Long-term Extension Study of the Safety, Tolerability, and Efficacy of Aclidinium Bromide in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) (LAS-MD-36): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Long-term Extension Study of the Safety, Tolerability, and Efficacy of Aclidinium Bromide in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) (LAS-MD-36) (NCT00970268), a randomized phase 3 study. The primary outcome is Change From Baseline in Morning Pre-dose (Trough) Forced Expiratory Volume in One Second (FEV1).

2. Clinical Question

This is an extension study, not a comparison in which one group remained on placebo throughout the 52-week treatment period. The registry describes patients as randomized from the lead-in study to one of two aclidinium doses for the extension. The posted arm labels also retain the lead-in treatment in the sequence name. This context matters when describing the reference group: it received placebo during the lead-in and aclidinium during the extension.

The primary question concerns a continuous lung-function measure and its change over time. The registry lists a secondary endpoint, change from baseline in peak FEV1, assessed at 52 weeks. The results therefore address recorded changes in two FEV1 measures, but do not by themselves establish broader effects on symptoms, daily functioning, or other outcomes that are not reported in the registry record.

3. Trial Design

The registry describes a randomized, quadruple-masked, parallel-group phase 3 extension study sponsored by AstraZeneca. It enrolled patients with moderate to severe chronic obstructive pulmonary disease. The study started in 2009-08, had primary completion in 2010-10, and is listed as completed. The meaning of each masking role is not reported in the registry record, so the masking label does not identify which individuals or groups were masked.

The study was designed to evaluate long-term safety, tolerability, and efficacy of inhaled aclidinium bromide at two dose levels. The description specifies a 52-week double-blind treatment period and a 2 week follow-up phone call, with the extension following a 12 week lead-in study. The total stated duration is 54 weeks. Patients were randomized from the lead-in study to one of the two aclidinium doses. The registry’s arm labels distinguish sequences that began with placebo from sequences that began with aclidinium.

The posted primary endpoint is change from baseline in morning pre-dose, or trough, FEV1, measured from the lead-in baseline to week 52. The secondary endpoint is change from baseline in peak FEV1 at 52 weeks. The registry describes least-squares means and standard errors for the continuous outcomes. It reports an enrollment of 291, while the analysis population descriptions specify 289 patients who received at least one dose of double-blind treatment and 246 patients who qualified for the ITT Population by having baseline and at least one postbaseline FEV1 assessment.

The registry record does not report the original sample-size justification, detailed randomization procedures, the allocation ratio used in the trial, or the statistical analysis plan. It also does not report how missing outcome measurements were handled or whether any interim analyses were conducted. Those omissions limit what can be concluded about design choices and the full analysis process.

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: From the total of 291 patients enrolled, 289 patients (99.3%) received at least 1 dose of double-blind treatment and therefore were included in the Safety Population. Of these patients, 246 (84.5%) had a baseline and at least 1 postbaseline FEV1 assessment and qualified for the Intent To Treat (ITT) Population.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: From the total of 291 patients enrolled, 289 patients (99.3%) received at least 1 dose of double-blind treatment and therefore were included in the Safety Population. Of these patients, 246 (84.5%) had a baseline and at least 1 postbaseline FEV1 assessment and qualified for the ITT Population

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 Morning Pre-dose (Trough) Forced Expiratory Volume in One Second (FEV1), measured over Change from baseline (visit 2 of lead-in study LAS-MD-33) to 52 weeks.

The primary endpoint is change from baseline in morning pre-dose, or trough, forced expiratory volume in one second (FEV1), measured in liters. Baseline is defined as visit 2 of the lead-in study, and the endpoint is assessed at week 52 of the extension. FEV1 is the volume of air forcibly exhaled in the first second of a forced expiration; as a continuous measure, it records lung function on a numeric scale.

The morning pre-dose timing is part of the endpoint definition: the measurement is taken before the next scheduled dose, rather than at a peak time after dosing. This makes the endpoint specifically a trough measurement. The registry also posts a separate peak FEV1 endpoint, which is not interchangeable with the trough measure because it refers to a different measurement time.

The reported group values are least-squares means, with standard errors as the measure of dispersion. A least-squares mean is a model-based estimate of a group average; the registry record does not describe the model or its covariates. The endpoint is used to summarize the change in the measured lung-function value over the specified period. It does not, by itself, describe every aspect of a patient’s COPD or establish the implications of a measured change for symptoms, functioning, or long-term health.

7. Results Posted in the Registry

• Aclidinium Bromide 200 μg - Aclidinium Bromide 200 μg: mean 0.07 versus -0.04 on control; difference 0.10 (95% CI 0.01 to 0.20), standardized effect d = 0.42; z-test p = 0.033.
• Placebo - Aclidinium Bromide 400 μg: mean 0.07 versus -0.04 on control; difference 0.10 (95% CI -0.00 to 0.21), standardized effect d = 0.43; z-test p = 0.056.
• Aclidinium Bromide 400 μg - Aclidinium Bromide 400 μg: mean 0.06 versus -0.04 on control; difference 0.09 (95% CI -0.00 to 0.18), standardized effect d = 0.38; z-test p = 0.054.

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 Peak FEV1

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Aclidinium Bromide 200 μg - Aclidinium Bromide 200 μg: mean 0.21 versus 0.11 on control; difference 0.10 (95% CI 0.01 to 0.20), standardized effect d = 0.42; z-test p = 0.037.
  • Placebo - Aclidinium Bromide 400 μg: mean 0.22 versus 0.11 on control; difference 0.11 (95% CI 0.00 to 0.22), standardized effect d = 0.45; z-test p = 0.044.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aclidinium Bromide 200 μg - Aclidinium Bromide 200 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Placebo - Aclidinium Bromide 400 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint: change from baseline in peak FEV1 at 52 weeks. Its overall pattern is directionally consistent with the primary endpoint: group mean changes are positive, and the posted comparisons with the reference sequence are positive. This provides a related measure of lung function, but peak and trough FEV1 describe different measurement times and should not be treated as identical outcomes.

The registry posts recalculated comparisons for two secondary contrasts, both against the placebo-to-aclidinium 200 μg sequence. The secondary endpoint does not have a posted comparison for every primary sequence contrast. The registry record lists no reported analyses for this secondary outcome, so the displayed estimates should be understood as recalculations from posted summaries rather than as a complete account of a sponsor analysis.

Secondary results generally carry less weight than a prespecified primary result because they are additional opportunities to observe a difference. If multiple outcomes or contrasts are examined, the chance of at least one apparently noteworthy result can increase unless the analysis plan accounts for that multiplicity. The registry record does not report an adjustment strategy or a hierarchy for secondary hypotheses. Accordingly, the secondary pattern can be described as supportive in direction, but it should not be used alone to settle the primary question.

The peak measure’s consistency with the direction of the trough estimates does not resolve the uncertainty in the primary comparisons. Nor does it establish that both measurements have the same clinical meaning. The record does not report a threshold for a clinically meaningful change or provide a rationale for how the secondary outcome was selected. Interpreting it alongside the primary endpoint is most useful as context, with attention to its unadjusted status and the incomplete analysis information.

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

• Change From Baseline in Peak FEV1

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: FEV1 change is measured in liters, and the registry reports a mean for each group. A mean describes the central value of the measurements, while a standard error describes the precision of an estimated mean. It is not the same as the spread of individual patient measurements. The registry identifies the group estimates as least-squares means, but does not describe the model that produced them. Without that model information, the precise role of adjustment or covariates cannot be assessed.

What does a mean difference represent?

A mean difference compares the estimated average change in one sequence with the estimated average change in the reference sequence. Positive estimates in the posted primary comparisons indicate a higher average change in the named sequence than in the reference, according to the direction used for the calculation. The contrast is about changes from baseline, not a comparison of final FEV1 values alone.

The posted comparison values are recalculated, simple unadjusted comparisons from the registry’s group summaries. They use the reported means and standard errors. The pooled standard deviations used for standardized effect-size summaries are marked as approximate because they are reconstructed from those standard errors. Such recalculations can clarify the scale and uncertainty of a contrast, but they do not reproduce an undocumented trial model. The registry record lists no reported analyses for the primary endpoint, and no discrepancy is flagged between the recalculations and a sponsor analysis.

How should a p-value be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the assumptions of the calculation. A small p-value is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The primary comparison p-values are explicitly unadjusted. That means they do not account for a family of comparisons unless an adjustment is separately reported; no such adjustment is reported in the registry record.

The conventional 0.05 reference can be useful for describing the posted unadjusted values, but it does not remove uncertainty or correct for examining multiple comparisons. Results near that threshold are especially easy to overstate if treated as a binary verdict. The estimated difference, its confidence interval, the number of comparisons, and the availability of a prespecified analysis all matter to interpretation.

What does a confidence interval add?

A confidence interval expresses the uncertainty around an estimated contrast. In general, a wider interval indicates less precision than a narrower one. If an interval includes zero for a difference, the data are compatible with a range of values that includes no difference, as well as values on either side of zero. If it excludes zero, that still does not establish clinical importance or remove concerns about multiplicity, model assumptions, or bias.

For the primary endpoint, one posted recalculated interval lies entirely above zero, while the other two include zero. The interval bounds should be considered alongside the corresponding point estimates, not as stand-alone conclusions. The registry does not report the confidence-interval method or a confidence level, so neither should be inferred from the record.

Why does variance estimation matter?

Uncertainty calculations depend on the variability of measurements and the number of observations contributing to each estimate. The posted standard errors are used in the recalculations; pooled standard deviations are approximate derived quantities. An approximate variance estimate can be useful for descriptive effect-size and planning calculations, but it is not a replacement for the analysis model or individual-level data. Over-dispersion, in general, means the observed variability exceeds what a chosen model expects; if present and unaccounted for, standard errors can understate uncertainty. The registry record does not report an assessment of over-dispersion, so its presence or absence cannot be determined.

What analysis details are absent?

The registry record does not report the original statistical analysis plan, the model specification for least-squares means, handling of missing measurements, or adjustment for multiple comparisons. It also does not list sponsor-reported analyses for these outcomes. The population definitions do give some information: 289 patients received at least one dose of double-blind treatment and were included in the Safety Population, while 246 had a baseline and at least one postbaseline FEV1 assessment and qualified for the ITT Population. The record does not explain whether additional exclusions or imputation procedures were used for the endpoint analysis.

These distinctions matter because the group estimates and recalculated contrasts depend on which observations are analyzed and how they are modeled. The ITT label alone does not establish that every randomized patient contributed to every outcome estimate, particularly when the record defines the population by availability of FEV1 assessments. In general, missing-data methods can influence both estimates and precision, so those methods are important when judging how robust an analysis may be.

11. Confidence Intervals and Precision

The primary comparisons have estimated mean differences of 0.104 L for aclidinium 200 μg followed by aclidinium 200 μg, 0.104 L for placebo followed by aclidinium 400 μg, and 0.091 L for aclidinium 400 μg followed by aclidinium 400 μg, each relative to the placebo-to-aclidinium 200 μg sequence. The associated intervals show how much uncertainty surrounds those point estimates. The interval for the 200 μg-to-200 μg sequence lies above zero. The intervals for both 400 μg sequences include zero, so those data are compatible with no difference as well as with a positive difference.

A confidence interval is a range of values generated by a statistical procedure intended to reflect uncertainty in an estimate. In general, narrower intervals indicate greater precision, while wider intervals indicate less precision. An interval should not be interpreted as a range that contains a fixed proportion of individual patient outcomes. It describes uncertainty about the estimated contrast, under the assumptions of the method used.

The standard errors for the group means are reported, but the registry record does not describe the method used for the comparison intervals or state their confidence level. The available estimates are recalculated from summary statistics and should not be mistaken for a full model-based analysis. The intervals also do not address multiplicity unless an adjustment is made, and the registry record does not report such an adjustment. Precision therefore concerns the uncertainty represented by these particular recalculated contrasts, not every source of uncertainty in the study.

The contrast estimates are more informative when read together with their intervals rather than ranked by point estimate alone. Similar point estimates can have different interval widths and p-values because uncertainty also depends on the information available in each comparison. The recorded comparison group sizes differ, and the reported standard errors vary across groups. This is one reason that estimates should not be interpreted as equally precise merely because their point estimates are close.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect, not the trial’s original sample-size calculation. The assumptions stated for these illustrations 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 design assumptions and sample-size justification are not reported in the registry record.

For each comparison, the 80% power column gives the illustrated number of participants per arm needed for an 80% chance of detecting the specified effect under those planning assumptions, if that effect and the assumptions hold. The 90% power column gives the corresponding number per arm for a higher target chance of detection. These are planning targets, not measures of what the completed trial achieved.

The rows represent planning for 100%, 75%, and 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the target effect becomes smaller. The required number also differs between comparisons because the observed effects and estimated variability differ. These figures do not establish what sample size would be appropriate for a future study without considering its design, outcome, analysis plan, and assumptions.

This is not observed power. It does not describe the probability that the completed trial detected an effect, nor does it change the interpretation of the posted estimates and confidence intervals. It is a forward-looking planning illustration calculated from the observed effect and stated assumptions.

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 = 0.104; pooled standard deviation σ = 0.245.
2. n = 2 × (1.96 + 0.842)² × 0.245² / 0.104² = 87.1, rounded up to 88 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 <- 0.104                      # observed difference in means
sigma <- 0.244919811950186                     # 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(970268)
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 = 88 (80% power), 117 (90% power)
 75% of observed effect: n per arm = 155 (80% power), 208 (90% power)
 50% of observed effect: n per arm = 349 (80% power), 467 (90% power)
power.t.test: 88 
Simulated power at n = 88 per arm: 0.797 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled. The primary outcome has three recalculated comparisons against one reference sequence, and the registry also lists a secondary endpoint with posted comparisons. When several hypotheses are tested, unadjusted p-values do not account for the wider set of opportunities to find a result that appears unusual by chance. Without a reported adjustment or prespecified testing hierarchy, the p-values should be described as unadjusted and interpreted cautiously.

The record does not report the original statistical analysis plan, the intended model for the least-squares means, or whether any interim analyses were conducted. The model and analysis plan would help establish which comparisons were prespecified, how missing observations were handled, and whether the posted summaries correspond to the planned analysis. These details are not reported in the registry record.

The population descriptions distinguish safety from outcome assessment. The Safety Population includes 289 patients who received at least one dose of double-blind treatment. The ITT Population includes 246 patients who had a baseline and at least one postbaseline FEV1 assessment. The registry does not report why other enrolled patients did not meet those descriptions or whether additional analysis exclusions were made. It also does not describe an imputation method or sensitivity analysis for missing FEV1 values.

Missing data can affect an estimated change if the availability of measurements is related to outcomes or treatment history. In general, analysis choices for missing values can influence both the estimate and its uncertainty. The registry’s population definitions are useful, but they do not establish that missingness was harmless or explain the assumptions used to address it. These gaps limit assessment of the robustness of both the primary and secondary results.

The registry record does not report a sample-size justification for the trial. The planning illustrations based on observed effects are separate from an original design calculation and cannot fill that gap. Taken together, absent multiplicity, missing-data, and model details mean that the posted results are best read as a limited summary of outcomes, rather than a fully documented statistical analysis.

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 (5.7%), pneumonia (3.2%), coronary artery disease (2.3%), dehydration (2.3%), hypertension (2.3%).

The registry reports serious adverse events by treatment sequence and gives the number at risk and the number affected. Serious adverse events were reported for 7 of 44 patients in the placebo-to-aclidinium 200 μg group, 13 of 93 in the aclidinium 200 μg-to-aclidinium 200 μg group, 7 of 46 in the placebo-to-aclidinium 400 μg group, and 13 of 106 in the aclidinium 400 μg-to-aclidinium 400 μg group. These are descriptive counts within the recorded groups; they are not adjusted comparisons.

The registry also lists serious adverse-event terms with percentages, including chronic obstructive pulmonary disease at 5.7%, pneumonia at 3.2%, and coronary artery disease, dehydration, hypertension, and acute coronary syndrome at 2.3% each. The record does not provide enough detail in these summaries to infer comparative risks for individual terms. The number of deaths is not reported in the registry record.

Safety counts should be read alongside the stated population at risk and the treatment-sequence context. They do not establish that a treatment caused an event, and differences in counts alone do not account for follow-up, event timing, or other factors. The registry summaries support a description of reported events, not a causal safety conclusion.

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

The posted results describe average changes in trough and peak FEV1 among patients in the listed treatment sequences. For the primary endpoint, the recalculated point estimates favor the three sequences relative to the placebo-to-aclidinium 200 μg reference in the sense that their estimated mean changes are higher. The uncertainty differs across comparisons: one primary interval excludes zero, while two include it. These estimates are not a complete account of all possible clinical outcomes.

A statistically noteworthy unadjusted comparison is not the same as proof that a difference is clinically important. The registry does not state a threshold for a meaningful FEV1 change, and the reported lung-function measure does not alone describe symptoms, quality of life, exacerbations, or other outcomes. Those outcomes cannot be inferred from the FEV1 results.

The study is an extension in which the registry describes patients randomized from a lead-in to aclidinium at one of two doses. The treatment-sequence labels preserve the lead-in treatment history, and the reference group received aclidinium during the extension after placebo in the lead-in. Therefore, it would be inaccurate to characterize the primary comparison as a 52-week aclidinium-versus-placebo trial. The comparisons are also not direct tests between the 200 μg and 400 μg dose levels.

The outcome estimates are recalculated from posted summary statistics, and the registry record lists no sponsor-reported analyses for these endpoints. Important information about the model, multiplicity, and missing-data handling is not reported in the registry record. These limitations mean the reported results should be described as observed group summaries and unadjusted comparisons with uncertainty, rather than as definitive evidence about efficacy or safety.

The record does provide useful details about the study’s randomized, masked, parallel design, its long treatment period, and its defined analysis populations. Those details give context for reading the estimates, but do not remove the uncertainty or omissions. The meaning of the result is consequently bounded: it concerns the recorded FEV1 changes and reported adverse-event counts in this study, not a general guarantee of benefit or harm.

17. Why This Trial Matters Statistically

This trial illustrates why an extension study’s treatment history matters to statistical interpretation. Although all extension arms received aclidinium during the 52-week treatment period, the registry labels distinguish whether patients received placebo or aclidinium during the lead-in. The reference group is therefore not a group maintained on placebo throughout the extension. Describing the comparison accurately is essential to avoid overstating what the randomized contrast represents.

The registry also shows how a point estimate, a confidence interval, and an unadjusted p-value answer related but different questions. The primary comparisons have positive estimated differences, but their intervals do not all exclude zero. A single p-value threshold cannot convey the size and precision of an estimate, and unadjusted testing does not account for the multiple comparisons and endpoint information available.

Another important statistical issue is the gap between a registry summary and a full analysis report. Least-squares means are posted, but the model, analysis plan, missing-data methods, and multiplicity approach are not reported in the registry record. Recalculations can help readers understand contrasts from the posted summaries, but cannot substitute for those absent details.

Finally, the planning illustrations show how strongly a sample-size target depends on the effect being targeted. Smaller fractions of the observed effect require more participants per arm under the stated assumptions. These illustrations are distinct from the trial’s original design rationale and from observed power. Together, these features make the study useful for teaching careful reading of trial comparisons, uncertainty, and what registry summaries can and cannot establish.

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 and secondary contrasts are recalculations from posted summary statistics, not analyses listed as sponsor-reported in the registry. The least-squares means are available, but the model specification is not reported in the registry record. The approximate pooled standard deviations used in recalculated summaries are based on the reported standard errors, so standardized effect-size calculations depend on that approximation.

The primary comparisons use one sequence as the reference and do not directly compare the two aclidinium dose levels. The sequence labels include treatment received during the lead-in, making it important not to describe the reference as a group that remained on placebo during the extension. The registry does not report the detailed randomization procedure or allocation ratio.

Important analysis details are absent, including the original statistical analysis plan, multiplicity handling, missing-data methods, and any interim-analysis information. The endpoint population is defined by having baseline and at least one postbaseline FEV1 assessment, but the record does not describe the treatment of measurements that were missing or the reasons patients did not qualify for that population. No clinical-importance threshold is reported for changes in FEV1.

The safety summaries are counts and listed event terms, not adjusted causal comparisons. The number of deaths is not reported in the registry record. These limitations restrict interpretation to the posted group-level outcome estimates and event summaries; they do not permit a comprehensive assessment of clinical relevance, robustness, or causality.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Long-term Extension Study of the Safety, Tolerability, and Efficacy of Aclidinium Bromide in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) (LAS-MD-36) — NCT00970268.
• Registry record last updated 2017-01-06; status last verified 2016-11.
• Results first posted 2012-09-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed randomized, quadruple-masked, parallel-group phase 3 extension study enrolled patients with moderate to severe COPD and assessed two aclidinium dose levels. The stated extension included 52 weeks of double-blind treatment and a 2 week follow-up phone call after a 12 week lead-in.

The primary outcome was change from baseline in morning pre-dose trough FEV1 at week 52. The registry also lists change from baseline in peak FEV1 as a secondary outcome. The posted primary comparisons are recalculated, unadjusted contrasts against the placebo-to-aclidinium 200 μg sequence; the registry record lists no reported analyses for these outcomes.

The registry reports 289 patients in the Safety Population and 246 in the ITT Population. It does not report the original sample-size justification, multiplicity strategy, missing-data methods, or full model specification. Safety information is descriptive, and deaths are not reported in the registry record.