Randomized, Placebo-Controlled, Multidose, Study Comparing Generic Budesonide/Formoterol Fumarate Dihydrate to Symbicort® in Asthmatic Participants: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Randomized, Placebo-Controlled, Multidose, Study Comparing Generic Budesonide/Formoterol Fumarate Dihydrate to Symbicort® in Asthmatic Participants (NCT02495168), a randomized phase 3 study. The primary outcome is Equivalence Analysis of Area Under the Serial FEV1-Time Effect Curve From Time 0 to 12 Hours (FEV1 Area Under Curve [AUC0-12]) on the First Day of Treatment.

2. Clinical Question

The question concerns a measured lung-function response over a defined period after dosing, rather than a long-term asthma outcome. The registry’s primary endpoint is the area under the curve (AUC) for FEV1 over the first 12 hours of Day 1. The trial also included placebo, so the posted arm summaries allow the active groups to be described relative to placebo. Those placebo comparisons are not the same statistical question as whether the two active products are equivalent to one another. Equivalence requires a direct comparison and a prespecified range of acceptable differences; the registry posts a ratio and confidence interval for the active products but does not report the equivalence margin. The record therefore supports describing the endpoint, the reported comparison, and its precision, while the margin and details of the sponsor’s decision rule are not reported in the registry record.

3. Trial Design

This was a randomized, blinded, parallel-group, placebo-controlled, multiple-dose study listed as Phase 3. The official title describes it as multicenter and multinational, and the registry lists triple masking. The record does not specify which participants, investigators, or other study personnel were masked, so the masking label should not be taken to identify particular roles.

The study enrolled 1714 participants and is marked completed. The recorded start date is 2017-01-13, and the primary completion date is 2018-05-31. The brief description states that participants first had a two-week open placebo run-in, followed by a six-week treatment period. During the run-in, participants used two inhalations twice daily through a generic placebo pMDI device. During treatment, the groups received generic budesonide/formoterol, Symbicort, or generic placebo. The arm descriptions state that treatment was given as two inhalations twice daily for up to 50 days.

Random allocation and the parallel-group design mean that participants were assigned to a treatment group and remained in that group rather than crossing between treatments. The placebo arm posted a concurrent reference for describing the endpoint response, while the active-product comparison addressed therapeutic equivalence. The primary endpoint was measured on Day 1, despite the longer treatment period. That timing matters: the registry’s primary analysis concerns an early post-dose lung-function response, not a summary of the entire treatment period.

The posted primary endpoint analysis included 437 participants in the generic group, 437 in the Symbicort group, and 99 in placebo. These are the analysis counts for this endpoint, not the overall enrollment count. The record does not report the original allocation ratio, the planned sample size for each arm, or the trial’s own sample-size justification.

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: Participants (N=1714) were provided a generic placebo pressurized metered dose inhaler (pMDI) device for use during a 2-week Run-in Period for device training. Then, qualified participants (N=1147) were randomly assigned to treatment on a 4:4:1 ratio of generic budesonide/formoterol fumarate dihydrate, Symbicort, or Placebo, respectively.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Randomized participants who received at least 1 dose of study drug, no major inclusion/exclusion violations, enrolled in the study only once, and no major protocol violations that impacted analysis of the Day 1 FEV1 AUC (D1PPS Population).

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Randomized participants who received at least 1 dose of study drug during Treatment Period (Safety Population).

6. Primary Endpoint

The registry lists the primary outcome as Equivalence Analysis of Area Under the Serial FEV1-Time Effect Curve From Time 0 to 12 Hours (FEV1 Area Under Curve [AUC0-12]) on the First Day of Treatment, measured over 0 to 12 hours on Day 1.

The primary endpoint was baseline-adjusted FEV1 AUC from time 0 to 12 hours on Day 1, reported in liter-hours (Lh). FEV1 is the amount of air a participant can forcibly exhale in the first second of a forced breath, measured by spirometry. Rather than relying on one post-dose measurement, an AUC combines serial measurements across the stated observation period into a single summary of the response over time.

The registry says the curve was calculated using the linear trapezoidal method. Values were adjusted for baseline, with the Day 1 baseline defined as the average of predose FEV1 measurements. At least two predose measurements were required for a baseline; a participant with only one or none would have a missing baseline and be excluded from analysis. At dosing time, the baseline-adjusted value was assumed to be zero. The calculation used available post-dose assessments, including unscheduled measurements if any, and their actual elapsed times.

As a general statistical concept, an AUC can capture both the size and persistence of a measured response over a defined interval, whereas a single time point captures only one moment. The endpoint is useful for comparing the overall first-day response profile, but it does not by itself describe later responses, symptoms, exacerbations, or longer-term outcomes. The registry record does not report a clinical threshold for interpreting a particular AUC difference.

7. Results Posted in the Registry

• Generic Budesonide/Formoterol Fumarate Dihydrate: mean 3.64 versus 1.46 on control; difference 2.18 (95% CI 1.46 to 2.90), standardized effect d = 0.67; z-test p = <0.001.
• Symbicort (Budesonide/Formoterol Fumarate Dihydrate): mean 3.58 versus 1.46 on control; difference 2.12 (95% CI 1.41 to 2.84), standardized effect d = 0.70; z-test p = <0.001.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary analysis is an equivalence analysis for the generic product compared with Symbicort. The registry reports a test/reference least-squares mean ratio of 101.9 and a 90% confidence interval from 92.7 to 111.9. The method used to obtain that ratio, including model details and any covariate adjustments, is not reported in the registry record. The equivalence margin is also not reported, so the interval cannot be checked against the sponsor’s acceptance limits from the registry information alone.

What an equivalence analysis asks

As a general statistical concept, an equivalence analysis asks whether the difference between treatments is sufficiently small to lie within a prespecified range considered acceptable for the question being studied. It is not simply a test that fails to find a statistically significant difference. The range has to be defined in advance, and the confidence interval for the treatment comparison is assessed against that range. The registry’s title and reported analysis identify an equivalence question, but its numerical margin and the detailed decision procedure are not reported in the registry record. Without those details, the reported ratio and interval should be presented directly rather than converted into a definitive equivalence claim.

What the mean differences describe

The additional calculations compare each active arm’s posted mean with the placebo mean. The generic-versus-placebo estimate is a mean difference of 2.177 Lh, with a 95% confidence interval from 1.456 to 2.898 and p < 0.001. The Symbicort-versus-placebo estimate is 2.124 Lh, with a 95% confidence interval from 1.413 to 2.835 and p < 0.001. These are unadjusted recalculations from the posted summary statistics. They use the reported means, standard deviations, and group sizes; they are not substitutes for the registry’s sponsor-reported equivalence analysis.

As a general concept, a mean difference expresses the estimated separation of two group averages in the endpoint’s original units. A confidence interval conveys the range of values compatible with the estimate under the calculation’s assumptions. A p-value describes how inconsistent the observed data are with a specified null hypothesis under a statistical model; it is not the probability that a treatment works, nor does it measure the size or importance of a difference. Here the recalculated p-values are unadjusted and concern active-versus-placebo contrasts, not equivalence between the active products.

Why variability matters

The registry reports standard deviations for the endpoint: 3.253 in the generic group, 2.991 in the Symbicort group, and 3.318 in placebo. Standard deviation describes how spread out individual observations are around a group mean. It is distinct from the standard error, which describes the uncertainty in an estimated mean or contrast. As a general statistical concept, greater variation among participants makes a group mean less precise when other conditions are held constant. The posted recalculations use the reported group variability and sizes; they do not model unreported participant-level details.

For continuous measurements, distributions may be more variable or less well represented by a normal approximation than a simple summary suggests. The posted record does not provide distributional plots or enough individual-level information to assess that issue independently. No further model assumptions for the sponsor’s ratio estimate are available in the registry record. The sponsor’s analysis is therefore the relevant reported result for the equivalence question, while the unadjusted mean-difference calculations provide a separate, transparent description of the arm summaries.

What the endpoint calculation involves

The endpoint is based on baseline-adjusted serial FEV1 measurements. The record specifies use of the linear trapezoidal method, which estimates the area between observed time points by treating the change between measurements as linear. The calculation uses actual elapsed time after dosing and includes available post-dose assessments, including unscheduled ones if present. At time 0, the adjusted value was assumed to be zero. Baseline was the average of the available predose FEV1 values on Day 1, provided that at least two were available.

The registry says participants without the required baseline were to be excluded from the analysis. It does not describe how missing post-dose measurements were handled, whether any imputation was used, or how missing endpoint values were treated beyond the baseline rule. Those details are important for assessing how the analysis population was formed and how robust the results may be to missing data, but they are not reported in the registry record.

Multiplicity and interpretation of tests

The registry lists four outcome measures and six analyses, but no secondary outcomes are posted in the record. The reported primary analysis is an active-product equivalence analysis; the recalculated placebo contrasts are separate unadjusted comparisons. As a general concept, when multiple outcomes or comparisons are tested, the chance of at least one apparently unusual result can increase unless the analysis plan accounts for multiplicity. The record does not report whether multiplicity adjustments or a hierarchy of tests were prespecified or used. The unadjusted p-values should therefore be read as unadjusted results, not as evidence that all possible comparisons were controlled as a single family.

The record identifies a D1PPS population for the primary endpoint, but does not give full details of the statistical analysis plan, the model used for the sponsor’s LS mean ratio, or the handling of every protocol deviation. These limits do not invalidate the posted values; they constrain how much of the analysis can be independently reconstructed from summary data.

10. Confidence Intervals and Precision

The registry-reported active-product result is a test/reference LS mean ratio of 101.9, with a 90% confidence interval from 92.7 to 111.9. The interval expresses uncertainty around the estimated ratio: values nearer its lower and upper limits are less precisely distinguished from the point estimate by the posted analysis. The confidence interval is not a guarantee that the true ratio lies within those limits, and it does not state the probability that any particular value is true.

For an equivalence question, precision is judged in relation to the acceptable equivalence range. If the confidence interval lies within that range, the analysis may support equivalence under the specified method; if it extends outside, the conclusion may differ. The numerical range and the sponsor’s decision rule are not reported in the registry record. Consequently, the interval should be reported as posted without claiming that it does or does not satisfy the trial’s criterion.

The unadjusted recalculated mean differences from placebo have 95% confidence intervals: 1.456 to 2.898 Lh for generic budesonide/formoterol and 1.413 to 2.835 Lh for Symbicort. These intervals describe precision for those separate mean-difference estimates, not for the sponsor’s ratio. They do not directly quantify the uncertainty in a generic-versus-Symbicort difference. The active group summaries are based on 437 participants each, whereas the placebo summary is based on 99; the observed analysis counts and variability contribute to the precision of the recalculated comparisons.

As a general concept, a narrower confidence interval indicates greater precision for an estimate under its model assumptions, while a wider interval indicates more uncertainty. Precision is not the same as clinical importance. The registry does not report a clinical threshold for the endpoint, and it does not provide enough detail to assess the effect of missing post-dose measurements on interval width. The sponsor’s reported interval and the recalculated placebo intervals answer distinct questions and should not be interchanged.

11. 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 relate to the unadjusted active-versus-placebo mean differences, not to the sponsor’s equivalence analysis. All entries are participants per arm, rather than total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each illustration uses the stated fraction of the observed effect as the effect to detect. The registry’s original sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under the listed assumptions, if that effect and model are correct. The 90% power column gives the corresponding planning count for a higher chance of detecting that specified effect. These are planning calculations based on the observed summary effect; they are not observed power and should not be read as a retrospective measure of whether the trial succeeded.

The rows labeled 100%, 75%, and 50% of the observed effect represent different assumed effects for planning. Smaller effects require more participants to detect with the same power and significance level, which is why the illustrative counts rise as the assumed effect becomes smaller. The illustration does not establish what sample size the trial actually planned, nor does it show that the original design used these assumptions. The registry does not report whether its design was based on these placebo contrasts, the active-product equivalence question, or another calculation. The sponsor’s own design assumptions are not reported in the registry record.

12. 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 = 2.177; pooled standard deviation σ = 3.265.
2. n = 2 × (1.96 + 0.842)² × 3.265² / 2.177² = 35.3, rounded up to 36 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 <- 2.177                      # observed difference in means
sigma <- 3.26524443276921                     # 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(2495168)
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 = 36 (80% power), 48 (90% power)
 75% of observed effect: n per arm = 63 (80% power), 85 (90% power)
 50% of observed effect: n per arm = 142 (80% power), 190 (90% power)
power.t.test: 36.3 
Simulated power at n = 36 per arm: 0.794 (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.

13. Analyses Reported by the Sponsor

The registry reports the sponsor’s active-product analysis as a test/reference LS mean ratio of 101.9, with a 90% confidence interval from 92.7 to 111.9. This result concerns generic budesonide/formoterol compared with Symbicort and is the direct posted analysis for the stated equivalence question. The registry does not report the model details, equivalence margin, or complete decision rule used for that analysis.

The recalculated results instead compare each active group’s posted mean with placebo using unadjusted mean differences. They are not an independent reconstruction of the sponsor’s ratio analysis, and they do not directly test equivalence between the active products. The record does not flag a discrepancy between the sponsor result and the recalculations. If a discrepancy were present, the sponsor’s own analysis would take precedence; no discrepancy is reported in this record. The two kinds of results should nevertheless remain distinct because they estimate different comparisons and use different reported summaries.

14. Multiplicity, Missing Data and Analysis Populations

The registry lists four outcome measures and six analyses, but reports no secondary outcomes in the record. The primary endpoint analysis is identified as an equivalence analysis. The unadjusted recalculations compare the generic product with placebo and Symbicort with placebo; they are additional contrasts and should not be mistaken for the sponsor’s primary equivalence test.

As a general statistical concept, multiplicity arises when several outcomes, time points, or treatment comparisons are evaluated. Without a planned strategy, repeated testing can increase the chance of a result that appears statistically notable by chance. Whether the sponsor used a multiplicity adjustment, a testing hierarchy, or another strategy is not reported in the registry record. The posted recalculated p-values are unadjusted, so they should be interpreted as such. The record does not provide enough information to judge whether the full analysis controlled the error rate across all analyses.

The primary endpoint population is defined as randomized participants who received at least one dose, had no major inclusion or exclusion violations, enrolled only once, and had no major protocol violations affecting the Day 1 FEV1 AUC analysis. The registry labels this the D1PPS population. For baseline construction, at least two predose FEV1 measurements were required; participants with only one or none were to have a missing baseline and be excluded. The treatment of missing post-dose measurements, other missing endpoint data, and protocol deviations beyond the stated population definition is not reported in the registry record.

The record also does not report the original statistical analysis plan or detailed model specification for the sponsor’s LS mean ratio. These omissions limit independent assessment of how the analysis population, missing observations, and multiple comparisons were handled. They do not change the reported estimates, but they leave important analysis decisions unavailable for review.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: anaemia (0.8%), uterine leiomyoma (0.3%), atrial fibrillation (0.2%), non-cardiac chest pain (0.2%), upper respiratory tract infection (0.2%).

The safety summaries list participants at risk and participants affected by serious adverse events (SAEs), other adverse events, and deaths. In the generic group, 501 participants were at risk for the SAE summary and 3 were affected; 70 were affected by other adverse events, and 0 deaths were reported. In the Symbicort group, 514 were at risk, 2 were affected by SAEs, 79 by other adverse events, and 0 deaths were reported. In placebo, 126 were at risk, 1 was affected by an SAE, 15 by other adverse events, and 0 deaths were reported.

These are counts from the registry safety summaries, not the primary endpoint analysis counts. The registry lists serious adverse event terms including anaemia (0.8%), uterine leiomyoma (0.3%), atrial fibrillation (0.2%), non-cardiac chest pain (0.2%), upper respiratory tract infection (0.2%), and hypertensive crisis (0.2%). The record does not provide an arm-specific breakdown for those listed terms in the registry record. Counts alone do not establish whether an event was caused by a treatment, and differences across groups should be interpreted in light of the group sizes and the limited event counts. These safety figures do not determine the first-day FEV1 AUC comparison.

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

The results describe a randomized comparison of generic budesonide/formoterol, Symbicort, and placebo for a first-day lung-function endpoint. In the primary endpoint analysis, the generic and Symbicort groups had reported mean FEV1 AUC values of 3.637 Lh and 3.584 Lh. The registry’s own active-product estimate was a test/reference LS mean ratio of 101.9, with a 90% confidence interval from 92.7 to 111.9. Those are the posted findings for the equivalence question.

The record does not report the equivalence margin or the sponsor’s detailed decision rule. The ratio and interval therefore cannot, by themselves, show whether the trial met its formal equivalence criterion. The recalculated active-versus-placebo mean differences are separate analyses. Their estimates and p-values describe the observed summaries under the stated recalculation; they do not establish equivalence between the active products and do not demonstrate clinical importance.

As a general principle, a statistically significant result is not automatically large enough to matter to patients, and a result near equality is not proof of equivalence unless an appropriate equivalence design and margin support that conclusion. The registry does not state a clinical threshold for the AUC endpoint. It also does not establish how the first-day measurement relates to symptoms, exacerbations, or outcomes over longer treatment.

The study’s findings are limited to the enrolled asthma population, the specified treatment regimens, the analysis population, and the endpoint and time window described. They should not be generalized to unstudied populations, other doses, other devices, or other outcomes based on this record alone. The safety summaries provide event counts but do not establish causation. The record supports a careful description of the posted analyses and their uncertainty, not medical advice or a broad claim about treatment effects.

17. Why This Trial Matters Statistically

This trial illustrates why the statistical question must be distinguished from the endpoint summaries. The study title and sponsor analysis concern therapeutic equivalence between two active products, while the posted arm means and simple recalculations also allow comparisons with placebo. A placebo contrast can show how each active group’s mean differs from placebo in the analysed data, but it cannot substitute for a direct equivalence analysis between active treatments.

Equivalence depends on both the estimate and a prespecified acceptable range. The registry reports the active-product ratio and its 90% confidence interval, but not the margin or decision rule. That missing information is consequential: a ratio centered near 100 is not sufficient, on its own, to judge whether the confidence interval falls within the trial’s acceptable limits. This is a practical example of why a registry estimate should be interpreted alongside the design assumptions that give it meaning.

The endpoint also demonstrates the trade-off involved in summarizing repeated measurements. An AUC combines serial FEV1 observations across a defined period, which can represent the response profile more fully than a single time point. At the same time, it depends on baseline definition, observation timing, and the availability of measurements. The registry provides important calculation details but not the handling of missing post-dose values or all model specifications.

Finally, the record distinguishes analysis counts from overall enrollment and safety counts from endpoint counts. Keeping those populations separate, and treating unadjusted recalculations as distinct from the sponsor’s model-based result, helps prevent overinterpretation. The trial is statistically informative as an example of how estimands, equivalence criteria, confidence intervals, and missing analysis details shape the conclusions that can responsibly be drawn from posted results.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several trial-specific details needed to fully assess the primary result are not reported in the registry record. These include the numerical equivalence margin, the sponsor’s complete decision rule, the model used to estimate the LS mean ratio, and any covariates or adjustments included. The confidence interval can be described, but its relationship to the formal equivalence criterion cannot be independently checked without the margin.

The registry gives a detailed baseline rule and describes the trapezoidal AUC calculation, but it does not explain how missing post-dose measurements were handled or whether imputation was used. It also does not provide participant-level data or distributional information with which to assess the endpoint assumptions. The D1PPS population definition is posted, but the record does not provide a full account of exclusions and protocol deviations by arm.

The trial enrolled 1714 participants overall, while the primary endpoint summaries include 437 participants in each active group and 99 in placebo. The reasons for the difference between overall enrollment and the endpoint analysis counts, including group-specific exclusions or missingness, are not reported in the registry record. The safety summaries have different at-risk counts and should not be conflated with the primary analysis population.

The registry lists four outcome measures and six analyses but does not post secondary outcomes or describe multiplicity procedures. The original sample-size justification and design assumptions are also not reported. The planning illustrations are based on the observed mean differences and stated assumptions; they do not reconstruct the trial’s original design. Finally, the endpoint is measured on Day 1 and does not represent longer-term asthma outcomes. These limitations constrain independent verification and the scope of interpretation, without changing the values reported in the registry.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Randomized, Placebo-Controlled, Multidose, Study Comparing Generic Budesonide/Formoterol Fumarate Dihydrate to Symbicort® in Asthmatic Participants — NCT02495168.
• Registry record last updated 2019-11-29; status last verified 2019-11.
• Results first posted 2019-11-29.
• 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

NCT02495168 is a completed Phase 3 randomized, blinded, parallel-group, placebo-controlled study in asthma. It enrolled 1714 participants and compared generic budesonide/formoterol with Symbicort and placebo following a two-week open placebo run-in. The treatment period was six weeks, with the arm descriptions stating dosing for up to 50 days.

The primary endpoint was baseline-adjusted FEV1 AUC from time 0 to 12 hours on Day 1. The sponsor’s reported active-product analysis gave a test/reference LS mean ratio of 101.9, with a 90% confidence interval from 92.7 to 111.9. The equivalence margin is not reported in the registry record. Unadjusted recalculations compare each active group with placebo; they are separate from the sponsor’s equivalence analysis. The registry also reports adverse-event counts and no deaths in the listed groups. Missing-data methods, multiplicity procedures, and the original sample-size justification are not reported in the registry record.