Efficacy and Safety of Aclidinium Bromide 400 µg BID (Twice a Day)Compared to Placebo in Patients With Stable Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Aclidinium Bromide 400 µg BID (Twice a Day)Compared to Placebo in Patients With Stable Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) (NCT01471171), a randomized phase 3 study. The primary outcome is Change From Baseline in Endurance Time (Seconds).

2. Clinical Question

The study also assessed change from baseline in trough inspiratory capacity and intensity of dyspnoea at week 3. Those outcomes provide related measures of lung volume and breathlessness, but the registry identifies endurance time as the primary endpoint. The record gives treatment-period summaries and a mean difference with a confidence interval for the primary result. The statistical methods used in the trial’s original protocol, including how the crossover structure was handled in the primary analysis, are not reported in the registry record.

3. Trial Design

This was a Phase 3, randomized, double-blind, placebo-controlled crossover trial sponsored by AstraZeneca. The registry lists enrollment of 112 and a completed study. The trial started in 2011-11, and primary completion was in 2012-06. Its official title describes a multiple-dose, two-period crossover study of aclidinium bromide 400 μg BID and exercise endurance in people with stable moderate to severe COPD.

In a crossover design, participants receive more than one treatment in different periods, so each participant may contribute information under both treatment conditions. This can allow comparisons that account for differences between participants, but interpretation depends on the analysis respecting the paired and period-based structure. The registry does not report the treatment sequences, washout arrangements, or the primary model’s treatment of participant, period, and sequence effects. Those details should not be inferred from the design label alone.

Each treatment is described as lasting 3 weeks. The primary endpoint and both posted secondary outcomes are changes from baseline assessed at week 3. The primary summary lists 109 participants for aclidinium bromide and 107 for placebo; these are the counts associated with the posted treatment summaries, not the enrollment figure. The reported ITT definition requires at least one dose and a baseline and post-dose primary efficacy assessment in one of the treatment periods. The registry wording after that definition is incomplete, so further details about exclusions or population handling are not reported in the registry record.

Randomization and double masking are reported, but the method used to generate the random sequence, how masking was maintained, and whether masking was assessed are not reported in the registry record. The original sample-size justification, planned statistical model, interim analyses, and prespecified multiplicity approach are also not reported in the registry record. The posted results include summary values and comparisons, but a registry record does not by itself establish all of the procedures used in the full trial conduct or analysis.

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: Eligible patients entered a 14-21 day run-in period to assess disease stability. During this period, one site visit was performed to familiarise patients with study testing procedures (body plethysmography, spirometry and a constant work rate cycle exercise test).

Treatment Period 1

Reasons for not completing this period:

Treatment Period 2

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 had at least a baseline and one post-dose corresponding assessment value of the primary efficacy variable in one of the 2 treatment periods. 2 patients from the safety population were excluded from 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 Endurance Time (Seconds), measured over Week 3.

The primary endpoint was change from baseline in endurance time, measured in seconds, at week 3. Endurance was assessed during constant work rate cycle ergometry, with participants exercising to symptom limitation at 75% of Maximum Work load (Wmax). The endpoint therefore expresses how the duration of exercise at a fixed workload changed from the participant’s baseline assessment over the treatment period.

Exercise endurance is used in this trial as a functional measure of performance during a standardized exercise test. It differs from a direct measure of lung function: it captures the time participants can continue the specified exercise before symptom limitation, rather than an isolated physiological measurement. The protocol description also connects the study question to hyperinflation and dyspnoea at rest and during exercise, while the posted secondary outcomes include trough inspiratory capacity and intensity of dyspnoea.

The registry reports least-squares means and standard errors for the treatment summaries. It gives an aclidinium bromide mean change of 68.3 seconds and a placebo mean change of 9.8 seconds. The posted comparison is a mean difference of 58.5 seconds, with a 95% confidence interval from 6.112 to 110.9 and an unadjusted p-value of 0.029. These statistics describe the reported treatment contrast; the registry does not report enough detail to establish how the original trial analysis incorporated the paired crossover observations.

7. Results Posted in the Registry

• Aclidinium Bromide 400 μg Bid: mean 68.30 versus 9.80 on control; difference 58.50 (95% CI 6.11 to 110.89), standardized effect d = 0.30; z-test p = 0.029.

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 Trough Inspiratory Capacity (IC) (Litres)

• 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 400 μg Bid: mean 0.10 versus 0.02 on control; difference 0.08 (95% CI 0.01 to 0.15), standardized effect d = 0.31; z-test p = 0.024.
• Interpretation:
  • 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.

Change From Baseline in Intensity of Dyspnoea

• 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 400 μg Bid: mean -0.48 versus 0.15 on control; difference -0.63 (95% CI -1.18 to -0.08), standardized effect d = -0.30; z-test p = 0.026.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Aclidinium Bromide 400 μg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes address related but distinct aspects of the study question: trough inspiratory capacity represents a lung-volume measure, while intensity of dyspnoea represents a symptom measure. Their posted comparisons point in directions that are broadly consistent with the primary result’s focus on exercise-related function and symptoms. This broad pattern can add context, but it does not make the secondary endpoints interchangeable with exercise endurance or establish that one measure explains another.

The registry reports two secondary outcomes and no reported analyses for them. Their posted estimates and unadjusted p-values are descriptive evidence within the study record. The record does not state a family-wise testing plan, hierarchical sequence, or multiplicity adjustment. When several outcomes are examined, the chance of at least one apparently noteworthy result can increase; adjustment or a prespecified testing strategy helps control that issue. Without such information, secondary p-values carry less confirmatory weight than a prespecified primary endpoint.

Secondary outcomes may also have different scales, measurement properties, and sources of variability. A common direction across measures can be informative, but it does not prove a shared mechanism or establish the robustness of the primary estimate. The results should be considered alongside the primary endpoint, the crossover design, the reported uncertainty, and the missing details about the original analysis plan. The registry does not report whether these secondary measures were selected in advance as confirmatory outcomes or how their missing observations were handled.

In particular, a statistically notable secondary result does not repair uncertainty about the primary model or its confidence interval. Nor should the absence of an adjustment be interpreted as evidence that no adjustment was needed. The record’s unadjusted results support a cautious account of the overall pattern, while stronger claims about confirmation or consistency would require information about prespecification and multiplicity that is not reported in the registry record.

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

• Change From Baseline in Trough Inspiratory Capacity (IC) (Litres)
• Change From Baseline in Intensity of Dyspnoea

9. Statistical Interpretation

10. Statistical Methods Explained

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of an average outcome. It may differ from a simple arithmetic average if the model adjusts for factors or accommodates the study design. In this registry record, the arm summaries are identified as least-squares means, but the model terms, covariates, and handling of the crossover structure are not reported. The posted arm means can be described, but the precise adjustment behind them cannot be reconstructed from the registry information.

What does the mean difference express?

The mean difference expresses the treatment contrast on the original outcome scale. For the primary endpoint, the unit is seconds, so a difference of 58.5 refers to the contrast in change in endurance time. Its sign follows the comparison as reported: a positive value indicates a higher change for aclidinium bromide than placebo. This is an estimate of an average contrast; it does not imply that all participants experienced the same change.

For the secondary outcomes, the contrasts are expressed in the outcomes’ own units. The registry reports a difference of 0.078 litres for trough inspiratory capacity and -0.63 units on a scale for intensity of dyspnoea. The meaning of a direction depends on how each measure is coded. The registry names the measures and units, but it does not give additional interpretation details or an explicit scale direction for dyspnoea.

Why does the crossover design matter?

In a crossover trial, treatment comparisons may use the fact that the same participant receives both treatments. This can account for stable differences between people, but it also means the paired observations are correlated. An analysis that treats all treatment summaries as independent can misrepresent uncertainty if it ignores that correlation. Period effects, sequence effects, and possible carryover from one treatment period to another may also be relevant to the design. The registry does not report the model or methods used to address these features, nor does it report sequence or washout details.

The comparison statistics also include recalculated, unadjusted quantities derived from posted summary statistics. The standard deviations used for these calculations are approximate, inferred from the reported standard errors and participant counts; they are not directly reported standard deviations. Accordingly, pooled standardized effects and planning illustrations based on those values should not be treated as exact trial estimates. The posted primary mean difference and confidence interval remain the principal reported contrast for interpretation. The registry record does not indicate a discrepancy between the posted result and the recalculated comparison.

How should the p-value be understood?

A p-value is a measure of how compatible the observed data are with a specified null model, under the assumptions of the analysis. A smaller p-value indicates less compatibility with that null model; it does not state the probability that the treatment has no effect. It also does not quantify the size, practical importance, or certainty of an effect on its own. The primary p-value is 0.029 and is unadjusted. The registry does not report a multiplicity adjustment or the complete statistical analysis plan, so the p-value should be interpreted in that context.

What information does the confidence interval add?

A confidence interval gives a range of values for the treatment contrast that are compatible with the data under the statistical model and its assumptions. In repeated use of the same procedure, 95% confidence intervals would cover the true parameter in 95% of such repetitions if the model assumptions hold. For a particular trial, the interval is not a probability statement that the fixed true value lies within its endpoints. It gives more information than a single estimate by showing the uncertainty and range of plausible effect sizes under the analysis.

For the primary outcome, the reported 95% confidence interval is 6.112 to 110.9 seconds. Its width reflects uncertainty in the estimated contrast. The interval does not account for unreported design or analysis choices, and it cannot determine whether any point within it meets a clinical-importance threshold. Such a threshold is not reported in the registry record.

What does a standardized effect add?

A standardized effect expresses a mean contrast relative to a measure of variability, allowing outcomes measured on different scales to be compared in a scale-free way. The primary recalculated standardized effect is 0.298. In this record, the pooled variability is approximate because it is derived from standard errors and counts. In addition, a simple pooled calculation may not represent the within-participant variability of a crossover trial. It is therefore a supplementary descriptive calculation, not a substitute for the treatment contrast in seconds or for the original trial analysis.

Standardized effects can help describe the magnitude relative to observed variation, but they depend on how that variation is estimated and on the population and design. They do not determine clinical importance. In a crossover study, an estimate based on independent-group assumptions may miss the precision available from paired data or fail to reflect the actual analysis. The registry does not report the covariance between treatment-period observations needed to reconstruct a paired standardized effect.

11. Confidence Intervals and Precision

The primary mean difference is 58.5 seconds, with a 95% confidence interval from 6.112 to 110.9 seconds. The estimate is positive, and the interval’s endpoints are both above zero. The interval nevertheless spans a range of possible average contrasts, from a relatively small positive difference to a substantially larger one. A point estimate alone would conceal that uncertainty; the interval makes the range of estimates compatible with the analysis more visible.

Precision describes how narrowly an estimate is located, not whether the estimate is clinically important or free of bias. The interval’s width depends on the data and the statistical model. Because the registry record does not report the primary model’s treatment of the crossover design, participant pairing, or period effects, the stated interval should be understood as the posted interval rather than independently verified as an appropriate interval for every feature of the design.

The endpoint summaries report standard errors of 18.8 seconds for aclidinium bromide and 19.0 seconds for placebo. A standard error describes uncertainty in an estimated mean, not the spread of individual participant values. The comparison interval is the more direct measure of precision for the treatment contrast. The registry does not provide the participant-level data or the within-participant covariance needed to assess the contrast independently.

The confidence interval is not a guarantee that the true effect is inside its endpoints, nor does it express the probability that the treatment has a particular effect. It also does not include uncertainty arising from unreported choices in the protocol, missing-data handling, or multiplicity procedures. No clinical threshold for interpreting the magnitude of change in endurance time is reported in the registry record. Thus, the interval supports a description of statistical precision, but not a judgment about clinical importance by itself.

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 participant counts per arm, not total event counts. They are illustrations based on the observed effect, rather than the original trial’s design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The trial’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm indicated by those assumptions for an 80% chance of detecting the specified effect if that effect is the true one and the model assumptions hold. The 90% power column gives the corresponding per-arm number for a 90% chance. These are design-planning quantities, not probabilities that the observed trial result is correct. This is not observed power.

Planning for 100% of the observed effect uses the full estimated contrast as the effect to detect. Planning for 75% or 50% of the observed effect asks what sample size would be needed if the true effect were smaller than the estimate. Smaller target effects require more participants to distinguish them from random variation at the stated significance level and power. The resulting numbers are illustrations rather than recommendations for a future trial: they inherit uncertainty from the observed estimate, and the calculation uses a normal approximation and equal allocation. The crossover design and its paired observations are not represented by the stated two-arm planning assumptions, so these figures should not be read as a reconstruction of the study’s actual design planning.

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 = 58.500; pooled standard deviation σ = 196.406.
2. n = 2 × (1.96 + 0.842)² × 196.406² / 58.500² = 176.9, rounded up to 177 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 <- 58.5                      # observed difference in means
sigma <- 196.406474377934                     # 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(1471171)
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 = 177 (80% power), 237 (90% power)
 75% of observed effect: n per arm = 315 (80% power), 422 (90% power)
 50% of observed effect: n per arm = 708 (80% power), 948 (90% power)
power.t.test: 177.9 
Simulated power at n = 177 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 lists one primary outcome and two secondary outcomes. The reported p-values are unadjusted. A multiplicity procedure, such as an adjustment across outcomes or a prespecified order for testing, is not reported in the registry record. When multiple statistical tests are conducted, interpreting each unadjusted p-value as if it were the only test can overstate the strength of evidence. The primary endpoint remains the central result, while the secondary comparisons warrant more caution.

The registry does not report the trial’s complete statistical analysis plan, including the prespecified model, covariates, treatment of period and sequence effects, or handling of the within-participant nature of the crossover design. It also does not report whether interim analyses were planned or conducted. These absences mean that the posted comparisons cannot be fully checked against the original analysis plan from the registry information alone.

The ITT population is described as randomized patients who took at least one dose and had a baseline and at least one post-dose primary assessment in one of the two treatment periods. That definition includes an assessment requirement, so it is not possible to determine from the wording alone how participants without the required measurements were handled. The registry does not report the missing-data method, reasons for missing observations, or sensitivity analyses. It also does not give a complete account of exclusions for each outcome or treatment period.

Because the study is a crossover trial, incomplete observations may affect paired comparisons differently from independent-group comparisons. Details about whether participants with only one evaluable period contributed to the analysis, and how any such data were used, are not reported in the registry record. These gaps do not establish that the analysis was inappropriate; they limit what can be assessed from the posted registry information. A full protocol and statistical analysis plan would be needed to evaluate these choices in detail.

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: troponin t increased (0.9%), chronic obstructive pulmonary disease (0.9%).

The registry reports serious adverse events for 0 of 111 participants in the aclidinium bromide group and 2 of 108 participants in the placebo group. It also reports other adverse events for 7 of 111 participants receiving aclidinium bromide and 4 of 108 receiving placebo. The record lists Troponin T increased and chronic obstructive pulmonary disease among the top serious event terms, each at 0.9%. The registry does not provide enough detail in these figures to establish event relatedness or explain individual cases.

These are counts recorded for the treatment groups, not a complete characterization of the nature, timing, severity, or cause of every event. The study’s crossover design means participants could contribute exposure to both treatments; the registry does not explain how adverse-event exposure periods or participant overlap were handled in these group summaries. Death counts are not reported in the registry record. The displayed counts should therefore be read as the posted safety summaries, not as a basis for concluding that one treatment is safer or less safe.

Rare or serious events can be difficult to characterize in a trial of this size and duration. These figures describe what was recorded in the study; they do not establish the presence or absence of risk outside the trial. No medical advice or individual treatment conclusion follows from these group-level counts.

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

The posted primary result is an estimated positive difference in change in exercise endurance time between the aclidinium bromide and placebo treatment periods. The mean difference is 58.5 seconds, with a 95% confidence interval from 6.112 to 110.9 seconds. This describes the average contrast estimated from the posted results. It does not mean that every participant improved, or that the same response would occur for each person.

The endpoint is a standardized exercise-test measure collected after 3 weeks of treatment. It is not a direct measure of every aspect of COPD, and it does not by itself describe longer-term outcomes, daily activity, or effects on outcomes not included in the registry results. The registry’s secondary outcomes add related physiological and symptom measures, but the unadjusted results should not be treated as separate confirmation without information on multiplicity and prespecification.

The estimate and confidence interval do not establish clinical importance. A threshold for a clinically important change in endurance time is not reported in the registry record. Nor does a p-value indicate the probability that a treatment effect exists, or guarantee that the reported association is free of bias. The primary p-value is unadjusted, and important details of the original crossover analysis are absent from the record.

The trial’s randomized, double-blind crossover design is relevant to how the findings should be analyzed and interpreted. Yet the registry does not report the treatment sequence, washout, handling of period or carryover effects, or the exact model. The reported estimate should be described faithfully while retaining that limitation. The findings are about the enrolled study population and the reported treatment periods; applicability to other groups, durations, or settings is not established by these results alone.

These statistics are not medical advice and should not be used as an individual treatment decision. They give a quantitative account of the posted trial results and the uncertainty and reporting gaps that surround them.

17. Why This Trial Matters Statistically

This trial illustrates why a study’s design matters alongside its headline estimate. In a crossover trial, each participant may receive both treatments, so the comparison can depend on within-participant pairing and on treatment-period structure. The registry identifies the design as crossover but does not report the model’s handling of those features. Without those details, readers should distinguish the posted treatment contrast from a fully assessable account of the original analysis.

The result also illustrates why a confidence interval is more informative than a p-value alone. The mean difference of 58.5 seconds is accompanied by a 95% confidence interval from 6.112 to 110.9 seconds, making visible the range of precision associated with the estimate. A p-value of 0.029 is unadjusted and does not describe effect size or clinical importance. The interval and estimate provide complementary information, while neither resolves missing methodological details.

Multiplicity is another statistical issue. The record includes a primary outcome and two secondary outcomes, but does not report an adjustment or testing hierarchy. Secondary results can support context, yet without a reported plan their evidential status is different from that of a primary endpoint. Clear reporting of prespecified outcomes and analysis procedures would help readers judge how much weight to place on each comparison.

Finally, sample-size illustrations based on observed effects are useful for understanding how planning needs change as a target effect gets smaller, but they do not reveal the assumptions used to design this trial. The original justification is not reported in the registry record. Separating planning illustrations from original design decisions, and separating posted estimates from unavailable analysis details, helps keep statistical interpretation accurate and appropriately bounded.

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.

Several trial-specific limitations follow from the information available in the registry record. The study is described as a two-period crossover trial, but the treatment sequences and any washout are not reported. The original analysis model and its handling of participant pairing, period effects, sequence effects, and possible carryover are also not reported. These details are especially relevant to interpreting the precision of a crossover comparison.

The registry’s description of the ITT population is incomplete after stating that participants needed a baseline and at least one post-dose assessment of the primary outcome in one treatment period. The number of participants with usable data in each period is not fully explained, and the missing-data approach and sensitivity analyses are not reported. It is therefore not possible to assess the potential effect of incomplete measurements on the posted estimates from the registry record alone.

The primary summaries are least-squares means, but the model specification and covariates are not reported. The statistical analysis plan, multiplicity strategy, and interim-analysis information are also not reported. The p-values are unadjusted, which limits the confirmatory interpretation of results across several outcomes.

In addition, the available primary comparison includes recalculated quantities based on summary statistics, with approximate standard deviations inferred from standard errors and participant counts. Such quantities do not recover the within-participant covariance required for a paired crossover analysis. The trial’s short treatment periods and the absence of a reported clinical-importance threshold also limit conclusions about duration of effect and practical importance. These are reporting and interpretive limits; they do not by themselves demonstrate that the study was conducted or analyzed improperly.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Aclidinium Bromide 400 µg BID (Twice a Day)Compared to Placebo in Patients With Stable Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) — NCT01471171.
• Registry record last updated 2017-01-04; status last verified 2016-10.
• Results first posted 2013-07-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry describes a completed Phase 3, randomized, double-blind, placebo-controlled, two-period crossover trial sponsored by AstraZeneca, with enrollment of 112. It assessed aclidinium bromide 400 μg BID and placebo during 3-week treatment periods in patients with stable moderate to severe COPD.

The primary outcome was change from baseline in endurance time at week 3 during constant work rate cycle ergometry to symptom limitation at 75% of Maximum Work load (Wmax). The posted mean difference was 58.5 seconds, with a 95% confidence interval from 6.112 to 110.9 and an unadjusted p-value of 0.029. Two secondary outcomes were posted. The registry does not report the complete analysis plan, multiplicity approach, missing-data methods, or key details of the crossover analysis.