Efficacy and Safety of Indacaterol in Patients With Chronic Obstructive Pulmonary Disease (COPD) Using Salmeterol as Active Control: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Indacaterol in Patients With Chronic Obstructive Pulmonary Disease (COPD) Using Salmeterol as Active Control (NCT00567996), a randomized phase 3 study. The primary outcome is Trough Forced Expiratory Volume in 1 Second (FEV1) After 12 Weeks of Treatment.

2. Clinical Question

3. Trial Design

The registry identifies NCT00567996 as a completed phase 3 trial sponsored by Novartis. It describes a randomized, triple-masked, parallel-group study with a planned treatment period of 26 weeks. The title also describes the study as multi-center, double-blind, double-dummy and placebo-controlled, with salmeterol as an active control. The registry lists enrollment as 1002. The treatment groups were indacaterol 150 μg, salmeterol 50 μg and placebo.

Indacaterol was given once daily in the morning. Salmeterol was given twice daily, in the morning and evening. The placebo regimen used matching inhaler schedules. Daily inhaled corticosteroid treatment, if applicable, was allowed to remain stable according to the arm descriptions. The registry gives the study start as 2007-11 and primary completion as 2009-01.

The primary outcome was trough FEV1 at week 12. The posted primary results include 320 participants in the indacaterol group, 317 in the salmeterol group and 316 in the placebo group. These are the group counts associated with the posted endpoint results, not a replacement for the registry enrollment figure. The registry says the endpoint analysis included only participants with week 12 trough FEV1 data, with missing data imputed using LOCF. Secondary outcomes were SGRQ total score after 12 weeks and the percentage of COPD days of poor control during 26 weeks.

The registry record does not report the original sample-size justification, the planned statistical analysis protocol, or the trial's original assumptions about power and significance testing. The planning illustrations are separate calculations based on posted effect estimates and should not be read as the trial's own design rationale.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 1002 participants were randomized. 3 randomized participants in the Indacaterol group and 1 randomized participant in the Salmeterol group did not receive study medication and were not included in the intent-to-treat milestone.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat population included all randomized participants who received at least one dose of study medication. The end point was analyzed only for those participants who had Trough FEV1 data at week 12. Missing data were imputed using 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.

6. Primary Endpoint

The registry lists the primary outcome as Trough Forced Expiratory Volume in 1 Second (FEV1) After 12 Weeks of Treatment, measured over Week 12.

Trough FEV1 is the amount of air a participant can forcefully exhale in the first second of an expiration, measured at the end of the interval before a subsequent dose. The registry defines this endpoint as the average of FEV1 readings taken 23 hour 10 minute and 23 hour 45 minute post-dose. It is expressed in liters and was assessed at week 12. Measuring at this trough point is intended to characterize lung function near the end of the dosing interval rather than shortly after inhalation.

The registry says spirometry followed internationally accepted standards. The outcome is reported as a least-squares mean, an adjusted group mean from the described mixed model. That model used baseline FEV1 and specified pre- and post-inhalation lung-function measures as covariates. The endpoint therefore represents a model-based comparison that accounts for those measured variables, rather than a simple raw average of the observed readings.

FEV1 is a continuous measurement, so the group summaries and comparisons retain its original unit, liters. A mean difference describes the estimated separation between a treatment group's adjusted mean and the placebo group's adjusted mean. The measure is useful for comparing average lung-function values across randomized groups, but an average does not show the range of individual responses or how many participants experienced any particular change. The registry record does not report a threshold for interpreting the size of an individual change as clinically important.

7. Results Posted in the Registry

• Indacaterol 150 μg: mean 1.45 versus 1.28 on control; difference 0.17 (95% CI 0.12 to 0.22), standardized effect d = 0.52; z-test p = <0.001.
• Salmeterol 50 μg: mean 1.39 versus 1.28 on control; difference 0.11 (95% CI 0.06 to 0.16), standardized effect d = 0.33; 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.

St. George's Respiratory Questionnaire (SGRQ) Total Score After 12 Weeks of Treatment

• 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 150 μg: mean 36.40 versus 42.60 on control; difference -6.20 (95% CI -9.10 to -3.30), standardized effect d = -0.34; z-test p = <0.001.
  • Salmeterol 50 μg: mean 38.50 versus 42.60 on control; difference -4.10 (95% CI -7.00 to -1.20), standardized effect d = -0.23; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Indacaterol 150 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 lower for Salmeterol 50 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of COPD "Days of Poor Control" During 26 Weeks of Treatment

• 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 150 μg: mean 34.10 versus 38.10 on control; difference -4.00 (95% CI -9.09 to 1.09), standardized effect d = -0.12; z-test p = 0.123.
  • Salmeterol 50 μg: mean 34.10 versus 38.10 on control; difference -4.00 (95% CI -9.09 to 1.09), standardized effect d = -0.12; z-test p = 0.123.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol 150 μg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Salmeterol 50 μg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes address two different dimensions from the primary lung-function measure: SGRQ total score after 12 weeks and the percentage of COPD days of poor control during 26 weeks. Considering them together with the primary result provides a broader view of what was measured, but they are not interchangeable outcomes. A difference in a questionnaire score or in reported days of poor control would not directly quantify the same construct as trough FEV1.

Overall, the posted SGRQ estimates are lower in both active-treatment groups than in placebo, while the posted days-of-poor-control estimates are also lower in both active groups than in placebo. The uncertainty differs across the outcomes: the SGRQ comparisons have intervals that do not include zero, whereas the days-of-poor-control intervals include zero. These statements describe the posted unadjusted recalculations, not a single joint analysis of the endpoints. The registry lists no reported analyses for the secondary outcomes.

The primary outcome is the designated main endpoint, while secondary outcomes generally add supporting or exploratory information. When several outcomes and comparisons are examined, the chance of observing apparently notable findings by chance can increase. Unless multiplicity is addressed, the unadjusted secondary p-values and intervals carry less weight than results from a prespecified analysis with an appropriate adjustment. The registry record does not report a multiplicity procedure or a full secondary analysis plan.

Secondary results can help indicate whether findings across measured domains point in a consistent direction, but directional consistency is not proof that the underlying effects are the same or that one endpoint validates another. Differences in measurement scale, timing, missingness and statistical precision matter. The secondary outcomes should therefore be read as additional evidence with greater inferential caution, rather than as independent confirmation of the primary result.

The record does not report a threshold for clinically important change in the SGRQ score or the days-of-poor-control measure. Nor does it explain how those endpoints were prioritized relative to each other. Their role in interpretation is consequently limited to describing the posted group summaries and uncertainty, without assigning a clinical meaning beyond what the registry states.

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

• St. George's Respiratory Questionnaire (SGRQ) Total Score After 12 Weeks of Treatment
• Percentage of COPD "Days of Poor Control" During 26 Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, meaning it is measured on a scale where numerical distances have meaning. FEV1 was recorded in liters. The registry reports a least-squares mean with a standard error for each group. A least-squares mean is an adjusted mean estimated by a statistical model; it need not equal the unadjusted average of all observed values. The described mixed model included baseline FEV1 and other specified lung-function measurements as covariates.

What does a mean difference represent?

A mean difference expresses the estimated contrast between two group means on the outcome's original measurement scale. For the primary outcome, the posted contrasts compare indacaterol with placebo and salmeterol with placebo. A positive contrast means the treatment group's estimate is higher than placebo's estimate for this outcome. The contrast is a group average comparison and does not describe the distribution of individual values. It also does not, by itself, establish the clinical importance of the difference.

What is a standard error?

A standard error describes the estimated sampling uncertainty of a statistic, such as a group mean. It is not the same thing as the spread of individual participant measurements. In this record, standard errors accompany the least-squares means. The reported comparison intervals and recalculated p-values use posted summary statistics and should be understood as approximate, rather than as a reproduction of the trial's mixed-model analysis.

The primary endpoint description specifies covariates, but the registry does not report the full model specification, the exact covariance structure, diagnostics, or detailed handling of all data features. A model's estimates can depend on its assumptions and included terms. Without the full analysis plan and model output, readers cannot verify every modeling choice or determine whether additional analyses were prespecified.

How should the p-values be read?

A p-value measures how incompatible the observed data are with a specified no-difference model, assuming that model and the test's assumptions apply. It is not the probability that the null hypothesis is true, and it does not quantify the size or practical value of a difference. The primary comparison p-values are described as unadjusted recalculations. They do not account for testing multiple outcomes or comparisons unless an adjustment is explicitly made; such an adjustment is not reported in the registry record.

A confidence interval gives a range of values reasonably compatible with the data under the calculation and assumptions used. Its width conveys precision: narrower intervals indicate greater precision, while wider intervals leave more uncertainty about the effect size. The interval does not capture every possible source of bias, such as missing data or model misspecification. It is also not a range containing a specified proportion of individual participants' results.

Why can over-dispersion matter?

Over-dispersion is a general statistical issue in which observed variation is greater than a model assumes. When that happens, standard errors based on the narrower model can be too small, leading to confidence intervals that are too narrow and p-values that overstate the evidence. This is a general concept, not a reported finding about this trial. The posted outcomes are continuous and the registry record does not report an over-dispersion assessment.

For continuous outcomes, an approximate standard deviation can sometimes be inferred from a standard error and group size when recalculating an unadjusted comparison. Such an approximation relies on assumptions about the summary statistics and is not a direct report of the trial's observed participant-level variability. The recalculated effect-size values in the posted material are therefore descriptive planning inputs, not a substitute for the original model estimates or a full analysis of individual data.

What does the analysis population mean?

The registry describes the primary population as an intent-to-treat population comprising randomized participants who received at least one dose. It also says the endpoint was analyzed only for participants with week 12 trough FEV1 data, with missing data imputed using LOCF. Thus, the analysis description combines a defined population with an endpoint-availability condition and an imputation method. The record does not provide the number of imputed observations, the reasons data were missing, or sensitivity analyses examining other missing-data assumptions.

LOCF carries the last observed value forward to fill a later missing value. As a general method, it can be problematic when the outcome would plausibly change after the last observation or when missingness is related to health status. Its use does not make the missing values observed measurements. Without information on missingness patterns and sensitivity analyses, the robustness of the primary result to the imputation choice cannot be assessed from the registry record.

The registry record does not report the full statistical analysis plan, whether interim analyses were conducted, or how multiplicity was handled. These omissions limit assessment of whether the reported comparisons were selected and adjusted according to prespecified rules. The calculated contrasts are useful for understanding the posted group summaries, but they should not be mistaken for a complete reconstruction of the trial's original inferential analysis.

11. Confidence Intervals and Precision

For indacaterol versus placebo, the posted mean difference in trough FEV1 was 0.17 liters, with a confidence interval from 0.119 to 0.221. For salmeterol versus placebo, the posted mean difference was 0.11 liters, with a confidence interval from 0.059 to 0.161. Both intervals lie above zero, and each is accompanied by an unadjusted p-value of <0.001. These intervals communicate uncertainty around the estimated average contrasts under the approximate recalculation, not the range of individual participant responses.

Precision concerns how narrowly the effect is estimated. The interval widths reflect sampling uncertainty under the calculation's assumptions; they do not account for every possible source of uncertainty. In particular, the comparisons were recalculated from posted summary values and are not a reproduction of the described covariate-adjusted mixed model. The registry does not report the sponsor's full model output, so the posted intervals should not be treated as definitive intervals from that model.

Confidence intervals are compatible ranges, not guarantees that the true effect lies within them. They also do not resolve whether an effect is important in practice. The registry record does not report a threshold for clinical importance of a trough FEV1 difference. The point estimates and intervals can therefore describe direction and statistical precision, while the practical meaning remains uncertain from the information recorded.

The intervals also need to be interpreted in the context of multiple outcomes and comparisons. The registry lists a primary outcome and secondary outcomes, but does not report multiplicity adjustment for the recalculated comparisons. The nominal intervals and p-values do not by themselves provide family-wise error control across all outcomes. These limitations do not change the reported arithmetic; they affect how strongly the inferential results can be generalized across the set of analyses.

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 illustrations express the number of participants per arm for 80% power and the number of participants per arm for 90% power. They are not total event counts. The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each comparison, the effect to detect is set as a stated fraction of the observed effect. The registry record does not report the trial's own original design assumptions or sample-size justification.

Power is the chance, under a specified true effect and model assumptions, of detecting an effect at the chosen significance level. The 80% column gives a planning illustration for a design intended to have 80% power under those assumptions; the 90% column uses a higher target. They are prospective planning quantities, not evidence about what power the completed trial actually had. This is not observed power.

Rows describing planning for 100% of the observed effect use the full posted comparison estimate as the target. Rows describing planning for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to attain the same target power under the stated assumptions. These calculations are illustrations based on the observed effects, not recommendations and not the original enrollment plan.

Real studies may differ from the illustration assumptions: allocation may not be equal, outcome variation may differ from the approximation, and missing data or analysis methods can affect precision. The registry's original planned power, significance level and sample-size inputs are not reported in the registry record. The figures are best used to see how assumptions about effect size influence planning, rather than to infer the rationale behind this completed study.

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 = 0.170; pooled standard deviation σ = 0.330.
2. n = 2 × (1.96 + 0.842)² × 0.330² / 0.170² = 59.1, rounded up to 60 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 <- 0.17                      # observed difference in means
sigma <- 0.329916966898216                     # 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(567996)
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 = 60 (80% power), 80 (90% power)
 75% of observed effect: n per arm = 106 (80% power), 141 (90% power)
 50% of observed effect: n per arm = 237 (80% power), 317 (90% power)
power.t.test: 60.1 
Simulated power at n = 60 per arm: 0.801 (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 trial record lists a primary endpoint and two secondary endpoints, each with comparisons against placebo in the posted recalculations. Testing multiple outcomes and contrasts raises the general issue of multiplicity: as the number of statistical tests grows, the chance of at least one apparently unusual result under no true effects may also grow. Adjustments or a prespecified hierarchy can address this issue, but the registry record does not report whether such a strategy was planned or used. The posted secondary results are unadjusted, so they should be interpreted cautiously.

The registry identifies an intent-to-treat population as randomized participants who received at least one dose of study medication. For the primary endpoint, it further says that only participants with week 12 trough FEV1 data were analyzed and missing values were imputed using LOCF. The record does not state how many values were imputed, give reasons for missingness, or report sensitivity analyses under alternative assumptions. These omissions make it difficult to assess whether missing data could have affected the estimates.

LOCF is an imputation approach, not a recovery of the unobserved value. Its validity depends on assumptions about how the outcome would have behaved after the last observed measurement and why data became unavailable. If missingness is related to participants' outcomes, a simple carried-forward value may not represent what would have been observed. This is a general methodological concern; the registry does not describe the trial's missingness patterns in enough detail to determine its practical effect.

The record also does not report the complete statistical analysis plan, details of interim analyses, or the original sample-size justification. It does describe the covariates used in the primary mixed model, but not the full specification or all analytic decisions. Consequently, the recalculated estimates can illuminate posted summaries but cannot establish whether every analysis followed a prespecified plan. The record's reported results remain informative as registry results, with these limits on independent evaluation.

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: chronic obstructive pulmonary disease (3.0%), pneumonia (0.9%), cholelithiasis (0.6%), lower respiratory tract infection (0.6%), upper respiratory tract infection bacterial (0.6%).

The safety summaries report participants at risk and participants with serious adverse effects or other adverse effects in each treatment group. For serious adverse effects, the posted figures are 29 of 330 for indacaterol, 19 of 333 for salmeterol and 26 of 335 for placebo. For other adverse effects, the figures are 69 of 330, 68 of 333 and 71 of 335, respectively. These counts describe the registry's reported group summaries; they are not adjusted comparisons and do not establish that a treatment caused an event.

The registry lists serious adverse-event terms including chronic obstructive pulmonary disease at 3.0%, pneumonia at 0.9%, cholelithiasis at 0.6%, lower respiratory tract infection at 0.6%, upper respiratory tract infection bacterial at 0.6% and coronary artery disease at 0.6%. These are listed terms and percentages, not a complete account of all possible safety outcomes. The record does not report deaths for the groups; death counts are not reported in the registry record.

Group counts alone do not convey event timing, duration, severity beyond the reported classification, recurrence, or causal attribution. They also do not provide a formal comparison with uncertainty. Safety interpretation should therefore distinguish reported events during the study from events judged related to treatment; that relationship is not established by these figures.

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

The posted primary outcome estimates show higher average trough FEV1 at week 12 in the indacaterol and salmeterol groups than in the placebo group. Their unadjusted recalculated mean differences are positive, and the associated confidence intervals lie above zero. This is a description of the group-level estimates in the registry record. It does not mean that every participant's lung function changed in the same way or by the same amount.

Statistical evidence and clinical importance are different questions. The reported p-values address compatibility with a no-difference model under the calculation used, while the effect estimates and confidence intervals describe magnitude and uncertainty. The registry does not state a threshold for a clinically important FEV1 difference, so the practical significance of the estimated contrasts cannot be determined from the record alone. No treatment recommendation follows from these statistical summaries.

The results also do not establish the full benefit-risk profile. The safety figures are event counts and listed terms, not evidence of causation or a complete comparative safety analysis. Secondary outcomes add information about questionnaire scores and days of poor control, but their analyses are unadjusted in the posted recalculations and the registry does not report a multiplicity strategy. Those findings have less inferential weight than a fully specified, prespecified analysis would carry.

Interpretation is further limited by the analysis details available. The primary endpoint used a mixed model with stated covariates and LOCF for missing data, but the full model output, imputation counts and sensitivity analyses are not reported in the registry record. The simple recalculations are not identical to the trial's model-based inference. These gaps constrain independent assessment of assumptions and robustness.

In short, the record supports a careful description of estimated group differences in the measured outcomes, with uncertainty. It does not establish individual outcomes, long-term effects beyond the recorded treatment period, mechanisms, or results in populations not described by this trial. It also does not answer whether the observed differences meet a threshold that participants or clinicians would consider important.

17. Why This Trial Matters Statistically

This trial illustrates why a clinical result needs more than a point estimate. The group means, mean differences, standard errors and confidence intervals each answer different questions: the means describe adjusted outcome levels, the contrasts quantify average separation, and the uncertainty measures indicate how precisely that separation is estimated. Keeping these concepts distinct prevents a p-value from being treated as a measure of effect size or clinical importance.

It also demonstrates the difference between a trial's intended analysis and a simple recalculation from posted summaries. The primary endpoint is described as a covariate-adjusted mixed-model outcome, while the recalculated comparisons use summary statistics and approximate variability. Recalculations can provide a transparent way to inspect the reported estimates, but they cannot recover all details of the original analysis or replace its full output.

The record raises common questions about analysis populations and missing data. It describes an intent-to-treat population, restricts the endpoint analysis to participants with week 12 data, and states that LOCF was used. Understanding the consequences requires information about missingness patterns and sensitivity analyses, which are not reported in the registry record. This is a reminder that endpoint definitions and imputation choices are part of the statistical result, not administrative details.

Finally, the primary and secondary outcomes show why multiplicity matters. Several endpoints can provide complementary perspectives, but their combined interpretation depends on prespecification and appropriate handling of multiple tests. The registry results can be informative while still leaving important design and analysis questions unresolved. A statistically careful reading retains both the estimates and the limits of what the record establishes.

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 give a full protocol or statistical analysis plan, so the original sample-size assumptions, planned multiplicity handling and any interim analyses are not reported in the registry record. The planning illustrations based on posted effects do not fill that gap. They cannot explain why the trial enrolled the reported number of participants or establish what power its investigators intended.

The primary analysis description names a mixed model and covariates, but does not report the complete model specification, diagnostics or full sponsor analysis output. The posted recalculations are simple, unadjusted estimates from summary statistics, and their approximate standard deviations are not direct participant-level summaries. This limits exact comparison between the recalculated inference and the original adjusted analysis.

The record states that LOCF was used for missing primary endpoint data but does not report the amount or pattern of missingness, reasons for missing measurements, or sensitivity analyses. The primary endpoint was analyzed only for participants with week 12 data, so the relationship between the stated analysis population and the endpoint-specific analysis cannot be fully assessed from the record.

The record also does not report thresholds for clinically important differences in the outcomes. Secondary results have no reported analyses and are presented as unadjusted recalculations, with no stated multiplicity procedure. Safety summaries do not establish causality, and the death counts are not reported in the registry record. These are limitations of what can be concluded from the registry information, not proof that relevant analyses or data were absent from other study documents.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Indacaterol in Patients With Chronic Obstructive Pulmonary Disease (COPD) Using Salmeterol as Active Control — NCT00567996.
• Registry record last updated 2011-08-18; status last verified 2011-07.
• Results first posted 2011-08-18.
• 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

NCT00567996 is a completed phase 3 randomized, triple-masked, parallel-group trial of indacaterol, salmeterol and placebo in patients with COPD. The study treatment period was 26 weeks, and the primary endpoint was trough FEV1 at week 12. The registry lists enrollment as 1002.

The posted primary group means were 1.45 liters for indacaterol, 1.39 liters for salmeterol and 1.28 liters for placebo. Recalculated mean differences versus placebo were 0.17 liters and 0.11 liters, respectively, with both unadjusted p-values reported as <0.001. Secondary outcomes concerned SGRQ total score and percentage of COPD days of poor control.

The registry describes covariate adjustment and LOCF for missing primary endpoint data, but does not report the full statistical plan, multiplicity strategy, original sample-size justification or sensitivity analyses. The estimates describe group averages and should be interpreted with their uncertainty and these record-level limitations.