A Safety and Efficacy Study of Beclomethasone Dipropionate Delivered Via Breath-Actuated Inhaler (BAI) or Metered-Dose Inhaler (MDI) in Participants Ages 4-11 Years Old With Persistent Asthma: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Safety and Efficacy Study of Beclomethasone Dipropionate Delivered Via Breath-Actuated Inhaler (BAI) or Metered-Dose Inhaler (MDI) in Participants Ages 4-11 Years Old With Persistent Asthma (NCT02040766), a randomized phase 3 study. The primary outcome is Standardized Baseline-adjusted Trough Morning Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Area Under the Effect Curve From Time 0 to 12 Weeks (AUEC(0-12wk)).

2. Clinical Question

The registry describes a phase 3 randomized, parallel-group study. The central statistical question is about group-level changes in a spirometry-based measure, not about an individual child’s response. The posted primary results compare each of the four BDP device-and-dose groups with the placebo group. They do not report a direct randomized comparison of BAI against MDI at the same dose, so the reported placebo comparisons should not be read as a formal test of which device is preferable.

3. Trial Design

The registry describes a randomized, double-blind, double-dummy, placebo-controlled, parallel-group study lasting 12 weeks. Enrollment was 628, and the study status is completed. The study included children ages 4 through 11 years with persistent asthma. The recorded start was 2013-12 and primary completion was 2016-02.

There were five treatment groups: placebo BAI and MDI; BDP 80 mcg BAI; BDP 160 mcg BAI; BDP 80 mcg MDI; and BDP 160 mcg MDI. In the active groups, the participant used the active device and a matching placebo device. The placebo group used placebo through both devices. The study description says that participants took one inhalation from each of two devices twice daily, with caregiver assistance as needed. This matching-device arrangement was intended to maintain blinding across treatment groups.

The primary outcome was assessed at Day 1 (baseline) and Weeks 2, 4, 8, and 12. The registry describes electronic spirometry and central reading-center evaluation; the selected FEV1 measurement was the best attempt meeting the stated maneuver criteria. The posted primary result is a least-squares mean with standard error for each group. Although the registry lists enrollment, the number in each primary analysis group differs from the safety-group counts; the endpoint population is defined separately as the full analysis set.

The registry record does not report the original sample-size justification or the trial’s complete statistical analysis plan. It also does not state in the material available for these results how randomization was implemented or whether interim analyses were planned.

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: Patients were randomly assigned to treatment through a qualified randomization service provider. This system was used to ensure a balance across treatment groups, within each stratum

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The full analysis set (FAS) included all patients in the ITT population who received at least 1 dose of study drug and had at least 1 post baseline trough morning (pre-dose and pre-rescue bronchodilator) assessment of percent predicted FEV1.

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.

Population: Intent to treat (ITT) population

6. Primary Endpoint

The registry lists the primary outcome as Standardized Baseline-adjusted Trough Morning Percent Predicted Forced Expiratory Volume in 1 Second (FEV1) Area Under the Effect Curve From Time 0 to 12 Weeks (AUEC(0-12wk)), measured over Day 1 (baseline), Weeks 2, 4, 8, 12.

The primary endpoint is the standardized baseline-adjusted trough morning percent predicted FEV1 area under the effect curve from time 0 to 12 weeks. FEV1 is the amount of air forcibly exhaled in the first second of a forced expiratory maneuver. The registry identifies the endpoint unit as liters, while the endpoint title specifies percent predicted FEV1; the record does not clarify this distinction.

Measurements were taken in the morning before study dosing and before rescue bronchodilator treatment. Baseline was defined using baseline trough morning percent predicted FEV1. Spirometry was performed electronically, and a central reading center evaluated the pulmonary-function data. The endpoint description specifies use of the highest FEV1 from acceptable and repeatable maneuvers, subject to the stated maximum number of attempts.

A baseline-adjusted measure accounts statistically for the starting value when comparing follow-up outcomes. An area under the effect curve combines information across the scheduled follow-up period rather than relying on a single visit alone. Such a summary can represent the pattern of lung-function response over time, although its interpretation depends on the analysis model and the definition used for the curve. The registry reports a least-squares mean and standard error for each group. These are model-based group summaries, not raw individual measurements, and they should be interpreted alongside the sponsor’s reported between-group comparisons and their confidence intervals.

7. Results Posted in the Registry

• BDP 80 mcg BAI: mean 5.43 versus 2.62 on control; difference 2.81 (95% CI 0.75 to 4.87), standardized effect d = 0.36; z-test p = 0.007.
• BDP 160 mcg BAI: mean 3.25 versus 2.62 on control; difference 0.63 (95% CI -1.42 to 2.68), standardized effect d = 0.08; z-test p = 0.546.
• BDP 80 mcg MDI: mean 3.54 versus 2.62 on control; difference 0.92 (95% CI -1.13 to 2.97), standardized effect d = 0.12; z-test p = 0.379.
• BDP 160 mcg MDI: mean 3.71 versus 2.62 on control; difference 1.09 (95% CI -0.96 to 3.14), standardized effect d = 0.14; z-test p = 0.297.

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.

Change From Baseline in Weekly Average of Daily Trough Morning Peak Expiratory Flow (PEF) Over the 12-week Treatment Period

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BDP 80 mcg BAI: mean 15.60 versus 4.30 on control; difference 11.30 (95% CI 5.49 to 17.11), standardized effect d = 0.48; z-test p = <0.001.
  • BDP 160 mcg BAI: mean 12.80 versus 4.30 on control; difference 8.50 (95% CI 2.64 to 14.36), standardized effect d = 0.36; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 80 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 160 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Weekly Average of Daily Evening Peak Expiratory Flow (PEF) Over the 12-week Treatment Period

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • BDP 80 mcg BAI: mean 13.10 versus 1.40 on control; difference 11.70 (95% CI 5.88 to 17.52), standardized effect d = 0.50; z-test p = <0.001.
  • BDP 160 mcg BAI: mean 11.40 versus 1.40 on control; difference 10.00 (95% CI 4.14 to 15.86), standardized effect d = 0.43; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 80 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 160 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the Weekly Average of Total Daily (24-hour) Use of Albuterol/Salbutamol Inhalation Aerosol (Number of Inhalations) Over Weeks 1-12

• 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:
  • BDP 80 mcg BAI: mean -0.72 versus -0.36 on control; difference -0.36 (95% CI -0.55 to -0.17), standardized effect d = -0.47; z-test p = <0.001.
  • BDP 160 mcg BAI: mean -0.50 versus -0.36 on control; difference -0.14 (95% CI -0.33 to 0.05), standardized effect d = -0.18; z-test p = 0.151.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP 80 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between BDP 160 mcg BAI and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists secondary outcomes covering morning and evening peak expiratory flow, rescue albuterol/salbutamol use, asthma symptom score, and time to withdrawal for worsening asthma. Detailed numerical results are posted for morning peak flow, evening peak flow, and rescue-medication use. The posted patterns for the two peak-flow measures are broadly aligned with the lung-function direction of the primary endpoint, while the rescue-use outcome offers a different, supportive perspective. These measures address related but distinct aspects of asthma control and should not be treated as substitutes for the primary endpoint.

The secondary outcomes do not all have the same kind of scale or interpretation. Peak-flow changes are continuous measures, rescue use is recorded as number of inhalations, symptom score is a score-based measure, and time to withdrawal is a time-to-event outcome. The registry record does not report detailed numerical results for the symptom-score or withdrawal outcomes in the information available for this analysis. Their absence from the posted detailed results should not be interpreted as evidence of no effect.

Secondary comparisons generally carry less inferential weight than the prespecified primary comparison, particularly when many outcomes or treatment contrasts are examined. Unless the testing plan controls the chance of false-positive findings across those analyses, an apparently notable secondary result can arise by chance. The registry record does not report whether multiplicity adjustments were used. Accordingly, secondary results are best viewed as supportive or exploratory evidence, interpreted alongside their estimates, uncertainty, and relevance to the primary question rather than as independent confirmation.

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

• Change From Baseline in Weekly Average of Daily Trough Morning Peak Expiratory Flow (PEF) Over the 12-week Treatment Period
• Change From Baseline in Weekly Average of Daily Evening Peak Expiratory Flow (PEF) Over the 12-week Treatment Period
• Change From Baseline in the Weekly Average of Total Daily (24-hour) Use of Albuterol/Salbutamol Inhalation Aerosol (Number of Inhalations) Over Weeks 1-12
• Change From Baseline in the Weekly Average of the Total Daily Asthma Symptom Score Over Weeks 1-12
• Kaplan-Meier Estimates For Time to Withdrawal Due to Meeting Stopping Criteria for Worsening Asthma During the 12-week Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports a least-squares mean and standard error for the primary outcome in each treatment group. A least-squares mean is a model-based estimate of a group average, rather than necessarily the simple arithmetic average of every observed value. Its interpretation depends on the model and adjustment terms used. The registry identifies the primary comparison method as ANCOVA, but the specific covariates and other model details are not reported in the registry record.

What does baseline adjustment do?

In general, baseline adjustment accounts for the starting measurement when estimating follow-up group differences. This can improve the comparability of estimates when participants begin at different levels on the endpoint. The primary outcome is explicitly described as baseline-adjusted, but the full model specification is not reported in the registry record. It is therefore not possible to assess from the posted information which variables, beyond baseline, were included in the model or how model assumptions were checked.

How should the reported comparison be read?

The sponsor’s primary comparisons are mean differences between each active-treatment group and placebo, estimated using ANCOVA. The estimate is expressed in the endpoint’s recorded unit. A positive estimate indicates that the estimated value for the active group is higher than the placebo estimate under the stated comparison; it is not, on its own, a judgment about clinical benefit. The 95% confidence interval expresses uncertainty about the estimated difference under the analysis. If that interval includes zero, the posted result remains compatible with no difference as well as with differences in either direction at the confidence level used.

The posted recalculations are simpler, unadjusted comparisons based on group summary statistics. The group standard errors were used to approximate standard deviations, and the resulting calculations do not reproduce the sponsor’s adjusted ANCOVA model. These re-calculations can help readers inspect the direction and approximate scale of the comparisons, but they omit the trial model’s adjustment and any other features of the sponsor’s analysis. The record flags a discrepancy; accordingly, the sponsor’s own analysis takes precedence.

What does a p-value contribute?

In general, a p-value describes how compatible the observed data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. P-values are best read with the estimated difference and confidence interval, rather than in isolation. The reported comparisons are framed as superiority analyses. Whether and how the inference accounts for the multiple comparisons is not reported in the registry record.

What is the analysis population?

The full analysis set included patients in the intention-to-treat population who received at least one dose of study drug and had at least one post-baseline trough morning assessment of percent predicted FEV1. This definition requires both treatment exposure and a follow-up assessment for inclusion in the primary analysis. The registry record does not report the missing-data method, the extent or pattern of missing primary measurements, or sensitivity analyses for missing data. As a result, the posted information does not allow a full evaluation of how incomplete follow-up may have affected the estimates.

What do the secondary models add?

For the posted secondary outcomes, the registry lists mixed models analyses for comparisons of selected groups. In general, mixed models can use repeated measurements and account for the correlation of observations from the same participant. The full model specification, covariance structure, and missing-data assumptions are not reported in the registry record. The reported secondary comparisons therefore need to be interpreted from the estimates and intervals the sponsor posted, without assuming details that are absent from the record.

11. Confidence Intervals and Precision

A confidence interval conveys the range of effect estimates reasonably compatible with the data and the analysis assumptions at the stated confidence level. It communicates precision as well as direction: a narrower interval indicates less uncertainty about the estimate than a wider interval. It does not mean that the true effect has a specified probability of lying inside the particular calculated interval.

For the primary endpoint, the sponsor reported 95% confidence intervals for each active-treatment comparison with placebo. The interval for BDP 80 mcg BAI was 0.796 to 4.821 and did not include zero. The intervals for BDP 160 mcg BAI, BDP 80 mcg MDI, and BDP 160 mcg MDI extended across zero. Those intervals therefore leave greater uncertainty about the direction of the underlying difference than the BDP 80 mcg BAI interval. The endpoints of each interval also show that the possible effect sizes remain meaningfully spread around the point estimate; precision should not be judged from the estimate alone.

The posted group standard errors for the primary estimates range from 0.732 to 0.744. Standard errors describe the uncertainty of the estimated group means under the model, whereas the sponsor’s confidence intervals describe uncertainty in the between-group differences. These quantities answer related but distinct questions.

The re-calculated intervals are based on unadjusted summary statistics and do not exactly match the sponsor’s ANCOVA intervals. Given the discrepancy noted in the registry record, the sponsor’s intervals should guide interpretation of the trial’s primary comparisons. Confidence intervals also do not address every source of uncertainty: they do not resolve questions about missing data, model specification, multiplicity, or clinical importance. Those matters require information beyond interval width.

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 illustrations describe planning under specified assumptions, not the trial’s original design. For these continuous-outcome comparisons, figures are participants per arm, not total participants or total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses a stated fraction of the observed effect as the effect to detect. The original trial’s own sample-size assumptions and justification 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 assumed effect under those planning assumptions, if that effect were present and the assumptions held. The 90% power column gives the corresponding illustration for a design with a 90% chance. These are design-planning probabilities under a model, not guarantees about the result of a future study. This is not observed power.

Rows using 100% of the observed effect use the observed point estimate as the planning target. Rows for 75% or 50% of the observed effect represent smaller target effects; smaller effects generally require more participants to detect with the same design assumptions. The figures can therefore change substantially as the assumed effect is reduced. The curve should be read in the same way: it illustrates how the planning requirement changes with the assumed effect, rather than showing a measured property of this completed trial.

These calculations are based on observed estimates from the posted results, which can be uncertain. They do not account for features not included in the stated assumptions, such as multiplicity or missing data. They are best used to understand the relationship between effect size, sample size, and target power, rather than as a recommendation for a definitive future design.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 2.810; pooled standard deviation σ = 7.864.
2. n = 2 × (1.96 + 0.842)² × 7.864² / 2.810² = 122.9, rounded up to 123 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 <- 2.81                      # observed difference in means
sigma <- 7.86368608292643                     # 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(2040766)
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 = 123 (80% power), 165 (90% power)
 75% of observed effect: n per arm = 219 (80% power), 293 (90% power)
 50% of observed effect: n per arm = 492 (80% power), 659 (90% power)
power.t.test: 123.9 
Simulated power at n = 123 per arm: 0.793 (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 ANCOVA mean differences for each active group versus placebo, with 95% confidence intervals and p-values. The reported differences were 2.81 for BDP 80 mcg BAI, 0.63 for BDP 160 mcg BAI, 0.92 for BDP 80 mcg MDI, and 1.09 for BDP 160 mcg MDI. The sponsor’s interval for BDP 80 mcg BAI was 0.796 to 4.821; the other reported intervals included zero.

The recalculated estimates are simple unadjusted comparisons derived from the posted group summaries. They are close in broad direction to the sponsor’s estimates, but the recalculated confidence limits and p-values do not match the ANCOVA results exactly. That difference is expected to matter because the recalculation does not reproduce the sponsor’s adjusted analysis. The registry record marks a discrepancy, so the sponsor’s own analysis takes precedence for interpretation of the trial’s results.

The recalculations serve as a limited numerical cross-check, not an alternative confirmatory analysis. They do not reveal which particular model feature accounts for the difference, because the complete model specification is not reported in the registry record. The sponsor results should also be read as separate comparisons with placebo; they do not establish direct differences between BAI and MDI or between dose levels.

15. Multiplicity, Missing Data and Analysis Populations

The primary outcome was compared between placebo and each of four active-treatment groups. The registry also lists several secondary outcomes and multiple analyses. Conducting multiple statistical tests increases the chance that at least one result will appear notable even when there is no underlying effect. Statistical approaches can control this multiplicity, for example by adjusting significance thresholds or organizing testing hierarchically, but the registry record does not report whether such methods were used. The posted p-values therefore should not be assumed to account for all comparisons.

The registry describes the primary analysis population as the full analysis set, requiring study-drug exposure and at least one post-baseline trough morning assessment. This definition is useful for understanding who contributed to the primary endpoint analysis, but it does not answer how missing measurements were handled after inclusion in the analysis set. The missing-data method, the extent and reasons for missingness, and sensitivity analyses are not reported in the registry record. If missingness differed across groups or was related to outcomes, that could affect estimates; the posted record does not provide enough information to assess that possibility.

The record identifies ANCOVA for the sponsor’s primary analyses and mixed models analyses for certain secondary outcomes. It does not provide the complete statistical analysis plan, model covariates, detailed assumptions, or interim-analysis information. It also does not report the original sample-size justification. These omissions limit assessment of whether the analysis followed a prespecified plan and how robust the findings are to alternative assumptions.

These points do not invalidate the posted results, but they narrow what can be concluded from them. The estimates and confidence intervals describe the analyses as reported; they cannot by themselves settle concerns about unreported multiplicity handling, missing data, or model choices.

16. Safety Results

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

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events by group, with the number at risk and the number affected. It records zero serious adverse events for the run-in placebo group and for each of the five treatment groups. The run-in group is listed separately from the randomized treatment groups, so it should not be combined with them when interpreting treatment-period safety.

The number at risk differs across the listed groups, and the safety counts are not the same as the primary endpoint analysis counts. These are registry-recorded event counts, not estimates of comparative risk. No deaths value is reported for the listed groups; death information is therefore not reported in the registry record.

The record also includes counts for other adverse events, but these figures alone do not describe event type, severity, duration, or whether an event was considered related to study treatment. Zero recorded serious events in the registry does not establish that no safety concerns are possible, particularly when interpreting a study of this size and duration. Safety conclusions require the full event definitions and reporting context, which are not contained in these summary figures.

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

The primary results describe estimated group differences in a spirometry-based endpoint over the 12-week treatment period. In the sponsor’s analysis, the BDP 80 mcg BAI comparison had a positive estimated difference from placebo and a 95% confidence interval that did not include zero. The other three reported comparisons had confidence intervals that included zero. These results are specific to the trial’s endpoint, population, follow-up period, and analysis.

A result that is statistically distinguishable from zero is not automatically clinically important. The registry record does not give a threshold for a clinically meaningful change in the primary measure, and the endpoint unit description does not fully clarify the scale. The posted group estimates also do not show how much participants varied individually or how many experienced a particular level of change.

The comparisons are each against placebo. They do not test whether BAI is better than MDI, whether one dose is better than another, or whether the apparent pattern across groups reflects a true difference between devices or doses. Such claims would require the relevant direct comparisons and uncertainty estimates.

The results also do not establish effects beyond the recorded follow-up period. The record describes a 12-week study and does not provide longer-term outcome information in these results. In addition, uncertainty about multiplicity, missing-data handling, and full model specification remains because those details are not reported in the registry record.

In general, a trial estimate is evidence about an average contrast under a specified design and analysis. It is not a prediction of an individual participant’s outcome and should not be treated as medical advice. The appropriate statistical reading is that the sponsor reported a clearer placebo contrast for one active group on this endpoint, while the other primary comparisons remain less conclusive in the posted analysis.

18. Why This Trial Matters Statistically

This trial offers a useful example of why treatment labels alone are not enough to interpret a clinical result. The study varied both dose and delivery device, used a placebo group, and measured lung function repeatedly over the treatment period. The primary analysis therefore raises questions about the outcome definition, baseline adjustment, and how the reported average contrast relates to the uncertainty around it.

It also illustrates the importance of distinguishing group estimates from between-group effects. A higher least-squares mean in an active group does not by itself answer whether the group differs from placebo. That question is addressed by the contrast and its confidence interval. Here, the sponsor’s reported primary comparison for BDP 80 mcg BAI is more clearly separated from zero than the other reported placebo contrasts, but those comparisons do not establish differences between active devices or doses.

The record is also a practical case for comparing sponsor analyses with simple recalculations without treating them as interchangeable. A summary-statistic recalculation can provide a check on direction and scale, yet it cannot reproduce an adjusted model when the model details and individual-level data are unavailable. The discrepancy flag makes the distinction especially important: the sponsor’s analysis is the primary reference.

Finally, the record shows how uncertainty about multiplicity, missing data, and analysis details can constrain interpretation even when numerical results are available. Statistical significance is not a complete account of evidence, precision, or clinical meaning. Reading estimates alongside confidence intervals and the limits of the registry record gives a more careful account of what the trial can support.

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.

Several limitations are specific to interpreting this trial’s posted results. The primary endpoint title refers to standardized baseline-adjusted trough morning percent predicted FEV1, while the registry identifies the unit as liters. The record does not explain this difference, so the exact scale should be treated cautiously. The primary endpoint also uses an area-under-the-effect-curve summary, but the detailed calculation and model specification are not reported.

The sponsor’s primary ANCOVA estimates differ from the simple unadjusted recalculations. The recalculations rely on approximated standard deviations derived from group standard errors and do not reproduce the adjusted analysis. Since the registry flags a discrepancy, the sponsor results take precedence; the reason for the numerical differences is not fully documented in the registry record.

The record does not report the original sample-size rationale, multiplicity procedure, missing-data method, complete analysis plan, model covariates, or interim-analysis information. It also does not provide detailed numerical results for all listed secondary outcomes. These gaps limit evaluation of robustness and the weight that should be assigned to secondary findings.

The study followed participants for 12 weeks. The posted results therefore do not establish longer-term patterns. The primary analysis population required a post-baseline assessment, and the record does not describe the amount or handling of missing follow-up data. The safety summary records serious adverse events, but it does not provide enough detail to characterize the nature or broader context of adverse events. These constraints call for a focused interpretation of the reported comparisons rather than broad conclusions beyond the measured outcomes and follow-up.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Safety and Efficacy Study of Beclomethasone Dipropionate Delivered Via Breath-Actuated Inhaler (BAI) or Metered-Dose Inhaler (MDI) in Participants Ages 4-11 Years Old With Persistent Asthma — NCT02040766.
• Registry record last updated 2021-11-09; status last verified 2021-11.
• Results first posted 2018-02-12.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, double-blind, double-dummy, placebo-controlled, parallel-group phase 3 study of BDP delivered by BAI or MDI in children ages 4-11 with persistent asthma. The treatment period was 12 weeks, and enrollment was 628. Four active dose-and-device groups were compared with placebo delivered through both inhalers.

The primary outcome was baseline-adjusted trough morning percent predicted FEV1 summarized as an area under the effect curve. The sponsor reported ANCOVA comparisons with placebo; the BDP 80 mcg BAI confidence interval did not include zero, while the other reported primary intervals included zero. Simple recalculations differ from the sponsor analysis, and the sponsor’s results take precedence. The record does not report several details needed to fully evaluate multiplicity, missing data, model specification, or the original sample-size rationale.