Crossover Study Comparing Fluticasone Furoate (FF)/Vilanterol (VI) Once Daily Versus Fluticasone Propionate (FP) Twice Daily in Subjects With Asthma and Exercise-Induced Bronchoconstriction (EIB): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Crossover Study Comparing Fluticasone Furoate (FF)/Vilanterol (VI) Once Daily Versus Fluticasone Propionate (FP) Twice Daily in Subjects With Asthma and Exercise-Induced Bronchoconstriction (EIB) (NCT02730351), a randomized phase 4 study. The primary outcome is Maximal Percent Decrease in Forced Expiratory Volume in One Second (FEV1) Following Exercise Challenge at 12 Hours (Hrs) Post Evening Dose From Pre-exercise FEV1..

2. Clinical Question

3. Trial Design

This was a completed, Phase 4, randomized, double-blind, double-dummy, crossover study, registered as NCT02730351. The sponsor was GlaxoSmithKline. The record lists enrollment as 75 and describes a multicenter study in adolescent and adult participants with asthma and exercise-induced bronchoconstriction. The recorded study start was 2016-05-25, and primary completion was 2017-02-03.

In a crossover design, participants receive more than one treatment in an assigned sequence, so treatment comparisons can be made within participants as well as across treatment periods. This can account for some stable differences between participants. It also makes the timing and order of treatments important: period effects, sequence effects, and any carryover from an earlier treatment can matter. The registry record describes a 2-week washout period, but it does not report a detailed assessment of carryover or the model terms used to handle period and sequence.

The study included two 2-week double-blind treatment periods separated by the 2-week washout. The treatment sequences differed: one began with FF/VI and the other with FP. During the treatment periods, each active regimen was paired with its matching placebo through the other inhaler, supporting masking despite different dosing schedules. The brief study description also reports a 4-week single-blind run-in on FP 250 mcg twice daily before the randomized treatment periods. Participants with symptomatic allergic rhinitis at screening could receive intranasal corticosteroids for up to four weeks, followed by repeat screening to determine eligibility.

Exercise challenges were conducted on a treadmill, with FEV1 assessed before exercise and serially after exercise. The primary endpoint was assessed at 12 hours post evening dose at Week 2 of each treatment period. The registry record describes additional exercise testing and secondary outcomes at 23 hours post evening dose, as well as other secondary measures. The original sample-size justification, detailed randomization procedure, and full statistical analysis plan 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: The study consisted of 4-week single-blind run-in, 2-week double-blind treatment period 1, 2-week single-blind wash out, 2-week double-blind treatment period 2 and 1-week Follow-up. A total of 163 participants were screened, 75 were randomized and 74 were included in Intent-To-Treat (ITT) Population who received at least 1 dose of trial medication.

Treatment Period 1 (2 Weeks)

Reasons for not completing this period:

Wash-out Period (2 Weeks)

Reasons for not completing this period:

Treatment Period 2 (2 Weeks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: ITT Population. Participants with non-missing covariates and data specific to endpoint 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 Maximal Percent Decrease in Forced Expiratory Volume in One Second (FEV1) Following Exercise Challenge at 12 Hours (Hrs) Post Evening Dose From Pre-exercise FEV1., measured over At Week 2 of treatment period 1 and 2.

The primary endpoint was maximal percent decrease in forced expiratory volume in one second (FEV1) following an exercise challenge at 12 hours post evening dose, measured from pre-exercise FEV1. FEV1 is the volume of air forcibly exhaled in the first second of a forced breath. In this study, participants completed a treadmill exercise challenge and had FEV1 measured before exercise and at 5, 10, 15, 30, 45, and 60 minutes afterward.

For each assessment, the maximum decrease was calculated from the pre-exercise value and the smallest FEV1 value recorded within one hour after the challenge. It was expressed as a percentage of pre-exercise FEV1. Thus, the endpoint captures the greatest observed post-exercise fall during the specified observation window, rather than the average change across all post-exercise measurements. A larger percentage decrease represents a larger measured fall from the pre-exercise value.

This endpoint is used because exercise-induced bronchoconstriction is defined in relation to airway response after exercise, and FEV1 provides a standardized spirometric measure of that response. The 12-hour timing evaluates the response at a specified interval after the evening dose, at the end of the 2-week treatment period. The result is specific to that challenge procedure, timing, and study population; it does not by itself describe all aspects of asthma control or longer-term outcomes.

7. Results Posted in the Registry

• FP 250 µg BID Via DISKUS + Placebo QD Via ELLIPTA: mean 16.71 versus 15.02 on control; difference 1.69 (95% CI -1.29 to 4.67), standardized effect d = 0.19; z-test p = 0.267.

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.

Maximal Percent Decrease in FEV1 Following Exercise Challenge at 23 Hrs Post Evening Dose From Pre-exercise FEV1.

• 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 250 µg BID Via DISKUS + Placebo QD Via ELLIPTA: mean 14.05 versus 11.90 on control; difference 2.15 (95% CI -0.72 to 5.02), standardized effect d = 0.25; z-test p = 0.142.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FP 250 µg BID Via DISKUS + Placebo QD Via ELLIPTA and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the assessment beyond the primary 12-hour maximal FEV1 decrease. They include maximal percent decrease at 23 hours post evening dose, the proportion with a 30-minute post-challenge FEV1 no more than 5 percent below pre-exercise FEV1 at 12 and 23 hours, and a weighted mean of percentage decrease over 0–60 minutes at those time points. These outcomes examine response at a later dosing interval, a threshold-based response at a specified post-challenge time, and the pattern of response across the observation window.

The posted numerical results available for the maximal percent decrease endpoint at 23 hours show least-squares means of 11.9 for FF/VI and 14.05 for FP. The sponsor-reported mixed-model mean difference is -2.15, with a 95% confidence interval from -4.31 to 0.01 and p = 0.051. The unadjusted recalculation expresses the comparison as FP minus FF/VI and gives 2.15, with a 95% confidence interval from -0.721 to 5.021 and p = 0.142. As with the primary result, the sponsor result and summary-based recalculation are not the same analysis.

The 23-hour result has a numerical direction similar to the primary endpoint when the treatment means are read as reported, but it should not be treated as independent confirmation. Both outcomes are related measures from the same study and participants, and the secondary analysis is not a replacement for the prespecified primary comparison. Numerical results for the other listed secondary outcomes are not reported in the registry record.

General statistical explanation: multiple outcomes and time points create multiple opportunities to observe a small p-value by chance. Unless multiplicity is controlled, individual secondary p-values are usually less conclusive than a prespecified primary result. The registry record does not report a multiplicity adjustment. Secondary findings are therefore most useful for describing the range and consistency of measured responses, while avoiding selective emphasis on one result.

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

• Maximal Percent Decrease in FEV1 Following Exercise Challenge at 23 Hrs Post Evening Dose From Pre-exercise FEV1.
• Proportion of Participants With a 30 Min Post-challenge FEV1 no More Than 5 Percent Lower Than Pre-exercise FEV1 Following the Exercise Challenge at 12 Hrs and 23 Hrs Post Evening Dose.
• Weighted Mean 0-60 Min for Percentage Decrease From Pre-exercise FEV1 Following Exercise Challenge at 12 Hrs and 23 Hrs Post Evening Dose.

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous, and the registry reports a least-squares mean for each treatment. A least-squares mean is a model-based estimate of the treatment mean after accounting for terms included in the statistical model. The registry record does not list the full model specification, so it is not possible to state which covariates, period terms, sequence terms, or other factors were included. The reported dispersion for each treatment mean is a standard error, which describes the uncertainty in the estimated mean rather than the spread of individual participant measurements.

What does the treatment difference represent?

The sponsor-reported analysis is a mixed models analysis of final values. Its mean difference is -1.69, with the comparison direction determined by the group order used in that analysis. The simple recalculation instead presents FP minus FF/VI and gives a mean difference of 1.69. The sign changes when the subtraction order changes; it does not, on its own, mean that the underlying comparison has changed. When reading any treatment difference, identify which treatment is subtracted from which and what outcome is being compared.

The recalculation uses the posted treatment means and standard errors to estimate an unadjusted difference and confidence interval. It is labeled approximate because the posted summaries do not provide the participant-level data or all details needed to reproduce a crossover model. General statistical explanation: a model using participant-level data can account for features of the design that a comparison of separate summary means cannot fully represent. In a crossover study, within-participant correlation and treatment period can affect the precision and estimated treatment contrast. The recalculated comparison should therefore be read as a supplementary summary-based analysis, not as an alternative fitted crossover model.

Why are confidence intervals important?

A confidence interval gives a range of values compatible with the observed data under the assumptions of the analysis. For the sponsor analysis, the 95% interval runs from -3.76 to 0.39. For the unadjusted recalculation, it runs from -1.294 to 4.674 in the opposite comparison direction. Both intervals include zero, the value corresponding to no mean difference. That does not prove there is no difference; it indicates that the estimates are not sufficiently precise to rule out zero under these analyses. The intervals also include values on either side of zero, so the data do not determine the direction with certainty.

The p-value measures how unusual data at least as incompatible with a null hypothesis would be if that null and the analysis assumptions were true. The sponsor reported p = 0.109, while the recalculated unadjusted comparison has p = 0.267. Neither should be interpreted as the probability that the null hypothesis is true or as a measure of the size or clinical importance of a difference. The two values differ because the analyses use different methods; the unadjusted value does not replace the model-based result.

What does over-dispersion mean in general?

General statistical explanation: for count outcomes, over-dispersion means that observed variability is greater than a simple model assumes. It can make standard errors too small if the extra variability is ignored. That issue is not the main one for this continuous FEV1 endpoint, and the registry record does not report an over-dispersion model. The relevant endpoint uncertainty is described through standard errors and confidence intervals for the continuous outcome.

How does the design affect interpretation?

General statistical explanation: a crossover study can be efficient because participants serve as their own comparison, but the analysis must account for repeated measurements within a participant and possible differences between treatment periods. A washout interval is intended to separate treatment periods, but the registry description alone does not establish whether carryover was absent. The registry record states that the sponsor used a mixed models analysis, but does not report its exact structure or assumptions. The original statistical plan and sample-size justification are not reported in the registry record.

The endpoint population is described as the ITT Population, comprising randomized participants who received at least one dose, with the primary analysis limited to participants with non-missing covariates and endpoint-specific data. This wording indicates that the endpoint analysis was not necessarily based on every randomized participant. The number and pattern of missing values, the missing-data handling method, and any sensitivity analyses are not reported in the registry record. These omissions limit an independent assessment of how missingness may have affected the estimate.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the available data and the analysis assumptions. The sponsor-reported 95% confidence interval for the primary mean difference is -3.76 to 0.39. It includes zero, and it extends to estimates on either side of zero. The interval therefore does not identify a single direction for the treatment difference with high certainty. The reported p-value, 0.109, is consistent with that uncertainty under the sponsor’s mixed-model analysis.

The unadjusted recalculation has a 95% confidence interval from -1.294 to 4.674 for FP minus FF/VI. This interval also includes zero and allows for a range of possible differences in either direction. The point estimate is 1.69, but the interval indicates that the estimate is not precise enough to treat that point value as the exact underlying difference. The recalculated interval is based on posted summary statistics and should not be confused with the sponsor’s model-based interval.

General statistical explanation: a confidence interval is not a range containing a fixed proportion of individual participant outcomes, nor does it assign a probability to the true effect after the data have been observed. It describes uncertainty in the estimated contrast under the statistical procedure and its assumptions. A wider interval generally indicates less precision, while a narrower interval indicates more precision. Precision depends on factors such as variability, the amount of information, and the analysis design.

The registry reports standard errors of 1.058 and 1.095 for the primary treatment means. These quantify uncertainty around the separate least-squares mean estimates, not the full participant-to-participant spread. In a crossover design, the uncertainty of the treatment contrast also depends on the relationship between repeated observations within participants and on the model used. The registry record does not report enough detail to independently determine how those aspects contribute to the sponsor’s confidence interval.

Neither interval establishes equivalence. A conclusion of equivalence would require a prespecified margin and an analysis designed to assess whether the plausible treatment difference falls within that margin. Such a margin is not reported in the registry record. The numerical findings should therefore be read as estimates with uncertainty, rather than as proof of no difference.

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 for a two-arm comparison, not total participants and not total events. The assumptions listed for these planning illustrations are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set at the stated fraction of the observed effect: 100%, 75%, or 50%. These are planning assumptions for the illustrations, not the original assumptions used to design this trial. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect if that effect is the true one and the planning assumptions hold. The 90% power column gives the corresponding illustrative number per arm for a 90% chance. Power is a design property under assumed conditions, not a measure of how likely the observed result is to be correct.

The displayed figures increase as the target effect gets smaller. This is the usual planning relationship: a smaller difference is harder to distinguish from random variation, so more participants are needed to achieve the same planned power, all else equal. For the primary endpoint, the illustrations use the observed effect from the summary-statistic recalculation. Because the observed estimate is uncertain, these scenarios should not be treated as a guarantee that a future study would detect that effect.

This is not observed power. Observed power is not a substitute for examining the estimated effect and its confidence interval. The planning figures are hypothetical sample-size illustrations based on the stated assumptions, not results of the randomized comparison and not evidence about whether the observed treatment difference is important.

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 = 1.690; pooled standard deviation σ = 8.974.
2. n = 2 × (1.96 + 0.842)² × 8.974² / 1.690² = 442.6, rounded up to 443 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 <- 1.69                      # observed difference in means
sigma <- 8.97374655053756                     # 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(2730351)
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 = 443 (80% power), 593 (90% power)
 75% of observed effect: n per arm = 787 (80% power), 1,054 (90% power)
 50% of observed effect: n per arm = 1,771 (80% power), 2,371 (90% power)
power.t.test: 443.6 
Simulated power at n = 443 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’s own reported primary analysis is a mixed models analysis of final values. It reports a mean difference of -1.69, a 95% confidence interval from -3.76 to 0.39, and p = 0.109. The treatment means reported for the endpoint are 15.02 for FF/VI and 16.71 for FP. The sign of a difference depends on the order of subtraction; the sponsor’s reported direction is opposite to the FP-minus-FF/VI direction used for the unadjusted recalculation.

The recalculation from the posted summary statistics gives a mean difference of 1.69, a confidence interval from -1.294 to 4.674, and an unadjusted p-value of 0.267. It is a simple summary-based calculation and does not reproduce the sponsor’s mixed model. A crossover analysis can use information about repeated observations and the design that is not recoverable from the posted treatment summaries alone. The registry record does not report enough detail about the model to explain every difference between the two intervals and p-values.

The recalculation is therefore best read as a check on the direction and approximate scale of the comparison, not as a competing trial analysis. The sponsor’s analysis is the reported model-based result. Both analyses have confidence intervals that include zero, but their estimates and uncertainty should be interpreted according to their distinct methods rather than combined or treated as interchangeable.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists one primary endpoint and three secondary outcomes. The primary endpoint is maximal percent decrease in FEV1 after exercise at 12 hours post evening dose. The secondary outcomes include the corresponding maximal decrease at 23 hours, a threshold-based 30-minute response, and a weighted mean response across 0–60 minutes at 12 and 23 hours. The record reports numerical results for the primary endpoint and for the 23-hour maximal-decrease outcome; numerical results for the other listed secondary outcomes are not reported in the registry record.

When several endpoints, time points, or comparisons are examined, the chance of at least one apparently unusual result can increase. General statistical explanation: multiplicity procedures address this by adjusting how evidence is evaluated across a family of tests or by specifying a hierarchy of analyses. Such procedures can make statistical claims more conservative, but the appropriate approach depends on the analysis plan. The registry record does not report whether multiplicity was controlled, how the primary and secondary hypotheses were ordered, or whether any adjustment was prespecified.

The record states that the primary analysis population was the ITT Population, defined as randomized participants who received at least one dose, and that participants with non-missing covariates and endpoint-specific data were analyzed. This makes the endpoint analysis dependent on availability of the required observations. The number of missing endpoint values, reasons for missingness, and the handling of missing data are not reported in the registry record. No sensitivity analyses for missing data are described in the information available.

For a crossover study, interpretation also depends on how the analysis accounts for treatment sequence, period, repeated measurements within participants, and possible carryover. The registry identifies the sponsor method as mixed models analysis but does not report the full model or its assumptions. The 2-week washout is described, but the record does not report a carryover assessment. The original sample-size justification and detailed statistical analysis plan are not reported in the registry record. These missing details limit independent evaluation of the analysis choices and the robustness of the results.

16. Safety Results

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

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroenteritis (1.4%).

The serious adverse event figures are reported separately for the two treatment regimens. In the FF/VI period, the number at risk for serious adverse events was 73 and the number affected was 1; in the FP period, the number at risk was 72 and the number affected was 0. The registry lists gastroenteritis at 1.4% among the serious adverse event terms. Deaths were reported as 0 in each treatment group.

For other, non-serious adverse events, the number at risk was 73 with 5 affected in the FF/VI group, and 72 with 4 affected in the FP group. These are descriptive counts, not estimates of a causal difference. The study used a crossover design, so treatment-period summaries are not equivalent to counts from separate parallel groups of distinct participants. The group denominators should not be combined.

Adverse event counts do not by themselves show whether an event was caused by a treatment, and the counts are too limited to establish a comparative safety profile. The registry record does not provide additional detail in these figures about event timing, severity beyond serious versus other events, or participant-level recurrence. These results describe the safety information posted for this study and should be interpreted in light of the study’s size and design.

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

The primary result is an estimate of the difference between FF/VI and FP in maximal percent decrease in FEV1 after an exercise challenge at 12 hours post evening dose, at the end of the 2-week treatment periods. The sponsor-reported mixed-model analysis gives a mean difference of -1.69, with a 95% confidence interval from -3.76 to 0.39 and p = 0.109. The unadjusted recalculation gives the comparison in the reverse direction, with a mean difference of 1.69, a 95% confidence interval from -1.294 to 4.674, and p = 0.267.

These estimates do not establish a statistically clear difference under the reported analyses. They also do not prove that the treatments are identical. The confidence intervals include zero and allow for values in both directions, so the findings remain uncertain about the direction and size of the underlying mean difference. The registry record does not report a prespecified equivalence or non-inferiority margin, and the results should not be described as demonstrating equivalence or non-inferiority.

The outcome is specific to exercise-induced change in FEV1 at a defined time after dosing. It does not directly measure symptoms, everyday activity, asthma exacerbations, long-term control, or outcomes beyond the study’s treatment periods. The study used a crossover design with a 2-week washout, and its results depend on the model and assumptions used to analyze repeated treatment periods. The registry record does not provide the complete model specification, missing-data details, or multiplicity plan.

The secondary findings add context, but they do not remove the uncertainty in the primary result. Numerical results for the 23-hour maximal decrease are reported, while numerical results for other listed secondary outcomes are not reported in the registry record. The safety counts are also descriptive and do not establish a comparative safety conclusion. Overall, the record supports a cautious reading of the measured outcomes in this study population and setting, not a broad claim about all people with asthma or all treatment circumstances.

18. Why This Trial Matters Statistically

This trial raises several statistical issues that are common in clinical research. First, the crossover design allows the treatments to be compared across treatment periods within participants, but it requires analysis that respects repeated measurements and treatment order. The registry reports a mixed models analysis, yet does not provide the full model specification. That makes the sponsor’s estimate available for interpretation, while limiting independent reproduction of the analysis.

Second, the reported sponsor analysis and a summary-statistic recalculation have different confidence intervals and p-values. Their treatment-difference signs use opposite comparison directions, and the methods differ: one is a mixed model and the other is an unadjusted calculation from group summaries. This illustrates why a numerical contrast cannot be interpreted without knowing the estimand, subtraction order, and statistical method.

Third, both primary confidence intervals include zero. This directs attention away from a binary significant/not-significant label and toward the estimate’s precision and the range of differences compatible with the data. A non-significant result does not establish no effect, while a numerical difference does not establish a meaningful or important difference. No clinical threshold for interpreting the size of the endpoint difference is reported in the registry record.

Finally, the listed secondary outcomes broaden the assessment across time and outcome definitions, but their interpretation depends on what was prespecified and whether multiplicity was handled. The multiplicity plan is not reported. Taken together, the record shows why careful interpretation requires attention to design, model, uncertainty, outcome selection, and the distinction between trial-reported analysis and post hoc summary-based recalculation.

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 registry record leaves important details about the primary analysis unspecified. It identifies a mixed models analysis but does not report the model terms, covariance structure, treatment sequence and period handling, or assumptions used to address potential carryover. Although a 2-week washout is described, the record does not report an assessment of carryover. These omissions make it difficult to reproduce the sponsor’s result or evaluate the sensitivity of the estimate to alternative modeling choices.

The primary endpoint analysis included participants with non-missing covariates and endpoint-specific data, but the number and pattern of missing values and the missing-data method are not reported in the registry record. It is therefore not possible to assess whether missing observations could have affected the estimated treatment difference. The original sample-size justification and the trial’s detailed statistical analysis plan are also not reported.

Multiplicity handling is not described, despite the primary and secondary outcome measures spanning more than one time after dosing and more than one outcome definition. Numerical secondary results are not reported for all of the listed secondary outcomes. This limits a full assessment of the consistency of the secondary findings and how they were interpreted relative to the primary endpoint.

The recalculated primary comparison relies on summary statistics and is unadjusted; it cannot fully represent the crossover design or reproduce the sponsor’s mixed model. The registry record also does not state a clinical threshold for judging the importance of a difference in maximal percent decrease in FEV1. Finally, the endpoint is limited to a measured response following a treadmill exercise challenge at specified post-dose times and does not capture all dimensions of asthma outcomes.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Crossover Study Comparing Fluticasone Furoate (FF)/Vilanterol (VI) Once Daily Versus Fluticasone Propionate (FP) Twice Daily in Subjects With Asthma and Exercise-Induced Bronchoconstriction (EIB) — NCT02730351.
• Registry record last updated 2019-07-16; status last verified 2019-07.
• Results first posted 2017-10-13.
• 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

NCT02730351 was a completed Phase 4 randomized, double-blind, double-dummy, crossover study sponsored by GlaxoSmithKline. It compared FF/VI 100/25 mcg once daily with FP 250 mcg twice daily in adolescent and adult participants with asthma and exercise-induced bronchoconstriction. The registry lists enrollment as 75 and describes two 2-week treatment periods separated by a 2-week washout.

The primary endpoint was maximal percent decrease in FEV1 following exercise challenge at 12 hours post evening dose. The sponsor-reported mixed-model mean difference was -1.69, with a 95% confidence interval from -3.76 to 0.39 and p = 0.109. The summary-statistic recalculation is unadjusted and uses the opposite comparison direction. Both confidence intervals include zero. The record does not report the full analysis plan, missing-data details, or multiplicity approach, which limits independent assessment of the results.