Efficacy and Safety of Indacaterol Acetate Delivered Via the Concept1 Inhalation Device in Children Greater or Equal to 6 and Less Than 12 Years of Age With Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of Indacaterol Acetate Delivered Via the Concept1 Inhalation Device in Children Greater or Equal to 6 and Less Than 12 Years of Age With Asthma (NCT02892019), a randomized phase 2 study. The primary outcome is Trough Forced Expiratoty Volume in 1 Second (FEV1).

2. Clinical Question

The study asked whether two once-daily doses of indacaterol acetate, delivered through the Concept1 inhaler, were associated with different changes in lung function over 2 weeks in children with asthma. Its primary measure was change from baseline in pre-dose trough forced expiratory volume in 1 second (FEV1). The registry describes children aged greater than or equal to 6 and less than 12 years; the brief summary describes the age range as 6–11 years.

The registry’s stated aim also included exploring lung-function effects across the two doses and comparing plasma exposure with historical adult data to identify a dose for Phase III evaluation. The numerical results available for the primary comparison address the lung-function endpoint; a numerical plasma-exposure result is not reported in the registry record. The comparison therefore describes the posted results for these two dose groups, rather than establishing how either dose compares with no indacaterol treatment.

3. Trial Design

This was a Phase 2, randomized, parallel-group study described in the official title as multicenter, double-blind, active-controlled, and lasting 2 weeks. The registry labels masking as quadruple. Both descriptions indicate that masking was part of the design, but the registry record does not explain which people were masked or how masking was implemented.

The two groups received indacaterol acetate 75 μg once daily or 150 μg once daily through the Concept1 inhaler. The 150 μg group is the reference group in the posted comparison with the 75 μg group. Because both groups received an active dose, the trial directly informs the contrast between these doses; it does not include a placebo or untreated group in the listed interventions.

Enrollment is listed as 79, and the study status is completed. For the primary outcome, the listed group sizes are 41.0 in the 150 μg group and 38.0 in the 75 μg group. The record identifies the primary analysis population as the full analysis set. It does not report the randomization ratio, the allocation-concealment process, or the operational definition of that analysis population.

The primary outcome was measured after 2 weeks. The registry lists several secondary outcomes, including asthma control, peak expiratory flow, rescue medication use, FEV1 and forced vital capacity, symptoms, and plasma exposure. Numerical results are posted for some, but not all, of these outcomes. Details of the statistical analysis plan, including handling of missing outcome data and any interim analyses, are 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: randomized set : 80 participants (41 and 39) Full analysis set : 79 participants (41 and 38) safety set : 79 participants (41 and 38) per protocol set : 35 participants (35 and 34)

Overall Study

Reasons for not completing this period:

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 Trough Forced Expiratoty Volume in 1 Second (FEV1), measured over 2 weeks.

The primary endpoint is change from baseline in pre-dose trough FEV1 after 2 weeks of treatment. FEV1 is the amount of air exhaled in the first second of a forced breath; it is used as a lung-function measure. The endpoint definition describes trough FEV1 as the mean of two pre-dose readings, taken at -45 min and -15 min. Averaging the readings defines the endpoint from more than one measurement at the pre-dose time point.

Change from baseline focuses the comparison on how the measured value shifted over the treatment period, rather than only on the value at the end. The registry lists the unit as L, while the endpoint definition describes the measurements in mL. The group results are reported as mean changes, with standard deviations listed as the measure of spread. The registry record does not give further detail on baseline adjustment or other modeling steps.

A trough, pre-dose measure captures lung function at a specified point before the next dose, as defined by this study’s measurement schedule. Such a measure can be useful for comparing changes in lung function at a consistent point in the dosing cycle. It is one endpoint among several, however, and it does not by itself describe all aspects of asthma control, symptoms, safety, or longer-term outcomes. The registry’s brief summary identifies lung-function effects as the study’s focus, while the study duration limits interpretation to the stated 2-week assessment.

7. Results Posted in the Registry

• Indacaterol Acetate 75 μg o.d.: mean 0.21 versus 0.17 on control; difference 0.04 (95% CI -0.05 to 0.14), standardized effect d = 0.19; z-test p = 0.397.

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.

Asthma Control as Assessed by Pediatric Interviewer-administered Asthma Control Questionnaire

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Indacaterol Acetate 75 μg o.d.: mean -0.27 versus -0.38 on control; difference 0.10 (95% CI -0.13 to 0.34), standardized effect d = 0.20; z-test p = 0.376.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol Acetate 75 μg o.d. and the control. The interval gives the range of effects that remain compatible with the data.

Rescue Medication Usage (Mean Daiily Number of Puffs)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Indacaterol Acetate 75 μg o.d.: mean -0.22 versus -0.19 on control; difference -0.03 (95% CI -0.57 to 0.51), standardized effect d = -0.02; z-test p = 0.913.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol Acetate 75 μg o.d. and the control. The interval gives the range of effects that remain compatible with the data.

Rescue Medication Usage (Percentage of Rescue Medication Free Days)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Indacaterol Acetate 75 μg o.d.: mean 3.10 versus 7.40 on control; difference -4.30 (95% CI -13.52 to 4.92), standardized effect d = -0.20; z-test p = 0.361.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Indacaterol Acetate 75 μg o.d. and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists a broad set of secondary questions, including asthma control, peak expiratory flow, rescue medication use, lung-function measures, symptoms, and plasma exposure. Numerical comparative results are posted for three secondary endpoints: asthma control, mean daily rescue-medication puffs, and the percentage of rescue-medication-free days. Their estimates vary in direction and their confidence intervals include zero. This pattern does not offer a consistent, precise separation between the dose groups across the posted secondary comparisons.

These secondary measures provide context around the primary lung-function result because they address related but distinct aspects of asthma control and reported experience. They are not interchangeable with trough FEV1, and agreement or disagreement between measures would not by itself validate or invalidate the primary endpoint. The posted numerical secondary comparisons do not establish a clear contrast between doses, while the remaining registered secondary outcomes do not have numerical comparative results in the record summarized for these analyses.

Secondary results generally carry less confirmatory weight when many outcomes are considered without a reported multiplicity strategy. Testing or examining multiple outcomes increases the chance of finding an apparently notable result by chance. An unadjusted p-value for an individual secondary endpoint does not account for that wider set of questions. The registry record does not report a prespecified hierarchy, multiplicity adjustment, or which secondary outcomes were intended to be confirmatory.

Accordingly, the secondary results are best treated as exploratory descriptions that can suggest questions for further study, rather than as independent confirmation of a dose effect. Their interpretation also depends on how each outcome was defined, measured, and analyzed, details that are not fully reported in the registry record. The absence of numerical results for some listed outcomes prevents a comprehensive assessment of whether the secondary pattern aligns with the primary comparison.

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

• Systemic Exposure to Indacaterol in Plasma
• Asthma Control as Assessed by Pediatric Interviewer-administered Asthma Control Questionnaire
• Pre-dose Morning and Evening Peak Expiratoty Flow (PEF)
• Rescue Medication Usage (Mean Daiily Number of Puffs)
• Rescue Medication Usage (Percentage of Rescue Medication Free Days)
• Forced Expiratoty Volume in 1 Second (FEV1) and Forced Vital Capacity (FVC)
• Symptoms as Recorded by Patient E-diary (Mean Total Daily Symptom Score)
• Symptoms as Recorded by Patient E-diary (Percentage of Asthma Symptoms Free Days)

9. Statistical Interpretation

10. Statistical Methods Explained

In general, a mean summarizes the center of a continuous outcome across participants. Here, the primary endpoint is continuous change in FEV1, and the registry reports a mean for each dose group. A mean difference compares the two group means on the same measurement scale. The stated comparison is the 75 μg group relative to the 150 μg group, with a positive estimate indicating a higher mean change in the former for this subtraction order.

In general, a standard deviation describes how dispersed individual observations are around a group mean. It is not an uncertainty interval for the mean and should not be read as a range containing every participant’s result. The primary outcome is reported with standard deviations, but the posted comparison’s confidence interval is the relevant summary for uncertainty in the difference of group means. The record does not provide participant-level distributions, so the shape of those distributions cannot be assessed from the summary statistics alone.

A confidence interval is a range generated by a statistical procedure that, under its assumptions and repeated use, has a stated coverage property. For this primary comparison, the 95% interval runs from -0.054 to 0.136 L. Because zero lies within that range, the estimate is compatible with no mean difference as well as with differences on either side of zero. That does not prove the groups are equivalent: equivalence requires a prespecified margin and an analysis designed to assess it, neither of which is reported in the registry record.

The unadjusted p-value for the primary comparison is 0.397. In general, a p-value measures how unusual data at least as discordant with a specified null model would be if that model and the test assumptions held. It does not measure the size or importance of an effect. It also does not account for multiplicity unless the method explicitly includes such an adjustment. The registry record does not report a multiplicity procedure, so the posted p-value should be treated as unadjusted.

The listed comparison is a comparison of means. The registry record does not report a regression model, covariate adjustment, repeated-measures model, or other analytic approach used to obtain the posted estimate. It also does not report details of missing-data handling, assumptions about the distribution of the endpoint, or how any protocol deviations were handled. Those details matter because different analysis choices can affect the estimate and its uncertainty. No more specific description of the calculation can be justified from the record.

In general, over-dispersion matters when data vary more than a model assumes: standard errors can then be too small if the model fails to account for that extra variation. This endpoint is reported as a continuous measure with standard deviations, not as a count outcome, and the registry does not report a model or an over-dispersion assessment. It would therefore be inappropriate to claim that over-dispersion was tested or adjusted for in this trial. The relevant general lesson is that uncertainty calculations depend on the assumed data structure and model.

The primary population is named as the full analysis set. In general, an analysis population defines which randomized participants contribute to an estimate; the exact definition can vary across trials. The record does not define the full analysis set or report how many participants were included in the endpoint analysis, whether all randomized participants had an observed endpoint, or how missing values were treated. The listed enrollment and arm sizes should not be substituted for an unreported endpoint-analysis count.

The planning illustrations use the observed effect as a reference and show hypothetical participant requirements under stated assumptions. These are not the original trial’s design calculations. The registry record does not report the original sample-size justification, target effect, interim-analysis plan, or detailed statistical plan. The planning figures are therefore best read as conditional illustrations of the sample sizes implied by their stated assumptions, not as a reconstruction of the study design.

Finally, statistical evidence and clinical relevance are distinct. The mean difference and its interval describe the size and precision of the contrast on the FEV1 scale. A clinically meaningful threshold is not reported in the registry record. Without such a threshold, the statistical summary can describe uncertainty, but it cannot determine whether a difference would matter to patients or clinicians.

11. Confidence Intervals and Precision

The primary estimate is a mean difference of 0.041 L, with a 95% confidence interval from -0.054 to 0.136 L. The interval is centered around the posted estimate as a measure of the range of values compatible with the data under the calculation’s assumptions. It spans zero, so the posted summary does not distinguish the observed contrast from no mean difference at the conventional interval-exclusion level.

Precision concerns the width of the uncertainty around an estimate, not whether the estimate is large or small. A narrower interval would indicate greater precision; a wider interval leaves more uncertainty about the underlying contrast. The interval in this trial permits both a modest result in one direction and a result in the other direction. It should not be reduced to the point estimate alone, and its endpoints are not individual participant outcomes.

The p-value of 0.397 is consistent with the interval’s inclusion of zero, but the two summaries answer different questions and neither establishes equivalence. A finding of equivalence would require a clinically justified margin and an appropriate analysis, not merely an interval that includes zero. The registry record does not report such a margin.

Precision is also bounded by what was measured and when. The primary result concerns a 2-week change in pre-dose trough FEV1 in the specified study population. It does not quantify precision for outcomes or time points not reported. The interval also does not incorporate uncertainty about unreported design or analysis decisions. Its interpretation depends on the statistical procedure used, details of which are not reported in the registry record.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participant counts per arm, not total event counts. The listed 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 set at the stated fraction of the observed effect. These are planning assumptions for the illustrations; the original trial’s design assumptions are not reported in the registry record.

For 100% of the observed primary effect, the illustration gives 420 participants per arm for 80% power and 562 participants per arm for 90% power. For 75% of the observed effect, it gives 746 participants per arm for 80% power and 999 participants per arm for 90% power. For 50% of the observed effect, it gives 1,679 participants per arm for 80% power and 2,247 participants per arm for 90% power.

In plain language, power is the probability that a planned study would meet its statistical detection criterion if the assumed effect and other planning conditions were true. The 80% and 90% columns represent different target probabilities under those assumptions; the higher target generally calls for more participants. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm when the assumed effect is reduced.

These numbers are planning illustrations, not observed power. They do not describe the actual chance that this completed trial detected an effect, and they are not evidence that a future study will have the stated performance unless the assumptions are suitable. The curve should be read in the same conditional way: it relates assumed effect size and planned sample size under the stated calculation, rather than depicting observed results from the trial.

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 = 0.041; pooled standard deviation σ = 0.212.
2. n = 2 × (1.96 + 0.842)² × 0.212² / 0.041² = 419.5, rounded up to 420 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 <- 0.041                      # observed difference in means
sigma <- 0.211950483374295                     # 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(2892019)
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 = 420 (80% power), 562 (90% power)
 75% of observed effect: n per arm = 746 (80% power), 999 (90% power)
 50% of observed effect: n per arm = 1,679 (80% power), 2,247 (90% power)
power.t.test: 420.5 
Simulated power at n = 420 per arm: 0.801 (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. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when a study evaluates several outcomes, contrasts, time points, or analyses. Even when each individual test uses the same threshold, considering many tests can increase the chance that at least one result appears statistically notable by chance. This study lists multiple secondary outcomes in addition to the primary FEV1 endpoint, so the approach to multiplicity is relevant when interpreting secondary findings.

The registry record does not report whether a family-wise error procedure, false-discovery procedure, hierarchical testing plan, or other multiplicity strategy was used. It also does not identify a prespecified order for interpreting secondary endpoints. The posted secondary comparisons should therefore be read as unadjusted unless an adjustment is explicitly documented; no such adjustment is reported in the registry record. The unadjusted results are not equivalent to a set of independently confirmatory tests.

Missing-data handling is also not reported in the registry record. The primary analysis population is named as the full analysis set, but its criteria are not defined. The record does not state how many participants contributed observed values to each endpoint, whether any values were missing, or whether missing data were imputed, excluded, or handled through a model. Without these details, it is not possible to assess how missing observations may have affected the estimates.

The registry record also does not report the full statistical analysis plan, interim analyses, stopping rules, covariate adjustments, or sensitivity analyses. These are not details that can be inferred from randomization, masking, or the outcome summaries. Their absence limits assessment of whether the posted estimates follow a prespecified analysis and how robust the findings are to alternative assumptions.

These reporting gaps do not show that a particular method was or was not used. They mean that the registry record does not document it. The primary comparison can still be described from its estimate and confidence interval, but confidence in a broader confirmatory interpretation requires information about multiplicity, missing data, and the analysis population that is not reported.

15. 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 2% reporting threshold.

Most frequent non-serious adverse event terms

The serious adverse event figures list 0 affected participants in the 150 μg group, among 41 at risk, and 0 in the 75 μg group, among 38 at risk. Deaths are listed as 0 in each group. No serious adverse event terms are listed. These are the counts recorded during this study; they do not establish that a serious event could not occur.

For other adverse events, the record lists 3 affected participants in the 150 μg group and 13 in the 75 μg group. These counts should be read as reported, not as proof that dose caused a difference. The record does not provide event-term detail in the summary used for this comparison, nor does it report statistical testing for these safety counts. The 2-week duration and the group sizes also define the scope of the observed safety information.

Serious and other adverse events are separate categories in the registry listing. The figures should not be combined or interpreted as a complete account of tolerability without detailed event definitions, timing, severity, and relatedness assessments. Those details are not reported in the registry record.

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

The primary result describes a difference in mean change from baseline in pre-dose trough FEV1 between two active-dose groups after 2 weeks. The estimate favors a larger mean change in the 75 μg group by the subtraction used, but its confidence interval extends across zero and into both directions. It is therefore a point estimate with substantial uncertainty about the direction and magnitude of the underlying difference.

This result does not show that one dose is definitively better than the other. It also does not show that the doses are equivalent; no equivalence margin or equivalence analysis is reported. A nonzero point estimate and a p-value do not by themselves resolve clinical importance. The registry record does not report a threshold for a clinically meaningful FEV1 change.

The study compares 75 μg with 150 μg, not either dose with placebo or no treatment. The observed changes from baseline within each group cannot, on their own, separate treatment effects from changes that might occur over time for other reasons. The study’s randomized active-controlled design supports the dose contrast, but the available comparison does not answer every causal or clinical question about indacaterol.

The endpoint concerns lung function over a short stated period. It does not establish effects on longer-term asthma control, exacerbations, quality of life, or other outcomes not numerically reported. The secondary outcomes provide additional questions, but the available numeric results are limited and the record does not report a multiplicity strategy. Safety counts likewise describe the recorded events in this study and cannot establish broader safety patterns.

The most defensible interpretation is consequently narrow: the posted data estimate the short-term mean FEV1 contrast between these two doses, with an interval that leaves considerable uncertainty. Broader conclusions require additional evidence and details not reported in the registry record.

17. Why This Trial Matters Statistically

This trial illustrates why an estimated difference should be read with its uncertainty. The primary point estimate is easy to compare across dose groups, but the confidence interval shows that the data do not pin down a single value or even a single direction for the underlying contrast. Reporting both the estimate and interval gives a more complete account than treating a p-value as a verdict.

The active-dose design also makes the estimand clear and limited. Randomization can support a comparison between the two assigned doses, while the absence of a placebo group means that the trial does not directly estimate either dose’s contrast with no active treatment. Identifying the exact comparison is essential to avoid extending a result beyond the question the design addresses.

The range of secondary measures shows the statistical challenge of interpreting multiple endpoints. Measures of lung function, symptoms, medication use, and asthma control can offer complementary information, but multiple unadjusted comparisons increase the risk of chance findings. The absence of a reported multiplicity plan is therefore important when deciding how much confirmatory weight to give secondary results.

Finally, the planning illustrations demonstrate how assumptions about the effect size and power target translate into participant requirements. They are useful for understanding design tradeoffs, but they are not a retrospective score of the study’s success. Keeping planning calculations separate from observed results helps prevent a hypothetical sample-size exercise from being mistaken for evidence about what the trial detected.

18. 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 primary assessment covers 2 weeks, so the result does not describe longer-term changes. The enrolled population is children aged greater than or equal to 6 and less than 12 years with asthma; the registry record does not report subgroup estimates by age or other participant characteristics. Generalization beyond the listed population cannot be assessed from the posted summary.

The comparison is between two active doses delivered with the same inhalation device. There is no listed placebo or untreated group, limiting interpretation of the within-group changes as effects attributable to treatment. The primary comparison estimates the difference between the assigned doses, not the effect of either dose against an untreated counterfactual.

Although the record names the full analysis set, it does not define its membership or report endpoint-specific analysis counts. Missing-data methods, adherence information, protocol deviations, and sensitivity analyses are not reported in the registry record. This makes it difficult to judge how the analysis population and unobserved measurements may have affected the posted estimate.

The registry lists systemic exposure and several clinical secondary outcomes, but numerical results are not reported for all of them in the outcome details. The absence of results for those outcomes limits assessment of the study’s broader stated aims. The record also does not report a multiplicity strategy or a clinically meaningful threshold for the primary measure.

There is a unit-label difference within the primary endpoint description: the listed unit is L, while its definition refers to mL. The reported arm means and contrast are presented in L in the primary results. This discrepancy in labeling should be kept in mind when interpreting the endpoint definition; the registry record does not explain it.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Efficacy and Safety of Indacaterol Acetate Delivered Via the Concept1 Inhalation Device in Children Greater or Equal to 6 and Less Than 12 Years of Age With Asthma — NCT02892019.
• Registry record last updated 2020-01-27; status last verified 2020-01.
• Results first posted 2020-01-27.
• 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.

22. Record Summary

The registry record describes a completed Phase 2 randomized, parallel-group, active-controlled study of once-daily indacaterol acetate 75 μg and 150 μg delivered via the Concept1 inhaler in children with asthma aged greater than or equal to 6 and less than 12 years. The official title describes a multicenter, double-blind study lasting 2 weeks, while the registry labels masking as quadruple.

The primary endpoint is change from baseline in pre-dose trough FEV1 after 2 weeks, analyzed in the full analysis set. The posted mean difference for 75 μg versus 150 μg is 0.041 L, with a 95% confidence interval from -0.054 to 0.136 L and an unadjusted p-value of 0.397. The interval includes zero and permits differences in either direction.

Planning illustrations use stated hypothetical assumptions and are not observed power. Details of the original sample-size justification, missing-data handling, multiplicity strategy, and complete statistical analysis plan are not reported in the registry record. The results support a limited description of the short-term active-dose comparison, not broader conclusions about placebo-controlled effects or longer-term outcomes.