A Non-inferiority Study to Evaluate Efficacy, Safety and Tolerability of NEUMOTEROL® 400 and SYMBICORT® Forte in Adults With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Non-inferiority Study to Evaluate Efficacy, Safety and Tolerability of NEUMOTEROL® 400 and SYMBICORT® Forte in Adults With Asthma (NCT02233803), a randomized phase 4 study. The primary outcome is Change From Baseline (BL) in Trough Morning Forced Expiratory Volume in One Second (FEV1) at Day (D)29.

2. Clinical Question

3. Trial Design

This was a Phase IV, randomized, multicentre, open-label, two-way crossover study in adults with asthma. The registry lists 239 participants enrolled. In a crossover design, a participant receives each study regimen during separate periods; the order is randomized, so participants can contribute observations under both regimens. The registry lists two sequences: NEUMOTEROL 400 followed by SYMBICORT Forte, and the reverse sequence.

The treatment periods were described as 4 weeks each, separated by a washout period of at least 4 weeks in the study summary. The sequence descriptions specify a 4-week washout. The overall schedule included prescreening, a 4-week screening/run-in, Treatment Period 1, washout, Treatment Period 2, and a 1-week follow-up. The registry says the study duration for each participant was at least 17 weeks, with up to 6 study visits and a follow-up telephone call. During run-in and washout, participants received NEUMOTEX 400 and salbutamol as needed, according to the registry summary.

The study was open label, meaning masking was not used. The primary outcome was change from baseline in trough morning FEV1 at D29 of each treatment period. The registry describes an intent-to-treat population consisting of randomized participants who received at least one dose, analyzed according to randomized treatment; only participants with data at the indicated time points were included in each analysis. The primary outcome results list 188 participants for each regimen. The reason those endpoint counts differ from the overall enrollment is not reported in the registry record.

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: Total 6 phases of study; pre-screening, screening/run-in, treatment period (TP) 1 washout, TP2, and follow-up. Out of total 239 enrolled participants, only 199 participants were randomized. 29 were screen failures and 10 were Run-in failures. One participant not randomized as the target number of participants for study was reached

Treatment Period 1 (4-Wks)

Reasons for not completing this period:

Washout Period (4-Wks)

Reasons for not completing this period:

Treatment Period 2 (4-Wks)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent to treat (ITT) population comprised of all randomized participants who received at least one dose of study treatment. This population was based on the treatment to which the participant was randomized. Only those participants with data available at the indicated time points were analyzed.

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline (BL) in Trough Morning Forced Expiratory Volume in One Second (FEV1) at Day (D)29, measured over BL (D1) and D29 (each TP).

The primary endpoint was change from baseline in trough morning forced expiratory volume in one second, or FEV1, at D29 of each treatment period, measured in litres. FEV1 is the amount of air forcefully exhaled in one second. A trough measurement is taken before the morning dose and before bronchodilator use; the registry defines it as 12 hours after the last evening dose on D28. The spirometry assessment was conducted in the morning and within 30 minutes before dosing.

FEV1 is used as a measure of lung function. Measuring change from baseline focuses the comparison on how the outcome changed relative to a participant’s starting measurement rather than only comparing endpoint values. In this crossover study, the primary endpoint was measured during each treatment period. The registry describes a model that accounts for subject-level and period-specific baselines, treatment, period, and participant-level variation. Least-squares means are model-adjusted estimates, rather than simple arithmetic averages.

The stated non-inferiority objective concerns whether the difference between regimens is sufficiently small under a prespecified margin. That margin is not reported in the registry record. Without it, the reported estimate and interval can be described, but the non-inferiority decision rule cannot be evaluated from the registry results alone.

7. Results Posted in the Registry

• SYMBICORT FORTE: mean 0.15 versus 0.19 on control; difference -0.04 (95% CI -0.10 to 0.02), standardized effect d = -0.15; z-test p = 0.144.

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 Area Under the Curve (AUC) (0-10 h) at D1 of Each TP

• 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:
  • SYMBICORT FORTE: mean 23.59 versus 24.57 on control; difference -0.98 (95% CI -1.49 to -0.47), standardized effect d = -0.38; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for SYMBICORT FORTE than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From BL in Asthma Control Test (ACT) at 4 Wks for Each TP

• 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:
  • SYMBICORT FORTE: mean 1.00 versus 1.60 on control; difference -0.60 (95% CI -1.15 to -0.05), standardized effect d = -0.22; z-test p = 0.034.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for SYMBICORT FORTE than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes provide a broader view of the measurements collected during the trial, but they address different questions from the primary trough morning FEV1 endpoint. The posted results include FEV1 area under the curve over 0-10 h at D1 of each treatment period and change from baseline in Asthma Control Test score at 4 weeks for each period. The registry therefore reports both an additional lung-function measure and a participant asthma-control measure.

Across the posted secondary analyses, the estimates favor NEUMOTEROL 400 in the displayed direction, and the reported analysis for FEV1 area under the curve has a confidence interval above zero. The ACT comparison also has a reported interval above zero, while its unadjusted recalculation has p-value 0.034. These findings are secondary; their meaning should not be elevated to the status of the primary endpoint or treated as independent confirmation of the primary non-inferiority question. They concern distinct measures and time points, and the primary question remains the adjusted D29 trough FEV1 comparison.

Unadjusted secondary results carry less weight because multiple outcomes and comparisons create more opportunities for results to appear notable by chance. The registry does not report a multiplicity adjustment or a hierarchy governing secondary hypotheses. The posted estimates can be read as descriptive evidence about those outcomes, with their uncertainty, but the record does not establish that the secondary analyses were confirmatory. They also do not resolve the missing non-inferiority margin for the primary endpoint.

The overall pattern is that the secondary estimates point in the same displayed direction, but they cannot substitute for a prespecified primary decision rule. Their interpretation should account for their secondary status, the absence of reported multiplicity handling, and the fact that each measures a different aspect of the study outcomes.

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

• FEV1 Area Under the Curve (AUC) (0-10 h) at D1 of Each TP
• Change From BL in Asthma Control Test (ACT) at 4 Wks for Each TP

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint description says change from baseline was analyzed with a mixed-effects ANCOVA model. ANCOVA is a regression approach that estimates a treatment comparison while adjusting for selected baseline covariates. A mixed-effects model can include both fixed terms, such as treatment and period, and a random effect representing participant-level variation. This is relevant to a crossover study because each participant contributes observations in different treatment periods and measurements from the same participant are related.

How were baseline values handled?

The registry describes two baseline concepts. A period-specific baseline was the pre-dose assessment on D1 of each treatment period. The subject-level baseline was the arithmetic mean of the participant’s period-specific baseline values. If one period-specific baseline was missing, the other value was used for the subject-level baseline; if both were missing, the subject-level baseline was set to missing. The period-level baseline was calculated as the period-specific baseline minus the associated subject-level baseline. These definitions indicate how baseline information entered the described model; they do not fully specify every detail of the analysis implementation.

The model description says it included subject-level baseline, adjusted period-specific baseline, treatment group, and period, with participant as a random effect. The registry outcome is a least-squares mean, which is an adjusted mean estimated from a statistical model. Its standard error describes uncertainty in that estimate. Least-squares means and their contrasts can differ from raw averages because they account for the model’s covariates and structure.

What does a crossover comparison add?

As a general statistical explanation, crossover designs can use within-participant comparisons: differences between treatment-period measurements for the same participant can reduce the influence of characteristics that remain relatively stable across periods. This advantage depends on the conduct and assumptions of the design, including whether treatment effects carry into a later period and whether period effects are appropriately handled. The registry lists a washout and includes period in the primary model. Further details about testing for carryover, sequence effects, or other diagnostics are not reported in the registry record, so no conclusion about those checks can be made.

The registry identifies the analysis population as randomized participants who received at least one dose, analyzed according to randomized treatment, with only participants having data at the relevant time points included. This description does not give a detailed account of how missing outcome measurements were handled beyond that availability rule. Imputation procedures, sensitivity analyses for missing data, and the number of participants with incomplete measurements are not reported in the registry record.

How should the recalculation be distinguished?

The recalculated comparison is a simple, unadjusted comparison derived from the posted arm-level summaries. Its standard deviation is approximate, as indicated in the calculation details. It does not use the individual participant data, the crossover pairing, the baseline adjustment, or the mixed-effects ANCOVA described for the primary result. The resulting estimate, interval, and p-value are therefore useful as a rough summary-statistic comparison, not as a replication of the sponsor’s model.

The recalculated p-value is unadjusted. A p-value measures how unusual data at least as discrepant as those observed would be under a specified null model; it does not measure the probability that a hypothesis is true or the size or importance of an effect. Confidence intervals give a range of estimates compatible with the data and analysis assumptions at the stated confidence level. Neither a p-value nor an interval supplies the missing non-inferiority margin.

What is not specified?

The registry record does not report the original sample-size justification, the non-inferiority margin, or a complete statistical analysis plan. It also does not report whether interim analyses were conducted, how multiplicity was handled, or the details of any sensitivity analyses. The primary endpoint description provides a model outline, but the reported-analysis entry does not name a method. The available information supports describing the stated model and posted results, not inferring additional protocol decisions or analysis procedures.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is a difference of least-squares means of 0.044, with a 95% confidence interval from -0.008 to 0.096. A confidence interval describes the uncertainty around an estimate under the assumptions of the analysis. It is not a range that guarantees the true value lies within it, nor does it directly give the probability that a particular treatment difference is true.

The interval spans zero, so the reported primary result is compatible with a small difference in either direction under its sign convention. The interval’s width also matters: it shows that the estimate is not known with exact precision. Whether its upper or lower boundary is acceptable for non-inferiority depends on the prespecified margin, which is not reported in the registry record. A zero-crossing interval alone does not decide a non-inferiority question.

The unadjusted recalculation has an estimate of -0.044 for SYMBICORT Forte minus NEUMOTEROL 400, with an interval from -0.103 to 0.015. Its sign is reversed relative to the sponsor-reported contrast, and its interval differs because it is calculated from summary statistics rather than the adjusted crossover model. The recalculation is not the more authoritative estimate when the sponsor’s analysis is posted; the sponsor analysis takes precedence.

Arm-level standard errors and the reported participant counts provide context for the estimates, but precision also depends on the model, within-participant association, missing data, and design. Those features are not fully reconstructable from arm summaries. The primary reported interval is the most relevant measure of precision for the stated primary analysis. Because no margin is given, precision can be described but not judged against the trial’s intended non-inferiority boundary.

12. Planning a Similar Trial: Sample Size

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

The sample-size figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these continuous outcomes, the figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The trial’s own original sample-size assumptions are not reported in the registry record.

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 the planning assumptions, if that effect and model assumptions were correct. The 90% power column uses a higher target chance of detection, so it generally calls for more participants per arm. These are planning targets, not guarantees about the result of a particular trial. Smaller effects require more participants to distinguish them from random variation under otherwise similar assumptions.

Rows for 100%, 75%, and 50% of the observed effect represent increasingly smaller target effects. The corresponding participant counts rise as the target effect shrinks. These figures are hypothetical planning comparisons using the observed effect as a reference point; they do not establish what sample size would be adequate under different assumptions, outcome variability, or crossover-specific design inputs. They are not observed power. Observed power is not a useful substitute for interpreting the estimated effects and their confidence intervals after the data have been collected.

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 = -0.044; pooled standard deviation σ = 0.292.
2. n = 2 × (1.96 + 0.842)² × 0.292² / -0.044² = 691.6, rounded up to 692 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 <- -0.044                      # observed difference in means
sigma <- 0.292050885977084                     # 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(2233803)
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 = 692 (80% power), 926 (90% power)
 75% of observed effect: n per arm = 1,230 (80% power), 1,646 (90% power)
 50% of observed effect: n per arm = 2,767 (80% power), 3,704 (90% power)
power.t.test: 692.6 
Simulated power at n = 692 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor-reported primary analysis gives a difference of least-squares means of 0.044, with a 95% confidence interval from -0.008 to 0.096. The unadjusted recalculation gives -0.044 for SYMBICORT Forte minus NEUMOTEROL 400, with an interval from -0.103 to 0.015. The signs reflect opposite contrast directions: the sponsor result is presented as the difference in the other direction. The estimates are therefore directionally consistent when expressed using the same contrast, but the intervals are not identical.

The distinction is methodological, not evidence of a discrepancy. The sponsor result is an adjusted least-squares comparison from the crossover trial. The endpoint description specifies mixed-effects ANCOVA terms for baseline, treatment, and period, with participant as a random effect. The recalculation uses arm-level means and standard errors, an approximate pooled standard deviation, and an unadjusted comparison; it does not account for the paired crossover data or the described adjustment. The recalculated p-value is 0.144 and is not a replacement for the sponsor analysis.

The sponsor’s reported analysis takes precedence for interpreting the primary result, and the record indicates no discrepancy. The sponsor analysis does not report a p-value in the registry entry. Although the result is categorized as non-inferiority or equivalence, the non-inferiority margin is not reported in the registry record. Consequently, the posted estimate and interval can be described, but whether they satisfy the study’s intended decision rule cannot be determined from this record alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary outcome and two secondary outcomes, while the count of posted outcome measures is three. It does not report how the statistical plan handled multiplicity across outcomes, comparisons, or time points. No adjustment method or hierarchy for secondary testing is stated in the registry record. Without such information, unadjusted secondary p-values should be interpreted cautiously: conducting multiple tests can increase the chance of at least one apparently notable result even when no corresponding effect exists.

The primary outcome description identifies an intent-to-treat population comprising randomized participants who received at least one dose, analyzed according to randomized treatment. It also states that only participants with data available at the indicated time points were analyzed. This identifies the broad population rule and the timepoint-specific availability rule, but it does not provide a detailed account of missing-data methods. The record does not report imputation, sensitivity analyses, reasons for unavailable measurements, or an account of participants’ completion by treatment sequence.

The endpoint results list 188 participants for each treatment, while the safety denominators are 193 and 194 and overall enrollment is 239. The record does not explain the differences among these figures. The outcome-specific population rule means the results may use different available-data counts, but the reasons for the observed counts are not reported. No assumption about attrition or missingness can be inferred from the counts alone.

The primary endpoint description gives a mixed-effects ANCOVA outline, including baseline, treatment, period, and participant random effect. However, the registry does not report a complete statistical analysis plan, the non-inferiority margin, the original sample-size justification, or whether interim analyses occurred. These omissions limit evaluation of the prespecified decision process and of the robustness of the results. The absence of a reported detail should not be interpreted as evidence that a particular method was or was not used.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 3% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: cholelithiasis (0.5%), rash (0.5%).

The safety results list serious adverse events affecting 1 of 193 participants in the NEUMOTEROL 400 group and 1 of 194 participants in the SYMBICORT Forte group. Other adverse events affected 10 of 193 and 11 of 194 participants, respectively. Deaths were 0 in each group. The registry also lists cholelithiasis and rash among the top serious adverse event terms, each at 0.5%.

These counts describe events recorded in the registry; they are not adjusted comparisons and do not establish that the regimens have identical safety profiles. The denominators differ from the primary outcome counts, and the record does not explain the difference. Small counts can leave substantial uncertainty about comparative event frequencies. The listed terms and counts should be read as a summary of reported events, not as a complete characterization of all possible harms or as evidence about longer-term safety.

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

The primary result is an adjusted estimate of the difference in change in trough morning FEV1 between the study regimens at D29 of each treatment period. The sponsor-reported difference of least-squares means is 0.044, with a 95% confidence interval from -0.008 to 0.096. This describes the estimate and its uncertainty under the analysis reported in the registry. It is not, by itself, a general statement about all asthma outcomes or all participants with asthma.

Because the registry record does not report the non-inferiority margin, it is not possible to determine from the posted result whether the study met the intended non-inferiority criterion. The interval crossing zero does not answer that question: non-inferiority is judged against a prespecified margin, which can differ from zero. No unreported margin or decision threshold can be inferred from the category assigned to the analysis.

The secondary outcomes address lung-function response over a time interval and change in asthma-control score. They add context but are not substitutes for the primary endpoint. Their unadjusted status and the absence of reported multiplicity handling mean that they should be interpreted as secondary evidence. The recalculated comparisons are likewise supplementary: they use summary statistics and do not reproduce the adjusted crossover analysis.

The safety counts show serious adverse events and other adverse events recorded in both groups, with no deaths listed. Those figures are descriptive and do not demonstrate equivalence of safety. The study’s open-label crossover design, endpoint-specific analysis counts, and incomplete reporting of missing-data and multiplicity procedures all matter when interpreting the scope of the evidence.

Thus, the registry supports a precise account of the posted estimates, intervals, and event counts, but it does not support a definitive non-inferiority judgment without the missing margin. It also does not establish conclusions about outcomes that were not measured, longer-term effects, or populations outside the eligibility description.

18. Why This Trial Matters Statistically

This trial illustrates why a non-inferiority result requires more than comparing two observed means or checking whether a confidence interval includes zero. The decision depends on a prespecified margin that defines how large a difference would still be considered acceptable for the study question. Although the registry labels the primary analysis as non-inferiority or equivalence, it does not report that margin. The estimate and 95% confidence interval can therefore be examined, but the intended decision boundary cannot be checked.

The crossover structure also matters statistically. Each participant received both regimens in separate periods, with randomized treatment sequence and a washout. The primary model description includes period and participant effects, reflecting the repeated, within-participant structure. A simple comparison of arm summaries does not preserve that structure, which is why an unadjusted recalculation can differ from the sponsor’s adjusted estimate and interval even when the contrast direction is reconciled.

The record also demonstrates the importance of distinguishing an analysis population from overall enrollment. The primary results list 188 participants per treatment, while enrollment and safety denominators are different. The available-data rule is described, but reasons for the endpoint counts and detailed missing-data procedures are not. Such reporting affects how readers assess the scope and potential precision of an estimate.

Finally, secondary outcomes and safety counts add information but require separate interpretation. Multiple secondary comparisons may require multiplicity planning, and the registry does not state how this was handled. The result is therefore a useful case for reading estimates, confidence intervals, design features, and reporting gaps together rather than treating a single statistic as a complete answer.

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 registry record leaves several trial-specific questions unresolved. Most importantly for the primary objective, it does not report the non-inferiority margin. Without that boundary, the reported 95% confidence interval cannot be assessed against the criterion intended to define non-inferiority. The record also does not report the original sample-size justification, so the relationship between planned enrollment and the precision required for the primary comparison is unclear.

The open-label design means masking was not used. The primary outcome is an objective spirometry measure, but the record does not report blinding of outcome assessment. It also does not report detailed procedures for adherence, protocol deviations, or sensitivity analyses. Those details should not be assumed to have been absent from study conduct; they are simply not reported in the registry record.

The crossover design is described with randomized sequences and a washout period, and the primary model includes period and participant terms. Further information about sequence effects, carryover assessment, or the handling of departures from the planned treatment sequence is not reported. The registry’s primary outcome description gives a model outline, but the reported-analysis entry does not specify a method.

The primary endpoint analysis lists 188 participants per regimen, whereas overall enrollment is 239 and safety denominators are 193 and 194. The record does not explain these differences. It states that only participants with data at the indicated time points were analyzed, but does not report the missing-data mechanisms, imputation, or sensitivity analyses. Multiplicity handling for the secondary outcomes is also not reported. These gaps limit independent assessment of analysis robustness and of the relative weight to give secondary findings.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Non-inferiority Study to Evaluate Efficacy, Safety and Tolerability of NEUMOTEROL® 400 and SYMBICORT® Forte in Adults With Asthma — NCT02233803.
• Registry record last updated 2017-09-15; status last verified 2017-08.
• Results first posted 2017-08-18.
• 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 record describes a completed Phase IV, randomized, multicentre, open-label crossover trial comparing NEUMOTEROL 400 with SYMBICORT Forte in adults with asthma. Enrollment was 239. Participants received the regimens in randomized order across treatment periods, with a washout between periods.

The primary outcome was change from baseline in trough morning FEV1 at D29 of each treatment period. The sponsor-reported difference of least-squares means was 0.044, with a 95% confidence interval from -0.008 to 0.096. The non-inferiority margin is not reported in the registry record, so the criterion for a non-inferiority conclusion cannot be evaluated from the posted information.

The registry also reports FEV1 area under the curve and Asthma Control Test results, along with adverse event counts. Multiplicity and detailed missing-data procedures are not reported. The summary statistics support description of the posted estimates and their uncertainty, while leaving important elements of the intended decision rule and analysis process unspecified.