Efficacy, Tolerability and Safety of NVA237 in Patients With Chronic Obstructive Pulmonary Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy, Tolerability and Safety of NVA237 in Patients With Chronic Obstructive Pulmonary Disease (NCT01513460), a randomized phase 3 study. The primary outcome is Change From Baseline in Mean Trough Forced Expiratory Volume in 1 Second (FEV1) (NVA237 Versus Tiotropium).

2. Clinical Question

3. Trial Design

The registry describes a randomized, quadruple-masked, active-controlled, parallel-group phase 3 study. It was multicenter, and its stated purpose was to compare the efficacy, tolerability, and safety of NVA237 with tiotropium when added to fluticasone/salmeterol in people with COPD. The record lists an enrollment of 773 and a completed status. The study began in 2012-04, and primary completion was recorded as 2013-12.

Three groups are described: NVA237 plus Flu/Sal, tiotropium plus Flu/Sal, and Flu/Sal with placebo to both additional drugs. The primary outcome compares the first two groups. The intervention descriptions specify NVA237 50 µg once daily, tiotropium 18 µg once daily, and Flu/Sal 500/50 µg twice daily. The registry identifies the masking level as quadruple, but does not report which specific roles were masked or give further details of the masking procedures in the posted record.

The primary endpoint analysis used a per-protocol set, rather than all randomized participants. Its recorded definition requires at least one dose, baseline and week 12 outcome values, and no major protocol or non-protocol deviations. The posted primary outcome counts are 194 for NVA237 plus Flu/Sal and 185 for tiotropium plus Flu/Sal. The safety section uses different at-risk counts, so these populations should not be treated as interchangeable. The registry record does not report the randomization ratio, site locations, full participant flow, or the original sample-size justification. The posted enrollment figure alone does not explain how the analysis populations were formed.

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: Participants from the per-protocol set (PPS), who had values at both baseline and week 12, were included in the analysis. The PPS included all randomized participants who had at least one dose of study drug and who were without any major protocol or non-protocol deviations.

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 Mean Trough Forced Expiratory Volume in 1 Second (FEV1) (NVA237 Versus Tiotropium), measured over baseline, 12 weeks.

The primary endpoint is change from baseline in mean trough FEV1, measured in liters, comparing NVA237 with tiotropium. FEV1 is the volume of air exhaled in the first second of a forced breath. The registry defines trough FEV1 as the mean of measurements taken at 23:15 and 23:45 after the morning dose of study drug. Baseline was the average of clinic measurements taken 45 minutes and 15 minutes before the first randomized-treatment dose at Visit 3. The outcome was assessed at baseline and 12 weeks.

Change from baseline expresses each participant’s follow-up measure relative to the specified starting measure, and the group mean summarizes those changes. The registry states that a positive change indicates improvement. Trough timing is intended to characterize lung function at a defined point in the dosing schedule rather than immediately after a dose. This endpoint therefore provides a standardized, continuous measure for comparing the two add-on treatments over the specified follow-up.

As a general statistical point, a continuous endpoint retains information about the size of measurements rather than reducing them to categories. Its interpretation still depends on how it was measured, who was included in the analysis, and how precisely the difference was estimated. The primary analysis was limited to the per-protocol set described in the registry record, so its result does not directly summarize every randomized participant.

7. Results Posted in the Registry

• Tiotropium + Flu/Sal: mean 0.10 versus 0.10 on control; difference 0.01 (95% CI -0.03 to 0.04), standardized effect d = 0.04; z-test p = 0.710.

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 Total Score of the St George's Respiratory Questionnaire for COPD Patients (SGRQ-C) 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:
  • Tiotropium + Flu/Sal: mean -3.90 versus -2.81 on control; difference -1.10 (95% CI -2.99 to 0.80), standardized effect d = -0.10; z-test p = 0.258.
  • Flu/Sal: mean -0.65 versus -2.81 on control; difference 2.15 (95% CI 0.26 to 4.04), standardized effect d = 0.20; z-test p = 0.026.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Flu/Sal and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Flu/Sal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Mean Daily Number of Puffs of Rescue Medication Use

• 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:
  • Tiotropium + Flu/Sal: mean 2.09 versus 2.19 on control; difference -0.10 (95% CI -0.48 to 0.29), standardized effect d = -0.04; z-test p = 0.618.
  • Flu/Sal: mean 2.91 versus 2.19 on control; difference 0.72 (95% CI 0.33 to 1.10), standardized effect d = 0.33; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Flu/Sal and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Flu/Sal than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Mean Percentage of Nights With 'no Nighttime Awakenings'

• 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:
  • Tiotropium + Flu/Sal: mean 0.82 versus 0.83 on control; difference -0.02 (95% CI -0.05 to 0.02), standardized effect d = -0.09; z-test p = 0.305.
  • Flu/Sal: mean 0.82 versus 0.83 on control; difference -0.01 (95% CI -0.05 to 0.02), standardized effect d = -0.06; z-test p = 0.530.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium + Flu/Sal 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 Flu/Sal and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists six secondary outcomes, including respiratory health status, rescue medication use, nighttime awakenings, usual activities, and additional FEV1 comparisons. Numerical results are posted for three of those secondary outcomes. The available results do not form a single uniform pattern across all measures: the between-arm contrasts vary in direction and in how much uncertainty surrounds them. They should be considered alongside, rather than as a replacement for, the primary FEV1 comparison.

Some posted secondary comparisons involve NVA237 plus Flu/Sal versus tiotropium plus Flu/Sal, while others compare NVA237 plus Flu/Sal with Flu/Sal alone. Those are distinct questions. A contrast against the active add-on comparator does not answer the same question as a contrast against the Flu/Sal group, and results should not be combined as if they were one treatment comparison. The secondary measures also describe different aspects of COPD-related outcomes, so agreement is not guaranteed even when measured in the same study.

The numerical secondary comparisons are unadjusted recalculations from posted summaries, and the registry does not list reported analyses for them. No multiplicity correction or testing hierarchy is reported. When many secondary endpoints and contrasts are considered, some apparently notable results can arise by chance. Therefore unadjusted secondary findings carry less inferential weight than a clearly prespecified, fully reported primary analysis. The record does not identify which secondary outcomes were designated as key confirmatory outcomes, if any.

These outcomes can still help describe the broader pattern of measurements collected, but they should be treated as exploratory evidence. The primary result itself is uncertain, with its interval spanning values in both directions. Secondary signals do not resolve that primary uncertainty unless a prespecified analysis plan and appropriate inferential control support such an interpretation. Those details are not reported in the registry record.

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

• Change From Baseline in Mean Trough FEV1 (Flu/Sal Versus NVA237/Tiotropium+Flu/Sal)
• Change From Baseline in Mean Trough FEV1
• Change From Baseline in Total Score of the St George's Respiratory Questionnaire for COPD Patients (SGRQ-C) After 12 Weeks of Treatment
• Change From Baseline in the Mean Daily Number of Puffs of Rescue Medication Use
• Mean Percentage of Nights With 'no Nighttime Awakenings'
• Mean Percentage of Days With Performance of Usual Activities

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a mean change in FEV1 measured in liters. The registry reports group means and standard errors. A mean describes the central value of a set of measurements. A standard error describes the statistical precision of an estimated mean; it is not the spread of individual participant measurements. General statistical explanation: a smaller standard error usually indicates a more precisely estimated mean, while the standard deviation describes variation among observations. The record does not provide standard deviations for the primary arms in the primary outcome listing.

What did the trial specify for the primary model?

The outcome description states that a mixed model was used. Treatment was a fixed effect, and the model included baseline trough FEV1, FEV1 before inhalation of short-acting bronchodilators, FEV1 after inhalation of bronchodilators, and stratification factors as covariates. A fixed treatment effect estimates the contrast between the randomized treatment groups while accounting for the listed covariates. General statistical explanation: adjustment can improve precision or account for measured differences, but the interpretation depends on the model specification and data. The registry record does not report further model details, such as the covariance structure, estimation method, or diagnostics.

The primary endpoint summary gives an arm mean and standard error for each group. The posted mean difference and interval are simple unadjusted recalculations from those summary statistics, not output from the described mixed model. The recalculated comparison is useful for understanding the direction and approximate uncertainty in the posted arm summaries, but it should not be mistaken for a reported adjusted trial analysis. The registry record does not report a model-based estimate alongside these outcome summaries.

How should the interval and p-value be understood?

A confidence interval gives a range of values compatible with the data and the method used to calculate it. Its width reflects precision: a wider interval leaves more uncertainty about the size and direction of the contrast. For the primary comparison, the interval crosses zero, so values representing a difference in either direction remain compatible with the recalculation. The confidence level is not stated in the registry record, so it should not be assigned from the information posted.

A p-value is calculated under a null hypothesis and statistical assumptions. The unadjusted value of 0.71 does not say there is a 71% probability that the null hypothesis is true, and it does not establish equivalence. It indicates that the simple recalculated contrast is not unusual under the no-difference model. General statistical explanation: a p-value does not convey the magnitude or clinical importance of an effect, and it does not replace consideration of the estimate and interval.

The posted comparison is labeled unadjusted because it uses the arm-level summaries without the covariate adjustment specified in the primary outcome description. It is not evidence that the trial’s mixed model omitted those covariates. No discrepancy is flagged between the recalculation and a sponsor result, but the registry record does not provide a sponsor model estimate to compare against.

Why does the analysis population matter?

The primary outcome includes participants from the per-protocol set who had both baseline and week 12 values. The record defines this set as randomized participants who received at least one dose and had no major protocol or non-protocol deviations. This differs from an analysis of all randomized participants. General statistical explanation: excluding participants after randomization can weaken the protection that randomization provides against confounding, especially if exclusions are related to treatment or outcome. The record does not report the exclusion counts, reasons, or a separate all-randomized analysis, so the consequences of this choice cannot be assessed from the posted information alone.

The secondary endpoint summaries have their own reported analysis counts, which vary by endpoint and arm. These counts should be read as outcome-specific analysis populations rather than assumed to be identical to the primary set. The record does not explain all reasons for differences in those counts, describe how missing outcome values were handled, or report imputation methods. General statistical explanation: missing-data assumptions matter because conclusions can change if participants without observed outcomes differ systematically from those with observed outcomes.

What does over-dispersion mean in general?

Over-dispersion occurs when observed variation is greater than a statistical model expects. It matters particularly for count or binary outcomes when a model assumes a fixed relationship between the mean and variance: underestimating variability can make standard errors too small and uncertainty appear less than it is. The primary FEV1 endpoint is continuous and the record does not state that over-dispersion was assessed or that it affected this analysis. This general concept should not be taken as a claim about this trial’s data.

The registry lists no reported analyses for the secondary outcomes, while the numerical comparisons available for them are unadjusted recalculations from posted summary statistics. The record does not report adjustment for multiple comparisons. Consequently, the inferential meaning of secondary p-values is more limited than a prespecified, fully reported analysis would be. The statistical plan, including any prespecified hierarchy or multiplicity procedure, is not reported in the registry record.

11. Confidence Intervals and Precision

The primary difference is 0.007 liters in the direction of tiotropium relative to NVA237. Its interval includes negative and positive values, crossing zero. This means the available summary data do not pinpoint the contrast’s direction with precision: the values compatible with the interval include a difference favoring either arm. The limits are not repeated because the posted interval is more precise than the permitted display precision in this narrative.

Precision is about the range of effects compatible with the data, not whether an effect is important to patients. The registry record does not state a clinical threshold for a meaningful FEV1 difference, so the interval cannot be classified against such a threshold. The confidence level for the interval is also not reported in the registry record. The reported standard errors describe uncertainty in the arm means, while the interval for the contrast describes uncertainty in the between-arm difference.

The p-value of 0.71 is consistent with substantial uncertainty about the contrast; it does not show that the true difference is zero. A non-significant result cannot establish equivalence or non-inferiority without an appropriate design, margin, and analysis, none of which is reported as part of this primary comparison. The registry record does not report the model-adjusted interval from the mixed model described in the endpoint methods. Thus the recalculated interval is an informative summary of the posted arm statistics, but it should not be treated as a replacement for the trial’s adjusted analysis.

General statistical explanation: intervals tend to become narrower when estimates are based on more information and less variable observations, but their width also depends on the analysis method and assumptions. The primary set is per protocol and excludes participants without both specified measurements, which limits what can be inferred about precision for the full randomized population. Without a reported participant flow and missing-data analysis, the effect of those exclusions on precision cannot be determined.

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 for 80% power and participants per arm for 90% power. They are not total enrollment targets and do not describe the number of participants actually analyzed. For the primary continuous outcome, the illustrative calculation uses equal allocation between two arms, a two-sided significance level of 0.05, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

In plain language, 80% power means that, if the assumed effect and statistical assumptions were correct, a study of that planned size would have an 80% chance of producing a statistically significant result under the calculation’s model. The 90% column uses a higher chance of detecting the assumed effect and therefore gives a larger planning estimate. These are prospective planning illustrations based on an observed contrast, not observed power for this completed trial.

For example, planning around 100% of the observed primary effect gives 10,732 participants per arm for 80% power and 14,367 participants per arm for 90% power. The entries for 75% and 50% of the observed effect require larger per-arm estimates. That pattern is expected: smaller effects are harder to distinguish from random variation, so more participants are needed to detect them under otherwise unchanged assumptions.

These calculations should not be read as proof that the original trial was under-sized or over-sized. They use the observed effect as an input, and an observed estimate can be uncertain. They also simplify the design to equal allocation and a normal approximation. The registry record does not report whether the original design used the same assumptions, incorporated attrition, or allowed for any planned interim analysis.

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 = 0.007; pooled standard deviation σ = 0.183.
2. n = 2 × (1.96 + 0.842)² × 0.183² / 0.007² = 10,731.9, rounded up to 10,732 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 <- 0.00699999999999999                      # observed difference in means
sigma <- 0.183027962525711                     # 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(1513460)
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 = 10,732 (80% power), 14,367 (90% power)
 75% of observed effect: n per arm = 19,079 (80% power), 25,542 (90% power)
 50% of observed effect: n per arm = 42,928 (80% power), 57,468 (90% power)
power.t.test: 10732.9 
Simulated power at n = 10,732 per arm: 0.798 (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 registry record lists one primary endpoint and six secondary outcomes. It posts numerical secondary results for three outcomes, but the analyses listing contains no reported analyses for those outcomes. The record does not state whether the secondary endpoints were tested in a prespecified sequence, whether a family-wise error procedure was used, or whether any outcomes were considered confirmatory. It also does not report multiplicity-adjusted p-values or intervals.

Multiplicity matters when several outcomes or contrasts are tested. General statistical explanation: when more hypotheses are examined, the chance of at least one apparently unusual result under a collection of no-effect hypotheses can increase. A correction or prespecified testing hierarchy can help control that risk, but the appropriate approach depends on the intended claims and study plan. Since no adjustment method is reported, unadjusted secondary p-values should not be treated as if they accounted for all outcome testing.

The primary analysis population is the per-protocol set, with inclusion requiring baseline and week 12 values, at least one dose, and no major protocol or non-protocol deviations. The registry record does not report how many randomized participants were excluded from this set, the reasons for exclusion, or an all-randomized sensitivity analysis. The number of participants with an outcome varies across the posted secondary outcomes. The record does not explain all differences or give a missing-data method.

Missing outcomes can affect both the analyzed population and the precision of estimates. General statistical explanation: complete-case analyses rely on assumptions about why data are missing; alternative methods may be needed if missingness relates to treatment or outcome. No imputation approach, sensitivity analysis, or missing-data assumption is reported in the registry record.

The endpoint description names the mixed model and its covariates, but the registry record does not report additional statistical-plan details such as the significance threshold for the trial’s original analysis, interim analyses, the model’s handling of missing values, or the prespecified approach to secondary comparisons. These omissions limit assessment of whether the posted summaries follow the original 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: small intestinal obstruction (0.8%), pneumonia (0.8%), chronic obstructive pulmonary disease (0.8%), atrial fibrillation (0.8%), anaemia (0.4%).

For serious adverse events, the safety figures list 15 affected participants among 257 at risk in the NVA237 plus Flu/Sal group, 22 among 258 in the tiotropium plus Flu/Sal group, and 15 among 257 in the Flu/Sal group. The other-adverse-event figures list 114 among 257, 124 among 258, and 111 among 257, respectively. These are group-specific counts and denominators; the safety population differs from the primary per-protocol population.

The most frequently listed serious-event terms include small intestinal obstruction, pneumonia, chronic obstructive pulmonary disease, and atrial fibrillation, each reported as 0.8%. Anaemia and acute coronary syndrome are each reported as 0.4%. Those percentages describe the listed terms, not a treatment-effect estimate. The registry record does not report deaths in the safety results.

These counts describe events recorded in the study; they do not by themselves establish that a treatment caused an event. The record does not provide enough detail to compare event timing, severity beyond the serious classification, or individual clinical circumstances. Different at-risk counts and the absence of a reported adjusted safety comparison also limit direct interpretation. Safety findings should be considered descriptively and in the context of the full clinical record.

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

The posted primary summaries show similar mean changes in trough FEV1 in the two active add-on groups, with an unadjusted difference of 0.007 liters. The interval crosses zero, and the unadjusted p-value is 0.71. These results indicate considerable uncertainty about the direction and size of the contrast in the recalculated comparison. They do not establish that the treatments have equal effects, nor do they demonstrate that either treatment is superior.

The endpoint is a measured lung-function outcome over 12 weeks, not a complete account of symptoms, daily functioning, long-term outcomes, or safety. The registry also lists secondary measures that concern respiratory health status, rescue medication use, nighttime awakenings, and usual activities. Their posted unadjusted results vary, and the statistical plan for multiple secondary tests is not reported. They therefore do not justify a single broad conclusion across all aspects of the condition.

The primary analysis uses a per-protocol population with baseline and week 12 values and excludes participants with major deviations. It does not automatically represent the full randomized population. Further, the registry describes a covariate-adjusted mixed model but does not post its model-based estimate in the analyses listing. The recalculated comparison from arm summaries is not the same as that adjusted analysis.

Nothing in these results establishes clinical equivalence, non-inferiority, or a difference important to patients. The registry record does not state a clinical importance threshold or a non-inferiority margin. It also does not report a complete account of missing data, multiplicity handling, or the original sample-size justification. The results are best understood as a limited statistical description of the posted outcomes and analysis populations, not as a comprehensive assessment of treatment benefit or harm.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison should be read through more than its point estimate. The primary mean difference is close to zero, but the interval spans both negative and positive values. That combination conveys uncertainty about direction as well as size. A single p-value cannot capture that uncertainty, and a non-significant result is not evidence that the treatments are equivalent.

It also demonstrates the importance of distinguishing the analysis described in the protocol-level outcome information from a recalculation based on posted summaries. The registry states that the primary outcome used a mixed model with several covariates. The displayed unadjusted comparison does not reproduce that model. When a model-based result is not reported, readers should avoid treating a summary-statistic recalculation as the full trial analysis.

Population definitions matter too. The primary endpoint uses a per-protocol set requiring treatment exposure, baseline and week 12 measurements, and absence of major deviations. The safety counts use another population. Neither the overall enrollment nor the safety denominators can stand in for the primary analysis set. Without participant-flow details and missing-data methods, the effects of exclusions are difficult to evaluate.

Finally, the study includes multiple secondary endpoints and comparisons, while the registry record does not report a multiplicity strategy. This is a reminder that secondary findings are more credible when their place in a prespecified testing plan is clear. The planning illustrations also show how sample-size requirements depend strongly on the effect assumed: smaller effects call for larger planned groups. Such calculations are not a retrospective measure of the trial’s power, and the original design assumptions are not reported.

18. Limitations

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

The registry record leaves several trial-specific questions unresolved. The primary outcome is reported for a per-protocol population rather than an explicitly posted all-randomized analysis. Although the population definition is stated, the numbers and reasons for exclusions are not reported in the registry record. The record also does not give a participant-flow account or explain whether deviations were assessed without knowledge of outcomes.

The endpoint description says that a mixed model was used and names its covariates, but a model-based treatment estimate is not included in the reported analyses listing. The available contrast is an unadjusted recalculation from posted group summaries. The registry record does not report further model details, including handling of missing values, model diagnostics, or an adjusted interval. Thus, the posted recalculation should not be treated as the definitive trial-model result.

Only some of the listed secondary outcomes have numerical results posted, and the registry does not report an approach to multiplicity or identify a testing hierarchy. This limits the strength of conclusions from secondary p-values. The original sample-size assumptions, attrition allowance, interim-analysis plan, and statistical analysis plan are not reported in the registry record, so the planning illustrations cannot be compared directly with the original design rationale.

The safety summaries give counts and at-risk denominators, but the record does not report deaths or a detailed treatment-adjusted safety comparison. It also does not provide additional detail in these results on timing, event duration, or individual-level context. The registry record does not report site locations or broader information needed to judge how closely the enrolled population reflects other clinical settings.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy, Tolerability and Safety of NVA237 in Patients With Chronic Obstructive Pulmonary Disease — NCT01513460.
• Registry record last updated 2015-01-05; status last verified 2014-12.
• Results first posted 2015-01-05.
• 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

This completed, randomized, quadruple-masked, parallel-group phase 3 study enrolled 773 participants with COPD. It compared NVA237 50 µg once daily with tiotropium 18 µg once daily, with both added to Flu/Sal. The primary outcome was change from baseline in mean trough FEV1 at 12 weeks in a per-protocol population.

The posted arm means were 0.095 liters for NVA237 plus Flu/Sal and 0.102 liters for tiotropium plus Flu/Sal. The unadjusted recalculated mean difference was 0.007 liters, with an interval crossing zero and an unadjusted p-value of 0.71. The registry describes a covariate-adjusted mixed model, but its model-based estimate is not reported in the analyses listing.

The registry lists six secondary outcomes and posts numerical results for three. Safety counts are reported separately for the three treatment groups. Multiplicity handling, missing-data methods, the original sample-size assumptions, and several details of the primary model are not reported in the registry record. The primary summaries therefore describe the posted per-protocol data but do not establish equivalence or resolve the uncertainty around the treatment contrast.