Evaluate the Effect of Aclidinium Bromide on Long-term Cardiovascular Safety and Exacerbations in Moderate to Very Severe COPD Patients.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Evaluate the Effect of Aclidinium Bromide on Long-term Cardiovascular Safety and Exacerbations in Moderate to Very Severe COPD Patients. (NCT01966107), a randomized phase 4 study. The primary outcome is Rate of Moderate or Severe Chronic Obstructive Pulmonary Disease (COPD) Exacerbations Per Subject Per Year During the First Year of Treatment.

2. Clinical Question

The clinical question is framed as a comparison of event rates over exposure time, rather than simply a comparison of the proportion of participants who had at least one exacerbation. A participant may experience more than one event, and the rate expresses the number of events relative to time under observation and treatment. This makes exposure time relevant to the endpoint.

The registry describes a study of long-term cardiovascular safety as well as COPD exacerbations. The primary result discussed in the record concerns exacerbations during the first year, while the treatment period could continue longer. The record identifies a secondary cardiovascular outcome concerning participants with a major adverse cardiovascular event or other serious cardiovascular events of interest, but a numerical result for that outcome is not reported in the registry record.

3. Trial Design

ASCENT COPD was a Phase IV, randomized, double-blind, placebo-controlled, parallel-group study sponsored by AstraZeneca. The registry record lists the study as completed. It records a start date of 2013-10-16 and a primary completion date of 2017-09-21. Enrollment was 3635. The primary endpoint analysis included participants in the Full Analysis Set who took at least one dose of double-blind study treatment and were analyzed according to their randomized group.

Participants were assigned to aclidinium bromide or placebo. Both arm descriptions specify a two-week washout/run-in period for patients using a long-acting muscarinic antagonist, followed by a double-blind treatment period of up to 36 months. The primary endpoint covers the first 12 months of treatment, so its measurement window is shorter than the maximum treatment period.

Randomization is intended, in general, to make treatment groups comparable at baseline on average, including for measured and unmeasured characteristics. Double blinding is intended, in general, to limit the influence of treatment knowledge on participant behavior, care, and outcome assessment. The registry lists quadruple masking; it does not specify in the record which roles were included in that masking designation.

The primary outcome description says the rate analysis accounted for treatment group, baseline inhaled corticosteroid use, baseline COPD severity, history of at least 1 exacerbation in the past year, and smoking status. It also describes log exposure time as an offset, adjusted for the time participants experienced exacerbations. The specific model used for the primary analysis and its full fitted results are not reported in the registry record. The registry does report a Negative Binomial Regression model for the secondary hospitalization-rate analysis.

The registry record does not report the original sample-size justification, planned allocation ratio, detailed treatment adherence, or the statistical decision rules for the trial. Those items should not be inferred from the observed enrollment or from planning illustrations based on the observed effect.

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: Informed consent form was signed; inclusion/exclusion, smoking status, electrocardiogram, pregnancy test, Pulmonary function testing, Chronic obstructive pulmonary disease (COPD) exacerbation were assessed. Out of 3635 subjects, 5 subjects were duplicated, who, in violation of protocol entrance criteria, entered the study more than once.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The Full Analysis Set (FAS) population consisted of all subjects in the Randomized Population who took at least one dose of the double-blind IP (aclidinium bromide or placebo). Subjects were analyzed according to their randomized treatment.

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.

Population: The Full Analysis Set (FAS) population consisted of all subjects in the Randomized Population who took at least one dose of the double-blind IP (aclidinium bromide or placebo). Subjects were analyzed according to their randomized treatment.

6. Primary Endpoint

The registry lists the primary outcome as Rate of Moderate or Severe Chronic Obstructive Pulmonary Disease (COPD) Exacerbations Per Subject Per Year During the First Year of Treatment, measured over 12 months.

The primary endpoint is the rate of moderate or severe COPD exacerbations per subject per year during the first 12 months of treatment. The unit is events per subject per year. The registry describes an on-treatment analysis and an offset based on exposure time, with the analysis accounting for several baseline factors. An offset allows the model to relate event counts to the amount of time participants were observed and at risk of recording events.

Rates are useful when participants contribute different amounts of observation time or when the outcome can recur. A count of participants with any event would not distinguish a participant with one event from a participant with multiple events. A rate retains information about the event count while putting it in relation to exposure time. This is a general statistical explanation of rate outcomes.

The posted group estimates are 0.44 events per subject per year for aclidinium bromide, with a 95% confidence interval from 0.4 to 0.5, and 0.57 for placebo, with a 95% confidence interval from 0.52 to 0.64. The comparison is expressed as a rate ratio, so the reference value for no relative rate difference is 1. The registry describes the endpoint timeframe as 12 months. The endpoint does not, by itself, summarize cardiovascular safety, all COPD outcomes, or the experience of every randomized participant regardless of treatment exposure.

7. Results Posted in the Registry

• Aclidinium Bromide: 0.44 versus 0.57 (Events per subject per year) on control; rate ratio 0.77 (95% CI 0.66–0.90, derived from the posted confidence limits); p ≈ <0.001.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Rate of Hospitalizations Due to COPD Exacerbation Per Subject Per Year During the First Year of Treatment- on Treatment Analysis

• Endpoint type: Event rate: events per unit of follow-up, compared as a rate ratio.
• Test: Poisson rate ratio, with the standard error taken from the posted confidence limits.
• Result:
  • Aclidinium Bromide: 0.07 versus 0.10 (Events per subject per year) on control; rate ratio 0.70 (95% CI 0.50–0.98, derived from the posted confidence limits); p ≈ 0.039.
• Interpretation:
  • The 95% confidence interval excludes no difference (a ratio of 1), so the event rate is statistically lower for Aclidinium Bromide than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the clinical questions beyond the primary first-year rate of moderate or severe COPD exacerbations. One secondary outcome concerns the rate of hospitalizations due to COPD exacerbation during the first year of treatment. The other concerns the number of participants with a major adverse cardiovascular event or other serious cardiovascular events of interest. This makes the secondary outcomes relevant to interpreting the trial's broader respiratory and cardiovascular aims, but they are not substitutes for the primary endpoint.

For hospitalization rates, the registry reports both an unadjusted recalculation from posted summary statistics and a Negative Binomial Regression result. The model-based result is reported as a rate ratio of 0.65, with a 95% confidence interval from 0.48 to 0.89 and p = 0.006. The distinction between the recalculation and the model result matters: they arise from different analytical approaches, and the model result should be identified as the registry's reported analysis rather than combined with the recalculation.

A numerical result for the secondary cardiovascular event outcome is not reported in the registry record. The adverse-event counts elsewhere in the record are not equivalent to a result for the specifically defined MACE or other serious cardiovascular events outcome, and should not be treated as such.

Secondary outcomes generally carry less evidential weight than a prespecified primary outcome when multiple outcomes or comparisons are examined. If many tests are performed, the chance of at least one apparently notable result can increase unless the analysis plan accounts for multiplicity. The registry record does not report whether a multiplicity adjustment was used, how outcomes were prioritized beyond naming the primary endpoint, or whether secondary results were confirmatory. The secondary findings therefore provide additional descriptive and analytical context, but the available record does not establish how they were intended to affect formal trial-wide conclusions.

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

• Rate of Hospitalizations Due to COPD Exacerbation Per Subject Per Year During the First Year of Treatment- on Treatment Analysis
• Number of Participants With Major Adverse Cardiovascular Event (MACE) or Other Serious Cardiovascular Events of Interest - On-study Analysis

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a recurrent-event rate, not a single event time or a simple binary outcome. In general, recurrent-event data can contain multiple events for a participant, and the time each participant contributes to the analysis can differ. A rate model relates the event count to exposure time. The registry's description says the log of exposure time was used as an offset and that time associated with experienced exacerbations was accounted for. The offset serves to put counts on a common time-exposure scale rather than treating every participant as if they contributed identical observation time.

Why use a rate ratio?

A rate ratio compares the estimated event rate in one group with the estimated rate in another. A value of 1 represents equal rates under the comparison; values below or above 1 indicate lower or higher estimated rates in the numerator group, respectively. This is a general interpretation of the measure. For this primary endpoint, the posted unadjusted recalculation gives a rate ratio of 0.772, and its 95% confidence interval is 0.663 to 0.899. These values are relative, so the arm-specific rates are also important for understanding the scale of events per subject per year.

What does the confidence interval represent?

A confidence interval reflects the uncertainty associated with an estimate under a statistical procedure and its assumptions. In general, a 95% confidence procedure is designed to produce intervals that contain the target parameter in 95% of repeated samples under those assumptions. It is not a statement that the particular interval has a 95% probability of containing a fixed parameter. For a rate ratio, an interval containing 1 is compatible with equal rates under the model, while an interval entirely on one side of 1 indicates that the corresponding two-sided interval excludes equality. These are general explanations; the interval's reliability depends on whether the statistical assumptions are suitable.

What does the offset do?

In a count model, an offset commonly incorporates exposure time so that the estimated quantity is a rate rather than a raw count. A participant observed for a shorter time does not automatically contribute the same exposure as someone observed for longer. The registry description specifies the log of exposure time as the offset and says it was adjusted for the time participants experienced exacerbations. It also lists baseline inhaled corticosteroid use, baseline COPD severity, history of at least 1 exacerbation in the past year, and smoking status as factors. The exact primary model specification and the adjusted primary estimates are not reported in the registry record.

How should the posted comparison be distinguished from a model result?

The primary arm rates and comparative estimate are accompanied by a Poisson-based unadjusted recalculation from posted summary statistics. That calculation is not a substitute for a reported adjusted model analysis. The primary endpoint description indicates that baseline factors were included in the analysis plan as described in the record, but the registry does not give the primary model's fitted rate ratio, confidence interval, or p-value. Therefore, the estimate discussed as a recalculation should be read as a summary-statistic comparison, not as a claim about the full adjusted analysis.

The distinction matters because adjustment can change an estimate or its uncertainty, particularly if adjustment variables relate to event frequency or exposure time. In general, a model-based result also depends on how the outcome distribution is represented. A Poisson model typically assumes that the conditional variance is tied to the conditional mean. When event counts are more variable than that assumption permits, over-dispersion may lead to standard errors that are too small. Models such as negative binomial regression can allow greater variability. This is a general explanation, not evidence that a particular assumption was violated in this primary analysis. The registry reports a Negative Binomial Regression model for a secondary hospitalization-rate analysis, but does not identify the primary endpoint model by that name.

The secondary hospitalization outcome illustrates why result source and analysis method should be kept distinct. Its posted summary-statistic recalculation gives a rate ratio of 0.7, with a 95% confidence interval from 0.499 to 0.981 and an unadjusted p-value of 0.039. The registry also reports a Negative Binomial Regression model result for that outcome: a rate ratio of 0.65, a 95% confidence interval from 0.48 to 0.89, and p = 0.006. These are different analyses, not interchangeable estimates. The reported model result is the model-based result recorded by the sponsor; the recalculation is an unadjusted calculation from posted summary values.

Masking and randomization relate to trial conduct, while the model and its assumptions relate to statistical analysis. In general, random assignment helps support a fair group comparison, and masking can reduce some influences of treatment knowledge. Neither feature removes uncertainty in the estimated effect or resolves limitations in reporting. The registry record does not describe interim analyses, a multiplicity adjustment strategy, missing-data procedures, or a full statistical analysis plan. Those details should not be inferred from the endpoint description or from the reported p-values.

11. Confidence Intervals and Precision

The primary unadjusted rate ratio is 0.772, with a 95% confidence interval from 0.663 to 0.899. The interval gives a range of estimates consistent with the posted calculation under its statistical assumptions. Its endpoints are both below 1, the equal-rate reference for a rate ratio. This conveys uncertainty about the magnitude of the relative comparison; it does not make the estimate exact or remove dependence on the analysis assumptions.

The arm-specific rates also have confidence intervals: 0.44 events per subject per year, from 0.4 to 0.5, for aclidinium bromide; and 0.57, from 0.52 to 0.64, for placebo. These intervals describe uncertainty in the individual group rates. They should not be used as a substitute for the interval around the rate ratio, because the comparative estimate has its own uncertainty calculation.

Precision depends on factors such as the number of observed events, exposure time, and variability in event counts. In general, a confidence interval becomes more informative when the data contain more information, but event clustering or over-dispersion can reduce precision relative to a simple count model's assumptions. The registry identifies a Poisson-based calculation for the posted primary comparison. The primary model's full specification and an adjusted primary confidence interval are not reported in the registry record, limiting assessment of precision under the described covariate-adjusted analysis.

The reported p-value, <0.001, addresses compatibility with a no-difference null under the calculation; it is not a precision measure by itself. The interval communicates both direction and a range of plausible relative values. Neither should be interpreted as a measure of clinical importance without a relevant clinical context, which is not quantified in the registry record.

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 illustrations express sample size as participants per arm, not total events. They are planning calculations based on the observed effect, rather than a report of the trial's original design assumptions. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect as the effect to detect.

The row for 100% of the observed effect uses the full observed effect as the planning target. The 75% and 50% rows consider progressively smaller effects. For example, planning for 75% of the observed effect gives 809 participants per arm for 80% power and 1,083 participants per arm for 90% power. Planning for 50% of the observed effect gives 1,758 participants per arm for 80% power and 2,353 participants per arm for 90% power. The full-effect scenario gives 472 participants per arm for 80% power and 632 participants per arm for 90% power.

In plain language, the 80% power column is the estimated number of participants per arm for a design that would have an 80% chance of detecting the specified effect under the planning assumptions if that effect were real. The 90% power column uses a higher target chance of detection and therefore requires more participants per arm for the same effect scenario. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants when the target effect is reduced.

These calculations are not observed power. They are planning illustrations derived from the observed effect and stated assumptions. The original trial sample-size rationale, original target effect, and original design assumptions are not reported in the registry record. They cannot be inferred from enrollment or from these retrospective illustrations.

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, λ₀ and λ₁ are event rates per patient-year, and T is follow-up per participant in years. This assumes Poisson counts and equal follow-up.

Worked calculation for this trial

1. Control rate λ₀ = 0.5700; treatment rate λ₁ = 0.4400 events per patient-year; follow-up T = 1.00 years.
2. n = (1.96 + 0.842)² × (1/0.5700 + 1/0.4400) / (1.00 × [ln(0.772)]²) = 471.7, rounded up to 472 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
lambda0 <- 0.57                      # control rate, events per patient-year
lambda1 <- 0.44                      # treatment rate
tt      <- 1                       # follow-up per participant, years
n_per_arm <- function(power, frac = 1) {
  l1 <- lambda0 * (lambda1 / lambda0)^frac   # smaller effect = fraction of the observed log rate ratio
  ceiling(round((z_a + qnorm(power))^2 * (1 / lambda0 + 1 / l1) / (tt * log(l1 / lambda0)^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 = ",")))

# Simulation 1: Poisson counts. Simulation 2: over-dispersed counts (variance = 1.5 x mean), analysed with the matching variance.
set.seed(1966107)
n    <- n_per_arm(0.80)
reps <- 20000
m0 <- lambda0 * n * tt; m1 <- lambda1 * n * tt
x0 <- rpois(reps, m0); x1 <- rpois(reps, m1)
z  <- log(x1 / x0) / sqrt(1 / x0 + 1 / x1)
cat(sprintf("Simulated power, Poisson counts, n = %s per arm: %.3f\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE)))
phi <- 1.5
y0 <- rnbinom(reps, mu = m0, size = m0 / (phi - 1)); y1 <- rnbinom(reps, mu = m1, size = m1 / (phi - 1))
z2 <- log(y1 / y0) / sqrt(phi * (1 / y0 + 1 / y1))
cat(sprintf("Simulated power, over-dispersed counts (phi = 1.5), same n: %.3f\n", mean(abs(z2) > z_a, na.rm = TRUE)))

Output from running the code

100% of observed effect: n per arm = 472 (80% power), 632 (90% power)
 75% of observed effect: n per arm = 809 (80% power), 1,083 (90% power)
 50% of observed effect: n per arm = 1,758 (80% power), 2,353 (90% power)
Simulated power, Poisson counts, n = 472 per arm: 0.802
Simulated power, over-dispersed counts (phi = 1.5), same n: 0.634

The first simulation draws Poisson counts and should land close to the target power. The second allows extra variability (variance 1.5 times the mean, a purely illustrative value), which lowers the power at the same sample size, so rate trials usually need more participants than the Poisson formula suggests.

14. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when several outcomes, timepoints, groups, or statistical comparisons are evaluated. In general, carrying out multiple tests can increase the chance of obtaining at least one small p-value even when no underlying effect exists. A prespecified testing sequence or an adjustment procedure can address this issue, but the approach depends on the trial's design and analysis plan. The registry record does not report a multiplicity strategy, an outcome hierarchy beyond identifying the primary endpoint, or whether reported secondary tests were adjusted.

The record identifies four outcome measures and two analyses, and lists secondary outcomes concerning hospitalization rates and MACE or other serious cardiovascular events. This listing does not establish that every outcome was analyzed or reported in a comparable way. The registry record does not report a numerical result for the cardiovascular secondary outcome. The reported p-values should therefore be read in the context of the outcome and analysis to which each applies, without assuming that they were adjusted for other comparisons.

The primary population is defined as the Full Analysis Set: all randomized participants who took at least one dose of double-blind study treatment, analyzed according to randomized treatment. This is the population definition recorded for the primary outcome. It does not mean that every randomized participant necessarily contributed the same amount of exposure time or remained on treatment throughout the full possible treatment period.

The primary outcome is described as an on-treatment analysis, and its rate calculation uses exposure time as an offset. This indicates that the analysis concerns events and exposure while participants were on treatment, as described in the record. The registry does not report how treatment discontinuation, missed visits, incomplete outcome information, or other missing data were handled. It also does not report sensitivity analyses assessing the effect of missingness or deviations from the on-treatment approach. These omissions limit assessment of whether missing information could have influenced the estimates.

The original statistical analysis plan, interim analysis procedures, and rationale for the original sample size are not reported in the registry record. Without those details, it is not possible to determine from the record whether the posted analyses followed prespecified decision rules or how any unreported analyses were treated. This is a limitation of the available reporting, not evidence that a particular procedure was or was not used.

15. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 2% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pneumonia (3.7%), atrial fibrillation (1.3%), coronary artery disease (1.2%), cardiac failure congestive (1.2%), non-cardiac chest pain (0.9%).

The registry lists serious adverse events affecting 409 participants in the aclidinium bromide group and 356 in the placebo group. It lists other adverse events affecting 1105 and 1065 participants, respectively. Deaths are listed as 75 in the aclidinium bromide group and 64 in the placebo group. These are counts, not risk-adjusted comparisons, and they should not be interpreted as evidence of a treatment effect by themselves. The record does not provide a comparative safety estimate or confidence interval for these counts.

The listed serious adverse-event terms include Pneumonia at 3.7%, Atrial Fibrillation at 1.3%, Coronary Artery Disease at 1.2%, Cardiac Failure Congestive at 1.2%, Non-Cardiac Chest Pain at 0.9%, and Acute Respiratory Failure at 0.9%. The registry record does not specify the denominator basis for these term percentages in the information, so they should not be converted into comparative risks.

Counts of participants with serious adverse events are distinct from the specifically defined secondary outcome concerning MACE or other serious cardiovascular events of interest. The numerical result for that outcome is not reported in the registry record. Group counts alone do not account for differences in exposure, event timing, severity mix, or chance variation.

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

The posted primary result is an estimate of the first-year rate of moderate or severe COPD exacerbations during on-treatment follow-up in the Full Analysis Set. The arm-specific estimates are 0.44 events per subject per year for aclidinium bromide and 0.57 for placebo. Their unadjusted recalculated rate ratio is 0.772, with a 95% confidence interval from 0.663 to 0.899 and an unadjusted p-value of <0.001. In statistical terms, the posted comparison estimates a lower rate in the aclidinium bromide group over this defined period.

This result does not alone establish the size of an individual participant's benefit or predict an individual's future outcome. It is a group-level estimate with uncertainty. It also does not by itself answer the study's cardiovascular safety question, which concerns a different outcome. The registry record gives serious adverse-event counts and deaths, but does not report a numerical result for the named MACE or other serious cardiovascular event outcome.

The result is specific to the recorded population, endpoint definition, analysis window, and on-treatment approach. It should not automatically be generalized to people outside the moderate to very severe COPD population described, to longer-term rates beyond the stated first-year endpoint, or to unreported subgroups. The registry does not report subgroup-specific primary results or a fully specified adjusted primary model estimate.

The confidence interval and p-value characterize statistical evidence under the posted calculation, not clinical importance or certainty that the same estimate would appear in another study. Clinical interpretation also depends on the outcome's relevance, study conduct, and the broader evidence, none of which can be fully resolved by a single registry result. No treatment recommendation follows from these statistical results alone.

Finally, the record's omissions matter. The original sample-size rationale, multiplicity approach, detailed missing-data handling, and primary model's fitted adjusted result are not reported. Those details would help readers judge how the primary and secondary analyses were planned and how robust the conclusions are to analytic choices. The posted numbers support a description of the recorded comparison, while leaving those broader questions open.

17. Why This Trial Matters Statistically

This trial is statistically informative because its primary endpoint is a recurrent-event rate rather than a one-time binary outcome. The distinction matters: repeated exacerbations contribute to the count, and exposure time is incorporated into the rate. The registry's description of an offset makes explicit that time under observation is part of the outcome analysis rather than an incidental detail.

The trial also illustrates why relative estimates, absolute rate scales, and uncertainty should be read together. The rate ratio gives a relative comparison, while the rates express events per subject per year. The confidence interval conveys uncertainty around the relative estimate. A p-value alone would not communicate the estimated magnitude or its precision.

There is a further methodological distinction between a simple unadjusted recalculation from posted summary statistics and a model-based result. The primary endpoint description names baseline factors and exposure-time adjustment, but the adjusted primary model result is not reported in the registry record. For the secondary hospitalization-rate outcome, both a recalculation and a Negative Binomial Regression result are reported. Keeping those results separate prevents an unadjusted calculation from being mistaken for the sponsor's model analysis.

Finally, the trial's broad cardiovascular safety aims and its primary COPD exacerbation endpoint address different questions. Serious adverse-event counts are not equivalent to a comparative estimate for a defined cardiovascular outcome. The record therefore demonstrates why endpoint-specific reporting, analysis details, multiplicity information, and missing-data methods are important to interpreting a complex clinical trial.

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.
• Rate comparisons use a Poisson approximation unless the sponsor posted confidence limits; real event counts are often over-dispersed.

The record does not report the adjusted primary model's estimate, confidence interval, p-value, or full model specification. Although it describes the factors and exposure-time offset used for the primary endpoint, the posted comparative calculation is an unadjusted recalculation from summary statistics. Readers cannot use the registry record alone to determine how the adjusted primary result compares with that recalculation.

The primary outcome is defined as an on-treatment rate during the first 12 months. The record does not explain how events after treatment discontinuation were treated, how incomplete exposure or outcome information was handled, or whether sensitivity analyses assessed the on-treatment restriction. This limits assessment of the possible influence of missing information or treatment changes.

The registry does not report the original sample-size calculation, the trial's initial design assumptions, a multiplicity plan, or interim-analysis procedures. It also does not report the numerical result for the named MACE or other serious cardiovascular event secondary outcome. The serious adverse-event counts and listed event terms cannot fill that gap because they are not the same as a comparative result for that defined endpoint.

The available record does not include subgroup-specific outcome estimates or enough detail to assess whether the results vary across participant characteristics. The registry record also does not provide a detailed account of adherence or outcome ascertainment. These reporting limitations do not establish that the relevant procedures were absent; they mean that those aspects cannot be evaluated from the registry information recorded.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Evaluate the Effect of Aclidinium Bromide on Long-term Cardiovascular Safety and Exacerbations in Moderate to Very Severe COPD Patients. — NCT01966107.
• Registry record last updated 2018-12-06; status last verified 2018-11.
• Results first posted 2018-12-06.
• 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

ASCENT COPD was a completed Phase IV randomized, double-blind, placebo-controlled, parallel-group trial of aclidinium bromide in patients with moderate to very severe COPD. Enrollment was 3635. The registry records a study start date of 2013-10-16 and a primary completion date of 2017-09-21.

The primary endpoint was the rate of moderate or severe COPD exacerbations per subject per year during the first 12 months. Posted rates were 0.44 for aclidinium bromide and 0.57 for placebo. The unadjusted recalculated rate ratio was 0.772, with a 95% confidence interval from 0.663 to 0.899 and p < 0.001. The primary model's adjusted result is not reported in the registry record.

The record also lists secondary hospitalization and cardiovascular outcomes, serious adverse-event counts, and deaths. A Negative Binomial Regression result is reported for the hospitalization-rate outcome; a numerical result for the named MACE or other serious cardiovascular event outcome is not reported. Multiplicity procedures, missing-data methods, and the original sample-size rationale are not reported in the registry record.