A 12 Week Treatment, Multi-center, Randomized, Double-blind, Parallel-group, Placebo and Active Controlled Study to Assess the Efficacy, Safety, and Tolerability of Indacaterol Maleate / Glycopyrronium Bromide in COPD Patients With Moderate to Severe Airflow Limitation.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A 12 Week Treatment, Multi-center, Randomized, Double-blind, Parallel-group, Placebo and Active Controlled Study to Assess the Efficacy, Safety, and Tolerability of Indacaterol Maleate / Glycopyrronium Bromide in COPD Patients With Moderate to Severe Airflow Limitation. (NCT01727141), a randomized phase 3 study. The primary outcome is Change From Baseline in Standardized Forced Expiratory Volume in 1 Second (FEV1) Area Under the Curve (AUC) (0-12 Hours (h)).

2. Clinical Question

3. Trial Design

This completed Phase 3 study was a randomized, double-blind, parallel-group trial with placebo and active controls. The registry record reports enrollment of 1042 participants and describes treatment over 12 weeks. The sponsor was Novartis Pharmaceuticals. The recorded study start was 2012-11, and primary completion was 2014-02.

Four treatment groups were included: QVA149, QAB149, NVA237, and placebo. QVA149 was described as 27.5/12.5 ug twice daily by single-dose dry powder inhaler; QAB149 as 27.5 ug twice daily; and NVA237 as 12.5 ug twice daily. Placebo was described as twice daily. The registry record identifies the condition as chronic obstructive pulmonary disease and gives the target population as participants with moderate to severe airflow limitation.

The primary outcome was analyzed in a Full Analysis Set defined as randomized participants who received at least one dose. Participants missing day 1 or week 12 FEV1 AUC measurements were not included in that analysis. Consequently, enrollment and the number contributing to the primary outcome are not the same quantity. The outcome-specific group counts are displayed with the results.

Randomization and masking are features of the trial design, but the registry record does not report allocation concealment procedures, the exact randomization ratio, or details about which roles were masked. It also does not report the trial's original sample-size justification, planned interim analyses, or a complete statistical analysis plan. The reported model and endpoint description clarify some analysis choices, but do not supply those missing design details.

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: One thousand forty two participants were randomized. (One participant was randomized twice and was counted twice in the randomized set.) In the safety set, participants were analyzed according to the treatment received.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set: The full analysis set included all randomized participants who received at least one dose of study treatment. Participants, who were missing day 1 and/or week 12 FEV1 AUC 0-12h measurements, were not included in the analysis.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Standardized Forced Expiratory Volume in 1 Second (FEV1) Area Under the Curve (AUC) (0-12 Hours (h)), measured over baseline (BL), 12 Weeks.

The primary endpoint is change from baseline in standardized forced expiratory volume in 1 second area under the curve from 0 to 12 hours, measured in liters, at 12 weeks. FEV1 is the volume of air exhaled in the first second of a forced expiratory maneuver. AUC summarizes measurements over the stated post-dose time window; standardizing the area by the time interval expresses it as an average over that interval rather than as an unscaled accumulated area.

According to the registry description, spirometry was conducted centrally and followed international standards. Baseline FEV1 was defined as the average of the pre-dose measurements at -45 minutes and -15 minutes on day 1. The trapezoidal rule was used to estimate the area from measured time points, followed by normalization to the length of time. These choices define how the physiological measurements were combined into the endpoint.

In general, an AUC measure can represent lung function across several scheduled measurements, rather than relying on a single reading. It is useful for comparing average pulmonary-function responses over the specified interval. The posted primary endpoint is a continuous measure and its reported group summaries are least-squares means from a repeated-measures model. It does not directly measure symptoms or quality of life; those were addressed by secondary outcomes.

7. Results Posted in the Registry

• QVA149: mean 0.21 versus -0.02 on control; difference 0.23 (95% CI 0.19 to 0.27), standardized effect d = 1.01; z-test p = <0.001.
• QAB149: mean 0.12 versus -0.02 on control; difference 0.14 (95% CI 0.10 to 0.18), standardized effect d = 0.60; z-test p = <0.001.
• NVA237: mean 0.11 versus -0.02 on control; difference 0.13 (95% CI 0.09 to 0.17), standardized effect d = 0.58; z-test p = <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score

• 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:
  • QVA149: mean -6.40 versus -2.70 on control; difference -3.70 (95% CI -5.82 to -1.58), standardized effect d = -0.32; z-test p = <0.001.
  • QAB149: mean -4.60 versus -2.70 on control; difference -1.90 (95% CI -4.02 to 0.22), standardized effect d = -0.16; z-test p = 0.079.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for QVA149 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between QAB149 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With a Clinically Important Improvement of at Least 4 Units in the SGRQ Total Score

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • QVA149: 57.3% (141/246) versus 39.0% (87/223) on control; risk difference 18.3 percentage points (95% CI 9.4 to 27.2), risk ratio 1.47 (1.21–1.79); unadjusted two-proportion z-test p = <0.001.
  • QAB149: 48.0% (117/244) versus 39.0% (87/223) on control; risk difference 8.9 percentage points (95% CI -0.0 to 17.9), risk ratio 1.23 (1.00–1.52); unadjusted two-proportion z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for QVA149 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between QAB149 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Pre-dose Trough FEV1

• 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:
  • QVA149: mean 0.16 versus -0.04 on control; difference 0.20 (95% CI 0.16 to 0.24), standardized effect d = 0.87; z-test p = <0.001.
  • QAB149: mean 0.08 versus -0.04 on control; difference 0.12 (95% CI 0.08 to 0.16), standardized effect d = 0.52; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for QVA149 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 QAB149 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the assessment beyond the primary 0–12-hour FEV1 AUC. They include respiratory health status measured with the St. George's Respiratory Questionnaire, the proportion meeting a specified improvement threshold on that questionnaire, additional FEV1 and FVC measures, and the Transitional Dyspnea Index. These outcomes relate to different aspects of respiratory function and participant experience, so their results need not mirror one another exactly.

Across the secondary summaries with results, the direction of the QVA149 estimates generally favors improvement relative to placebo. The other active-treatment patterns are less consistent in their statistical certainty. This broad pattern is compatible with the primary pulmonary-function contrast but does not make the outcomes interchangeable: a change in lung-function measurements is not the same construct as a quality-of-life score or a threshold-based responder outcome. The specific estimates and intervals for each posted endpoint should be interpreted on that endpoint's own scale.

The registry lists other secondary measures, including additional spirometry and dyspnea outcomes, but their results are not reported in the registry record. The record also does not list reported secondary analyses. That absence means the overall secondary picture is incomplete and should not be interpreted as evidence that an unreported outcome had no effect.

Unadjusted secondary comparisons carry less weight because multiple outcomes and treatment contrasts create more opportunities for chance findings. The registry record does not report a multiplicity adjustment or a hierarchy for secondary outcomes. Consequently, the secondary results are useful for describing the observed pattern and identifying questions for further evaluation, but they do not have the same confirmatory status as a clearly prespecified primary endpoint analyzed under a fully reported plan.

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

• Change From Baseline in St. George's Respiratory Questionnaire (SGRQ) Total Score
• Percentage of Participants With a Clinically Important Improvement of at Least 4 Units in the SGRQ Total Score
• Change From Baseline in Trough FEV1
• Change From Baseline in Pre-dose Trough FEV1
• Change From Baseline in FEV1
• Change From Baseline in FVC
• Change From Baseline in Standardized FEV1 AUC (0-4 h), FEV1 AUC (4-8h), FEV1 AUC (8-12h) and FEV1 AUC (0-12 h)
• Transitional Dyspnea Index (TDI) Focal Score

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes a mixed model for repeated measures (MMRM) for the primary endpoint. In general, this type of model analyzes repeated observations over time while accounting for the fact that measurements from the same participant are related. It can estimate treatment-group means at a follow-up visit while using the specified covariates and visit structure. The registry record lists terms for treatment, baseline FEV1 measurements, smoking status at baseline, baseline inhaled corticosteroid use, region, baseline FEV1 by visit, visit, and treatment by visit.

What does a least-squares mean represent?

In general, a least-squares mean is a model-based estimate of a group mean after accounting for the terms included in the model. It is not necessarily identical to the simple arithmetic mean of all observed participant values. For this trial, the reported primary group values are least-squares means, with standard errors as their dispersion measures. The model's covariate adjustment is one reason to distinguish its analysis from a simple comparison of group summaries.

The analysis population is also important. The Full Analysis Set included randomized participants who received at least one dose. However, participants missing the required day 1 and/or week 12 FEV1 AUC measurements were excluded from this endpoint analysis. In general, excluding participants with missing endpoint measurements can affect how representative the analyzed set is of all randomized participants. The registry record says those missing values were not imputed for this endpoint; it does not report a sensitivity analysis assessing the impact of missing data.

How were the AUC measurements formed?

Centralized spirometry was performed according to international standards. Baseline was the average of pre-dose FEV1 measured at -45 minutes and -15 minutes on day 1. The trapezoidal rule estimates area between measured time points by connecting adjacent observations; the resulting FEV1 AUC was then normalized to the length of time. In general, this method uses the sequence of measurements in the interval rather than treating any single measurement as the whole response. The registry record states that missing day 1 and week 12 AUC values were not imputed.

What do the recalculated comparisons represent?

The posted arm values are least-squares mean changes. The recalculated contrasts subtract the placebo summary from each active-treatment summary, and the associated intervals and p-values are unadjusted. These calculations are useful as a transparent summary-scale comparison, but they do not reproduce the MMRM's full covariance structure or necessarily match the model's treatment contrasts. The planning illustrations also derive from observed effects and simple assumptions; they are not an analysis of the trial's original design.

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be under that hypothesis and the test's assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The p-values in the recalculated comparisons are unadjusted. When many outcomes or contrasts are examined, the chance of at least one apparently strong result can increase; therefore, a collection of unadjusted secondary results carries less confirmatory weight than a prespecified primary analysis with a reported multiplicity strategy.

The registry record does not report whether interim analyses were planned or conducted, how the original sample size was justified, or a complete plan for controlling multiplicity. The model description is informative but does not answer these questions. There are no reported secondary analyses in the record's analysis listings, even though secondary outcome summaries are posted. These gaps limit reconstruction of the original inferential framework and make the displayed unadjusted secondary comparisons exploratory in interpretation.

Standard errors describe the estimated sampling uncertainty of a model-based mean, under the analysis model. Confidence intervals express a range of values compatible with the data and method at the stated confidence level. The intervals accompanying recalculated contrasts are based on posted summaries; they should not be confused with a model-derived interval from the original MMRM unless explicitly identified as such. This distinction matters because statistical adjustment, repeated-measure correlations, and analysis-population choices can affect uncertainty estimates.

11. Confidence Intervals and Precision

The primary recalculated QVA149-versus-placebo mean difference is 0.232 liters, with a 95% confidence interval from 0.193 to 0.272. This interval gives a range of estimates compatible with the posted summary data under the unadjusted calculation. Its endpoints are both positive, indicating that this recalculated interval excludes a zero difference. The interval does not indicate the probability that the true effect lies within it; in general, a 95% confidence procedure produces intervals that cover the target value in 95% of repeated applications under its assumptions.

The recalculated intervals for QAB149 and NVA237 versus placebo are also entirely above zero. They are 0.099 to 0.177 liters for QAB149 and 0.093 to 0.173 liters for NVA237. These estimates are precise enough, under the simple recalculations, to distinguish their contrasts from zero statistically. The intervals overlap, but overlap alone is not a valid test of whether the active treatments differ from each other; no direct active-treatment comparison is posted.

Precision is not the same as clinical importance. A narrow interval can still include effects whose practical meaning is uncertain, and a confidence interval does not determine whether a measured change matters to participants. The registry record does not report a clinical-importance threshold for the primary endpoint. In general, interpretation should consider both the range of plausible effect sizes and the relevance of those sizes to the outcome.

The primary intervals are recalculated from the posted summary statistics and are unadjusted. The primary endpoint's stated MMRM includes repeated observations and covariate terms. Therefore, the model-based result from the sponsor's analysis, if separately reported, would be the appropriate inferential reference. The registry record does not include a discrepancy flag, but the calculation method still limits how directly these intervals represent the fitted model.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total participants, and the underlying comparison uses equal allocation between two arms. They are planning illustrations based on the observed effect, not the trial's original design calculations. The listed assumptions are a two-sided significance level of 0.05, equal allocation, a normal approximation, and a target effect set to the stated fraction of the observed effect. The trial's own original sample-size justification and assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the specified effect under those assumptions, if that effect and the model assumptions held. The 90% column describes the corresponding target for a 90% chance. These are prospective planning quantities, not a probability calculated from the completed trial. This is not observed power.

Rows planning for 100% of the observed effect use the full observed contrast as the target; rows planning for 75% or 50% use smaller target effects. Smaller effects generally require more participants to distinguish them from random variation at the same significance level and target power. The figures therefore rise as the target effect is reduced. Because the observed effects are estimates with uncertainty, they should not be treated as known truths for a future study. The sample-size curve should be read as a visual representation of this relationship between effect size and required participants, rather than as a forecast of the results of a new trial.

For time-to-event outcomes, planning displays may instead report total events; that convention does not apply to these continuous and binary outcomes. The figures relevant to the comparisons described for this trial are participants per arm.

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 = 0.232; pooled standard deviation σ = 0.229.
2. n = 2 × (1.96 + 0.842)² × 0.229² / 0.232² = 15.3, rounded up to 16 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 <- 0.232                      # observed difference in means
sigma <- 0.229400174198889                     # 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(1727141)
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 = 16 (80% power), 21 (90% power)
 75% of observed effect: n per arm = 28 (80% power), 37 (90% power)
 50% of observed effect: n per arm = 62 (80% power), 83 (90% power)
power.t.test: 16.4 
Simulated power at n = 16 per arm: 0.786 (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 statistical conclusions are drawn across several outcomes, contrasts, or analysis choices. In general, testing many hypotheses without adjustment increases the chance of at least one result appearing statistically persuasive by chance. This concern is relevant to a trial with one primary endpoint and multiple secondary measures, especially where each active treatment is compared with placebo. The posted recalculations are unadjusted, and the registry record does not report a method for controlling the family-wise error rate, a hierarchy of testing, or another multiplicity strategy.

The registry record also does not report whether interim analyses were planned or conducted. It does not give the original sample-size justification or a complete statistical analysis plan. These items matter because planned looks at accumulating data, endpoint priorities, and testing rules can affect how confirmatory p-values are interpreted. Their absence from the registry record does not establish that no such procedures existed; their details are not reported in the registry record.

Missing data are addressed explicitly for the primary endpoint: missing day 1 and/or week 12 FEV1 AUC measurements were not imputed, and participants without the required measurements were not included in that analysis. This is a complete-measurement analysis for that endpoint within the defined Full Analysis Set. In general, such an approach can be sensitive to why measurements are missing and whether missingness is related to outcome or treatment. The registry record does not report reasons for missing measurements or sensitivity analyses to evaluate alternative assumptions.

The analysis population included randomized participants who received at least one dose, rather than all randomized participants regardless of treatment received. That definition and the endpoint-specific exclusion for missing measurements should be kept in view when interpreting the analysis counts. The record does not report a secondary analysis population or results from alternative missing-data methods. These reporting gaps constrain assessment of robustness, multiplicity, and the extent to which the posted estimates reflect the original intended inferential plan.

15. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 1% 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 (1.9%), atrial fibrillation (0.8%), pneumonia (0.8%), colitis (0.4%), intestinal obstruction (0.4%).

The registry reports serious adverse events for each group as counts among participants at risk: 10 of 258 in QVA149, 13 of 260 in QAB149, 8 of 262 in NVA237, and 8 of 260 in placebo. These are group-specific counts; they should be read with their denominators rather than as stand-alone totals. The registry also reports other adverse events affecting 86 of 258, 87 of 260, 85 of 262, and 90 of 260 participants, respectively. These categories are reported separately.

The most frequent serious-event terms listed include chronic obstructive pulmonary disease at 1.9%, atrial fibrillation at 0.8%, pneumonia at 0.8%, colitis at 0.4%, intestinal obstruction at 0.4%, and small intestinal obstruction at 0.4%. These terms describe events recorded in the registry; they do not establish that a study treatment caused them. The record does not report death counts. A safety comparison would require details beyond these descriptive counts, including event definitions, timing, exposure, and an analysis plan; those details are not reported in the registry record.

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

The posted primary results describe a positive difference in change in standardized FEV1 AUC between QVA149 and placebo over 12 weeks. The unadjusted recalculated estimate is 0.232 liters, with a confidence interval that excludes zero. The other active-treatment comparisons with placebo also have positive estimates and unadjusted intervals excluding zero. These findings concern the specified lung-function endpoint in the analyzed participants.

They do not by themselves show that the observed difference is clinically important. The registry record does not provide a threshold for interpreting the primary endpoint's clinical relevance. Nor does a result on FEV1 AUC establish a corresponding change in symptoms, daily activities, exacerbations, or long-term health. Separate outcomes are needed for those questions, and some secondary results are not reported in the registry record.

The study's 12-week follow-up does not answer questions about effects beyond that period. The posted endpoint analysis also excluded participants missing day 1 and/or week 12 AUC measurements, and the record does not report sensitivity analyses for those missing values. Thus, interpretation should remain tied to the defined analysis population and available follow-up.

Statistical significance is not a treatment recommendation. The results are estimates from a randomized trial, with precision and limitations; they do not settle every clinical or comparative question. In particular, the placebo comparisons do not establish differences among QVA149, QAB149, and NVA237. Direct active-treatment comparisons, a complete account of multiplicity procedures, and a broader follow-up assessment are not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates how a randomized, masked, parallel-group design can compare a combination treatment with both placebo and active controls. The four-arm structure gives context to the primary contrast while also allowing separate comparisons against two active treatments. Those comparisons remain distinct from direct head-to-head tests among active treatments, a distinction that is important when reading several estimates side by side.

It also shows why the endpoint's construction and analysis population matter. The primary outcome is an average FEV1 response across a stated time window, estimated using a repeated-measures model with baseline and other listed covariates. Participants missing required endpoint measurements were excluded rather than having the values imputed. These choices affect what the estimates represent and which participants contribute to them.

The statistical record demonstrates a further distinction between model-based trial analysis and transparent recalculation from summary data. The posted arm summaries support simple unadjusted contrasts and intervals, but they cannot reproduce every feature of the MMRM. Reporting both a detailed model specification and complete inferential results would help readers connect the trial design to the formal conclusions.

Finally, the secondary outcomes and safety counts show why a single primary endpoint is only one part of a trial's evidence. Multiple outcomes can describe different dimensions, but unadjusted testing and incomplete reporting limit the strength of broad conclusions. This trial is therefore useful for understanding both the potential information in randomized comparisons and the importance of complete analysis-plan and missing-data reporting.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record does not report the original sample-size justification, interim-analysis plans, or a complete multiplicity strategy. Although planning illustrations are available based on observed effects, those are not the trial's design calculations. The missing design details make it difficult to assess how the trial's original operating characteristics related to its intended primary and secondary questions.

The primary analysis excludes participants without the required day 1 and/or week 12 FEV1 AUC measurements and does not impute those values. Reasons for missingness and sensitivity analyses are not reported in the registry record. This limits assessment of how robust the primary estimate is to assumptions about incomplete outcome data. The analysis population also requires participants to have received at least one dose, so it is not simply every randomized participant.

The posted recalculated contrasts are unadjusted and based on summary statistics. They are not a substitute for the specified repeated-measures model, and their intervals do not necessarily capture the model's full structure. The registry record does not provide reported secondary analyses, despite posting some secondary outcome summaries; results for other listed secondary measures are not reported in the registry record.

Follow-up is limited to 12 weeks for the treatment period described. The results therefore do not address longer-term outcomes. The registry safety summary gives counts and selected event terms but does not provide detailed comparative analyses, event timing, or death counts. No direct active-treatment comparison is posted. These limitations restrict interpretation to the endpoints, contrasts, participants, and follow-up described in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A 12 Week Treatment, Multi-center, Randomized, Double-blind, Parallel-group, Placebo and Active Controlled Study to Assess the Efficacy, Safety, and Tolerability of Indacaterol Maleate / Glycopyrronium Bromide in COPD Patients With Moderate to Severe Airflow Limitation. — NCT01727141.
• Registry record last updated 2016-03-29; status last verified 2016-03.
• Results first posted 2015-06-09.
• 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

NCT01727141 is a completed Phase 3 randomized, double-blind, parallel-group study of QVA149, QAB149, NVA237, and placebo in COPD patients with moderate to severe airflow limitation. Enrollment was 1042, and the treatment period was 12 weeks.

The primary endpoint was change from baseline in standardized FEV1 AUC over 0–12 hours. The posted adjusted group means favor each active-treatment group relative to placebo, and the unadjusted recalculated primary contrasts have confidence intervals above zero. The registry reports several secondary outcome summaries and descriptive adverse-event counts. Multiplicity procedures, original sample-size justification, interim analyses, and some secondary results are not reported in the registry record.