Study of Fluticasone Propionate MDPI Compared With Fluticasone/Salmeterol MDPI in Adolescent and Adult Patients With Persistent Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of Fluticasone Propionate MDPI Compared With Fluticasone/Salmeterol MDPI in Adolescent and Adult Patients With Persistent Asthma (NCT02139644), a randomized phase 3 study. The primary outcome is Standardized Baseline-Adjusted Forced Expiratory Volume in 1 Second (FEV1) Area Under the Effect Curve From Time Zero to 12 Hours Postdose (FEV1 AUEC0-12h) at Week 12.

2. Clinical Question

The trial was designed to evaluate efficacy and safety over 12 weeks in people with persistent asthma who were symptomatic despite prior inhaled corticosteroid therapy. Its primary endpoint summarized serial spirometry after dosing, rather than relying on a single postdose measurement. This allows the analysis to represent lung-function response across the observation period specified for the endpoint.

The comparison includes two combination-inhaler doses, two fluticasone-alone doses, and placebo. This arrangement makes it possible to examine the reported combination-versus-placebo and fluticasone-alone-versus-placebo results, as well as the sponsor-reported comparisons between matched-dose combination and fluticasone-alone arms. The results on this page describe the posted endpoint estimates and analyses; they do not establish how the trial’s complete protocol defined every planned comparison.

3. Trial Design

This was a Phase 3, randomized, triple-masked, parallel-group study. The registry record lists total enrollment as 787 and describes a 12-week treatment period. Participants had persistent asthma and were aged 12 years and older; the study description specifies symptoms despite low-dose or mid-dose inhaled corticosteroid therapy.

There were five arms: FS MDPI 100 / 12.5 mcg, FS MDPI 50 / 12.5 mcg, Fp MDPI 100 mcg, Fp MDPI 50 mcg, and placebo MDPI. The active study inhalers were taken twice daily. The two combination arms included fluticasone propionate and salmeterol, while the monotherapy arms contained fluticasone propionate. Participants performed spirometry at each visit, kept a diary between visits, and could receive albuterol/salbutamol rescue medication as determined by investigational center personnel.

The primary analysis population was not the full enrolled group. It was a subset of participants who performed postdose serial spirometry at baseline and Week 12. The reported arm sizes for this endpoint were 61 for FS MDPI 100 / 12.5 mcg, 56 for FS MDPI 50 / 12.5 mcg, 72 for Fp MDPI 100 mcg, 63 for Fp MDPI 50 mcg, and 60 for placebo MDPI. A subset of approximately 300 participants was described for the serial-spirometry endpoint.

The registry record lists study completion, but the original design’s sample-size justification, planned interim analyses, and full statistical analysis plan are not reported in the registry record. The posted planning illustrations elsewhere on this page are recalculations from observed results, not a reconstruction of the trial’s original design.

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: Patients were randomized 1:1:1:1:1 to one of the five treatment arms during the Treatment Period.

Run-In Period (Pre-assignment)

Reasons for not completing this period:

Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set: a subset of patients who performed postdose serial spirometry at the baseline visit and week 12

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: Intent to treat population

6. Primary Endpoint

The registry lists the primary outcome as Standardized Baseline-Adjusted Forced Expiratory Volume in 1 Second (FEV1) Area Under the Effect Curve From Time Zero to 12 Hours Postdose (FEV1 AUEC0-12h) at Week 12, measured over Day 1 (predose, baseline), Week 12 and was performed at the following times relative to the administration of study drug (±5 minutes): 15 and 30 minutes and 1, 2, 3, 4, 6, 8, 10, and 12 hours.

The primary endpoint was baseline-adjusted FEV1 area under the effect curve from time zero to 12 hours after dosing at Week 12, standardized by the number of hours between dose administration and the last nonmissing FEV1 measurement. FEV1 measures the volume of air exhaled during the first second of a forced breath. In this endpoint, repeated FEV1 measurements after dosing are combined to summarize the response over the specified interval.

Measurements were scheduled at 15 and 30 minutes and 1, 2, 3, 4, 6, 8, 10, and 12 hours after dosing. The registry description says the area under the curve was calculated with the trapezoidal rule using actual measurement times. Baseline was the average of the two predose FEV1 measurements, taken 30 and 10 minutes before dosing; if one was missing, the other was used, and if both were missing, baseline was treated as missing. Baseline-adjusted FEV1 was postdose FEV1 minus baseline FEV1.

Using an area across repeated measurements can describe the pattern over the observation interval more fully than a single measurement at one time. Standardization expresses that area relative to the observed dosing-to-measurement interval. The result is an average response measure in liters, reported as a least-squares mean with a standard error. The endpoint population was the subset with serial spirometry at both baseline and Week 12, so its estimates do not represent every enrolled participant.

7. Results Posted in the Registry

• FS MDPI 100 / 12.5 mcg: mean 0.41 versus 0.07 on control; difference 0.33 (95% CI 0.20 to 0.47), standardized effect d = 0.90; z-test p = <0.001.
• FS MDPI 50 / 12.5 mcg: mean 0.40 versus 0.07 on control; difference 0.33 (95% CI 0.19 to 0.46), standardized effect d = 0.88; z-test p = <0.001.
• Fp MDPI 100 mcg: mean 0.25 versus 0.07 on control; difference 0.18 (95% CI 0.05 to 0.31), standardized effect d = 0.48; z-test p = 0.006.
• Fp MDPI 50 mcg: mean 0.27 versus 0.07 on control; difference 0.19 (95% CI 0.06 to 0.32), standardized effect d = 0.52; z-test p = 0.004.

8. Secondary Efficacy Endpoints

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

Change From Baseline in the Weekly Average of the Daily Morning Trough Peak Expiratory Flow (PEF) Over the 12 Week Treatment

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • FS MDPI 100 / 12.5 mcg: mean 24.41 versus 3.59 on control; difference 20.82 (95% CI 12.09 to 29.56), standardized effect d = 0.59; z-test p = <0.001.
  • FS MDPI 50 / 12.5 mcg: mean 24.86 versus 3.59 on control; difference 21.27 (95% CI 12.59 to 29.96), standardized effect d = 0.60; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FS MDPI 100 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FS MDPI 50 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Weekly Average of the Total Daily Asthma Symptom Score Over the 12-Week Treatment Period

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • FS MDPI 100 / 12.5 mcg: mean -0.36 versus -0.14 on control; difference -0.23 (95% CI -0.32 to -0.14), standardized effect d = -0.64; z-test p = <0.001.
  • FS MDPI 50 / 12.5 mcg: mean -0.33 versus -0.14 on control; difference -0.19 (95% CI -0.28 to -0.11), standardized effect d = -0.54; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FS MDPI 100 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FS MDPI 50 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Weekly Average of the Total Daily (24-hour) Use of Albuterol/Salbutamol Inhalation Aerosol Over the 12-Week Treatment Period

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • FS MDPI 100 / 12.5 mcg: mean -0.68 versus -0.00 on control; difference -0.67 (95% CI -0.93 to -0.41), standardized effect d = -0.64; z-test p = <0.001.
  • FS MDPI 50 / 12.5 mcg: mean -0.71 versus -0.00 on control; difference -0.70 (95% CI -0.96 to -0.44), standardized effect d = -0.66; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FS MDPI 100 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for FS MDPI 50 / 12.5 mcg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results give additional context to the primary lung-function endpoint. They include measures of morning peak expiratory flow, daily asthma symptom score, and daily rescue albuterol/salbutamol use. Across those measures, the reported arm summaries generally show greater numerical changes in the combination-inhaler arms than in placebo. The posted analyses also include mixed-model comparisons for fluticasone-alone doses versus placebo; their results are not identical across endpoints. Other listed secondary outcomes include quality of life, time-to-improvement measures, remaining in the study, and treatment-emergent adverse experiences.

These outcomes address different aspects of the study and should not be treated as interchangeable with the primary FEV1 AUEC endpoint. Their overall direction can help describe whether the broader set of measurements appears consistent with the primary pattern, but secondary measures do not independently confirm the primary analysis. The registry lists nine outcome measures and 43 analyses overall; only some secondary estimates and comparisons are detailed in the record excerpt. Results for the other listed outcomes are not reported in the registry record.

Unadjusted secondary results carry less weight when many outcomes, time points, arms, or comparisons are examined. In general, the more statistical questions asked, the greater the chance that some results appear notable by chance alone unless the analysis plan accounts for multiple testing. The registry record does not report the full multiplicity strategy, including whether particular secondary comparisons were confirmatory or exploratory. Therefore, the secondary findings are best read as descriptive supporting context rather than as a set of independent definitive tests.

The primary endpoint remains the central result. Secondary findings can broaden the account of what was measured, but should be interpreted in light of their specific models, missing observations, and multiplicity. These details are not all reported in the registry record.

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

• Change From Baseline in the Weekly Average of the Daily Morning Trough Peak Expiratory Flow (PEF) Over the 12 Week Treatment
• Change From Baseline in the Weekly Average of the Total Daily Asthma Symptom Score Over the 12-Week Treatment Period
• Change From Baseline in the Weekly Average of the Total Daily (24-hour) Use of Albuterol/Salbutamol Inhalation Aerosol Over the 12-Week Treatment Period
• Kaplan-Meier Estimate of Probability of Remaining in Study At Week 12
• Change From Baseline in the Asthma Quality of Life Questionnaire With Standardized Activities (AQLQ(S)) Score at Endpoint for Patients >=18 Years Old
• Kaplan-Meier Estimates for Time to 15% and 12% Improvement From Baseline in FEV1 Postdose on Day 1
• Patients With Treatment-Emergent Adverse Experiences (TEAE) During the Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a continuous measure, and the registry reports least-squares means and standard errors for each arm. The recalculations displayed with the results are simple, unadjusted comparisons derived from those posted summaries. The sponsor’s own analyses are reported separately. These approaches answer related but not identical statistical questions, so their estimates and uncertainty intervals need not match exactly.

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of an arm’s mean outcome. In general, such estimates can account for terms included in the fitted model, whereas a raw mean is calculated directly from observed values. The registry identifies the primary arm summaries as least-squares means, but the full model specification for this endpoint is not reported in the registry record. As a result, readers cannot reconstruct every adjustment used to obtain those posted arm estimates from the registry description alone.

The primary endpoint population was a subset with postdose serial spirometry at baseline and Week 12. This defines who contributed to the primary analysis. It is not the same as saying that all randomized participants had endpoint measurements, and the registry description does not give a complete account of how missing endpoint observations were handled in the sponsor’s analysis.

How is the primary endpoint formed?

The endpoint first adjusts postdose FEV1 measurements for baseline. It then summarizes the repeated adjusted values from time zero through 12 hours using the trapezoidal rule and actual measurement times. In general, the trapezoidal rule approximates the area under a curve by joining adjacent observed values with straight lines and adding the resulting areas. The registry says that this area was standardized by the hours from dose administration to the last nonmissing measurement. This approach uses repeated measurements rather than selecting one postdose time as the entire endpoint.

Baseline was based on the average of two predose measurements, with a rule for using one measurement when the other was missing. If both predose values were missing, baseline was missing. The registry’s endpoint description gives this baseline rule, but broader missing-data methods, such as any imputation or sensitivity analyses, are not reported in the registry record.

What is the unadjusted recalculation?

The recalculated comparisons use the posted arm means and standard errors to form simple active-versus-placebo contrasts and approximate confidence intervals and p-values. They do not reproduce the sponsor’s full analysis model. In general, a standard error describes the estimated sampling variability of a mean; it is not the same as the spread of individual participant outcomes. Because the recalculation uses summary statistics and approximations, it should be read as a secondary statistical check rather than as the trial’s primary model-based result.

In general, over-dispersion matters when a model assumes less variability than the observed data contain. It can make standard errors too small and statistical evidence appear stronger than warranted. The registry record does not report an over-dispersion assessment for this endpoint, and the primary outcome is continuous rather than a count outcome for which over-dispersion is a common modeling concern. It is therefore not appropriate to claim that the trial did or did not require a correction on this basis.

How should p-values and intervals be read?

In general, a p-value summarizes how incompatible the observed data are with a specified null hypothesis under the assumptions of the analysis. It does not measure the probability that a treatment effect is true, and a small p-value does not measure clinical importance. A confidence interval gives a range of values compatible with the data and method at its stated confidence level. Its width conveys precision: narrower intervals indicate less statistical uncertainty than wider intervals, conditional on the model and data.

The recalculated primary comparisons use approximate, unadjusted methods. The sponsor’s reported primary comparisons use ANCOVA and report least-squares mean differences with 95% confidence intervals. Where model-based and unadjusted results differ, the sponsor’s own analysis takes precedence. The registry record does not report all model details needed to independently reproduce those sponsor estimates.

What do the planning illustrations show?

The sample-size illustrations use the observed effect as a planning reference, then show hypothetical participant counts for detecting the full observed effect or a stated fraction of it. They are not the trial’s original sample-size calculation. The original design assumptions and justification are not reported in the registry record. The illustrations are planning aids, and their interpretation depends on the stated assumptions in the sample-size section.

More broadly, statistical conclusions rely on design, measurement, analysis-population, and missing-data choices. Randomization helps support fair comparisons between assigned groups, while masking can reduce certain sources of bias. Neither feature removes uncertainty from limited analysis populations, missing observations, model assumptions, or multiple testing. The registry record does not provide enough detail to resolve each of these issues fully.

11. Confidence Intervals and Precision

The recalculated primary comparisons are accompanied by confidence intervals that quantify uncertainty around the simple active-versus-placebo differences. For FS MDPI 100 / 12.5 mcg, the estimated difference was 0.334 liters, with a 95% confidence interval from 0.202 to 0.466. For FS MDPI 50 / 12.5 mcg, it was 0.325 liters, with an interval from 0.191 to 0.459. For Fp MDPI 100 mcg, it was 0.18 liters, with an interval from 0.052 to 0.308. For Fp MDPI 50 mcg, it was 0.194 liters, with an interval from 0.063 to 0.325.

Each of these intervals lies above zero, which is consistent with the positive point estimates for the active-versus-placebo contrasts in the simple recalculation. The intervals still cover a range of plausible effect sizes; they do not establish one exact value. They also do not capture every source of uncertainty, such as uncertainty from model choices or the effect of unreported missing-data procedures.

The sponsor’s ANCOVA comparisons are distinct and also report 95% confidence intervals. For the two combination-versus-matched-monotherapy comparisons, the reported differences were 0.154 liters (95% CI 0.041 to 0.267) and 0.131 liters (95% CI 0.011 to 0.250). For combination-versus-placebo comparisons, the reported differences were 0.335 liters (95% CI 0.216 to 0.453) and 0.325 liters (95% CI 0.203 to 0.447). These are model-based sponsor estimates, not the unadjusted recalculations above.

In general, confidence intervals are most informative when read together with the estimate, the analysis method, and the population analyzed. The primary endpoint estimates come from the serial-spirometry subset rather than the full enrolled group. The registry does not report enough detail to assess all reasons why endpoint data might be unavailable or how that uncertainty was addressed. Statistical precision should therefore not be confused with certainty about effects in every participant or setting.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size tables and curve are planning illustrations based on observed results, not a record of the trial’s original design calculation. For these continuous primary comparisons, the displayed values are participants per arm, not total event counts. The time-to-event convention, when such a table is used, is to report total events; that is not the quantity shown for these continuous-outcome comparisons.

The illustrations use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each row considers an effect equal to the stated fraction of the observed effect: 100%, 75%, or 50%. The original trial’s sample-size justification and design assumptions are not reported in the registry record, so these calculations should not be read as the basis on which the study was planned.

The 80% power column gives the estimated participants per arm for a hypothetical study to have an 80% chance of detecting the chosen effect under the illustration’s assumptions, if that effect is the true one. The 90% power column uses a higher target chance of detection under those same assumptions. These are planning targets, not guarantees about what a future study will find.

Smaller effects generally require more participants to detect under otherwise similar assumptions. That relationship is visible in the rows that use smaller fractions of the observed effect. The figures are not observed power: observed power is not a useful substitute for interpreting the confidence intervals and results actually posted. For planning, the effect size, outcome variability, allocation, significance threshold, and analysis design should all be considered rather than treating a single row as a definitive target.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 0.334; pooled standard deviation σ = 0.370.
2. n = 2 × (1.96 + 0.842)² × 0.370² / 0.334² = 19.3, rounded up to 20 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 <- 0.334                      # observed difference in means
sigma <- 0.370210224175445                     # 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(2139644)
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 = 20 (80% power), 26 (90% power)
 75% of observed effect: n per arm = 35 (80% power), 46 (90% power)
 50% of observed effect: n per arm = 78 (80% power), 104 (90% power)
power.t.test: 20.3 
Simulated power at n = 20 per arm: 0.798 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses for the primary outcome using ANCOVA and presenting least-squares mean differences with 95% confidence intervals. These include comparisons of FS MDPI 100 / 12.5 mcg with Fp MDPI 100 mcg, FS MDPI 50 / 12.5 mcg with Fp MDPI 50 mcg, and each combination dose with placebo. The reported p-values for those comparisons are 0.008, 0.032, < 0.001, and < 0.001, respectively. A displayed p-value of < 0.001 reflects the registry’s formatting and should not be interpreted as a probability exactly equal to zero.

The recalculated estimates on this page are simple unadjusted contrasts using posted arm summaries. The sponsor’s ANCOVA estimates are model-based; their values can differ because they arise from a different analysis approach. The registry record does not contain all details of the ANCOVA specification, so a complete independent reconstruction is not possible from the posted summaries alone.

The recalculation is useful as a transparent check on the direction and rough scale of the arm differences, but it is not a replacement for the sponsor’s analysis. In general, when an unadjusted summary-based calculation differs from the sponsor’s model-based analysis, the sponsor’s own analysis takes precedence for describing the trial’s reported inferential result. Readers should keep the methods and comparison being addressed explicit when looking across the two sets of estimates.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple treatment arms, outcome measures, and analyses. The primary endpoint has comparisons with placebo in the simple recalculation, while the sponsor also reports combination-versus-monotherapy and combination-versus-placebo ANCOVA comparisons. Several secondary outcomes are measured over time or across treatment arms. When multiple hypotheses are tested, the chance of at least one apparently unusual result can increase. In general, a multiplicity plan can define which tests are confirmatory and whether statistical thresholds are adjusted or testing is conducted in a specified sequence.

The complete multiplicity strategy is not reported in the registry record. The record therefore does not establish which secondary findings were prespecified as confirmatory, whether the primary comparisons were protected by a testing hierarchy, or how the sponsor handled the family of analyses. The reported p-values should be read as the results of the specific listed analyses, not as evidence that all comparisons were accounted for in a particular way.

For the primary outcome, the stated analysis population was a subset of participants who performed postdose serial spirometry at baseline and Week 12. The registry describes how the baseline value was formed when one predose measurement was missing, and how baseline was treated when both were missing. It does not report the complete missing-data procedure for unavailable Week 12 or postdose measurements, any imputation approach, or sensitivity analyses addressing missingness.

The stated analysis population is important because it differs from total enrollment. The registry record does not provide enough information to determine why each participant was or was not included in this subset, or to assess the consequences of missing endpoint data. The record also does not report a complete statistical analysis plan, interim-analysis plan, or the original sample-size rationale. These absences limit independent assessment of prespecification, multiplicity, and robustness; they do not, by themselves, show that a particular analysis was inappropriate.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: pancreatitis (0.8%), cholecystitis (0.8%), cholelithiasis (0.8%), plasma cell myeloma (0.8%), abortion spontaneous (0.8%).

The registry lists serious adverse events for each arm with the number at risk and the number affected. The reported counts were 1 of 126 for FS MDPI 100 / 12.5 mcg, 0 of 128 for FS MDPI 50 / 12.5 mcg, 1 of 129 for Fp MDPI 100 mcg, 0 of 129 for Fp MDPI 50 mcg, and 2 of 129 for placebo MDPI. These are counts during the registry’s adverse-event reporting period, not a comparison adjusted for differences between participants or time at risk.

The listed serious-event terms are each shown as 0.8%: pancreatitis, cholecystitis, cholelithiasis, plasma cell myeloma, abortion spontaneous, and asthma. The record does not provide an arm attribution for each term in this list, so those terms should not be assigned to particular treatment groups based on the summary alone. Death counts are not reported in the registry record.

These figures are descriptive. They do not establish whether an event was caused by study treatment, and small counts are not sufficient to characterize uncommon risks precisely. The registry also lists treatment-emergent adverse experiences as a secondary outcome, but these serious-event counts alone do not describe the full adverse-event profile.

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

The primary result describes a specific measurement: standardized, baseline-adjusted FEV1 area under the effect curve from time zero to 12 hours after dosing at Week 12. The posted arm means and recalculated active-versus-placebo differences are numerically positive for all four active arms. The sponsor’s ANCOVA results also report positive differences for the listed comparisons. This is a statistical description of the posted results, not a claim about what an individual should use or whether a treatment is appropriate.

The result does not mean that every participant experienced the arm-average response. An average can conceal variation among individuals, and the primary endpoint was analyzed in a serial-spirometry subset rather than the entire enrolled population. Nor does the endpoint describe lung function at every time beyond the measured period, all symptoms, future exacerbations, or every outcome that matters to participants. The registry lists several such domains as secondary outcomes, but the posted details are incomplete.

A confidence interval conveys uncertainty about an estimated contrast under its analysis assumptions; it does not guarantee that the true effect lies within the interval in every sense, nor does it describe all sources of uncertainty. The recalculated intervals are based on simple summary-statistic methods. The sponsor’s model-based analyses provide a different inferential account and should be distinguished from those recalculations.

Statistical evidence should also be separated from clinical importance. The registry record does not specify a threshold for a clinically important difference in this endpoint, so this page cannot determine whether a particular estimate meets such a threshold. The trial’s posted results inform the measured comparisons in this study; they do not settle questions outside its population, treatment period, endpoints, or analysis methods.

18. Why This Trial Matters Statistically

This trial illustrates several statistical features that are common in clinical research. First, the primary endpoint is based on repeated measurements summarized over time, rather than a single observation. The trapezoidal area-under-the-curve approach uses the scheduled postdose spirometry series and actual measurement times, while baseline adjustment accounts for each participant’s starting FEV1 as described in the endpoint definition.

Second, the arm summaries and sponsor-reported comparisons are not identical forms of evidence. Least-squares means and ANCOVA contrasts are model-based, while the recalculations on this page are unadjusted comparisons reconstructed from posted summaries. Keeping those estimands and methods distinct helps prevent apparent numerical differences from being mistaken for a contradiction.

Third, a five-arm design yields multiple potentially interesting comparisons, and the registry lists many secondary outcomes and analyses. That breadth makes prespecification and multiplicity handling important to interpretation. The complete strategy is not reported in the registry record, which makes it useful to distinguish the primary result from secondary evidence and exploratory-looking comparisons.

Finally, the full enrollment and primary analysis population are not the same. A subset with serial spirometry at baseline and Week 12 contributed to the primary endpoint, making clarity about the analysis population and missing-data handling important. The registry reports some endpoint-specific procedures but not the full missing-data or analysis plan. These reporting details shape how confidently readers can assess reproducibility and generalizability, even when the posted estimates are precise within the stated analysis.

19. 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 primary endpoint was analyzed in a subset who completed postdose serial spirometry at baseline and Week 12, rather than in all 787 enrolled participants. The registry describes the subset as approximately 300 participants and lists the arm-specific endpoint counts, but does not give a complete account of inclusion and exclusion from the analysis population or the reasons observations were unavailable.

The endpoint description specifies how baseline was calculated and how serial measurements were combined, but the full statistical model and handling of missing postdose or Week 12 measurements are not reported in the registry record. The sponsor’s ANCOVA comparisons are posted, yet the full model specification is not available for complete independent reproduction. Summary-based recalculations use approximate, unadjusted methods and cannot reproduce all features of those analyses.

The registry lists many outcomes and analyses, but the complete multiplicity strategy is not reported. This limits assessment of how the reported inferential results should be viewed across the full set of tests. The original sample-size justification and design assumptions are also not reported in the registry record; the displayed planning calculations are retrospective illustrations based on observed effects, not the study’s original design calculation.

Some listed secondary outcomes have no detailed result in the record excerpt, so a full outcome-by-outcome account is not possible. The serious adverse-event summary gives counts and a list of terms, but the terms are not attributed to arms in the listed summary, and deaths are not reported in the registry record. These limitations concern available reporting and analysis detail; they do not by themselves determine the direction or validity of the posted results.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of Fluticasone Propionate MDPI Compared With Fluticasone/Salmeterol MDPI in Adolescent and Adult Patients With Persistent Asthma — NCT02139644.
• Registry record last updated 2021-11-12; status last verified 2021-11.
• Results first posted 2017-04-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

This completed Phase 3 study randomized 787 adolescents and adults with persistent asthma to FS MDPI, Fp MDPI, or placebo MDPI treatment arms for 12 weeks. The primary outcome was a standardized, baseline-adjusted FEV1 area-under-the-effect-curve measure through 12 hours after dosing at Week 12, assessed in a serial-spirometry subset.

The posted primary arm means were higher in each active arm than in placebo, and the recalculated unadjusted active-versus-placebo differences were positive. The registry also reports ANCOVA comparisons for combination therapy versus matched fluticasone-alone doses and versus placebo. Secondary results cover lung function, symptoms, rescue medication, and other outcomes, but the full multiplicity strategy and several analysis details are not reported in the registry record.

The findings should be read as estimates for the measured outcomes, analysis populations, and treatment period. The simple recalculations are distinct from the sponsor’s model-based analyses, and the planning illustrations are not the trial’s original sample-size rationale.