Study in Adult and Adolescent Subjects With Seasonal Allergic Rhinitis (SAR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study in Adult and Adolescent Subjects With Seasonal Allergic Rhinitis (SAR) (NCT01024608), a randomized phase 3 study. The primary outcome is Change From Baseline in Average Subject-Reported AM and PM Reflective Total Nasal Symptom Score (rTNSS) Over the Two-week Treatment Period.

2. Clinical Question

The primary outcome summarizes participant ratings recorded in the morning and evening. The comparison is between the change from baseline in the active-treatment group and the change from baseline in the placebo group over the two-week treatment period. A negative change from baseline means symptoms improved relative to baseline; the treatment contrast describes how those changes differed between groups.

This is a statistical question about the size and uncertainty of a between-group difference in reported symptom-score change. It is not, by itself, a complete assessment of every benefit, harm, or outcome relevant to a treatment decision. The registry record also includes secondary symptom and quality-of-life outcomes, along with a limited serious-adverse-event summary.

3. Trial Design

The registry record describes a randomized, double-blind, placebo-controlled, parallel-group phase 3 trial of BDP HFA nasal aerosol for seasonal allergic rhinitis. It lists an enrollment of 340 and a completed study. The record gives a start date of 2009-12-31 and a primary completion date of 2010-02-28. The treatment period was two weeks.

Participants assigned to the BDP HFA 320 µg/day group self-administered four actuations, two per nostril, once each morning. Participants in the placebo group used four placebo actuations in the same way and on the same schedule. Double masking means the study was described as double-blind; details about who was masked and how masking was maintained are not reported in the registry record. Details of the randomization procedure and allocation concealment are also not reported in the registry record.

The primary endpoint was the change from baseline in average subject-reported morning and evening reflective total nasal symptom score over the two-week treatment period. The endpoint description identifies the intent-to-treat population. The registry record reports 167 participants in the BDP HFA group and 171 in the placebo group for this outcome. Reasons for the relationship between those analysis counts and the listed enrollment are not reported in the registry record.

The posted outcome analyses include three secondary measures: an instantaneous nasal symptom score, a quality-of-life measure in participants with impaired quality of life at baseline, and an ocular symptom score. The record does not describe the trial’s original sample-size justification or its full statistical analysis plan. Specific eligibility criteria beyond age and seasonal allergic rhinitis, site information, and the handling of protocol deviations are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Before assignment: During the 7 to 10 day Run-in Period, participants self-administered a single-blind placebo nasal aerosol once daily in the morning and assessed and recorded their seasonal rhinitis symptoms twice daily to determine eligibility for randomization.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to treat population

5. Baseline Characteristics

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

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Average Subject-Reported AM and PM Reflective Total Nasal Symptom Score (rTNSS) Over the Two-week Treatment Period, measured over Baseline (Days -3 to 0), and Days 1-15.

The primary endpoint is the change from baseline in average subject-reported morning and evening reflective total nasal symptom score over the two-week treatment period. Participants rated sneezing, runny nose, nasal itching, and nasal congestion based on symptoms over the prior 12 hours. Each symptom was scored from 0, absent, through 3, severe. The total score sums the four symptom ratings and ranges from 0 to 12, with higher scores representing worse symptoms.

The endpoint is a continuous measure of symptom severity. Averaging ratings across morning and evening assessments over the treatment period is intended to represent symptoms across repeated daily assessments rather than a single observation. Comparing change from baseline between randomized groups helps distinguish the average change during treatment from the change observed in the placebo group. In the registry’s definition, a negative change from baseline indicates improvement in the score.

Repeated participant reports can capture symptom experience that may not be represented by a single clinical observation. They also depend on participants completing and interpreting the ratings consistently. The registry record does not report the exact calculation used to aggregate daily ratings into the endpoint, the approach to missing diary entries, or a threshold for interpreting the importance of a score difference to participants. The endpoint therefore describes the measured score change; it does not alone establish how noticeable or important that change was in everyday life.

7. Results Posted in the Registry

• BDP HFA 320 µg/Day: mean -2.00 versus -1.00 on control; difference -1.00 (95% CI -1.43 to -0.57), standardized effect d = -0.50; 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 Average Subject-Reported AM and PM Instantaneous Total Nasal Symptom Score (iTNSS) Over the Two-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 HFA 320 µg/Day: mean -1.70 versus -0.80 on control; difference -0.90 (95% CI -1.32 to -0.48), standardized effect d = -0.46; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP HFA 320 µg/Day than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline at Week 2 in Rhinoconjunctivitis Quality of Life Questionnaire (RQLQ) in Participants With Impaired Quality of Life at Baseline

• 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 320 µg/Day: mean -1.20 versus -0.80 on control; difference -0.40 (95% CI -0.73 to -0.07), standardized effect d = -0.30; z-test p = 0.018.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP HFA 320 µg/Day than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in AM and PM Subject-reported Reflective Ocular Symptom Score Over the 2-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 HFA 320 µg/Day: mean -1.30 versus -0.70 on control; difference -0.60 (95% CI -0.95 to -0.25), standardized effect d = -0.37; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for BDP HFA 320 µg/Day than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The secondary outcomes show a broadly aligned pattern: the posted comparisons favor BDP HFA in the direction of greater reduction from baseline across nasal symptoms, ocular symptoms, and the quality-of-life measure. The registry’s reported analyses for these outcomes give estimates below zero and confidence intervals on the negative side of zero. This direction is consistent with the primary symptom-score comparison, while the outcomes assess distinct aspects of participants’ reported experience.

The secondary findings add context but do not independently confirm the primary result. The instantaneous nasal symptom score is related to, but distinct from, the reflective symptom measure. The ocular symptom score concerns a different symptom domain. The quality-of-life analysis is restricted to participants described as having impaired quality of life at baseline, so it pertains to that subgroup rather than all participants in the primary analysis. These differences in measurement and analysis population affect how directly the secondary results can be compared with the primary result.

Multiple outcomes create a multiplicity concern: when several hypotheses are tested, the chance of at least one apparently positive finding can increase if no adjustment is made. The registry record does not report a multiplicity adjustment or a hierarchy for interpreting secondary outcomes. The posted secondary p-values should therefore be viewed as outcome-specific results, not as a single confirmatory family of tests. They provide supportive descriptive context, but carry less weight than the primary analysis unless a prespecified testing strategy is documented. That strategy is not reported in the registry record.

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

• Change From Baseline in Average Subject-Reported AM and PM Instantaneous Total Nasal Symptom Score (iTNSS) Over the Two-week Treatment Period
• Change From Baseline at Week 2 in Rhinoconjunctivitis Quality of Life Questionnaire (RQLQ) in Participants With Impaired Quality of Life at Baseline
• Change From Baseline in AM and PM Subject-reported Reflective Ocular Symptom Score Over the 2-week Treatment Period

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports an ANCOVA analysis for the primary comparison. ANCOVA, or analysis of covariance, is a model-based approach for comparing group means while accounting for one or more covariates. In a trial with a baseline and follow-up measure, an ANCOVA model may include baseline score as a covariate, but the registry record does not identify the covariates used in this analysis. It also does not report the model specification, assumptions checks, or how any missing outcome observations were handled. Those details matter for reproducing or fully evaluating an adjusted estimate.

The reported primary treatment effect is a least-squares mean difference from placebo. A least-squares mean is a model-based group estimate, rather than necessarily the raw arithmetic mean of all observed scores. The reported treatment difference of -0.91 units is the registry’s ANCOVA estimate. Its 95% confidence interval runs from -1.3 to -0.5, and its reported p-value is <0.001. The interval and test are tied to the sponsor-reported model; the registry record does not include enough model detail to independently reconstruct them.

The posted arm values are also least-squares means, with standard errors. A standard error describes the estimated sampling variability of a statistic, such as a mean, under the analysis used. It is not the same quantity as the spread of individual participants’ scores. Smaller standard errors generally indicate more precise estimates, though precision also depends on the model and the data being analyzed. The registry record does not report standard deviations for the primary outcome arms.

The accompanying re-calculation is a simple, unadjusted comparison based on the posted arm summaries. Its pooled standard deviation is approximate because it is derived from the reported standard errors rather than from participant-level observations. Consequently, its mean difference and interval should be understood as a transparent summary-statistic calculation, not as a reproduction of the ANCOVA. It does not use any unreported covariates or participant-level information. The sponsor’s reported analysis is the appropriate reference for the trial’s own posted inferential result.

A confidence interval expresses a range of values compatible with the data and the statistical procedure, under the model’s assumptions. It gives information about both direction and precision. An interval that does not include zero is consistent with a nonzero difference under that procedure, but the interval does not establish the importance of the difference or eliminate uncertainty about model assumptions. A p-value addresses a related but distinct question: how inconsistent the observed data are with a specified null hypothesis, under the statistical model. Neither measure gives the probability that the treatment effect is true.

Over-dispersion is a general statistical concern when observed variability exceeds what a model’s assumed distribution allows. When it is present and not accounted for, standard errors can be too small and confidence intervals too narrow. The registry record does not report an over-dispersion assessment, and the outcome is described as continuous; no claim about over-dispersion in this trial can be made from the posted information. More generally, model diagnostics and sensitivity analyses can help assess whether a model represents the data adequately, but those details are not reported in the registry record.

Randomization supports a comparison between groups by assigning participants to treatment independently of their expected outcome, in expectation. It does not guarantee that every measured characteristic is identical across groups, and the registry record does not provide the randomization sequence or baseline characteristics needed to review balance. Blinding can reduce the influence of treatment knowledge on participant reports or study conduct, but the posted record does not describe masking success or whether participants could infer their assignment.

The endpoint consists of repeated subjective ratings combined into a total score. Repeated measures can provide a broader account of symptoms over the treatment period, but they also create practical questions about missed entries and the choice of aggregation. The registry record identifies the baseline and treatment assessment windows but does not report the detailed derivation of each participant’s average, rules for incomplete records, or a missing-data sensitivity analysis. These omissions limit assessment of how robust the endpoint estimate is to incomplete reporting.

The intent-to-treat population is named for the primary endpoint. In general, an intent-to-treat approach aims to analyze participants according to their randomized group, preserving the randomized comparison. The registry record does not define its operational intent-to-treat population, state whether all randomized participants were included, or describe how missing outcomes were addressed. Those distinctions should not be inferred from the label alone.

The posted p-values and confidence intervals concern the listed comparisons. The record does not report whether the primary analysis was prespecified in a protocol, whether there were interim analyses, or what multiplicity procedure, if any, was planned. These are aspects of the statistical plan, not details that can be inferred from the reported results.

11. Confidence Intervals and Precision

The sponsor-reported primary estimate is a treatment difference of -0.91 units, with a 95% confidence interval from -1.3 to -0.5. The interval lies on the negative side of zero and is not especially wide relative to the direction of the estimated effect. It communicates a range of values compatible with the ANCOVA analysis, under its assumptions. The interval does not mean there is a 95% probability that the true difference falls within these particular limits.

The simple unadjusted re-calculation has a mean difference of -1.0 units and an approximate 95% confidence interval from -1.43 to -0.570. Its endpoints are not identical to the sponsor-reported interval because the recalculation uses posted summary statistics and an approximate standard deviation, whereas the registry reports an ANCOVA estimate. The two intervals are therefore not interchangeable. The registry record does not give the covariates or full model specification needed to explain the numerical difference in more detail.

Precision concerns the uncertainty around a group-level estimate, not the certainty of an individual participant’s response. The reported standard errors describe uncertainty in the arm estimates, while the confidence interval describes uncertainty in the treatment contrast. A confidence interval can be narrow enough to identify a likely direction while still covering effects of differing magnitudes. The clinical importance of any value in the interval cannot be determined from statistical precision alone; the registry record does not report a meaningful-change threshold for the symptom scale.

The interval also depends on the analysis assumptions, outcome completeness, and model specification. The registry record does not report detailed missing-data methods, covariates, or sensitivity analyses. Therefore, the posted confidence interval quantifies uncertainty within the reported analysis, but does not capture every source of uncertainty about measurement, generalizability, or analytic choices.

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 table and curve translate an observed comparison into hypothetical sample-size requirements under stated assumptions. For these continuous outcomes, the figures are participants per arm, not total participants across both groups and 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 planning scenario uses the stated fraction of the observed effect as the effect to detect. The registry record’s original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the illustrative number of participants per arm that the calculation associates with an 80% chance of detecting the specified effect under the assumptions, if that effect and the model assumptions hold. The 90% power column uses a higher target probability of detection, which generally requires more participants for the same assumed effect. These are planning illustrations, not observed power. Observed power is not a useful substitute for interpreting the estimate and its confidence interval after a study has been completed.

The scenarios that plan for 100%, 75%, or 50% of the observed effect show how the required sample size changes as the effect assumed for planning becomes smaller. Smaller effects are harder to distinguish from random variation, so they require more participants for the same target power under the same general assumptions. The displayed figures are not proof that the trial was designed around the observed result; they are calculations based on the posted effect after the fact.

These illustrations also do not incorporate unreported elements of the original protocol, such as any allowance for missing outcomes or other design considerations. They should be read as conditional planning scenarios rather than as a reconstruction of the trial’s own design rationale.

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 = -1.000; pooled standard deviation σ = 2.015.
2. n = 2 × (1.96 + 0.842)² × 2.015² / -1.000² = 63.7, rounded up to 64 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 <- -1                      # observed difference in means
sigma <- 2.01464740504801                     # 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(1024608)
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 = 64 (80% power), 86 (90% power)
 75% of observed effect: n per arm = 114 (80% power), 152 (90% power)
 50% of observed effect: n per arm = 255 (80% power), 342 (90% power)
power.t.test: 64.7 
Simulated power at n = 64 per arm: 0.800 (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’s own primary analysis is an ANCOVA estimate of the least-squares mean treatment difference from placebo: -0.91 units, with a 95% confidence interval from -1.3 to -0.5 and p < 0.001. That is the sponsor-reported inferential result and should remain distinct from the simple unadjusted re-calculation.

The re-calculation based on posted arm summaries estimates a difference of -1.0 units and gives an approximate 95% confidence interval from -1.43 to -0.570, with an unadjusted p-value of <0.001. It uses an approximate pooled standard deviation inferred from standard errors and does not reproduce the ANCOVA model. The registry record does not report the covariates or model details required to reproduce the adjusted estimate.

Both analyses point to a negative difference, but they answer the comparison using different methods. The sponsor analysis is the trial’s reported analysis; the re-calculation is a secondary descriptive check based on available summary values. It is not evidence of an inconsistency that changes the registry conclusion, and it should not be presented as a replacement for the sponsor’s model-based result.

15. Multiplicity, Missing Data and Analysis Populations

Multiplicity arises when investigators assess more than one outcome or conduct multiple statistical tests. Even if each test is evaluated using its own conventional threshold, testing a collection of hypotheses can increase the chance that at least one result appears statistically significant by chance. A prespecified hierarchy or adjustment procedure can address that issue, but the registry record does not report whether either was planned or used. The primary outcome is clearly identified in the record; the status of the secondary analyses as confirmatory or exploratory is not reported in the registry record.

Missing outcome data can also affect interpretation. The registry names the intent-to-treat population for the primary endpoint and posts arm-specific analysis counts, but does not report the number of missing symptom records, reasons for missingness, or how incomplete diaries were handled. The operational definition of the intent-to-treat population is not reported in the registry record. It is also not reported whether the analysis used imputation, a repeated-measures model, or another method for handling missing values. These details matter because conclusions can depend on whether missingness is related to participants’ symptoms or treatment assignment.

The registry record does not report the full statistical analysis plan, the covariates used in the ANCOVA, or sensitivity analyses exploring alternative assumptions. It also does not report interim analyses or a protocol-based sample-size justification. These omissions limit a review of prespecification and robustness; they do not establish that such procedures were absent, only that they are not reported in the registry record.

The primary outcome is identified as an intent-to-treat analysis, which generally aims to preserve the randomized comparison by analyzing participants in their assigned groups. However, without the population definition and missing-data methods, that label alone is insufficient to determine precisely how all randomized participants contributed to the estimate. The reported result remains interpretable as the registry’s stated analysis, with these reporting limitations kept in view.

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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: hypertensive crisis (0.6%).

The serious-adverse-event summary lists one affected participant among 167 in the BDP HFA 320 µg/day group and none among 171 in the placebo group. The registry lists hypertensive crisis at 0.6% as a top serious-event term. These figures are descriptive counts from the posted record; they do not establish that treatment caused or prevented an event. The registry record does not provide enough detail in this summary to assess event timing, relatedness, clinical course, or comparative risk precisely.

The record also lists other adverse events affecting 11 participants in the BDP HFA group and 10 in the placebo group. Those counts are separate from the serious-event figures. Death counts are not reported in the registry record. The treatment period was two weeks, so this safety summary should be read in the context of the reported study period and the information actually recorded. A small number of events, especially when the counts are low, provides limited precision for comparing uncommon harms.

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

The primary result describes a difference in average change in a participant-reported nasal symptom score during a two-week treatment period. The sponsor’s ANCOVA analysis estimates a negative treatment difference, and the reported 95% confidence interval is entirely below zero. The posted data therefore indicate that the average score change in the BDP HFA group was more negative than in the placebo group under the registry’s reported analysis.

That statistical comparison does not establish how much an individual participant’s symptoms changed, whether every participant experienced a similar response, or whether the score difference was noticeable or important to participants. The registry record does not report a threshold for meaningful change on this scale. A group average can also conceal variation among participants, which cannot be evaluated fully from the posted summary values.

The result is limited to the measures and timeframe recorded. It does not establish what might happen beyond the two-week treatment period, and the registry record does not report longer-term outcomes. The primary endpoint is based on subjective symptom ratings; this makes participants’ recorded experience central to the outcome, while also making consistent reporting and completeness relevant. The record does not describe missing diary data or sensitivity analyses.

The findings should not be extended automatically to people outside the trial’s stated population or to outcomes that were not measured. The registry identifies participants 12 years of age and older with seasonal allergic rhinitis, but further details about eligibility and the study population are not reported in the registry record. The secondary findings and limited adverse-event summary offer additional information, but neither removes the uncertainty around outcome importance, longer-term results, or less common harms.

In short, the posted statistics quantify a between-group difference in the specified symptom score and its statistical uncertainty. They do not, on their own, settle broader questions about clinical importance, individual experience, durability, or overall benefit and harm.

18. Why This Trial Matters Statistically

This trial illustrates the distinction between a within-group change and a randomized between-group comparison. Both arms had negative average changes from baseline, so looking only at change in the active-treatment arm would not isolate the treatment contrast. The difference between randomized groups is the relevant estimate for the comparative question.

It also shows why adjusted and unadjusted results should not be treated as identical. The registry reports an ANCOVA estimate, while a re-calculation from arm summaries provides an approximate, unadjusted comparison. The two methods produce results in the same direction, but the re-calculation cannot recover the model-based analysis without details that are not reported. Statistical readers should identify which estimate comes from the registry’s analysis and which is a supplementary calculation.

The interval adds information beyond a significance test. It conveys a range of values compatible with the model and shows uncertainty around the estimated contrast. At the same time, statistical precision does not answer whether a score difference matters to participants. That interpretation requires a meaningful-change threshold or other contextual evidence, which is not reported in the registry record.

Finally, the trial provides a useful example of how multiplicity, missing data, and reporting detail affect confidence in secondary and model-based results. The registry posts several outcomes, but does not report a multiplicity strategy, detailed missing-data methods, or the full ANCOVA specification. Recognizing these boundaries allows the posted estimates to be interpreted without treating unreported analytic details as known.

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 ANCOVA covariates, full model specification, or diagnostic checks, limiting independent reproduction of the sponsor’s primary estimate. The re-calculation is consequently an approximate unadjusted check based on summary values, not a substitute for participant-level analysis. Details of the randomization sequence, allocation concealment, and masking procedures are also not reported in the registry record.

The primary outcome depends on repeated participant ratings, but the record does not report the handling of missing diary entries, the aggregation rules for incomplete ratings, or sensitivity analyses. Although the endpoint is identified as intent-to-treat, the operational population definition is not reported. These gaps limit evaluation of how incomplete outcome data may affect the estimate.

The record posts several outcomes but does not report a multiplicity adjustment or a testing hierarchy. The secondary results therefore warrant caution, particularly when interpreted as confirmatory evidence. The quality-of-life outcome applies to participants with impaired quality of life at baseline, and the record does not describe how broadly those findings may generalize beyond that subgroup.

The study’s primary endpoint covers a two-week treatment period. Longer-term outcomes are not reported in the registry record, and no meaningful-change threshold is given for the symptom scale. The safety summary includes low event counts and does not provide detailed event descriptions, relatedness assessments, or death counts. These limitations constrain interpretation of clinical importance, durability, and uncommon harms.

Other details that could inform generalizability, including fuller eligibility criteria, baseline characteristics, and site information, are not reported in the registry record. The record also does not report the trial’s original sample-size justification or interim-analysis procedures. These are limitations of the available registry reporting, not evidence that such information was absent from the study’s full documentation.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study in Adult and Adolescent Subjects With Seasonal Allergic Rhinitis (SAR) — NCT01024608.
• Registry record last updated 2021-12-03; status last verified 2021-12.
• Results first posted 2012-05-23.
• 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 record describes a completed randomized, double-blind, placebo-controlled, parallel-group phase 3 study of BDP HFA nasal aerosol in participants 12 years of age and older with seasonal allergic rhinitis. The primary endpoint was change from baseline in average morning and evening reflective total nasal symptom score over the two-week treatment period.

The sponsor-reported ANCOVA estimate was a least-squares mean treatment difference from placebo of -0.91 units, with a 95% confidence interval from -1.3 to -0.5 and p < 0.001. The posted secondary outcomes generally point in the same direction, while multiplicity and missing-data methods are not reported in the registry record. The serious-adverse-event summary lists one affected participant in the BDP HFA group and none in the placebo group; further safety interpretation is limited by the detail available.