Therapeutic Equivalence of Two Formulations of Fluticasone Propionate and Salmeterol Inhalation Powder in Subjects With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Therapeutic Equivalence of Two Formulations of Fluticasone Propionate and Salmeterol Inhalation Powder in Subjects With Asthma (NCT03756883), a randomized phase 3 study. The primary outcome is Baseline-adjusted Area Under the Serial FEV1-time Curve Calculated From Time Zero to 12 Hours (AUC0-12h) on Day 1 of Treatment.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, parallel-design, multiple-center Phase 3 clinical study in subjects with asthma. Its registered title describes multiple doses and a placebo-controlled design. The registry record lists an enrollment of 999 and identifies Actavis Inc. as sponsor. The study is marked completed; its recorded start date is 2018-12-03 and its primary completion date is 2019-10-26.

Three arms are described: Test, Reference, and Placebo. The Test treatment was Fluticasone Propionate and Salmeterol Inhalation Powder, 100 mcg/50 mcg. The Reference was ADVAIR DISKUS® 100/50 (fluticasone propionate and salmeterol) Inhalation Powder, and the third arm received placebo. The active-treatment comparison for the primary endpoint included only Test and Reference. The placebo arm was used in superiority analysis only, according to the endpoint description.

The primary endpoint was a continuous measure: baseline-adjusted area under the serial FEV1-time curve from time zero to 12 hours on Day 1 of treatment, expressed in liters x hours. The primary analysis population is described as the Per-Protocol Population that completed the serial assessments on Day 1. The posted primary endpoint counts are 451 for Test and 379 for Reference. These counts refer to the endpoint analysis and do not account for all participants enrolled in the study.

The registry record does not report the allocation ratio, the precise masking procedures, the number of sites, or the dose schedule beyond the multiple-dose description. It also does not report the original sample-size justification or the detailed protocol for the trial's statistical design. Those details cannot be inferred from the fact that the study was randomized, masked, parallel-group, and placebo-controlled.

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: The protocol included a minimum 14-day washout of all pre-study medication prior to assignment in the randomized treatment phase of the study.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Per-Protocol Population that completed the serial assessments on Day 1 of 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: Safety Population

6. Primary Endpoint

The registry lists the primary outcome as Baseline-adjusted Area Under the Serial FEV1-time Curve Calculated From Time Zero to 12 Hours (AUC0-12h) on Day 1 of Treatment, measured over 12 hours.

The primary endpoint measures the cumulative FEV1 response over the first 12 hours after treatment on Day 1. FEV1 is the volume of air forcibly exhaled in the first second of a forced expiratory maneuver. Serial measurements are combined as the area under the FEV1-time curve, or AUC, from time zero to 12 hours. The result is expressed in liters x hours. The endpoint is adjusted for baseline, so the analysis accounts for the starting FEV1 measurement as described in the registry record.

In general, an area-under-the-curve measure captures both the magnitude and persistence of a response across a stated time interval. It can therefore represent the overall pattern of serial measurements rather than a single time point. The primary outcome is reported as a least-squares mean, a model-based estimate described in the registry record as the basis for statistical analysis. The registry record does not identify the model specification or covariates used to produce those estimates.

The primary endpoint compares the two active treatments only. Placebo was used in superiority analysis, not in this primary active-treatment comparison. The analysis population was the Per-Protocol Population that completed the serial Day 1 assessments. The registry record does not report whether any additional endpoint-specific rules were used to determine inclusion in that population.

7. Results Posted in the Registry

• Test: mean 4.03 versus 3.96 on control; difference 0.07 (95% CI -0.42 to 0.56), standardized effect d = 0.02; z-test p = 0.777.

8. Statistical Interpretation

9. Statistical Methods Explained

What does the primary summary estimate?

The primary outcome is continuous: it records a quantity that can take values across a numerical scale. For this endpoint, the registry reports least-squares means for the Test and Reference arms. In general, a least-squares mean is a model-based estimate of an arm's mean, often adjusted for features included in the statistical model. The registry record says that least-squares means were used but does not report the model, the included covariates, or the estimation details. It is therefore not possible to reconstruct the sponsor's model from the posted description alone.

The arm estimates are 4.03 liters x hours for Test and 3.96 liters x hours for Reference. The sponsor's reported comparison is a Test-to-Reference ratio rather than a difference between means. It is reported as 101.80, with a 90% confidence interval from 92.68 to 111.94. A ratio expresses the Test estimate relative to the Reference estimate on a ratio scale. A difference instead expresses how far apart the estimates are in the endpoint's own units. These are distinct ways of expressing a treatment comparison.

What is the unadjusted re-calculation?

The simple re-calculation uses the posted arm summaries to estimate an unadjusted difference in means. It gives a Test-minus-Reference difference of 0.07 liters x hours and an unadjusted p-value of 0.777. The posted standard errors are 0.17 for Test and 0.18 for Reference. The re-calculation uses an approximate pooled standard deviation derived from those standard errors and the arm counts. This is a summary-statistic approximation, not a reproduction of the sponsor's model-based analysis.

In general, a standard error describes the estimated sampling variability of an estimate: smaller standard errors imply greater precision, all else being equal. A p-value measures how incompatible the observed data are with a specified null hypothesis under the test's assumptions. The unadjusted p-value of 0.777 is not the probability that the treatments are equivalent, and it does not establish equivalence. It also does not replace the sponsor's reported ratio analysis.

The re-calculated interval for the mean difference extends to both sides of zero. In general, an interval that includes zero is compatible with no difference under the interval's assumptions, but it can also include nonzero differences. The registry record does not state the confidence level for this re-calculated interval, so no confidence level should be attributed to it from the posted summaries. Its construction is approximate and unadjusted.

How does equivalence differ from a difference test?

In general, a conventional test of a difference asks whether the data provide evidence against a null hypothesis of no difference. Failure to reject that null hypothesis does not demonstrate that two treatments are sufficiently similar. Equivalence analysis instead asks whether the estimated treatment contrast is precise enough to exclude differences beyond a prespecified acceptable range. That requires a margin or margins defining acceptable differences and a suitable analysis plan.

The sponsor analysis is labelled EQUIVALENCE and reports a Test-to-Reference ratio with a 90% confidence interval. The equivalence margins are not reported in the registry record, and the analysis method field is not specified. As a result, a reader can identify the sponsor's estimate and its reported interval but cannot independently determine from the registry record whether the interval met the prespecified equivalence boundary. The registry record does not provide a p-value for that reported analysis.

Why can variability and over-dispersion matter?

General statistical context: the precision of a continuous-outcome comparison depends on the variability of the measurements, the amount of information in each arm, and the analysis model. When outcome variability is greater than a model assumes, standard errors can be too small if the model does not account for that extra variability. This is often called over-dispersion in settings where a model expects less variability than the data exhibit. It can lead to intervals that are too narrow and tests that appear more conclusive than warranted. The registry record does not report a finding of over-dispersion for this study, so this is a general explanation rather than a claim about the trial.

What does the analysis population imply?

The primary endpoint description specifies a Per-Protocol Population that completed serial assessments on Day 1. In general, a per-protocol analysis focuses on participants who meet specified protocol requirements, but the exact requirements vary by study. Here, the registry record identifies completion of the serial assessments as part of the population description but does not give full eligibility or exclusion rules. The outcome counts are 451 for Test and 379 for Reference. The registry record does not report the number of participants with missing individual measurements or how any missing observations were handled.

Analysis-population choice affects the question answered and the participants represented in an estimate. A per-protocol analysis is not automatically interchangeable with an analysis of all randomized participants. For an equivalence question, population definitions and missing-data handling can be especially important because exclusions or incomplete measurements can affect the estimated similarity between treatments. The registry record does not report whether other analysis populations were used for the sponsor's primary comparison.

What can be inferred from the posted multiplicity information?

The registry record lists four outcome measures and six analyses, while no secondary outcome results are posted. It does not report a multiplicity adjustment, a hierarchy for testing outcomes, or a detailed statistical analysis plan. In general, testing multiple outcomes or contrasts can increase the chance of at least one result appearing unusual by chance if no adjustment or prespecified strategy is used. That general concern cannot be resolved for this study from the posted information. It would be inappropriate to assume either that an adjustment was applied or that it was not applied.

10. Confidence Intervals and Precision

Precision is about how narrowly an estimate is determined by the data under the assumptions of its analysis. A confidence interval communicates this uncertainty by giving a range of values compatible with the estimate and statistical procedure. It is not a range containing a fixed proportion of individual participants' outcomes, and it is not a guarantee that the true value lies within the interval.

The sponsor-reported Test-to-Reference ratio is 101.80, with a 90% confidence interval from 92.68 to 111.94. The estimate is close to 100 on the ratio scale, while the interval includes values on both sides of 100. The width of the interval matters: the point estimate alone does not convey how uncertain the comparison is. Whether this interval is sufficiently narrow for an equivalence conclusion depends on the prespecified margins, which are not reported in the registry record.

The unadjusted re-calculation gives a mean difference of 0.07 liters x hours. Its approximate interval extends both below and above zero. This illustrates that the posted summaries allow uncertainty in either direction around the estimated difference. The registry record does not state the confidence level for the re-calculated interval; it should not be read as the sponsor's interval or as a replacement for the reported equivalence analysis.

Precision also depends on the analysis population and assumptions. The primary analysis included 451 Test participants and 379 Reference participants who were in the stated per-protocol population. The sponsor's model details and handling of incomplete measurements are not reported in the registry record. These omissions limit independent assessment of how the reported uncertainty was estimated.

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 planning figures are illustrations based on the observed effect, not a report of the trial's original sample-size design. They assume 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. The figures are participants per arm, not total participants across arms and not total events.

For planning at 100% of the observed effect, the figures are 40,653 participants per arm for 80% power and 54,423 participants per arm for 90% power. At 75% of the observed effect, they are 72,272 participants per arm for 80% power and 96,751 participants per arm for 90% power. At 50% of the observed effect, they are 162,611 participants per arm for 80% power and 217,689 participants per arm for 90% power.

In general, the 80% power column describes a planning scenario in which a study of the stated size would have an 80% chance of detecting the chosen effect under the calculation's assumptions. The 90% column uses a higher target chance of detection, which requires more participants under the same assumptions. A smaller effect is harder to distinguish from random variation, so planning for smaller effects requires more participants. The listed figures rise as the assumed fraction of the observed effect becomes smaller.

These planning calculations are not observed power and are not evidence about the trial's original design. The registry record does not report the trial's original sample-size justification or its design assumptions. The planning values depend on the observed effect and the stated simplifying assumptions; they should not be treated as a recommendation or as a substitute for a prospective design calculation tailored to a future study.

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 = 0.070; pooled standard deviation σ = 3.562.
2. n = 2 × (1.96 + 0.842)² × 3.562² / 0.070² = 40,652.5, rounded up to 40,653 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 0.0700000000000003                      # observed difference in means
sigma <- 3.56223885389146                     # 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(3756883)
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 = 40,653 (80% power), 54,423 (90% power)
 75% of observed effect: n per arm = 72,272 (80% power), 96,751 (90% power)
 50% of observed effect: n per arm = 162,611 (80% power), 217,689 (90% power)
power.t.test: 40653.5 
Simulated power at n = 40,653 per arm: 0.801 (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 sponsor's posted analysis reports a Test-to-Reference ratio of 101.80 and a 90% confidence interval from 92.68 to 111.94. The analysis is labelled as an equivalence analysis. The registry record does not report a p-value or specify the statistical method for that result. It also does not report the equivalence margins needed to assess the interval against a decision rule.

The simple re-calculation from the posted arm summaries instead estimates an unadjusted difference of 0.07 liters x hours, with an unadjusted p-value of 0.777. This re-calculation uses the arm means and standard errors and is approximate. It does not reproduce the sponsor's ratio analysis or its model-based least-squares mean comparison. A ratio and a difference express the contrast on different scales, and the re-calculation does not supply the missing equivalence margin.

The registry record does not flag a discrepancy between the posted result and the re-calculation. The sponsor's reported analysis remains the relevant result for understanding the sponsor's equivalence assessment; the re-calculation is a separate, unadjusted check based on posted summaries. Because the equivalence boundary and analysis details are not reported, the ratio and interval can be described but cannot independently establish whether the sponsor's criterion was met.

14. Multiplicity, Missing Data and Analysis Populations

The registry record lists four outcome measures and six analyses. It does not report a detailed statistical analysis plan, the order in which outcomes or comparisons were tested, or whether any multiplicity adjustment was used. No secondary outcome results are posted. Without those details, the role of the other registered outcomes and analyses in the overall inferential plan cannot be established.

In general, multiplicity arises when several outcomes, time points, treatment contrasts, or analyses are considered. If each is assessed separately without an appropriate strategy, the chance of at least one apparently notable result can increase. Different strategies can address this issue, including prespecified testing sequences or adjustments, but the registry record does not identify one for this study. No conclusion about the presence or absence of multiplicity control should be inferred.

The primary population is described as the Per-Protocol Population that completed serial assessments on Day 1. The posted endpoint counts are 451 in Test and 379 in Reference. The registry record does not report the full per-protocol criteria, the number excluded from this analysis, or whether the primary result was also calculated in another analysis population. It does not report how missing FEV1 measurements were handled, whether incomplete serial measurements led to exclusion, or whether any imputation procedure was used.

These omissions matter because analysis populations and missing-data procedures can affect an estimate and its uncertainty. In general, an analysis restricted to participants with complete measurements may differ from an analysis that includes all randomized participants, especially when missingness is related to outcomes or treatment. That is a general methodological consideration, not a claim about why any study measurements may be absent. The registry record does not report the reasons for missing measurements or enough detail to assess their potential effect.

The registry record also does not report interim analyses, stopping rules, or a full statistical analysis plan. Those design and analysis details should not be guessed from the study's completed status, its listed number of analyses, or the posted primary result.

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: ischaemic stroke (0.2%), small intestinal obstruction (0.2%).

The safety figures are reported for the Test, Reference, and Placebo groups. For serious adverse events, the at-risk counts are 485, 413, and 101, respectively. The corresponding numbers affected are 0 in Test, 2 in Reference, and 0 in Placebo. No deaths are reported in any of the three groups. For other adverse events, the at-risk counts are 485, 413, and 101, and the numbers affected are 3, 1, and 5, respectively.

The registry record also lists Ischaemic Stroke and Small Intestinal Obstruction among the top serious terms, each with a reported value of 0.2%. The posted summary does not assign those terms to a specific arm, so they should not be attributed to one. The figures are counts of affected participants as reported, not a complete account of event timing, duration, severity, or relationship to treatment.

In general, adverse-event counts describe events observed and reported during the study; they do not by themselves establish cause or compare risk precisely. The registry record does not provide detailed event definitions, follow-up duration for safety, or an inferential comparison of adverse-event rates. The small number of serious events also means these figures should be read as descriptive safety information rather than as a precise estimate of comparative safety.

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

The primary outcome concerns a specific comparison: the baseline-adjusted area under serial FEV1 measurements from time zero to 12 hours on Day 1, among participants in the stated per-protocol population who completed the serial assessments. The Test and Reference least-squares means were 4.03 and 3.96 liters x hours. The sponsor-reported Test-to-Reference ratio was 101.80, with a 90% confidence interval from 92.68 to 111.94. The unadjusted re-calculation gives a difference of 0.07 liters x hours and a p-value of 0.777.

These are statistical estimates, not proof that the treatments are identical. Equivalence requires a prespecified margin and an analysis that demonstrates adequate precision relative to that margin. The registry record does not report the equivalence margins or the detailed method. Therefore, the posted ratio and interval do not allow independent verification of whether the equivalence criterion was met. A non-significant unadjusted difference test is not a substitute for an equivalence assessment.

The result is also confined to the Day 1 endpoint and its specified analysis population. It does not establish what the comparison would be for other outcome measures, other time periods, or participants outside that population. No secondary outcome results are posted in the registry record, and missing-data handling and analysis-population details are not fully reported.

The safety figures are descriptive: serious adverse events affected 0 Test participants, 2 Reference participants, and 0 Placebo participants; deaths were 0 in each group. Those counts alone do not establish a comparative safety profile, particularly without detailed event information and a formal safety analysis.

In general, interpreting a trial result requires attention to the estimate, its uncertainty, the design and analysis population, and the prespecified question. The registry record supports describing the reported primary comparison and its uncertainty, but the missing equivalence margins and analysis details limit what can be concluded about the formal equivalence decision.

17. Why This Trial Matters Statistically

This study is statistically notable because its primary question is therapeutic equivalence, which is not the same as asking whether two treatments differ. A small observed difference or a large p-value from a conventional difference test does not, on its own, demonstrate that treatments are sufficiently similar. Equivalence requires an acceptable range to be specified in advance and uncertainty narrow enough to remain within that range.

The registry record reports a Test-to-Reference ratio of 101.80 and a 90% confidence interval from 92.68 to 111.94, but does not report the equivalence margins. That combination illustrates why estimates cannot be interpreted in isolation: a point estimate near 100 is not enough to determine whether an equivalence criterion was met. The unadjusted re-calculation provides a separate contrast in liters x hours, but it is not a substitute for the sponsor's ratio analysis.

The trial also illustrates the importance of identifying the analysis population and endpoint precisely. The primary measure combines serial FEV1 observations over 12 hours on Day 1, and the primary analysis was restricted to a per-protocol population that completed those assessments. The posted endpoint counts differ from the overall enrollment count, so the population behind an estimate must be distinguished from the full trial enrollment.

Finally, registry transparency affects independent interpretation. The record does not describe the equivalence boundaries, full model specification, missing-data approach, or multiplicity strategy. Those omissions do not erase the reported estimates, but they limit independent assessment of the analysis and the strength of conclusions that can be drawn from it.

18. Limitations

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

The registry record does not report the equivalence margins. This is a central limitation for interpreting an analysis labelled EQUIVALENCE, because the reported 90% confidence interval cannot be assessed against a stated boundary. The statistical method for the sponsor's ratio analysis is also not specified, and no p-value is posted for that analysis.

The primary outcome description says least-squares means were used, but the model, covariates, and other estimation details are not reported. The re-calculated difference is an approximate, unadjusted analysis based on posted summary statistics; it should not be taken as a reconstruction of the sponsor's model. The registry record does not state the confidence level for that re-calculated interval.

The primary analysis is defined for the Per-Protocol Population that completed serial Day 1 assessments. Full rules for inclusion in that population, the number excluded, and the handling of incomplete measurements are not reported. The registry record also does not report whether the primary comparison was repeated in another analysis population.

Although four outcome measures and six analyses are listed, no secondary outcome results are posted. The record does not describe a multiplicity strategy, interim analyses, or the original sample-size justification. It also does not report the full safety follow-up details or a formal comparative safety analysis. These limits mean the posted results address a specific primary endpoint and do not provide a complete view of every planned analysis or outcome.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Therapeutic Equivalence of Two Formulations of Fluticasone Propionate and Salmeterol Inhalation Powder in Subjects With Asthma — NCT03756883.
• Registry record last updated 2021-09-24; status last verified 2021-08.
• Results first posted 2021-09-24.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

The registry record describes a completed, randomized, quadruple-masked, parallel-design, multiple-center Phase 3 study in subjects with asthma. It lists an enrollment of 999 and three arms: Test fluticasone propionate and salmeterol inhalation powder, Reference ADVAIR DISKUS® 100/50, and Placebo. The primary endpoint was baseline-adjusted area under the serial FEV1-time curve from time zero to 12 hours on Day 1, reported in liters x hours.

The primary analysis used a per-protocol population that completed serial assessments. The sponsor-reported Test-to-Reference ratio was 101.80, with a 90% confidence interval from 92.68 to 111.94. The registry record does not report the equivalence margins or enough analysis detail to verify the equivalence decision independently. Serious adverse events affected 0 Test participants, 2 Reference participants, and 0 Placebo participants; no deaths were reported. No secondary outcome results are posted.