A Study of the Effectiveness and Safety of Different Doses of Fluticasone Propionate Taken From a Dry Powder Inhaler (Puffer) in Adolescents and Adults Who Have Asthma That is Not Controlled by High Dose Inhaled Corticosteroid Asthma Medications: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study of the Effectiveness and Safety of Different Doses of Fluticasone Propionate Taken From a Dry Powder Inhaler (Puffer) in Adolescents and Adults Who Have Asthma That is Not Controlled by High Dose Inhaled Corticosteroid Asthma Medications (NCT01576718), a randomized phase 2 study. The primary outcome is Change From Baseline In Trough (Morning Predose And Pre-Rescue Bronchodilator) Forced Expiratory Volume In 1 Second (FEV1) Over The 12-Week Treatment Period.

2. Clinical Question

The central question was whether different twice-daily doses of fluticasone propionate delivered by a multidose dry powder inhaler were associated with changes in morning trough forced expiratory volume in 1 second (FEV1), compared with placebo, over 12 weeks. The study included adolescents and adults whose severe persistent asthma remained uncontrolled on high-dose inhaled corticosteroid therapy. It also evaluated safety and several other lung-function, symptom-related, study-retention, and pharmacokinetic outcomes.

3. Trial Design

This was a randomized, quadruple-masked, parallel-group Phase 2 study. The registry lists 889 participants enrolled and the study status as completed. The trial started in 2012-04, with primary completion in 2013-07. Its stated treatment period was 12 weeks.

Participants were assigned to one of four fluticasone propionate doses, placebo, or an active Flovent Diskus comparator. The fluticasone multidose dry powder inhaler doses were 50, 100, 200, and 400 mcg per dose, all administered twice daily. Flovent Diskus 250 mcg was open label; the other listed treatment arms were described as double blind. The primary treatment comparisons were fluticasone doses versus placebo, and the stated primary model excluded Flovent Diskus data.

During run-in and treatment, participants replaced their current rescue medication with albuterol/salbutamol. The registry describes the primary endpoint population as a full analysis set, including participants who contributed at least once to the analysis. Following blinded data review, data from one site were excluded because of good clinical practice concerns. The number of participants excluded from that site is not reported in the registry record.

The registry describes efficacy and safety aims and lists outcomes that include spirometry, peak expiratory flow, rescue-free periods, retention in the study, pharmacokinetic measures, and treatment-emergent adverse experiences. The original protocol’s sample-size justification, allocation ratio, and detailed schedule for any interim analyses are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: 1238 subjects with asthma at 180 centers were screened for enrollment. 889 subjects met entry criteria and were enrolled into the run-in period of the study. Of the 349 subjects who were not enrolled, 337 were excluded on the basis of inclusion/exclusion criteria, 5 subjects withdrew consent, and for 6 the reason given was "other".

Only the first 6 of 7 groups are shown.

Pre-Assignment Period (Run-In Placebo)

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, including participants who contributed at least once to the analysis. Based on blinded data review, data from one site are excluded due to good clinical practice (GCP) concerns. Flovent Diskus data was used for confirmatory and exploratory endpoints; FEV1 data for Flovent Diskus is reported in outcome #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 analysis set

Only the first 6 of 7 groups are shown.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline In Trough (Morning Predose And Pre-Rescue Bronchodilator) Forced Expiratory Volume In 1 Second (FEV1) Over The 12-Week Treatment Period, measured over Baseline (Day 1 pre-dose), Weeks 1, 2, 3, 4, 6, 8, 10 and 12.

The primary endpoint was change from baseline in trough morning FEV1 during the 12-week treatment period, measured in liters. FEV1 is the volume of air forcibly exhaled in the first second of a breathing maneuver. In general, it is used in respiratory research as an objective measure of airflow and lung function. The registry’s endpoint was specifically a morning measurement taken before the investigational dose and before albuterol/salbutamol.

Measurements were collected electronically by spirometry at morning study-site visits. The highest value from 3 acceptable and 2 reproducible maneuvers was used, and all FEV1 data were submitted to a central reading center for evaluation. The endpoint timeframe included baseline on Day 1 before dosing and follow-up visits at Weeks 1, 2, 3, 4, 6, 8, 10, and 12.

Change from baseline focuses the comparison on how measurements shifted during treatment relative to participants’ starting values. The reported arm summaries are least-squares means with standard errors, rather than unadjusted raw means. In general, least-squares means are model-based estimates that account for terms included in the specified analysis. The registry’s primary model included baseline FEV1, sex, age, treatment, visit, and the treatment-by-visit interaction, with an unstructured covariance matrix.

FEV1 is an objective physiologic endpoint, but the registry record does not state a threshold for a clinically important change. Statistical estimates therefore describe the measured changes and their uncertainty; they do not by themselves establish how meaningful a particular difference would be to patients.

7. Results Posted in the Registry

• Fp MDPI 50 mcg: mean 0.06 versus 0.05 on control; difference 0.01 (95% CI -0.07 to 0.08), standardized effect d = 0.02; z-test p = 0.878.
• Fp MDPI 100 mcg: mean 0.10 versus 0.05 on control; difference 0.05 (95% CI -0.03 to 0.12), standardized effect d = 0.17; z-test p = 0.218.
• Fp MDPI 200 mcg: mean 0.11 versus 0.05 on control; difference 0.06 (95% CI -0.02 to 0.13), standardized effect d = 0.20; z-test p = 0.158.
• Fp MDPI 400 mcg: mean 0.12 versus 0.05 on control; difference 0.07 (95% CI -0.01 to 0.15), standardized effect d = 0.26; z-test p = 0.068.

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 Weekly Average Of Daily Trough (Predose And Pre-Rescue Bronchodilator) Morning Peak Expiratory Flow (PEF) 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:
  • Fp MDPI 50 mcg: mean 10.48 versus 2.24 on control; difference 8.24 (95% CI -3.97 to 20.45), standardized effect d = 0.19; z-test p = 0.186.
  • Fp MDPI 100 mcg: mean 9.34 versus 2.24 on control; difference 7.10 (95% CI -5.03 to 19.23), standardized effect d = 0.16; z-test p = 0.251.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 50 mcg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 100 mcg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline In Weekly Average Of Daily Trough (Predose And Pre-Rescue Bronchodilator) Evening Peak Expiratory Flow (PEF) 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:
  • Fp MDPI 50 mcg: mean 3.81 versus 3.42 on control; difference 0.39 (95% CI -11.60 to 12.38), standardized effect d = 0.01; z-test p = 0.949.
  • Fp MDPI 100 mcg: mean 6.41 versus 3.42 on control; difference 2.99 (95% CI -9.03 to 15.01), standardized effect d = 0.07; z-test p = 0.626.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 50 mcg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 100 mcg and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline In The Percentage Of Rescue-Free 24-Hour Periods

• 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:
  • Fp MDPI 50 mcg: mean 22.78 versus 27.15 on control; difference -4.37 (95% CI -16.15 to 7.41), standardized effect d = -0.11; z-test p = 0.467.
  • Fp MDPI 100 mcg: mean 26.41 versus 27.15 on control; difference -0.74 (95% CI -12.52 to 11.04), standardized effect d = -0.02; z-test p = 0.902.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 50 mcg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Fp MDPI 100 mcg and the control. The interval gives the range of effects that remain compatible with the data.

The registry’s secondary outcomes span several kinds of information: morning and evening peak expiratory flow (PEF), rescue-free periods, remaining in the study, pharmacokinetic measures, and treatment-emergent adverse experiences. This range complements the primary FEV1 endpoint by describing other measures of lung function, treatment experience, and safety. The posted detailed summaries cover a subset of those measures; not every listed outcome has detailed numerical results in the record.

Across the posted secondary lung-function summaries, arm-level estimates do not tell a single uniform story. The morning PEF estimates are higher than placebo in the listed fluticasone arms, while the registry’s reported comparison for the 400 mcg arm has an interval that includes zero. Evening PEF estimates vary across doses, and the reported 400 mcg comparison likewise has an interval including zero. Rescue-free-period estimates also vary among treatment arms, and the registry’s listed comparisons do not consistently point in one direction. These secondary patterns do not overturn or independently confirm the primary FEV1 result.

In general, secondary outcomes are useful for exploring whether a primary finding is accompanied by changes in related measures. However, multiple outcomes and comparisons create more opportunities for apparently notable findings by chance. The registry does not report a multiplicity adjustment strategy. Consequently, unadjusted secondary results carry less inferential weight than a prespecified primary analysis and should be treated as exploratory context rather than as standalone confirmation.

The listed pharmacokinetic and safety outcomes address different questions from lung-function efficacy measures. They cannot be combined into a single claim about treatment effect. The registry record does not report a complete, detailed result for every secondary outcome listed, so the overall secondary evidence cannot be fully characterized from the posted numerical summaries alone.

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

• Change From Baseline In Weekly Average Of Daily Trough (Predose And Pre-Rescue Bronchodilator) Morning Peak Expiratory Flow (PEF) Over The 12-Week Treatment Period
• Change From Baseline In Weekly Average Of Daily Trough (Predose And Pre-Rescue Bronchodilator) Evening Peak Expiratory Flow (PEF) Over The 12-Week Treatment Period
• The Kaplan-Meier Estimate Of The Probability Of Remaining In The Study At Week 12
• Change From Baseline In The Percentage Of Rescue-Free 24-Hour Periods
• Area Under The Plasma Concentration-Time Curve From Time Zero To The Time Of The Last Measurable Concentration (AUC0-t)
• Maximum Observed Plasma Concentration (Cmax)
• Time Of Maximum Observed Plasma Concentration (Tmax)
• Patients With Treatment-Emergent Adverse Experiences (TEAE) During the Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis used a mixed model for repeated measures (MMRM). In general, this type of model uses repeated outcome observations across visits while accounting for the fact that measurements from the same participant are related. The registry specifies that the primary treatment comparisons to placebo came from an MMRM model excluding Flovent Diskus data.

What did the model include?

The registry describes the model as change from baseline explained by baseline FEV1, sex, age, treatment, visit, and the treatment-by-visit interaction. In general, including baseline and other listed terms can adjust the estimated treatment comparison for those variables within the model. A treatment-by-visit interaction allows the modelled treatment differences to vary across visits rather than requiring one common difference at every time point. The registry does not provide further detail on model diagnostics or the exact procedure used to obtain the reported endpoint estimates.

What does an unstructured covariance matrix mean?

The primary model assumed an unstructured covariance matrix. In general, a covariance structure describes how repeated measurements within a participant are related. An unstructured choice does not impose a simple pattern on those relationships; it allows the model to estimate them flexibly. Such flexibility can be useful when the relationship among visits is not assumed to follow a particular pattern, but it also relies on the available data being sufficient for estimating the model. The registry does not report alternative covariance structures or sensitivity analyses for this choice.

What are least-squares means and standard errors?

The registry reports least-squares mean changes for each arm and standard errors. In general, a least-squares mean is a model-based arm estimate, while a standard error describes the estimated sampling variability of that estimate. A standard error is not the spread of individual participant measurements. The posted means and standard errors can help describe the estimates, but a treatment comparison and its confidence interval are more directly informative about uncertainty in the difference between arms.

How should the reported comparisons be distinguished from recalculations?

The registry’s own comparisons are based on its stated repeated-measures model. Separately, the simple unadjusted recalculations use the posted arm summaries to estimate differences, confidence intervals, and p-values. In general, a summary-statistic recalculation cannot reproduce all adjustments or covariance handling in a participant-level repeated-measures analysis. Some pooled standard deviations used in those recalculations are approximate, derived from the posted standard errors. Since the recorded discrepancy flag is true, the sponsor’s own analysis takes precedence when the results differ.

What do the p-values and confidence intervals say?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the analysis assumptions; it is not the probability that the null hypothesis is true. A confidence interval gives a range of values compatible with the data and model at its stated confidence level. The primary reported pairwise intervals are 95% confidence intervals. Their width reflects uncertainty, and their inclusion of zero means the comparisons do not precisely distinguish a nonzero difference from no difference at that confidence level. Neither measure resolves clinical importance, which requires context not reported in the registry record.

What remains unspecified?

The registry gives the primary analysis model and describes the analysis population, but other statistical details are not reported in the registry record. These include the handling of missing outcome measurements, any imputation approach, a multiplicity adjustment strategy, a detailed prespecified analysis plan, and the trial’s original sample-size justification. These omissions do not change the reported estimates, but they limit a full appraisal of how all analysis decisions were planned and how uncertainty across multiple outcomes and comparisons was addressed.

11. Confidence Intervals and Precision

The registry reports 95% confidence intervals for the primary dose-versus-placebo comparisons. For Fp MDPI 400 mcg, the reported estimated difference was 0.072 liters, with an interval from -0.004 to 0.149 liters. For 200 mcg, it was 0.056 liters, with an interval from -0.022 to 0.133 liters; for 100 mcg, 0.048 liters, with an interval from -0.029 to 0.124 liters; and for 50 mcg, 0.006 liters, with an interval from -0.070 to 0.083 liters.

In general, a confidence interval communicates both the direction and precision of an estimate. These intervals span zero, so the registry results leave uncertainty about whether the underlying difference is positive, negative, or close to zero. Their breadth also shows that the observed estimates do not pin down a narrow range of plausible differences. The registry record does not supply a clinical-importance threshold for FEV1 change, so the intervals cannot be classified against such a threshold.

The arm-level standard errors describe uncertainty in the model-based mean changes, whereas the confidence intervals above describe uncertainty in between-arm differences. Those quantities answer related but distinct questions. The trial’s reported model-based intervals should be distinguished from the approximate intervals in the recalculations, which use posted summary statistics and do not reproduce the full repeated-measures model. Because the sponsor-analysis discrepancy is flagged, the sponsor’s estimates and intervals are the primary basis for interpretation.

Precision also depends on the analysis population and data available for each outcome. The endpoint summaries involve fewer participants per arm than the overall enrollment, and the full analysis set required at least one contribution to the analysis. The registry does not report the missing-data method or a clinical threshold, limiting further assessment of the intervals’ practical meaning.

12. Planning a Similar Trial: Sample Size

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

The planning figures are illustrations based on the observed effect, not a description of the trial’s original design calculation. For these continuous outcomes, the figures are participants per arm, not total events. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set at the stated fraction of the observed effect. Time-to-event calculations, if present, use total events under the Schoenfeld method; that distinction does not apply to the continuous outcomes.

The 80% power column represents the estimated participants per arm for a future two-arm study to have an 80% probability of detecting the selected effect under the stated assumptions, if that effect were the true one. The 90% power column uses a higher probability target and therefore generally requires more participants per arm for the same assumed effect. Smaller effects need more participants because they are harder to distinguish from ordinary sampling variation.

Rows using 100%, 75%, or 50% of the observed effect are alternative planning scenarios. They are not observed outcomes and do not establish the effect a future study will achieve. Some figures can become very large when the observed difference is small relative to variability. In particular, planning values based on a near-zero observed difference should not be read as evidence that the trial had a particular level of power.

These are planning illustrations, not observed power. The original trial’s sample-size assumptions and justification are not reported in the registry record. The planning calculations therefore should not be used to infer the rationale for the enrolled sample or to retrospectively judge the study as adequately or inadequately powered.

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 = 0.006; pooled standard deviation σ = 0.277.
2. n = 2 × (1.96 + 0.842)² × 0.277² / 0.006² = 33,498.5, rounded up to 33,499 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 <- 0.006                      # observed difference in means
sigma <- 0.277169358515692                     # 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(1576718)
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 = 33,499 (80% power), 44,846 (90% power)
 75% of observed effect: n per arm = 59,553 (80% power), 79,725 (90% power)
 50% of observed effect: n per arm = 133,995 (80% power), 179,381 (90% power)
power.t.test: 33499.5 
Simulated power at n = 33,499 per arm: 0.797 (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 sponsor’s reported primary analysis is based on the stated MMRM, which includes baseline FEV1, sex, age, treatment, visit, and treatment-by-visit, with an unstructured covariance matrix. Its placebo comparisons are the relevant registry analyses for the primary endpoint. For the highest fluticasone dose, the sponsor reported an LSM difference of 0.072 liters, a 95% confidence interval from -0.004 to 0.149, and p = 0.064. The other dose comparisons are also reported with confidence intervals spanning zero.

The separate recalculations use arm-level means, standard errors, and approximate pooled standard deviations to make simple, unadjusted comparisons. Their purpose is to offer a transparent check on the posted summaries, not to recreate the sponsor’s participant-level repeated-measures analysis. Differences between these calculations and the registry analyses can arise because they are not the same statistical procedure. The discrepancy flag is true, so the sponsor’s own analysis takes precedence.

The registry’s reported p-values are not all identical to the recalculated p-values, and the reported confidence limits also differ slightly in some comparisons. Interpretation should therefore rely on the sponsor analysis for the primary inference. The recalculated values can still help readers understand the scale of the observed contrasts, but should not be treated as confirmatory results or as evidence that a different analysis is more valid.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint includes multiple treatment comparisons against placebo, and the registry also lists numerous secondary outcomes. In general, evaluating many comparisons increases the chance that at least one result may appear notable by chance, even when no corresponding underlying effect exists. Statistical approaches such as prespecified adjustment or a testing hierarchy can address this issue, but the multiplicity strategy is not reported in the registry record. It is therefore not possible to tell from the record whether or how the primary dose comparisons or secondary analyses were adjusted for multiple testing.

The primary model and full analysis set are described. The analysis set includes participants who contributed at least once, and the registry says that one site’s data were excluded after blinded review because of good clinical practice concerns. The number excluded from that site and the detailed effects of its exclusion are not reported in the registry record.

The handling of missing FEV1 measurements is not reported in the registry record. The stated repeated-measures model does not, by itself, disclose what assumptions or procedures were used for missing observations, whether any imputation was performed, or how participants with incomplete visit data contributed. The registry also does not provide a complete account of sensitivity analyses addressing missingness.

The original protocol’s sample-size justification, detailed prespecified statistical analysis plan, and interim-analysis plan are not reported in the registry record. These omissions matter when assessing how the analysis was planned, how well the study could distinguish effects of different sizes, and how the many outcomes were interpreted. They do not invalidate the posted estimates, but they limit the extent to which the record alone can establish that every analysis decision was prespecified or that missing data and multiplicity were fully addressed.

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: myocardial infarction (0.9%), asthma (0.9%), kidney infection (0.9%), prostate cancer (0.9%).

The registry lists serious adverse experiences by treatment arm. One serious event was reported among 107 participants at risk in the Fp MDPI 50 mcg arm, one among 107 in the 100 mcg arm, one among 106 in the 200 mcg arm, none among 107 in the 400 mcg arm, and one among 106 in the placebo arm. No serious events were reported among 106 participants at risk in the Flovent Diskus arm. These are arm-specific counts; they should not be read as proof of equivalent safety or as a precise comparison of risk.

The registry lists myocardial infarction, asthma, kidney infection, and prostate cancer among the top serious-event terms, each at 0.9%. The deaths field is not populated, so deaths are not reported in the registry record. Counts for other adverse experiences are also listed, but the serious-event counts are the focus of this comparison.

In general, uncommon events and small counts leave considerable uncertainty about differences between arms. These results describe the adverse-event information posted for the treatment period and do not establish whether an event was caused by treatment. The registry’s safety summaries should be considered alongside the trial’s limited 12-week treatment timeframe and the specific enrolled population.

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

The primary results describe model-based changes in morning trough FEV1 and comparisons with placebo during the 12-week treatment period. The sponsor’s reported estimates are larger for the higher-dose arms than for placebo, but each listed primary pairwise confidence interval includes zero. The intervals indicate that the registry results leave uncertainty about the size and direction of the underlying between-group differences.

These findings do not establish that the treatments are equivalent, nor do they demonstrate that any dose produces a clinically important difference. A confidence interval including zero is not proof of no effect; it signals that the data and analysis do not precisely rule out no difference at the stated confidence level. The registry does not report a threshold for a meaningful FEV1 change, and statistical significance alone would not answer that clinical question.

The results also do not settle questions beyond the endpoint and study context. The trial focused on adolescents and adults with severe persistent asthma uncontrolled on high-dose inhaled corticosteroid therapy, used a 12-week treatment period, and assessed a particular inhaled formulation and dose range. The posted data do not establish longer-term outcomes or effects in other populations or settings.

Safety counts describe events recorded in the treatment arms, but the small serious-event counts do not support strong comparative conclusions. They should not be used as a substitute for a broader safety assessment. The registry record does not report deaths, and it does not establish a causal link between an event and a treatment.

Overall, the posted data are best read as estimates with uncertainty, not as a simple yes-or-no verdict. The sponsor’s model-based comparisons take precedence over the approximate recalculations, and the unadjusted secondary results provide supporting context with less inferential weight.

18. Why This Trial Matters Statistically

This study illustrates why treatment estimates need to be read together with their uncertainty. Arm-level mean changes can appear to rise across increasing doses, but the primary question is the estimated difference from placebo and how precisely that difference is measured. The sponsor’s reported confidence intervals make that uncertainty explicit and include zero for each listed dose comparison.

It also demonstrates the distinction between a registry’s main analysis and a summary-statistic recalculation. The primary MMRM accounts for repeated observations and includes specified baseline and participant terms. An unadjusted calculation from arm summaries is more limited. When the two approaches differ, the sponsor’s own analysis is the appropriate primary reference rather than treating a simpler recalculation as a competing trial result.

The trial’s outcomes also raise a common interpretive issue: several doses and multiple secondary outcomes create a broad set of comparisons. Without a reported multiplicity strategy, secondary findings warrant caution. Likewise, planning calculations based on the observed effect are not a substitute for the trial’s original sample-size rationale and are not a measure of observed power.

Finally, the record links statistical interpretation to the quality and scope of the underlying data. The primary analysis set excluded a site after blinded review, the endpoint estimates are based on participants contributing to the analysis, and details about missing-data methods are not reported. These features do not erase the posted results, but they define the limits of what can be inferred from the registry record alone.

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 inference is based on a 12-week endpoint in a specific population: adolescents and adults with severe persistent asthma uncontrolled on high-dose inhaled corticosteroid therapy. The registry record does not establish how the results apply to different populations, treatment durations, or settings. It also does not report a clinically important threshold for FEV1 change, limiting interpretation of practical importance.

One site was excluded from the primary analysis population following blinded data review because of good clinical practice concerns. The number of participants at that site and the effect of excluding its data are not reported in the registry record. The full analysis set required at least one contribution, and the method used to handle missing measurements is not reported.

The registry reports the MMRM model but does not report a multiplicity adjustment strategy, a detailed prespecified analysis plan, or the original sample-size justification. It also does not provide all detailed numerical results for every listed secondary outcome. These gaps limit evaluation of the broader analysis plan and the strength of secondary findings.

The sponsor and approximate recalculated comparisons differ in some details, and the discrepancy flag indicates that the sponsor’s analysis takes precedence. The recalculations use posted summary statistics rather than reproducing the full repeated-measures model. Finally, the serious adverse-event counts are small, and deaths are not reported in the registry record; these summaries do not support firm conclusions about comparative safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study of the Effectiveness and Safety of Different Doses of Fluticasone Propionate Taken From a Dry Powder Inhaler (Puffer) in Adolescents and Adults Who Have Asthma That is Not Controlled by High Dose Inhaled Corticosteroid Asthma Medications — NCT01576718.
• Registry record last updated 2018-05-08; status last verified 2018-05.
• 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

The registry describes a completed randomized, quadruple-masked, parallel-group Phase 2 study with 889 participants enrolled. It compared four twice-daily fluticasone propionate doses with placebo over 12 weeks in adolescents and adults with severe persistent asthma uncontrolled on high-dose inhaled corticosteroid therapy. An open-label Flovent Diskus comparator was also included.

The primary endpoint was change from baseline in morning trough FEV1. The sponsor’s reported dose-versus-placebo confidence intervals include zero, and the registry does not state a clinical-importance threshold. Approximate summary-statistic recalculations differ from some sponsor analysis details; the sponsor’s own analysis takes precedence. The record lists multiple secondary outcomes and safety summaries, while multiplicity adjustment and missing-data methods are not reported.