A Study of the Efficacy and Safety of NVA237 in Patients With Moderate to Severe COPD: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Efficacy and Safety of NVA237 in Patients With Moderate to Severe COPD (NCT02371629), a randomized phase 4 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1) at Week 12.

2. Clinical Question

The study was described as a post-authorization commitment to the European Medicines Agency. Its stated purpose was to evaluate efficacy and safety of NVA237 dosing once or twice daily in patients with COPD. The clinical question is therefore a regimen comparison, not a comparison of NVA237 with no active treatment: both groups received NVA237, with evening placebo used in the once-daily arm to support masking. The registry record also identifies secondary measures involving FEV1 over time, respiratory quality of life, dyspnea, and rescue-medication use. Those outcomes can add context, but the primary question remains the Week 12 trough FEV1 contrast.

3. Trial Design

This was a Phase 4, randomized, double-blind, parallel-group study of NVA237 in patients with moderate to severe COPD. The registry reports enrollment of 776 and a planned treatment period of 26 weeks. The record lists the study as completed. Its stated start date is 2015-06-24, and its primary completion date is 2016-11-16. Novartis Pharmaceuticals is listed as the sponsor.

The two treatment groups differed in dose schedule. The twice-daily group received a 22 μg NVA237 capsule in the morning and evening. The once-daily group received a 44 μg NVA237 capsule in the morning and a placebo capsule in the evening. Both groups received salbutamol as rescue medicine. The once-daily regimen therefore included an evening placebo, consistent with the stated double-blind design. The registry lists random allocation, double masking, and a parallel-group model.

The primary endpoint was change from baseline in trough FEV1 at Week 12, measured in liters. The primary analysis used a mixed model for repeated measures and reported a net mean difference between groups. The endpoint description says spirometry followed American Thoracic Society standards and defines trough FEV1 using measurements taken after dosing. It also describes baseline as an average of two measurements on Day 1.

The registry reports enrollment and outcome-specific analysis counts, which need not describe the same analysis population or be interchangeable. The original design assumptions, including any planned sample-size justification, are not reported in the registry record. The record also does not state a detailed protocol for interim analyses or give a complete account of how missing outcome measurements were handled. Those absences limit reconstruction of the original planning and analysis decisions from the registry alone.

4. Participant Flow and Accounting

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

Before assignment: A total of 1020 patients were screened for participation in this study; 776 were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) included all randomized patients who received at least one dose of study drug. Following the intent-to-treat principle, patients in the FAS were analyzed according to the treatment to which they were randomized. Patients with evaluable data at both baseline and week 12 were included in this analysis.

5. Baseline Characteristics

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

Population: Randomized set

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1) at Week 12, measured over Baseline, Week 12.

Trough forced expiratory volume in one second (FEV1) is the amount of air a person can forcefully exhale in the first second of a breath, measured at the specified trough time after dosing. The trial’s primary endpoint was the change from baseline in trough FEV1 at Week 12, expressed in liters. The record defines trough FEV1 as the mean of measurements taken 23 hours 15 minutes and 23 hour 45 minutes after dosing. Baseline was defined as the average of the -45 minutes and -15 minutes FEV1 values taken on Day 1.

FEV1 is used in COPD studies as a physiological measure of airflow. A change-from-baseline endpoint compares each participant’s follow-up measurement with their starting measurement, then the model estimates group-level changes and the difference between regimens. The registry reports least-squares mean changes rather than simple raw averages. These are model-based estimates that account for the factors and baseline covariate named in the analysis description.

The Week 12 timing makes this the primary comparison at a specified point during treatment, while the registry also lists other lung-function assessments and patient-reported outcomes. FEV1 does not capture every aspect of COPD or how participants feel and function. A change in this measure should therefore be interpreted as evidence about the specified lung-function endpoint, alongside other outcomes and the precision of the estimate, rather than as a complete account of overall clinical experience.

7. Results Posted in the Registry

• NVA237 Once Daily: mean 0.06 versus 0.09 on control; difference -0.03 (95% CI -0.07 to 0.00), standardized effect d = -0.14; z-test p = 0.063.

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 Area Under The Curve (AUC 0-12 Hour) for Forced Expiratory Volume in One Second (FEV1) Post Dosing at Day 1

• 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 Once Daily: mean 0.14 versus 0.14 on control; difference -0.00 (95% CI -0.03 to 0.02), standardized effect d = -0.02; z-test p = 0.748.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NVA237 Once Daily and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in the Percentage of Days With no Rescue Medication Use Over the 26 Weeks

• 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 Once Daily: mean 15.36 versus 16.57 on control; difference -1.21 (95% CI -7.79 to 5.36), standardized effect d = -0.03; z-test p = 0.718.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between NVA237 Once Daily and the control. The interval gives the range of effects that remain compatible with the data.

The registry identifies a broad set of secondary domains: lung-function measurements across post-dose time spans and visits, respiratory quality of life, dyspnea, and rescue-medication use. Numerically detailed summaries in the posted record include the Day 1 FEV1 area-under-the-curve measure and change in days with no rescue-medication use over the treatment period. The other listed secondary outcomes’ numerical results are not reported in the registry record.

The available secondary summaries do not materially sharpen the primary comparison. The Day 1 area-under-the-curve estimates are close, and the interval for the once-daily versus twice-daily contrast includes values on either side of no difference. For days without rescue medication, the estimated difference is also imprecise, with an interval spanning both directions. These outcomes use different measurements and timeframes from the primary Week 12 trough FEV1 endpoint. They provide context, but should not be read as replications of the primary test.

Secondary results generally carry less inferential weight when many outcomes and time points are examined. If each is tested independently without an adjustment or a prespecified hierarchy, the chance of obtaining apparently notable findings somewhere among them can increase. The registry record does not report a multiplicity procedure for these outcomes. Their simple unadjusted recalculations are therefore descriptive or exploratory, rather than confirmatory evidence of a separate treatment effect. This cautions against selecting one result from a larger outcome set and treating it as decisive.

The overall pattern in the numerical information available is one of modest estimated contrasts and considerable uncertainty, rather than a clear, consistently differentiated secondary profile. That pattern should be interpreted alongside the primary model result and the fact that the registry does not report numerical results for most of the listed secondary outcomes. Missing numerical detail is not evidence that an outcome was unchanged; it means the result cannot be assessed from the registry record.

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

• Change From Baseline in Area Under The Curve (AUC) for Forced Expiratory Volume in One Second (FEV1) for Different Time Spans Post Dosing at Week 12
• Change From Baseline in Area Under The Curve (AUC 0-12 Hour) for Forced Expiratory Volume in One Second (FEV1) Post Dosing at Day 1
• Change From Baseline in Area Under The Curve (AUC) for Forced Expiratory Volume in One Second (FEV1) for Different Time Spans Post Dosing at Week 26
• Change From Baseline in Total St. George's Respiratory Questionnaire (SGRQ) Score at Week 12 and Week 26
• Percentage of Patients With a Clinically Significant Improvement in St George Respiratory Questionnaire at Week 12 and Week 26
• Change From Baseline in Transitional Dyspnea Index (TDI) Focal Score at Week 12 and Week 26
• Percentage of Patients With a Clinically Important Improvement on Transitional Dyspnea Index (TDI) Focal Score at Week 12 and Week 26
• Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1) at Day 1 and Week 26

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: it is measured in liters and summarized as a change from baseline. For a continuous outcome, a group mean describes the center of the observed or model-estimated values. Here, the registry reports least-squares means, which are model-based estimates rather than unadjusted arithmetic averages. They are calculated within the specified statistical model, taking account of its included terms.

What does the repeated-measures model do?

The primary analysis used an analysis of covariance for repeated measurements, also called a mixed model for repeated measures (MMRM). Participants were assessed at more than one visit, and measurements from the same participant are related rather than independent. A repeated-measures model accounts for that within-participant structure while estimating treatment differences over visits. The registry says the model included treatment, COPD severity, baseline smoking status, baseline inhaled corticosteroid use, region, and visit as factors, and baseline FEV1 as a covariate. The visits named were Day 1 and Weeks 12 and 26.

In general, including baseline FEV1 as a covariate can improve adjustment for starting lung-function differences and help estimate the treatment contrast conditional on baseline. Including the listed factors lets the model account for those recorded characteristics and visit timing in its estimate. The registry does not provide enough detail to reproduce every aspect of the model, such as its covariance structure or all implementation choices; those details are not reported in the registry record.

Why distinguish the sponsor estimate from the recalculation?

The sponsor’s primary result is a net mean difference from the MMRM. It is an adjusted, model-based contrast. The recalculated contrast uses the posted summary means and standard errors to make a simple unadjusted comparison. The recalculation is useful as a check on the scale and direction of the summarized result, but it does not recreate the repeated-measures model. It does not use the full participant-level data or adjust for the same factors and visit structure. Its estimated variability is approximate, as reflected in the posted pooled standard deviation being approximate. These methods can yield slightly different confidence limits and p-values without indicating that the reported values are contradictory.

The contrasts are also written in opposite directions. The sponsor’s net difference is reported as twice-daily minus once-daily, while the recalculation is expressed as once-daily minus twice-daily. Changing subtraction order reverses the sign but leaves the underlying comparison unchanged. Readers should use both the group labels and the direction of the contrast when interpreting any positive or negative value.

What does a p-value tell the reader?

In general, a p-value describes how incompatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. The sponsor reports p = 0.051 for the primary comparison; the simple recalculation reports p = 0.063. These values are close, but neither should be treated as a measure of effect size. The estimated difference and its confidence interval provide information about magnitude and precision that a p-value alone does not.

A confidence interval gives a range of values reasonably compatible with the data and analysis assumptions. The sponsor’s interval is reported as 0.000 to 0.066 liters for the net difference. Because the lower limit is exactly as rounded in the registry, it is important not to silently replace it with a more precise value. The recalculated interval is -0.068 to 0.002 liters for the opposite contrast. The intervals refer to different presentations and analyses, so they should not be conflated.

Why can variability affect inference?

In general, greater outcome variability makes a group contrast harder to estimate precisely, while more information can improve precision. The standard error describes uncertainty in an estimated mean, not the spread of individual participant measurements. The primary arm summaries report standard errors of 0.013 and 0.013 liters. These are attached to the least-squares mean changes, and they should not be read as standard deviations of individual FEV1 changes. The recalculation uses an approximate pooled standard deviation derived from summary information; that is a different measure of variability.

For count outcomes, event counts and percentages can be informative but do not replace a comparison model or an interval estimate. For continuous outcomes, a mean difference focuses on average change and can conceal variation across participants. The registry does not provide participant-level distributions or subgroup-specific primary estimates, so the summaries cannot show the full range of individual responses.

How should multiple outcomes be considered?

The registry lists a primary endpoint and secondary endpoints, including repeated lung-function measures, respiratory quality of life, dyspnea, and rescue-medication use. When many outcomes, time points, or analyses are examined, some may appear notable by chance. Multiplicity procedures can control the overall false-positive risk, but the multiplicity strategy is not reported in the registry record. As a result, the secondary p-values from simple recalculations should be treated as exploratory unless the record documents a prespecified adjustment or testing hierarchy. The original statistical analysis plan and further analysis details are not reported in the registry record.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate the treatment contrast. The sponsor’s primary analysis reports a net mean difference of 0.033 liters, with a 95% confidence interval from 0.000 to 0.066. The interval extends from the rounded value of no difference to a positive contrast in the sponsor’s direction. This means the point estimate is not the only plausible value under the model: the lower end is close to no separation, while the upper end allows a larger difference. The p-value, p = 0.051, is consistent with that uncertainty.

The unadjusted recalculation gives the reverse-direction contrast, once daily minus twice daily, as -0.033 liters, with a 95% confidence interval from -0.068 to 0.002. This range includes zero and spans small contrasts in either direction. Because it is an approximate, unadjusted recalculation, the sponsor’s MMRM estimate and interval are the primary inferential results for the trial. Differences between the intervals reflect both contrast direction and analysis approach.

A confidence interval is not a guarantee that the true effect lies within its endpoints, nor does it identify which values are clinically important. Its interpretation depends on the model and assumptions used. The registry does not report a clinical-importance threshold for the primary FEV1 change. The interval therefore communicates statistical uncertainty but cannot, by itself, determine whether the possible effects would matter to patients.

The arm-level standard errors are 0.013 liters and 0.013 liters. They describe precision of the estimated least-squares means, not the variation among individual participants. The registry provides no participant-level distribution in the reported summaries. The estimates should consequently be read as average group changes with uncertainty, rather than as predictions for any particular participant.

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 describe participants per arm for 80% power and participants per arm for 90% power. They are based on a planning illustration computed from the observed effect, not on the trial’s original design calculations. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The original sample-size assumptions for this trial are not reported in the registry record.

In general, power is the probability that a planned analysis will detect an effect of a specified size under its assumptions, if that effect is present. The 80% and 90% columns therefore describe different planning targets: the latter aims for a greater chance of detecting the assumed effect and requires more participants per arm. These are design illustrations, not evidence about whether the completed study had a particular probability of obtaining a statistically significant result. This is not observed power.

The rows reduce the assumed effect from 100% of the observed effect to 75% and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so detecting them requires more participants. For the primary outcome, the displayed planning counts rise as the assumed fraction decreases. The same principle applies to the secondary illustrations. These figures should not be interpreted as a recommended future trial size without considering its own design, endpoint, analysis plan, and recruitment context.

All planning entries in this record are participant counts per arm, not total events. The sample-size assumptions specify total events for time-to-event outcomes, but the outcomes with planning figures are continuous, so the per-arm interpretation applies. The figures are planning illustrations based on simple assumptions and should not be mistaken for the observed enrollment or analysis counts.

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 = -0.033; pooled standard deviation σ = 0.238.
2. n = 2 × (1.96 + 0.842)² × 0.238² / -0.033² = 815.0, rounded up to 816 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 <- -0.033                      # observed difference in means
sigma <- 0.237786083386968                     # 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(2371629)
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 = 816 (80% power), 1,092 (90% power)
 75% of observed effect: n per arm = 1,449 (80% power), 1,940 (90% power)
 50% of observed effect: n per arm = 3,261 (80% power), 4,365 (90% power)
power.t.test: 816 
Simulated power at n = 816 per arm: 0.799 (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. Analyses Reported by the Sponsor

The sponsor’s primary analysis used a mixed model for repeated measures and reports a net mean difference of 0.033 liters, a 95% confidence interval from 0.000 to 0.066, and p = 0.051. That is the analysis directly reported for the trial’s primary endpoint, so it takes precedence over a recalculation based only on arm summaries.

The unadjusted recalculation expresses the contrast in the opposite direction, once daily minus twice daily. It gives -0.033 liters, with a 95% confidence interval from -0.068 to 0.002 and p = 0.063. The sign is reversed because the order of subtraction is reversed. The recalculation uses summary means and standard errors rather than the participant-level repeated-measures model, and its variability estimate is approximate. It is therefore a check on the posted summaries, not a replacement for the sponsor’s adjusted result.

The sponsor and recalculated estimates point in the same directional sense once the contrast orientation is aligned, and both intervals include or reach the value corresponding to no difference after accounting for direction and rounding. Small differences in interval endpoints and p-values are expected when the analyses are not identical. The registry does not report further information needed to reproduce the sponsor’s full model, including all implementation choices. The reported sponsor analysis remains the principal inferential result for the primary endpoint.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and 14 secondary outcomes. Those outcomes span lung function, respiratory quality of life, dyspnea, and rescue-medication use, with some assessed at multiple time points. Testing multiple outcomes or time points creates a multiplicity issue: even when no underlying differences exist, a collection of separate tests can produce a nominally notable result by chance. In general, a prespecified testing hierarchy or an adjustment can help control that risk.

The multiplicity strategy, any hierarchy among the secondary outcomes, and any adjustment to secondary p-values are not reported in the registry record. The registry also does not report interim analyses or whether any statistical monitoring rules were used. Without those details, the primary endpoint should be distinguished from secondary findings, and unadjusted secondary calculations should not be treated as confirmatory.

The primary endpoint description names the Full Analysis Set as the analysis population and says it included randomized patients who received at least one dose of study drug. It also says patients were analyzed according to randomized treatment, consistent with the stated intent-to-treat principle. The remaining endpoint-specific wording about evaluable data is incomplete in the registry record, so the exact analysis-population rule for the primary endpoint is not fully reported.

Handling of missing measurements is also important in a repeated-measures analysis. The registry describes the MMRM but does not report the assumptions or procedures used for missing data, the amount of missing primary outcome data, or sensitivity analyses testing alternative assumptions. Those details are not reported in the registry record. Consequently, the primary estimate can be interpreted as the reported model result, but its sensitivity to missing-data choices cannot be assessed from the registry alone.

The registry gives arm-level outcome counts and general enrollment information, but these counts need not represent the same population because endpoint availability and analysis eligibility can differ. It does not provide a full accounting of participant flow through every analysis or explain all exclusions and missing assessments. These reporting gaps do not establish that the analysis was inappropriate; they limit independent evaluation of the analysis population, multiplicity control, and robustness.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: chronic obstructive pulmonary disease (3.9%), pneumonia (1.0%), atrial fibrillation (0.8%), angina unstable (0.5%), bronchial carcinoma (0.5%).

The safety record reports serious adverse events for groups labeled NVA237 22 mcg b.i.d. and NVA237 44 mcg o.d. Each group has 388 participants at risk for the serious-adverse-event summary. Serious adverse events affected 33 participants in the twice-daily group and 30 in the once-daily group. The record reports one death in the twice-daily group and two in the once-daily group. These are counts, not estimates of a causal treatment effect.

Other adverse events affected 126 participants in the twice-daily group and 152 in the once-daily group, with 388 at risk in each group. The record’s listed serious-event terms include chronic obstructive pulmonary disease at 3.9%, pneumonia at 1.0%, atrial fibrillation at 0.8%, unstable angina at 0.5%, bronchial carcinoma at 0.5%, and schizophrenia at 0.5%. These percentages are reported as registry entries; they should not be combined or interpreted as mutually exclusive categories.

Safety counts describe events recorded during the study, but the registry summary does not provide enough detail to assess timing, recurrence, relatedness to study drug, or differences in participant characteristics. The figures alone do not establish that a regimen caused or prevented an event. The record’s safety summaries should be read as descriptive counts within the trial arms, not as a complete comparative safety analysis.

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

The primary result is an estimate of the average difference between two NVA237 dosing schedules for change in trough FEV1 at Week 12. The sponsor’s repeated-measures model estimates a net difference of 0.033 liters in favor of twice-daily dosing, with a 95% confidence interval from 0.000 to 0.066 and p = 0.051. This is a borderline estimate in statistical terms, with the reported interval reaching the rounded value of no difference. The registry therefore does not support treating the point estimate alone as a precise or definitive separation between regimens.

The result does not establish that one schedule is better for every participant. It is a group-level estimate for one lung-function endpoint at one specified time. It does not directly measure all symptoms, daily functioning, exacerbations, or quality of life. The registry lists outcomes in several of these domains, but numerical results for most listed secondary outcomes are not reported in the registry record. The available secondary summaries are not precise enough to resolve the uncertainty in the primary comparison.

The study compared two active NVA237 schedules, with evening placebo in the once-daily group and salbutamol available as rescue medicine in both groups. It was not a comparison of NVA237 against no treatment. The result therefore answers a regimen-comparison question in this study context, not a broader question about NVA237 versus all alternatives or usual care.

The posted result also does not determine clinical importance. No threshold for a clinically important change in FEV1 is reported in the registry record. A statistically estimated mean difference cannot be translated into a patient-level benefit without additional context, and this record does not support medical advice or a recommendation about dosing.

Finally, the interpretation depends on the reported model and its assumptions. Further details about multiplicity control, missing-data handling, and some analysis-population rules are not reported in the registry record. Those omissions leave uncertainty about robustness beyond the estimate and interval as posted. The appropriate reading is therefore focused: a modest model-estimated contrast, with imprecision around its size and limits on what can be inferred from the registry summaries alone.

18. Why This Trial Matters Statistically

This trial illustrates why the estimated contrast, its uncertainty, and the analysis method all matter. The arm-level least-squares mean changes are 0.092 liters and 0.059 liters, while the sponsor reports a net mean difference of 0.033 liters. The confidence interval reaches 0.000 and the p-value is 0.051. Reporting only the point estimate would conceal that the data remain compatible with little or no separation at the rounded lower limit.

It also illustrates why adjusted and unadjusted results need to be distinguished. The sponsor’s MMRM accounts for repeated visits and the listed baseline and clinical factors. The unadjusted recalculation uses posted summaries and produces a nearby but not identical interval and p-value. The comparison is useful for understanding the direction and scale of the result, but it cannot reproduce the sponsor’s model. Statistical interpretation depends not just on the numbers, but on how those numbers were estimated.

The regimen comparison is also clinically specific. Both groups received NVA237 and rescue salbutamol; the schedules differed in dose timing and evening placebo. The result addresses Week 12 trough FEV1, while other measures address different facets of COPD. This distinction prevents a single lung-function endpoint from being treated as a complete summary of symptoms, quality of life, or safety.

Finally, the record illustrates limits of registry reporting. It contains a primary model result and some secondary and safety summaries, but does not report full detail on multiplicity, missing-data handling, original sample-size assumptions, or most listed secondary numerical results. These are not minor technicalities: they affect how independently readers can assess robustness and how much weight to give exploratory findings. Transparent reporting of estimates and analysis context is central to interpreting clinical trial evidence.

19. 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.

Several limitations are specific to what is available in this registry record. The primary analysis description gives the model type and included factors, but does not report all model implementation details, such as the covariance structure. The record also does not report the detailed assumptions or procedures used for missing measurements, missing-data sensitivity analyses, or the amount of missing primary endpoint data. These omissions prevent a full assessment of how robust the MMRM estimate is to those choices.

The exact endpoint-specific analysis population is not fully described: the record begins to state an evaluable-data condition, but the remaining wording is not reported in the registry record. The record gives enrollment and outcome-specific counts, but does not provide a complete account of participant flow through each analysis. It is therefore not possible to assess all reasons that participants may not contribute to a particular outcome summary.

The registry does not report the original trial sample-size justification or its design assumptions. The planning illustrations based on observed effects are not a substitute for those original calculations. It also does not report a multiplicity procedure, an outcome-testing hierarchy, or interim-analysis details. These omissions matter when interpreting the primary result in relation to multiple secondary outcomes.

For the secondary outcomes, only selected numerical summaries are available in the record, despite its listing of 14 secondary outcomes. Numerical results for most listed outcomes are not reported in the registry record. The record also does not supply a clinical-importance threshold for the primary FEV1 outcome, so statistical uncertainty cannot be translated into a judgment about clinical importance based on this information alone.

Finally, the recalculated primary contrast is an approximate, unadjusted analysis based on summary statistics, not participant-level data. It is informative as a comparison with the sponsor’s report but has methodological limitations and should not supersede the sponsor’s repeated-measures analysis.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Efficacy and Safety of NVA237 in Patients With Moderate to Severe COPD — NCT02371629.
• Registry record last updated 2019-08-09; status last verified 2019-06.
• Results first posted 2019-08-09.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry record describes a completed Phase 4 randomized, double-blind, parallel-group study of once-daily versus twice-daily NVA237 in patients with moderate to severe COPD. The treatment period was 26 weeks, and both groups received salbutamol as rescue medicine. Enrollment was 776.

The primary endpoint was change from baseline in trough FEV1 at Week 12. The sponsor’s repeated-measures analysis reported a net mean difference of 0.033 liters, a 95% confidence interval from 0.000 to 0.066, and p = 0.051. An approximate unadjusted recalculation gave the opposite-direction contrast as -0.033 liters, with a 95% confidence interval from -0.068 to 0.002 and p = 0.063.

The registry lists 14 secondary outcomes and provides numerical detail for selected measures, along with descriptive adverse-event counts. Important analysis details, including multiplicity and missing-data procedures, are not reported in the registry record.