Efficacy, Safety and Tolerability 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, Safety and Tolerability of NVA237 in Patients With Chronic Obstructive Pulmonary Disease (NCT01566604), a randomized phase 3 study. The primary outcome is Trough Forced Expiratory Volume in One Second (FEV1).

2. Clinical Question

FEV1 is a measure of the volume of air a person can forcefully exhale in one second. The trial’s primary endpoint focused on trough FEV1: the average of measurements taken 23 h 15 min and 23 h 45 min after dosing. This timing evaluates lung function near the end of the dosing interval, rather than shortly after a dose.

The registry describes a randomized, double-blind, placebo-controlled, parallel-group study. Its stated treatment period was 26 weeks, while the primary endpoint’s stated timeframe was 12 weeks. The record lists additional lung-function, symptom, rescue-medication, and exacerbation outcomes. The central statistical question for the primary endpoint is whether the adjusted group means differed at the specified assessment, and how precisely that difference was estimated.

3. Trial Design

This was a phase 3, randomized, quadruple-masked, parallel-group study of NVA237 and placebo in people with COPD. The official title describes a 26-week treatment study; the brief summary describes once-daily inhaled NVA237 at 50 µg for moderate to severe COPD. Both the active treatment and placebo were delivered through a single-dose dry powder inhaler. The registry lists Novartis Pharmaceuticals as sponsor and the trial status as completed.

The registry enrollment was 460. The primary endpoint is reported at 12 weeks, whereas the overall treatment period and several secondary outcomes extend to 26 weeks. The record gives March 2012 as the study start and June 2013 as primary completion. These are registry dates, not a description of each participant’s follow-up.

The stated primary analysis used the full analysis set, defined in the record as randomized participants who received at least one dose of study medication. For the endpoint analysis, participants also needed both baseline and week 12 values. The posted primary arm summaries list 296 participants for NVA237 and 147 for placebo. These analysis counts should be read as reported for that endpoint, rather than assumed to be the same as the registry enrollment or the counts used for other outcomes. Secondary and safety summaries use their own reported counts.

Randomization is intended to allocate participants to treatment groups by chance, while masking is intended to limit the influence of treatment knowledge on care, measurement, and assessment. The registry identifies the allocation as randomized and masking as quadruple, but does not report which trial roles were masked. The parallel-group design means the record compares groups assigned to different study treatments over the treatment period.

The registry record does not report the original sample-size justification, the planned handling of missing data, or the detailed sequence of statistical analyses. Those omissions limit what can be inferred about the trial’s design assumptions beyond the information stated in the record.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The number of participants considered for the analysis was from the full analysis set (randomized participants who received at least one dose of study medication). However, participants analyzed had both baseline and week 12 values.

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 One Second (FEV1), measured over 12 weeks.

The primary endpoint was trough forced expiratory volume in one second (FEV1), measured in liters, at 12 weeks. FEV1 measures how much air can be forcefully exhaled in one second. It is a lung-function measure used in COPD studies to quantify airflow limitation and to assess change or between-group differences during treatment.

The registry defines baseline FEV1 as the average of measurements taken 45 min and 15 min before the first study dose on day 1. Trough FEV1 is the mean of measurements at 23 h 15 min and 23 h 45 min after dosing. Central spirometry was conducted according to ATS/ERS standardization. The near-end-of-interval timing is relevant because it assesses lung function before the next once-daily dose, rather than the peak response immediately after inhalation.

The reported endpoint statistic is a least-squares mean, not simply an unadjusted arithmetic average. The registry says the analysis used a mixed model with treatment as a fixed effect and included baseline FEV1, FEV1 before and after inhalation of a short-acting bronchodilator, and baseline inhaled corticosteroid use as covariates. Adjusted means aim to compare treatment groups after accounting for the listed variables under that model.

Using a prespecified endpoint can focus interpretation on a defined measurement and assessment time. The registry record does not report why this particular endpoint and time point were selected, or the clinical threshold considered important for interpreting a difference.

7. Results Posted in the Registry

• NVA237: mean 1.20 versus 1.06 on control; difference 0.14 (95% CI 0.10 to 0.18), standardized effect d = 0.64; 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 Daily Rescue Medication Use (Number of Puffs)

• 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:
  • NVA237: mean -0.77 versus -0.55 on control; difference -0.22 (95% CI -0.70 to 0.26), standardized effect d = -0.08; z-test p = 0.366.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NVA237 and the control. The interval gives the range of effects that remain compatible with the data.

Number of Moderate and Severe COPD Exacerbations

• 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 deviations.
• Result:
  • NVA237: mean 0.20 versus 0.30 on control; difference -0.10 (95% CI -0.21 to 0.01), standardized effect d = -0.19; z-test p = 0.065.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NVA237 and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad range of secondary outcomes, covering dyspnea, rescue medication, spirometry, COPD symptoms, and exacerbations. Numerical summaries are described for change in daily rescue medication use and the mean number of moderate and severe exacerbations. The other listed outcomes do not have numerical results reported in the registry record in the information, so their pattern cannot be evaluated from the outcome list alone.

For the two secondary comparisons with numerical results, the estimated contrasts are in the negative direction, but each confidence interval includes zero. Their unadjusted p-values are 0.366 for change in rescue medication use and 0.065 for exacerbations. These results are less conclusive than the primary trough FEV1 comparison, whose confidence interval excludes zero. They do not establish that the secondary outcomes were unchanged; the intervals allow for a range of possible differences, including no difference.

Secondary endpoints can provide useful context about whether a primary measurement is accompanied by patterns in symptoms, medication use, or clinical events. They do not automatically confirm or invalidate the primary result. Different endpoints capture different aspects of COPD, use different measurement scales, and may have different levels of variability or completeness. A consistent overall interpretation would require the relevant estimates, uncertainty, and analysis plans across outcomes.

Unadjusted secondary results carry less weight as confirmatory evidence when many outcomes are examined. Without a reported multiplicity strategy, individual p-values do not account for the number of comparisons considered. The registry lists 10 posted secondary outcomes, but does not report a multiplicity adjustment or identify a hierarchy for interpreting them. Accordingly, the secondary findings are best treated as descriptive or exploratory evidence rather than as a stand-alone set of definitive tests.

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

• Transition Dyspnea Index (TDI) Score
• Change From Baseline in Daily Rescue Medication Use (Number of Puffs)
• 24h Trough FEV1
• FEV1 and Forced Vital Capacity (FVC)
• Peak FEV1
• Standardized FEV1 Area Under the Curve (AUC(5 Min-4 h)) Post-dose
• Change From Baseline in Chronic Obstructive Pulmonary Disease (COPD) Symptoms (Cough, Wheezing, Shortness of Breath, Sputum Volume, Sputum Color and Night Time Awakenings)
• Time to First Moderate or Severe COPD Exacerbation

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of a group mean. Rather than comparing only the observed group averages, the analysis uses a statistical model to account for selected characteristics included as covariates. The registry identifies treatment as a fixed effect and lists baseline FEV1, FEV1 before inhalation of a short-acting bronchodilator, FEV1 45 min after that inhalation, and baseline inhaled corticosteroid use as covariates. The treatment contrast therefore reflects the comparison made by that model, conditional on its specification and the data available for analysis.

Adjustment can improve comparability in an analysis and can account for predictors of the outcome, but it does not remove all uncertainty or guarantee that a model is correct. Interpretation depends on the chosen covariates, the assumptions of the model, and the way incomplete observations are handled. Details about residual checks, model fit, covariance structure, and missing-data methods are not reported in the registry record.

Why measure trough FEV1?

The endpoint is defined as the mean of measurements made 23 h 15 min and 23 h 45 min after dosing. This is a near-end-of-interval assessment for a once-daily treatment. Averaging two close measurements is part of the registry’s endpoint definition; it is not a separate outcome. Central spirometry was conducted according to ATS/ERS standardization, which describes the measurement approach in the record. The registry does not report further details of quality control or the specific spirometry procedures beyond that description.

What does the standard error tell the reader?

The primary arm summaries report standard errors of 0.013 liters for NVA237 and 0.016 liters for placebo. A standard error describes the statistical uncertainty around an estimated mean: smaller standard errors indicate less sampling variability in the estimate, under the assumptions of the analysis. It is not the spread of individual participant measurements. A standard deviation, by contrast, describes variability among observations. Confusing these measures can make a precise estimate appear to imply that individual outcomes are tightly clustered, which does not follow from the standard errors alone.

The primary record reports least-squares means and standard errors, alongside a treatment contrast and its confidence interval. The uncertainty of the contrast is not determined by simply reading either group’s standard error in isolation; it depends on the model and the relationship between estimates. The confidence interval for the contrast is the more direct summary of uncertainty about the between-group estimate.

How should the p-value be read?

The posted primary p-value is p < 0.001. In general, a p-value measures how incompatible the observed data, or data more extreme, are with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. The registry labels the comparison p-value unadjusted. The record does not report whether any multiplicity adjustment was planned or applied to the primary or secondary outcome family.

For the secondary comparisons, the p-values are also identified as unadjusted. They should be read as individual comparisons, not as evidence that a prespecified family-wide error rate was controlled. The distinction matters when many outcomes or analyses are considered, because repeated testing can increase the chance of at least one apparently notable result even when none of the underlying effects is real.

What is the role of a confidence interval?

A confidence interval gives a range of values compatible with the observed data under the interval’s statistical procedure. Its width reflects precision: narrower intervals indicate greater precision, and wider intervals indicate greater uncertainty. The interval does not contain all possible true values with a stated probability after the data have been observed. Rather, the confidence level describes the long-run performance of the method under its assumptions. The registry reports the primary contrast with a 95% confidence interval.

For a difference in means, zero represents no between-group difference. An interval that includes zero is compatible with no difference under that interval procedure; an interval entirely on one side of zero indicates a direction of difference under the same framework. This interpretation does not, by itself, determine clinical relevance or resolve the effects of multiple testing, model assumptions, or missing data.

Why can over-dispersion matter?

General statistical note: count outcomes can vary more than a simple count model expects. This is called over-dispersion. When it is present, a model that assumes less variability than the data contain may understate uncertainty and make intervals or tests appear more decisive than warranted. The registry reports the number of exacerbations as a mean with a standard deviation, but does not report a count-model analysis or an over-dispersion assessment. The posted mean comparison should therefore be read as the stated summary comparison, not as evidence that a count-model assumption was tested.

The record also lists time to first moderate or severe COPD exacerbation as a secondary outcome, but no numerical time-to-event analysis is reported in the registry record in the outcome information described. Time-to-event methods account for when an event occurs and can also account for incomplete follow-up in particular ways. Without a posted analysis, no such result or method should be inferred.

11. Confidence Intervals and Precision

The primary estimate is a 0.141-liter mean difference in trough FEV1, with a 95% confidence interval from 0.1 to 0.182 liters. The interval is the main guide to the statistical precision of this estimate: it gives a range of values compatible with the data and the analysis procedure. Because both limits are above zero, the interval does not include no difference. Its limits also indicate that the estimate is not a single exact value; the true effect compatible with the data could be smaller or larger than the point estimate.

Precision is distinct from clinical importance. A confidence interval can be relatively informative about the location of an estimate without answering whether that range is meaningful to patients or clinicians. The registry record does not report a minimal clinically important difference or another clinical threshold for trough FEV1. It is therefore not possible to classify the entire interval against such a threshold using the record alone.

The primary arm standard errors are 0.013 liters for NVA237 and 0.016 liters for placebo. They describe uncertainty in the reported least-squares means, not the range of individual participant measurements. The model-based contrast has its own interval, which is the appropriate uncertainty summary for the group difference.

The secondary rescue-medication contrast has a 95% confidence interval from -0.697 to 0.257, and the exacerbation contrast has a 95% confidence interval from -0.206 to 0.006. Both include zero, so the corresponding summaries do not rule out no difference using those intervals. Their estimates should not be treated as precise evidence of a nonzero effect. The registry record does not report adjusted confidence intervals for these secondary comparisons or a multiplicity procedure that would alter their interpretation.

12. Planning a Similar Trial: Sample Size

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

The sample-size table and curve are planning illustrations based on the observed effect, not a reconstruction of the trial’s original design calculation. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The planning scenarios use the stated fractions of the observed effect: 100%, 75%, and 50%. For these continuous-outcome illustrations, the figures are participants per arm, not total participants. The record’s general note says time-to-event calculations, if present, give total events; the displayed planning examples for the outcomes are per-arm participant counts.

The 80% power column gives the number of participants per arm that the illustration estimates would be needed to have an 80% chance of detecting the assumed effect under those planning assumptions, if that effect were the true one. The 90% power column uses a higher target chance of detection, so it generally requires more participants per arm. Power is a design property calculated for a specified effect, analysis, significance level, and sample size; it is not a probability that a particular study result is correct.

Smaller effects are harder to distinguish from random variation and therefore require more participants for the same target power, all else equal. This is why the planning values increase when the scenario uses a smaller fraction of the observed effect. The observed effect is only an estimate and may not be a stable or realistic planning target, especially when it comes from a single trial. These figures are not observed power.

The registry record does not report the trial’s original sample-size justification, including the effect size, power target, or other assumptions used when planning enrollment. The illustrations should therefore be read as hypothetical planning aids rather than as evidence about what assumptions guided the completed trial.

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 = 0.141; pooled standard deviation σ = 0.220.
2. n = 2 × (1.96 + 0.842)² × 0.220² / 0.141² = 38.3, rounded up to 39 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 <- 0.141                      # observed difference in means
sigma <- 0.220329283567298                     # 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(1566604)
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 = 39 (80% power), 52 (90% power)
 75% of observed effect: n per arm = 69 (80% power), 92 (90% power)
 50% of observed effect: n per arm = 154 (80% power), 206 (90% power)
power.t.test: 39.3 
Simulated power at n = 39 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

Multiplicity arises when more than one hypothesis is tested. If a study examines several outcomes or several analyses, the chance of at least one apparently positive result can increase unless the testing strategy is planned and interpreted accordingly. The registry lists multiple secondary outcomes, including dyspnea, rescue medication use, several lung-function measures, COPD symptoms, and exacerbation outcomes. It does not report a family-wise error strategy, a hierarchy among secondary endpoints, or an adjustment to the secondary p-values.

The primary comparison is reported with p < 0.001, while the two secondary comparisons with numerical results have unadjusted p-values. The primary endpoint is identified as primary, but the registry record does not explain whether any multiplicity procedure was applied to the primary analysis or how the secondary outcome family was intended to be interpreted. The secondary p-values should therefore not be read as adjusted evidence across all outcomes.

Missing-data handling is also not reported in the registry record. The primary analysis population is defined as randomized participants who received at least one dose, and the endpoint analysis included participants with both baseline and week 12 values. That description clarifies who contributed to the reported endpoint, but does not say how participants without the required measurements were handled, whether values were imputed, or whether sensitivity analyses assessed alternative assumptions. The record also does not report the extent or reasons for missing data.

For the primary outcome, the model is described as a mixed model, but the registry does not report details such as its covariance structure, assumptions about missing observations, or model diagnostics. These omissions prevent a full appraisal of how robust the estimate is to incomplete follow-up and model specification.

The record identifies a full analysis set but does not report a per-protocol analysis or other analysis-population comparisons. It also does not report interim analyses or stopping rules. These items should be treated as not reported in the registry record, rather than assumed absent from the trial’s conduct. Together, the missing information limits a complete assessment of confirmatory testing and robustness, even though the primary estimate and its interval are reported.

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 (5.8%), pneumonia (1.9%), lung infection (0.7%), hypoproteinaemia (0.7%), respiratory failure (0.7%).

The safety summaries report participants affected by serious adverse events and other adverse events, with separate numbers at risk for NVA237 and placebo. For serious adverse events, the posted counts are 17 of 305 participants at risk in the NVA237 group and 14 of 154 in the placebo group. For other adverse events, the corresponding counts are 81 of 305 and 48 of 154. These are descriptive counts from the registry record, not adjusted comparisons.

The record lists serious adverse-event terms including chronic obstructive pulmonary disease at 5.8%, pneumonia at 1.9%, lung infection at 0.7%, hypoproteinaemia at 0.7%, respiratory failure at 0.7%, and acute pancreatitis at 0.6%. The registry record does not report deaths in these safety summaries. It also does not provide a statistical comparison of the event counts, a risk-adjusted analysis, or enough information to determine relatedness from these figures alone.

Safety counts need context: the groups have different reported numbers at risk, and event counts do not describe event severity, timing, recurrence, or causality. These summaries should be interpreted as reported adverse-event information, not as proof that an event was caused by or unrelated to study treatment.

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

The registry record supports a statistical description of the primary endpoint: the adjusted week 12 trough FEV1 mean was higher in the NVA237 group than in the placebo group, with a reported mean difference of 0.141 liters and a 95% confidence interval from 0.1 to 0.182 liters. The interval excludes zero, and the posted unadjusted p-value is p < 0.001. This is evidence of a between-group difference under the reported model and its assumptions.

The result does not, by itself, establish the clinical importance of the difference. The registry record does not state a threshold for a meaningful change in FEV1, so the estimate cannot be judged against such a threshold from the record alone. Statistical significance describes evidence in relation to a null hypothesis; it is not a direct measure of benefit, patient experience, or practical importance.

The posted secondary summaries are less conclusive: their confidence intervals include zero, and their p-values are unadjusted. Other listed secondary outcomes do not have numerical summaries reported in the registry record in the information described. The record also does not report multiplicity handling, detailed missing-data methods, or the original sample-size justification. These limitations matter when judging the overall evidence and how broadly the primary finding can be interpreted.

The safety information provides counts of participants affected by serious and other adverse events, along with selected serious-event terms. It does not establish whether events were caused by treatment, and the record does not provide a comparative safety analysis that would support a causal conclusion from these counts alone.

More broadly, a randomized, masked comparison is designed to support a treatment-group contrast, but interpretation still depends on trial conduct, completeness of follow-up, measurement quality, analysis choices, and the relevance of the enrolled population to the question of interest. The registry summary is not a substitute for the full protocol or a detailed clinical report. It describes the posted outcome results and their statistical precision without resolving every clinical or methodological question.

17. Why This Trial Matters Statistically

This trial illustrates why a treatment estimate should be read together with its endpoint definition, analysis model, and confidence interval. Trough FEV1 is tied to specific post-dose measurement times, while the reported least-squares means come from a model that accounts for stated baseline covariates. That context matters: the estimate is not simply an unadjusted comparison of two observed averages.

The primary result also shows the distinction between statistical evidence and clinical interpretation. The reported confidence interval excludes zero, but the record does not give a threshold for a clinically important difference. A small p-value and an interval on one side of zero describe statistical compatibility; they do not determine the value of the difference to patients or establish how it should be weighed against other outcomes.

The contrast between the primary and secondary summaries is instructive. The primary interval excludes zero, while the two reported secondary intervals include zero. This does not make the secondary outcomes irrelevant; it highlights that different measures can provide different levels of precision and evidence. At the same time, the registry’s list of many outcomes makes multiplicity important, and the record does not describe a family-wide testing strategy.

Finally, the record demonstrates the limits of registry summaries for evaluating a completed trial. It gives an analysis population definition and some model details, but not the original sample-size assumptions, missing-data approach, or a full account of secondary analyses. Statistical interpretation is strongest when the estimate is considered alongside those design and analysis details, and when limitations in the available record are kept distinct from conclusions about the treatment itself.

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 primary result is reported for participants with both baseline and week 12 values, but the registry record does not report the amount or pattern of missing data or the method used to address missing observations. The reported analysis population definition alone cannot show whether missingness could have affected the estimate.

The registry specifies a mixed model and names its covariates, but does not report further model details or diagnostics. The primary arm counts differ from the counts in the secondary and safety summaries; the record gives those endpoint-specific counts but does not explain the differences. They should not be treated as interchangeable analysis populations.

The primary endpoint has an unadjusted p-value and a confidence interval, while the record does not describe a multiplicity strategy for the collection of secondary outcomes. Numerical results are available for only some of the outcomes listed. As a result, the full pattern across secondary endpoints and the status of those analyses as confirmatory or exploratory cannot be established from the registry record.

The two reported secondary comparisons are summaries of continuous outcomes, including the number of exacerbations expressed as a mean and standard deviation. The record does not provide a count-model analysis or details of how event counts were modeled. It also does not provide a numerical analysis for the listed time-to-first-exacerbation outcome.

Finally, the record does not report a clinical importance threshold for the FEV1 difference, the original sample-size rationale, interim analyses, or detailed safety comparisons. These omissions do not negate the posted estimates, but they limit conclusions about clinical relevance, robustness, and the broader balance of outcomes.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy, Safety and Tolerability of NVA237 in Patients With Chronic Obstructive Pulmonary Disease — NCT01566604.
• Registry record last updated 2014-08-08; status last verified 2014-07.
• Results first posted 2014-08-08.
• 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

NCT01566604 was a completed phase 3 randomized, quadruple-masked, parallel-group study comparing once-daily NVA237 50 µg with placebo in COPD. The official title describes 26 weeks of treatment. Registry enrollment was 460.

The primary endpoint was trough FEV1 in liters at 12 weeks. The reported least-squares mean difference was 0.141 liters, with a 95% confidence interval from 0.1 to 0.182 liters and p < 0.001. The analysis used a mixed model with treatment and the listed baseline covariates.

Numerical secondary summaries are reported for change in daily rescue medication use and mean exacerbation counts. Their confidence intervals include zero, and their p-values are unadjusted. Serious and other adverse-event counts are also posted. The registry record does not report the original sample-size justification, detailed missing-data methods, or a multiplicity strategy.