Phase 2, Multi-center, Randomized, Double- Masked and Placebo-Controlled Study of YP-P10 Ophthalmic Solution Compared to Placebo in Subjects With Dry Eye (ICECAP 1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Phase 2, Multi-center, Randomized, Double- Masked and Placebo-Controlled Study of YP-P10 Ophthalmic Solution Compared to Placebo in Subjects With Dry Eye (ICECAP 1) (NCT05467293), a randomized phase 2 study. The primary outcome is Total Corneal Fluorescein Staining.

2. Clinical Question

3. Trial Design

ICECAP 1 is a Phase 2, randomized, parallel-group study of YP-P10 Ophthalmic Solution compared with placebo in people with dry eye. The registry lists three arms: 1% YP-P10, 0.3% YP-P10, and YP-P10 placebo vehicle. Enrollment is recorded as 257. The sponsor is Yuyu Pharma, Inc., and the study status is completed.

The registry lists the study start as 2022-06-27 and primary completion as 2023-03-06. It records triple masking, while the study title describes the study as double-masked. The record does not explain this difference. The registry identifies randomization and a parallel model; allocation procedures and details of masking are not reported in the registry record.

The main result is a continuous outcome: mean Total Corneal Fluorescein Staining score at Day 85. The record describes the outcome as using the modified National Eye Institute scale, with scores from 0 to 20 and higher scores indicating worse staining. The posted arm summaries give the mean and standard deviation for each group. The comparisons are between each YP-P10 concentration and the placebo group.

The registry also lists secondary staining outcomes, including regional fluorescein staining and lissamine green staining measures. Some secondary results include group means and unadjusted comparisons. A detailed statistical analysis plan, the trial’s originally planned sample-size assumptions, the analysis populations, and procedures for handling missing observations are not reported in the registry record. Those omissions limit how fully the posted summaries can be connected to the protocol’s intended analyses.

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

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 Total Corneal Fluorescein Staining, measured over Day 85.

Total Corneal Fluorescein Staining is a continuous score describing corneal staining, a clinical sign relevant to dry eye. The registry identifies the modified National Eye Institute scale, scored from 0 to 20, with higher scores indicating worse staining. The primary measurement is reported at Day 85.

Using a continuous score retains information about the observed level of staining rather than reducing the outcome to a simple event/no-event category. Comparing group means gives a direct summary of the average score in each arm, while the standard deviation describes variation among observations within an arm. The posted comparison expresses the mean in each YP-P10 arm relative to the placebo mean.

This endpoint addresses a sign of dry eye, not the full range of symptoms or all aspects of the condition. The registry objective mentions signs and symptoms, but the primary endpoint itself is corneal staining. The reason this endpoint was selected over other possible measures is not reported in the registry record. Nor is the clinical interpretation of a difference of any particular size defined in the record. Accordingly, the observed means and their uncertainty describe the recorded staining scores; they do not by themselves establish the importance of a difference to participants.

7. Results Posted in the Registry

• 1% YP-P10 Ophthalmic Solution: mean 7.35 versus 7.12 on control; difference 0.23 (95% CI -0.31 to 0.77), standardized effect d = 0.13; z-test p = 0.400.
• 0.3% YP-P10 Ophthalmic Solution: mean 7.25 versus 7.12 on control; difference 0.13 (95% CI -0.44 to 0.70), standardized effect d = 0.07; z-test p = 0.655.

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.

Fluorescein Staining: Inferior

• 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:
  • 1% YP-P10 Ophthalmic Solution: mean 1.71 versus 1.73 on control; difference -0.02 (95% CI -0.15 to 0.11), standardized effect d = -0.04; z-test p = 0.770.
  • 0.3% YP-P10 Ophthalmic Solution: mean 1.71 versus 1.73 on control; difference -0.02 (95% CI -0.17 to 0.13), standardized effect d = -0.04; z-test p = 0.789.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1% YP-P10 Ophthalmic Solution 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 0.3% YP-P10 Ophthalmic Solution and the control. The interval gives the range of effects that remain compatible with the data.

Fluorescein Staining: Superior

• 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:
  • 1% YP-P10 Ophthalmic Solution: mean 1.34 versus 1.26 on control; difference 0.08 (95% CI -0.07 to 0.23), standardized effect d = 0.15; z-test p = 0.311.
  • 0.3% YP-P10 Ophthalmic Solution: mean 1.36 versus 1.26 on control; difference 0.10 (95% CI -0.06 to 0.26), standardized effect d = 0.19; z-test p = 0.216.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1% YP-P10 Ophthalmic Solution 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 0.3% YP-P10 Ophthalmic Solution and the control. The interval gives the range of effects that remain compatible with the data.

Fluorescein Staining: Central

• 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:
  • 1% YP-P10 Ophthalmic Solution: mean 1.33 versus 1.29 on control; difference 0.04 (95% CI -0.12 to 0.20), standardized effect d = 0.07; z-test p = 0.627.
  • 0.3% YP-P10 Ophthalmic Solution: mean 1.28 versus 1.29 on control; difference -0.01 (95% CI -0.17 to 0.15), standardized effect d = -0.02; z-test p = 0.904.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 1% YP-P10 Ophthalmic Solution 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 0.3% YP-P10 Ophthalmic Solution and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary results concern regional fluorescein staining, including inferior, superior, and central regions, as well as a broader list of staining outcomes in the registry. Across the displayed regional comparisons, the mean differences are small in magnitude relative to the scale values, and the confidence intervals include zero. The direction is not uniform across regions and concentrations. Taken together, the posted regional summaries do not show a consistent separation from placebo across the staining measures considered.

This broad pattern is in line with the primary result in the limited sense that neither the primary comparison nor the displayed regional comparisons show a clear difference from placebo in the posted unadjusted summaries. Secondary measures are related to the primary endpoint because they also assess staining, but they are not interchangeable with the total corneal score. A result on one region or staining method cannot be assumed to represent the overall endpoint or symptoms.

The registry lists 38 posted secondary outcomes, while the record does not list sponsor-reported statistical analyses for the secondary results considered. Repeatedly testing outcomes creates a multiplicity concern: even when there is no true difference on any outcome, a collection of unadjusted tests can produce apparently notable results by chance. Without a reported prespecified hierarchy or adjustment, isolated secondary p-values carry less weight than a primary result defined in advance. They are best treated as exploratory evidence requiring cautious interpretation, not as independent confirmation.

Secondary outcomes can nevertheless help describe whether an observed pattern appears consistent across related measures. Here, their value is descriptive rather than conclusive because the registry record does not report the analysis plan, missing-data methods, or a multiplicity procedure. The overall pattern should not be used to claim effects on symptoms, safety, or unreported outcomes. The secondary summaries complement the primary score but do not resolve its uncertainty.

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

• Fluorescein Staining: Inferior
• Fluorescein Staining: Superior
• Fluorescein Staining: Central
• Fluorescein Staining: Temporal
• Fluorescein Staining: Nasal
• Lissamine Green Staining: Conjunctival Sum
• Lissamine Green Staining: Inferior Temporal
• Lissamine Green Staining: Superior Temporal

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is summarized as a mean and standard deviation in each arm. A mean is the arithmetic average of the recorded continuous scores. The standard deviation describes how spread out individual observations are around that average. A larger standard deviation indicates greater variation among scores; it does not mean that the group mean is less accurate by that same amount. The registry identifies the endpoint as a score on the modified National Eye Institute scale, with higher scores worse.

The posted treatment comparisons are unadjusted differences in means relative to placebo. The comparison for 1% YP-P10 is the 1% arm mean minus the placebo mean, and the comparison for 0.3% YP-P10 is the 0.3% arm mean minus the placebo mean. A value above zero therefore means a higher average staining score in the YP-P10 arm; a value below zero means a lower average score. Since higher scores are worse on this scale, the sign of a difference has a direct direction-of-score interpretation. The comparisons do not, by themselves, adjust for baseline values or other covariates.

A confidence interval gives a range of values compatible with the observed data under the assumptions of the statistical method. Its width conveys precision: a narrower interval generally indicates more precise estimation, while a wider interval leaves greater uncertainty about the size and direction of the difference. If an interval includes zero for a difference in means, the data are compatible with no difference as well as with some positive or negative differences within the interval. That does not prove that the true difference is zero.

The p-value quantifies how unusual data at least as incompatible with a null hypothesis of no mean difference would be, under the assumptions of the test. It is not the probability that the null hypothesis is true, nor is it a measure of clinical importance. The posted p-values are unadjusted. When multiple outcomes or comparisons are examined, the chance of at least one small p-value can increase; a multiplicity strategy may address that issue, but one is not reported in the registry record. The p-values should therefore be interpreted as individual unadjusted summaries, not as evidence that a family of outcomes has met a prespecified overall criterion.

In general, standard errors describe the sampling uncertainty of an estimate, while standard deviations describe variation among individual observations. The registry includes arm-level standard deviations and comparison-level uncertainty calculations. A confidence interval for a difference uses the uncertainty of the group means and the comparison method; it is not obtained by treating the observed standard deviation as if it were the confidence interval. The specific model used for the trial’s primary analysis is not reported in the registry record, so the posted simple comparisons should not be assumed to reproduce an adjusted or otherwise prespecified sponsor analysis.

In general, randomization is intended to make comparison groups similar on average with respect to measured and unmeasured baseline factors. It does not guarantee identical groups, and the registry summary does not provide baseline characteristics to assess the realized balance. Masking is intended to reduce the influence of knowledge of assigned treatment on study conduct, outcome assessment, or reporting. The record lists triple masking, whereas its title says double-masked; the record does not clarify the difference or identify the masked roles. The registry identifies a randomized parallel design but does not give enough detail to reconstruct implementation.

For continuous outcomes, the mean difference is most straightforward to interpret when the score’s scale and direction are understood. Here, the scale range and the fact that higher is worse are recorded. However, the registry does not identify a threshold for a clinically important difference. Statistical compatibility with a range of mean differences should not be confused with whether those differences matter to people with dry eye.

The registry contains no sponsor-reported analyses for the posted primary comparisons. The displayed recalculated comparisons are simple, unadjusted calculations from the posted group summaries. Because the discrepancy indicator is false, there is no reported discrepancy requiring an alternate interpretation; if a difference between a recalculation and a sponsor analysis were identified, the sponsor’s own analysis would take precedence. No additional adjustment, covariate model, or missing-data method should be inferred from the summary statistics alone.

General caution about dispersion: some continuous measures can have variability that is not well represented by a normal distribution, and bounded scores can have floor or ceiling patterns. Such features may affect the suitability of methods based on normal approximations. The registry does not report a distributional assessment or alternative model for this endpoint. These are general considerations, not claims about the observed score distribution in this trial.

11. Confidence Intervals and Precision

The primary mean difference for 1% YP-P10 versus placebo is 0.23, with a confidence interval that extends from a negative value to a positive value. For 0.3% YP-P10 versus placebo, the mean difference is 0.13, and its confidence interval also extends across zero. Both intervals therefore include no mean difference, while also allowing for differences in either direction. The registry record does not report a clinically important threshold for this scale, so the clinical meaning of the ranges cannot be judged from a threshold specified in the record.

Confidence intervals express uncertainty in the estimated group contrast, not the range containing most individual participants’ scores. Individual scores vary within each arm, as reflected by the standard deviations. The two kinds of uncertainty answer different questions: standard deviations describe variability among observations, while confidence intervals describe uncertainty in the estimated contrast.

The unadjusted p-values, 0.4 for 1% YP-P10 and 0.655 for 0.3% YP-P10, are consistent with the intervals’ inclusion of zero. Neither p-value establishes equivalence, and the intervals should not be read as proof that differences outside their bounds are impossible. They indicate the range of effects compatible with the data under the calculation assumptions.

The registry does not provide a sponsor-reported analysis or full analysis plan that would allow assessment of whether the posted intervals reflect all prespecified adjustments or analysis choices. In particular, baseline adjustment, missing-data handling, and multiplicity procedures are not reported in the registry record. Precision is therefore best understood as precision of the posted unadjusted comparisons, not necessarily of every analysis that may have been conducted.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size planning figures are participants per arm for the continuous-outcome comparisons. They are not total event counts. The planning illustration uses a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. It considers effects set at the stated fractions of the observed effect. The trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the chosen effect under those assumptions, if that effect were the true effect. The 90% power column describes the corresponding planning estimate for a 90% chance. These are prospective design calculations conditional on assumptions, not guarantees about a future study’s result. This is not observed power.

The rows use the observed comparison as a reference and consider planning for 100%, 75%, and 50% of that observed effect. Smaller effects are harder to distinguish from random variation, so planning for a smaller effect requires more participants per arm. The resulting figures can be very large when the observed effect is small. That pattern reflects the mathematical relationship between effect size and sample size under the stated assumptions; it does not establish that such a study is feasible or that the observed effect is the right effect to target.

These illustrations are not a reconstruction of ICECAP 1’s original design. The registry records enrollment of 257, but its original target, assumed effect, variance assumptions, and power target are not reported in the registry record. The planning figures should therefore be read as hypothetical illustrations based on the posted effect, not as evidence about the study’s planned power or whether its design was adequate.

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 = 0.230; pooled standard deviation σ = 1.791.
2. n = 2 × (1.96 + 0.842)² × 1.791² / 0.230² = 951.9, rounded up to 952 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 <- 0.23                      # observed difference in means
sigma <- 1.79100530429142                     # 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(5467293)
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 = 952 (80% power), 1,275 (90% power)
 75% of observed effect: n per arm = 1,693 (80% power), 2,266 (90% power)
 50% of observed effect: n per arm = 3,808 (80% power), 5,098 (90% power)
power.t.test: 952.8 
Simulated power at n = 952 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. Multiplicity, Missing Data and Analysis Populations

The registry record does not report how multiplicity was handled. It lists a primary outcome and multiple secondary outcomes, but does not give a testing hierarchy, family-wise error control, false-discovery approach, or other procedure for interpreting multiple comparisons together. The posted p-values are unadjusted. A p-value for an individual comparison does not account for the number of outcomes or comparisons examined, so secondary findings should be treated cautiously and should not be read as confirmatory without a documented plan.

The analysis populations are not reported in the registry record. The posted arm summaries include group sample sizes, but the record does not say whether the primary analysis used all randomized participants, participants who received treatment, participants with observed endpoint data, or another defined population. Those distinctions matter because exclusions after randomization can affect how well a comparison preserves the benefits of random assignment.

Missing-data procedures are also not reported. The record does not describe how missing Day 85 scores were handled, whether any values were imputed, or how missingness was assessed. If participants with missing outcomes differ systematically from those with recorded outcomes, a complete-case comparison may not represent the randomized groups as intended. This is a general concern; the registry summary does not establish that missing data occurred or that any particular bias arose.

Other details needed to assess the planned analysis are absent, including the primary statistical model, covariate adjustment, protocol deviations, and any interim analyses. Their presence or absence cannot be inferred from the posted summary. Without these details, the unadjusted estimates and intervals remain useful descriptions of the available summary results, but they cannot fully substitute for a protocol-linked analysis report.

The record lists triple masking, while the title uses the term double-masked. It does not explain this difference. The uncertainty is about the registry description, not evidence that masking failed. Additional protocol and statistical-analysis documentation would be needed to evaluate these design and analysis features.

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 1% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: serious adverse event (1.2%).

The registry reports serious adverse events affecting 1 participant in the 1% YP-P10 arm, 0 in the 0.3% arm, and 1 in the placebo arm. It lists 86, 85, and 86 participants at risk in those groups, respectively. The registry also lists “Serious Adverse Event” as the top serious-event term at 1.2%. These counts describe the posted safety record; they do not establish whether an event was caused by study treatment.

Deaths are recorded as 1 in the 1% YP-P10 group and 0 in each of the other groups. The record does not provide details about the death or its relationship to treatment. Serious adverse events and deaths are distinct safety summaries, and a count alone does not describe severity, timing, duration, or clinical context. The registry does not report those details in the registry record for these summaries.

The reported counts are small, so comparisons between arms are imprecise and should not be interpreted as evidence of a safety difference or equivalence. The “other adverse events” counts are 28, 34, and 42 in the 1%, 0.3%, and placebo groups, respectively. No causal conclusion should be drawn from these group totals alone. The registry record does not report event-level descriptions or an analysis comparing safety between groups.

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

The primary result describes mean corneal staining scores at Day 85 in the two YP-P10 groups and placebo. The posted unadjusted mean differences are positive, which corresponds to higher average scores in the YP-P10 groups on a scale where higher scores indicate worse staining. Both confidence intervals include zero, and the unadjusted p-values do not provide clear evidence of a difference in these comparisons. The result is uncertain: it does not establish a difference, but it also does not prove that the groups are equivalent.

The interpretation is limited to the primary score and the registry’s posted summaries. It does not establish what happened to every participant, whether individual participants improved or worsened, or whether other dry eye signs and symptoms followed the same pattern. A group mean can conceal variation in individual responses. The registry does not report a threshold for a clinically meaningful change, so the importance of a particular score difference cannot be determined from the record.

The study objective includes safety and efficacy, but an objective is not itself a result. The posted primary outcome addresses staining at one time point. It cannot answer broader questions about symptom relief, longer-term outcomes, or effects beyond the measures and timeframes recorded. Nor do the summaries establish whether any serious adverse event was attributable to treatment.

Interpretation also depends on analysis details that are not reported, including the analysis population, missing-data approach, and multiplicity procedure. As a result, the unadjusted estimates should be read as descriptive comparisons rather than as a complete account of every planned analysis. A nonsignificant p-value is not evidence that the treatments are interchangeable; establishing equivalence would require an appropriate design and prespecified margin, neither of which is reported in the registry record.

In short, the posted data show similar group-average staining scores in the three arms, with uncertainty broad enough to include no difference and differences in either direction. That is a statement about the summaries available for this endpoint, not a medical recommendation or a conclusion about the overall value of treatment.

17. Why This Trial Matters Statistically

This trial is statistically informative as an example of why an estimated effect, its uncertainty, and the analysis plan must be considered together. The primary outcome is a continuous score with a defined direction: higher staining scores are worse. That makes the sign of the mean difference interpretable, but the confidence intervals show that the comparisons are not precise enough to settle whether the groups differ.

The results also illustrate why a p-value alone is an incomplete summary. The unadjusted p-values do not establish a difference, yet that does not demonstrate equivalence. The confidence intervals provide a range of effects compatible with the data, and the registry does not specify a clinically meaningful threshold to help judge their practical importance.

Many outcomes are listed, including multiple staining measures. Without a reported multiplicity strategy, secondary results are less persuasive as confirmatory evidence. Likewise, without stated analysis populations and missing-data methods, readers cannot fully evaluate whether the posted summaries reflect the intended randomized comparison. These are not merely technical omissions: they shape how much confidence can be placed in a statistical interpretation.

The planning illustrations add another useful lesson. When calculations are based on a small observed effect, they can imply large future sample-size requirements. Such figures depend on assumptions and are not evidence of the study’s original design or its observed power. Separating planning calculations from trial results prevents a retrospective illustration from being mistaken for a design justification.

Overall, the record supports careful reading of effect direction and precision, while showing why complete protocol-linked analysis information matters for interpretation.

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 summary leaves important trial-specific details unreported. It does not describe eligibility criteria, baseline characteristics, dosing instructions, adherence, or the clinical setting in enough detail to judge how representative the enrolled population was. Enrollment is listed as 257, but the available record does not explain how that enrollment relates to the original target or to participants with endpoint measurements.

The primary endpoint is reported at Day 85, while several secondary staining results use a timeframe of 13 weeks. The registry record does not explain the relationship between these time descriptions or provide further visit details. It also does not identify a clinically important difference for the staining scale, limiting interpretation of the practical meaning of the observed contrasts.

The record does not provide a full statistical analysis plan, sponsor-reported analyses, analysis populations, missing-data procedures, or a multiplicity strategy. The posted comparisons are unadjusted. Those limitations prevent assessment of whether the summaries correspond to the planned inferential approach, whether baseline adjustment was intended, or how incomplete endpoint data were addressed.

There is also a terminology inconsistency: the title describes the study as double-masked, while the registry’s masking field says triple. The record does not clarify which roles were masked or explain the difference. This should be treated as an unresolved documentation issue, not as evidence about actual masking conduct.

Finally, the safety information is presented as counts without event-level context or attribution. The numbers of serious events and deaths cannot establish treatment causation, and the registry summaries do not provide sufficient detail to compare safety profiles. These are limitations of the available record, not proof that the underlying study did not collect additional information.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Phase 2, Multi-center, Randomized, Double- Masked and Placebo-Controlled Study of YP-P10 Ophthalmic Solution Compared to Placebo in Subjects With Dry Eye (ICECAP 1) — NCT05467293.
• Registry record last updated 2024-07-30; status last verified 2024-07.
• Results first posted 2024-07-30.
• 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

ICECAP 1 is recorded as a completed, randomized, parallel-group Phase 2 study comparing 1% YP-P10 Ophthalmic Solution and 0.3% YP-P10 with YP-P10 placebo vehicle in people with dry eye. The registry reports enrollment of 257 and identifies Total Corneal Fluorescein Staining at Day 85 as the primary outcome.

The posted mean staining scores were 7.35 for 1% YP-P10, 7.25 for 0.3% YP-P10, and 7.12 for placebo. Both unadjusted mean differences versus placebo were positive, and both confidence intervals included zero. The registry also lists secondary staining outcomes and safety counts, but does not report the analysis plan, missing-data methods, analysis populations, or multiplicity procedure.

The results are best understood as uncertain unadjusted comparisons of group-average staining scores. They do not establish equivalence, clinical importance, or treatment causation for safety events.