NVA237 BID Versus Placebo Twelve-week Efficacy Study: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for NVA237 BID Versus Placebo Twelve-week Efficacy Study (NCT01715298), a randomized phase 3 study. The primary outcome is Change From Baseline in Standardized Area Under the Curve for Forced Expiratory Volume in One Second Post Dosing.

2. Clinical Question

3. Trial Design

This was a completed phase 3, randomized, double-blind, parallel-group, placebo-controlled study sponsored by Novartis Pharmaceuticals. It enrolled 432 participants with stable COPD. The study title describes a 12-week efficacy study, and the arm descriptions state that both NVA237 and placebo were inhaled for 12 weeks. The registry record lists the study start as 2012-11 and primary completion as 2013-12.

Random allocation and double masking are important design features for interpreting a comparison between treatment groups. Randomization is intended to make groups comparable on average at the start of a trial, while masking can reduce the influence of expectations on participant experience, care, and outcome assessment. Those are general design principles; details of how randomization was generated, how assignments were concealed, and who was masked are not reported in the registry record.

The primary efficacy analysis used the full analysis set, defined in the registry as randomized patients who received at least one dose of trial drug, analyzed according to their randomized assignment, and with both baseline and corresponding week 12 values. The posted primary arm results list 215 participants for NVA237 and 213 for placebo. The safety figures use separate at-risk groups: 216 for NVA237 and 214 for placebo. These are endpoint-specific analysis counts, not interchangeable descriptions of the same analysis population.

The planned enrollment is reported, but the original sample-size justification, target power, and assumptions used to design the trial are not reported in the registry record. The registry also does not report the detailed statistical analysis plan, including any prespecified covariate adjustment or interim monitoring. The planning illustrations based on the observed effect are separate from the trial's original design assumptions.

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 full analysis set (FAS): all randomized patients who received at least one dose of trial drug, patients were analyzed according to the treatment they were assigned to at randomization. analyzed participants had values at both baseline and the corresponding time frame, i.e. week 12

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 Area Under the Curve for Forced Expiratory Volume in One Second Post Dosing, measured over Week 12.

The primary endpoint was change from baseline in standardized area under the curve for forced expiratory volume in one second (FEV1) after dosing, measured at week 12. FEV1 is the volume of air forcibly exhaled in the first second of a breathing maneuver. The endpoint combines serial FEV1 measurements collected after the morning dose at the listed post-dose time points, from 5 min through 11:55 h.

The registry defines the endpoint as the mean change from baseline over that post-dose period, divided by the elapsed interval of 11 h 50 mins. Standardizing the area under the curve expresses the average change over the measurement period in liters, rather than presenting an accumulated area whose magnitude would depend on the duration of observation. A negative value is possible when the FEV1 area is smaller than at baseline.

A serial summary can represent the pattern across the post-dose period more fully than a single measurement at one time point. It may therefore be useful for comparing overall lung-function change during the specified interval. It does not describe every feature of the response curve: a mean standardized AUC can obscure variation at individual measurement times, and it is not itself a direct measure of symptoms or daily functioning. The registry lists several secondary measures addressing related outcomes, including health status and breathlessness.

7. Results Posted in the Registry

• NVA237: mean 0.12 versus -0.01 on control; difference 0.12 (95% CI 0.08 to 0.17), standardized effect d = 0.55; 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 Standardized Area Under the Curve (AUC(0-12h)) for Forced Expiratory Volume in One Second Post Dosing

• 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 0.12 versus 0.00 on control; difference 0.12 (95% CI 0.09 to 0.14), standardized effect d = 0.84; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for NVA237 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Health Status Assessed by St. George's Respiratory Questionnaire

• 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 -6.40 versus -1.20 on control; difference -5.20 (95% CI -8.17 to -2.23), standardized effect d = -0.35; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for NVA237 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Breathlessness Assessed by Transition Dyspnea Index

• 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 0.95 versus 0.48 on control; difference 0.47 (95% CI -0.30 to 1.24), standardized effect d = 0.12; z-test p = 0.233.
• 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 secondary outcomes cover related but distinct aspects of COPD, including post-dose lung function, health status, breathlessness, and rescue-medication use. The available numerical results show a broadly supportive direction for the day 1 lung-function summary and the week 12 health-status comparison, while the breathlessness comparison is less precise and its interval includes zero. This pattern is not uniform across every outcome, and measures with different scales and meanings should not be treated as interchangeable.

The day 1 AUC result is conceptually close to the primary endpoint because both summarize post-dose FEV1 over time. The week 12 St. George's Respiratory Questionnaire and Transition Dyspnea Index address patient-reported health status and breathlessness, rather than lung function itself. Their results can complement the primary endpoint by describing other dimensions, but they do not redefine what the primary endpoint measures. Numerical results for many of the other listed outcomes are not reported in the registry record.

Secondary findings generally carry less inferential weight when the registry does not report a prespecified testing hierarchy or adjustment for multiple comparisons. Testing many outcomes increases the chance that some results appear notable by chance. The registry lists 15 secondary outcomes, but multiplicity procedures and the complete analysis plan are not reported in the registry record. The unadjusted secondary comparisons should therefore be viewed as supportive or exploratory evidence rather than as independent confirmation of the primary result.

The outcomes also differ in analysis counts and measurement schedules. For example, the posted results use endpoint-specific participant counts, so a count for one secondary measure should not be assumed to apply to another. A coherent overall assessment would consider the outcome definitions, estimates, uncertainty, missingness, and prespecified analysis plan together. The registry record does not report enough detail to reconstruct that full assessment.

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

• Change From Baseline in Standardized Area Under the Curve (AUC(0-12h)) for Forced Expiratory Volume in One Second Post Dosing
• Change From Baseline in Standardized Area Under The Curve for Forced Expiratory Volume in One Second for Different Time Spans Post Dosing
• Change From Baseline in Forced Expiratory Volume in One Second at All Individual Timepoints
• Mean Trough Forced Expiratory Volume in One Second
• Change From Baseline in the Health Status Assessed by St. George's Respiratory Questionnaire
• Breathlessness Assessed by Transition Dyspnea Index
• Change From Baseline in Mean Number of Puffs of Rescue Medication Per Day
• Change From Baseline in the Percentage of Days Without Rescue Medication Use

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: it is expressed in liters and summarized by least-squares means. A continuous endpoint can take many values along a scale, unlike an outcome recorded only as an event or category. Comparing group means is one way to describe the average separation between randomized groups. It does not imply that each participant experienced the group-average change.

What does the standardized AUC represent?

Area under the curve (AUC) condenses a sequence of measurements over time into a single summary. In this trial, serial FEV1 measurements after the morning dose contribute to the week 12 AUC. The registry defines the standardized value as the mean FEV1 change from baseline over the measurement period, divided by 11 h 50 mins. Standardization puts the summary on the scale of the measured FEV1 change in liters. It supports a group-level comparison of the average response over the specified period, while not replacing the underlying time-specific measurements.

Using a standardized AUC is a general strategy for combining measurements taken at multiple times. It can capture a broad post-dose pattern, but the same average could arise from different time courses. The registry lists separate secondary outcomes for different time spans and individual time points, although numerical results for most of those outcomes are not reported in the registry record.

What are least-squares means?

Least-squares means, often called adjusted means, are estimates from a statistical model. Depending on the model, they can account for specified covariates or other design features. Their interpretation depends on the model and the population to which the model applies. The registry record names the summary as a least-squares mean but does not report the model specification, covariates, or adjustment details. It is therefore not possible to infer from that label alone exactly what adjustment was performed.

The comparison is expressed as a mean difference, with NVA237 relative to placebo. The posted estimate is 0.123 liters. The arm summaries are 0.115 liters for NVA237 and -0.008 liters for placebo. The comparison also gives an interval and an unadjusted p-value. A difference near zero would indicate little separation on the scale of the endpoint; the sign indicates which group has the larger estimated change under the comparison's stated ordering.

How should standard errors and intervals be understood?

A standard error describes the estimated sampling variability of an estimate under a statistical model. It is not the spread of individual participant measurements. A smaller standard error generally indicates a more precise estimate, while a larger one indicates more sampling uncertainty. The registry lists standard errors for the arm-level least-squares means, but does not report the full model output needed to assess all sources of uncertainty.

An interval around a mean difference conveys a range of values consistent with the estimate and its uncertainty under the calculation used. Intervals are useful because they show both direction and precision; a p-value alone does not show the range. The confidence level for the posted comparison interval is not reported in the registry record. No confidence level should be assumed from the interval endpoints alone.

What does the recalculated comparison mean?

The comparison is identified as a simple unadjusted recalculation from posted summary statistics. Such a recalculation can offer a transparent descriptive contrast, but it is not a substitute for a prespecified sponsor analysis that may use a model, adjustment, or analysis population not captured by the summary values. In the registry record, the discrepancy flag is false. If a discrepancy is present in a registry analysis, the sponsor's own analysis takes precedence; that caveat does not alter the distinction between a recalculated comparison and a reported model result.

The recalculation also uses an approximate pooled standard deviation inferred from the posted standard errors, as indicated by the approximation flag. In general, recovering a standard deviation from standard errors depends on assumptions about the underlying analysis and sample sizes. It should not be treated as a directly reported raw-data dispersion estimate. The registry does not report participant-level data or the full analysis output needed to independently reproduce a more detailed model.

Why does over-dispersion matter in general?

Over-dispersion occurs when observed variability is greater than a statistical model assumes. If a model understates variability, standard errors may be too small and intervals too narrow, making apparent evidence stronger than warranted. If variability is modeled appropriately, uncertainty is more realistically represented. This is a general statistical concern, not a reported finding about this trial. The registry record does not report an over-dispersion assessment or a method for addressing it.

What does an unadjusted p-value establish?

The primary comparison's p-value is unadjusted. In general, a p-value evaluates how unusual the observed data, or more extreme data, would be under a specified null model. It does not measure the size or clinical relevance of a difference, and it does not give the probability that a null hypothesis is true. A small p-value should be read alongside the effect estimate, interval, endpoint definition, analysis population, and the analysis plan.

These results are based on a randomized comparison, but the posted statistical summary does not provide all details needed to evaluate the original model and its assumptions. In particular, the analysis specification, missing-data procedures, prespecified testing hierarchy, and multiplicity adjustment are not reported in the registry record. Those omissions limit how far the posted summary can support a complete audit of the inferential procedure.

11. Confidence Intervals and Precision

The primary comparison estimate is 0.123 liters, with an interval from 0.081 to 0.165. This interval is above zero, so the recalculated comparison is compatible with a positive difference under the calculation used. Its endpoints also indicate that the estimate is not a single exact value: uncertainty remains about the magnitude of the group contrast.

An interval is a precision summary, not a guarantee that the true value lies within its endpoints. In general, an interval reflects sampling variability and the assumptions of the method used to calculate it. A narrower interval indicates greater precision than a wider interval on the same scale, while the interval's location indicates which values are compatible with the estimate. The confidence level for the posted interval is not reported in the registry record, so its nominal coverage cannot be assessed from the record alone.

The arm-level least-squares means have standard errors of 0.015 liters in each group. Standard errors quantify uncertainty in estimated means, not the range of individual outcomes. A participant's measurement may be much closer to or farther from the group mean than the standard error suggests. The posted summary does not give the raw distribution or model details needed to evaluate other features of variability.

Precision also depends on the analysis population and handling of missing observations. The primary population requires baseline and week 12 values, but the registry record does not describe a missing-data model or sensitivity analysis. The interval should therefore be interpreted as uncertainty under the posted recalculation, not as a complete account of uncertainty from every possible source.

12. Planning a Similar Trial: Sample Size

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

The planning illustrations translate an observed comparison into hypothetical future-study sizes under stated assumptions. For these continuous outcomes, the figures are participants per arm, not total events. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to a stated fraction of the observed effect. The original design assumptions for this trial are not reported in the registry record.

The 80% power column means the hypothetical design would have an 80% probability of detecting the specified effect at the stated significance level, if the planning assumptions and effect were correct. The 90% power column uses a higher probability of detection under those same assumptions. These are planning concepts, not guarantees about a future study, and they do not describe the probability that the observed result is true.

For the primary endpoint, planning for 100% of the observed effect gives 52 participants per arm for 80% power and 70 participants per arm for 90% power. Planning for 75% of the observed effect gives 93 participants per arm for 80% power and 124 participants per arm for 90% power. Planning for 50% of the observed effect gives 208 participants per arm for 80% power and 279 participants per arm for 90% power. The pattern illustrates why smaller effects need more participants to detect under the same assumptions.

These figures are not observed power. They are sample-size planning illustrations calculated from the observed effect, and the observed effect itself may differ from the effect a later study aims to detect. They should not be read as a reconstruction of why this trial enrolled its planned population.

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 = 0.123; pooled standard deviation σ = 0.224.
2. n = 2 × (1.96 + 0.842)² × 0.224² / 0.123² = 52.0, rounded up to 52 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 <- 0.123                      # observed difference in means
sigma <- 0.223822159345505                     # 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(1715298)
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 = 52 (80% power), 70 (90% power)
 75% of observed effect: n per arm = 93 (80% power), 124 (90% power)
 50% of observed effect: n per arm = 208 (80% power), 279 (90% power)
power.t.test: 53 
Simulated power at n = 52 per arm: 0.793 (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 tests are conducted for several outcomes, time points, or contrasts. Even if each test uses a conventional significance threshold, the chance of at least one apparently notable result can increase as the number of tests grows. Common general approaches include defining a hierarchy of hypotheses, adjusting significance thresholds, or treating secondary analyses as exploratory. The registry record does not report a multiplicity adjustment, testing hierarchy, or detailed statistical analysis plan.

The primary endpoint is identified, which gives it a clearer interpretive role than the secondary outcomes. However, the registry record does not report whether the primary test was part of a larger family of confirmatory tests or how secondary outcomes were intended to be interpreted. The secondary p-values listed in the available results are unadjusted. Their strength should not be judged as if each were the sole prespecified test.

The full analysis set includes randomized patients who received at least one dose and had both baseline and week 12 values for the endpoint. This definition identifies who contributes to the posted primary analysis, but it does not explain what happened to randomized participants without an endpoint value. The registry record does not report the amount or pattern of missing primary data, the reasons for missingness, an imputation approach, or sensitivity analyses.

In general, complete-case analysis can be vulnerable when the chance of a missing measurement is related to a participant's outcome or condition. The direction and size of any resulting bias cannot be determined without information about missingness and the analysis methods. The registry does not report whether the least-squares model used additional observations, how repeated measurements were handled, or whether any alternative analysis populations were evaluated.

The registry defines analysis according to randomized assignment, but also requires receipt of at least one dose and an observed baseline and week 12 value for the primary measure. That operational definition should be kept in view when interpreting the results. Protocol deviations, exclusions, and sensitivity checks are not reported in the registry record.

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 0.9% 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 (1.4%), spinal compression fracture (0.5%), haemoptysis (0.5%), pulmonary mass (0.5%), acute myocardial infarction (0.5%).

The registry reports serious adverse events for groups at risk of 216 in the NVA237 arm and 214 in the placebo arm. It lists 9 serious adverse events for NVA237 and 5 for placebo. These figures describe the posted serious-event counts; the registry record does not provide an event-level account or establish that every event was caused by the assigned treatment.

Among the serious-event terms listed, chronic obstructive pulmonary disease is reported at 1.4%. Spinal compression fracture, haemoptysis, pulmonary mass, acute myocardial infarction, and angina pectoris are each listed at 0.5%. The registry does not give further context in the registry record about the denominator or attribution for each listed term, so the percentages should be read as registry-reported values rather than recalculated rates.

The deaths field is not reported in the registry record. The available serious adverse event figures are not a full assessment of safety: they do not by themselves describe non-serious events, event timing, exposure duration, or causal assessment. They should be read descriptively and alongside the registry's stated study scope, not as a conclusion about safety.

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

The posted primary result describes a difference in average change in a specific lung-function summary between randomized groups at week 12. It does not describe every participant's response, every moment after dosing, or every aspect of COPD. The standardized FEV1 AUC summarizes serial measurements over a defined post-dose interval; it is not a direct measure of daily symptoms, health status, or long-term disease course.

The point estimate and interval indicate the direction and precision of the recalculated comparison. They do not establish how important the magnitude is to patients. A clinically important threshold for this endpoint is not reported in the registry record. The statistical result should therefore not be converted into a claim about meaningful benefit or lack of benefit without additional context.

The trial was randomized and double-blind, features that can strengthen a group comparison when implemented appropriately. The registry record does not report detailed methods for sequence generation, allocation concealment, masking procedures, model specification, or missing-data handling. Those details matter when judging the reliability and generalizability of a result, but their absence from the registry summary does not demonstrate that methods were or were not used.

The primary endpoint result is not a complete evaluation of the intervention. Secondary outcomes address other measures, and the available pattern is not identical across them. The registry does not report a multiplicity strategy or full results for every listed outcome. Safety counts likewise require careful interpretation and do not establish causation. The registry entries in the registry support a description of the posted comparisons, not medical advice or a decision for an individual patient.

17. Why This Trial Matters Statistically

This trial illustrates why endpoint definition matters. A serial FEV1 AUC converts measurements taken at multiple post-dose times into one continuous summary. That can make a group comparison concise, but it also means the result depends on the selected time window, measurement schedule, baseline definition, and standardization. The registry specifies these features sufficiently to explain the primary measure's general construction.

The comparison also shows why an estimate should be read together with its uncertainty. The mean difference communicates the size and direction of the group contrast, while the interval conveys uncertainty around that estimate. A p-value alone would not show the range of plausible magnitudes or whether the interval includes zero. Statistical evidence and clinical importance remain separate questions, and the registry does not state a clinically important threshold.

Analysis populations and missing-data rules are part of the estimand, not administrative details. The primary population requires a baseline and week 12 observation, while the registry does not describe missingness or sensitivity analyses. Readers therefore need to distinguish the randomized design from the group of participants contributing to a particular posted endpoint.

Finally, multiple outcomes provide a broader view but increase interpretive complexity. Lung function, health status, and breathlessness are related yet distinct, and unadjusted secondary comparisons should not be treated as equivalent confirmatory evidence. The registry's incomplete reporting of multiplicity and modeling choices demonstrates why a compact result summary cannot replace a full statistical analysis plan and complete report.

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 detailed statistical model used for the least-squares means, including covariates and repeated-measure handling. The primary comparison available in the analysis is a recalculated unadjusted contrast from summary statistics, and the pooled standard deviation used for standardized effect calculations is approximate. These features limit independent verification of the sponsor's full analysis.

The primary analysis requires baseline and week 12 values, but missing-data counts, reasons, methods, and sensitivity analyses are not reported in the registry record. The extent to which the analyzed population represents all randomized participants therefore cannot be assessed from these registry entries alone. Analysis counts also vary by outcome, so findings should be interpreted on an endpoint-specific basis.

The registry lists 15 secondary outcomes, while numerical results are available for only a subset in the registry record. A complete outcome-level synthesis is not possible. The registry does not report a multiplicity strategy, so unadjusted secondary findings have limited confirmatory interpretation. The confidence level for comparison intervals is also not reported in the registry record.

Further details about eligibility criteria, baseline characteristics, treatment adherence, protocol deviations, randomization procedures, and masking procedures are not reported in the registry record. These omissions limit assessment of population comparability, implementation, and generalizability. The study describes a 12-week comparison in stable COPD; longer-term outcomes are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: NVA237 BID Versus Placebo Twelve-week Efficacy Study — NCT01715298.
• Registry record last updated 2015-03-11; status last verified 2015-03.
• Results first posted 2015-03-11.
• 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

The registry describes a completed phase 3 randomized, double-blind, parallel-group study comparing inhaled NVA237 with inhaled placebo over 12 weeks in stable COPD. Enrollment was 432, and the primary endpoint was change from baseline in standardized post-dose FEV1 AUC at week 12.

The posted primary least-squares mean changes were 0.115 liters for NVA237 and -0.008 liters for placebo. The recalculated unadjusted mean difference was 0.123 liters, with an interval from 0.081 to 0.165 and p < 0.001. Interpretation is limited by unreported model and missing-data details, and by the absence of a reported multiplicity plan. The secondary and safety findings provide additional context but do not replace the primary endpoint or establish clinical importance.