Pharmacokinetic, Safety and Tolerability Study of Aclidinium/Formoterol Fixed Dose Combination and Formoterol in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Pharmacokinetic, Safety and Tolerability Study of Aclidinium/Formoterol Fixed Dose Combination and Formoterol in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) (NCT01551888), a randomized phase 2 study. The primary outcome is Area Under the Formoterol Plasma Concentration Versus Time Curve (AUC) Over Dosing Interval at Steady State.

2. Clinical Question

3. Trial Design

The registry describes a randomized, phase 2a, two-way crossover study in patients with moderate to severe COPD. Enrollment was 24, and the posted primary pharmacokinetic results list 24 for each treatment. In a crossover design, treatment periods are compared within participants, which can reduce the influence of stable differences between people. The registry does not report the treatment sequence, period length, washout interval, or details about how period or sequence effects were handled.

The two treatments were aclidinium/formoterol 400/12 μg fixed-dose combination via the Almirall inhaler and formoterol 12 μg via the Foradil® Aerolizer®. Both regimens were described as twice-daily inhalations for 4 days, followed by a morning inhalation on Day 5. The study is marked randomized. Its official title describes it as open-label, while the registry’s masking entry is triple; the record does not explain this difference, so the masking details are unclear.

The primary endpoint was formoterol AUC over the dosing interval at steady state. Concentration measurements were scheduled across Day 1 and Day 5, with additional post-dose checks on Days 2–4. The registry identifies the pharmacokinetic analysis population as patients who completed the study and had evaluable pharmacokinetic parameters. It reports the study as completed. The original design’s sample-size rationale, planned treatment sequences, and statistical analysis plan 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.

Period 1

Period 2

Analysis population for the primary outcome, as defined in the registry: The pharmacokinetic (PK) analysis population included all patients who completed the study and had evaluable PK parameters

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 Area Under the Formoterol Plasma Concentration Versus Time Curve (AUC) Over Dosing Interval at Steady State, measured over Day 1: 0, 5, 15 and 30 min and 1, 1.5, 2, 3, 4, 6, 8, and 12 hours (5 min before PM dose) and 5 and 15 min post PM dose; Days 2-4: 0, 5 and 15 min post dose; Day 5: 0, 5, 15 and 30 min and 1, 1.5, 2, 3, 4, 6, 8, and 12 hours (post AM dose).

The primary endpoint is the area under the formoterol plasma concentration-versus-time curve over a dosing interval at steady state, measured in pg*hr/mL. AUC combines concentration measurements across time into a measure of overall drug exposure during the interval. In general, pharmacokinetic researchers use AUC to describe how much of a drug is present in the circulation over time; it is not itself a measure of symptom relief or disease control.

Concentrations were scheduled at multiple times after dosing on Day 1 and Day 5, including measurements through 12 hours, with additional measurements around the evening dose on Day 1. Measurements on Days 2–4 were scheduled shortly after dosing. The record describes the endpoint as a mean and labels its dispersion as standard deviation, with the accompanying description stating that the standard deviation is expressed as a coefficient of variation (%). The posted endpoint therefore concerns formoterol exposure, not the amount of aclidinium exposure.

Using AUC allows the study to compare overall formoterol exposure across the two inhaled regimens rather than relying on a single concentration reading. The registry does not report a clinically meaningful difference threshold for this pharmacokinetic measure, so the clinical importance of a particular difference cannot be determined from the record alone.

7. Results Posted in the Registry

• Aclidinium/Formoterol 400/12 μg FDC: mean 85.15 versus 87.14 on control; difference -1.99 (95% CI -17.86 to 13.88), standardized effect d = -0.07; z-test p = 0.806.

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.

Area Under the Formoterol Plasma Concentration Versus Time Curve (AUC) Over Dosing Interval Following a Single Dose

• 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 deviations.
• Result:
  • Aclidinium/Formoterol 400/12 μg FDC: mean 42.27 versus 41.63 on control; difference 0.64 (95% CI -17.33 to 18.61), standardized effect d = 0.02; z-test p = 0.944.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aclidinium/Formoterol 400/12 μg FDC and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoint concerns formoterol AUC over the dosing interval following a single dose. Its overall pattern is consistent with a small estimated contrast relative to the uncertainty in that comparison: the posted interval includes zero and the unadjusted p-value does not indicate a clear difference. This broadly aligns with the primary endpoint’s lack of conclusive evidence for a difference in formoterol exposure, but the endpoints address different dosing contexts and should not be treated as interchangeable.

The primary endpoint evaluates AUC at steady state, while the secondary endpoint evaluates AUC following a single dose. Together, these measures offer pharmacokinetic perspectives on exposure over time; they do not provide evidence about clinical outcomes such as COPD symptoms or exacerbations. The record lists one secondary outcome and does not report analyses for the secondary outcome in its reported analyses entry.

Unadjusted secondary results generally carry less weight when multiple endpoints or comparisons are considered, because the chance of at least one apparently notable result can increase as more tests are conducted. In general, multiplicity procedures define how to interpret a family of tests and may adjust the threshold or estimates. The registry does not report a multiplicity strategy, a hierarchy among endpoints, or a prespecified role for the secondary result. Accordingly, the secondary finding is best treated as supportive descriptive context rather than as independent confirmation.

The registry lists four outcome measures overall, while the posted secondary outcome information concerns the single-dose AUC measure. Details for any other outcome measures, including their results or analysis status, are not reported in the registry record. The absence of reported analyses means the overall pattern cannot be extended beyond the posted pharmacokinetic summaries.

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

• Area Under the Formoterol Plasma Concentration Versus Time Curve (AUC) Over Dosing Interval Following a Single Dose

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a continuous primary outcome summarized as a mean with dispersion. The comparison is presented as a mean difference between aclidinium/formoterol fixed-dose combination and formoterol. A mean is a summary of the observed measurements, while a mean difference expresses the contrast between the treatment means in the units of the outcome. Here those units are pg*hr/mL. The reported primary difference is -1.99, with a confidence interval from -17.86 to 13.88 and an unadjusted p-value of 0.806.

What does the confidence interval express?

In general, a confidence interval describes uncertainty around an estimated effect. It gives a range of values that are reasonably compatible with the data and the statistical procedure used. The interval is not a guarantee that the true effect lies within its limits, nor does it assign equal plausibility to every value in the interval. Because the primary interval extends below and above zero, the posted data are compatible with differences in either direction as well as with little or no mean difference.

What does the p-value add?

In general, a p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the test assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the probability that the result will replicate. The registry labels the reported comparison unadjusted. The p-value should therefore be read as the result of that comparison, not as evidence that accounts for possible testing across multiple outcomes or analyses.

Why is the crossover design relevant?

In general, a crossover design compares treatments within participants, allowing each person to contribute information under both treatments. Stable participant characteristics can then be less influential than they might be in a parallel-group comparison. This design also makes sequence, period, and carryover effects important considerations. The registry marks the model as crossover, but the treatment sequences, washout, period details, and method for handling these effects are not reported in the registry record. It is therefore not possible to assess from the posted information how these features entered the analysis.

How should the dispersion be understood?

The registry labels the primary measure’s dispersion as standard deviation and describes it as expressed as the coefficient of variation (%). A standard deviation describes spread around a mean in the measurement scale, while a coefficient of variation expresses spread relative to the mean. The record’s wording is important when interpreting the displayed variability: it indicates a percentage expression rather than a raw amount in pg*hr/mL. In general, variability can affect how precisely a treatment contrast is estimated, but it does not by itself indicate whether a difference is clinically important.

What are the limits of the posted analysis detail?

The record includes no reported analysis entries and does not describe an adjusted statistical model for the primary comparison. It does not report whether the comparison accounts for the crossover structure, nor does it state the confidence-interval construction or any prespecified analysis population beyond the definition of the pharmacokinetic population. The outcome is based on participants who completed the study and had evaluable PK parameters, but missing-data procedures and sensitivity analyses are not reported in the registry record. These gaps make it difficult to judge robustness beyond the posted summary comparison.

The simple recalculation displayed with the posted summary statistics is an unadjusted comparison, not a replacement for a sponsor analysis. The registry’s discrepancy indicator is false, so no difference between that recalculation and the posted comparison is flagged. In general, an unadjusted calculation from group summaries cannot reproduce analyses that account for participant-level crossover data or other model features when those details are unavailable.

11. Confidence Intervals and Precision

The primary mean difference is -1.99 pg*hr/mL, and its confidence interval ranges from -17.86 to 13.88. The interval includes zero, so it does not isolate a difference in one direction. It also spans values on either side of the point estimate, indicating that the estimated contrast is uncertain. The point estimate alone should not be treated as a precise statement of the underlying difference.

In general, a confidence interval communicates both the direction and the precision of an estimate. A narrow interval constrains the range of effects compatible with the data more tightly; a wide interval leaves more uncertainty. The primary interval allows a range of possible contrasts, and the registry does not report a threshold defining which differences would matter clinically. It is therefore not possible to classify the full interval as clinically negligible or important based on the record.

The unadjusted p-value is 0.806, but a p-value does not show that the estimate is precise. Nor does an interval that includes zero prove equality. Demonstrating equivalence would require a defined equivalence margin and a suitable analysis; neither is reported in the registry record. The crossover design may affect precision, but the available summary does not include the participant-level or period-level information needed to evaluate that contribution.

The result describes the pharmacokinetic analysis population: participants who completed the study and had evaluable PK parameters. The registry does not report how many otherwise eligible participants lacked evaluable measurements or how missing concentration data were handled. Such information would help readers assess whether the uncertainty captured by the interval reflects the full intended analysis population.

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 sample-size illustrations are expressed as participants per arm, not as total events. They use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These are planning assumptions for the illustration; the original trial’s design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the planned number of participants per arm that, under those assumptions, would give an 80% chance of detecting the chosen effect if that effect were real. The 90% power column uses a higher target chance of detection, so its participant requirement is larger under the same assumptions. Power is conditional on the assumed effect size and analysis conditions; it is not a guarantee that a study will find a result or that the assumed effect is correct.

The rows consider planning for the full observed effect and smaller fractions of it. Smaller effects are harder to distinguish from sampling variability, so the illustrations require more participants when the target effect is smaller. This is not observed power: it is a planning illustration based on the observed effect, rather than a measure of what the completed study achieved.

The registry does not report whether the original design used these assumptions or any related sample-size calculation. The illustrations also do not, by themselves, account for unreported features such as crossover sequence, missing data, or the analysis model. They should be read as conditional planning examples, not as a retrospective evaluation of the study’s success.

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 = -1.990; pooled standard deviation σ = 28.051.
2. n = 2 × (1.96 + 0.842)² × 28.051² / -1.990² = 3,119.1, rounded up to 3,120 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 <- -1.98999999999999                      # observed difference in means
sigma <- 28.0511140598729                     # 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(1551888)
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 = 3,120 (80% power), 4,176 (90% power)
 75% of observed effect: n per arm = 5,546 (80% power), 7,424 (90% power)
 50% of observed effect: n per arm = 12,477 (80% power), 16,703 (90% power)
power.t.test: 3120.1 
Simulated power at n = 3,120 per arm: 0.800 (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 four outcome measures overall and one posted secondary outcome. It reports no analyses in the reported analyses entry. The primary comparison and a secondary comparison are available as posted results, but the record does not explain which outcomes were prespecified for formal hypothesis testing, whether any hierarchy was planned, or whether a multiplicity adjustment was used. The primary p-value is explicitly unadjusted.

In general, multiplicity matters when several outcomes, time points, or comparisons are tested. Each test creates an opportunity for a result to look unusual by chance, and the chance of at least one such result can increase across a family of tests. A prespecified strategy may control that risk or define which outcomes are confirmatory. Without a reported strategy, individual unadjusted p-values should not be read as if they necessarily represent a single isolated test. The record does not establish whether multiplicity was addressed in the sponsor’s analysis.

The analysis population is described as all patients who completed the study and had evaluable PK parameters. The record does not report the number of participants excluded from that population, the reasons for missing or unevaluable concentration data, or procedures for missing values. It also does not describe sensitivity analyses to evaluate the influence of missing data.

Further details about the crossover analysis are not reported. The registry does not describe the handling of treatment sequence, period, or carryover effects, or whether a model accounted for repeated measurements within participants. The original statistical analysis plan, including any prespecified estimand or covariate adjustment, is not reported in the registry record. These absences limit assessment of whether the posted summary fully reflects the planned analysis and how robust the results are to alternative analytic choices.

These limitations do not invalidate the reported summaries, but they constrain the claims that can be made from them. The mean differences and their unadjusted intervals describe the posted comparisons; they do not settle how additional outcomes, unreported analyses, or missing data might affect an overall interpretation.

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

Serious events with the highest arm-level rate: aortic valve incompetence (4.2%), lacunar infarction (4.2%), aortic aneurysm (4.2%).

The registry reports serious adverse events affecting 0 participants in the aclidinium/formoterol group and 2 in the formoterol group. Other adverse events affected 0 participants in either group. Each group’s at-risk count is reported as 24. These are counts of participants affected as recorded, not a complete description of event timing, severity beyond the serious classification, or causal attribution.

The record lists Aortic valve incompetence, Lacunar infarction, and Aortic aneurysm among the top serious-event terms, each with a reported frequency of 4.2%. It does not link these terms to a specific treatment group in the posted information, so they should not be assigned to one group on that basis. Death counts are not reported in the registry record.

Safety counts from a study of this size are descriptive and do not establish whether an event was caused by treatment or whether there is a meaningful difference in risk. The registry’s short dosing schedule and the available summaries also do not provide a basis for conclusions about longer-term safety. These figures should be read as the adverse-event record for this study, not as a complete safety profile.

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

The primary result describes a comparison of formoterol exposure over a dosing interval at steady state. The estimated mean difference is -1.99 pg*hr/mL, with a confidence interval from -17.86 to 13.88 and an unadjusted p-value of 0.806. The interval includes zero and allows differences in either direction. The posted data therefore do not establish a clear difference in this pharmacokinetic endpoint.

That conclusion is narrower than saying the treatments are the same. The registry does not report an equivalence margin or a noninferiority analysis. A nonsignificant p-value does not prove equivalence, and a point estimate close to zero does not rule out differences that the interval still permits. The registry also does not define how large a change in AUC would be clinically important.

The endpoint is a measure of formoterol exposure, not a direct measure of COPD symptoms, lung function, exacerbations, quality of life, or survival. Consequently, the result does not establish whether either regimen changes those clinical outcomes. The study’s stated purpose included pharmacokinetics, safety, and tolerability, but the posted primary result should not be generalized to a claim about overall clinical benefit.

The safety summaries report serious adverse events in the formoterol group and none in the combination group, alongside no other adverse events affecting participants in either group. These descriptive counts do not determine causation or comparative risk. The event terms and death information are incomplete for assessing a broader safety profile, and the registry does not report deaths.

Interpretation is also limited by the absence of detail on crossover sequences, period effects, missing-data handling, multiplicity, and the original analysis plan. The record supports a focused reading of the posted pharmacokinetic estimates and adverse-event counts, while leaving questions about broader clinical meaning unresolved.

17. Why This Trial Matters Statistically

This study illustrates why a pharmacokinetic endpoint needs to be interpreted on its own terms. AUC summarizes drug exposure over time, but it is not a patient-centered clinical outcome. The posted estimate can inform a question about formoterol exposure under the tested regimens without answering whether COPD symptoms or other clinical outcomes differ.

The crossover design also highlights the value of reporting analytic details alongside summary comparisons. Within-participant treatment comparisons can be useful, but sequence, period, and carryover considerations affect how such evidence should be analyzed. The registry identifies the design as crossover without reporting how those features were handled. That makes the posted means and intervals interpretable at a descriptive level, while limiting evaluation of the full analytic approach.

The confidence interval offers more information than the point estimate alone: it indicates that the result remains compatible with a range of possible differences. At the same time, the absence of an equivalence margin prevents a claim that the regimens have equivalent exposure. This distinction is central to interpreting a result that does not show a clear difference.

Finally, the sample-size illustrations demonstrate how planning requirements depend on the effect targeted and on assumptions about the analysis. They are not a substitute for the trial’s original design rationale, which is not reported in the registry record. Overall, the record provides a focused pharmacokinetic comparison and descriptive safety counts, while showing why design, precision, and reporting details are essential to determine what a clinical trial can support.

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 limitations are specific to the information reported for this study. The official title describes the trial as open-label, but the registry masking entry is triple. The record does not explain the discrepancy, so the masking procedures and their practical implications cannot be determined from the registry information.

The study is identified as a two-way crossover, but the record does not report treatment sequence, period length, washout, or analyses of period and carryover effects. Those details matter when evaluating a within-participant pharmacokinetic comparison. Without them, the role of the crossover structure in the reported estimate cannot be assessed.

The primary analysis population includes study completers with evaluable PK parameters. The registry does not report missing-data counts, reasons for unevaluable profiles, or methods for handling incomplete concentration measurements. It also does not provide participant-level data or a detailed model specification, limiting independent evaluation of the comparison.

Although the registry lists four outcome measures, it provides only one posted secondary outcome description, and no reported analyses are listed. A multiplicity plan and the original statistical analysis plan are not reported. The record also does not report a clinically meaningful AUC threshold or an equivalence margin. Thus, statistical evidence about a difference cannot be translated into a claim about clinical importance or equivalence.

Finally, the safety information is descriptive, the event terms are not linked to treatment groups in the posted summary, and deaths are not reported in the registry record. These limits make the findings best suited to a focused reading of the available pharmacokinetic estimates and reported adverse-event counts.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Pharmacokinetic, Safety and Tolerability Study of Aclidinium/Formoterol Fixed Dose Combination and Formoterol in Patients With Moderate to Severe Chronic Obstructive Pulmonary Disease (COPD) — NCT01551888.
• Registry record last updated 2017-02-14; status last verified 2016-12.
• Results first posted 2016-11-23.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

This completed randomized phase 2a study compared aclidinium/formoterol 400/12 μg fixed-dose combination with formoterol 12 μg in patients with moderate to severe COPD. It used a two-way crossover design and evaluated pharmacokinetics, safety, and tolerability. The primary endpoint was formoterol AUC over the dosing interval at steady state.

The posted primary comparison reports a mean difference of -1.99 pg*hr/mL, with a confidence interval from -17.86 to 13.88 and an unadjusted p-value of 0.806. The interval includes zero, so the record does not establish a clear difference in the primary pharmacokinetic endpoint. Serious adverse events affected 0 participants in the combination group and 2 in the formoterol group; other adverse events affected 0 in either group.

Important details—including the original sample-size rationale, crossover analysis, missing-data procedures, and multiplicity plan—are not reported in the registry record. The results support a focused description of pharmacokinetic exposure and reported safety counts, not conclusions about clinical benefit or equivalence.