Single Dose Study of the Effect of Formoterol Fumarate in Combination With Mometasone Furoate Inhaled Via a Pressurized Metered Dose Inhaler (pMDI) in Children Aged 5-11 Years Old With Persistent Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Single Dose Study of the Effect of Formoterol Fumarate in Combination With Mometasone Furoate Inhaled Via a Pressurized Metered Dose Inhaler (pMDI) in Children Aged 5-11 Years Old With Persistent Asthma (NCT00746330), a randomized phase 2 study. The primary outcome is The Standardized Forced Expiratory Volume in 1 Second (FEV1) Using Area Under the Curve (AUC) From 0 to 12 Hours (0-12h) Post-dose by Treatment.

2. Clinical Question

3. Trial Design

This was a randomized, quadruple-masked, multicentre, four-way crossover study listed as Phase 2. The registry record gives enrollment as 32 and status as completed. The study began in 2008-08, with primary completion in 2009-04. The sponsor is Novartis.

In a crossover design, participants receive multiple treatments in sequence, so each participant can contribute outcome information under more than one treatment. The listed treatment conditions were mometasone furoate/formoterol fumarate (MFF), formoterol fumarate 12 μg via pMDI (F12M), formoterol fumarate 12 μg via DPI (F12D), and placebo. Participants were assigned to different treatment sequences. The sequence descriptions indicate that the single doses were separated by a washout period of 6-7 days. The record does not provide the number of participants assigned to each sequence.

Double-dummy masking uses matching placebo preparations so that differences in the devices or treatment presentations do not readily reveal the assigned treatment. The registry record labels masking as quadruple; it does not specify which groups of people were masked.

The primary outcome was standardized FEV1 AUC from 0 to 12 hours after each treatment. The planned observation period and the single-dose crossover structure make the outcome a measure of short-term post-dose response, rather than a measure of long-term asthma control. The registry record also lists serial FEV1, FVC and PEF measures, along with plasma and urine formoterol assessments. Numeric results for those secondary measures are not reported in the registry record.

The original rationale for the sample size, the intended model for the crossover analysis, and details of sequence allocation are not reported in the registry record. The approximate comparisons calculated from posted summaries should therefore not be read as a reconstruction of the trial’s original analysis plan.

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.

Period 1

Reasons for not completing this period:

Period 2

Period 3

Period 4

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set

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 The Standardized Forced Expiratory Volume in 1 Second (FEV1) Using Area Under the Curve (AUC) From 0 to 12 Hours (0-12h) Post-dose by Treatment, measured over From 0 to 12 Hours (0-12h) post-dose, after each treatment administered (approximately 1 treatment a week for 4 weeks of treatment)..

The primary endpoint was the standardized forced expiratory volume in 1 second (FEV1) area under the curve from 0 to 12 hours after each treatment. FEV1 is the volume of air exhaled in the first second of a forced exhalation. The endpoint summarizes measurements over the post-dose observation period rather than focusing on a single time point.

The registry record says the AUC was calculated using the trapezoidal rule at planned measurement times, through the last recorded measurement before rescue medication. The AUC was then divided by the length of time represented by the included measurements. The resulting unit was liters, described in the record as a weighted average of acceptable FEV1 measurements recorded over the observation period.

Standardizing by the measurement duration was intended to account for participants who did not complete all measurements during the 12-hour observation period without using rescue medication. This approach gives a summary of the observed post-dose FEV1 course, but it does not restore measurements that were not collected. The precise influence of rescue medication, incomplete measurement schedules, and other missing observations on the primary analysis is not fully described in the registry record.

AUC can be useful when a treatment’s response may change over time, because it incorporates the observed trajectory rather than selecting one measurement time. It also compresses that trajectory into a single value, so it does not show exactly when any difference arose or how the response varied at individual time points. The primary endpoint concerns a single-dose, 0–12-hour response; it is not itself a measure of sustained benefit or long-term outcomes.

7. Results Posted in the Registry

• MFF10: mean 1.77 versus 1.71 on control; difference 0.06 (95% CI -0.06 to 0.18), standardized effect d = 0.25; z-test p = 0.328.
• F12M: mean 1.77 versus 1.71 on control; difference 0.06 (95% CI -0.06 to 0.18), standardized effect d = 0.26; z-test p = 0.314.
• F12D: mean 1.80 versus 1.71 on control; difference 0.09 (95% CI -0.03 to 0.21), standardized effect d = 0.38; z-test p = 0.142.

8. Statistical Interpretation

9. Statistical Methods Explained

What does a least-squares mean represent?

A least-squares mean is a model-based estimate of an outcome mean, often adjusted for terms included in the statistical model. It is not necessarily the same as a simple arithmetic average of all observed values. The registry record labels the primary endpoint statistic as a least-squares mean and gives a 95% confidence interval for each treatment. However, the model terms and estimation details are not reported in the registry record. The posted treatment estimates can be described, but their precise adjustment cannot be reconstructed from the registry information.

In a crossover trial, observations from the same participant are related: a participant’s measurements under different treatments may be more alike than measurements from different participants. A crossover analysis can use this within-participant structure and may also account for treatment period or sequence. The statistical plan and model details are not reported in the registry record. A simple comparison of treatment-level summaries does not preserve the participant-level pairing, so it is not equivalent to a complete crossover analysis.

What is the role of the confidence interval?

A confidence interval describes the uncertainty around an estimate under the method’s assumptions. A narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the underlying value. The 95% intervals for the treatment means describe uncertainty around each estimated mean. They should not be interpreted as containing 95% of individual participants’ measurements.

For a treatment difference, the interval is more directly informative about the contrast. If it includes zero, the data and calculation method are compatible with no difference as well as with differences in either direction. If the interval extends across a wide range, the estimate is imprecise even if its center is not zero. The recalculated intervals in this analysis all include zero. They are approximate intervals based on posted summaries and are not estimates from a reported crossover model.

Why is an unadjusted comparison limited?

The recalculated differences are simple, unadjusted comparisons of the treatment and placebo summaries. They do not account for the study’s repeated measurements within participants, treatment sequence, or period. The standard deviations used in the calculations are approximate. The unadjusted p-values likewise should not be mistaken for p-values from a sponsor analysis of the crossover data. Since the registry record does not report the sponsor’s primary inferential analysis, there is no basis to claim that these recalculations reproduce it.

An unadjusted p-value summarizes how unusual data at least as discrepant as those observed would be under a particular null hypothesis and statistical model. It does not measure the probability that the null hypothesis is true, nor does it measure the size or clinical importance of an effect. Here, the values are attached to the approximate recalculations. They do not incorporate a reported adjustment for multiple comparisons.

Why can over-dispersion matter?

For count outcomes, over-dispersion means that variability exceeds what a simple model assumes. A model that understates variability can produce confidence intervals that are too narrow and tests that are too optimistic. The primary outcome is continuous, not a count, so over-dispersion is not the main issue for the reported FEV1 means. More generally, model choice should reflect the data structure and variability. For this trial, the repeated observations and crossover design are more directly relevant concerns than count-data over-dispersion.

How does the endpoint construction affect interpretation?

The endpoint uses a trapezoidal AUC based on planned measurement times, and the record says values after the last measurement before rescue medication were excluded from the calculation. Dividing the AUC by the length of time represented produces a duration-standardized summary. This can make summaries more comparable when observation durations differ, but it does not eliminate uncertainty caused by incomplete measurements or rescue medication. The rules for other missing data and the statistical handling of those cases are not reported in the registry record.

An AUC summary has a different interpretation from a measurement at a particular time. It combines the levels observed across the interval and weights them according to the measurement schedule. A treatment contrast in AUC therefore does not say that the same contrast occurred at every time point. The listed secondary outcomes include serial FEV1, FVC and PEF measures at specified post-dose times, but numerical results for these measures are not reported in the registry record.

What information is missing from the statistical record?

The registry record does not report the original sample-size justification, the prespecified analysis model, treatment-period or sequence terms, a multiplicity strategy, interim analyses, or detailed rules for missing data beyond the endpoint’s stated AUC construction. It identifies the Full Analysis Set for the primary outcome, but does not define membership or explain how exclusions were handled. Those omissions limit how fully the treatment estimates and uncertainty can be assessed.

The planning figures discussed separately are illustrations calculated from observed effects under stated assumptions. They are not retrospective measures of the trial’s power and are not evidence that the original trial was designed using those assumptions. In general, a power calculation asks how often a chosen analysis would detect a specified effect if that effect and the calculation assumptions were true. Planning estimates can help show how sample size depends on effect size, but they do not resolve limitations in the trial’s reported analysis.

10. Confidence Intervals and Precision

The treatment-specific 95% confidence intervals give a sense of the uncertainty around each posted least-squares mean. MFF10 is reported as 1.77 liters with an interval from 1.69 to 1.86; F12M is 1.77 liters with an interval from 1.69 to 1.85; F12D is 1.8 liters with an interval from 1.72 to 1.89; and placebo is 1.71 liters with an interval from 1.62 to 1.79. These intervals overlap. Overlap between separate treatment-mean intervals is not itself a formal test of the difference between treatments.

The recalculated comparisons give a more direct, though approximate, view of contrast precision. MFF10 versus placebo has an estimated difference of 0.06 liters and a confidence interval from -0.060 to 0.180. F12M versus placebo has an estimated difference of 0.06 liters and a confidence interval from -0.057 to 0.177. F12D versus placebo has an estimated difference of 0.09 liters and a confidence interval from -0.030 to 0.210. Each interval includes zero, and each spans values in both directions.

In general, the width of an interval reflects both the amount of information and the variability assumed by the analysis. The recalculated intervals are approximate and use summaries rather than participant-level crossover data, so they do not capture all features of the study design. The registry record does not report a sponsor-model confidence interval for these treatment contrasts. This means precision should be interpreted cautiously: the estimates are not precise enough to distinguish a range of plausible differences from no difference using these approximate calculations.

Confidence intervals also do not indicate whether an effect is important to patients. The registry record does not give a threshold for a clinically important difference in standardized FEV1 AUC. Statistical uncertainty and clinical importance are separate questions, and the posted summaries alone do not answer both.

11. 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 computed from the observed effect, using a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The calculation considers the stated effect or a fraction of it: 100%, 75%, or 50% of the observed effect. The original trial’s own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for an illustrative design to have an 80% chance of detecting the specified effect under the calculation assumptions, if that effect and those assumptions hold. The 90% power column gives the corresponding number for a 90% chance. These are planning quantities, not guarantees about any future study’s result. They are also not directly tailored to the crossover structure of this trial: the stated calculation assumes equal allocation between two arms.

The rows vary by contrast because the observed effects and estimated variability differ. They also show that planning for 75% or 50% of the observed effect requires more participants per arm than planning for the full observed effect. In general, smaller target effects are harder to distinguish from random variation and therefore require larger samples, all else equal. The displayed planning curves express that same relationship across the assumed effect sizes.

For example, the F12D-versus-placebo illustration gives 112 participants per arm for 80% power when planning for 100% of the observed effect, and 445 participants per arm when planning for 50%. These figures illustrate sensitivity to the assumed effect size; they do not imply that the original crossover trial should have enrolled those numbers or that its results had any particular probability of being statistically significant. This is not observed power.

12. 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 = 0.060; pooled standard deviation σ = 0.243.
2. n = 2 × (1.96 + 0.842)² × 0.243² / 0.060² = 258.4, rounded up to 259 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 <- 0.0600000000000001                      # observed difference in means
sigma <- 0.243434769928203                     # 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(746330)
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 = 259 (80% power), 346 (90% power)
 75% of observed effect: n per arm = 460 (80% power), 615 (90% power)
 50% of observed effect: n per arm = 1,034 (80% power), 1,384 (90% power)
power.t.test: 259.4 
Simulated power at n = 259 per arm: 0.798 (20000 replicates)

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

13. Multiplicity, Missing Data and Analysis Populations

The study addressed several questions: the primary standardized FEV1 AUC comparison, serial lung-function measurements, and plasma and urine formoterol assessments. The registry record lists five secondary outcome measures in addition to the primary endpoint. When several outcomes or treatment comparisons are examined, the chance of obtaining at least one apparently unusual result can increase. A prespecified multiplicity strategy can control or otherwise address that issue, but such a strategy is not reported in the registry record.

The three treatment-versus-placebo p-values discussed in the interpretation are unadjusted recalculations. They should not be treated as multiplicity-adjusted findings or as the sponsor’s analysis. The registry record lists no analysis entries and does not report whether adjustments were planned or applied to the original analyses. Numeric results for the secondary measures are not reported in the registry record, so their estimates and uncertainty cannot be assessed alongside the primary outcome.

The primary analysis population is identified as the Full Analysis Set. The definition of that set, including eligibility after randomization and any exclusions, is not reported in the registry record. The treatment-specific primary endpoint sample sizes are 32 for MFF10, 31 for F12M, 30 for F12D, and 31 for placebo. Because this is a crossover study, those counts refer to treatment observations and should not be added as if they represented distinct participants.

The endpoint definition specifies that the AUC calculation used measurements through the last recorded time before rescue medication and was standardized by the duration included. That is a stated feature of the outcome construction, but broader missing-data methods are not reported in the registry record. The record does not explain how unavailable measurements, incomplete treatment periods, or missing outcomes were handled in the underlying model. It also does not describe interim analyses or an analysis plan for incomplete crossover sequences. Those omissions constrain interpretation of both the estimates and their precision.

14. 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.

The registry record reports serious adverse events for four treatment groups. The number at risk was 31 for F12M, 31 for F12D, 32 for MFF10, and 31 for placebo. The serious adverse event count was zero in each group. The record also reports zero other adverse events in each group, using the same group-specific numbers at risk.

These are event counts as reported, not proof that no adverse events could occur. The record’s safety figures describe the reported groups and exposure in this study; the small enrollment and single-dose design limit the amount of safety information they can provide. The death entries are null, so death counts are not reported in the registry record. No serious adverse event terms are listed.

In this crossover study, participants received multiple treatments over separate periods. The group counts should not be interpreted as four wholly separate sets of people. The registry record does not provide details about how adverse events were attributed across treatment periods, their timing, or their severity beyond the serious-versus-other categories. The figures therefore give a concise account of the posted counts, but not a complete characterization of safety.

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

The primary endpoint offers a summary of lung function over the 0–12-hour period after a single dose. The posted treatment means range from 1.71 liters for placebo to 1.8 liters for F12D, with MFF10 and F12M each reported at 1.77 liters. The approximate recalculated treatment-versus-placebo differences are positive, but all three confidence intervals include zero and the unadjusted p-values are 0.328, 0.314, and 0.142.

Those results do not show a precise separation from placebo in the approximate comparisons. They also do not demonstrate equivalence or rule out potentially relevant differences. The intervals include values below and above zero, and no clinical-importance threshold for this endpoint is reported in the registry record. A statement that the treatments are the same, or that a meaningful difference is impossible, would go beyond these data.

The treatment-level estimates are not the same as a complete analysis of the crossover trial. Participants received multiple treatments, so a suitable comparison can use within-participant information and account for the treatment sequence or period. The registry record does not provide the sponsor’s model-based comparison results. The displayed recalculations use summary statistics and should not replace that missing analysis.

The endpoint is also limited to a short-term, single-dose response summarized over the stated observation period. It does not establish long-term effects, sustained control, or outcomes beyond the measures listed for this trial. The registry record’s secondary outcome descriptions include repeated lung-function measurements and pharmacokinetic assessments, but their numeric results are not reported in the registry record.

The appropriate conclusion is therefore descriptive and bounded: the posted primary outcome means are close in magnitude, and the approximate unadjusted comparisons are uncertain. They do not, by themselves, answer every clinical question about these treatments or the broader course of asthma. No medical decision should be inferred from these registry summaries alone.

16. Why This Trial Matters Statistically

This study is statistically informative because it uses a randomized, masked crossover design for a short-term treatment comparison. In a crossover study, each participant can contribute observations under multiple treatments, which can help separate treatment differences from stable differences between participants. That advantage depends on an analysis that respects the paired structure and accounts appropriately for treatment order and period. The registry record does not report enough model detail to evaluate that analysis.

The endpoint also illustrates how a clinical outcome can be constructed to summarize a time course. The standardized FEV1 AUC combines multiple post-dose measurements while adjusting the summary for the duration represented. That offers a compact measure of response, but it cannot describe the shape of the response at each measurement time. The record’s secondary endpoint descriptions recognize this distinction by listing serial lung-function outcomes, although their numeric results are not reported in the registry record.

The primary results demonstrate why estimates and confidence intervals should be read together. Treatment means alone might encourage a simple ranking, but the approximate contrast intervals are broad and include zero. The associated recalculated p-values do not resolve the uncertainty, especially because they are unadjusted and do not reflect a reported crossover model.

Finally, planning illustrations based on observed effects make the dependence of sample size on the target effect explicit. Smaller effects require larger planned samples under the stated assumptions. Those calculations are not a substitute for the trial’s original design rationale, which is not reported, and they do not measure the study’s observed power. Together, these features make the record a useful example of how design, analysis structure, endpoint construction, and precision all shape interpretation.

17. 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.

Several limitations specific to this trial affect interpretation. The enrollment was 32, and treatment-specific primary outcome counts range from 30 to 32. Those counts provide a limited base for estimating treatment contrasts, especially when the uncertainty is assessed using approximate summary-based calculations rather than participant-level crossover data.

The study used a four-way crossover design with multiple treatment sequences. The registry record describes the treatment sequence structure and a washout period of 6-7 days, but does not report the statistical model, details of sequence allocation, or how possible period and sequence effects were addressed. The recalculated comparisons therefore do not reflect the full design information and should be regarded as approximate.

The primary outcome is a duration-standardized AUC through the last measurement before rescue medication. While the record explains this construction, it does not report how other forms of missingness were handled or how incomplete treatment sequences were analyzed. The definition of the Full Analysis Set is also not reported in the registry record.

The record lists several secondary outcomes, but their numeric results are not reported in the registry record. It also does not report the original sample-size justification, a multiplicity strategy, or interim analyses. These gaps prevent a complete assessment of the prespecified statistical plan and the consistency of evidence across outcomes.

Finally, this was a single-dose study in children aged 5–11 years with persistent asthma. Its primary endpoint covers a 0–12-hour period after dosing. The results should not be extended to longer-term outcomes or populations not described in the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Single Dose Study of the Effect of Formoterol Fumarate in Combination With Mometasone Furoate Inhaled Via a Pressurized Metered Dose Inhaler (pMDI) in Children Aged 5-11 Years Old With Persistent Asthma — NCT00746330.
• Registry record last updated 2011-06-07; status last verified 2011-06.
• Results first posted 2011-04-14.
• 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.

21. Record Summary

NCT00746330 was a completed randomized, quadruple-masked, multicentre, four-way crossover Phase 2 study sponsored by Novartis. It enrolled 32 children aged 5–11 years with persistent asthma. The study began in 2008-08 and reached primary completion in 2009-04.

The primary endpoint was standardized FEV1 AUC from 0 to 12 hours after a single treatment. Posted least-squares means ranged from 1.71 liters for placebo to 1.8 liters for F12D. Approximate unadjusted recalculated treatment-versus-placebo differences were 0.06 liters for MFF10, 0.06 liters for F12M, and 0.09 liters for F12D; all corresponding confidence intervals included zero. The registry record does not report the sponsor’s crossover-model comparisons.

The record reports zero serious and zero other adverse events in each listed group. Death counts are not reported in the registry record. The original sample-size rationale, detailed analysis plan, and numeric secondary outcome results are not reported in the registry record.