Efficacy and Safety of Aclidinium Bromide at Two Dose Levels Versus Placebo Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Aclidinium Bromide at Two Dose Levels Versus Placebo Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients (NCT01001494), a randomized phase 3 study. The primary outcome is Change From Baseline in Morning Pre-dose (Trough) Forced Expiratory Volume in the First Second (FEV1) at Week 24 on Treatment.

2. Clinical Question

3. Trial Design

The registry record describes a phase 3, randomized, double-blind, parallel-group trial of aclidinium bromide in patients with COPD. It lists an enrollment of 828 and identifies three groups: aclidinium bromide 200 μg twice daily by inhalation, aclidinium bromide 400 μg twice daily by inhalation, and placebo. The trial status is completed. The record lists AstraZeneca as the sponsor, a start date of 2009-10, and primary completion in 2010-11.

Randomization means assignment to the study groups was intended to occur by chance. Double masking means the record identifies the trial as double-blind, but the precise masking procedures and which parties were masked are not reported in the registry record. The parallel design means the listed groups received their assigned regimens in separate groups rather than cycling through treatments. Details of allocation concealment, the treatment period beyond the endpoint timeframe, and the procedures used to support adherence are not reported in the registry record.

The primary endpoint was the change from baseline in morning pre-dose, or trough, FEV1 at Week 24 on treatment. The recorded primary population was the ITT population, with eligibility for this analysis requiring at least one dose and both a baseline and at least 1 post-baseline FEV1 assessment. The registry also lists secondary endpoints concerning peak FEV1, TDI focal score, and SGRQ total score. Numerical secondary outcome results are not available in the registry record for all of these listed endpoints.

The enrollment figure is a trial-level record, while the endpoint arm counts are 277 for the 200 μg group, 269 for the 400 μg group, and 273 for placebo. These are the reported counts for the primary endpoint summaries, not a claim about how many participants contributed to every outcome. The trial's original sample-size justification, detailed statistical analysis plan, and handling of participants without endpoint measurements are not reported in the registry record.

4. Participant Flow and Accounting

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

Before assignment: Patients fulfilling inclusion/exclusion criteria at the time of the Screening Visit were entered into a run-in period of 14±3 days to assess patient's disease stability.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intention-to-treat (ITT) population: all randomised patients who took at least one dose of Investigational Medicinal Product and who had a baseline and at least 1 post-baseline FEV1 assessment.

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 the First Second (FEV1) at Week 24 on Treatment, measured over Baseline and Week 24.

The primary endpoint measures change from baseline in morning pre-dose, or trough, forced expiratory volume in the first second (FEV1) at Week 24 on treatment. FEV1 is the amount of air a person can forcefully exhale during the first second of an expiration, expressed in liters. A change score compares the Week 24 measurement with the baseline measurement, so positive and negative values describe the direction of change from each participant's starting measurement at the group-summary level.

Morning pre-dose timing identifies a measurement taken before a scheduled dose. In general, a trough measurement can describe lung function at a consistent point in the dosing schedule, rather than at a time chosen soon after a dose. The trial's brief description identifies bronchodilator efficacy as a main purpose, and FEV1 is a lung-function measure relevant to that question. The registry record does not report why this particular measurement time or the Week 24 time point was selected.

The primary summaries are least-squares means, with standard errors, in liters. In general, a least-squares mean is a model-based estimate of a group mean. The model and any adjustment variables used to obtain the registry's primary endpoint estimates are not reported in the registry record. A standard error describes the precision of an estimated mean, not the spread of individual patients' measurements. The registry defines the ITT analysis population as randomized patients who took at least one dose and had a baseline and at least 1 post-baseline FEV1 assessment. This population definition is narrower than an unrestricted count of everyone randomized because it requires endpoint measurements.

7. Results Posted in the Registry

• Aclidinium Bromide 200 μg Bid: mean 0.03 versus -0.07 on control; difference 0.10 (95% CI 0.05 to 0.14), standardized effect d = 0.37; z-test p = <0.001.
• Aclidinium Bromide 400 μg Bid: mean 0.06 versus -0.07 on control; difference 0.13 (95% CI 0.08 to 0.17), standardized effect d = 0.49; 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 Peak Forced Expiratory Volume in the First Second (FEV1) at Week 24 on Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Aclidinium Bromide 200 μg Bid: mean 0.21 versus 0.02 on control; difference 0.18 (95% CI 0.14 to 0.23), standardized effect d = 0.65; z-test p = <0.001.
  • Aclidinium Bromide 400 μg Bid: mean 0.23 versus 0.02 on control; difference 0.21 (95% CI 0.16 to 0.26), standardized effect d = 0.75; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aclidinium Bromide 200 μg Bid 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 Aclidinium Bromide 400 μg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists secondary outcomes covering peak FEV1, the TDI focal score, and the SGRQ total score. The numerical secondary results available in the record include arm summaries and comparisons for peak FEV1. Those summaries show positive changes in both aclidinium bromide groups and a smaller positive change in the placebo group; the recalculated contrasts are in the same direction as the primary endpoint comparisons. This directional agreement links the available secondary lung-function result with the primary lung-function result without making them interchangeable outcomes.

The other listed secondary outcomes concern whether patients achieved a specified decrease from baseline in TDI focal score or SGRQ total score at Week 24. Numerical results for those outcomes are not reported in the registry record. Their direction, size, uncertainty, and group-level event counts therefore cannot be assessed from this record. The available peak FEV1 result also does not establish what the unreported health-status outcomes would show.

Secondary results generally carry less weight than a prespecified primary result when the registry record does not document the analysis plan or control of multiplicity. Examining several outcomes and comparisons creates more opportunities for apparently notable findings to arise by chance. Without a reported multiplicity procedure, the unadjusted p-values for secondary comparisons should be treated as descriptive rather than as a family-wise confirmatory test. The registry record lists no sponsor-reported analyses for these secondary outcomes; the numerical comparisons are recalculations from posted summaries.

The incomplete reporting of the listed secondary endpoints also limits any claim about the full pattern across lung function, symptoms, and health status. The record's stated aims include COPD symptoms and disease-related health status, but the numerical secondary information available does not cover every listed endpoint. Thus, the available secondary evidence is consistent in direction with the primary lung-function comparison where results are posted, while leaving important secondary questions unanswered in the registry record.

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

• Change From Baseline in Peak Forced Expiratory Volume in the First Second (FEV1) at Week 24 on Treatment
• Percentage of Patients Who Achieved at Least a 1-unit Decrease From Baseline in TDI Focal Score at Week 24 on Treatment
• Percentage of Patients Who Achieved at Least a 4-unit Decrease From Baseline in the SGRQ Total Score at Week 24 on Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: FEV1 change is measured in liters, and its group summaries are reported as least-squares means. A continuous outcome retains the magnitude of a measurement rather than reducing it to a yes-or-no category. In general, a group mean provides a central summary, while its standard error describes the uncertainty in estimating that mean. It does not describe how widely individual patient measurements vary. The reported standard errors for the primary arm summaries are 0.016 liters in each group.

What does a least-squares mean represent?

In general, a least-squares mean is an estimated mean derived from a statistical model. It can differ from a simple arithmetic average when the model accounts for other factors or uses a particular structure for the data. The record identifies the estimates as least-squares means but does not report the model specification, adjustment variables, covariance structure, or method used to address repeated measurements. It is therefore not possible to determine from the registry record exactly how the reported estimates were adjusted.

How should the between-group differences be read?

A mean difference is a contrast between two group means on the original outcome scale. The posted comparisons set placebo against each aclidinium bromide dose. The unadjusted recalculated mean differences are 0.099 liters for the 200 μg group and 0.128 liters for the 400 μg group. These are arithmetic contrasts of the posted means, rather than estimates from a reported sponsor model. The recalculated p-values are p < 0.001 for each dose comparison. A p-value describes how compatible the observed contrast is with a specified null model under the calculation's assumptions; it is not a measure of effect size or clinical importance.

The comparison calculations use approximate pooled standard deviations inferred from the arm-level standard errors. The record marks these estimates as approximate. That matters because the arm summaries do not include the individual-level data or a directly reported pooled standard deviation. The resulting recalculated comparisons should therefore be interpreted as approximations based on posted summaries, not as a replacement for the trial's full analysis. The record lists no sponsor-reported statistical analyses for these outcomes. No discrepancy is flagged between the recalculated quantities and a sponsor analysis.

Why do confidence intervals matter?

A confidence interval gives a range of estimates compatible with the data and the method used to calculate it. In general, an interval communicates precision more fully than a point estimate alone: a narrower interval indicates less uncertainty under the calculation's assumptions, while a wider interval indicates more. The displayed intervals for the primary comparisons are based on the summary-statistic recalculations, with approximate standard deviations. Their interpretation does not account for unreported features of the original analysis or for multiplicity across endpoints and comparisons.

What do the planning illustrations mean?

The sample-size illustrations are based on the observed comparison effects and specified planning assumptions. For each active-dose comparison, they consider planning for 100%, 75%, or 50% of the observed effect. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The figures are participants per arm for 80% power or 90% power; they are planning illustrations, not a reconstruction of the trial's original design. The trial's original sample-size assumptions and justification are not reported in the registry record.

Power is the probability, under a particular planning model and assumed effect, of detecting an effect at the chosen significance level. In general, the 80% and 90% columns describe different target probabilities for a future study under the stated assumptions. They are not probabilities that the observed result is true. These illustrations use the observed effects as inputs, so they should not be interpreted as observed power or as evidence about how likely the trial was to detect an effect before it began.

How do the safety counts differ from the efficacy summaries?

The serious adverse event information is reported as counts of affected participants within groups and counts at risk. These are not continuous outcome means and do not have the same interpretation as the FEV1 estimates. The registry also lists selected serious adverse event terms and percentages. No inferential comparison or adjustment for differences between the groups is reported for the safety summaries. The record does not report deaths in the adverse event fields, so death results are not reported in the registry record.

Across these methods, the most important distinction is between the registry's arm-level summaries and the recalculated contrasts. The arm summaries are reported as least-squares means with standard errors. The differences, intervals, p-values, standardized effects, and planning figures are unadjusted calculations based on those summaries. They offer one way to describe the posted data, but they cannot reveal details that require the original analysis plan or participant-level data. Those details—including model choices, multiplicity procedures, and missing-data methods—are not reported in the registry record.

11. Confidence Intervals and Precision

The primary comparison estimates are 0.099 liters for aclidinium bromide 200 μg twice daily versus placebo and 0.128 liters for aclidinium bromide 400 μg twice daily versus placebo. The posted recalculations also include confidence intervals for both differences, and each interval lies on the positive side of zero. The interval bounds are displayed with more than three decimal places in the underlying calculations, so the values are not repeated. The recalculated p-value for each comparison is p < 0.001.

In general, a confidence interval communicates a range of values reasonably compatible with the data and the interval method, rather than a guarantee that the true effect lies within those bounds. The range also helps readers assess precision: a point estimate should not be considered in isolation from the uncertainty around it. For these comparisons, the interval calculations use approximate pooled standard deviations reconstructed from the arm-level standard errors. The confidence intervals therefore reflect the recalculation method and its assumptions, not necessarily the sponsor's original inferential procedure.

The arm-level standard errors for the primary outcome are 0.016 liters for each group. A standard error measures the estimated precision of a group mean, not the variation among individual patients. The registry record does not provide the underlying participant-level measurements, the sponsor's model-based intervals, or enough methodological detail to compare different interval methods. The reported intervals cannot account for uncertainty from unreported design or analysis decisions.

Precision is also distinct from clinical importance. The record does not report a threshold for deciding what size of FEV1 change is important to patients or clinicians. Nor do the confidence intervals incorporate any adjustment for examining more than one dose, endpoint, or comparison. They should be read as uncertainty intervals for the unadjusted recalculated comparisons, with these limits in mind.

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 estimates are participants per arm for the two-arm comparison of an active dose with placebo; they are not total event counts. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect is a stated fraction—100%, 75%, or 50%—of the observed effect for the corresponding comparison. These assumptions describe the illustrations, not the trial's original sample-size design, which is not reported in the registry record.

The 80% power column gives the planned number of participants per arm under the stated assumptions for a future study with an 80% probability of detecting the assumed effect at the specified significance level. The 90% power column uses a higher target probability and therefore gives a separate planning estimate. The figures are conditional on the assumed effect, allocation, significance level, and approximation; changing those assumptions could change the planning requirement.

When the assumed effect is a smaller fraction of the observed effect, more participants are needed to detect it under the same planning setup. This is why planning for 50% of the observed effect yields higher participant requirements than planning for the full observed effect. The associated curve communicates the same relationship across the range of effects being considered: smaller target effects require more participants per arm under these assumptions.

These are planning illustrations based on the observed results, not a report of the study's original calculations. They are not observed power. The trial's original design assumptions and sample-size justification are not reported in the registry record.

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 = 0.099; pooled standard deviation σ = 0.265.
2. n = 2 × (1.96 + 0.842)² × 0.265² / 0.099² = 112.8, rounded up to 113 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 <- 0.099                      # observed difference in means
sigma <- 0.265337025735719                     # 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(1001494)
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 = 113 (80% power), 151 (90% power)
 75% of observed effect: n per arm = 201 (80% power), 269 (90% power)
 50% of observed effect: n per arm = 452 (80% power), 604 (90% power)
power.t.test: 113.7 
Simulated power at n = 113 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. Multiplicity, Missing Data and Analysis Populations

The trial record identifies a primary endpoint and several secondary outcomes, but it does not report a statistical analysis plan describing how multiplicity was handled. In general, multiplicity arises when several hypotheses are tested, such as comparisons across dose groups or outcomes. If each is evaluated without adjustment, the chance of at least one apparently unusual result can increase. The recalculated p-values are unadjusted, and no multiplicity-adjusted results are reported in the registry record. The unadjusted values should therefore not be interpreted as if they controlled error across all trial comparisons.

The primary endpoint is described as a least-squares mean change, but the model specification is not reported in the registry record. The record does not state which covariates, if any, were included, how repeated or incomplete measurements were modeled, or whether the analysis used a prespecified testing sequence. The sponsor's full statistical analysis and its inferential results are not reported. Consequently, the recalculated comparisons cannot reproduce undocumented modeling or multiplicity decisions.

The primary population definition requires randomization, at least one dose, a baseline FEV1 assessment, and at least 1 post-baseline FEV1 assessment. The record does not report how many randomized participants lacked those measurements, how missing measurements were handled, or whether any sensitivity analyses assessed the consequences of missing data. It also does not report whether participants were analyzed according to their randomized group after treatment discontinuation or other protocol events. These omissions prevent a full assessment of the impact of missingness or deviations from the intended analysis population.

These reporting gaps do not change the numerical summaries that are posted, but they limit interpretation of the inferential claims that could be made from them. A complete evaluation would require the prespecified analysis methods, missing-data procedures, and multiplicity approach. Those details 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 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 (3.7%), pneumothorax (0.4%), angina pectoris (0.4%), cardiac discomfort (0.4%), cardiac failure acute (0.4%).

The serious adverse event summaries report 12 affected participants in the aclidinium bromide 200 μg group, 15 in the 400 μg group, and 15 in the placebo group. The corresponding numbers at risk are 277, 269, and 273. These are group counts; they are not adjusted comparisons and do not establish that an event was caused by a study treatment. The record does not report a statistical comparison of serious adverse events between groups.

The registry lists chronic obstructive pulmonary disease at 3.7% among the top serious adverse event terms. Pneumothorax, angina pectoris, cardiac discomfort, cardiac failure acute, and cardiac failure congestive are each listed at 0.4%. These terms describe selected reported events; they do not by themselves provide a complete safety profile or establish whether the same participant contributed to more than one term. Death counts are not reported in the registry record.

Serious adverse event counts should be read alongside the stated groups at risk and the limitations of the reporting. The record does not give event-level timing, severity detail beyond the serious-event classification, relatedness assessments, or a formal between-group safety analysis. These summaries describe reported counts only and cannot establish comparative safety on their own.

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

The posted primary summaries show positive mean changes from baseline in morning pre-dose FEV1 for both aclidinium bromide groups and a negative mean change for placebo at Week 24. The unadjusted recalculated mean differences versus placebo are positive for both active-dose comparisons, with p < 0.001 for each. The intervals for these recalculated differences are entirely above zero. These findings describe the posted lung-function summaries and the uncertainty calculated from them; they do not establish how clinically important the changes are.

The registry record does not report a threshold for a meaningful FEV1 change, the detailed sponsor analysis, or the original analysis plan. The comparisons are unadjusted recalculations based on posted summary statistics, and the pooled standard deviations used in the calculations are approximate. The evidence should therefore not be read as a complete reproduction of the trial's sponsor analysis. The record also does not report results for all listed secondary outcomes, including the TDI and SGRQ outcomes.

The primary endpoint is a lung-function measure at a defined time point. It does not, by itself, answer all of the study's stated questions about health status, COPD symptoms, exacerbations, safety, and tolerability. The serious adverse event counts are descriptive, and they do not establish a causal relationship between treatment assignment and an event or provide a complete comparison of risks. The death information is not reported in the registry record.

More generally, a statistical comparison does not make a treatment recommendation. Its interpretation depends on the outcome, analysis population, precision, clinical context, and quality of reporting. The registry record provides useful group summaries and trial design information, but missing details about model assumptions, missing data, multiplicity, and sponsor analyses constrain conclusions beyond those summaries. The results should be understood as evidence about this trial's posted endpoints and record, not as a complete account of every potential benefit or harm.

17. Why This Trial Matters Statistically

This trial illustrates why the distinction between an endpoint summary and a between-group comparison matters. The least-squares means describe change within each group, while the mean differences compare each active-dose group with placebo. A group mean alone is not the treatment contrast, and a contrast needs an uncertainty estimate to show its precision. The posted results make these quantities available for the primary FEV1 endpoint.

It also demonstrates the importance of distinguishing registry-reported analyses from recalculations. The arm-level means and standard errors are reported, but the comparisons and p-values are unadjusted recalculations using approximate pooled standard deviations. They are informative for reading the posted summaries, but cannot reveal the sponsor's model choices or substitute for a complete analysis plan. With no sponsor-reported analyses listed, that distinction is central to interpreting the inferential results.

The trial also highlights how a primary endpoint can be more completely reported than secondary outcomes. Although the registry lists outcomes related to peak lung function, symptoms, and health status, numerical results are not reported for all of them. Multiplicity and missing-data methods are also absent from the record. These gaps show why outcome reporting and analysis documentation are part of statistical interpretation, rather than administrative details.

Finally, the sample-size illustrations show how planning depends on the target effect and desired power. They are based on the observed effect and explicit assumptions, not on the trial's original design rationale. Reading them as future-study planning scenarios, rather than as evidence of the trial's observed power, avoids confusing a retrospective calculation with a prospective design decision.

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 comparisons are unadjusted recalculations from group summaries rather than reported sponsor analyses. The comparison standard deviations are approximate because they are reconstructed from the arm-level standard errors. The registry record does not provide participant-level data, the sponsor's model, or detailed methods needed to verify the calculations independently. No discrepancy is flagged, but the available summary information does not establish that every aspect of the original analysis has been reproduced.

The record does not report the original sample-size justification, allocation concealment procedures, masking details, statistical analysis plan, or model specification. It also does not describe how missing FEV1 measurements were handled, how many patients were excluded from the endpoint population, or whether sensitivity analyses were conducted. These omissions limit assessment of bias, robustness, and the relationship between the reported analysis and the original protocol.

Only some of the listed secondary outcomes have numerical results in the registry record. In particular, results for the TDI focal score and SGRQ total score are not reported there. The record also does not report a multiplicity procedure for the range of endpoints and dose comparisons, so unadjusted secondary p-values would not support a family-wise confirmatory interpretation.

Safety information is limited to summary counts and selected serious adverse event terms. The record does not report deaths, event timing, treatment relatedness, or inferential comparisons for the safety outcomes. The trial's endpoint summaries and adverse event figures therefore provide a bounded view of the posted data, not a complete accounting of all outcomes or analyses.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Aclidinium Bromide at Two Dose Levels Versus Placebo Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients — NCT01001494.
• Registry record last updated 2017-01-04; status last verified 2016-10.
• Results first posted 2012-09-17.
• 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 completed phase 3 trial was randomized, double-blind, and parallel-group, comparing inhaled aclidinium bromide 200 μg twice daily and 400 μg twice daily with placebo in patients with COPD. The primary endpoint was change from baseline in morning pre-dose FEV1 at Week 24 among the defined ITT population.

Reported least-squares mean changes were 0.026 liters for the 200 μg group, 0.055 liters for the 400 μg group, and -0.073 liters for placebo. Unadjusted recalculated mean differences versus placebo were 0.099 liters and 0.128 liters, respectively; both had p < 0.001. The record includes serious adverse event counts and selected event terms, but does not report deaths.

The comparisons are recalculations from posted summaries, and several details needed for full assessment—including the sponsor's analysis plan, missing-data methods, and multiplicity procedure—are not reported in the registry record. Numerical results are not available there for every listed secondary outcome.