Study of an Investigational Nasal Aerosol or Placebo Nasal Aerosol in Children (Ages 6-11) With Seasonal Allergies: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of an Investigational Nasal Aerosol or Placebo Nasal Aerosol in Children (Ages 6-11) With Seasonal Allergies (NCT01307319), a randomized phase 3 study. The primary outcome is Change From Baseline in the Average Morning (AM) and Evening (PM) Subject-Reported Reflective Total Nasal Symptom Score (rTNSS) During the Two Weeks of Treatment.

2. Clinical Question

The primary comparison concerns change from baseline over the two weeks of treatment, rather than a single symptom or a single measurement. Participants recorded the reflective score twice daily, with help from parents, guardians, or caregivers as needed. The two active-dose groups allow the posted results to be read as separate comparisons with placebo. The record also includes an instantaneous symptom-score endpoint as a secondary outcome. That measure concerns symptoms at the time of recording, whereas the primary reflective measure summarizes the preceding 12 hours.

The posted treatment contrasts are negative, consistent with greater decreases in symptom scores in the active groups than in the placebo group. The registry record also reports mixed-model analyses for both active-dose comparisons. These results describe the study’s measured outcomes; they do not establish how important the differences are to children and families, because a threshold for a clinically important change is not reported in the registry record.

3. Trial Design

This was a phase 3, randomized, quadruple-masked, parallel-group study. It compared two BDP HFA nasal aerosol doses with placebo in children with seasonal allergic rhinitis. The registry record reports enrollment of 715 and a completed study. The reported study dates are 2011-03 for the start and 2011-07 for primary completion.

The three treatment groups were BDP HFA 80 mcg/day, BDP HFA 160 mcg/day, and placebo nasal aerosol once daily. Each regimen was administered once daily for 15 days. The active treatments were delivered as one spray in each nostril; the placebo was described as a spray with no medication in each nostril. The registry record identifies the study as randomized and parallel, but the specific allocation method and the details of sequence generation or concealment are not reported in the registry record.

Quadruple masking indicates that the record classifies the study as masked at four roles or levels, but which roles were masked and how masking was maintained are not reported in the registry record. The planned sample-size justification, the trial’s original power assumptions, and any interim analyses are not reported in the registry record. The planning illustrations elsewhere on this page are based on posted results and are not a substitute for those original design details.

The primary outcome was change from baseline in average morning and evening subject-reported reflective Total Nasal Symptom Score during the two weeks of treatment. The posted population definition for that endpoint includes randomized participants who received at least one dose and had at least one post-baseline assessment. The registry record notes that two enrolled participants were excluded from the described population: one was randomized in error and did not receive test medication. The reason for the other participant’s exclusion 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: A total of 1026 subjects were screened and 906 were enrolled and participated in the Run-in Period. Of the 906 enrolled subjects, 715 were randomized to treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: The intent to treat (ITT) population included all randomized participants who received at least one dose of randomized study medication and had at least one post-baseline assessment. Two enrolled participants were excluded. One was randomized in error and did not receive test medication. The other provided no post-baseline assessment.

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: Safety population: the safety population included all randomized participants who received at least one dose of randomized study medication.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in the Average Morning (AM) and Evening (PM) Subject-Reported Reflective Total Nasal Symptom Score (rTNSS) During the Two Weeks of Treatment, measured over Baseline (Day -4 to Day 1 predose), Days 1 (postdose) to Day 15.

The primary endpoint is change from baseline in the average morning and evening reflective Total Nasal Symptom Score, or rTNSS, during the two weeks of treatment. Participants assessed four symptoms: runny nose, nasal congestion, nasal itching, and sneezing. Each symptom was scored from 0, absent, to 3, severe. The total score ranged from 0 to 12, with higher scores representing more severe symptoms.

The reflective score asks participants to consider symptom severity over the 12 hours before recording it. Scores were recorded in the morning and evening, with parents, guardians, or caregivers assisting as needed. Baseline was defined as the average morning and evening rTNSS over the four days before randomization. The endpoint then summarizes change from that baseline through the treatment period, which the record describes as baseline (Day -4 to Day 1 predose) and Days 1 (postdose) to Day 15.

A repeated symptom measure can represent the pattern over a treatment period more fully than a single assessment. The reflective format is intended to capture symptoms across the preceding interval, while the morning and evening assessments provide repeated reports. The posted group results are least-squares means with standard errors. Negative changes indicate that reported scores fell from baseline. On this scale, that direction corresponds to less reported symptom severity; it does not by itself determine whether the size of the change is important to participants. A threshold for meaningful change is not reported in the registry record.

7. Results Posted in the Registry

• BDP HFA 80 mcg/Day: mean -1.90 versus -1.20 on control; difference -0.70 (95% CI -1.09 to -0.31), standardized effect d = -0.33; z-test p = <0.001.
• BDP HFA 160 mcg/Day: mean -2.00 versus -1.20 on control; difference -0.80 (95% CI -1.19 to -0.41), standardized effect d = -0.37; z-test p = <0.001.

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 the Average Morning (AM) and Evening (PM) Subject-Reported Instantaneous Total Nasal Symptom Score (iTNSS) During the Two Weeks of Treatment

• 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 HFA 80 mcg/Day: mean -1.60 versus -1.00 on control; difference -0.60 (95% CI -0.96 to -0.24), standardized effect d = -0.30; z-test p = 0.001.
  • BDP HFA 160 mcg/Day: mean -1.70 versus -1.00 on control; difference -0.70 (95% CI -1.06 to -0.34), standardized effect d = -0.35; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP HFA 80 mcg/Day 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 HFA 160 mcg/Day than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry record posts one secondary outcome: change from baseline in the average morning and evening instantaneous Total Nasal Symptom Score during the treatment period. The posted arm results and sponsor analyses show the same broad direction as the primary endpoint: both active-dose comparisons favor a larger decrease in the symptom score than the placebo comparison. The secondary results therefore provide a related view of symptom reporting, rather than a wholly separate type of outcome.

The distinction between the two symptom measures matters. The primary reflective score asks participants to report symptoms over the preceding 12 hours. The secondary instantaneous score captures symptoms at the time of recording. Similar direction across these measures can be viewed as a pattern of consistency, but the two measures are related because they assess the same four symptoms and are collected within the same trial. They should not be treated as independent replications.

The secondary analyses are less central to interpretation than the prespecified primary endpoint, and their p-values are unadjusted in the recalculated summaries. When several outcomes or treatment comparisons are examined, the chance of obtaining at least one apparently strong result can increase. Adjustment methods can address some forms of this multiplicity, but a multiplicity procedure is not reported in the registry record. This makes it important not to read secondary p-values in isolation or give them the same inferential weight as a clearly designated primary result.

The secondary findings can add context to the primary result, especially because the measurement asks about symptoms at a different time scale. They do not establish a separate clinical benefit, resolve the importance of the observed differences, or show that one dose is superior to the other. A direct comparison between doses is not reported in the registry record.

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

• Change From Baseline in the Average Morning (AM) and Evening (PM) Subject-Reported Instantaneous Total Nasal Symptom Score (iTNSS) During the Two Weeks of Treatment

9. Statistical Interpretation

10. Statistical Methods Explained

What does a change score represent?

A change score expresses how an outcome differs from its baseline value. Here, the outcome is a symptom score, and lower values represent less severe symptoms. A negative change therefore means that the average score was lower during the treatment period than at baseline. The reported least-squares means summarize changes after the model’s specified calculations; the registry record does not report all model details needed to reproduce those adjusted estimates independently.

Comparing each active group with placebo focuses on the difference between groups, rather than on whether either group changed on its own. Symptoms can change over time for reasons that affect participants in both groups, including the course of the condition and study participation. A placebo comparison helps interpret whether the average change in an active group differs from the change observed in the comparator group. It does not, on its own, explain why any difference occurred.

What does the repeated-measures model do?

The sponsor reported a mixed-model for repeated measures, commonly abbreviated MMRM. In general, this kind of model can analyze repeated outcome measurements while accounting for the fact that measurements from the same participant are related. A model can use information across the observed time points to estimate treatment contrasts, rather than treating each measurement as unrelated. The posted endpoint is an average across morning and evening assessments during the treatment period, and the registry reports the model as the method for the treatment differences.

The record does not report the model’s full specification. Details such as the covariance structure, fixed effects, degrees-of-freedom method, exact handling of missing repeated measurements, and any covariates are not reported in the registry record. Those details can affect model estimates and their standard errors, so the reported MMRM contrasts should be read as results of the sponsor’s analysis rather than as a model that can be fully reconstructed from the posted summary alone.

How do the recalculations differ?

The comparison table includes recalculated mean differences, confidence intervals, and unadjusted p-values derived from the posted arm-level means and standard errors. These are simple, unadjusted summaries of the active-versus-placebo contrasts. They do not reproduce the MMRM, which uses the repeated-measure structure and may incorporate other model features that are not shown in the record.

The recalculated pooled standard deviations are marked as approximate. They are inferred from the posted standard errors and group sizes, rather than taken from a directly posted standard deviation. That makes them useful for an approximate standardized description and for the planning illustrations, but they should not be mistaken for directly reported raw-score variability. The posted standard errors describe the uncertainty around the reported group means; they are not themselves measures of how much individual participants’ scores varied.

The recalculated p-values are unadjusted. They do not account for the presence of multiple treatment comparisons or outcomes. The sponsor’s own reported p-values are attached to the MMRM contrasts. The registry record does not report a multiplicity procedure, so the degree to which the sponsor’s inference accounted for multiple comparisons is not reported in the registry record.

Why does over-dispersion matter in general?

In general, over-dispersion means that observed variability is greater than a statistical model expects. When a model underestimates variability, standard errors can be too small and confidence intervals too narrow, which may make evidence appear more precise than it is. This trial’s primary outcome is a bounded symptom score summarized as a continuous measure; the posted results do not report an over-dispersion assessment, and there is no basis in the registry record to say that over-dispersion was identified or was a concern for the sponsor’s model.

More generally, methods should match the outcome’s structure and the data collected. Repeated measures need consideration of within-participant dependence; bounded scores may also have features that differ from an unbounded continuous variable. The registry record identifies the MMRM but does not describe diagnostic checks or alternative modeling analyses. These omissions limit what can be concluded about the model’s assumptions from the posted summary.

How should statistical evidence be read?

A p-value summarizes how compatible the observed data are with a specified null model, given the analysis assumptions. It is not the probability that the null hypothesis is true, nor does it measure how large or important a difference is. The reported p-values are below 0.001 for both sponsor MMRM comparisons. The confidence intervals provide a complementary view by showing a range of treatment differences compatible with the data and the model at the stated confidence level.

All such summaries depend on the analysis population, outcome definition, and modeling choices. The endpoint population was defined in the registry record, but full details of missing-data handling and model specification are not reported there. The tables on this page should therefore be read as a presentation of the posted results and transparent summary-based recalculations, not as a complete reanalysis of participant-level data.

11. Confidence Intervals and Precision

The sponsor-reported primary comparisons include 95% confidence intervals. For the 80 mcg/day group versus placebo, the estimated treatment difference is -0.71, with a 95% confidence interval from -1.1 to -0.3. For the 160 mcg/day group versus placebo, the estimate is -0.76, with a 95% confidence interval from -1.1 to -0.4. Both intervals lie below zero, matching the direction of the reported negative contrasts.

A confidence interval is a range of values compatible with the observed data and the analysis model at the stated confidence level. It communicates uncertainty around an estimate, rather than guaranteeing that the true treatment difference lies inside a particular interval. The width of an interval reflects the information available and the analysis’s uncertainty assumptions. Here, the interval endpoints are reported to one decimal place, so they show less numerical detail than the recalculated intervals in the comparison table.

The recalculated intervals are based on posted arm-level means and standard errors and are unadjusted. They are not identical to the sponsor’s MMRM intervals because they arise from a different calculation and do not use the repeated-measures model. The recalculated standard deviations used in related summaries are approximate, as noted in the table. The sponsor’s model-based estimates are the direct reported analyses; the summary-based intervals should be interpreted as approximate checks, not replacements.

Precision is not the same as clinical importance. A narrow interval can be statistically informative while still covering effects whose practical meaning is uncertain. A threshold for a clinically important score difference is not reported in the registry record. Nor does the interval establish whether the result applies outside the enrolled population or beyond the stated treatment period.

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 table and curve are planning illustrations based on the observed effect in the posted results, not the trial’s original design calculation. The figures are participants per arm, not total events. The planning assumptions are a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. Each row uses the stated fraction of the observed effect as the effect to detect. The original sample-size justification and design assumptions are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm under those assumptions for a design with an 80% chance of detecting the effect used in that row, if that effect and the other assumptions were correct. The 90% power column gives the corresponding number per arm for a 90% chance. These are planning targets for hypothetical two-arm comparisons, not counts observed in this study and not a reconstruction of the study’s actual analysis.

The rows that plan for 75% or 50% of the observed effect represent smaller target differences than the row using 100% of the observed effect. Smaller effects are harder to distinguish from random variation, so they require more participants per arm under the same assumptions. The table should be read as a sensitivity illustration: the required sample size depends on the effect size chosen for planning, as well as the stated statistical assumptions.

This is not observed power. Observed results should be interpreted using the estimates, confidence intervals, and analysis methods, rather than by calculating power after the study from its observed effect. The planning numbers are useful for showing how design requirements could change under different target effects; they do not measure the probability that the posted finding is true.

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 = -0.700; pooled standard deviation σ = 2.151.
2. n = 2 × (1.96 + 0.842)² × 2.151² / -0.700² = 148.2, rounded up to 149 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 <- -0.7                      # observed difference in means
sigma <- 2.15079836735601                     # 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(1307319)
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 = 149 (80% power), 199 (90% power)
 75% of observed effect: n per arm = 264 (80% power), 353 (90% power)
 50% of observed effect: n per arm = 593 (80% power), 794 (90% power)
power.t.test: 149.2 
Simulated power at n = 149 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry reports sponsor analyses using a mixed-model for repeated measures. For BDP HFA 80 mcg/day versus placebo, the sponsor reports a treatment difference of -0.71, a 95% confidence interval from -1.1 to -0.3, and p < 0.001. For BDP HFA 160 mcg/day versus placebo, the reported difference is -0.76, a 95% confidence interval from -1.1 to -0.4, and p < 0.001.

The recalculations in the comparison table use the posted arm-level means and standard errors to form simple unadjusted contrasts. They give estimates of -0.7 and -0.8, respectively, with their own intervals and unadjusted p-values. The broad pattern is consistent: both sets of comparisons are negative, and both suggest lower average scores in the active groups relative to placebo. The estimates are not expected to match exactly because the methods differ. The MMRM uses repeated-measures modeling, while the recalculation uses summary statistics and does not reproduce that model.

The recalculated pooled standard deviations are approximate, and the recalculated tests are unadjusted. They are best treated as transparent supplementary calculations, not as a substitute for the sponsor’s reported model analysis. The registry record does not include participant-level data or sufficient detail to reconstruct the full MMRM. It also does not report the sponsor’s multiplicity procedure. The posted sponsor results and the recalculation therefore answer related but not identical statistical questions.

15. Multiplicity, Missing Data and Analysis Populations

The registry record identifies one primary symptom endpoint and one posted secondary symptom endpoint, and it reports comparisons of each active dose with placebo. These multiple analyses create a multiplicity question: if many tests are conducted, the chance of at least one apparently positive result can increase. Statistical procedures such as adjustment or a prespecified testing sequence can control particular forms of this problem, but the multiplicity plan is not reported in the registry record.

The sponsor’s primary MMRM p-values are reported as below 0.001, and the secondary analyses also include reported comparisons. The registry record does not explain whether these tests were part of a hierarchical plan, whether alpha was allocated across comparisons, or whether any adjustment was applied. The recalculated p-values are explicitly unadjusted. In the absence of the analysis plan, the nominal p-values should not be interpreted as resolving the multiplicity issue.

The endpoint population is described as the intent-to-treat population, defined as randomized participants who received at least one dose of randomized medication and had at least one post-baseline assessment. The record says two enrolled participants were excluded and describes one as randomized in error who did not receive test medication. The reason for the other exclusion is not reported in the registry record. This operational definition is narrower than a simple count of everyone enrolled, so the endpoint group sizes should be read in the context of that stated eligibility definition.

Missing-data handling beyond the reported use of MMRM is not reported in the registry record. In general, repeated-measures models can use available measurements without requiring a complete set of observations for every participant, but their validity depends on assumptions about why data are missing and how the model is specified. The record does not describe missingness patterns, imputation, sensitivity analyses, or the assumptions used for incomplete measurements. It is therefore not possible to assess from the posted summary whether conclusions are robust to alternative missing-data assumptions.

The record also does not report the full statistical analysis plan, model diagnostics, or details of any interim analyses. These omissions do not negate the posted results, but they limit independent evaluation of multiplicity control, missing-data sensitivity, and the exact analysis population.

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.

The registry record lists zero participants with serious adverse events in each treatment group. The numbers at risk are 239 for BDP HFA 80 mcg/day, 241 for BDP HFA 160 mcg/day, and 234 for placebo. The posted counts for other adverse events are also zero in each of these groups. These are the figures shown in the safety summary and should be read as reported counts, not as proof that no adverse events of any kind occurred outside the categories or reporting captured there.

The deaths fields have no reported values. Death counts are therefore not reported in the registry record; a blank or absent value should not be restated as a reported zero. No serious adverse event terms are listed in the record.

Safety counts are descriptive. They do not by themselves establish that the groups have identical safety profiles, especially when an event is uncommon or when the record does not provide event definitions, follow-up detail, or a complete narrative of collection and adjudication. The available figures describe what is posted for the listed groups and categories; they do not support broader conclusions beyond that summary.

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

The posted primary results show average decreases in reflective nasal symptom scores in all study groups, with more negative average changes in both BDP HFA groups than in placebo. The sponsor’s MMRM comparisons also report negative treatment differences, with 95% confidence intervals below zero and p-values below 0.001. The results therefore show a statistical separation between each active-dose group and placebo on the reported primary endpoint under the sponsor’s analysis.

That statistical finding does not, by itself, say how noticeable or valuable the difference would be to children or caregivers. The registry record does not report a threshold for a clinically important difference, and the posted summaries do not provide individual response distributions. A group average can conceal variation among participants, and an average change cannot show what proportion experienced a particular degree of change unless that result is reported.

The two active-dose groups have similar directions of change relative to placebo in the posted analyses. The registry record does not report a direct comparison between the active doses, so these results do not establish that one dose is more effective than the other. Nor do the results establish durability beyond the 15-day treatment period, because longer-term outcome findings are not reported in the registry record.

The study concerns children ages 6–11 years with seasonal allergic rhinitis and the specific regimens described in the record. The findings should not be extended automatically to different ages, conditions, doses, administration schedules, or durations. The record also does not provide enough detail to evaluate every aspect of missing-data handling or multiplicity control. Those limitations shape the strength and scope of the statistical interpretation.

In short, the posted data describe lower average symptom scores relative to baseline and negative active-versus-placebo contrasts over the stated treatment period. They do not establish clinical importance, a preferred dose, effects beyond the measured period, or conclusions about unreported outcomes.

18. Why This Trial Matters Statistically

This trial provides a useful example of how the same clinical question can be summarized by different statistical methods. The registry reports a repeated-measures model for the treatment contrasts, while the comparison tables also show simple recalculations from arm-level means and standard errors. The methods produce estimates that are close in direction and broad magnitude, but they are not interchangeable. The distinction helps readers understand why a summary-based check can be informative without replacing the sponsor’s model.

The symptom endpoint is measured repeatedly and uses both morning and evening reports. That structure makes the modeling of within-participant observations relevant. In general, repeated measures from one participant are correlated, and treating them as independent can misstate uncertainty. The registry’s identification of MMRM makes the analysis approach visible, while the lack of a full model specification leaves limits on independent reproduction.

The trial also illustrates why statistical significance, precision, and clinical meaning are separate considerations. The sponsor’s confidence intervals and p-values address evidence and uncertainty under the reported model. The record does not provide a clinically important difference threshold, so statistical separation alone cannot determine practical importance.

Finally, the sample-size illustrations show how planning requirements depend on the target effect. They are based on the observed results and stated assumptions, not on the original trial design. Keeping that distinction clear avoids treating post-study planning scenarios as evidence about the trial’s original justification or as a measure of its observed power.

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 a clinical-importance threshold for the reflective symptom-score difference. As a result, the statistical estimates cannot be translated from the posted information into a judgment about whether the average difference was meaningful to participants. The summary results also do not show individual-level response patterns.

The primary analysis is reported as an MMRM, but the full model specification is not available in the registry record. The covariance structure, model covariates, degrees-of-freedom method, and detailed handling of incomplete repeated measurements are not reported. Missing-data patterns and sensitivity analyses are also not reported, limiting assessment of whether the estimates are robust to alternative assumptions.

The simple recalculations use posted arm summaries and are unadjusted. Their pooled standard deviations are approximate, and they do not account for the repeated-measures structure. They offer a transparent comparison but cannot reproduce participant-level analyses. The registry record also does not report the multiplicity procedure, so the inferential role of multiple endpoint and treatment comparisons remains unclear.

The endpoint population description notes two enrolled participants were excluded, but the reason for one exclusion is not reported in the registry record. The record reports endpoint group sizes, yet the available summaries do not describe all participant flow or reasons for missing assessments. Safety reporting is likewise limited to the posted counts; event definitions and broader details of ascertainment are not reported in the registry record.

Finally, the posted primary outcome covers the stated two-week treatment period. Longer follow-up, a direct active-dose comparison, and a threshold for interpreting clinical importance are not reported in the registry record. These limits constrain conclusions to the measured outcomes and analyses shown.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of an Investigational Nasal Aerosol or Placebo Nasal Aerosol in Children (Ages 6-11) With Seasonal Allergies — NCT01307319.
• Registry record last updated 2015-02-20; status last verified 2015-02.
• Results first posted 2015-02-20.
• 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

This completed phase 3 study randomized children ages 6–11 years with seasonal allergic rhinitis to BDP HFA 80 mcg/day, BDP HFA 160 mcg/day, or placebo nasal aerosol once daily for 15 days. The registry record reports enrollment of 715 and describes the study as parallel-group, quadruple-masked, and randomized.

The primary endpoint was change from baseline in morning and evening reflective Total Nasal Symptom Score. The sponsor reported MMRM treatment differences versus placebo of -0.71 and -0.76, with 95% confidence intervals below zero and p < 0.001 for each comparison. Simple unadjusted recalculations from the posted summaries show the same broad direction but do not reproduce the MMRM.

The secondary instantaneous symptom endpoint showed a similar overall direction. The record lists zero serious adverse events in each group; deaths are not reported in the registry record. Original design assumptions, multiplicity procedures, full model details, and several aspects of missing-data handling are not reported in the registry record.