Bepotastine Besilate Nasal Sprays in the Treatment of Seasonal Allergic Rhinitis (SAR): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Bepotastine Besilate Nasal Sprays in the Treatment of Seasonal Allergic Rhinitis (SAR) (NCT01753739), a randomized phase 2 study. The primary outcome is Mean Change From Baseline (Pre-Dose) Twice Daily Averaged Subject-rated Reflective Total Nasal Symptom Score (TNSS).

2. Clinical Question

The outcome is a symptom score: lower scores correspond to fewer nasal allergy symptoms, and a negative change from baseline indicates a decrease in the score. The comparisons are therefore read as differences in change, with negative estimates indicating a greater decrease in the bepotastine group than in the placebo group. That direction describes the score contrast; it does not by itself establish a reliable difference or a clinical benefit.

The registry record describes a dose-ranging study. Its posted primary results allow each active concentration to be considered against the same placebo group, but they do not establish a ranking among the concentrations. Nor do the results establish what would happen beyond the 14-day assessment or in people who do not match the study description. The posted comparisons are unadjusted recalculations from the group summaries, rather than reported sponsor analyses.

3. Trial Design

The registry record identifies this as a Phase 2, randomized, double-masked, parallel-group study of bepotastine besilate nasal spray for seasonal allergic rhinitis. The recorded enrollment is 617. The brief study description refers to 600 male or female subjects aged 12 years and older, with active seasonal allergic rhinitis and a demonstrated history of Mountain Cedar pollen sensitivity for at least 2 years. The registry record does not explain the relationship between the enrollment figure and the number in the brief description.

Participants were assigned to placebo or one of four bepotastine besilate concentrations: 0.5%, 1%, 2%, or 4%. Each arm description states that the nasal spray was taken twice daily for 14 days. The parallel-group design means each assigned group received its designated spray over the study period; the registry record does not describe a crossover between treatments. Randomization is intended, in general, to support comparable groups at the start of a trial, while masking is intended to limit the influence of treatment knowledge on participants or study conduct. The registry record does not give further details about the randomization procedure or who was masked.

The primary outcome was assessed at 14 days and was based on subject-rated reflective nasal symptoms averaged across morning and evening. The analysis population included randomized participants who had received at least one dose of study drug. The record states that missing Day 14 data were not imputed. Recorded study dates are 2013-01 for start and 2013-02 for primary completion, and the status is completed.

The registry record does not report the original sample-size justification, allocation ratio, detailed conduct of masking, or a full statistical analysis plan. These missing details limit how fully the design and the intended analysis can be reconstructed from the 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.

Overall Study

Analysis population for the primary outcome, as defined in the registry: The analysis population included randomized participants who had received at least 1 dose of study drug. There was no imputation of missing data at Day 14.

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 Mean Change From Baseline (Pre-Dose) Twice Daily Averaged Subject-rated Reflective Total Nasal Symptom Score (TNSS), measured over 14 Days.

The primary endpoint is mean change from baseline in the twice-daily averaged, subject-rated reflective total nasal symptom score (TNSS) over 14 days. TNSS combines ratings for nasal itching, runny nose, nasal congestion, and sneezing. Each symptom is rated on a four-point scale from 0 to 3, with no half-unit ratings. The four symptom ratings are summed to give a score from 0 to 12; higher scores correspond to increased nasal allergy symptoms.

Morning and evening scores were averaged. A change score compares the assessment with the participant’s baseline, so negative group means indicate that the score decreased from baseline on average. The endpoint is useful for summarizing several nasal symptoms in one continuous measure and for comparing mean changes between randomized groups. It also has limits: a mean can conceal differences among individual symptoms and participants, and the registry record does not report a threshold for interpreting a change as important to participants.

The posted endpoint summaries give the group mean change and standard deviation. They do not report individual participant data, an adjusted model, or imputation for missing Day 14 values. Thus, the numerical comparisons describe the posted group summaries and should not be read as a complete account of every feature of the analysis.

7. Results Posted in the Registry

• Bepotastine Besilate 0.5%: mean -1.58 versus -1.19 on control; difference -0.39 (95% CI -0.96 to 0.18), standardized effect d = -0.17; z-test p = 0.177.
• Bepotastine Besilate 1%: mean -1.68 versus -1.19 on control; difference -0.49 (95% CI -1.05 to 0.07), standardized effect d = -0.22; z-test p = 0.086.
• Bepotastine Besilate 2%: mean -1.63 versus -1.19 on control; difference -0.44 (95% CI -1.00 to 0.12), standardized effect d = -0.20; z-test p = 0.121.
• Bepotastine Besilate 4%: mean -1.55 versus -1.19 on control; difference -0.36 (95% CI -0.92 to 0.20), standardized effect d = -0.16; z-test p = 0.205.

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.

Mean Change From Baseline (Pre-Dose) in Morning Averaged Subject-rated Reflective (TNSS)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Bepotastine Besilate 0.5%: mean -1.68 versus -1.29 on control; difference -0.39 (95% CI -0.97 to 0.19), standardized effect d = -0.17; z-test p = 0.189.
  • Bepotastine Besilate 1%: mean -1.72 versus -1.29 on control; difference -0.43 (95% CI -0.99 to 0.13), standardized effect d = -0.19; z-test p = 0.136.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bepotastine Besilate 0.5% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bepotastine Besilate 1% and the control. The interval gives the range of effects that remain compatible with the data.

Mean Change From Baseline (Pre-Dose) in Evening Averaged Subject-rated Reflective Total Nasal Symptom Score (TNSS)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Bepotastine Besilate 0.5%: mean -1.55 versus -1.14 on control; difference -0.41 (95% CI -0.99 to 0.17), standardized effect d = -0.18; z-test p = 0.163.
  • Bepotastine Besilate 1%: mean -1.70 versus -1.14 on control; difference -0.56 (95% CI -1.13 to 0.01), standardized effect d = -0.25; z-test p = 0.056.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bepotastine Besilate 0.5% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Bepotastine Besilate 1% and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes examine morning-averaged and evening-averaged TNSS change over 14 days. Across the group summaries, mean changes are negative for placebo and each bepotastine concentration, so the broad within-group pattern is a decrease from baseline. The unadjusted active-versus-placebo estimates generally point toward larger decreases in the active groups, as in the primary endpoint. This resemblance is useful context, but it does not create independent confirmation: the outcomes measure related symptoms in the same trial population and are assessed over the same period.

The secondary endpoint summaries do not overturn the primary reading. The registry record lists recalculated comparisons for only some of the active concentrations for each secondary outcome, and it lists no reported analyses for these outcomes. The record does not explain whether those particular comparisons were prespecified, whether additional comparisons were conducted, or why other concentrations do not have posted comparison results. The absence of a listed comparison should not be interpreted as evidence about its result.

Unadjusted secondary results carry less weight because many outcomes and comparisons can create more opportunities for chance findings. A multiplicity adjustment or prespecified hierarchy can help manage that issue, but the registry record does not report one. In addition, secondary outcomes are generally less central than the primary endpoint for the trial’s main question. A pattern across related measures can support descriptive consistency, but it does not replace a clear primary analysis or establish an effect.

The secondary findings should therefore be considered exploratory in the statistical sense: they add context about symptom-score patterns, while the record leaves the planned analysis and multiplicity handling unclear. Their relationship to the primary result is one of broadly similar direction in the group summaries, not a separate demonstration that resolves the uncertainty in the primary comparisons.

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

• Mean Change From Baseline (Pre-Dose) in Morning Averaged Subject-rated Reflective (TNSS)
• Mean Change From Baseline (Pre-Dose) in Evening Averaged Subject-rated Reflective Total Nasal Symptom Score (TNSS)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical symptom score, and the registry reports the mean change and standard deviation for each group. A mean is the arithmetic average of observed values. The standard deviation describes how dispersed those values are around the mean. It is not the uncertainty of the mean itself; uncertainty also depends on the amount of information in the group and the analysis method.

The reported group means are changes from baseline, not end-of-study scores. Negative values indicate decreases in TNSS. The comparison of interest is the difference between a bepotastine group’s mean change and the placebo group’s mean change. The posted comparisons are labeled as mean differences and are simple unadjusted recalculations from the group summaries. They are not presented as sponsor-reported model estimates. The registry record lists no reported analyses for the primary outcome.

In general, a confidence interval gives a range of values reasonably compatible with the data and the method used to calculate it. A narrow interval conveys greater precision than a wide one, though precision does not resolve bias or other design limitations. If an interval includes zero for a difference in means, the data do not clearly distinguish that estimated contrast from no difference under the calculation used. Inclusion of zero does not establish that the groups are identical; the interval also allows for nonzero differences within its range. The confidence level and the method used for the posted intervals are not reported in the registry record, so they should not be inferred.

A p-value, in general, measures how unusual data at least as incompatible with a specified null hypothesis would be if that null hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor a measure of the size or importance of an effect. The posted p-values are unadjusted recalculations. Without a reported multiplicity plan, they should not be treated as if only one comparison had been considered.

Randomization, in general, aims to make treatment groups comparable in expectation, including with respect to factors that are measured or not measured. A parallel design assigns participants to a group that remains their assigned group during the study. Double masking is intended to reduce the influence of knowledge of treatment assignment. These design features support fair comparisons, but they do not guarantee that every source of bias is absent. The registry record does not report the randomization sequence method, masking procedures, or details of allocation concealment.

The stated analysis population consists of randomized participants who received at least one dose. The record explicitly states that no missing Day 14 data were imputed. In general, not imputing missing outcomes means the calculation uses available observed values rather than filling in unobserved values through a statistical model. This approach does not remove the possibility that missingness affects the comparison; interpretation depends in part on how much outcome data were missing and why. The amount and pattern of missing primary outcome data are not reported in the registry record.

Over-dispersion is a general concern when a statistical model assumes less variability than the data contain. For a continuous outcome analyzed with group means, the reported standard deviations give a direct indication of observed spread, but the registry record does not identify a model or report checks of model assumptions. The posted calculations use the standard deviations and group sizes as summary inputs. They do not adjust for baseline covariates, repeated observations, or other factors not included in those summaries.

Multiple comparisons arise when several hypotheses are considered in the same analysis. Testing several concentrations against a shared placebo can make it more likely that at least one result appears unusually favorable by chance if each comparison is interpreted independently. A multiplicity procedure can control that issue, but the registry record does not report whether one was planned or used. The listed p-values and intervals should therefore be read as unadjusted, and no concentration should be selected on their basis alone.

The registry describes a dose-ranging purpose, but the posted primary comparisons are each against placebo; they do not constitute a formal trend test or direct pairwise comparisons among concentrations. A pattern in the group means can be described, but it is not enough to establish a dose-response relationship. The original statistical plan, including any planned dose-response analysis, sample-size justification, or interim analysis, is not reported in the registry record.

General statistical interpretation also separates estimation from decision-making. Estimates describe the direction and magnitude of a contrast, while intervals communicate uncertainty and a prespecified analysis plan determines how formal evidence is assessed. Here, the registry record provides group summaries and the posted comparisons are recalculated without adjustment. These are useful for understanding the scale and precision of the observed contrasts, while leaving the sponsor’s original inferential approach and its assumptions unavailable.

11. Confidence Intervals and Precision

The primary mean differences are small relative to the spread of individual changes, and their confidence intervals are broad enough to extend across zero. For 0.5%, the estimated difference is -0.39 with a confidence interval from -0.956 to 0.176. For 1%, the estimate is -0.49 with an interval from -1.05 to 0.070. For 2%, the estimate is -0.44 with an interval from -0.996 to 0.116, and for 4%, it is -0.36 with an interval from -0.917 to 0.197.

In general, an interval’s width reflects how precisely the data estimate a contrast under the calculation method. These intervals allow a range of plausible mean differences, including zero and values on both sides of zero. The point estimates all lie on the negative side, but the intervals show uncertainty about whether the underlying contrast is negative, absent, or positive. Their overlap also cautions against treating the point estimates as a dependable ranking of concentrations.

The group standard deviations for the primary outcome range from 2.21 to 2.28, while the groups contributing to the outcome summaries have sample sizes from 121.0 to 123.0. These figures give context for why mean estimates can remain uncertain even when group sizes are similar. The registry record does not state the confidence level or interval calculation method, so no unstated convention should be attached to the intervals.

These intervals are unadjusted recalculations from the posted summary statistics. They do not account for multiple comparisons or any covariate adjustment. Their precision should therefore be understood as conditional on the simple comparison represented by the calculation, rather than as a complete account of uncertainty from all aspects of trial conduct and analysis.

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, not total events. They are illustrations based on the observed effect, rather than the trial’s original design assumptions. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The target effect is set to the stated fraction of the observed effect. The registry record does not report the original sample-size justification or assumptions used when planning the trial.

The 80% power column indicates the number of participants per arm estimated to give an 80% chance of detecting the target difference under those planning assumptions, if that difference is the true effect and the assumptions hold. The 90% power column gives the corresponding planning number for a 90% chance. These are design illustrations, not probabilities that the observed result is correct. They are not observed power.

Rows that plan for a smaller fraction of the observed effect require more participants per arm. In general, smaller target differences are harder to distinguish from random variation, so larger studies are needed to achieve the same planned power. The figures are specific to each comparison and its observed effect and variability; they should not be treated as a single recommended sample size for a future study.

Power calculations depend on assumptions about the outcome, allocation, significance level, and analysis. The illustrations use equal allocation for a two-arm comparison and do not describe a plan for jointly testing all concentrations against placebo or for controlling multiplicity. They also do not account for unreported design features such as missing outcomes or an adjusted analysis. Their role is to show how planning numbers change when the target effect changes, not to reconstruct the study’s original planning.

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 = -0.390; pooled standard deviation σ = 2.250.
2. n = 2 × (1.96 + 0.842)² × 2.250² / -0.390² = 522.5, rounded up to 523 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 <- -0.39                      # observed difference in means
sigma <- 2.25007551740489                     # 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(1753739)
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 = 523 (80% power), 700 (90% power)
 75% of observed effect: n per arm = 929 (80% power), 1,244 (90% power)
 50% of observed effect: n per arm = 2,091 (80% power), 2,799 (90% power)
power.t.test: 523.5 
Simulated power at n = 523 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. Multiplicity, Missing Data and Analysis Populations

Multiplicity matters because the trial compares four bepotastine concentrations with placebo and also records secondary morning and evening symptom outcomes. In general, considering multiple comparisons increases the chance of at least one apparently unusual result if each is assessed as though it were the only test. Statistical plans may address this through a prespecified hierarchy or adjustment, but the registry record does not report whether such a method was planned or used. The posted comparisons are unadjusted recalculations, so their p-values and intervals do not reflect a multiplicity correction.

The record lists no reported analyses for the primary or secondary outcomes. It therefore does not identify a sponsor-reported model, analysis method, or inferential procedure for these results. The original sample-size justification, interim analyses, and statistical analysis plan are not reported in the registry record. The stated planning illustration is separate from the trial’s original design and cannot fill those gaps.

For the primary outcome, the specified analysis population included randomized participants who received at least one dose of study drug. The registry record states that there was no imputation of missing data at Day 14. It does not report how many outcome values were missing, the reasons for missingness, or whether missingness differed among groups. Without those details, the possible effect of missing outcomes on the comparison cannot be assessed from the registry record.

The outcome summaries include group-specific analysis counts, while the safety record gives separate counts at risk. These are reported for different purposes, and the registry record does not explain the relationship between the analysis populations. The listed primary outcome counts range from 121.0 to 123.0; serious-event safety counts at risk range from 123 to 124. Those counts should not be silently treated as interchangeable denominators.

These omissions do not invalidate the descriptive summaries, but they limit evaluation of how the sponsor intended to handle the full family of outcomes and comparisons, missing data, and analysis populations. The unadjusted recalculations should be interpreted with those gaps in view.

15. Safety Results

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

Deaths

Other (non-serious) adverse events

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

Most frequent non-serious adverse event terms

The registry record reports zero serious adverse events in each of the five safety groups. The counts at risk are 124 for placebo, 123 for bepotastine besilate 0.5%, 123 for 1%, 124 for 2%, and 123 for 4%. The record also lists zero deaths in each group. No serious adverse event terms are listed.

These are counts, not estimates of comparative risk. Zero reported serious events in a group does not establish that the risk is absent, especially when the study’s follow-up was 14 days and the groups were limited in size. The registry record does not provide detail about event definitions, collection procedures, or uncertainty intervals for these counts.

The record lists other adverse events separately: one for placebo and 8, 12, 15, and 18 across the four concentrations in ascending order. Those figures are not serious-event counts and should not be conflated with the serious adverse event summary. The reported safety figures describe events recorded in this trial; they do not establish comparative safety beyond its population, treatment period, and recorded outcomes.

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

The primary results describe mean changes in a nasal symptom score over 14 days. All groups had negative mean change from baseline, and the unadjusted estimated differences versus placebo were also negative. Those details describe the direction of the posted averages; they do not show that every participant improved or that the active groups differed reliably from placebo.

All primary confidence intervals include zero, and the registry record does not report a sponsor inferential analysis or multiplicity plan. The recalculated comparisons therefore leave uncertainty about the size and direction of the underlying differences. A p-value should not be read as the probability that a treatment effect exists, and a point estimate should not be read as a guaranteed effect for an individual.

The outcome is a four-symptom sum score. It can summarize overall nasal symptoms, but it does not show which symptom contributes most to the change, how changes vary among participants, or whether a difference is important to participants. The record does not report a threshold for a clinically meaningful score change. Without that information, statistical contrasts alone cannot establish the importance of a difference.

The study concerns people described as having active seasonal allergic rhinitis and established Mountain Cedar pollen sensitivity, and the intervention period is 14 days. Its findings cannot automatically be extended to other populations, allergy triggers, treatment durations, or outcomes not reported in the registry record. Nor do the posted summaries establish a dose-response relationship, since they do not report a formal trend analysis or direct statistical comparisons among concentrations.

Accordingly, the posted data support a cautious account of observed group averages and their uncertainty. They do not justify medical advice, a definitive statement that a concentration works or does not work, or a conclusion that one concentration is superior to another.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of the distinction between within-group change and a randomized comparison. Every group’s mean TNSS change is negative, including placebo. The treatment question is not whether a group’s score changed from baseline, but how its change compares with the change in the randomized placebo group. That distinction prevents a common overreading of before-and-after results.

The study also illustrates why effect estimates and precision should be considered together. The active-versus-placebo point estimates are consistently negative, but their confidence intervals include zero. A directional pattern across estimates can be described without treating it as conclusive evidence. The intervals reveal that the data are compatible with a range of differences, not just the point estimate.

Its dose-ranging structure raises a further issue: multiple concentrations create multiple comparisons, and secondary outcomes add further opportunities for testing. Without a reported analysis plan or multiplicity approach, nominal unadjusted results need cautious interpretation. The registry record’s missing details are not merely administrative; they affect how readers can evaluate the inferential claims and whether comparisons were chosen in advance.

Finally, planning illustrations based on observed effects help show how target effect size and sample size relate, but they are not evidence about the trial’s achieved power or its original design rationale. Keeping planning assumptions distinct from the original protocol is important when using posted results to inform the design of later research. This trial therefore offers a useful case in reading estimates, intervals, multiplicity, missing-data reporting, and planning calculations together rather than relying on a single numerical result.

18. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The registry record leaves several trial-specific details unavailable. It does not report the original sample-size justification, the randomization procedure, allocation concealment, who was masked, or a full statistical analysis plan. The record also does not explain the difference between the 617 recorded enrollment and the 600 described in the brief study summary.

The primary outcome analysis used randomized participants who received at least one dose, with no imputation of missing Day 14 data. The record does not report the amount or pattern of missing outcome data, reasons for missingness, or sensitivity analyses. As a result, readers cannot assess how missing observations might affect the posted means and comparisons.

The posted primary and secondary comparisons are unadjusted recalculations rather than sponsor-reported analyses. The record does not describe adjustment for multiple concentrations or outcomes, a dose-response test, covariate adjustment, or interim analyses. Several secondary comparisons are not listed, and the record does not explain their selection or absence.

The outcome is subject-rated and combines four nasal symptoms. The record does not provide individual symptom results, a threshold for a meaningful score change, or longer-term follow-up. The study description is specific to active seasonal allergic rhinitis and Mountain Cedar pollen sensitivity, and the intervention period was 14 days. These features constrain interpretation beyond the reported score summaries and study population.

Safety counts are also limited to the events recorded in the registry summary. The record does not provide detailed event definitions, collection methods, or comparative uncertainty estimates. These limitations favor a descriptive reading of the posted results rather than a broad or definitive conclusion.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Bepotastine Besilate Nasal Sprays in the Treatment of Seasonal Allergic Rhinitis (SAR) — NCT01753739.
• Registry record last updated 2020-10-05; status last verified 2020-10.
• Results first posted 2020-09-14.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

22. Record Summary

NCT01753739 is a completed, randomized, double-masked, parallel Phase 2 dose-ranging study of bepotastine besilate nasal spray for seasonal allergic rhinitis. It compared placebo with concentrations of 0.5%, 1%, 2%, and 4%, each administered twice daily for 14 days. The study description focuses on participants with active symptoms and a history of Mountain Cedar pollen sensitivity.

The primary endpoint was mean change in twice-daily averaged reflective TNSS at 14 days. All groups had negative mean changes. The unadjusted recalculated active-versus-placebo differences were negative, while all corresponding confidence intervals included zero. The registry record reports no sponsor analyses and does not describe multiplicity handling. Missing Day 14 data were not imputed in the stated analysis population.

The record lists zero serious adverse events and zero deaths in each group. It does not report the original sample-size rationale or a full analysis plan. The posted results are best read as estimates with uncertainty and notable reporting limitations, rather than as a definitive conclusion about treatment effects or concentration ranking.