A Study in Asthmatic Children (6 to <12 Yrs) Comparing Single Doses of Formoterol and Foradil® Evaluating Efficacy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study in Asthmatic Children (6 to <12 Yrs) Comparing Single Doses of Formoterol and Foradil® Evaluating Efficacy (NCT01136655), a randomized phase 2 study. The primary outcome is Average 12 Hour Forced Expiratory Volume in 1 Second (FEV1).

2. Clinical Question

The study was designed to compare relative bronchodilating effects and safety after single doses. Its crossover structure means participants received treatment in multiple periods, rather than being assigned to only one treatment for the entire study. The registry record does not report the sequence details or interval between periods.

3. Trial Design

This was a randomized, quadruple-masked, phase 2, multicenter, five-period crossover study. The registry lists 54 enrolled participants and a completed study. The recorded start was 2010-09, and primary completion was 2011-12. AstraZeneca is listed as the sponsor.

The five treatment groups were BUD 160/FM 2.25, BUD 160/FM 4.5, BUD 160/FM 9.0, BUD 160, and BUD 160/Foradil 12.0. The first three combined budesonide with different single doses of formoterol delivered through Symbicort pMDI. The budesonide-only group served as a comparison without formoterol, while the Foradil group received formoterol as Foradil Aerolizer alongside budesonide. The registry descriptions also list placebo inhalations as part of some regimens.

In a crossover design, a participant receives more than one treatment across study periods. General statistical context: this can allow treatment comparisons to use within-participant information, but interpretation depends on the design and analysis accounting for the period structure. The registry record does not report the treatment sequences, any washout interval, or the model details used to account for periods and within-participant correlation.

The primary efficacy analysis set required randomization, at least one dose, and sufficient data for at least one efficacy endpoint. The primary endpoint was average 12-hour FEV1. Secondary endpoints included FEV1 at 12 hours, maximal FEV1 during the 12-hour study period, and urinary formoterol excretion during the 12 hours after inhalation. The registry record does not report the original sample-size justification or the detailed masking procedures.

4. Participant Flow and Accounting

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

Before assignment: The study consisted of a screening visit, an enrolment visit, a 1- to 2-week run-in (standardization) period, randomization at Visit 3, and 4 further visits (Visits 4-7)separated by approximately 7-day (minimum 3 days; maximum 14 days) wash-out (stabilization) periods. Subjects received 1 of 5 single-dose treatments at Visits 3-7, in random order.

BUD 160/FM 2.25 (1 Dose)

Washout After BUD 160/FM 2.25 (7 Days)

Reasons for not completing this period:

BUD 160/FM 4.5 (1 Dose)

Washout After BUD 160/FM 4.5 (7 Days)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Efficacy analysis set including all patients who were randomized (defined as having a randomization code recorded on the demography case report form), received at least one dose of study medication, and contributed sufficient data for at least one efficacy endpoint.

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 Average 12 Hour Forced Expiratory Volume in 1 Second (FEV1), measured over at 3, 9, 15, 60, 120, 180, 240, 360, 480, 600 and 720 minutes postdose.

The primary endpoint was average FEV1 over 12 hours after study medication inhalation, measured in liters. FEV1 is the volume of air a person forcefully exhales during the first second of a spirometry maneuver. The study used repeated pulmonary function measurements at 3, 9, 15, 60, 120, 180, 240, 360, 480, 600, and 720 minutes after dosing.

To form the 12-hour average, the registry describes calculating the area under the curve from the serial FEV1 measurements and dividing by time. This produces one summary measure for each treatment period, rather than treating every recorded time point as a separate primary outcome. Repeated measures capture the course of lung function across the observation period; the average provides a concise summary of that course.

FEV1 is used in pulmonary function testing as a measurable indicator of expiratory airflow. For this trial, the endpoint addresses the stated question about relative bronchodilating effects over the post-dose observation period. It does not, on its own, describe long-term control, symptoms, quality of life, or outcomes beyond the 12-hour study window. The registry record does not report a threshold for a clinically important difference, so the statistical contrasts should be read as differences in the measured outcome rather than as proof of clinical importance.

7. Results Posted in the Registry

• BUD 160/FM 4.5: mean 1.59 versus 1.55 on control; difference 0.05 (95% CI 0.02 to 0.08), standardized effect d = 0.67; z-test p = <0.001.
• BUD 160/FM 9.0: mean 1.60 versus 1.55 on control; difference 0.06 (95% CI 0.03 to 0.08), standardized effect d = 0.80; z-test p = <0.001.
• BUD 160: mean 1.49 versus 1.55 on control; difference -0.06 (95% CI -0.08 to -0.03), standardized effect d = -0.80; z-test p = <0.001.
• BUD 160/ Foradil 12.0: mean 1.60 versus 1.55 on control; difference 0.06 (95% CI 0.03 to 0.08), standardized effect d = 0.80; 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.

FEV1 at 12 Hours After Study Medication Inhalation

• 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:
  • BUD 160/FM 4.5: mean 1.69 versus 1.64 on control; difference 0.05 (95% CI 0.00 to 0.10), standardized effect d = 0.40; z-test p = 0.040.
  • BUD 160/FM 9.0: mean 1.73 versus 1.64 on control; difference 0.09 (95% CI 0.04 to 0.14), standardized effect d = 0.70; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BUD 160/FM 4.5 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 BUD 160/FM 9.0 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Maximal FEV1 During the 12-hour Study 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:
  • BUD 160/FM 4.5: mean 1.89 versus 1.83 on control; difference 0.06 (95% CI 0.02 to 0.09), standardized effect d = 0.64; z-test p = <0.001.
  • BUD 160/FM 9.0: mean 1.88 versus 1.83 on control; difference 0.05 (95% CI 0.02 to 0.08), standardized effect d = 0.58; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BUD 160/FM 4.5 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 BUD 160/FM 9.0 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes extend the primary question in two ways: FEV1 at 12 hours focuses on the end of the observation period, while maximal FEV1 summarizes the highest measurement during the 12-hour period. Urinary formoterol excretion is a different type of outcome, relating to drug excretion rather than lung function.

Across the posted lung-function summaries, the formoterol-containing regimens generally have higher group mean values than BUD 160. Sponsor-reported analyses for the 4.5 and 9.0 µg regimens versus BUD 160 also show positive differences for the posted secondary lung-function outcomes. This overall direction is consistent with the primary endpoint pattern, but secondary endpoints answer distinct questions and should not be treated as independent confirmation of the primary result.

The registry record lists urinary formoterol excretion as a secondary outcome, but does not include a posted result for that outcome in the secondary results summarized in the record. The posted secondary analyses are limited: only selected pairwise sponsor comparisons are reported for the two lung-function endpoints, rather than a complete set of sponsor comparisons for every treatment pair.

Unadjusted secondary results carry less weight because multiple outcomes, time points, and treatment comparisons increase the chance of finding apparently notable results by chance. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting the secondary outcomes. These results are therefore best read as supporting descriptive context for the primary endpoint, not as a separate definitive test of benefit or as a basis for conclusions about outcomes not measured.

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

• FEV1 at 12 Hours After Study Medication Inhalation
• Maximal FEV1 During the 12-hour Study Period
• Urinary Excretion of Formoterol During the 12 Hours Following Inhalation of Study Drug

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports an ANCOVA for the sponsor’s primary comparisons, with results expressed as least-squares mean differences. ANCOVA is a regression-based method that compares group outcomes while accounting for variables included in the model. The registry record does not report the covariates, the full model specification, or how period and participant effects were handled. Those details matter in a crossover study because each participant contributes information across treatment periods.

What is a least-squares mean?

A least-squares mean is a model-based group average. Unlike a simple arithmetic average, it is estimated from the fitted statistical model and can be adjusted for variables included in that model. In this study the sponsor reported differences between least-squares means, in liters of average FEV1. Interpreting such a difference depends on the model being appropriate and on knowing which terms were included. The registry record reports ANCOVA but does not give those details.

How should the standard error be read?

The posted primary group results are least-squares means with standard errors. A standard error describes the estimated uncertainty in a mean, not the spread of individual participant measurements. Smaller standard errors generally indicate a more precisely estimated mean, subject to the analysis assumptions. The recalculated pairwise comparisons use approximations from posted summary statistics and do not reproduce the sponsor’s crossover ANCOVA.

What does the confidence interval contribute?

A confidence interval gives a range of values compatible with the data and the statistical method, under its assumptions. For a difference in means, an interval spanning zero is compatible with no difference as well as differences in either direction at the stated confidence level. An interval excluding zero indicates that zero is not among the values covered by that interval; it does not establish that the estimated difference is clinically important. Width is also informative: a wider interval reflects greater uncertainty about the size of the difference.

Why are the recalculations different from the sponsor analysis?

The recalculated comparisons are simple, unadjusted approximations based on posted group summary statistics. They do not account for participant-level pairing, treatment sequence, period, or any covariates unless those features can be recovered from the summaries; they cannot be recovered in full. The sponsor’s reported ANCOVA uses a model and produces least-squares mean differences. The reported values differ, so the sponsor’s own analysis takes precedence. The recalculations are best treated as a separate descriptive check, not as a replacement analysis or a correction to the sponsor’s results.

Why does over-dispersion matter in general?

General statistical context: over-dispersion occurs when observed variability is greater than a model assumes. If a model understates variability, standard errors can be too small and confidence intervals too narrow, which can make evidence appear more precise than it is. The primary outcome is continuous, and the registry does not report an over-dispersion assessment or suggest that over-dispersion was a concern. This general concept should not be read as a claim about the trial’s fitted model.

What role do p-values have?

A p-value measures how unusual the observed data, or more extreme data, would be under a specified null hypothesis and analysis model. It does not give the probability that the null hypothesis is true, nor does it measure effect size. The sponsor’s p-values accompany the estimated differences and confidence intervals. Because the record reports many pairwise analyses and does not report a multiplicity adjustment, the p-values should not be interpreted as if only one comparison had been planned.

Finally, the study is a crossover trial, so general methods for two independent groups are not a full substitute for a participant-level crossover analysis. The planning illustrations based on two-arm summary comparisons use a normal approximation and equal allocation, as described in the sample-size assumptions. They are not analyses of observed power and should not be mistaken for the design calculations used when the trial was planned.

11. Confidence Intervals and Precision

The sponsor’s 95% confidence intervals indicate the range of differences compatible with each reported ANCOVA comparison under that analysis. For example, the difference between BUD 160/FM 2.25 and BUD 160 was 0.058 liters, with a 95% confidence interval from 0.030 to 0.085. The intervals for the reported comparisons of BUD 160/FM 4.5 and BUD 160/FM 9.0 with BUD 160 also exclude zero. These intervals suggest that the sponsor’s model distinguishes those average FEV1 comparisons from zero, while still leaving uncertainty about the precise magnitude.

By contrast, the interval for BUD 160/FM 4.5 versus BUD 160/FM 9.0 extended from -0.036 to 0.018 liters. Because it includes zero, the data do not clearly distinguish the two group means in that reported comparison. A non-significant result is not evidence that the treatments are identical; the interval remains compatible with differences in either direction within its bounds.

Precision is about the range of plausible effect sizes, not just whether a p-value crosses a threshold. The group estimates are based on 51 to 54 participants, and the sponsor’s model-based confidence intervals are relatively narrow in liters, but the registry record does not provide a clinically important difference threshold to judge their practical importance. Nor does the record report the detailed model specification needed to assess all sources of uncertainty in the crossover analysis.

The approximate unadjusted recalculations produce confidence intervals from posted summary statistics, but these differ from the sponsor’s ANCOVA results. Given that discrepancy, the sponsor’s estimates and intervals take precedence. The confidence intervals describe uncertainty in average FEV1 under the reported analyses; they do not address long-term outcomes or prove that a difference matters to patients.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect in a comparison and show how the required number per arm changes when planning to detect the full observed effect, 75% of it, or 50% of it. The assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The registry record does not report the trial’s original sample-size assumptions or justification.

The 80% power column gives the estimated number of participants per arm for an 80% chance of detecting the stated effect if that effect is true and the planning assumptions hold. The 90% power column gives the corresponding number per arm for a 90% chance. These are planning concepts, not guarantees: actual results also depend on the true effect, variability, analysis model, and other design features.

For example, for the primary comparison of BUD 160/FM 4.5 with BUD 160, planning for 100% of the observed effect gives 36 participants per arm for 80% power and 47 participants per arm for 90% power. Planning for 75% of that effect gives 63 participants per arm for 80% power and 84 participants per arm for 90% power. Planning for 50% gives 141 participants per arm for 80% power and 188 participants per arm for 90% power. Smaller effects need more participants because they are harder to distinguish from random variation.

These figures are planning illustrations, not observed power. They use the observed effect as an input and do not show what power the completed trial actually had. The trial’s own design calculations are not reported in the registry record. The illustrations also use a two-arm framework and do not reproduce all aspects of the five-period crossover design.

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 = 0.048; pooled standard deviation σ = 0.072.
2. n = 2 × (1.96 + 0.842)² × 0.072² / 0.048² = 35.0, rounded up to 36 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 <- 0.048                      # observed difference in means
sigma <- 0.0716739402731963                     # 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(1136655)
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 = 36 (80% power), 47 (90% power)
 75% of observed effect: n per arm = 63 (80% power), 84 (90% power)
 50% of observed effect: n per arm = 141 (80% power), 188 (90% power)
power.t.test: 36 
Simulated power at n = 36 per arm: 0.800 (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 analyses using ANCOVA and least-squares mean differences. Those analyses are the primary basis for interpreting the posted treatment comparisons. The separate recalculations are simple, unadjusted approximations from the group summary statistics. They are not participant-level crossover analyses and do not necessarily estimate the same quantity as the sponsor’s model.

The discrepancy flag indicates that the recalculated values differ from the sponsor-reported results. Under that circumstance, the sponsor’s own analysis takes precedence. In particular, the recalculated difference between group means should not be substituted for a sponsor-reported least-squares mean difference, and its approximate confidence interval or p-value should not be used to overturn the sponsor’s findings.

The sponsor analysis reports positive differences for the formoterol-containing Symbicort groups compared with BUD 160, with reported 95% confidence intervals excluding zero. It also reports no clear difference between the 4.5 and 9.0 µg Symbicort regimens on the primary endpoint, because that comparison’s interval includes zero. These interpretations refer to the sponsor’s posted primary analyses, not proof of clinical importance. The registry record does not provide enough ANCOVA detail to reconstruct the model or explain exactly why the adjusted and unadjusted estimates differ.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports several treatment comparisons for the primary outcome and also lists secondary outcomes. It does not report whether the sponsor adjusted for multiple comparisons, specified a testing hierarchy, or otherwise controlled the overall type I error rate. Without that information, individual p-values should be read as results for their specific comparisons and not as if there had been only one statistical test. The chance of at least one false-positive finding can increase when many hypotheses are tested; this is a general statistical concern, not a claim that any particular posted result is false.

The primary efficacy analysis set included participants who were randomized, received at least one dose, and contributed sufficient data for at least one efficacy endpoint. The record reports group counts for the primary outcome, but does not describe the reasons for all differences in those counts or provide a full account of missing observations. It does not report a missing-data method, such as an imputation approach, or sensitivity analyses to assess the effect of missing data. The stated eligibility condition of sufficient efficacy data for at least one endpoint is not the same as a detailed rule for handling missing measurements at particular time points.

The endpoint description notes that one participant was incorrectly administered BUD 160/FM 9.0 rather than BUD 160/Foradil 12.0 at Period 4. That participant was included in the efficacy analysis set but not the safety analysis set for BUD 160/Foradil 12.0. This is an important treatment-allocation detail when interpreting the different efficacy and safety group counts.

The registry record does not report the full ANCOVA model, its covariates, or how the crossover sequence and period were incorporated. It also does not report a prespecified analysis population beyond the efficacy set description. These omissions limit independent assessment of model assumptions, missing-data handling, and the robustness of the reported comparisons.

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 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists zero serious adverse events among participants at risk in each treatment group: 54 for BUD 160/FM 2.25, 53 for BUD 160/FM 4.5, 53 for BUD 160/FM 9.0, 51 for BUD 160, and 50 for BUD 160/Foradil 12.0. These are counts of participants with serious adverse events in the listed groups; the registry lists no serious adverse event terms.

Other adverse events were reported for 1, 1, 5, 2, and 0 participants, respectively, across those groups. These counts describe what was recorded and should not be taken as evidence that one regimen is safer than another. The study involved relatively small group counts and single-dose treatment periods, so the registry safety figures are limited for assessing uncommon events or safety over longer exposure.

Deaths are not reported in the registry record. The safety analysis group for BUD 160/Foradil 12.0 included 50 participants, while the efficacy group included 51. The endpoint description explains that one participant received a different treatment at Period 4 and was excluded from the safety analysis set for that Foradil group.

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

The posted primary analyses describe differences in average FEV1 over the 12 hours after single-dose treatment periods in children with asthma. The sponsor’s ANCOVA estimates are higher for the formoterol-containing regimens than for BUD 160, and the reported confidence intervals for those comparisons exclude zero. The direct comparison between the 4.5 and 9.0 µg Symbicort regimens has an interval that includes zero, so the posted analysis does not clearly distinguish those two regimens on this outcome.

These statistical results do not by themselves establish how important the differences are in clinical terms. The registry record does not report a threshold for a clinically important change in average FEV1. A p-value addresses compatibility with a statistical null model, while the estimated difference and its confidence interval describe magnitude and precision. Neither alone captures all dimensions of how a treatment might matter to participants.

The findings are limited to a short observation period after single doses in this study population. They do not establish effects with repeated or long-term use, effects on symptoms or quality of life, or results in people outside the enrolled age group. The registry record does not report these outcomes as primary endpoints.

Safety results should be interpreted on their own terms. Zero serious adverse events were recorded in the listed treatment groups, but the group sizes and limited exposure do not establish the absence of risk. The other adverse event counts also do not support a definitive comparative safety conclusion. These are descriptions of registry results, not medical advice or a recommendation about treatment.

18. Why This Trial Matters Statistically

This trial illustrates why the design and analysis both matter when interpreting clinical comparisons. In a crossover study, participants receive treatments across different periods, and the data can contain within-participant information. A simple comparison of group summary means cannot fully reproduce an analysis that accounts for the crossover structure. The registry’s sponsor-reported ANCOVA results and the separate unadjusted recalculations therefore should not be treated as interchangeable.

It also illustrates the value of reading estimates together with confidence intervals. The primary comparisons with BUD 160 have positive sponsor-reported differences and intervals excluding zero, while the comparison between the 4.5 and 9.0 µg regimens has an interval that spans zero. This distinction is more informative than treating every p-value as a simple yes-or-no conclusion, although the practical importance of the estimates cannot be determined without a clinical threshold.

Finally, the study presents several treatment contrasts and secondary outcomes, but the registry record does not report a multiplicity plan or the full statistical model. Recognizing what is and is not documented helps readers avoid giving isolated secondary findings more weight than warranted. The case also shows why trial planning numbers must be separated from actual enrollment and why sample-size illustrations based on observed effects are not evidence of the trial’s power.

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 assessed single-dose treatment periods and followed FEV1 for 12 hours after dosing. It therefore does not answer questions about longer-term use or outcomes outside that observation period. The population was children with asthma aged 6 to under 12 years; the registry results do not establish whether the same estimates apply to other age groups or populations.

The crossover format makes full analysis details particularly relevant. Although the registry identifies ANCOVA, it does not report the model terms, covariates, treatment sequence, or washout interval. The absence of those details limits independent evaluation of how period effects and within-participant correlation were addressed. The recalculated unadjusted comparisons cannot resolve this issue, and the discrepancy means the sponsor analysis takes precedence.

The registry does not report the original sample-size justification, handling of missing data, sensitivity analyses, or multiplicity strategy. It also does not report a clinical importance threshold for the FEV1 difference. These gaps limit assessment of whether the study was planned to detect a meaningful effect, how robust results are to missing observations, and how to interpret the many comparisons.

Enrollment was 54, with primary endpoint group counts between 51 and 54 and smaller safety counts for the Foradil group. The safety observation is based on limited exposure, and the record does not report deaths. One participant’s treatment was incorrectly administered at Period 4 and that participant was excluded from the Foradil safety set, though included in the efficacy set. These details should be considered when reading the different analysis counts.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study in Asthmatic Children (6 to <12 Yrs) Comparing Single Doses of Formoterol and Foradil® Evaluating Efficacy — NCT01136655.
• Registry record last updated 2013-10-31; status last verified 2013-10.
• Results first posted 2013-08-30.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, quadruple-masked, phase 2, five-period crossover study of single-dose formoterol-containing regimens and Foradil in children with asthma aged 6 to under 12 years. It enrolled 54 participants. The primary outcome was average FEV1 over 12 hours after dosing.

Sponsor-reported ANCOVA results show positive least-squares mean differences for the formoterol-containing Symbicort groups compared with BUD 160. The comparison between the 4.5 and 9.0 µg regimens did not clearly distinguish their average FEV1. The registry reports no serious adverse events in the listed treatment groups. The original sample-size rationale, multiplicity plan, missing-data methods, and full ANCOVA specification are not reported in the registry record.