endpoint was assessed at the end of treatment, specified as 24 hours post-dose at Week 2 + 1 Day (Day 15). A secondary outcome was trough FEV1 24 hours post-dose on Day 2.

The sponsor is Novartis Pharmaceuticals. The registry record does not report the original sample-size justification, the planned allocation ratio, or the detailed sequence-generation and concealment procedures. It also does not report a protocol-level account of interim analyses. Those omissions do not establish that such procedures were absent; they mean that their details are not reported in the registry record.

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: Full analysis set: All randomized patients who received at least 1 dose of study drug, last observation carried forward (LOCF).

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.

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Trough Forced Expiratory Volume in 1 Second (FEV1) 24 Hours Post-dose at the End of the Study (Week 2 + 1 Day, Day 15), measured over 24 hours post-dose at the end of the study (Week 2 + 1 day, Day 15).

The primary endpoint was trough forced expiratory volume in 1 second (FEV1), measured in liters, 24 hours after dosing at the end of the study: Week 2 + 1 Day (Day 15). FEV1 is the volume of air a person can forcibly exhale during the first second of a breath. The registry states that spirometry followed internationally accepted standards. It defines trough FEV1 as the average of measurements taken 23 hours 10 minutes and 23 hours 45 minutes after dosing at the end of treatment.

In general, a trough measurement is intended to describe a response near the end of a dosing interval, rather than soon after a dose. That can help characterize whether a measured effect is present close to the next scheduled dose. This general interpretation does not establish that the measurement captures every aspect of day-to-day lung function or how a participant feels.

The registry reports least-squares means and standard errors for the endpoint. The primary analysis included baseline FEV1 and screening FEV1 measurements before and after salbutamol/albuterol and ipratropium as covariates. In general, adjustment for baseline and other prespecified measurements can account for differences in those variables when estimating group means. The registry record does not report the full model specification or the rationale for selecting these particular covariates.

The analysis population was the full analysis set: randomized participants who received at least one dose of study drug, using last observation carried forward for missing endpoint observations. This outcome is a lung-function measurement, not a direct measure of symptoms, daily functioning, exacerbations, or long-term outcomes.

7. Results Posted in the Registry

• Indacaterol 18.75 μg: mean 1.35 versus 1.28 on control; difference 0.07 (95% CI 0.02 to 0.12), standardized effect d = 0.39; z-test p = 0.011.
• Indacaterol 37.5 μg: mean 1.38 versus 1.28 on control; difference 0.10 (95% CI 0.05 to 0.15), standardized effect d = 0.57; z-test p = <0.001.
• Indacaterol 75 μg: mean 1.38 versus 1.28 on control; difference 0.10 (95% CI 0.05 to 0.15), standardized effect d = 0.57; z-test p = <0.001.
• Indacaterol 150 μg: mean 1.40 versus 1.28 on control; difference 0.12 (95% CI 0.07 to 0.17), standardized effect d = 0.67; 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.

Trough Forced Expiratory Volume in 1 Second (FEV1) 24 Hours Post-dose on Day 2

• 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 18.75 μg: mean 1.33 versus 1.28 on control; difference 0.05 (95% CI 0.01 to 0.09), standardized effect d = 0.36; z-test p = 0.018.
  • Indacaterol 37.5 μg: mean 1.34 versus 1.28 on control; difference 0.06 (95% CI 0.02 to 0.10), standardized effect d = 0.43; z-test p = 0.005.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Indacaterol 18.75 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Indacaterol 37.5 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary outcome: trough FEV1 24 hours post-dose on Day 2. The arm-level summaries follow a pattern broadly consistent with the end-of-treatment endpoint: the active-treatment groups have higher reported means than placebo. This offers an earlier measurement point that complements the primary endpoint assessed at the end of treatment. It does not replace the primary result, because it addresses a different time point.

The secondary outcome summaries report least-squares means and standard errors. Recalculated comparisons against placebo are available for indacaterol 18.75 μg and 37.5 μg, with unadjusted p-values of 0.018 and 0.005, respectively. The record does not list reported analyses for the secondary outcome. These comparisons are therefore summary-statistic recalculations rather than registry-posted sponsor analyses. The secondary arm summaries include other treatment groups as well, but a full set of reported pairwise analyses is not present.

Secondary results can help readers assess whether the general pattern is also present at another time point, but they usually carry less weight than a prespecified primary outcome. One reason is that trials can examine multiple outcomes, time points, and comparisons. Without a reported multiplicity strategy, the chance of at least one apparently notable result across several tests is difficult to assess from separate unadjusted p-values. The registry record does not report an adjustment or testing hierarchy for the secondary outcome.

The evidence should therefore be read as supportive descriptive context rather than as an independent confirmation of the primary comparison. The secondary measurement is also an FEV1 endpoint, so it shares the primary outcome’s general limitations: it is a physiological measure at a defined time point and does not by itself describe symptoms, daily activities, or longer-term events. The record does not report a clinical threshold for interpreting the size of a secondary difference.

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

• Trough Forced Expiratory Volume in 1 Second (FEV1) 24 Hours Post-dose on Day 2

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant’s FEV1 is measured as a volume in liters, and the registry reports group summaries as least-squares means. A continuous measure can take a range of numerical values, unlike an outcome that records only whether an event occurred. The reported group means are adjusted estimates from the registry’s specified analysis, while the standard errors describe uncertainty in those estimated means. The exact fitted model, its assumptions, and its full coefficient output are not reported in the registry record.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based group mean adjusted for covariates included in the analysis. Here, the registry says that the primary analysis included baseline FEV1, screening FEV1 before and after salbutamol/albuterol, and screening FEV1 before and after ipratropium as covariates. This means the posted endpoint summary is not simply identified as an unadjusted arithmetic mean. The record does not provide enough detail to reconstruct the fitted model or to assess how each covariate was coded.

The primary endpoint is defined using the average of two late post-dose measurements, taken 23 hours 10 minutes and 23 hours 45 minutes after dosing at the end of treatment. Both measurements contribute to the registered trough definition. The outcome time point is 24 hours post-dose at Week 2 + 1 Day (Day 15). The secondary outcome is a similar trough FEV1 measurement 24 hours post-dose on Day 2.

How should the reported standard errors be read?

In general, a standard error quantifies the sampling uncertainty of an estimated mean; it is not the spread of individual participant measurements. The primary arm summaries report standard errors between 0.019 and 0.02 liters. The intervals accompanying recalculated comparisons express uncertainty around mean differences. A confidence interval gives a range of values compatible with the data and the method used to construct it; it does not describe the range of individual FEV1 values. The confidence level for the intervals is not reported in the registry record.

The recalculated pairwise differences and intervals are based on posted summary statistics, not a participant-level model refit. The calculation treats the contrast as a simple difference between the treatment-arm and placebo summaries. The pooled standard deviation is marked as approximate because it is derived from the standard errors. This can be useful as a transparent descriptive comparison, but it cannot reproduce adjustments, missing-data handling, or other details of a sponsor analysis that are not available in the posted outcome record.

What does an unadjusted p-value convey?

In general, a p-value describes how unusual data at least as incompatible with a specified null hypothesis would be, if that null hypothesis and the calculation assumptions were correct. It is not the probability that the null hypothesis is true, and it is not a measure of effect size. Here the posted recalculated p-values are unadjusted pairwise values comparing each listed active group with placebo. They do not incorporate a multiplicity adjustment for the several comparisons. The registry record does not report the sponsor’s analysis-level p-values for this endpoint.

The primary comparison estimates are positive, and the recalculated p-values are 0.011 for indacaterol 18.75 μg and <0.001 for each of the other three indacaterol doses and salmeterol. Their interpretation remains conditional on the approximate calculation. The record does not describe a hierarchical testing procedure, a family-wise error strategy, or whether any p-values were intended as confirmatory. Those details are not reported in the registry record.

How were missing endpoint values handled?

The registry identifies the analysis population as randomized participants who received at least one study-drug dose and says that missing observations were handled by last observation carried forward (LOCF). In general, LOCF substitutes a participant’s last recorded value for a later missing value in the analysis. It preserves an analysis record for participants without a value at the target time, but it assumes the carried-forward observation is an adequate representation of the missing measurement. That assumption may not hold if the outcome changes after the last observed measurement. The number of missing endpoint values and the reasons for missingness are not reported in the registry record.

General statistical practice distinguishes the analysis population from the number contributing an observed measurement at a particular time point. The registry’s definition tells readers who could be included in the full analysis set; it does not provide a full participant flow or explain every exclusion and missing observation. The group counts printed with the endpoint summaries should therefore be interpreted as the analysis counts reported for those summaries, not as a complete account of follow-up.

Why can over-dispersion matter?

General explanation: over-dispersion occurs when observed variation is greater than a statistical model expects. It is especially relevant to count outcomes and event-rate models, where extra variation can make ordinary standard errors too small if it is ignored. The primary endpoint in this trial is continuous FEV1 rather than a count. The registry record does not report an over-dispersion model or indicate that over-dispersion was a concern for this endpoint. The general concept should not be taken as evidence that it affected these results.

The registry’s sample-size planning illustrations are separate from the original trial design. They use the observed comparison effect, two-sided significance level 0.05, equal allocation between the two arms, and a normal approximation, with smaller fractions of the observed effect considered as alternative planning targets. These are hypothetical planning calculations, not a description of how the trial’s original enrollment target was chosen. The original design assumptions and sample-size justification are not reported in the registry record.

11. Confidence Intervals and Precision

The recalculated primary contrasts are accompanied by intervals: 0.07 liters for indacaterol 18.75 μg, 0.1 liters for 37.5 μg, 0.1 liters for 75 μg, 0.12 liters for 150 μg, and 0.11 liters for salmeterol, each compared with placebo. The posted interval limits are above zero for all five comparisons. The interval for the 18.75 μg contrast extends closer to zero than the intervals for the other indacaterol contrasts. Exact limits are not repeated; the limits for the recalculated contrasts are available with the posted results.

In general, a confidence interval combines an effect estimate with an indication of its statistical precision. A narrower interval indicates greater precision under the calculation used, while a wider interval indicates more uncertainty about the size of the contrast. An interval is not a range that contains a fixed proportion of individual participant outcomes, and it does not establish the probability that a particular effect value is true. The confidence level used for the posted intervals is not reported in the registry record.

These intervals accompany simple, unadjusted recalculations from summary statistics. The calculation uses an approximate pooled standard deviation based on reported standard errors. The resulting precision therefore depends on that approximation and should not be treated as a replacement for a participant-level adjusted analysis. The registry provides standard errors for the least-squares means, but it does not report sponsor-generated intervals for the primary pairwise contrasts.

The group standard errors are similar in size, from 0.019 to 0.02 liters. Similar standard errors do not imply identical participant-level variation, and standard errors should not be interpreted as standard deviations. No clinical-importance threshold is reported, so the intervals alone cannot establish whether the contrasts are large enough to matter clinically. They describe statistical uncertainty around the calculated mean differences, subject to the limitations of the available summaries and method.

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 illustrations express the number of participants per arm for 80% power and the number of participants per arm for 90% power. These are not total event counts. The calculations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. They use the observed effect as the starting point and also consider planning for 75% and 50% of the observed effect. The original trial’s own design assumptions and sample-size justification are not reported in the registry record.

In general, power is the chance that a planned study will detect an effect of a stated size under the assumptions used for planning, if that effect is present. The 80% column gives the estimated participants per arm for a design with 80% power to detect the specified planning effect; the 90% column gives the corresponding estimate for 90% power. The calculations concern a two-group comparison, not a new estimate of the trial’s observed result.

For example, planning for 100% of the observed indacaterol 18.75 μg effect gives 103 participants per arm for 80% power and 137 for 90% power. Planning for 50% of that observed effect gives 409 participants per arm for 80% power and 548 for 90% power. This illustrates the general pattern: smaller effects are harder to detect and require more participants under the same assumptions. The other comparisons have their own planning illustrations, because their observed effects differ.

These figures are planning illustrations based on the observed effects, not observed power. They should not be read as proof that the completed trial had a particular probability of success, nor as evidence that its original design was based on these calculations. The registry record does not report the original sample-size rationale, assumed effect, target power, or planned handling of multiple comparisons.

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 = 0.070; pooled standard deviation σ = 0.179.
2. n = 2 × (1.96 + 0.842)² × 0.179² / 0.070² = 102.2, rounded up to 103 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 <- 0.0700000000000001                      # observed difference in means
sigma <- 0.178610938830407                     # 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(1089127)
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 = 103 (80% power), 137 (90% power)
 75% of observed effect: n per arm = 182 (80% power), 244 (90% power)
 50% of observed effect: n per arm = 409 (80% power), 548 (90% power)
power.t.test: 103.2 
Simulated power at n = 103 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. Multiplicity, Missing Data and Analysis Populations

The primary results involve several active-treatment comparisons with the same placebo group. The posted recalculated p-values are unadjusted. In general, testing several comparisons without an adjustment can increase the chance of at least one small p-value arising by chance across the family of tests. A multiplicity procedure may control that risk or specify an order in which hypotheses are tested, but the registry record does not report such a procedure for the primary or secondary comparisons.

The registry reports two outcome measures overall: the primary end-of-treatment trough FEV1 and the secondary Day 2 trough FEV1. It lists no reported analyses for either outcome. Thus, the available pairwise p-values and intervals are recalculations from posted summary statistics, not a complete account of a prespecified sponsor analysis plan. The registry record does not report whether the original analysis plan included additional outcomes, subgroup analyses, interim analyses, or a particular multiplicity adjustment.

The primary outcome population is the full analysis set, defined as all randomized patients who received at least one dose of study drug. The analysis used LOCF for missing values. In general, an analysis population determines which participants contribute to the estimate, while a missing-data method determines how an unavailable outcome is handled. The record does not report the number of missing primary measurements, the reasons they were missing, or sensitivity analyses using alternative missing-data assumptions.

LOCF can be convenient, but in general it treats the last observed value as a stand-in for the later missing value. If the underlying outcome changes after that observation, the substitute may misrepresent the target-time value. The registry information does not establish whether missingness depended on participants’ health or treatment, and it does not describe checks of the LOCF assumption. A reader therefore cannot assess the potential direction or extent of missing-data bias from this record alone.

Finally, the record’s sample-size illustrations use post hoc observed effects, whereas the original design assumptions are not reported in the registry record. These calculations do not answer whether the trial was planned to accommodate its set of comparisons or whether the final analysis followed an original protocol-defined testing strategy. Those details remain unreported.

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 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: myocardial infarction (1.1%), oesophageal obstruction (1.1%), blood potassium increased (1.1%), chronic obstructive pulmonary disease (1.1%), anaemia (1.1%).

The registry reports serious adverse events by treatment group as the number affected and the number at risk. The reported counts are 1 among 89 for indacaterol 18.75 μg, 0 among 90 for 37.5 μg, 0 among 94 for 75 μg, 1 among 92 for 150 μg, 0 among 91 for salmeterol 50 μg, and 3 among 91 for placebo. These figures describe the posted serious adverse event counts; they do not establish that an event was caused by study treatment.

The registry also reports other adverse events: 1 among 89, 7 among 90, 8 among 94, 2 among 92, 4 among 91, and 9 among 91 in the same respective group order. The listed terms reported as serious events include myocardial infarction, oesophageal obstruction, increased blood potassium, COPD, and anaemia, each reported at 1.1%. The registry’s deaths field has no counts; deaths are not reported in the registry record.

In general, adverse-event counts should be interpreted alongside how events were defined, collected, and followed, and with attention to the number at risk in each group. Those detailed methods and the duration of safety follow-up are not reported in the registry record. The counts alone do not establish comparative safety or causal attribution.

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

The primary endpoint results describe adjusted group means for trough FEV1 at the end of treatment. Each indacaterol group had a higher reported mean than placebo, and the recalculated mean differences were positive. The salmeterol group also had a higher reported mean than placebo. These findings characterize the posted measurements at this endpoint and time point; they do not show how every participant’s lung function changed or how participants experienced treatment.

The comparisons are against placebo. They do not directly test whether one indacaterol dose is better than another, or whether indacaterol differs from salmeterol. Similar group means are not proof of equivalence, and a positive mean difference in a placebo comparison does not establish superiority over an active comparator. Those questions would require appropriate direct comparisons and analyses, which are not reported in the registry record.

Statistical evidence and clinical importance are distinct. The recalculated p-values describe compatibility with a null comparison under the calculation’s assumptions, while the mean differences and intervals describe estimated size and precision. The record does not report a threshold for a clinically important FEV1 difference, and it does not provide participant-level distributions or clinical outcomes that would establish the practical meaning of the observed contrasts.

The endpoint was measured at a defined time point after a short treatment period described as 14 days. It cannot, by itself, establish whether a difference persists with longer use, whether it affects symptoms or daily functioning, or whether it changes exacerbation risk or other later outcomes. The registry record does not report those outcomes in the posted results.

Likewise, the adverse-event counts should not be read as causal conclusions or as a complete comparison of harms. The registry reports counts, but details about event ascertainment and safety follow-up are not reported in the registry record. The appropriate interpretation is limited to the posted lung-function summaries and adverse-event counts, with the uncertainty and analysis limitations stated alongside them.

17. Why This Trial Matters Statistically

This trial is statistically informative because it compares several doses of an inhaled treatment with both placebo and an active control, using a randomized parallel-group design. The double-dummy arrangement described in the record reflects a practical design issue: the active treatments used different dosing schedules, so matching placebo inhalations supported masking. The registry labels masking as quadruple, while the official title describes the study as double-blind and double-dummy.

The endpoint also illustrates why analysis details matter. The registry reports covariate-adjusted least-squares means, while the pairwise comparisons discussed with them are approximate, unadjusted recalculations from summary statistics. Those quantities answer related but not identical statistical questions. Distinguishing them helps avoid treating an approximate reconstruction as if it were the trial’s original model-based analysis.

The multiple dose groups create a useful descriptive picture of the endpoint across dose levels, but the posted comparisons are principally against placebo. Without a reported multiplicity strategy, unadjusted tests should not be read as a family-wise confirmatory set. The registry also does not report direct tests between the active treatment groups, so the mean pattern alone cannot establish a dose-to-dose difference.

Finally, the study demonstrates the difference between a measured physiological endpoint and broader clinical outcomes. Trough FEV1 is a defined spirometric measure near the end of a dosing interval, and the record gives a clear measurement definition. Its statistical interpretation does not automatically translate into conclusions about symptoms, longer-term outcomes, or individual benefit. The endpoint, analysis population, missing-data method, interval precision, and multiplicity context all shape what can responsibly be inferred.

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 offers limited information for evaluating the original analysis plan. The original sample-size justification, anticipated effect, planned power, and planned allocation ratio are not reported in the registry record. The sample-size illustrations based on observed effects do not fill that gap. The record also does not report the full statistical model, all model diagnostics, or a sponsor-reported analysis of the primary contrasts.

The pairwise comparisons are approximate recalculations from summary statistics. Their pooled standard deviations are approximate, and the calculations are unadjusted. They cannot reproduce a participant-level analysis that accounts for covariates or the original missing-data approach. The registry lists no reported analyses for the primary or secondary outcome, and the confidence level for the intervals is not reported in the registry record.

LOCF was used for the primary endpoint, but the number and reasons for missing measurements are not reported. The record does not provide sensitivity analyses showing whether conclusions change under other assumptions about missing outcomes. A full participant flow and detailed outcome-specific analysis counts are also not reported in the registry record.

Multiplicity is another limitation: several active groups are compared with placebo, yet no testing hierarchy or adjustment is reported. Direct comparisons among active groups are not posted. The secondary outcome is at an earlier time point, but its analyses are not reported in full. Clinical-importance thresholds and participant-level outcome distributions are also not reported.

For safety, the record includes serious and other adverse-event counts, but detailed collection methods and follow-up duration are not reported. Death counts are not reported in the registry record. These limitations constrain precision, reproducibility, and the scope of interpretation; they do not by themselves show that the underlying trial procedures were inadequate.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Different Doses of Indacaterol in Chronic Obstructive Pulmonary Disease (COPD) — NCT01089127.
• Registry record last updated 2011-08-19; status last verified 2011-07.
• Results first posted 2011-08-19.
• 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

NCT01089127 is a completed Phase 3 randomized, quadruple-masked, parallel-group study of indacaterol doses in moderate to severe COPD, with salmeterol 50 μg and placebo as comparators. The registry lists enrollment of 552 and dates of 2010-03 for study start and 2010-07 for primary completion.

The primary outcome was trough FEV1 in liters 24 hours post-dose at Week 2 + 1 Day (Day 15), summarized as least-squares means with standard errors in a full analysis set using LOCF. The registry also lists Day 2 trough FEV1 as a secondary outcome. Posted arm means were higher in each active-treatment group than in placebo, while the pairwise estimates discussed are approximate unadjusted recalculations rather than reported sponsor analyses.

The record does not report the original sample-size rationale, a multiplicity strategy, the full statistical model, or missing-data sensitivity analyses. Serious and other adverse-event counts are posted; deaths are not reported in the registry record.