A Single Dose PD & PK Study With Two Formulations of Abediterol in Patients With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Single Dose PD & PK Study With Two Formulations of Abediterol in Patients With Asthma (NCT02777827), a randomized phase 1 study. The primary outcome is Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1)..

2. Clinical Question

The central statistical question is about the size and precision of the change in lung-function measurement within this study, not whether the treatment is effective in broader clinical use. The registry reports treatment-specific means and standard deviations, along with sponsor ANCOVA estimates, confidence intervals and p-values for comparisons with placebo. Those summaries describe the observed data under the study conditions.

The crossover design means treatment conditions were evaluated within a study structured around multiple treatments, rather than as a simple parallel comparison in which each participant receives only one assigned treatment. The registry record does not report the treatment sequence, washout details or other period-specific procedures. Such details matter when interpreting how treatment contrasts were estimated and whether treatment periods could have affected one another.

3. Trial Design

This was a randomized, double-blind, double-dummy, placebo-controlled, multicentre, six-way crossover study, registered as a Phase 1 trial. The registry lists 30 enrolled participants with asthma who were on inhaled corticosteroids. The study status is completed. The recorded start date is 2016-06-21, and the primary completion date is 2016-11-29.

The treatment conditions included abediterol at 0.156 μg and 2.5 μg through a dry powder inhaler, and at 0.05μg, 0.156 μg and 2.5μg through a pressurised metered-dose inhaler, as well as placebo. The placebo condition used both devices, consistent with the double-dummy description. This design helps maintain masking when treatment conditions use different inhaler devices.

The study’s stated aim was to assess pharmacodynamics, pharmacokinetics and safety after a single dose. The primary outcome was change from baseline in trough FEV1 on Day 1. Secondary outcomes included peak FEV1 response, time to peak FEV1, and pharmacokinetic measures such as maximum concentration, time to maximum concentration, terminal rate constant, half-life and area under the curve.

In a crossover study, a participant may contribute measurements under more than one treatment condition. General statistical practice therefore needs to account for within-participant dependence and treatment-period structure when estimating contrasts. The registry identifies the overall model as crossover and reports ANCOVA for the primary comparisons, but does not report the complete model specification, treatment sequence, washout period, or how period and sequence effects were handled. Those design and analysis details are not reported in the registry record, so the posted summaries do not permit a full assessment of those aspects.

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: In total, 42 patients were screened; 30 patients were eligible to participate and were randomised.

Treatment Period 1

Washout Between Periods 1 and 2

Treatment Period 2

Washout Between Periods 2 and 3

Analysis population for the primary outcome, as defined in the registry: All randomised participants who received investigational product, irrespective of protocol adherence and continued participation in the study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

Population: Includes all randomised participants who received at least one dose of investigational product

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Trough Forced Expiratory Volume in 1 Second (FEV1)., measured over 45 mins and 15 mins pre-dose, and 23.00-24.00 h post-dose on Day 1.

The primary endpoint is change from baseline in trough forced expiratory volume in 1 second (FEV1), measured in liters. FEV1 is the volume of air exhaled during the first second of a forced breath. The endpoint captures the change in this continuous lung-function measure after the single-dose treatment conditions.

Baseline was defined separately for each treatment period as the mean of two measurements taken 30 min apart, at -45 min and -15 min, before investigational product administration on Day 1. If both baseline measurements were missing, the screening value was used. Trough was defined as the mean of FEV1 values measured at 23 h and 24 h after dosing; if one of those readings was missing, the other was used.

Using change from baseline focuses the comparison on how the measurement shifted from the participant’s starting value in a treatment period. The trough time point represents a later post-dose measurement rather than an immediate response. That makes it distinct from secondary outcomes based on peak FEV1 or the time taken to reach a peak.

General statistical context: continuous endpoints preserve information about the magnitude of measured change, rather than reducing observations to a yes-or-no response category. The mean describes the average change, while the standard deviation describes variation among the measurements. Neither summary alone describes every participant’s response. The endpoint is a physiological measurement; it does not, by itself, establish how a participant feels or functions, nor does it answer longer-term clinical questions.

7. Results Posted in the Registry

• Abediterol Dry Powder Inhaler 0.156 μg: mean 0.23 versus -0.00 on control; difference 0.23 (95% CI 0.11 to 0.34), standardized effect d = 1.03; z-test p = <0.001.
• Abediterol Dry Powder Inhaler 2.5 μg: mean 0.40 versus -0.00 on control; difference 0.40 (95% CI 0.27 to 0.53), standardized effect d = 1.56; z-test p = <0.001.
• Abediterol Pressurised Metered-dose Inhaler 0.05μg: mean 0.11 versus -0.00 on control; difference 0.11 (95% CI -0.01 to 0.23), standardized effect d = 0.48; z-test p = 0.067.
• Abediterol Pressurised Metered-dose Inhaler 0.156 μg: mean 0.17 versus -0.00 on control; difference 0.17 (95% CI 0.06 to 0.29), standardized effect d = 0.76; z-test p = 0.004.

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.

Percentage of Participants Achieving a ≥ 200 mL and ≥12% Increase From Baseline in Peak FEV1 on Day 1.

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Abediterol Dry Powder Inhaler 0.156 μg: 72.4% (21/29) versus 24.1% (7/29) on control; risk difference 48.3 percentage points (95% CI 25.8 to 70.8), risk ratio 3.00 (1.51–5.94); unadjusted two-proportion z-test p = <0.001.
  • Abediterol Dry Powder Inhaler 2.5 μg: 82.8% (24/29) versus 24.1% (7/29) on control; risk difference 58.6 percentage points (95% CI 37.8 to 79.4), risk ratio 3.43 (1.76–6.68); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Abediterol Dry Powder Inhaler 0.156 μg 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 proportion with the event is statistically higher for Abediterol Dry Powder Inhaler 2.5 μg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Time to Peak FEV1 at Day 1

• 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 deviations.
• Result:
  • Abediterol Dry Powder Inhaler 0.156 μg: mean 3.70 versus 2.90 on control; difference 0.80 (95% CI -0.23 to 1.83), standardized effect d = 0.40; z-test p = 0.130.
  • Abediterol Dry Powder Inhaler 2.5 μg: mean 3.30 versus 2.90 on control; difference 0.40 (95% CI -0.63 to 1.43), standardized effect d = 0.20; z-test p = 0.449.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Abediterol Dry Powder Inhaler 0.156 μg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Abediterol Dry Powder Inhaler 2.5 μg and the control. The interval gives the range of effects that remain compatible with the data.

Time to Peak FVC at Day 1

• 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 deviations.
• Result:
  • Abediterol Dry Powder Inhaler 0.156 μg: mean 2.80 versus 1.90 on control; difference 0.90 (95% CI -0.03 to 1.83), standardized effect d = 0.50; z-test p = 0.057.
  • Abediterol Dry Powder Inhaler 2.5 μg: mean 2.30 versus 1.90 on control; difference 0.40 (95% CI -0.55 to 1.35), standardized effect d = 0.22; z-test p = 0.410.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Abediterol Dry Powder Inhaler 0.156 μg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Abediterol Dry Powder Inhaler 2.5 μg and the control. The interval gives the range of effects that remain compatible with the data.

The available secondary outcome summaries cover a responder measure for peak FEV1 and timing measures for peak FEV1 and peak FVC. Across the responder summaries, the listed active-treatment percentages are above the placebo percentage. The time-to-peak summaries vary across the active conditions and include broad uncertainty in the recalculated comparisons. Taken together, these outcomes add context about response patterns and timing, but they are not interchangeable with the primary trough FEV1 endpoint.

The secondary outcomes address different questions. The responder measure classifies whether a participant reached the stated increase threshold in peak FEV1. Time-to-peak measures describe when the peak value occurred during the assessment window. The primary outcome instead describes change from baseline in trough FEV1. Differences across these measures are not inherently contradictory because the measurement, timing and definition differ.

Although the registry lists additional pharmacokinetic outcomes, numerical results for those outcomes are not reported in the registry record. The record also does not provide sponsor inferential analyses for the posted responder comparisons. Any simple recalculation of those comparisons is unadjusted and should not be treated as a substitute for a prespecified model-based analysis.

Secondary outcomes generally carry less weight than the primary outcome because they are additional questions and may involve multiple tests. If many outcomes are tested, some may appear notable by chance even when there is no corresponding underlying effect. The registry does not report a multiplicity strategy or identify how secondary outcomes were prioritized. These results are therefore most useful as descriptive supporting information, rather than as independent confirmation of the primary finding.

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

• Percentage of Participants Achieving a ≥ 200 mL and ≥12% Increase From Baseline in Peak FEV1 on Day 1.
• Time to Peak FEV1 at Day 1
• Observed Maximum Concentration of Abediterol (Cmax)
• Time (h) to Maximum Concentration of Abediterol (Tmax).
• Terminal Rate Constant of Abediterol (λz)
• Terminal Half-life (h) of Abediterol (t½λz)
• AUClast of Abediterol
• AUC of Abediterol.

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports arm-level means and standard deviations for the primary continuous outcome, as well as sponsor-reported ANCOVA comparisons with placebo. It also supports simple unadjusted recalculations from the posted summary statistics. These are different kinds of summaries: arm means describe the observed data, sponsor estimates come from the stated model, and recalculations are not the sponsor’s adjusted analysis.

What does the mean describe?

A mean is the arithmetic average of measurements in a group. For this endpoint, the reported value is the mean change from baseline in trough FEV1. A positive mean indicates that the average measured change was in the positive direction; a negative mean indicates a negative average change. The mean does not show how individual measurements are distributed around that average.

The standard deviation describes the spread of individual observations around the mean. It is not the same as the uncertainty in the estimated mean or the uncertainty in a treatment contrast. For instance, a group can have a substantial standard deviation while its mean estimate is more precise than any one participant’s measurement, depending on the amount of information and the analysis design.

What does ANCOVA contribute?

ANCOVA is a model-based method for comparing outcomes while accounting for covariates included in the analysis. The sponsor reports least square mean estimates from ANCOVA. A least square mean is an adjusted model estimate, not simply the raw mean printed for an arm. The registry does not report which covariates were included or the full model specification, so the exact adjustment cannot be reconstructed from the record.

General statistical context: in a crossover study, observations from the same participant are generally related. Treating them as independent when they are not can misstate uncertainty. A suitable model can account for repeated measurements and treatment-period structure. The record identifies a crossover design and ANCOVA, but does not give enough detail to determine how within-participant correlation, period effects, treatment sequence or carryover were handled.

What does the recalculation represent?

The recalculated comparisons use the posted arm-level means and standard deviations to form simple, unadjusted contrasts with placebo. They do not reproduce the sponsor’s ANCOVA, and they do not account for any model features that are absent from the published summaries. The registry flags a discrepancy between these calculations and the sponsor analysis. For interpretation of the trial’s inferential results, the sponsor’s own analysis takes precedence.

The recalculated p-values are unadjusted comparisons. They do not establish that the same inference would follow from the sponsor’s model, nor do they account for multiple treatment comparisons. This distinction is especially important when several active conditions are compared with a shared placebo condition.

Why does over-dispersion matter in general?

Over-dispersion is a general issue for count or binary data when variability exceeds what a simple model assumes. It can lead to uncertainty estimates that are too small if ignored. The primary endpoint is continuous, so this is not the central issue for its reported mean contrasts. For binary secondary outcomes, event rates and uncertainty should be interpreted using methods appropriate to that outcome type. The registry does not report sponsor inferential analyses for the posted peak-FEV1 responder outcomes.

What does a p-value say?

A p-value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of a difference. The sponsor reports p-values alongside effect estimates and confidence intervals; the estimates and intervals are needed to understand magnitude and precision.

General statistical context: a confidence interval gives a range of values compatible with the data and the method’s assumptions at the stated confidence level. Its width reflects precision. It does not guarantee that the true value lies in the interval, and it does not incorporate limitations that are not represented in the analysis model, such as unreported multiplicity handling or missing-data assumptions.

11. Confidence Intervals and Precision

The sponsor reports 95% confidence intervals for each ANCOVA contrast between an abediterol condition and placebo. For dry powder inhaler 0.156 μg, the estimate is 0.222 L with an interval from 0.132 L to 0.312 L. For dry powder inhaler 2.5 μg, the estimate is 0.404 L, with an interval from 0.315 L to 0.494 L. The other sponsor-reported intervals are 0.016 L to 0.195 L for pressurised metered-dose inhaler 0.05μg, 0.081 L to 0.259 L for pressurised metered-dose inhaler 0.156 μg, and 0.317 L to 0.495 L for pressurised metered-dose inhaler 2.5μg.

All of these sponsor intervals lie above zero, but their widths differ. An interval’s width indicates how precisely the model estimates a contrast under its assumptions: a narrower interval indicates greater precision than a wider interval. The endpoints are estimates of uncertainty, not a range of individual participant responses. The registry does not report a clinical threshold for interpreting these changes, so the intervals cannot determine whether a difference is clinically important.

For general interpretation, a confidence interval is not a probability statement about a fixed treatment effect, and it does not account for unreported sources of uncertainty. In particular, the registry does not report whether or how the intervals were adjusted for the set of multiple comparisons. Therefore, the stated confidence level should be read as applying to each reported model-based interval, not automatically to a family of all treatment contrasts.

The recalculated unadjusted intervals differ from the sponsor intervals because they are based on a different calculation and do not reproduce the ANCOVA. The registry record flags a discrepancy; the sponsor’s own analysis takes precedence. Neither set of intervals resolves limitations from the short-term endpoint, the crossover analysis details that are not reported, or the small study context.

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 figures are planning illustrations based on the observed contrast, not the trial’s original design calculations. For the primary continuous outcome, the figures are participants per arm. They are not total study enrollment and should not be summed across the crossover treatment conditions.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The registry’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative participants per arm needed, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column gives the corresponding planning figure for a 90% chance. These are design probabilities under an assumed effect and model, not probabilities that the study result is true.

The rows describe planning for the full observed effect, 75% of the observed effect, and 50% of the observed effect. A smaller assumed effect requires more participants to distinguish it from random variation at the same target power and significance level. That pattern is a general consequence of statistical precision: subtle contrasts are harder to detect than larger contrasts.

These calculations are not observed power. Observed power calculated from an effect estimated in the same trial does not add useful evidence beyond the estimate and its confidence interval. The planning figures are best used to understand how assumptions about the target effect influence design requirements, not to judge whether the completed study was adequately powered under its original plan.

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 = 0.226; pooled standard deviation σ = 0.220.
2. n = 2 × (1.96 + 0.842)² × 0.220² / 0.226² = 14.8, rounded up to 15 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 <- 0.226                      # observed difference in means
sigma <- 0.219544984001002                     # 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(2777827)
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 = 15 (80% power), 20 (90% power)
 75% of observed effect: n per arm = 27 (80% power), 36 (90% power)
 50% of observed effect: n per arm = 60 (80% power), 80 (90% power)
power.t.test: 15.8 
Simulated power at n = 15 per arm: 0.780 (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 sponsor ANCOVA estimates, 95% confidence intervals and p-values for all five primary comparisons with placebo. These are the trial’s own reported inferential analyses. The posted arm summaries also allow simple unadjusted recalculations, but those calculations do not reproduce the sponsor’s model.

The two approaches give estimates that are close in some comparisons but not identical. For example, the unadjusted recalculated difference for pressurised metered-dose inhaler 2.5μg is 0.408 L, whereas the sponsor’s ANCOVA estimate is 0.406 L. For pressurised metered-dose inhaler 0.05μg, the recalculated estimate is 0.109 L and the sponsor estimate is 0.106 L. The record flags a discrepancy and does not explain its source.

Because the sponsor’s analysis uses ANCOVA and is the analysis reported by the registry, it takes precedence for interpretation of the trial’s stated comparisons. The recalculations are useful as checks based on the posted summary statistics, but should not be presented as adjusted results or substituted for the sponsor’s estimates. The record does not provide enough model detail to independently reproduce the ANCOVA or identify which analysis choices account for the differences.

The sponsor’s estimates and p-values also do not settle questions about multiplicity. Whether the reported inferential findings were adjusted across comparisons is not reported in the registry record. The estimates should therefore be read as the sponsor-reported results for the individual contrasts, with that limitation in mind.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports five sponsor ANCOVA comparisons of active abediterol conditions with placebo for the primary endpoint. It does not report whether the p-values or confidence intervals were adjusted for making multiple comparisons. Without that information, the individual reported p-values should not be interpreted as controlling the overall chance of a false-positive conclusion across the full set of treatment contrasts.

Multiplicity also arises across the many secondary outcomes. The registry lists pharmacodynamic and pharmacokinetic measures, while 23 secondary outcomes are posted. The specific hierarchy among these outcomes, any prespecified testing sequence, and any adjustment method are not reported in the registry record. Secondary findings should consequently be interpreted with caution, particularly when their analyses are exploratory or unadjusted.

The registry describes the primary analysis population as all randomized participants who received investigational product, irrespective of protocol adherence or continued participation. It does not report the detailed handling of missing primary outcome measurements, exclusions from individual treatment-period analyses, or any sensitivity analyses for missing data. The endpoint definition does specify how a missing baseline pair or a missing trough reading was handled, but that does not describe the full missing-data strategy for the analysis.

The study is a crossover trial, and the registry names ANCOVA as the primary comparison method. However, the covariates, repeated-measures structure, period and sequence terms, and any carryover assessment are not reported in the registry record. The treatment sequence and washout details are also not reported. These omissions limit independent assessment of whether the model fully reflects the design.

The absence of these details does not show that the trial lacked a plan or that the analysis was inappropriate. It means only that the registry record does not provide enough information to evaluate those decisions. Interpretation should distinguish the sponsor’s posted results from aspects of the statistical plan that remain undocumented.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry reports zero serious adverse events in each treatment condition and zero deaths. The number at risk for serious events is listed as 29 for dry powder inhaler 0.156 μg, 29 for dry powder inhaler 2.5 μg, 30 for pressurised metered-dose inhaler 0.05μg, 30 for pressurised metered-dose inhaler 0.156 μg, 30 for pressurised metered-dose inhaler 2.5μg, and 29 for placebo.

These are the posted serious-event counts for the listed conditions; they do not establish that an event is impossible or characterize safety under longer exposure. The study evaluated single doses, and the registry record does not give detailed duration or follow-up information for safety beyond the study summary.

The record separately lists other adverse events affecting participants in each condition. Those counts are not serious-event counts and should not be conflated with the serious adverse event figures. Because this is a crossover design, the treatment-condition entries should not be added to infer a total number of distinct participants. The registry record does not report serious adverse event terms because none are listed.

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

The posted primary results describe measured change in trough FEV1 after single-dose treatment conditions in a Phase 1 crossover study of participants with asthma on inhaled corticosteroids. The sponsor’s ANCOVA estimates for each active condition are positive relative to placebo, and the reported confidence intervals lie above zero. This is a description of the sponsor’s statistical findings in this particular study.

It does not establish how the measurements translate into symptoms, daily functioning, future health outcomes or longer-term response. The endpoint is a physiological measure recorded on Day 1, not a direct measure of how participants felt. No clinical threshold for interpreting the size of the change is reported in the registry record.

The result also does not compare abediterol with other active bronchodilators. The registry describes placebo-controlled conditions using different devices and doses, but does not report a head-to-head inferential analysis between devices or dose levels. Numerical differences between treatment summaries should not be treated as evidence of superiority of one active condition over another unless such a comparison was analyzed and reported.

The study’s single-dose focus does not answer questions about repeated administration, long-term safety, or use in populations other than the participants described. It does not establish efficacy in COPD or support conclusions about combination treatment, despite those broader areas appearing in the study background. Those outcomes are not addressed by the posted primary result.

Finally, the reported statistical findings are subject to the limits of the available record: the full ANCOVA specification, missing-data methods and multiplicity approach are not reported. The sponsor analysis takes precedence over the flagged unadjusted recalculations, but the registry record does not provide enough information to independently reproduce the sponsor model.

18. Why This Trial Matters Statistically

This trial illustrates how a crossover design can be used to compare several treatment conditions with placebo while collecting pharmacodynamic and pharmacokinetic information in a focused study. The central statistical challenge is to represent the structure of measurements across treatment periods, rather than treating each treatment condition as an unrelated group. That distinction matters for both estimated contrasts and their uncertainty.

It also shows why arm-level means and model-based comparisons should not be conflated. The posted means and standard deviations provide descriptive information, while the sponsor’s ANCOVA yields adjusted least square mean contrasts. Simple recalculations can check the scale and direction of the contrasts, but cannot reconstruct a model when the analysis specification is not posted. The recorded discrepancy makes that distinction especially relevant.

The range of outcomes also demonstrates that primary and secondary endpoints answer different statistical questions. A trough measurement, a peak-response threshold, time to peak, and pharmacokinetic measures describe different aspects of response. Their results should be interpreted in their own terms and with attention to the possibility of multiple testing.

For clinical researchers, a central lesson is to evaluate estimates alongside uncertainty and analysis details, not p-values alone. Confidence intervals help show precision, but they cannot resolve missing information about model specification or multiplicity. Planning illustrations similarly depend on assumptions about the target effect and should not be confused with the completed trial’s observed power or original design rationale.

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 study was a single-dose investigation with a Day 1 primary endpoint. The posted result therefore does not address repeated dosing or longer-term outcomes. The registry record describes participants with asthma on inhaled corticosteroids; it does not establish how these results apply to other populations or treatment settings.

The crossover structure makes the analysis dependent on how within-participant measurements and treatment periods were handled. Although the registry identifies ANCOVA, it does not report the covariates, period or sequence terms, correlation structure, washout details or carryover assessment. This limits independent evaluation of the model’s suitability for the design.

The registry does not report the original sample-size justification, the trial’s design assumptions, the missing-data strategy in full, or whether multiplicity adjustments were used. Those details would help place the reported uncertainty and multiple treatment comparisons in context. The record also flags differences between the sponsor analysis and simple unadjusted recalculations without explaining why they differ.

Some listed secondary outcomes have no numerical results in the registry record, including the pharmacokinetic measures. The available secondary summaries do not include sponsor-reported inferential analyses for the responder outcome. Consequently, the secondary evidence is incomplete for assessing the full set of stated study aims.

The sample-size illustrations use the observed effect for planning and do not represent the original trial design. Finally, the reported safety information is limited to posted event counts by treatment condition. It does not provide detailed event descriptions or establish safety with longer exposure.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Single Dose PD & PK Study With Two Formulations of Abediterol in Patients With Asthma — NCT02777827.
• Registry record last updated 2019-01-24; status last verified 2019-01.
• Results first posted 2019-01-24.
• 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

NCT02777827 is a completed Phase 1, randomized, double-blind, double-dummy, placebo-controlled, multicentre, six-way crossover study of single-dose abediterol in participants with asthma on inhaled corticosteroids. The registry lists an enrollment of 30.

The primary endpoint was change from baseline in trough FEV1 on Day 1. The sponsor reported ANCOVA comparisons with placebo for five abediterol treatment conditions, with positive estimates and 95% confidence intervals above zero. The record also includes arm-level summaries and secondary outcome information.

A discrepancy is flagged between sponsor analyses and simple unadjusted recalculations; the sponsor’s own analysis takes precedence. Multiplicity handling, detailed model specifications, full missing-data methods, and the original sample-size justification are not reported in the registry record.