Safety and Blood Level Study of Unit Dose Budesonide: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Safety and Blood Level Study of Unit Dose Budesonide (NCT00627679), a randomized phase 1 study. The primary outcome is Cmax of of Budesonide After Administration of Pulmicort and Three Dose Levels of MAP0010.

2. Clinical Question

This was a pharmacokinetic and tolerability study, not a trial of clinical outcomes. Its primary question concerns the concentration of budesonide measured in plasma after a single dose. Cmax is the highest measured concentration during the stated assessment period. It provides a summary of the peak exposure observed under each treatment, but does not by itself describe the full concentration-time profile or establish a clinical effect.

The registry reports four treatment conditions: Treatment A was Pulmicort Respules, while Treatments B, C, and D were MAP0010 at low, intermediate, and high dose levels, respectively. The study used a crossover arrangement, so participants were assigned to treatment sequences that included the different conditions. The record describes treatment visits as separated by a 48-72 hour washout period.

The posted mean Cmax values were 303.5 pg/mL for Treatment A, 106.2 pg/mL for Treatment B, 239.9 pg/mL for Treatment C, and 434.5 pg/mL for Treatment D. The registry also posts unadjusted comparisons of each MAP0010 condition with Treatment A. These summaries describe the measured concentration data; they do not establish that one treatment is clinically preferable or characterize outcomes beyond the recorded pharmacokinetic and tolerability measures.

3. Trial Design

The registry identifies this as a randomized, triple-masked, active-controlled, single-dose, four-arm, four-period crossover Phase 1 study. Its stated purpose was to evaluate tolerability and pharmacokinetics of three MAP0010 dose levels in comparison with budesonide inhalation suspension in healthy volunteers. The record lists enrollment of 16 and status as completed.

In a crossover design, participants receive more than one study treatment in an ordered sequence rather than remaining in only one treatment group throughout. The registry lists four sequences: A, B, D, C; B, C, A, D; C, D, B, A; and D, A, C, B. Treatment A corresponds to Pulmicort Respules, and Treatments B, C, and D correspond to MAP0010 low, intermediate, and high dose levels. The record says treatment visits were separated by a 48-72 hour washout period. This arrangement allows observations under different treatments to be collected from the same participants, although interpretation can depend on the sequence and period structure.

The primary outcome population is described as patients with available data at specified time points. The term “patients” appears in the registry description, while the study summary describes healthy volunteers. Posted outcome counts are 16 for Treatment A, 15 for Treatment B, 16 for Treatment C, and 16 for Treatment D. The record does not explain why Treatment B has a count of 15 or state how unavailable measurements were handled.

The registry record does not report the planned sample-size justification, the original statistical analysis plan, or details of a model for the crossover structure. It also does not report whether period, sequence, or carryover effects were assessed. The design information therefore describes the intended treatment arrangement, but does not establish the specific statistical procedures used for the primary endpoint.

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: All subjects received all 4 treatments in a randomly assigned order. The treatments were: Treatment A: Pulmicort Respules® Treatment B: MAP0010 low dose Treatment C: MAP0010 intermediate dose Treatment D: MAP0010 high dose The sequences were Treatments ABDC, BACD, CDBA, DACB.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Patients with available data at specified time points are included in the analysis population.

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 Cmax of of Budesonide After Administration of Pulmicort and Three Dose Levels of MAP0010, measured over 8 hours.

The primary endpoint is the maximum concentration of budesonide in plasma, called Cmax, measured over 8 hours and expressed in pg/mL. Plasma is the clear portion of blood, and a concentration measurement describes the amount of the drug measured in a given volume of that fluid. The registry reports the endpoint as a mean with standard deviation for each treatment condition.

Cmax is used in pharmacokinetic studies as a concise measure of peak exposure after administration. Comparing this measure across treatment conditions can describe how the observed peak concentrations differ in the study. It is only one part of a concentration-time profile: it does not state when the peak occurred, how long concentrations remained elevated, or the total exposure across the assessment period. Those are distinct pharmacokinetic features and should not be inferred from Cmax alone.

The reported mean Cmax values were 303.5 pg/mL for Pulmicort Respules, 106.2 pg/mL for MAP0010 low dose, 239.9 pg/mL for MAP0010 intermediate dose, and 434.5 pg/mL for MAP0010 high dose. The corresponding standard deviations were 177.4, 63.47, 140.1, and 246.9 pg/mL. These summaries show the average and the observed spread of measurements within each treatment condition. The endpoint is a laboratory measure; by itself, it is not a measure of symptom improvement, disease control, or a clinical benefit.

The registry's primary endpoint description says participants with available data at specified time points were included. It does not give a more detailed account of data availability or the analysis population. The meaning of the endpoint is therefore clear as a peak plasma concentration, while the record leaves some aspects of its analysis and completeness unspecified.

7. Results Posted in the Registry

• Treatment B: mean 106.20 versus 303.50 on control; difference -197.30 (95% CI -289.97 to -104.63), standardized effect d = -1.46; z-test p = <0.001.
• Treatment C: mean 239.90 versus 303.50 on control; difference -63.60 (95% CI -174.36 to 47.16), standardized effect d = -0.40; z-test p = 0.260.
• Treatment D: mean 434.50 versus 303.50 on control; difference 131.00 (95% CI -17.97 to 279.97), standardized effect d = 0.61; z-test p = 0.085.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary endpoint is continuous: Cmax is a measured concentration, and the registry summarizes it using a mean and standard deviation. A mean gives the arithmetic center of the observed values, while the standard deviation describes their spread around that mean. Neither measure alone reveals the distribution's shape, whether there are unusually influential observations, or how individual participants' measurements changed across crossover periods.

What does a mean difference represent?

A mean difference expresses the contrast between two treatment means on the endpoint's original scale, here pg/mL. In the posted comparisons, Treatment A is the reference and each MAP0010 condition is compared with it. A negative estimate indicates that the MAP0010 treatment's posted mean is lower than the comparator mean; a positive estimate indicates that it is higher. For example, the low-dose comparison is -197.3 pg/mL, while the intermediate-dose comparison is -63.6 pg/mL and the high-dose comparison is 131.0 pg/mL. These estimates summarize the observed contrast and do not, on their own, show whether a difference is statistically distinguishable from zero.

The registry's comparisons are labelled as recalculated and are simple unadjusted calculations from the posted summary statistics. They are not described as adjusted estimates from a crossover model. In a crossover study, measurements from the same participant under different conditions are generally related. A comparison that uses that pairing can have different uncertainty from a calculation that treats treatment summaries without the within-participant information. The registry does not provide the paired data needed to reconstruct that relationship, nor does it report the original analysis model. The posted recalculated comparisons should therefore be interpreted as summary-based contrasts rather than as a complete analysis of the crossover design.

How should the confidence intervals be read?

A confidence interval describes the range of effect estimates that are compatible with the data and the method used to calculate the interval, under that method's assumptions. It conveys uncertainty about the estimated mean difference. For low-dose Treatment B, the interval is -290.0 to -104.6 pg/mL. For intermediate-dose Treatment C, it is -174.4 to 47.16 pg/mL. For high-dose Treatment D, it is -17.97 to 280.0 pg/mL. Intervals that include zero do not rule out no mean difference under the calculation used. An interval excluding zero indicates incompatibility with a zero difference at the corresponding unadjusted confidence level, subject to the calculation's assumptions.

A confidence interval is not a range containing every participant's value, nor does it directly give the probability that the true effect lies within that particular interval. Its width is a measure of precision: wider intervals indicate greater uncertainty about the effect size. The intervals for the intermediate and high dose comparisons extend across zero, and the high-dose interval includes both negative and positive values. The interpretation is consequently not simply a question of whether an estimate is positive or negative; the uncertainty around that estimate matters.

What does the p-value add?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The low-dose comparison has p < 0.001; the intermediate-dose comparison has p = 0.26; and the high-dose comparison has p = 0.085. These are unadjusted p-values. The registry does not report multiplicity adjustment, so the values should not be read as familywise-error-controlled tests across the set of treatment comparisons.

The interpretation of these p-values depends on the method used to generate the estimates and uncertainty. In particular, a crossover trial can call for accounting for within-person correlation and treatment period. Those details are not reported for the registry's primary analysis, and the displayed recalculations are unadjusted summary-statistic comparisons. The p-values describe those calculations, rather than a documented prespecified crossover analysis.

Why does spread matter?

Standard deviations quantify variability in the measured Cmax values. The posted standard deviations are 177.4 pg/mL for Treatment A, 63.47 pg/mL for Treatment B, 140.1 pg/mL for Treatment C, and 246.9 pg/mL for Treatment D. Greater variability can make an estimated mean less precise when the sample size is limited. In a crossover design, however, the precision of a treatment contrast also depends on how strongly each participant's measurements under different treatments are related. Separate treatment standard deviations do not provide that information.

Over-dispersion is a general concern when observed data vary more than a model assumes; failing to account for that extra variability can make standard errors too small and intervals too narrow. It is a general statistical issue, not a reported finding about this trial. The registry does not report a model check or a specific assessment of over-dispersion for this endpoint.

What can be concluded about analysis choices?

The registry reports no posted analysis records for this outcome and does not describe a statistical model, adjustments for multiple comparisons, interim analyses, or handling of missing measurements. It does define the analysis population as participants with available data at specified time points. These omissions do not demonstrate that particular procedures were or were not performed; they mean those details are not reported in the registry record. Consequently, the most transparent reading is to describe the posted arm means and the recalculated unadjusted contrasts as such, while keeping the crossover design and incomplete analysis detail in view.

10. Confidence Intervals and Precision

Precision concerns how much uncertainty surrounds an estimate. The standard deviations describe the observed spread of Cmax measurements within treatment conditions, while confidence intervals for mean differences describe uncertainty in the contrasts. The reported standard deviations range across treatment conditions from 63.47 pg/mL for Treatment B to 246.9 pg/mL for Treatment D. These are not standard errors or confidence intervals: they describe variation among observations rather than the precision of a treatment mean.

The low-dose comparison has an estimated mean difference of -197.3 pg/mL and a confidence interval from -290.0 to -104.6. This interval lies below zero. The intermediate-dose estimate is -63.6 pg/mL, with an interval from -174.4 to 47.16. The high-dose estimate is 131.0 pg/mL, with an interval from -17.97 to 280.0. The latter two intervals include zero, indicating that their unadjusted calculations do not precisely distinguish the estimates from no mean difference. Their ranges also allow differences of meaningful magnitude in either direction, so a nonsignificant result is not evidence that the treatments are equivalent.

These intervals are based on simple unadjusted recalculations from the posted summaries. The record does not report the primary analysis model or its confidence intervals. In a crossover study, the uncertainty of a within-participant treatment contrast depends on the relationship between measurements from the same participant. That relationship is not captured by treatment-specific means and standard deviations alone. Thus, the displayed intervals provide a summary-based view of precision, not a substitute for a documented crossover analysis.

The outcome counts are 16 for Treatment A, 15 for Treatment B, 16 for Treatment C, and 16 for Treatment D. The reason for the lower count in Treatment B and any impact of unavailable measurements are not reported in the registry record. With a small study, estimates can be sensitive to individual observations, but the record does not provide participant-level values to assess that sensitivity. The intervals should be read alongside these limitations rather than as exact boundaries on all plausible treatment effects.

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 sample-size figures are planning illustrations based on the observed effect, not the trial's original design calculation. The registry record does not report the original sample-size justification or the assumptions used when the study was designed. The displayed planning scenarios use a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each scenario considers detecting a stated fraction of the observed effect. The figures are participants per arm, not total participants or total events.

The 80% power column gives the illustrative number of participants per arm for a design with an 80% chance of detecting the specified effect under those assumptions, if the effect and model assumptions are correct. The 90% power column gives the corresponding per-arm planning figure for a 90% chance. These are design-planning quantities; they do not describe the chance that the completed trial detected an effect after the results were observed. This is not observed power.

Rows for 100% of the observed effect use the observed contrast as the target effect; rows for 75% or 50% use smaller target effects. Smaller effects are harder to distinguish from background variation, so planning for a smaller effect requires more participants. This relationship is visible across the displayed scenarios for each comparison. For example, in the low-dose comparison, planning for 100% of the observed effect gives 8 participants per arm for 80% power and 10 for 90% power, while planning for 50% gives 30 and 40, respectively. These are illustrations only, not estimates of what this trial needed or proof of what its actual design could detect.

The illustrations use two-arm assumptions and do not account for the crossover structure described in the registry. They should not be treated as a direct redesign calculation for this four-period trial. Their purpose is to show how planning figures change when the target effect or desired power changes, not to replace the trial's missing original design rationale.

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 = -197.300; pooled standard deviation σ = 134.992.
2. n = 2 × (1.96 + 0.842)² × 134.992² / -197.300² = 7.3, rounded up to 8 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 <- -197.3                      # observed difference in means
sigma <- 134.991643751599                     # 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(627679)
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 = 8 (80% power), 10 (90% power)
 75% of observed effect: n per arm = 14 (80% power), 18 (90% power)
 50% of observed effect: n per arm = 30 (80% power), 40 (90% power)
power.t.test: 8.4 
Simulated power at n = 8 per arm: 0.776 (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 registry presents comparisons of each MAP0010 dose level with the Pulmicort Respules comparator. It does not report a multiplicity adjustment or a plan specifying how the family of comparisons was to be interpreted. The posted p-values are therefore described as unadjusted. When several comparisons are examined, the chance of at least one apparently unusual result can increase if each is interpreted using an unadjusted threshold. This is a general statistical concern; the record does not say whether another multiplicity procedure was used outside the posted results.

The registry record does not report a prespecified statistical analysis plan, interim analyses, or the model used for the primary endpoint. It does not state whether the analysis included treatment, period, sequence, or carryover terms, or whether it estimated a within-participant treatment contrast. These details are relevant because this is a four-period crossover study. The posted comparisons are simple unadjusted recalculations from treatment summaries and should not be mistaken for a reported crossover-model analysis.

The endpoint population is described as participants with available data at specified time points. The treatment-specific outcome counts are 16 for Treatment A, 15 for Treatment B, 16 for Treatment C, and 16 for Treatment D. The record does not explain the difference in counts, state why a measurement was unavailable, or describe imputation or other missing-data handling. It also does not report whether the analysis used all randomized participants or a different analysis population beyond the available-data description.

The registry posts no analysis records for this primary comparison. That absence does not establish that no analysis occurred; it means the analysis details and results of any sponsor-defined model are not reported in the registry record. Interpretation should consequently separate the directly posted means and standard deviations from the recalculated contrasts and recognize that the treatment of multiplicity, missing data, and crossover-specific structure remains undocumented.

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.

Most frequent non-serious adverse event terms

The adverse-event summary lists 16 participants at risk for serious adverse events under each treatment condition. It records zero participants affected by a serious adverse event for Treatment A, Treatment B, Treatment C, and Treatment D. The registry's serious-adverse-event term list is empty. These figures describe the recorded serious-event counts in this study; they do not establish that an event is impossible or provide a precise estimate of rare-event risk.

For other adverse events, the record lists 4 participants affected under Treatment A, 4 under Treatment B, 3 under Treatment C, and 3 under Treatment D, with 16 at risk in each condition. Those are counts, not rates calculated or compared. Because this was a crossover study, the same participants could contribute to more than one treatment condition; the group counts should not be interpreted as independent sets of people. The record does not provide event-level details in the summarized information, nor does it report a comparative safety analysis.

Deaths are recorded as null for all four conditions. This means the death figures are not reported in the registry record, rather than establishing a count of zero. The available safety summary is limited to the listed counts and should not be used to make broader safety conclusions.

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

The results describe measured peak plasma budesonide concentrations after single doses of Pulmicort Respules and three MAP0010 dose levels in a small Phase 1 crossover study of healthy volunteers. The posted mean Cmax was lower for the MAP0010 low and intermediate dose conditions than for the comparator, and higher for the high-dose condition. The simple unadjusted comparison for the low-dose condition had a confidence interval below zero and p < 0.001. The intervals for the intermediate- and high-dose comparisons included zero, leaving substantial uncertainty about the direction and size of their mean differences under those calculations.

These findings concern a pharmacokinetic endpoint, not a clinical outcome. Cmax describes the highest measured plasma concentration during the assessment period. It does not alone show the timing of that peak, total exposure, symptom response, disease control, or a treatment's clinical value. The study's stated purpose includes tolerability, but the posted adverse-event counts do not provide a detailed comparative analysis.

The results do not establish equivalence between MAP0010 and Pulmicort Respules, nor do intervals that include zero prove that there is no difference. Conversely, a low unadjusted p-value does not establish the clinical importance of the observed concentration contrast. The clinical meaning of any pharmacokinetic difference is not established by the registry summaries.

Interpretation is further limited because the registry does not report the analysis model for the crossover design, multiplicity procedures, or missing-data handling. The treatment summaries include 15 observations for low-dose Treatment B and 16 for each other condition, with no explanation of the count difference. The displayed mean differences and intervals are unadjusted recalculations from summaries, rather than documented estimates from a sponsor's crossover analysis. They should be read as descriptions of these posted data and not as definitive estimates of every aspect of treatment performance.

16. Why This Trial Matters Statistically

This study illustrates a common distinction in biostatistics between a treatment's measured concentration profile and a clinical outcome. The primary endpoint, Cmax, is a continuous pharmacokinetic measure that can characterize peak plasma exposure. Its usefulness does not make it interchangeable with symptoms, clinical response, or other outcomes. Careful interpretation depends on keeping the endpoint's meaning within its proper scope.

The crossover structure also matters statistically. Each participant was assigned to a sequence involving the four treatment conditions, with treatment visits separated by a 48-72 hour washout period. This allows comparisons across conditions within the study design, but the precision of a within-participant contrast depends on paired measurements. Treatment-specific means and standard deviations do not show the full relationship between repeated observations. Without a reported crossover model or paired results, summary-based contrasts cannot communicate all the information that the design may have collected.

The contrast between the low-dose interval and the intervals for the intermediate and high dose comparisons is another useful teaching point. An estimate alone does not convey precision, and a p-value alone does not convey effect size. The low-dose unadjusted interval lies below zero, whereas the other two intervals include zero and extend over a range of possible differences. These patterns should be described without treating a nonsignificant comparison as proof of equivalence or turning a statistically notable result into a claim of clinical importance.

Finally, the study record demonstrates why transparency about the analysis plan, missing observations, and multiplicity matters. The design is identifiable, and the posted endpoint summaries are interpretable, but key details about statistical handling are not reported in the registry record. Keeping the reported details distinct from unreported methods is essential to a calibrated reading of a small pharmacokinetic trial.

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.

The study enrolled 16 participants, and the primary endpoint counts are 16 for Treatment A, 15 for Treatment B, 16 for Treatment C, and 16 for Treatment D. The reason for the lower count for Treatment B is not reported in the registry record. Without a description of unavailable measurements or participant-level data, it is not possible to assess how that difference affects the comparisons.

The registry describes a randomized, triple-masked, four-period crossover design, but it does not report the statistical model used for the primary endpoint. In particular, no crossover-specific estimate accounting for repeated measurements, period, sequence, or carryover is posted. The comparisons available in the record are simple unadjusted recalculations from treatment summaries. They may not capture the precision obtainable from a paired analysis, and the degree of difference cannot be determined from the posted aggregate data.

The record also does not report a multiplicity procedure, missing-data strategy, interim analysis plan, or original sample-size justification. The sample-size illustrations based on observed effects are not a substitute for the missing design rationale. The confidence intervals and p-values for the recalculated contrasts should therefore be interpreted in the context of the stated unadjusted approach, not as documented results from a prespecified trial analysis.

The endpoint is limited to Cmax measured over 8 hours. It does not summarize all pharmacokinetic features or clinical outcomes. The safety summary lists zero serious adverse-event participants in each condition but does not provide a detailed event-level comparison; death counts are not reported in the registry record. The study's size and single-dose setting also limit how broadly these summaries can describe other populations, dosing patterns, or outcomes. No further details about generalizability are reported in the registry record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: Safety and Blood Level Study of Unit Dose Budesonide — NCT00627679.
• Registry record last updated 2014-01-09; status last verified 2013-12.
• Results first posted 2013-10-23.
• 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

The registry record describes NCT00627679, a completed randomized, triple-masked, active-controlled, single-dose, four-arm, four-period crossover Phase 1 study sponsored by Allergan. It lists enrollment of 16 and describes the study purpose as evaluating tolerability and pharmacokinetics of three MAP0010 dose levels compared with Pulmicort Respules in healthy volunteers.

The primary endpoint was budesonide Cmax over 8 hours, reported as a mean and standard deviation. Posted mean values were 303.5 pg/mL for Treatment A, 106.2 pg/mL for Treatment B, 239.9 pg/mL for Treatment C, and 434.5 pg/mL for Treatment D. Treatment A was Pulmicort Respules; Treatments B, C, and D were MAP0010 low, intermediate, and high dose levels. The registry also contains unadjusted recalculated comparisons with the comparator.

The serious adverse-event counts were zero for all four conditions, with 16 at risk in each. Other adverse events affected 4, 4, 3, and 3 participants, respectively. Several analysis details, including the crossover model, multiplicity handling, and the reason for the difference in outcome counts, are not reported in the registry record.