Efficacy of Aclidinium Bromide Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy of Aclidinium Bromide Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients (NCT00868231), a randomized phase 2 study. The primary outcome is Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 0-12 hr at Day 15 on Treatment..

2. Clinical Question

The registry describes the study’s broader purpose as evaluating efficacy, safety, and tolerability of multiple doses of inhaled aclidinium in moderate to severe COPD. The interventions listed include aclidinium at 400 μg twice daily, tiotropium at 18 μg once daily, and placebo. The posted primary result is specifically for the 400 μg aclidinium regimen and the Day 15 FEV1 endpoint; the record does not establish results for other aclidinium doses.

The primary outcome is a continuous lung-function measure. Its reported treatment summaries are least-squares means, with standard errors as the measure of spread. The key statistical comparison is the mean difference between each active treatment and placebo, expressed in liters. The estimates and intervals describe the posted data; they do not by themselves answer every question about the study’s broader efficacy, safety, or tolerability aims.

3. Trial Design

This was a phase 2, randomized, double-blind crossover study sponsored by AstraZeneca. The registry records 30 participants enrolled and lists COPD as the condition. The study started in 2009-03, reached primary completion in 2009-07, and is recorded as completed. It included inhaled aclidinium bromide 400 μg twice daily, inhaled tiotropium 18 μg once daily, and placebo.

In a crossover design, participants receive more than one study condition in a planned sequence. In general, this can allow comparisons to account for stable differences between participants, because a participant may contribute observations under multiple conditions. Correct interpretation can also depend on treatment sequence, period effects, and whether effects from one period carry into another. The sequence, period structure, washout details, and the statistical handling of these features are not reported in the registry record, so the posted summary statistics do not establish how those design features were handled.

The primary endpoint population is described as patients who took at least one dose and had both a baseline and a post-dose FEV1 value. For that endpoint, the reported numbers are 29 for aclidinium, 28 for tiotropium, and 27 for placebo. These are outcome-specific counts; they are not the same as the enrollment count. The registry does not explain why the counts differ across treatment conditions or whether all enrolled participants contributed data to every period.

The trial is registered as phase 2, but its original sample-size justification, intended power, allocation sequence, and detailed statistical plan are not reported in the registry record. The record lists 12 outcome measures and no reported analyses. As a result, the posted results give useful summaries of the measured outcomes, but they do not document all design and analysis decisions needed for a full reconstruction of the trial’s statistical approach.

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 had at least a 5-day run-in period (and a maximum of 9 days) to assess patient's clinical stability.

Treatment Period 1

Reasons for not completing this period:

Treatment Period 2

Reasons for not completing this period:

Treatment Period 3

Reasons for not completing this period:

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

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 Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 0-12 hr at Day 15 on Treatment., measured over Day 15.

The primary endpoint is change from baseline in normalized forced expiratory volume in one second (FEV1) area under the curve over 0–12 hours at Day 15, measured in liters. FEV1 is the volume of air a person can forcefully exhale in the first second of a breath. An area-under-the-curve measure combines readings across a stated time window to describe lung function over that window, rather than at a single instant. Normalization expresses the area in a form intended to represent the average level across the interval.

Change from baseline focuses on how the Day 15 measurement differs from the participant’s starting measurement. Comparing changes between treatment conditions can help describe whether the average change differs across those conditions. The registry reports least-squares means, which are model-based means, and standard errors for the treatment summaries. The detailed model used to obtain those means is not reported in the registry record.

FEV1 is commonly used in clinical research as a quantitative measure of airflow limitation. In general, a continuous endpoint preserves more information about the range of measured values than a binary classification would. Its interpretation still depends on the measurement protocol, analysis model, and study context. The endpoint is a physiological measurement; it does not alone describe symptoms, daily functioning, or every aspect of COPD.

The primary result estimates the difference in mean change between each active treatment and placebo at Day 15. It therefore addresses a particular treatment contrast, time point, and lung-function interval. It should not be read as a direct measure of all outcomes included in the study’s broader aims.

7. Results Posted in the Registry

• Aclidininum Bromide 400 μg Bid: mean 0.24 versus 0.01 on control; difference 0.22 (95% CI 0.03 to 0.41), standardized effect d = 0.60; z-test p = 0.025.
• Tiotropium 18 μg Once-daily: mean 0.26 versus 0.01 on control; difference 0.24 (95% CI 0.05 to 0.44), standardized effect d = 0.67; z-test p = 0.013.

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 Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 12-24hr at Day 15 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:
  • Aclidininum Bromide 400 μg Bid: mean 0.17 versus -0.03 on control; difference 0.21 (95% CI 0.01 to 0.40), standardized effect d = 0.56; z-test p = 0.039.
  • Tiotropium 18 μg Once-daily: mean 0.10 versus -0.03 on control; difference 0.13 (95% CI -0.07 to 0.32), standardized effect d = 0.35; z-test p = 0.199.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aclidininum Bromide 400 μg Bid than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Tiotropium 18 μg Once-daily and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 0-24 hr at Day 15 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:
  • Aclidininum Bromide 400 μg Bid: mean 0.23 versus -0.01 on control; difference 0.23 (95% CI 0.06 to 0.41), standardized effect d = 0.70; z-test p = 0.009.
  • Tiotropium 18 μg Once-daily: mean 0.18 versus -0.01 on control; difference 0.18 (95% CI 0.01 to 0.36), standardized effect d = 0.56; z-test p = 0.039.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aclidininum Bromide 400 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 Tiotropium 18 μg Once-daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC0-12) in Liters at Day 1 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:
  • Aclidininum Bromide 400 μg Bid: mean 0.23 versus 0.02 on control; difference 0.21 (95% CI 0.10 to 0.32), standardized effect d = 0.98; z-test p = <0.001.
  • Tiotropium 18 μg Once-daily: mean 0.18 versus 0.02 on control; difference 0.16 (95% CI 0.05 to 0.27), standardized effect d = 0.75; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Aclidininum Bromide 400 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 Tiotropium 18 μg Once-daily than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary FEV1 results generally point in the same direction as the primary comparison: active-treatment estimates tend to be higher than placebo estimates across the reported time windows. The degree of precision varies. Some unadjusted intervals exclude zero, while others include zero, so the secondary comparisons do not all provide the same level of statistical evidence. The values and intervals for each endpoint are reported with the corresponding results.

These secondary outcomes examine FEV1 over other time windows and at another treatment day, complementing rather than replacing the Day 15 0–12-hour primary endpoint. The registry also identifies secondary FVC outcomes. The record lists 11 posted secondary outcome measures, but the registry does not report a complete set of analysis details for interpreting their results collectively.

Secondary outcomes can help describe whether patterns are consistent across related measures and measurement windows. They are usually less decisive when numerous outcomes are examined and the analysis plan does not state how they were prioritized. Here, the record lists 12 outcome measures and no reported analyses. It does not report a multiplicity adjustment or a testing hierarchy. As a result, unadjusted secondary p-values should be treated as exploratory evidence rather than as independent confirmation of the primary result.

The alignment in direction across the posted secondary FEV1 contrasts is relevant context, but it does not remove uncertainty about model specification, missing observations, or multiple testing. Nor should consistency across related lung-function measurements be mistaken for evidence about outcomes that were not measured or reported. The secondary findings broaden the description of the trial’s lung-function data while leaving the primary endpoint as the main registered question.

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

• Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 12-24hr at Day 15 on Treatment
• Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 0-24 hr at Day 15 on Treatment
• Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC0-12) in Liters at Day 1 on Treatment
• Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 12-24 hr at Day 1 on Treatment
• Change From Baseline in Normalised Forced Expiratory Volume in One Second (FEV1) Area Under the Curve (AUC) 0-24 hr at Day 1 on Treatment
• Change From Baseline in Normalised Forced Vital Capacity (FVC) Area Under the Curve (AUC) 0-12 hr at Day 15 on Treatment
• Change From Baseline in Normalised Forced Vital Capacity (FVC) Area Under the Curve (AUC) 12-24 hr at Day 15 on Treatment
• Change From Baseline in Normalised Forced Vital Capacity (FVC) Area Under the Curve (AUC) 0-24 hr at Day 15 on Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and its arm summaries are reported as least-squares means with standard errors. A least-squares mean is generally a model-based estimate of an average, often adjusted for terms in a statistical model. The record does not give enough detail to identify the model terms or confirm how the estimates account for the crossover design. The standard error describes the estimated uncertainty in a mean; it is not the same as the spread of individual participant measurements.

What does the contrast estimate represent?

The reported contrast is the difference between an active treatment’s estimated mean change and the placebo estimated mean change. For the primary endpoint, the posted summaries give a positive difference for aclidinium versus placebo and for tiotropium versus placebo. A difference is expressed in the endpoint’s units, liters. The recalculated estimates use the posted arm-level means and standard errors. Their pooled standard deviations are approximate, as indicated in the calculation record, rather than directly reported participant-level variability.

In general, an unadjusted comparison does not account for additional covariates or design features unless those are already reflected in the summary estimates. The registry does not report the analysis code or full model specification, and it lists no reported analyses. The contrast and p-value calculations should therefore be distinguished from a sponsor-reported model result. The discrepancy indicator is false, but that does not add details about the analysis plan or prove that every design feature has been handled.

How should the p-value be read?

A p-value summarizes how unusual data at least as incompatible with a specified no-difference model would be, assuming that model and its assumptions apply. The primary p-values reported for the recalculated contrasts are unadjusted. In general, an unadjusted p-value does not account for the fact that several outcomes or treatment comparisons may have been examined. It is not the probability that the no-difference hypothesis is true, nor does it measure clinical importance. A smaller p-value also does not guarantee a more precise or more consequential estimate.

The record lists 12 outcome measures and no reported analyses. It does not report whether a primary analysis was specified in advance, how secondary outcomes were prioritized, or whether any multiplicity adjustment was planned or applied. Those omissions matter when considering the overall evidence across many measurements. The p-values are most appropriately viewed together with the effect estimates and confidence intervals, rather than as standalone labels.

Why does the crossover structure matter?

In general, crossover trials can use within-participant comparisons, which may reduce the influence of stable differences between participants. The statistical analysis must still represent the sequence and period structure appropriately, and it may need to consider carryover. Those details can affect standard errors and treatment contrasts. The registry record identifies a crossover model but does not report the treatment sequences, period-specific data, washout arrangements, or analysis terms. The available arm summaries do not let a reader verify how within-person correlation was handled. For that reason, the recalculated contrasts from summary statistics should not be mistaken for a reconstruction of a crossover model.

What does the uncertainty calculation assume?

The comparison calculations use estimated means and standard errors, with approximate pooled variability. Such summary-based calculations cannot reproduce the full participant-level analysis. In general, a confidence interval quantifies uncertainty under the calculation’s assumptions; it does not capture every source of uncertainty, such as model misspecification, measurement limitations, or missing data. The registered record does not document the original analysis assumptions in enough detail to evaluate them fully.

The planning illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They use the observed effect or a stated fraction of it as the target effect. These are planning calculations derived from the posted summaries, not evidence about the original trial’s sample-size design. The original sample-size assumptions are not reported in the registry record.

In general, over-dispersion means that observed variability is greater than a chosen model expects. If it is not accounted for, standard errors can be too small and intervals too narrow. The registry’s use of standard errors and approximate pooled standard deviations does not provide enough information to assess over-dispersion. That assessment would require details of the participant-level data and model diagnostics, which are not reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated mean differences are accompanied by 95% confidence intervals: 0.028 to 0.414 liters for aclidinium versus placebo, and 0.051 to 0.439 liters for tiotropium versus placebo. Each interval is above zero, while each also spans a range of possible differences rather than identifying a single exact value. The endpoints of the intervals indicate the uncertainty around the estimated contrasts under the calculation’s assumptions.

In general, a confidence interval is a range produced by a statistical procedure that, over repeated use under its assumptions, would cover the true parameter at the stated rate. It is not a probability statement that this particular interval contains the true value. Nor does it account automatically for bias, incomplete outcome data, an incorrectly specified model, or the multiplicity of analyses.

The intervals are based on unadjusted recalculations from posted summary statistics. Their precision depends on the reported means and standard errors, and the recalculations use approximate pooled variability. Because the registry does not report participant-level data or the full crossover analysis, the intervals cannot be checked against a complete model that accounts for within-participant measurements, treatment sequence, and period effects.

The study enrolled 30 participants, while the primary outcome summaries use treatment-specific counts of 29, 28, and 27. This limited number of observations contributes to uncertainty, but the registry does not provide a formal analysis of how enrollment or missing observations affected precision. The confidence intervals describe statistical precision under the calculation, not the overall certainty of all conclusions about treatment or clinical importance.

Both intervals include differences that are closer to zero than the point estimates, as well as larger positive differences. The registry does not report a clinically important threshold for this endpoint. Therefore, statistical precision can be described from the intervals, but clinical importance cannot be inferred from their position alone.

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 event counts. This is a continuous-outcome study, so the event-count convention for time-to-event outcomes does not apply. Each planning row uses a target effect defined as a stated fraction of the observed effect for the relevant comparison; the figures should be read as hypothetical design illustrations, not as the number of participants in the completed study.

The calculations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The 80% power column indicates the number of participants per arm that the calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning estimate for a 90% chance. These are probability targets for a hypothetical future study, not guarantees that a study with that enrollment will produce a particular result.

Planning for a smaller effect requires more participants per arm, because a smaller difference is harder to distinguish from random variation when variability is otherwise similar. The rows for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect illustrate that relationship. The assumed effect sizes are based on the observed contrasts, which may be uncertain estimates themselves.

The original sample-size justification, assumptions, and intended power for this trial are not reported in the registry record. These planning calculations do not show whether the trial was adequately sized according to its original protocol. They are not observed power: observed power is not an appropriate way to reinterpret the p-value after results are known, and these figures are forward-looking planning illustrations based on the posted effect estimates.

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 = 0.221; pooled standard deviation σ = 0.368.
2. n = 2 × (1.96 + 0.842)² × 0.368² / 0.221² = 43.5, rounded up to 44 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 <- 0.221                      # observed difference in means
sigma <- 0.367819702209294                     # 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(868231)
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 = 44 (80% power), 59 (90% power)
 75% of observed effect: n per arm = 78 (80% power), 104 (90% power)
 50% of observed effect: n per arm = 174 (80% power), 233 (90% power)
power.t.test: 44.5 
Simulated power at n = 44 per arm: 0.796 (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 lists 12 outcome measures and no reported analyses. The primary endpoint is identifiable, but the record does not report a statistical analysis plan describing a hierarchy among the outcomes, a prespecified testing sequence, or an adjustment for multiple comparisons. The p-values attached to the recalculated comparisons are unadjusted.

In general, testing many outcomes or contrasts increases the chance that at least one result will appear unusual by chance, even if no true difference exists. Multiplicity procedures can control that risk in different ways, but the appropriate method depends on the planned questions and how conclusions will be drawn. Without a documented testing strategy, isolated secondary p-values should not be treated as if each were the only comparison made.

The primary endpoint population is described as patients who took at least one dose and had a baseline and at least one post-dose FEV1 value. That definition gives some information about who contributed to the primary measure, but the record does not explain how participants with incomplete measurements were handled, whether imputation was used, or whether sensitivity analyses were performed. Missing-data assumptions and methods are not reported in the registry record.

Outcome-specific counts vary across treatment conditions. The registry does not explain the reasons for the differences or describe how missing observations in a crossover study were incorporated. It also does not report whether all randomized participants were analyzed according to their assigned sequence or whether any additional analysis populations were defined. The stated ITT description should therefore be read as the registry’s operational definition for the primary outcome, not as evidence about every analysis detail.

In general, missingness can affect both the estimated treatment contrast and its precision, especially if the likelihood of missing data is related to treatment or outcome. The available summaries cannot establish whether missingness was balanced or whether the analysis assumptions were reasonable. These gaps limit assessment of the robustness of the estimates and the strength of conclusions drawn across the full set of registered outcomes.

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 (3.3%).

The registry reports serious adverse events for 0 of 29 participants in the aclidinium group, 0 of 28 in the tiotropium group, and 1 of 30 in the placebo group. The listed top serious adverse event term is chronic obstructive pulmonary disease, reported as 3.3%. These figures describe events recorded in the registry; they do not establish that an event was caused by a study treatment.

Other adverse events affected 2 of 29 participants in the aclidinium group, 0 of 28 in the tiotropium group, and 3 of 30 in the placebo group. The serious-event and other-event counts are distinct registry summaries, and the record does not provide enough detail to infer event timing, recurrence, severity beyond the serious classification, or treatment relatedness for the individual events.

Death counts are not reported in the registry record. Zero serious adverse events in a group does not mean that no safety risk exists; it means no serious event was recorded for that group in these posted results. With 30 participants enrolled, these counts are descriptive and limited in their ability to characterize uncommon events. They should not be used alone to compare overall safety or to make treatment decisions.

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

The primary posted summaries show positive estimated changes in FEV1 for the active treatment conditions and a smaller positive change for placebo. The recalculated active-versus-placebo differences are positive, and their 95% confidence intervals exclude zero. This describes the pattern of the measured primary endpoint at Day 15 under the study conditions.

The estimates do not establish the size of any effect in a broader population with precision, because the study enrolled 30 participants and the intervals allow a range of possible differences. The record does not report a threshold for clinical importance, so statistical separation from zero cannot by itself establish that a difference matters to patients. It also does not provide enough information to assess how the analysis handled all features of the crossover design.

The secondary findings offer related measurements of lung function, with varying precision and unadjusted analyses. Their overall direction provides context, but the number of outcomes and absence of a reported multiplicity strategy limit the weight of isolated secondary results. The registry’s safety counts are descriptive, and the small enrollment does not allow strong conclusions about uncommon adverse events.

These results address a specific treatment comparison and lung-function endpoint. They do not directly establish effects on symptoms, quality of life, exacerbations, long-term outcomes, or other outcomes not described in the posted results. Nor do they show how the results apply outside the participants and conditions studied. Whether a treatment is appropriate for an individual is a clinical question, not one answered by these statistical summaries.

The most defensible reading is therefore narrow: the registry’s primary summaries favor active treatments over placebo on the specified Day 15 FEV1 change measure, with uncertainty represented by the reported intervals. Further interpretation depends on details not reported in the registry record, including the original analysis plan, crossover modeling, missing-data handling, and clinical-importance criteria.

17. Why This Trial Matters Statistically

This study illustrates how a small randomized crossover trial can produce detailed repeated lung-function measurements while still leaving substantial uncertainty about analysis and interpretation. The design may offer within-participant information in general, but the registry record does not report the sequences, periods, or model terms needed to assess whether the posted comparisons fully reflect that structure.

It also demonstrates why effect estimates, confidence intervals, and p-values need to be read together. A positive contrast gives the estimated direction and size in liters; the interval expresses uncertainty; the p-value summarizes compatibility with a no-difference model under calculation assumptions. None of these alone establishes clinical importance, and unadjusted p-values become harder to interpret when many outcomes are registered.

The planning illustrations show how sample-size requirements depend on the effect chosen for detection. Using a fraction of the observed effect can be useful for planning future research, but an observed estimate from a small study is uncertain. These illustrations are distinct from the original design justification, which is not reported in the registry record, and they are not evidence of observed power.

Finally, the record distinguishes enrollment from endpoint-specific participant counts and gives a limited operational definition of the primary outcome population. That distinction is important when reading results from trials with repeated measurements and multiple conditions. Without detailed reporting of missing-data handling, the analysis model, and multiplicity decisions, readers can describe the posted statistics but cannot fully audit the original inferential framework.

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 main limitation is the modest enrollment: 30 participants were enrolled, with primary endpoint counts of 29, 28, and 27 across the listed treatment conditions. The registry does not explain the differences in these counts or report a missing-data analysis. The estimates may therefore be sensitive to individual observations, while the available record does not permit an assessment of that sensitivity.

The study is identified as a crossover trial, but details needed to evaluate the analysis of a crossover design are not reported. Treatment sequence, period effects, washout arrangements, carryover assessment, and the model used to account for repeated observations are not described. Summary-based recalculations cannot reproduce a participant-level crossover analysis, and their approximate pooled variability adds another limitation.

The registry lists 12 outcome measures and no reported analyses. It does not document a multiplicity plan, statistical analysis plan, sample-size justification, or the original intended power. Unadjusted secondary comparisons consequently require particular caution. The planning illustrations are based on observed effects and do not fill the gap in the original design rationale.

The primary endpoint measures FEV1, not every dimension of COPD or patient experience. A clinical-importance threshold is not reported, and the results do not establish effects on outcomes beyond those measured. Safety information is also limited: the small number of participants and the registry’s summary counts cannot characterize uncommon events or establish causality. These limitations constrain how broadly the posted findings can be interpreted.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy of Aclidinium Bromide Administered in Chronic Obstructive Pulmonary Disease (COPD) Patients — NCT00868231.
• Registry record last updated 2017-01-04; status last verified 2016-09.
• Results first posted 2012-09-12.
• 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 2, randomized, double-blind crossover study of inhaled aclidinium, tiotropium, and placebo in moderate to severe COPD. It records 30 participants enrolled and identifies change from baseline in normalized FEV1 area under the curve over 0–12 hours at Day 15 as the primary outcome.

The primary posted summaries show positive recalculated differences versus placebo for aclidinium and tiotropium, with 95% confidence intervals above zero. These are unadjusted calculations from summary statistics; the record lists no reported analyses. It also lists 12 outcome measures, while original sample-size assumptions, multiplicity methods, detailed crossover modeling, and missing-data handling are not reported in the registry record.

Serious adverse event counts were 0 of 29 for aclidinium, 0 of 28 for tiotropium, and 1 of 30 for placebo; death counts are not reported in the registry record. Overall, the posted results describe a limited set of lung-function and safety observations from a small trial and should be interpreted with the stated statistical and reporting uncertainties.