A Safety and Efficacy Study of Beclomethasone Dipropionate Delivered Via Breath-Actuated Inhaler (BAI) or Metered-Dose Inhaler (MDI) in Participants >=12 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 >=12 Years Old With Persistent Asthma (NCT02031640), a randomized phase 3 study. The primary outcome is Standardized Baseline-adjusted Trough Morning 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 central question was whether beclomethasone dipropionate (BDP), delivered by a breath-actuated inhaler (BAI) or a metered-dose inhaler (MDI), changed standardized baseline-adjusted trough morning FEV1 over the treatment period compared with placebo in adolescents and adults with persistent asthma. The primary endpoint used measurements at baseline and scheduled follow-up visits through Week 12.

This is a comparison of the posted group estimates and their uncertainty, not a claim about an individual participant’s experience. The registry record gives a continuous lung-function outcome and comparisons with placebo. It does not report a threshold for a clinically important difference, so statistical estimates alone cannot establish whether an observed change would be meaningful to participants.

3. Trial Design

This was a Phase 3, randomized, double-blind, double-dummy, placebo-controlled, parallel-group study. It enrolled 1113 participants and is listed as completed. The study period was 12 weeks; the registry lists a start of 2013-12 and primary completion of 2014-11. The sponsor was Teva Branded Pharmaceutical Products R&D, Inc.

The five groups were BDP 320 mcg BAI, BDP 640 mcg BAI, BDP 320 mcg MDI, BDP 640 mcg MDI, and placebo BAI and MDI. BDP groups received their assigned inhaler twice daily. The placebo group used placebo versions of both inhalers twice daily. A double-dummy arrangement uses matching placebo devices so that treatment assignment can remain masked when the active treatments use different delivery devices. This is a general description of the design, not a claim about how masking performed in practice.

Randomization and double blinding help limit systematic differences in treatment allocation and outcome assessment. The parallel-group model means participants were assigned to a group rather than crossing between treatment groups. The registry record does not report the allocation ratio or the sequence-generation and concealment procedures. It also does not report the trial’s original sample-size justification, details of masking assessment, or whether interim analyses were planned.

The primary endpoint used trough morning FEV1 measurements obtained before the dose and before rescue bronchodilator treatment. Measurements were collected at Day 1 and Weeks 2, 4, 8, and 12, with spirometry data submitted to a central reading center. The posted primary analysis population required randomization, at least one dose, and at least one postbaseline trough morning FEV1 measurement. Its size is not the same as the overall enrollment count; the reason for the difference 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: There were two periods prior to treatment assignment: a screening period and a run-in period.

Screening Period

Reasons for not completing this period:

Run-In Period

Reasons for not completing this period:

Double-blind Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set- randomized patients with at least 1 dose of drug and 1 postbaseline trough am 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: Patients administered 4 inhalations from each of the 2 devices twice daily as per the double dummy study design: 1 treatment device or placebo and 1 placebo device for a total of 8 inhalations each time.

6. Primary Endpoint

The registry lists the primary outcome as Standardized Baseline-adjusted Trough Morning 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 was standardized baseline-adjusted trough morning FEV1 area under the effect curve from time 0 to 12 weeks, reported in liters. FEV1 is the volume of air exhaled during the first second of a forced expiratory maneuver. In this study, trough morning measurements were taken before study dosing and before rescue bronchodilator treatment. The baseline value was the measurement at randomization on Day 1.

The endpoint combines repeated lung-function measurements across the treatment period rather than relying on a single follow-up visit. The registry describes calculating baseline-adjusted AUEC with the trapezoidal rule, which approximates the area under a curve from measurements at successive times. Standardization divides the area by the duration used for that participant, allowing the endpoint to accommodate participants who left the study before Week 12. For participants completing the Week 12 assessment, the duration was 12 weeks; for earlier withdrawals, it was the duration through the last listed assessment.

This approach uses the trajectory of measured FEV1 and expresses it on a standardized time basis. That can retain information from participants with early discontinuation rather than requiring every participant to contribute a Week 12 measurement. It does not, by itself, show that missing measurements are unbiased or that the underlying causes of withdrawal are unrelated to outcomes. The registry record does not report a clinically important difference threshold for this endpoint.

7. Results Posted in the Registry

• BDP 320 mcg BAI: mean 0.09 versus 0.06 on control; difference 0.03 (95% CI -0.03 to 0.09), standardized effect d = 0.15; z-test p = 0.274.
• BDP 640 mcg BAI: mean 0.10 versus 0.06 on control; difference 0.05 (95% CI -0.02 to 0.11), standardized effect d = 0.20; z-test p = 0.148.
• BDP 320 mcg MDI: mean 0.04 versus 0.06 on control; difference -0.01 (95% CI -0.08 to 0.05), standardized effect d = -0.07; z-test p = 0.627.
• BDP 640 mcg MDI: mean 0.10 versus 0.06 on control; difference 0.04 (95% CI -0.02 to 0.10), standardized effect d = 0.18; z-test p = 0.193.

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 Using a Mixed Model for Repeated Measures (MMRM)

• 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 320 mcg BAI: mean 5.09 versus -5.52 on control; difference 10.62 (95% CI 3.47 to 17.76), standardized effect d = 0.40; z-test p = 0.004.
  • BDP 640 mcg BAI: mean 2.90 versus -5.52 on control; difference 8.42 (95% CI 1.28 to 15.56), standardized effect d = 0.32; z-test p = 0.021.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 320 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 640 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 Using a Mixed Model for Repeated Measures (MMRM)

• 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 320 mcg BAI: mean 4.44 versus -4.71 on control; difference 9.15 (95% CI 1.84 to 16.45), standardized effect d = 0.34; z-test p = 0.014.
  • BDP 640 mcg BAI: mean 4.46 versus -4.71 on control; difference 9.17 (95% CI 1.88 to 16.46), standardized effect d = 0.34; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for BDP 320 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 640 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 Using a Mixed Model for Repeated Measures (MMRM)

• 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 320 mcg BAI: mean -0.23 versus 0.48 on control; difference -0.70 (95% CI -1.05 to -0.36), standardized effect d = -0.57; z-test p = <0.001.
  • BDP 640 mcg BAI: mean -0.21 versus 0.48 on control; difference -0.69 (95% CI -1.03 to -0.35), standardized effect d = -0.56; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP 320 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 lower for BDP 640 mcg BAI than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes broaden the assessment beyond the primary FEV1 endpoint. The posted results include morning and evening peak expiratory flow (PEF), and weekly average total daily albuterol or salbutamol inhalations. Across those outcomes, the pattern is mixed by measure and treatment group: some reported comparisons favor the BDP group in the numerical direction of the outcome, while the primary FEV1 comparisons do not exclude zero. These secondary measures provide context, but they do not reverse or replace the primary result.

PEF is a separate lung-function measure from FEV1, and rescue inhaler use is a measure of medication use rather than spirometry. The secondary endpoint list also includes asthma symptom score and worsening-asthma-related withdrawal measures. Results for those listed outcomes are not reported in the registry record’s posted endpoint data. The registry lists seven outcome measures in total, but the scope and completeness of all secondary results cannot be determined from the listed results alone.

The registry describes MMRM analyses for the continuous repeated secondary measures. Their estimates should be understood with the same caution about model detail and missing-data assumptions: those specifications are not reported. The posted secondary p-values are not a substitute for the primary endpoint analysis.

When many outcomes and comparisons are examined, the chance of observing apparently notable results by chance can increase. This is a general multiplicity concern. The registry record does not report whether the secondary analyses were adjusted for multiple comparisons, whether they were designated as confirmatory, or what testing hierarchy was planned. Consequently, individual secondary findings carry less inferential weight than a prespecified primary result with a documented multiplicity strategy. They are useful as supporting or exploratory evidence, but should not be treated as independent confirmation of a primary effect.

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 Using a Mixed Model for Repeated Measures (MMRM)
• Change From Baseline in Weekly Average of Daily Evening Peak Expiratory Flow (PEF) Over the 12-week Treatment Period Using a Mixed Model for Repeated Measures (MMRM)
• 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 Using a Mixed Model for Repeated Measures (MMRM)
• Change From Baseline in the Weekly Average of the Total Daily Asthma Symptom Score Over Weeks 1-12 Using a Mixed Model for Repeated Measures (MMRM)
• Kaplan-Meier Estimates for Time to Withdrawal From Study Treatment Due to Meeting Stopping Criteria for Worsening Asthma
• Number of Participants Withdrawn From Study Due to Meeting Stopping Criteria for Worsening Asthma During the 12-Week Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The registry describes the primary analysis as ANCOVA and reports least-squares mean differences between each BDP group and placebo. A least-squares mean is a model-based group estimate. ANCOVA is a general method for comparing group means while accounting for specified covariates. The registry record does not list the covariates included in this primary model, so their identities or roles should not be inferred.

What does a least-squares mean difference represent?

A least-squares mean difference is the estimated contrast between two model-based group means, expressed in the outcome’s units. Positive estimates in this study indicate a higher adjusted endpoint estimate in the BDP group than in the placebo group; a negative estimate indicates a lower estimate. The primary measure is in liters. The direction of an estimate is not, on its own, a determination of clinical importance.

The posted arm summaries give a least-squares mean and standard error for each group. A standard error describes the estimated sampling uncertainty around a mean estimate. It is not a measure of how much individual participants varied. The sponsor’s comparisons provide confidence intervals, which express a range of values compatible with the fitted analysis under its statistical assumptions.

Why use repeated measurements?

The primary outcome incorporates measurements at baseline and follow-up visits, and the registry describes an area-under-the-curve calculation using the trapezoidal rule. In general, the trapezoidal rule approximates the area beneath a trajectory by joining observed measurements across time. Dividing by the relevant follow-up duration yields a standardized value. In this study, the endpoint definition states that this standardization accommodates participants who withdrew before the Week 12 measurement.

Several secondary outcomes were analyzed using a mixed model for repeated measures (MMRM). In general, this type of model analyzes repeated outcomes over time while accounting for the fact that measurements from the same participant are related. The registry lists the MMRM method for the secondary outcomes but does not provide full model specifications, such as the covariance structure, covariates, or missing-data assumptions. It would therefore be inappropriate to infer those details.

What does a confidence interval add?

A confidence interval communicates uncertainty around an estimated difference. A wider interval indicates less precision than a narrower interval, all else being equal. If an interval includes zero, the posted data are compatible with no group difference as well as with values on either side of zero. This does not mean every value in the interval is equally plausible, or that the interval assigns a probability to the true effect. The primary sponsor analyses report 95% confidence intervals.

The displayed recalculations use unadjusted comparisons derived from posted summary statistics. In general, such recalculations do not reproduce adjustments or details of a fitted model that are unavailable from summary data. The recalculated standard deviations are approximate, as indicated in the analysis information. The primary registry result remains the sponsor’s ANCOVA analysis, and the posted discrepancy flag is false.

How should p-values be read?

A p-value measures how unusual data at least as incompatible with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. The sponsor reports p-values for the primary comparisons; recalculated p-values are explicitly unadjusted. The registry record does not describe a multiplicity adjustment for the sponsor’s tests.

General statistical methods cannot settle design choices that are not documented. The trial’s original sample-size justification, interim-analysis plan, and full statistical analysis plan are not reported in the registry record. The posted planning illustrations are based on observed results and stated assumptions, rather than a documented reconstruction of the trial’s original planning.

11. Confidence Intervals and Precision

Precision is best judged from the confidence intervals, not from the point estimates alone. For the primary comparisons, the sponsor-reported 95% intervals all include zero. For BDP 320 mcg BAI, the interval runs from -0.027 to 0.095 liters; for BDP 640 mcg BAI, from -0.015 to 0.106 liters. For BDP 320 mcg MDI, it runs from -0.075 to 0.046 liters, and for BDP 640 mcg MDI, from -0.02 to 0.1 liters. These ranges include both lower and higher estimates relative to placebo.

The point estimates are therefore not precise enough to establish the direction of the primary difference in each comparison. An interval crossing zero is consistent with no difference, but also with possible differences in either direction. The interval does not show that all values within it are equally likely, and its width should not be interpreted without considering the endpoint scale and any clinically important threshold. Such a threshold is not reported in the registry record.

As a general statistical concept, a confidence interval reflects sampling uncertainty under the fitted model and its assumptions. It does not automatically account for every possible source of uncertainty, such as bias from missing data or selective reporting. The registry record does not provide enough information to assess all such sources. The listed standard errors describe uncertainty in the estimated group means; they are not standard deviations of participant-level FEV1.

The primary estimates and intervals are broadly consistent between the sponsor analyses and the unadjusted summary-statistic recalculations. The sponsor’s confidence intervals are the relevant ones for interpreting the trial’s reported ANCOVA analyses. Their inclusion of zero means that the results remain compatible with no primary difference, while the widths show that some nonzero differences also remain compatible with the data.

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 participants per arm for 80% power and participants per arm for 90% power. They are not total trial enrollment and do not describe the numbers observed in each study group. The calculations are planning illustrations based on the observed effect, not the trial’s own original design assumptions. The registry record does not report the original sample-size justification.

The stated illustration 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 to the stated fraction of the observed effect. The comparison rows consider planning for 100%, 75%, and 50% of the observed effect. These values are hypothetical targets for future planning, not effects established in advance by the registry record.

The 80% power column describes the number of participants per arm that the calculation estimates would be needed for an 80% chance of detecting the specified effect under the stated assumptions. The 90% column gives the corresponding planning count for a higher chance of detection. These are conditional planning quantities; they do not say whether this completed trial had a particular probability of finding a result. This is not observed power.

The planning curve expresses the same general relationship: when the effect to be detected is smaller, more participants are needed under the same assumptions. The figures are specific to the observed estimates and the stated calculation method. They should not be treated as recommendations or as a substitute for choosing a clinically relevant target and designing a future study around its full objectives.

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 = 0.034; pooled standard deviation σ = 0.225.
2. n = 2 × (1.96 + 0.842)² × 0.225² / 0.034² = 686.8, rounded up to 687 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 <- 0.034                      # observed difference in means
sigma <- 0.224890624193721                     # 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(2031640)
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 = 687 (80% power), 920 (90% power)
 75% of observed effect: n per arm = 1,221 (80% power), 1,635 (90% power)
 50% of observed effect: n per arm = 2,748 (80% power), 3,678 (90% power)
power.t.test: 687.7 
Simulated power at n = 687 per arm: 0.798 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary results come from ANCOVA and are the principal analyses to use when interpreting the registry’s primary endpoint. The summary-statistic recalculations are simple, unadjusted comparisons and are included as a check on the posted group summaries, not as a competing fitted analysis.

The recalculated differences are close to the sponsor-reported differences, and the corresponding intervals also span zero. The registry indicates no discrepancy between the recalculations and the sponsor’s analyses. This agreement supports the reading that the primary comparisons do not show a clear separation from placebo in the posted analysis, while the recalculations do not reproduce every detail of ANCOVA.

The sponsor reported p-values of 0.272, 0.141, 0.636, and 0.193 across the four primary comparisons. The recalculated unadjusted p-values are 0.274, 0.148, 0.627, and 0.193, respectively. Small differences between these analyses can arise because they use different analysis procedures and available information. The sponsor’s model-based estimates, confidence intervals, and p-values take precedence for the trial’s reported result. The registry record does not provide enough model detail to reconstruct the ANCOVA independently.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary endpoint and multiple secondary outcomes, with several treatment-versus-placebo comparisons. It does not report a multiplicity-control procedure, a testing hierarchy, or whether any secondary outcomes were intended to support formal confirmatory claims. Without those details, the familywise interpretation of the reported p-values cannot be established. The listed p-values should not be assumed to have been adjusted.

The registry record does not report interim analyses, the original sample-size justification, or the complete statistical analysis plan. It also does not specify all model covariates or the missing-data assumptions used for the primary and secondary analyses. These omissions limit independent assessment of the planned analysis and how closely the posted results follow that plan.

The primary analysis population is defined as randomized participants who received at least one dose and had at least one postbaseline trough morning FEV1 measurement. This is the registry’s stated full analysis set; it is not simply all enrolled participants. The endpoint description says standardization accommodates participants who discontinued before Week 12 by using their available follow-up duration. That endpoint construction is not enough to determine how missing measurements were handled in the fitted ANCOVA model or whether sensitivity analyses were conducted.

For the secondary outcomes, the registry names MMRM but does not report the model’s missing-data assumptions or sensitivity analyses. In general, a model can use available repeated observations without requiring every participant to have every scheduled measurement, but that does not eliminate the need to consider why observations are missing. The reasons for missing measurements, withdrawal patterns, and robustness checks are not reported in the registry record.

These limitations do not invalidate the posted estimates, but they constrain how confidently they can be interpreted as a complete account of the prespecified statistical plan. They also make it difficult to assess how multiplicity and missingness may have affected the overall evidential picture.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: gastroenteritis (0.9%), hypokalaemia (0.9%), renal failure acute (0.9%), asthma (0.9%), abdominal pain (0.9%).

The registry reports serious adverse events, other adverse events, and deaths by group. In the four BDP treatment groups, serious adverse events affected 1, 1, 1, and 2 participants, respectively; the placebo BAI and MDI group reported 0. Deaths were reported as 0 in each of these five groups. The risk counts listed for the treatment groups range from 106 to 107, and the placebo group lists 106 participants at risk.

During the run-in period, the registry lists 1 serious adverse event and 8 other adverse events among 532 randomized participants, with 0 deaths. The run-in period is presented separately from the randomized treatment groups and should not be combined with them when reading group-specific treatment-period results.

The listed serious-event terms include gastroenteritis, hypokalaemia, renal failure acute, asthma, abdominal pain, and diverticular perforation, each reported as 0.9%. These are event terms, not evidence that every listed event occurred in every treatment group. The figures describe events recorded in this trial; they do not establish comparative safety beyond the study period or in other populations. The registry record does not provide a detailed narrative for each event in the information.

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

The primary results show estimated differences in standardized baseline-adjusted trough morning FEV1 between each BDP group and placebo. The sponsor-reported confidence intervals include zero in every comparison, and the reported p-values do not indicate a statistically distinguishable difference in these analyses. The estimates therefore leave uncertainty about both the direction and size of the primary treatment-versus-placebo differences.

This does not demonstrate that the groups were identical, nor does it establish that BDP had no effect. An inconclusive comparison is different from evidence of equivalence or noninferiority, which would require a stated margin and an analysis designed for that purpose. Such a margin or design is not reported in the registry record. The estimates also do not answer whether the difference is clinically important, because a clinical-importance threshold is not reported.

The results concern the listed population, analysis set, outcome, and 12-week treatment period. They do not establish durability beyond the study period or outcomes for populations not represented in the registry description. The primary endpoint is a group-level lung-function measure; it does not directly describe every participant’s symptom experience, rescue medication use, or later course.

Secondary outcomes provide additional dimensions, including PEF and rescue inhaler use, but their multiplicity handling and confirmatory status are not reported. Their findings therefore should be read as supporting context rather than a basis for overriding the primary result. Likewise, the safety counts describe events observed during the trial and are not a guarantee about events that may occur outside it.

Overall, the posted results support a cautious statistical conclusion: the primary comparisons are estimated with uncertainty that includes no difference, and the registry information does not establish a clinically meaningful effect in either direction. This is a description of what the reported analysis can and cannot resolve, not treatment advice.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate, confidence interval, and p-value need to be read together. The primary comparisons have numerical estimates in both directions, while each sponsor-reported interval includes zero. The p-values alone would not communicate the range of compatible effects or the uncertainty around their direction. The interval-based reading makes clear that the analysis does not establish a placebo difference, but also does not establish that the groups are identical.

The endpoint also highlights a design choice in longitudinal trials. A standardized area-under-the-curve outcome combines measurements across visits and uses the available follow-up duration for participants who discontinued before the last assessment. This can make better use of observed follow-up than a single final-visit measure, while leaving important questions about missingness and model assumptions that must be addressed separately.

Having two delivery devices and two doses creates multiple treatment comparisons, and the study also evaluates several secondary measures. That makes clarity about prespecification, multiplicity, and model details important. The registry record provides the design and several results, but does not report the full statistical plan, multiplicity strategy, or original sample-size justification. Those gaps matter when interpreting a collection of results rather than a single endpoint.

Finally, planning calculations based on observed effects can illustrate how sample requirements change when a target effect is smaller. They are not a retrospective measure of a trial’s success or a substitute for prospective design assumptions. Distinguishing such illustrations from the sponsor’s fitted analysis helps prevent a planning scenario from being mistaken for an observed result.

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 does not report the original sample-size justification, so the rationale for the enrolled sample cannot be assessed from these results. It also does not provide the full statistical analysis plan, the ANCOVA covariates, or enough detail to reconstruct the sponsor’s primary model independently. The reported primary differences and intervals remain the appropriate registry results, but the model’s full specification is not available in the record.

The primary endpoint was standardized to accommodate participants who discontinued before Week 12. The registry does not state the assumptions about missing outcomes, reasons for discontinuation, or sensitivity analyses used to test the robustness of that approach. The full analysis set requires at least one postbaseline primary measurement, so participants without such a measurement are not part of that defined population.

Multiple primary comparisons against placebo and multiple secondary outcomes raise questions about multiplicity. The registry record does not report a correction method, testing hierarchy, or confirmatory status for the secondary analyses. It also does not report results for every outcome named in the secondary-outcome list. This limits a complete assessment of the planned outcome family and increases the importance of distinguishing the primary analysis from secondary findings.

The study lasted 12 weeks, and the reported data do not establish longer-term outcomes. The registry description specifies participants 12 years of age and older with persistent asthma; it does not provide enough detail in the registry record listed for assessing how representative the enrolled participants were of broader clinical populations. A threshold for clinical importance is also not reported, making it impossible to classify the size of a compatible difference as clinically meaningful from these results alone.

The summary-statistic recalculations are unadjusted and use approximate standard deviations. They serve as a check, not as a substitute for the sponsor’s fitted analyses.

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 >=12 Years Old With Persistent Asthma — NCT02031640.
• Registry record last updated 2021-11-09; status last verified 2021-11.
• Results first posted 2018-01-05.
• 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

NCT02031640 is a completed Phase 3 randomized, double-blind, double-dummy, placebo-controlled, parallel-group study of BDP in participants 12 years of age and older with persistent asthma. It enrolled 1113 participants and compared two daily doses delivered by BAI or MDI with placebo BAI and MDI over 12 weeks.

The primary endpoint was standardized baseline-adjusted trough morning FEV1 AUEC from time 0 to 12 weeks. Sponsor-reported ANCOVA comparisons against placebo had 95% confidence intervals that included zero. The listed secondary findings cover PEF and rescue inhaler use, while some other listed secondary outcomes have no results reported in the registry record. Safety summaries include serious and other adverse events and no reported deaths in the randomized groups.

The registry does not report the original sample-size justification, full statistical analysis plan, multiplicity strategy, or detailed missing-data assumptions. The posted estimates should therefore be interpreted with their stated uncertainty and the limits of the available analysis detail.