Clinical Study Evaluating Safety and Efficacy of Fluticasone Furoate and Fluticasone Propionate in People With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Clinical Study Evaluating Safety and Efficacy of Fluticasone Furoate and Fluticasone Propionate in People With Asthma (NCT01436110), a randomized phase 3 study. The primary outcome is Change From Baseline in Clinic Visit Evening (Pre-bronchodilator and Pre-dose) Forced Expiratory Volume in One Second (FEV1) at the End of the 24-week Treatment Period.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, parallel-group, quadruple-masked, multicentre study with a placebo control. The registry describes the study as double-blind and double-dummy. It evaluated fluticasone furoate inhalation powder, fluticasone propionate inhalation powder, and placebo in adults and adolescents with asthma who were not currently treated with inhaled corticosteroids. The registry reports an enrollment of 351 and a completed study.

The fluticasone furoate regimen was 50 mcg once daily using a Novel Dry Powder Inhaler. Fluticasone propionate was 100mcg twice daily using DISKUS/ ACCUHALER. The placebo regimen used inhalation powder through both device types. The double-dummy design means the comparison used matching inhalation procedures alongside the assigned active treatment or placebo; the registry does not report further operational detail about how masking was maintained.

The primary endpoint concerned change from baseline in evening clinic-visit FEV1 at the end of the 24-week treatment period. Secondary measures included rescue-free periods, evening and morning peak expiratory flow, symptom-free periods, and withdrawals due to lack of efficacy. Quantitative results are available for rescue-free periods and the two peak-flow outcomes. Results for symptom-free periods and withdrawals due to lack of efficacy are not reported in the registry record.

The study began in 2011-09 and its primary completion was recorded as 2012-09. The registry record does not report the original design assumptions behind enrollment, such as the effect size used for planning or the sample-size justification.

4. Participant Flow and Accounting

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

Before assignment: Participants meeting eligibility criteria at the Screening visit entered a 2-week Run-in Period for Baseline safety evaluations and to obtain measures of asthma status. Participants were then randomized to a 24-week Treatment Period. A total of 655 participants were screened; 351 were randomized, and 347 received \>=1 dose of study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent-to-Treat (ITT) Population: all participants randomized to treatment who received at least one dose of study medication. Only those participants with non-missing covariates and post-Baseline FEV1 data were analyzed.

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.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Clinic Visit Evening (Pre-bronchodilator and Pre-dose) Forced Expiratory Volume in One Second (FEV1) at the End of the 24-week Treatment Period, measured over Baseline and Week 24.

The primary endpoint was change from baseline in evening clinic-visit FEV1 at Week 24, measured in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second, and it is used as a measure of lung function. For this endpoint, the clinic measurement was taken in the evening before bronchodilator and before the dose. Spirometry was performed electronically, with the highest of 3 technically acceptable measurements recorded at scheduled clinic visits.

Change from baseline was defined as the Week 24 value minus the baseline value. Baseline was the pre-dose measurement obtained at Visit 2. Comparing change, rather than only the final measurement, incorporates where participants started into the outcome. The registry reports least-squares mean estimates, which are model-based group summaries rather than simple averages of the observed values.

The primary analysis used analysis of covariance, adjusting for baseline FEV1, region, sex, age, and treatment. Missing measurements were imputed using last observation carried forward: the last non-missing, pre-dose, post-baseline, on-treatment value at a scheduled clinic visit was used for a missing value. These analysis choices affect what the estimates represent, so the results describe the registry's specified analysis rather than an unadjusted comparison of every recorded measurement.

7. Results Posted in the Registry

• FF 50 µg OD: mean 0.13 versus 0.09 on control; difference 0.04 (95% CI -0.05 to 0.13), standardized effect d = 0.11; z-test p = 0.424.
• FP 100 µg BID: mean 0.19 versus 0.09 on control; difference 0.10 (95% CI 0.01 to 0.19), standardized effect d = 0.29; z-test p = 0.029.

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 Percentage of Rescue-free 24-hour (hr) Periods Over the 24-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:
  • FF 50 µg OD: mean 28.90 versus 21.10 on control; difference 7.80 (95% CI -1.03 to 16.63), standardized effect d = 0.23; z-test p = 0.083.
  • FP 100 µg BID: mean 31.70 versus 21.10 on control; difference 10.60 (95% CI 1.72 to 19.48), standardized effect d = 0.31; z-test p = 0.019.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FF 50 µg OD and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FP 100 µg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Daily Evening (PM) Peak Expiratory Flow (PEF) Averaged Over the 24-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:
  • FF 50 µg OD: mean 24.90 versus 7.60 on control; difference 17.30 (95% CI 6.05 to 28.55), standardized effect d = 0.40; z-test p = 0.003.
  • FP 100 µg BID: mean 12.00 versus 7.60 on control; difference 4.40 (95% CI -6.92 to 15.72), standardized effect d = 0.10; z-test p = 0.446.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF 50 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FP 100 µg BID and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Daily Morning (AM) PEF Averaged Over the 24-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:
  • FF 50 µg OD: mean 30.00 versus 10.80 on control; difference 19.20 (95% CI 8.58 to 29.82), standardized effect d = 0.47; z-test p = <0.001.
  • FP 100 µg BID: mean 21.40 versus 10.80 on control; difference 10.60 (95% CI -0.09 to 21.29), standardized effect d = 0.26; z-test p = 0.052.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for FF 50 µg OD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FP 100 µg BID and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcome pattern is not uniform across measures or treatment comparisons. The available quantitative outcomes cover change in the percentage of rescue-free periods and change in evening and morning peak expiratory flow over the 24-week treatment period. Across these measures, some comparisons have intervals that include zero and others have intervals that do not. The outcomes therefore provide supporting context rather than a single consistent signal across every measure and regimen.

These secondary outcomes relate to the primary FEV1 measure by assessing other aspects of asthma symptoms, rescue medication use, and airflow. They are not interchangeable with the primary endpoint: a change in peak flow or rescue-free time does not directly answer the primary question about evening clinic-visit FEV1. Nor do secondary outcomes resolve the uncertainty around the primary comparison.

The registry also lists symptom-free periods and withdrawal due to lack of efficacy among the secondary outcomes, but quantitative results for those outcomes are not reported in the registry record. This limits how comprehensively the secondary evidence can be assessed.

Unadjusted secondary results carry less weight because multiple outcomes and treatment comparisons create more opportunities for apparently notable findings by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. Consequently, individual secondary p-values should be read as exploratory evidence, not as definitive confirmation. Looking across the set of outcomes is more informative than selecting one result in isolation, while keeping the primary endpoint and the sponsor's analysis central to interpretation.

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

• Change From Baseline in the Percentage of Rescue-free 24-hour (hr) Periods Over the 24-week Treatment Period
• Change From Baseline in Daily Evening (PM) Peak Expiratory Flow (PEF) Averaged Over the 24-week Treatment Period
• Change From Baseline in Daily Morning (AM) PEF Averaged Over the 24-week Treatment Period
• Change From Baseline in the Percentage of Symptom-free 24-hour (hr) Periods During the 24-week Treatment Period
• Number of Participants Who Withdrew Due to Lack of Efficacy During the 24-week Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a measurement on a numerical scale, expressed in liters. The reported group estimates are least-squares means from an analysis of covariance (ANCOVA). In general, ANCOVA compares outcome values between groups while accounting for selected covariates. Here, the registry lists baseline FEV1, region, sex, age, and treatment as covariates. Adjusting for baseline and the other listed factors can produce estimates that differ from raw group averages. The posted least-squares means and sponsor comparisons therefore represent the specified model-based analysis.

What does the mean difference represent?

A mean difference describes the separation between two group means on the outcome's original scale. The comparison is oriented as active treatment against placebo in the posted results. A positive estimate indicates a higher estimated change in the active-treatment group than in placebo; a negative estimate would indicate a lower estimated change. The estimate alone does not communicate its precision, so it should be read with its interval estimate. The clinical meaning of a difference also depends on whether a meaningful-change threshold has been established; such a threshold is not reported in the registry record.

Why is there a recalculated result as well as a sponsor result?

The recalculated comparisons use posted group summary statistics to make simple, unadjusted comparisons. They are not a re-creation of the ANCOVA model, since the individual-level data and full model output are not reported in the registry record. The standard deviations used for these recalculations are approximate, inferred from the reported standard errors and group sizes. This makes the recalculated interval and p-value useful as a consistency check, but not a substitute for the sponsor's analysis. Because the record flags a discrepancy, the sponsor's own ANCOVA analysis takes precedence.

What does the standard error tell the reader?

A standard error describes the estimated uncertainty around a group mean. In general, it reflects how precisely the mean is estimated, rather than how widely individual measurements vary. Standard errors should not be mistaken for standard deviations. The primary endpoint lists standard errors for each group, while the recalculated comparison uses approximate variability reconstructed from these summary values. That reconstruction does not recover the original participant-level distribution or the covariance structure used in ANCOVA.

How were missing primary measurements handled?

The primary analysis used last observation carried forward (LOCF). In general, LOCF replaces a missing follow-up value with the participant's last eligible observed value. The registry specifies that the value had to be non-missing, pre-dose, post-baseline, on-treatment, and from a scheduled clinic visit. This approach carries an earlier measurement forward as if it were a proxy for the missing scheduled measurement. It does not, by itself, account for uncertainty about what the unobserved value would have been. The record does not report sensitivity analyses using alternative missing-data assumptions.

Who contributed to the primary analysis?

The intention-to-treat population was defined as all participants randomized to treatment who received at least one dose of study medication. The endpoint analysis further required non-missing covariates and post-baseline FEV1 data. Thus, the analysis population for this outcome was narrower than the definition of the intention-to-treat population alone. The registry record does not report additional detail about exclusions or the number of participants omitted from the endpoint analysis.

How should p-values be used?

A p-value is a measure of how compatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that a treatment effect is true, and it does not measure the size or clinical importance of an effect. A smaller p-value is not a replacement for an estimate and its interval. The p-values in the recalculation are unadjusted, and the registry record does not report whether the sponsor adjusted for multiple comparisons across outcomes or treatment contrasts. The primary comparison results should therefore be interpreted with the design, uncertainty, and reporting limitations in view.

These explanations of ANCOVA, standard errors, LOCF, and p-values are general statistical context. They do not add analysis details beyond those recorded for this trial.

11. Confidence Intervals and Precision

For fluticasone furoate versus placebo, the recalculated mean difference in primary FEV1 change was 0.037 liters. Its interval runs from -0.054 to 0.128, spanning zero. That range is compatible with values on either side of zero under the recalculation, so the estimate is not precise enough to rule out no difference on that basis. The unadjusted p-value was 0.424.

For fluticasone propionate versus placebo, the recalculated mean difference was 0.102 liters, with an interval from 0.011 to 0.193. The interval does not include zero, but it still spans a range of possible effect sizes. The unadjusted p-value was 0.029. The estimate's direction and apparent separation from zero should not be treated as proof of clinical importance; no threshold for a meaningful difference is reported in the registry record.

The sponsor reports 95% confidence intervals for its ANCOVA comparisons. For fluticasone furoate, the reported interval is -0.055 to 0.128; for fluticasone propionate, it is 0.010 to 0.194. In general, a confidence interval describes the uncertainty associated with an estimate under the assumptions of the analysis. A wider interval indicates less precision than a narrower interval, while an interval spanning zero leaves a zero difference among the values compatible with the data at that confidence level.

The recalculated intervals are based on approximate standard deviations inferred from summary statistics, whereas the sponsor's intervals come from the reported ANCOVA analysis. They are not interchangeable. The sponsor's results take precedence because the record flags a discrepancy, and the full underlying model details are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect and 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 as the stated fraction of the observed effect. These are planning assumptions for the illustration; the original trial design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a design to have an 80% chance of detecting the specified effect under the planning assumptions, if that effect and those assumptions hold. The 90% power column describes the corresponding target for a 90% chance. These are prospective design calculations, not statements about what the completed study was able to detect. They are not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. That pattern reflects a general feature of study planning: smaller differences are harder to distinguish from sampling variation, so more information is needed. The observed effect used as a planning reference is itself uncertain, particularly when estimated in a study with limited precision. It should not be assumed that a future study will reproduce it.

The curve is another way to read how the planning calculation changes as the target effect changes. It represents an illustration under the stated assumptions, not a forecast of a future study's results. Readers should distinguish these planning values from the enrollment in this completed trial and from any claim about the trial's observed ability to detect an effect.

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 = 0.037; pooled standard deviation σ = 0.348.
2. n = 2 × (1.96 + 0.842)² × 0.348² / 0.037² = 1,391.0, rounded up to 1,392 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 <- 0.037                      # observed difference in means
sigma <- 0.348296723434998                     # 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(1436110)
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 = 1,392 (80% power), 1,863 (90% power)
 75% of observed effect: n per arm = 2,473 (80% power), 3,311 (90% power)
 50% of observed effect: n per arm = 5,565 (80% power), 7,449 (90% power)
power.t.test: 1392 
Simulated power at n = 1,392 per arm: 0.804 (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 the sponsor's primary endpoint comparisons from ANCOVA, alongside recalculations made from posted summary statistics. For fluticasone furoate versus placebo, the sponsor reports a mean difference of 0.037 liters, a 95% confidence interval from -0.055 to 0.128, and p = 0.430. The recalculation gives 0.037 liters, an interval from -0.054 to 0.128, and p = 0.424.

For fluticasone propionate versus placebo, the sponsor reports a mean difference of 0.102 liters, a 95% confidence interval from 0.010 to 0.194, and p = 0.030. The recalculation gives 0.102 liters, an interval from 0.011 to 0.193, and p = 0.029. Thus, the estimates are close, while interval bounds and p-values differ slightly.

The recalculations are unadjusted and depend on approximate variability inferred from summary statistics. They do not reproduce the sponsor's ANCOVA with its listed covariates. Since the record flags a discrepancy, the sponsor's own analysis takes precedence. The recalculated values serve as an independent summary-statistic check, not as a correction to the sponsor's reported analysis.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study examines several outcomes, treatment contrasts, or analyses. In general, the more statistical comparisons made, the greater the chance that at least one result may appear unusual by chance even when there is no underlying difference. This matters in this study because the registry lists a primary endpoint, several secondary outcomes, and active-treatment comparisons against placebo. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a strategy for controlling the overall error rate. It is therefore not possible to determine from the record how the sponsor intended the secondary comparisons to contribute to formal conclusions.

The primary endpoint analysis used ANCOVA with baseline, region, sex, age, and treatment as covariates. The record describes this model and reports sponsor comparisons, but a full statistical analysis plan is not reported in the registry record. Details such as model diagnostics, handling of departures from model assumptions, and any planned sensitivity analyses are also not reported in the registry record.

Missing primary FEV1 values were handled using LOCF, with the last eligible on-treatment measurement carried forward. This is a specific imputation rule, not a complete description of all possible missing-data behavior. The registry record does not report the extent or reasons for missingness, nor does it report sensitivity analyses showing how conclusions might change under alternative assumptions.

The primary analysis population required randomization, receipt of at least one study dose, non-missing covariates, and post-baseline FEV1 data. The record does not report further detail on participants excluded from the endpoint analysis or how missing covariates affected inclusion. These reporting gaps limit assessment of robustness and make it important to distinguish the stated analysis population from a broader interpretation of all randomized participants.

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 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholelithiasis (0.9%), pneumonia (0.9%), premenstrual syndrome (0.9%), dermatitis (0.9%).

The registry lists serious adverse event counts by safety group. The reported figures are 3 affected participants among 115 at risk in the placebo group, 0 among 117 at risk in the fluticasone furoate group, and 1 among 115 at risk in the fluticasone propionate group. These are counts from the registry record, not estimates of comparative risk adjusted for follow-up or other factors.

For other adverse events, the record reports 36 affected participants among 115 at risk with placebo, 38 among 117 at risk with fluticasone furoate, and 39 among 115 at risk with fluticasone propionate. The listed top serious adverse event terms each have a reported frequency of 0.9%: Cholelithiasis, Pneumonia, Premenstrual syndrome, and Dermatitis. The record does not provide enough detail in these summary figures to assess event timing, duration, severity beyond serious-event status, or causal attribution.

Death counts are not reported in the registry record. These safety counts should be read as descriptive summaries; the record does not report a formal statistical comparison of adverse events.

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

The registry results describe changes in a specific lung-function measure during a 24-week treatment period in adults and adolescents with asthma who were not currently treated with inhaled corticosteroids. For the primary endpoint, the sponsor's ANCOVA estimates differ between placebo and each active-treatment group, with different degrees of statistical precision. The sponsor's comparison for fluticasone furoate has a 95% confidence interval spanning zero; the fluticasone propionate interval is on the positive side of zero. Those are statements about the estimates and intervals reported for this endpoint, not a general judgment about treatment.

A statistical difference is not automatically a clinically important difference. The registry record does not report a threshold that would define a meaningful change in FEV1. Conversely, an interval that includes zero does not prove that the groups are identical; it indicates that the analysis has not ruled out zero difference within the interval's range. Estimates, intervals, study design, and analysis assumptions all contribute to interpretation.

The results do not establish effects on outcomes that were not measured or quantitatively reported. The available secondary results address rescue-free periods and peak expiratory flow, while results for symptom-free periods and withdrawal due to lack of efficacy are not reported in the registry record. The findings also do not settle longer-term outcomes beyond the treatment period recorded.

The observed adverse-event counts are descriptive and do not establish whether an event was caused by a study treatment. The registry record does not report deaths, multiplicity handling, or a full statistical analysis plan. These limitations, along with LOCF imputation and the endpoint-specific analysis population, are relevant when deciding how broadly to interpret the numerical findings. No medical recommendation follows from these registry statistics alone.

18. Why This Trial Matters Statistically

This study illustrates why reading a clinical-trial result involves more than looking at which group has the largest mean. The endpoint is a change from baseline, and the reported group values are adjusted least-squares means from ANCOVA. The group contrast, its uncertainty interval, the analysis population, and missing-data handling all affect what the result means.

It also provides a useful example of the distinction between a sponsor's adjusted analysis and a simple recalculation from posted summaries. The recalculated primary estimates are close to the sponsor's estimates, but their intervals and p-values are not identical. Since the record flags a discrepancy, the sponsor's model-based results take precedence. This highlights why a summary-statistic check should not be mistaken for a reproduction of an analysis using participant-level data.

The secondary outcomes show why multiplicity and consistency matter. Several related outcomes can add context, but they do not each carry the same evidentiary weight as a prespecified primary outcome, especially when the registry does not report how multiple comparisons were handled. Similarly, sample-size illustrations based on observed effects can inform future planning but cannot establish what the original trial was designed to detect or how much power it had after completion.

Finally, precision and clinical relevance are distinct. Confidence intervals communicate uncertainty about estimated contrasts, while clinical interpretation requires context and a meaningful-change threshold. The threshold is not reported in the registry record. Keeping these distinctions clear supports a measured reading of the results without overstating what a single study can show.

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 comparison is reported alongside a recalculation based on summary statistics, and the record flags a discrepancy. The recalculation uses approximate standard deviations inferred from standard errors and group sizes; it cannot reproduce the sponsor's adjusted ANCOVA or the information in participant-level data. The sponsor's analysis should therefore be treated as primary.

The endpoint analysis used LOCF for missing values. Although the imputation rule is described, the extent and reasons for missing primary measurements are not reported in the registry record, and alternative missing-data analyses are not reported. The endpoint population also required non-missing covariates and post-baseline FEV1 data, so the analysis was not necessarily based on every randomized participant.

The registry record does not report the original sample-size justification, the assumptions used to plan the completed study, or whether an interim analysis was planned or conducted. The planning illustrations based on observed effects are not evidence about the trial's original design. A multiplicity strategy for the several secondary outcomes and treatment comparisons is also not reported in the registry record.

Quantitative secondary results are not reported for symptom-free periods or withdrawals due to lack of efficacy, despite their inclusion in the listed outcomes. The record also does not report a clinically meaningful FEV1 threshold, a full analysis plan, or detailed safety comparisons. These omissions limit assessment of clinical relevance, robustness, and the full balance of outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Clinical Study Evaluating Safety and Efficacy of Fluticasone Furoate and Fluticasone Propionate in People With Asthma — NCT01436110.
• Registry record last updated 2017-01-09; status last verified 2016-11.
• Results first posted 2014-09-03.
• 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 record describes a completed, randomized, quadruple-masked, parallel-group Phase 3 asthma study with placebo control and enrollment of 351. It compared once-daily fluticasone furoate 50 mcg, twice-daily fluticasone propionate 100mcg, and placebo over a 24-week treatment period.

The primary outcome was change from baseline in evening clinic-visit FEV1 at Week 24. The sponsor reported ANCOVA mean differences versus placebo of 0.037 liters for fluticasone furoate and 0.102 liters for fluticasone propionate, with their respective 95% confidence intervals and p-values reported in the registry. Recalculations from posted summary statistics are close but differ slightly; the sponsor's analysis takes precedence because the record flags a discrepancy.

Secondary results provide additional measures of rescue-free time and peak flow, while some listed secondary outcomes lack quantitative results in the registry record. Safety summaries report serious adverse event counts by group. Details of multiplicity handling, original sample-size assumptions, and several analysis limitations are not reported in the registry record.