Effectiveness of Olopatadine HCl Ophthalmic Solution for the Treatment of Allergic Conjunctivitis in Japan: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effectiveness of Olopatadine HCl Ophthalmic Solution for the Treatment of Allergic Conjunctivitis in Japan (NCT02251613), a randomized phase 4 study. The primary outcome is Mean Ocular Itching at 7 Minutes Post-CAC, Day 1.

2. Clinical Question

3. Trial Design

This completed Phase 4 trial compared the two eye drops in a randomized, double-masked, within-participant arrangement. Olopatadine was placed in one eye and epinastine in the fellow eye; randomization determined whether olopatadine went to the right or left eye. This structure allows each participant's eyes to be compared under the same participant-level circumstances, although the eyes are not independent observations.

After study medication was instilled, a conjunctival allergy challenge was performed using one drop of allergen solution in each eye. The primary endpoint was assessed on Day 1, at 7 minutes after challenge. The registry record describes an assessment window of 7 (±1) minutes. Conjunctival hyperemia was assessed at 20 minutes after challenge on Day 1.

The record lists 50 participants in each eye-treatment group and describes the primary analysis population as all randomized participants. It does not report withdrawals, missing endpoint observations, or how those events, if any, were handled. The start and primary completion dates are recorded as 2013-12 and 2014-01, respectively. The trial status is completed, and Alcon Research is listed as sponsor.

The record identifies randomized allocation and double masking, but it does not report the method used to generate the random sequence, conceal allocation, or maintain masking. Although both treatments were used within each participant, the registry's model field is recorded as single-group. Details explaining that classification, including the planned statistical handling of the paired eyes, 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: All subjects qualifying for treatment at Visit 3 were randomized. This reporting group includes all randomized participants (50).

Overall Study

Analysis population for the primary outcome, as defined in the registry: This analysis population includes all randomized participants.

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: This reporting group includes all randomized participants.

6. Primary Endpoint

The registry lists the primary outcome as Mean Ocular Itching at 7 Minutes Post-CAC, Day 1, measured over Day 1, 7 minutes post-CAC.

The primary endpoint was mean ocular itching at 7 minutes after the conjunctival allergy challenge on Day 1. Each eye was assessed separately by the participant on a 0–4 scale: 0 represented no itching, while 4 represented incapacitating itching with an irresistible urge to rub. The endpoint is a continuous score, and the registry record reports a mean and standard deviation for each treatment-eye group.

Itching is a directly experienced symptom of allergic conjunctivitis, so an eye-specific patient rating can describe symptom intensity after exposure to the allergen. Measuring both eyes in the same participant makes the treatment-eye comparison relevant to the study's fellow-eye design. The challenge provides a defined context for assessing the symptom after the study medications were instilled.

The score should be interpreted as a scale measurement, not as a count of episodes or a percentage of participants with symptoms. A lower mean indicates less reported itching on this scale within the observed group. A difference between group means describes an average contrast; it does not show how every participant's two eyes compared. The endpoint is measured at a particular time after challenge and does not, by itself, describe symptoms at other times or outside the challenge setting.

7. Results Posted in the Registry

• Epinastine 0.05%: mean 0.37 versus 0.23 on control; difference 0.14 (95% CI -0.01 to 0.29), standardized effect d = 0.37; z-test p = 0.066.

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 Conjunctival Hyperemia at 20 Minutes Post-CAC, Day 1

• 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:
  • Epinastine 0.05%: mean 1.12 versus 0.89 on control; difference 0.23 (95% CI -0.13 to 0.59), standardized effect d = 0.25; z-test p = 0.209.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Epinastine 0.05% and the control. The interval gives the range of effects that remain compatible with the data.

The secondary endpoint is mean conjunctival hyperemia at 20 minutes after challenge on Day 1. Its observed mean difference is in the same direction as the primary itching contrast: the mean is higher in the epinastine-treated eyes than in the olopatadine-treated eyes. The secondary interval includes zero, and its unadjusted p-value does not provide clear evidence of a difference under the displayed summary comparison.

Considering the endpoints together, the observed group means have a consistent direction, but neither comparison yields a precise distinction from no difference. The secondary result therefore offers context about another sign measured after the same challenge, but it does not resolve the uncertainty in the primary result or independently confirm a treatment effect.

Secondary outcomes are often examined alongside a primary outcome, and the chance of a seemingly notable result can increase when multiple endpoints or analyses are considered. Statistical adjustment or a prespecified hierarchy can help control that issue. The registry record does not report a multiplicity strategy, so the secondary comparison should be read as exploratory rather than as confirmatory evidence. It is also important that the record lists no reported analyses, and does not explain whether these outcomes were part of a prespecified analysis plan.

Because the study used both treatments in the eyes of each participant, dependence between the two eye measurements is relevant to the secondary comparison as well as the primary one. The record does not describe the paired analysis for hyperemia. Thus, the group averages indicate the direction of the observed data, while the inferential weight of this secondary result remains limited by uncertainty about both multiplicity handling and paired statistical methods.

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

• Mean Conjunctival Hyperemia at 20 Minutes Post-CAC, Day 1

9. Statistical Interpretation

10. Statistical Methods Explained

The outcomes are continuous scale measurements, so the registry record summarizes each treatment-eye group with a mean and standard deviation. A mean gives the average score across the observations contributing to that summary. A standard deviation describes how spread out the individual scores are around that average. It is not the uncertainty in the mean difference; that uncertainty is described by a standard error or confidence interval.

What does a mean difference represent?

The reported contrast is defined as the epinastine mean minus the olopatadine mean. With that orientation, a positive value means the observed average score is higher in the epinastine-treated eyes, while a negative value means it is higher in the olopatadine-treated eyes. For a scale on which higher scores mean more itching or hyperemia, lower average scores indicate less of the measured symptom in the observed data. The contrast is an average and does not imply that every participant had the same direction of difference between eyes.

The primary mean difference is 0.14, with an unadjusted confidence interval that includes zero. The corresponding unadjusted p-value is 0.066. The secondary mean difference is 0.23, also with an interval that includes zero, and its unadjusted p-value is 0.209. These are summary-level comparisons. The registry record does not report the investigators' statistical analysis plan or list reported analyses.

Why does pairing matter?

In a fellow-eye study, each participant receives both treatments, and the outcomes from the two eyes belong to the same person. A paired analysis evaluates the within-participant difference between eyes. An independent-groups analysis instead treats the treatment-eye observations as if they came from unrelated participants. These approaches can yield different standard errors because the two eyes may be correlated. If the eyes tend to have similar scores within a participant, accounting for that pairing can improve precision; if the correlation differs, the estimated uncertainty can change in other ways.

The registry record reports group means and standard deviations and includes unadjusted comparisons, but it does not report the paired differences, within-participant covariance, or a method specifying how eye pairing was handled. The group summaries alone cannot reconstruct that information. Therefore, the posted interval and p-value should not be interpreted as a confirmed paired analysis. The original trial's statistical method for the fellow-eye comparison is not reported in the registry record.

What do the confidence interval and p-value convey?

A confidence interval gives a range of effect values reasonably compatible with the estimate and its statistical uncertainty under the method used. An interval that crosses zero indicates that the data do not clearly separate a positive mean difference from no difference or a negative mean difference at the confidence level represented. It is not a probability statement that the true effect lies within the particular interval. The registry record does not state a confidence level for its comparison interval, so that level is not reported in the registry record.

A p-value measures how unusual data at least as discrepant as those observed would be under a specified null hypothesis and statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of a difference. The p-values posted for these comparisons are unadjusted. The record does not report whether other analyses were planned or how the paired structure was incorporated into the model behind these inferential summaries.

Why can extra variability matter?

General statistical explanation: a standard deviation describes variation among observations, while a standard error describes variation in an estimate across repeated samples under a model. Greater variability generally makes an estimate less precise when other features are held constant. In a paired design, the variability of the within-person differences is more directly relevant than the separate group standard deviations. Those difference scores can be less variable than either group's raw scores when paired measurements are strongly related, or more variable when they are not. That is why paired outcomes need methods that reflect their dependence.

Over-dispersion is a concern mainly for count outcomes, when observed variation exceeds what a simple count model expects. These outcomes are scale scores summarized as means, not event counts, so over-dispersion is not the central issue for the primary comparison. The key uncertainty is the unreported handling of within-participant dependence and the limited detail about the analysis plan.

How should the effect-size and planning values be read?

The registry-derived planning illustrations use the observed mean difference as a reference and show scenarios for detecting a stated fraction of that difference. Such scenarios depend on assumptions about the statistical test, allocation, significance level, and outcome variability. They are hypothetical design calculations, not evidence that the original trial had those design assumptions. The original sample-size justification and planned power are not reported in the registry record.

The comparison's standardized effect-size summary is based on the mean contrast relative to a pooled standard deviation. It places the difference on a scale that is less tied to the original measurement units, but it does not correct for paired-eye dependence or make the estimate more certain. The posted planning figures are illustrations based on the observed effect and should be read as design aids, not as additional trial findings.

11. Confidence Intervals and Precision

The primary mean difference is 0.14, with a confidence interval that extends slightly below zero and to a positive value. The interval therefore includes no mean difference. Its width indicates that the data remain compatible with a range of contrasts rather than pinning down a single value precisely. The unadjusted p-value of 0.066 is consistent with that uncertainty: the result does not clearly distinguish a difference from no difference under the posted summary comparison.

The secondary hyperemia contrast is 0.23, and its confidence interval also includes zero. Its unadjusted p-value is 0.209. This interval likewise leaves uncertainty about both the size and direction of the underlying mean contrast. These intervals do not establish that the treatments are equivalent, because a failure to distinguish a difference is not the same as demonstrating that any difference is acceptably small.

Confidence intervals are useful because they show a range of estimates consistent with the data and analysis method, rather than reducing interpretation to whether a p-value crosses a threshold. Their validity depends on the statistical method and its assumptions. Here, the fellow-eye arrangement makes accounting for within-participant dependence important, but the paired analysis details are not reported in the registry record. The confidence intervals should therefore be treated as unadjusted summary comparisons with that limitation in mind.

The record does not state the confidence level for these intervals, nor does it report missing observations or the number of paired eye assessments used in the endpoint analysis. Without those details and the paired covariance, the precision of a properly paired treatment contrast cannot be established from the posted group summaries alone.

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 illustrate the number of participants per arm that would be used in a hypothetical equal-allocation design under the stated assumptions. The registry record's own original sample-size assumptions and justification are not reported in the registry record.

The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect being targeted is set to a stated fraction of the observed effect. The entries for 80% power describe the planned sample size per arm that, under those assumptions, would give an 80% chance of detecting the target effect if that effect were the true one. The 90% power entries use the same idea but aim for a greater chance of detecting the target effect, and therefore require more participants per arm.

The values are 117 participants per arm when planning for 100% of the observed effect, 207 when planning for 75% of the observed effect, and 465 when planning for 50% of the observed effect at 80% power. For 90% power, the corresponding figures are 156, 277, and 622 participants per arm. These are planning illustrations based on the observed effect, not observed power.

The pattern reflects a general design principle: smaller effects are harder to distinguish from random variation, so detecting a smaller effect generally requires more participants. These calculations do not establish what the trial was designed to detect, and the registry record does not report whether its original design used these assumptions. The illustration also does not address the fellow-eye pairing unless that structure is incorporated into the design calculation; such detail is not reported in the registry record.

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 = 0.140; pooled standard deviation σ = 0.381.
2. n = 2 × (1.96 + 0.842)² × 0.381² / 0.140² = 116.0, rounded up to 117 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 <- 0.14                      # observed difference in means
sigma <- 0.380591644679701                     # 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(2251613)
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 = 117 (80% power), 156 (90% power)
 75% of observed effect: n per arm = 207 (80% power), 277 (90% power)
 50% of observed effect: n per arm = 465 (80% power), 622 (90% power)
power.t.test: 117 
Simulated power at n = 117 per arm: 0.803 (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

The registry record identifies one primary outcome and one secondary outcome, but it does not report a strategy for controlling the chance of false-positive findings across multiple outcomes or analyses. It does not state whether an outcome hierarchy, adjustment procedure, or other multiplicity plan was used. The posted p-values are unadjusted, so the secondary result in particular should not be treated as confirmatory without more information about the analysis plan.

Missing-data information is also limited. The primary analysis population is described as all randomized participants, and each eye-treatment group has a reported sample size of 50. The record does not report whether all randomized participants contributed primary and secondary endpoint data, whether any assessments were missing, or how missing measurements were handled. It also does not describe imputation, exclusions, or sensitivity analyses. The reported group sizes alone do not establish that all endpoint observations were complete.

The paired-eye structure raises an additional analysis-population question: a treatment contrast based on paired eye measurements generally depends on having both eyes assessed for the same participant. The registry record does not state how incomplete pairs were treated or how many complete pairs contributed to each outcome. The posted group summaries cannot answer that question.

The record lists no reported analyses and does not provide the full statistical analysis plan. Details of the planned model, the treatment of within-participant dependence, the confidence level for the intervals, and any adjustment for covariates are not reported in the registry record. These gaps limit assessment of whether the displayed inferential summaries match the trial's intended analysis and how sensitive the results might be to missing observations or analytic choices.

15. 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 serious adverse events among 50 participants at risk in the olopatadine group and zero among 50 at risk in the epinastine group. It also lists zero other adverse events among 50 at risk in each group. No serious adverse-event terms are listed. These figures describe what was recorded in the registry and do not, on their own, establish that no adverse events occurred outside the reported categories or observation period.

Deaths are not reported in the registry record. The record does not provide additional detail about adverse-event definitions, severity grading, collection windows, or the method used to compare safety between the fellow eyes. Because participants received both treatments, the group labels refer to the eye-treatment assignments, not to separate participant groups. The safety counts should therefore be read as descriptive registry figures, not as a definitive comparative safety analysis.

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

The posted results show lower average itching and hyperemia scores in olopatadine-treated eyes than in epinastine-treated eyes. The unadjusted mean differences are 0.14 for itching and 0.23 for hyperemia. Both confidence intervals include zero, and the unadjusted p-values are 0.066 and 0.209, respectively. The observed direction is consistent across these measures, but the estimates remain uncertain.

These results do not establish that one treatment is superior, that the treatments are equivalent, or that one has no effect. Demonstrating equivalence or non-inferiority requires a suitable prespecified framework and margins, which are not reported in the registry record. A non-significant comparison does not prove sameness; it indicates that the available comparison does not clearly separate the observed means from no difference using the displayed unadjusted analysis.

The findings concern a short-term, Day 1 response to a Japanese cedar pollen conjunctival challenge in healthy Japanese adults with a history of allergic conjunctivitis. They do not directly describe longer-term outcomes, routine exposure, other populations, or other clinical settings. The registry record does not provide results beyond the listed outcomes and time points.

Interpretation is further constrained by the fellow-eye design and the lack of reported detail on paired analysis. Since both eyes belong to the same participant, an analysis that ignores that dependence may not represent the intended treatment contrast. The registry record also does not report the original sample-size justification, handling of missing observations, or multiplicity strategy. Accordingly, the most defensible reading is descriptive: the group averages differ in the observed direction, while precision and methodological reporting are insufficient to support a firm comparative conclusion.

17. Why This Trial Matters Statistically

This trial is statistically notable for its fellow-eye design. Each participant received both study treatments, with randomized eye assignment. That arrangement controls many characteristics shared by a participant's eyes, but it also creates correlated observations. Correctly representing that dependence is central to estimating uncertainty. The registry record gives group-level means and standard deviations but does not report the paired differences or the analysis method used to account for within-participant correlation.

The contrast between the observed mean differences and their uncertainty is also instructive. The primary and secondary averages point in the same direction, yet each unadjusted interval includes zero. Statistical interpretation therefore needs to consider effect estimates and precision together, rather than relying only on direction or a thresholded p-value. These results neither prove no difference nor establish a clear difference.

The planning illustrations offer a separate lesson: sample-size requirements depend on the effect a study aims to detect. Targeting a smaller fraction of the observed effect requires more participants per arm under the stated assumptions. Those illustrative calculations should not be confused with the trial's original design rationale, which is not reported in the registry record.

Finally, registry summaries are not a substitute for a full statistical analysis plan and report. Information about multiplicity, missing observations, paired analysis, and confidence-level conventions would help readers judge how well the posted uncertainty reflects the design. These considerations are especially important when outcomes are measured separately in eyes but treatment assignment occurs within participants.

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 central trial-specific limitation is that the two treatments were assigned to fellow eyes, but the registry record does not explain how the statistical analysis accounted for correlation between eyes. The reported group summaries do not include within-participant differences or their variability. As a result, the posted unadjusted comparison may not convey the precision of a paired treatment contrast.

The study outcomes are assessed after a controlled conjunctival allergy challenge on Day 1. These measurements describe itching and hyperemia at specified post-challenge times; the registry record does not report longer-term outcomes or measurements in other exposure settings. The results are also specific to healthy Japanese adults aged 20 years or older with a history of allergic conjunctivitis to Japanese cedar pollen. Generalization to other populations or settings is not established by this record.

The registry record does not report the original sample-size justification, detailed analysis plan, confidence level for the intervals, missing-data procedures, or multiplicity strategy. It also does not state whether endpoint observations were available for every randomized participant or how incomplete eye pairs were treated. These omissions make it difficult to assess the robustness of the posted estimates.

The safety summary is limited to event counts and does not provide further detail on ascertainment, timing, or comparative analysis. The record lists no reported analyses, leaving the status of formal investigator-reported inferential results unclear. Together, these limitations mean the summary supports a description of the observed averages, but not a complete appraisal of the statistical analysis or the broader clinical implications.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Effectiveness of Olopatadine HCl Ophthalmic Solution for the Treatment of Allergic Conjunctivitis in Japan — NCT02251613.
• Registry record last updated 2015-10-07; status last verified 2015-10.
• Results first posted 2015-02-09.
• 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

NCT02251613 is a completed Phase 4 randomized, double-masked study sponsored by Alcon Research. It compared olopatadine HCl ophthalmic solution, 0.1%, in one eye with epinastine HCl ophthalmic solution, 0.05%, in the fellow eye of healthy Japanese adults with a history of allergic conjunctivitis to Japanese cedar pollen.

The primary outcome was mean ocular itching at 7 minutes after a Day 1 conjunctival allergy challenge. The observed mean was 0.23 for olopatadine and 0.37 for epinastine; the unadjusted mean difference was 0.14, with an interval including zero and an unadjusted p-value of 0.066. The secondary hyperemia comparison also had an interval including zero.

The direction of the observed means is consistent across the listed outcomes, but uncertainty remains. The registry record does not report the paired-eye analysis details, multiplicity plan, missing-data handling, or original sample-size justification.