Efficacy and Safety Study in Subjects With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety Study in Subjects With Asthma (NCT00980200), a randomized phase 2 study. The primary outcome is Change From Baseline in Trough (Pre-bronchodilator and Pre-dose) FEV1 on Day 7 of the Treatment Period.

2. Clinical Question

3. Trial Design

This was a phase 2, randomized, double-blind, placebo-controlled, multicenter crossover study sponsored by GlaxoSmithKline. The registry lists enrollment of 75 participants. The study started in 2009-09, reached primary completion in 2010-01, and has a completed status.

Rather than assigning each participant to just one treatment for the whole trial, the crossover design used five treatment periods. Sequences varied the order of placebo and the four GW642444 dose schedules. This structure permits comparisons that use measurements from the same participant across treatment periods, while also requiring attention to period effects and the treatment sequence. Details such as washout intervals, adherence procedures, and the rationale for the particular sequence allocation are not reported in the registry record.

The study was double-blind, but the registry record does not describe which trial personnel were masked or how masking was maintained. Randomization is reported; the randomization procedure and allocation concealment details are not reported in the registry record. The planned sample-size justification and the assumptions used in the trial’s original design are also not reported in the registry record.

The primary endpoint was change from baseline in trough pre-bronchodilator, pre-dose FEV1 on Day 7 of a treatment period. The analysis population included randomized participants who received at least one dose, subject to the registry’s stated assumption about whether medication was received. The reported treatment-period sample counts were 74.0 for placebo, 73.0 for 6.25 µg QD, 74.0 for 6.25 µg BID, 73.0 for 12.5 µg QD, and 73.0 for 25 µg QD. A crossover trial’s treatment-period counts are not a count of distinct people assigned to separate parallel groups.

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 was a multi-centre, double-blind, placebo-controlled, five-period cross-over study. Following the 7(+7)-day RIP, eligible participants were randomized to 1 of 5 sequences of GW642444 at doses of 6.25 micrograms (µg) once daily (QD), 6.25 µg twice daily, 12.5 µg QD, 25 µg QD, and placebo.

7-day Treatment Period 1

Reasons for not completing this period:

7-day Washout Period 1

7-day Treatment Period 2

7-day Washout Period 2

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 trial medication. Randomized participants were assumed to have received trial medication unless definitive evidence to the contrary existed. Only participants available at the indicated time point 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 Trough (Pre-bronchodilator and Pre-dose) FEV1 on Day 7 of the Treatment Period, measured over Baseline and Day 7 of the treatment period (up to Study Day 63).

The primary endpoint is change from baseline in trough FEV1 on Day 7 of each treatment period, measured in liters. FEV1 is the maximal amount of air that can be forcefully exhaled in one second and is used as a continuous measure of pulmonary function. Change was defined as the Day 7 value minus the baseline value for that treatment period.

Trough FEV1 was defined as the mean of the two last scheduled measurements at the Day 7 clinic visit. These were taken 11 and 12 hours after the morning dose, or 23 and 24 hours after the evening dose. The endpoint therefore targets lung function measured near the end of the dosing interval, rather than the highest value recorded after dosing.

Using a continuous endpoint preserves the size and direction of measured change, rather than reducing the result to a yes-or-no outcome. The registry reports adjusted least-squares means and standard errors for treatment groups, with comparisons analyzed using a mixed-model ANCOVA. This approach accounts for listed treatment and period terms and includes participant-level variation. The endpoint is a measured lung-function outcome; it does not, on its own, describe symptoms, daily functioning, longer-term outcomes, or individual treatment response.

7. Results Posted in the Registry

• GW642444 6.25 µg QD: mean 0.15 versus 0.06 on control; difference 0.09 (95% CI 0.03 to 0.16), standardized effect d = 0.50; z-test p = 0.003.
• GW642444 6.25 µg BID: mean 0.20 versus 0.06 on control; difference 0.14 (95% CI 0.08 to 0.20), standardized effect d = 0.73; z-test p = <0.001.
• GW642444 12.5 µg QD: mean 0.16 versus 0.06 on control; difference 0.10 (95% CI 0.04 to 0.16), standardized effect d = 0.54; z-test p = 0.001.
• GW642444 25 µg QD: mean 0.18 versus 0.06 on control; difference 0.12 (95% CI 0.06 to 0.19), standardized effect d = 0.66; z-test p = <0.001.

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 Weighted Mean 24-hour FEV1 on Day 7 of the 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:
  • GW642444 6.25 µg QD: mean 0.18 versus 0.03 on control; difference 0.15 (95% CI 0.10 to 0.21), standardized effect d = 0.92; z-test p = <0.001.
  • GW642444 6.25 µg BID: mean 0.19 versus 0.03 on control; difference 0.17 (95% CI 0.11 to 0.22), standardized effect d = 0.99; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for GW642444 6.25 µg QD than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for GW642444 6.25 µg BID than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary outcome: change from baseline in weighted mean 24-hour FEV1 on Day 7 of the treatment period. The posted least-squares mean changes are positive across placebo and all four GW642444 dose schedules. The overall pattern of higher adjusted values for active treatment relative to placebo is directionally consistent with the primary trough FEV1 result, though weighted mean 24-hour FEV1 measures a different aspect of pulmonary function from a trough measurement.

The secondary endpoint is not simply another version of the primary endpoint. A weighted mean across the 24-hour period summarizes measurements over a different window, while trough FEV1 focuses on measurements at the end of the dosing interval. Agreement in general direction can be viewed as supportive descriptive context, but it does not establish that the endpoints are interchangeable or that the result generalizes beyond the posted outcomes.

The registry posts no sponsor-reported inferential analyses for the secondary outcome. Recalculated comparisons are available for only some of the active-treatment contrasts, and those are unadjusted calculations from summary statistics. They should be treated as exploratory rather than as a complete inferential analysis of every secondary comparison.

Multiple outcomes and multiple dose comparisons create multiplicity: testing many hypotheses increases the chance that some results appear notable by chance if each is judged independently. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting the secondary outcome. As a result, the secondary pattern carries less inferential weight than the primary endpoint and should not be used as a stand-alone confirmation. The registry does not report additional secondary outcomes beyond this listed measure.

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

• Change From Baseline in Weighted Mean 24-hour FEV1 on Day 7 of the Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The primary analysis used a mixed-model analysis of covariance, or ANCOVA. In general, ANCOVA compares an outcome across treatment groups while adjusting for specified covariates. In this trial, the registry states that treatment, period, sex, and age were fixed effects, while participant was included as a random effect. The period baseline measurement was included as part of a bivariate response, and the model for the period baseline value was not affected by treatment group.

A fixed effect estimates the contribution of a listed model term under the specified model. Treatment is the principal term for the dose-versus-placebo comparisons; period allows the analysis to account for systematic variation across treatment periods. Sex and age were also included as fixed effects. A random participant effect represents variation associated with individual participants and is relevant in a crossover study, where a participant can contribute measurements under more than one treatment. These are general explanations of model terms; the registry does not provide coefficients or detailed diagnostics for each term.

Why use a mixed model in a crossover trial?

General statistical reasoning: observations from the same person are often correlated, so they should not automatically be treated as if they came from unrelated people. A participant-level random effect can represent this within-person structure. Period is also important because measurements may differ across periods for reasons not attributable to treatment. Adjusting for period helps distinguish treatment comparisons from period-related variation under the fitted model.

The registry’s description includes baseline measurements in a bivariate response. General statistical reasoning: modeling baseline jointly with the outcome can account for the relationship between a participant’s baseline and later measurement, and can support adjusted comparisons. The record specifically says that the period baseline model is not affected by treatment group. It does not describe the full covariance structure, model diagnostics, convergence checks, or sensitivity analyses; those details are not reported in the registry record.

What do least-squares means and standard errors describe?

A least-squares mean is a model-based adjusted mean, evaluated while accounting for terms in the analysis. It is not necessarily the same as a simple arithmetic average of the observed participant measurements. The registry posts least-squares mean changes for each treatment, along with standard errors. A standard error describes uncertainty in an estimated mean under the model; it is not a measure of the spread of individual participant outcomes.

The sponsor’s comparison is reported as an ANCOVA mean difference in final values, with a 95% confidence interval and a p-value. The posted sponsor estimates compare each active treatment with placebo. The record does not say that these p-values were adjusted for making multiple treatment comparisons. They should therefore be read as the reported comparisons, not as a family-wise multiplicity-controlled set of tests.

What is the role of the recalculations?

The recalculated contrasts are simple, unadjusted comparisons reconstructed from posted summary statistics. General statistical reasoning: an unadjusted comparison based on group summaries may not reproduce a model that accounts for period, participant, baseline, age, and sex. The recalculated confidence intervals are likewise approximate, and the pooled standard deviations used in them were approximated from the reported standard errors. These recalculations are useful as a rough independent reading of the posted means, not as a replacement for the sponsor’s specified analysis.

For the primary endpoint, the recalculated mean differences closely track the sponsor’s point estimates as displayed, but the recalculated intervals are not the sponsor’s ANCOVA intervals. The registry lists no discrepancy flag. The reported analysis remains the authoritative description of the trial’s own model-based results. The exact computational details needed to reproduce that model, including participant-level data and full model output, are not reported in the registry record.

Why can over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variability is greater than a model’s assumed variability. If the model understates variability, standard errors may be too small and intervals too narrow; if it overstates variability, uncertainty estimates may be too large. This is a general issue for statistical models, not a finding reported for this trial. The registry does not report an over-dispersion assessment, and the primary FEV1 endpoint is continuous rather than a count outcome for which over-dispersion is commonly discussed.

Several model choices cannot be evaluated from the registry summary alone. Carryover effects, sequence effects, missing-data methods, and sensitivity analyses are not described in the registry record. Their absence from the record should not be taken to mean that a particular method was or was not used.

11. Confidence Intervals and Precision

The sponsor reports 95% confidence intervals for each active-treatment comparison with placebo. For 6.25 µg QD, the mean difference is 0.094 liters, with a 95% interval from 0.049 to 0.140. For 6.25 µg BID, the estimate is 0.140 liters, with an interval from 0.095 to 0.185. For 12.5 µg QD, the estimate is 0.102 liters, with an interval from 0.057 to 0.147. For 25 µg QD, the estimate is 0.125 liters, with an interval from 0.080 to 0.170.

A confidence interval expresses the uncertainty around an estimated comparison under the analysis used. General statistical interpretation: an interval that is narrower indicates greater precision than a wider interval, while the interval’s location indicates which effect sizes remain compatible with the model and data at the stated confidence level. The sponsor intervals are all above zero, matching the reported p-values of <0.001. This does not mean that every participant’s response was positive or that the true effect is known exactly.

The recalculated intervals are a separate, approximate, unadjusted analysis and should not be substituted for the sponsor’s intervals. Because the recalculation uses group summary values rather than the full crossover model, its uncertainty estimates may differ. The registry’s adjusted means and sponsor intervals are the most direct basis for describing the trial’s reported primary comparisons.

Precision is also limited by the study’s size and scope. The registry lists enrollment of 75, with treatment-period analysis counts ranging from 73.0 to 74.0. These counts describe available data by treatment, not separate parallel-group samples. The confidence intervals quantify model-based uncertainty for the primary comparisons, but they do not address unreported sources of uncertainty such as sensitivity to missing data, model assumptions, or multiplicity procedures.

12. Planning a Similar Trial: Sample Size

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

The sample-size illustrations describe participants per arm for 80% power and participants per arm for 90% power. They are not total event counts: the endpoint is continuous, and the illustrations concern a two-arm comparison. The calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect set to the stated fraction of the observed effect.

Rows planning for 100% of the observed effect use the observed contrast as the target effect in the illustration. Rows planning for 75% or 50% of the observed effect use smaller target effects. Smaller effects are harder to distinguish from variation, so the planning illustrations require more participants per arm to reach the same power level.

The 80% power column gives the illustrated participants per arm for a design with an 80% chance of detecting the selected effect under the stated assumptions and test procedure. The 90% column gives the corresponding participants per arm for a 90% chance. Power is a property of a hypothetical design and assumed effect, not a probability that the posted result is true. These figures are planning illustrations based on the observed effect, not observed power.

The registry does not report the original trial’s sample-size justification or the assumptions used to choose enrollment of 75. The illustrations therefore should not be read as the trial’s prospective design calculation. They also do not account for crossover-specific features in the trial’s design: the listed calculation assumes equal allocation between two arms, and the description does not state that it models the within-participant structure or five treatment periods.

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 = 0.094; pooled standard deviation σ = 0.190.
2. n = 2 × (1.96 + 0.842)² × 0.190² / 0.094² = 64.1, rounded up to 65 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 <- 0.094                      # observed difference in means
sigma <- 0.189895758337259                     # 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(980200)
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 = 65 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 114 (80% power), 153 (90% power)
 50% of observed effect: n per arm = 257 (80% power), 344 (90% power)
power.t.test: 65 
Simulated power at n = 65 per arm: 0.793 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s posted primary comparisons come from ANCOVA and include model-based mean differences, 95% confidence intervals, and p-values. For the active treatments, the sponsor reports differences of 0.094, 0.140, 0.102, and 0.125 liters, respectively. Each interval excludes zero and each p-value is <0.001.

The simple recalculations use posted group summaries to estimate unadjusted mean differences and approximate intervals. Their point estimates are similar to the sponsor’s estimates, but their intervals are not identical to the sponsor’s intervals. This is expected to be possible because the recalculation does not reproduce the mixed-model ANCOVA with its treatment, period, sex, age, participant, and baseline structure. The sponsor’s analysis is the direct report of the trial’s specified model; the recalculation is a supplementary, approximate check.

The registry discrepancy indicator is false. The record does not identify a conflict requiring a choice between incompatible results. Differences in interval construction should still be kept clear: sponsor intervals describe the posted ANCOVA analysis, whereas recalculated intervals are derived from summary statistics. No individual participant data or full model output is reported in the registry record, so the sponsor’s model cannot be independently reconstructed from the posted summary alone.

15. Multiplicity, Missing Data and Analysis Populations

The primary analysis involves comparisons of four active dose schedules with placebo, and the registry also lists a secondary FEV1 outcome. When multiple hypotheses are examined, the chance of at least one apparently strong result can increase. General statistical approaches to this issue include adjusting the significance threshold, controlling a family-wise error rate, or defining a prespecified hierarchy. The registry record does not report whether any such procedure was planned or applied.

The sponsor’s reported p-values are shown as reported for individual comparisons. The registry does not label them as multiplicity-adjusted. The approximate recalculated p-values are explicitly unadjusted. Neither set should be interpreted as establishing a family-wide error rate without a documented procedure.

The primary population is described as randomized participants who received at least one dose, with randomized participants assumed to have received medication unless definitive evidence to the contrary existed. The record further says that only participants available at the indicated time were included. That statement identifies availability as relevant to the reported analysis, but it does not specify how missing endpoint measurements were handled, whether any values were imputed, or what sensitivity analyses were performed. Those details are not reported in the registry record.

The registry does not report a complete disposition of missing measurements by treatment period or reasons for missingness. It also does not state whether the analysis population differed from the randomized population beyond the stated eligibility definition. These limitations matter because a complete-case or available-data analysis can be affected if missingness is related to treatment, outcome, or participant characteristics.

Other analysis-plan details are also not reported in the registry record, including a detailed protocol for carryover or sequence effects in the crossover design, model diagnostics, and sensitivity analyses. This is a statement about what is documented in the registry, not evidence that the investigators did or did not perform additional analyses.

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 affected participants in each treatment group: placebo, 6.25 µg QD, 6.25 µg BID, 12.5 µg QD, and 25 µg QD. The corresponding numbers at risk are 74, 73, 74, 73, and 73. The registry lists no top serious adverse event terms.

For other adverse events, the posted counts are one participant with placebo, none with 6.25 µg QD, three with 6.25 µg BID, none with 12.5 µg QD, and three with 25 µg QD. These counts are not counts of serious adverse events. The registry’s death fields are null, so deaths are not reported in the registry record.

These figures describe the adverse-event entries posted for this study. They do not establish that no events occurred outside the registry’s reported categories, and they do not provide event-level detail or a comparison of rates adjusted for the crossover periods. The study’s enrollment and duration also limit what can be inferred about uncommon or longer-term events. Safety interpretation should remain descriptive and tied to the recorded counts.

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

The registry results describe adjusted mean changes in trough FEV1 during Day 7 of treatment periods. The sponsor’s model-based comparisons favor higher mean change with each listed GW642444 dose than with placebo, and the reported confidence intervals are above zero. This is evidence about the average outcome under the fitted model for the participants and treatment periods contributing data.

The estimates do not show that every participant experienced an increase, nor do they reveal how responses varied across individuals. Group means can conceal meaningful differences among participants. The registry does not report distributions of individual responses or a clinically important difference threshold, so the practical importance of the estimated changes cannot be determined from these results alone.

The endpoint is lung function measured in liters at a particular time point in each treatment period. It is not a direct measure of symptoms, exacerbations, quality of life, long-term disease control, or outcomes beyond the trial’s stated measures. The record identifies participants with persistent asthma who were receiving inhaled corticosteroid treatment; generalization to other populations or settings is not established by this record.

The study is phase 2 and used a five-period crossover design. Its findings should be interpreted within that design and the reported time frame. The posted outcome estimates do not, by themselves, establish longer-term effects or the balance of benefits and harms in broader use. The safety figures are limited counts from the registry record and should not be treated as proof that uncommon events are absent.

Statistical evidence and clinical judgment are different questions. A p-value addresses compatibility with a specified statistical null under the analysis assumptions; it does not quantify the chance that a treatment works, and it does not tell whether an observed change is important to patients. The registry record does not provide enough information to make those broader judgments.

18. Why This Trial Matters Statistically

This trial illustrates why design and analysis need to be read together. In a crossover study, participants receive treatment sequences across periods, so each person can contribute information under more than one condition. A participant-level random effect and adjustment for period are relevant features of the posted primary model. The comparison is therefore not adequately described as a simple parallel-group contrast alone.

The record also distinguishes model-based trial results from summary-statistic recalculations. The sponsor’s ANCOVA estimates reflect the stated model, while the recalculations offer approximate unadjusted contrasts. Similar point estimates do not make the methods interchangeable, and confidence intervals can differ when the underlying analysis differs.

Another statistical lesson is that several dose comparisons and an additional endpoint require attention to multiplicity. Individual p-values can look strong while the overall set of tests requires a clearly stated interpretation plan. The registry does not report a multiplicity procedure, so the primary results and secondary observations should not be assigned the same inferential weight automatically.

Finally, a statistically precise estimate is not the same as a clinically meaningful one. The sponsor reports confidence intervals for the primary comparisons, but the record does not set a threshold for clinical importance or connect the FEV1 changes to patient-centered outcomes. Keeping these distinctions clear allows the posted numbers to be interpreted without claiming more than the design and reported endpoints can support.

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 trial enrollment was 75, and treatment-period analysis counts were 73.0 or 74.0. That is a limited basis for detecting uncommon outcomes, and the record does not supply a long-term safety assessment. No deaths are listed as numerical results; the death information is not reported in the registry record.

The crossover design can be efficient for comparing treatments within participants, but interpretation depends on period structure and potential sequence or carryover effects. The registry describes period adjustment but does not report whether carryover or sequence effects were evaluated, whether washout periods were used, or what sensitivity analyses were performed. These details are not reported in the registry record.

The registry states that only participants available at the indicated time were included, but it does not fully describe missing-data handling, reasons for missing endpoint measurements, or sensitivity analyses. The stated analysis population and treatment-period counts should therefore be read with the limits of the available-data description in mind.

The primary endpoint is a short-term Day 7 measurement within treatment periods, with the stated timeframe extending up to Study Day 63. The record does not report outcomes beyond those listed or a threshold for clinical importance. It also does not report the original sample-size rationale, full model diagnostics, detailed masking procedures, or multiplicity adjustment. Approximate recalculations cannot resolve these gaps because they use summary statistics rather than participant-level data and the complete fitted model.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety Study in Subjects With Asthma — NCT00980200.
• Registry record last updated 2017-01-30; status last verified 2016-12.
• 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

NCT00980200 is a completed phase 2 randomized, double-blind, placebo-controlled, multicenter, five-period crossover study sponsored by GlaxoSmithKline. It enrolled 75 adults aged ≥18 years with persistent asthma who were receiving inhaled corticosteroid treatment.

The primary outcome was change from baseline in trough FEV1 on Day 7 of a treatment period. Sponsor-reported ANCOVA comparisons gave positive mean differences for each of four GW642444 schedules versus placebo, with 95% confidence intervals above zero and p-values of <0.001. These are model-based average comparisons, not individual response guarantees.

The record also posts a secondary weighted mean 24-hour FEV1 outcome and adverse-event counts. Details on multiplicity, missing-data handling, and the original sample-size justification are not reported in the registry record.