Safety and Efficacy of GW685698X an Inhaled Corticosteroid Once Daily and Twice Daily for the Treatment of Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Efficacy of GW685698X an Inhaled Corticosteroid Once Daily and Twice Daily for the Treatment of Asthma (NCT00766090), a randomized phase 2 study. The primary outcome is Trough Forced Expiratory Volume in One Second (FEV1) at Day 28 of the Relevant Treatment Period.

2. Clinical Question

The study was designed as a randomized, double-blind crossover study in people with asthma. A crossover design evaluates treatments across treatment periods, rather than assigning each participant to only one treatment throughout. This can support within-participant comparisons, but interpretation depends on design details such as treatment sequences and any handling of period effects. The registry record identifies a period term in the primary ANCOVA but does not report treatment sequences or further design details.

3. Trial Design

This Phase 2 study was randomized, double-blind and used a crossover model. The registry record describes a multi-centre study of adults and adolescents with asthma. It lists enrollment of 190 and status as completed. The recorded study start was 2008-10, and primary completion was 2009-03.

The official title identifies the central comparison as GW685698X 200mcg once daily versus 100mcg twice daily. In the results, these treatments are labelled FF 200 µg OD and FF 100 µg BID. The record also contains placebo and FP treatment results. The registry does not report the sequence or allocation schedule for the different treatments, nor does it provide details about any washout between periods. Those details should not be inferred from the crossover label alone.

The primary endpoint was trough FEV1 measured at Day 28 of the relevant treatment period, with the stated timeframe extending up to Study Day 112. The registry describes three 28-day treatment periods for several secondary outcomes. For the primary outcome, it reports an ANCOVA with treatment, period, sex and age as fixed effects, participants as a random effect, and period baseline measurement included as part of a bivariate response. The primary analysis population included randomized participants who received at least one dose of study medication.

The study’s stated aim was to compare once- and twice-daily GW685698X in asthma. The official title characterizes the comparison as non-inferiority, but the non-inferiority margin and original sample-size justification are not reported in the registry record. The registry lists adverse events, urinary cortisol, oropharyngeal candidiasis, blood pressure, heart rate and withdrawals due to worsening asthma among the secondary outcomes.

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: Eligible participants (par.) at screening entered a 14-day Run-in Period. Par. were then randomized to 1 of 12 sequences: 6 had placebo and two doses of fluticasone furoate (FF), and 6 had placebo and two doses of fluticasone proprionate (FP) (allocation ratio of 7:2 \[FF:FP\]). 320 par. were screened and 190 were randomized.

Only the first 6 of 12 groups are shown.

Treatment Period 1 (28 Days)

Reasons for not completing this period:

Washout Period 1 (14 Days)

Reasons for not completing this period:

Treatment Period 2 (28 Days)

Reasons for not completing this period:

Washout Period 2 (14 Days)

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

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 Trough Forced Expiratory Volume in One Second (FEV1) at Day 28 of the Relevant Treatment Period, measured over Day 28 of the relevant treatment period (up to Study Day 112).

The primary endpoint was trough forced expiratory volume in one second (FEV1), measured in liters at Day 28 of the relevant treatment period. FEV1 is the maximal amount of air that can be forcefully exhaled in one second. The measurement was taken electronically by spirometry. Trough FEV1 was defined as the evening pre-dose, pre-rescue bronchodilator measurement on Day 28.

FEV1 is a continuous measure of lung function. Using it as an endpoint allows the analysis to compare average measured values between treatments, rather than only whether participants crossed a threshold. The registry reports least-squares means and standard errors for treatment groups. Least-squares means are model-based estimates that account for the specified terms in the analysis; they are not simply unadjusted averages of all recorded measurements.

The timing at the end of a treatment period makes this a treatment-period endpoint, rather than a measure of immediate response after a dose. The primary analysis used ANCOVA, with treatment and period among its fixed effects, participants as a random effect, and period baseline included as part of a bivariate response. This modelling approach reflects the repeated treatment-period structure described for the crossover study.

The official title frames the principal question as non-inferiority of once-daily versus twice-daily GW685698X. A non-inferiority conclusion requires a prespecified margin and an appropriate comparison against that margin. The margin is not reported in the registry record, so the clinical meaning of the sponsor’s estimate cannot be fully assessed against a stated non-inferiority threshold from the record alone.

7. Results Posted in the Registry

• FF 200 µg OD: mean 2.71 versus 2.60 on control; difference 0.11 (95% CI -0.01 to 0.23), standardized effect d = 0.19; z-test p = 0.079.
• FF 100 µg BID: mean 2.70 versus 2.60 on control; difference 0.10 (95% CI -0.02 to 0.22), standardized effect d = 0.17; z-test p = 0.114.
• FP 200 µg OD: mean 2.69 versus 2.60 on control; difference 0.09 (95% CI -0.05 to 0.22), standardized effect d = 0.16; z-test p = 0.201.
• FP 100 µg BID: mean 2.74 versus 2.60 on control; difference 0.13 (95% CI -0.00 to 0.27), standardized effect d = 0.24; z-test p = 0.055.

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.

Number of Participants Who Withdrew Due to Worsening of Asthma During the Three Treatment Periods

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • FP 200 µg, FP 100 µg, and Placebo Via DISKUS: 2.3% (1/43) versus 3.4% (5/147) on control; risk difference -1.1 percentage points (95% CI -6.4 to 4.3), risk ratio 0.68 (0.08–5.70); unadjusted two-proportion z-test p = 0.723.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between FP 200 µg, FP 100 µg, and Placebo Via DISKUS and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes spanning adverse events, serious adverse events, urinary cortisol, oropharyngeal candidiasis, blood pressure, heart rate and withdrawal due to worsening asthma. This range includes safety measures, physiological measurements and a treatment-discontinuation outcome. Secondary outcomes can add context to the primary FEV1 result, but they address different questions and do not independently settle the primary non-inferiority question.

Quantitative results are posted for withdrawal due to worsening asthma, while results for the other listed secondary endpoints are not reported in the registry record in the registry record for this analysis. The registry record therefore does not support a complete assessment of the overall secondary-outcome pattern. Absence of a posted result is not evidence that an outcome was measured with no events or no difference.

The withdrawal summary compares treatment sequences that include FF and placebo via DPI with sequences that include FP and placebo via DISKUS. This is not the same direct contrast as the primary FF once- versus twice-daily comparison. Its interpretation should remain tied to the outcome definition and groups recorded, rather than being treated as a substitute for the primary endpoint.

Secondary results usually carry less weight than a prespecified primary result because they may involve more comparisons, smaller event counts, or different analysis populations. When many outcomes are tested, some results can appear unusual by chance alone unless multiplicity is addressed. The registry’s multiplicity adjustment plan is not reported. No adjustment should be assumed. Consequently, secondary findings are best read as supportive or exploratory context rather than decisive evidence, especially when the analysis plan and complete endpoint results are not reported.

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

• Number of Participants With Any Adverse Event (AE) and Any Serious Adverse Event (SAE) Throughout the Three 28-day Treatment Periods
• 24-hour Urinary Cortisol Excretion at Day 28 of the Relevant Treatment Period
• Number of Participants With Evidence of Oropharyngeal Candidiasis at Day 0 and Day 28 of the Relevant Treatment Period
• Systolic and Diastolic Blood Pressure at Day 0 and Day 28 of the Relevant Treatment Period
• Heart Rate at Day 0 and Day 28 of the Relevant Treatment Period
• Number of Participants Who Withdrew Due to Worsening of Asthma During the Three Treatment Periods

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: trough FEV1 is recorded in liters. The registry reports treatment-group least-squares means with standard errors. A least-squares mean is an estimate from a statistical model, adjusted for the factors included in that model. It differs from a simple arithmetic mean when the model accounts for design features or covariates. The standard error describes the uncertainty in an estimated mean; it is not the spread of individual participants’ measurements.

The sponsor’s primary analysis used ANCOVA, or analysis of covariance. In general, ANCOVA estimates treatment differences while accounting for other variables specified in the model. The registry says the model included treatment, period, sex and age as fixed effects. It treated participants as a random effect and included period baseline measurement as part of a bivariate response. In general, fixed effects represent specified features whose effects are estimated directly, while a random effect can account for participant-level variation. Including period in the model is relevant to a crossover design, where outcomes are recorded across treatment periods.

The main sponsor-reported comparison between FF 200 µg OD and FF 100 µg BID is a mean difference in final values. Its reported estimate is 0.011, with a 95% confidence interval from -0.035 to 0.056 and p = 0.641. A mean difference expresses the estimated separation between the two treatment results on the FEV1 scale. The confidence interval gives a range of values compatible with the data and the statistical model at the stated confidence level, under the assumptions of that analysis. Because the interval includes zero, it is compatible with no difference as well as with differences in either direction within its limits.

A p-value describes how unusual the observed data, or more extreme data, would be under a specified null hypothesis and model. It is not the probability that the null hypothesis is true, nor does it measure the size or clinical importance of a difference. In a non-inferiority study, the central question is not simply whether a conventional test finds a difference. The estimated treatment contrast and its confidence interval need to be assessed against the non-inferiority margin. That margin is not reported in the registry record.

The supplementary unadjusted recalculations use posted arm summaries to estimate differences and intervals. The standard deviations used in those calculations are approximate, as indicated in the comparison details. These calculations do not account for the full crossover model described by the sponsor, including its treatment and period terms, participant random effect, and baseline structure. For that reason, the recalculated comparisons are not substitutes for the sponsor’s ANCOVA results. The discrepancy flag also indicates that the sponsor’s own analysis takes precedence.

In general, crossover studies can make within-participant comparisons, because a participant may contribute observations under more than one treatment. This can reduce the influence of stable differences between participants, but the advantage depends on the design and analysis. Period effects, treatment sequence, and possible carryover can matter. The registry describes inclusion of period in the ANCOVA, but treatment sequence and any carryover assessment are not reported in the registry record. It is therefore not appropriate to assume how those issues were handled beyond the stated model.

The treatment comparisons against placebo are also reported using ANCOVA. Their estimates and intervals are model-based and should be interpreted within that analysis. The statistical significance of a comparison does not establish the size of a clinically important effect. No threshold for clinically important FEV1 change is reported in the registry record.

The simple recalculations include p-values and planning illustrations based on the observed summary effects. Those calculations are distinct from the primary sponsor analysis and from the study’s original design assumptions. The planning illustrations use a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. They are hypothetical design calculations, not evidence about the trial’s observed power. The original sample-size assumptions and justification are not reported in the registry record.

For secondary binary outcomes, general statistical interpretation differs from that for a continuous endpoint. Counts describe how many participants had an event, while a risk difference compares event proportions between groups. Such comparisons can be imprecise when events are uncommon or group sizes are limited. Any unadjusted secondary p-values or recalculations should be treated cautiously, particularly when multiple outcomes are assessed. The registry’s multiplicity plan is not reported.

11. Confidence Intervals and Precision

The sponsor-reported comparison of FF 200 µg OD with FF 100 µg BID has an estimate of 0.011 liters and a 95% confidence interval from -0.035 to 0.056. The interval crosses zero, so the reported data are compatible with a small difference in either direction, as well as with no difference under the fitted model. The range also shows that the estimate is not precise enough to pin down a single treatment contrast.

A confidence interval is not a guarantee that the true effect lies inside its limits. In general, it describes the range of estimates that are compatible with the observed data and the assumptions of the statistical model at the stated confidence level. Its width is informative about precision: narrower intervals indicate less uncertainty about the estimated contrast, while wider intervals indicate more. Interpretation also depends on whether the model reflects the study design and whether the interval is judged against a clinically meaningful threshold.

Here, the sponsor’s model-based interval is the relevant reported interval for the primary FF schedule comparison. The unadjusted recalculation gives a different estimate and interval because it is based on posted summary statistics and does not reproduce the crossover ANCOVA. With a true discrepancy flagged, the sponsor’s own analysis takes precedence. The recalculated interval should not be used to replace or overrule the registry’s sponsor analysis.

The official objective is non-inferiority, but the margin needed to judge the interval against an acceptable difference is not reported in the registry record. Thus, the confidence interval can describe statistical precision, but it cannot establish from the registry record whether the result falls within a specified non-inferiority boundary. No clinical-importance threshold is reported either.

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 expressed as participants per arm, not as a total across arms. They illustrate the group size that a hypothetical two-arm comparison would require under the stated assumptions. The assumptions 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 as a stated fraction of the observed effect. These calculations are planning illustrations based on the observed effect, not the trial’s own original design assumptions.

The 80% power column represents the participant count per arm associated with an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one and the model assumptions held. The 90% power column uses a higher target chance of detection and therefore generally calls for more participants per arm. These percentages describe prospective planning targets, not the probability that the trial’s conclusion is correct.

The rows for 100%, 75% and 50% of the observed effect show what happens when the target effect becomes smaller. Smaller effects are harder to distinguish from random variation, so the planning figures require more participants per arm. This relationship is a general feature of sample-size planning, not evidence that a particular trial actually had the stated power.

The original sample-size justification and design assumptions are not reported in the registry record. These values are not observed power and should not be read as a retrospective statement about how likely the completed trial was to find a result. For a crossover study, the simple planning assumptions may also differ from the study’s actual design and analysis structure. The illustrations are useful for understanding how assumed effect size and desired power influence planning, but they do not reconstruct the trial’s protocol.

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 = 0.109; pooled standard deviation σ = 0.565.
2. n = 2 × (1.96 + 0.842)² × 0.565² / 0.109² = 422.3, rounded up to 423 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 <- 0.109                      # observed difference in means
sigma <- 0.565349856338125                     # 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(766090)
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 = 423 (80% power), 566 (90% power)
 75% of observed effect: n per arm = 751 (80% power), 1,006 (90% power)
 50% of observed effect: n per arm = 1,690 (80% power), 2,262 (90% power)
power.t.test: 423.3 
Simulated power at n = 423 per arm: 0.803 (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 ANCOVA results for the primary FEV1 comparisons. For the direct FF schedule contrast, the sponsor reports a mean difference of 0.011, a 95% confidence interval from -0.035 to 0.056, and p = 0.641. These are model-based results from the analysis described in the record.

The unadjusted recalculations use the posted treatment-group summaries and approximate standard deviations. They yield a different estimate and confidence interval from the sponsor’s analysis. They are not a reconstruction of the ANCOVA, which accounts for treatment, period, sex and age, participant-level random effects, and period baseline measurement. In a crossover study, omitting the stated model structure can change the estimated contrast and its uncertainty.

Because a discrepancy is flagged, the sponsor’s own analysis takes precedence. The recalculations may help illustrate an unadjusted contrast based on the summary statistics, but should not be used to revise the reported trial result. The registry record does not explain the source of the discrepancy. It also does not report the non-inferiority margin, so neither the recalculation nor the sponsor’s p-value alone establishes whether the study met a specified non-inferiority criterion.

15. Multiplicity, Missing Data and Analysis Populations

The registry record reports several secondary outcomes in addition to the primary FEV1 endpoint. Testing multiple outcomes can raise the chance of apparently notable findings occurring by chance. Statistical methods can address this through prespecified approaches such as adjusting significance thresholds or controlling a defined error rate. Whether such an approach was planned or applied is not reported in the registry record.

The primary comparison is presented as a non-inferiority question, but the non-inferiority margin is not reported in the registry record. Without that margin, the reported confidence interval cannot be evaluated against the trial’s stated acceptance boundary. The record also does not provide the original sample-size justification, so the rationale for the planned enrollment cannot be assessed from the available information.

The primary analysis population is described as randomized participants who received at least one dose of study medication. This definition is reported, but the registry record does not describe how missing primary endpoint measurements were handled, how many measurements were missing, or whether sensitivity analyses were performed. It also does not report details of any per-protocol analysis. These omissions matter because non-inferiority conclusions can be sensitive to population definitions and missing-data assumptions.

The record identifies a crossover model and says the ANCOVA included a period effect and participant random effect. It does not report treatment sequence details, any assessment of carryover, or how incomplete treatment periods were handled. These are relevant considerations in general for crossover analyses, but no specific handling should be inferred from the information recorded.

The available secondary results are incomplete across the listed outcomes. For outcomes whose numerical results are absent, results are not reported in the registry record. This limits assessment of the consistency of secondary evidence and the extent to which multiplicity may affect interpretation. The record also does not explain the flagged discrepancy between the sponsor analysis and unadjusted recalculations.

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 non-serious adverse event terms

The posted serious adverse event figures show zero serious adverse events in each listed treatment group: placebo, FF 200 µg OD, FF 100 µg BID, FP 200 µg OD and FP 100 µg BID. These are the reported counts for the groups and periods described in the registry record. The event count should be read alongside the corresponding at-risk group counts in the posted safety results.

Zero reported serious adverse events in these groups does not establish that serious harms are impossible or that risk is absent. A trial’s ability to detect uncommon events depends on its size, duration and follow-up, and the registry record does not provide enough information to quantify that ability. The death fields are null; deaths are not reported in the registry record, rather than being documented as zero.

The safety figures are descriptive and do not establish a comparative safety conclusion. The record also lists other adverse events, but those counts should not be confused with serious adverse events. The trial’s crossover structure and the reported treatment-period context should be kept in mind when interpreting event summaries. These results are not medical advice and should not be generalized beyond what the registry reports.

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

The primary result describes the estimated difference in trough FEV1 between the once-daily and twice-daily FF schedules at Day 28 of the relevant treatment period. The sponsor’s ANCOVA estimate is 0.011 liters, with a 95% confidence interval from -0.035 to 0.056 and p = 0.641. The estimate is close to zero, while the interval includes values on both sides of zero. It therefore does not demonstrate a statistically clear difference between the schedules in this analysis.

That finding is not proof that the schedules are identical. A failure to show a difference can reflect a small true difference, uncertainty in the estimate, or both. Nor does a non-significant difference test by itself demonstrate non-inferiority. The official title states a non-inferiority objective, but the margin required to assess that objective is not reported in the registry record. The reported confidence interval cannot be judged against an unreported boundary.

The placebo comparisons reported by the sponsor are separate analyses and should not be substituted for the direct comparison of dosing schedules. Likewise, the simple recalculations based on treatment-group summaries are not equivalent to the sponsor’s crossover ANCOVA. Because the discrepancy flag is true, the sponsor’s own analysis takes precedence.

The secondary outcomes offer additional domains of observation, but results are not reported in the registry record for several listed measures. The safety counts and withdrawal summary do not answer the primary lung-function question, and the record does not report a multiplicity plan. The findings therefore describe the analyses and results registered, not every possible consequence of treatment.

These statistical results do not determine what treatment is appropriate for an individual. They also do not establish a clinically important effect, because a threshold for clinical importance is not reported in the registry record. Interpretation is bounded by the available analysis details, the reported endpoints and the uncertainty in the estimates.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a crossover design with a non-inferiority objective. The comparison asks whether once-daily administration can be judged acceptably close to twice-daily administration, rather than simply asking whether the treatments differ. That distinction matters: a non-significant test for difference is not enough to establish non-inferiority. Interpretation requires a defined margin and an interval assessed against it, while the margin is not reported in the registry record.

The crossover model also makes the analysis structure important. The sponsor’s ANCOVA includes treatment and period effects, participant as a random effect, and baseline measurement as part of a bivariate response. Those design features are not reflected in simple calculations from treatment-group summaries. The flagged difference between the sponsor analysis and the recalculations illustrates why model-based results should not be casually replaced by simpler estimates.

The registry reports several clinically distinct secondary outcomes, but complete numerical results are not available for all of them. Multiplicity handling is also not reported. These gaps limit how confidently secondary findings can reinforce or qualify the primary comparison.

More broadly, the record demonstrates that precision, analysis population and prespecified decision criteria all matter when interpreting a trial. An estimate and p-value alone do not answer a non-inferiority question, and a confidence interval is only meaningful for that question when the relevant margin is known. The statistical interpretation must remain tied to the analysis that the sponsor reported and to the limitations of the registry record.

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 does not report the non-inferiority margin, even though the official title describes a non-inferiority objective. This prevents direct assessment of the primary estimate against the intended decision boundary. The original sample-size justification and design assumptions are also not reported, so the planned precision and power rationale cannot be evaluated.

The sponsor’s reported ANCOVA and unadjusted recalculations differ, and the registry record does not explain why. The sponsor analysis takes precedence, but the discrepancy limits how confidently summary-statistic recalculations can be used as a cross-check. The recalculations use approximate standard deviations and do not reproduce the crossover model.

Some crossover details are not reported, including treatment sequences and any washout or carryover assessment. The primary analysis description includes period and participant effects, but does not resolve all questions about incomplete periods or missing measurements. Missing-data handling, sensitivity analyses and a per-protocol analysis are not reported in the registry record.

Several secondary outcomes are listed without numerical results in the information available for this analysis, and the multiplicity plan is not reported. The death fields are null, so deaths are not reported in the registry record rather than established as absent. Finally, no clinical-importance threshold for FEV1 is reported. These limitations restrict interpretation of the primary objective, the broader secondary evidence and the clinical meaning of the estimated differences.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Safety and Efficacy of GW685698X an Inhaled Corticosteroid Once Daily and Twice Daily for the Treatment of Asthma — NCT00766090.
• Registry record last updated 2016-12-08; status last verified 2016-10.
• Results first posted 2013-08-07.
• 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

NCT00766090 is a completed Phase 2 randomized, double-blind crossover study of inhaled treatment in adults and adolescents with asthma. The registry lists enrollment of 190 and records a study start of 2008-10 and primary completion of 2009-03.

The primary endpoint was trough FEV1 in liters at Day 28 of the relevant treatment period. The sponsor’s ANCOVA reports a mean difference of 0.011 for FF 200 µg OD versus FF 100 µg BID, with a 95% confidence interval from -0.035 to 0.056 and p = 0.641. The non-inferiority margin is not reported in the registry record.

Unadjusted recalculations differ from the sponsor analysis; the sponsor’s own analysis takes precedence. The registry lists multiple secondary and safety outcomes, but complete numerical results and the multiplicity plan are not reported in the registry record.