A Study to Confirm the Efficacy and Safety of K-161 Ophthalmic Solution for Treatment of Moderate to Severe Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Confirm the Efficacy and Safety of K-161 Ophthalmic Solution for Treatment of Moderate to Severe Dry Eye Disease (NCT05403827), a randomized phase 3 study. The primary outcome is Change in EDS (VAS) From Baseline to Day 85.

2. Clinical Question

The primary endpoint addresses a symptom reported by participants rather than an examiner-rated sign of the ocular surface. The scale runs from 0 mm, meaning “None,” to 100 mm, meaning “Worst Possible.” The comparison is between average changes over the stated timeframe, not simply the scores at Day 85.

The registry record also lists changes in staining scores, Ocular Surface Disease Index score, Schirmer’s test, and tear film break-up time as secondary outcomes. These offer other perspectives on symptoms and ocular surface measures. They do not replace the primary question: whether the average change in self-rated eye dryness differed between randomized groups by Day 85.

The record describes the study as a Phase 3 randomized trial with quadruple masking and a parallel-group design. It includes a 12-week administration period and a 40-week extension in its official title. Details of how participants entered or were handled in the extension are not reported in the registry record.

3. Trial Design

The registry record describes a Phase 3, randomized, quadruple-masked, parallel-group, vehicle-controlled study of K-161 ophthalmic solution for moderate to severe dry eye disease. The listed enrollment is 644. The study is marked completed. The registry dates are 2022-07-03 for study start and 2023-08-25 for primary completion.

Participants were assigned to K-161 or vehicle solution. The official title describes a 12-week administration period and a 40-week extension. The primary outcome is change in Eye Dryness Score from baseline to Day 85, which falls within the stated 12-week period. The registry record does not report enough detail to describe the extension’s assignment structure, eligibility, or analysis population.

Quadruple masking indicates that the record classifies the study as masked across four roles, but the specific roles are not reported in the registry record. The record also does not give details of the randomization sequence, allocation concealment, or site-level procedures. These omissions do not establish that a procedure was absent; they limit what can be described from the registry information.

Enrollment and outcome analysis counts should not be treated as interchangeable. The primary outcome lists 292 participants in the K-161 group and 306 in the vehicle group; the registry record notes that the number analyzed may differ from the overall group counts. The reason for every difference and the complete analysis-population definitions 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: At Visit 1 (Screening), eligible participants were provided single-masked run-in product (Vehicle) for self-administration in the morning and evening, for approximately 14 days. At Visit 2 (Baseline), participants who remained eligible for the study were randomized in a 1:1 ratio to double-masked IP (K-161 or Vehicle). Each participant provided voluntary informed consent before any study-specific assessments or procedures were performed.

12 Week Primary

52 Week Overall

Analysis population for the primary outcome, as defined in the registry: The number of participants analyzed for the outcome measure may differ from the overall number of participants in each group. This discrepancy can be attributed to several factors, including: • Missing data: Some participants may have incomplete data due to factors such as missed visits, early withdrawal, or loss to follow-up.

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: Baseline analysis was based on the Safety Population in the 12-week Primary Period (SP12).

6. Primary Endpoint

The registry lists the primary outcome as Change in EDS (VAS) From Baseline to Day 85, measured over Baseline to Day 85.

The primary endpoint is change from baseline to Day 85 in Eye Dryness Score measured on a visual analog scale, in millimeters. Participants rate the severity of eye dryness themselves. The scale anchors are 0 mm for “None” and 100 mm for “Worst Possible.” A negative change indicates a lower reported score at follow-up than at baseline; it does not, by itself, establish the cause or importance of that change.

This measure captures the participant’s experience of dryness directly. It therefore addresses a symptom that may not be fully represented by examination-based signs. The study also lists ocular surface and tear-function measures among its secondary outcomes, making the primary symptom measure one part of a broader set of assessments.

The reported arm values are mean changes: -18.0 mm for K-161 and -19.4 mm for vehicle. The unadjusted mean difference is defined as K-161 minus vehicle, so its positive value of 1.4 mm reflects a less negative average change in the K-161 group. Whether a difference of this size is meaningful to participants cannot be determined from these results alone; a threshold for clinical importance is not reported in the registry record.

7. Results Posted in the Registry

• K-161: mean -18.00 versus -19.40 on control; difference 1.40 (95% CI -2.64 to 5.44), standardized effect d = 0.06; z-test p = 0.497.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline to Day 85 in Total Eye Sum Fluorescein Staining Score (Study Eye)

• 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:
  • K-161: mean -4.73 versus -5.44 on control; difference 0.71 (95% CI -0.19 to 1.61), standardized effect d = 0.13; z-test p = 0.123.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between K-161 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Day 85 in Corneal Sum Fluorescein Staining Score (Study Eye)

• 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:
  • K-161: mean -1.92 versus -2.19 on control; difference 0.27 (95% CI -0.19 to 0.73), standardized effect d = 0.09; z-test p = 0.251.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between K-161 and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline to Day 85 in Ocular Surface Disease Index Score (OSDI©)

• 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:
  • K-161: mean -14.12 versus -14.17 on control; difference 0.05 (95% CI -2.73 to 2.83), standardized effect d = 0.00; z-test p = 0.972.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between K-161 and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover ocular surface staining, participant-reported symptoms, and tear-related measures. Across the three secondary outcomes with arm summaries and recalculated contrasts included in the record, the estimated differences are modest relative to their uncertainty, and each corresponding unadjusted confidence interval includes zero. This broad pattern does not provide a clear contrast that changes the interpretation of the primary result.

The registry record lists five secondary outcomes, but summary results are posted for only three in the information analyzed. Results for the other listed secondary outcomes are not reported in the registry record. The outcomes that are posted should be considered alongside the primary symptom result, not treated as independent replications of it: they assess different features, use different scales, and may have different variability.

Unadjusted secondary tests carry less confirmatory weight when several outcomes are examined. Without a reported testing hierarchy or multiplicity adjustment, a nominal p-value for one secondary measure does not account for the number of comparisons being considered. The registry record does not report whether a pre-specified strategy controlled the overall false-positive risk.

These secondary findings are therefore useful as descriptive context about the range of measured outcomes, but they do not independently establish a reliable treatment-group difference. Their interpretation is further limited by the absence of complete posted results for all listed secondary outcomes and by the lack of reported analysis-population details and missing-data sensitivity results.

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

• Change From Baseline to Day 85 in Total Eye Sum Fluorescein Staining Score (Study Eye)
• Change From Baseline to Day 85 in Corneal Sum Fluorescein Staining Score (Study Eye)
• Change From Baseline to Day 85 in Ocular Surface Disease Index Score (OSDI©)
• Change From Baseline to Day 85 in Schirmer's Test (Unanesthetized) (Study Eye)
• Change From Baseline to Day 85 in Tear Film Break-up Time (TFBUT) (Study Eye)

9. Statistical Interpretation

10. Statistical Methods Explained

The primary measure is continuous: each participant has an Eye Dryness Score on a scale in millimeters, and the posted arm summaries use means and standard deviations. A mean describes the group’s average score change. A standard deviation describes how spread out individual changes are around that average. When participant responses vary substantially, the group mean alone does not show how closely individual experiences cluster around it.

What does the mean difference represent?

The comparison is a difference between the two arm means for change from baseline to Day 85. The reported contrast is K-161 minus vehicle. A positive contrast means the average change in the K-161 group was numerically higher, or less negative, than the vehicle-group change. A negative contrast would mean the K-161-group average was numerically lower. This direction is a feature of the stated subtraction order, not a judgment about clinical value.

The recalculated comparison uses the posted arm-level means, standard deviations, and analyzed sample sizes to produce a simple unadjusted estimate. It is not the same as a participant-level model that could account for baseline values, sites, repeated measurements, or other covariates. Those details are not reported in the registry record for the sponsor’s full analysis. The recalculated result is best understood as a transparent summary-statistic comparison rather than a reconstruction of every step in the trial analysis.

What does the confidence interval add?

A confidence interval describes the uncertainty around an estimated group contrast under the method used. A narrower interval indicates greater precision, while a wider interval indicates that a broader range of contrasts remains compatible with the data and calculation. For the primary comparison, the 95% interval extends from -2.643 to 5.443 mm. Because it includes zero, it does not distinguish the observed contrast from no average difference at the conventional zero point. The interval also includes values in both directions, so it does not establish which direction the underlying contrast takes.

A p-value addresses how unusual the observed data, or data more extreme, would be under a specified null hypothesis and analysis. It is not the probability that the null hypothesis is true, nor a measure of clinical importance. The primary recalculated p-value is 0.497. The sponsor analysis reports a p-value of 0.502 from its control-based mean-imputation analysis. The p-values are close, but their analyses are not identical: the recalculation is unadjusted from posted summaries, while the sponsor’s stated method handles missing values through control-based mean imputation.

Why can analysis methods differ?

Missing outcome data can affect a comparison if participants with observed results differ systematically from those without them. A method for imputing missing values assigns values according to an assumption about what those unobserved results would have been. The sponsor analysis is labelled control-based mean imputation. The registry record does not report the full imputation algorithm, the amount or pattern of missing data, or the sensitivity analyses used to assess dependence on that assumption. The registry notes that outcome analysis counts may differ from overall group counts and mentions missing data among possible reasons, but it does not give a complete account of missingness for this outcome.

General statistical context: imputation does not recover the unobserved answers as known details. It makes assumptions so an analysis can include participants whose outcomes are missing. Different reasonable assumptions can yield different estimates, particularly when missingness is substantial or related to outcomes. For that reason, the sponsor analysis and the simple recalculation answer related but not identical statistical questions.

Why do secondary outcomes need care?

Several outcomes were assessed, and the registry record lists seven outcome measures and seven analyses. Five secondary outcomes are posted. Testing many outcomes increases the chance that at least one result may look notable by chance if each is judged without adjustment. The registry record does not report a multiplicity strategy, such as a hierarchy of tests or an adjustment controlling the overall error rate. The unadjusted secondary p-values therefore should not be treated as if each were an isolated confirmatory test.

General statistical context: over-dispersion means that observed variation is greater than a chosen model expects. It matters because a model that understates variation can make intervals too narrow and tests too optimistic. The posted outcomes are summarized as continuous means and standard deviations; the registry record does not report an over-dispersion analysis or a special model for it. That general issue should not be mistaken for a finding that over-dispersion occurred in this trial.

The registry record does not report the trial’s original statistical analysis plan, exact model specification, covariate adjustment, missing-data sensitivity analyses, interim analyses, or original sample-size justification. These elements cannot be inferred from the posted summary results. The calculations and explanations should be read within that boundary.

11. Confidence Intervals and Precision

The primary unadjusted mean difference is 1.4 mm, with a 95% confidence interval from -2.643 to 5.443 mm. This interval is the main guide to the precision of the recalculated contrast. It includes zero and extends to values on either side, so the observed estimate does not tightly resolve the direction or size of the underlying average difference.

The standard deviations are 25.1 mm in the K-161 group and 25.34 mm in the vehicle group, much larger than the estimated mean contrast. This describes substantial variation in individual changes relative to the between-group estimate. It does not mean every participant had a change near the group mean, and it does not establish whether any individual participant experienced an important change.

A confidence interval is not a range containing a fixed share of individual participant results. It is an interval for the group contrast, constructed using a statistical method. Its interpretation depends on the assumptions of that method, including how the available summary data represent the analyzed groups. The recalculated interval is unadjusted and does not incorporate the sponsor’s control-based mean-imputation procedure.

The registry record does not report the sponsor analysis’s confidence interval for the primary comparison. It also does not report a threshold for a clinically important difference on the Eye Dryness Score scale. Thus, the posted record supports a description of statistical uncertainty but does not establish whether every value in the interval would be clinically meaningful or negligible.

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 estimates are planning illustrations based on the observed effect, not the trial’s original design calculation. For continuous outcomes such as this one, the displayed figures are participants per arm, not total participants across both arms and not total events. The listed assumptions are a two-sided significance level of 0.05, equal allocation between arms, and a normal approximation. Each scenario uses the stated fraction of the observed effect as the effect to detect.

The 80% power column describes the number of participants per arm that the planning calculation would require to have an 80% chance of detecting the assumed effect under its stated assumptions, if that effect and the model assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. For example, planning around 100% of the observed primary effect gives estimates of 5,096 participants per arm for 80% power and 6,822 participants per arm for 90% power.

The smaller-effect scenarios require larger sample sizes: planning for 75% or 50% of the observed effect yields larger estimates than planning for the full observed effect. This is expected because smaller group differences are harder to distinguish from random variation. These calculations do not show that the trial had a particular chance of success, and they are not observed power. The original design assumptions and sample-size justification are 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 = 1.400; pooled standard deviation σ = 25.223.
2. n = 2 × (1.96 + 0.842)² × 25.223² / 1.400² = 5,095.4, rounded up to 5,096 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 1.4                      # observed difference in means
sigma <- 25.2231040886282                     # 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(5403827)
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 = 5,096 (80% power), 6,822 (90% power)
 75% of observed effect: n per arm = 9,059 (80% power), 12,127 (90% power)
 50% of observed effect: n per arm = 20,382 (80% power), 27,286 (90% power)
power.t.test: 5096.4 
Simulated power at n = 5,096 per arm: 0.802 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry record reports a sponsor superiority analysis using control-based mean imputation. Its p-value is 0.502; an estimate and confidence interval for that analysis are not reported in the registry record. The recalculated comparison is a simple unadjusted contrast from the posted arm summaries: the mean difference is 1.4 mm, the 95% confidence interval is -2.643 to 5.443 mm, and the unadjusted p-value is 0.497.

These results are close in their p-values, but they are not identical analyses. The sponsor’s stated approach uses an imputation method for missing values, whereas the recalculation uses group-level summary statistics and does not reproduce that missing-data procedure. The registry does not give enough information to recreate the sponsor’s model or assess all assumptions behind it.

The small difference between the p-values should not be read as a substantive contradiction. Both are non-small p-values, but neither is a measure of effect size or clinical importance. Since the reported sponsor analysis has no posted estimate or interval in the registry record, its precision and estimated direction cannot be compared in full with the recalculated contrast.

15. Multiplicity, Missing Data and Analysis Populations

The record lists seven outcome measures and seven analyses, including a primary measure and secondary outcomes. Five secondary outcomes are listed, while results are posted for three of them in the information analyzed. A complete account of how the outcomes were prioritized and how the analyses related to one another is not reported in the registry record.

Multiplicity arises when several outcomes or hypotheses are tested. If each test is interpreted without considering the others, the chance of at least one apparently positive result by chance can increase. Researchers may address this by specifying a primary hypothesis, a testing sequence, or an adjustment to the decision threshold. The registry record does not report whether such a strategy was used for the secondary outcomes. This makes unadjusted secondary p-values less persuasive as confirmatory evidence, even when an individual value appears notable.

The record describes control-based mean imputation for the sponsor’s primary superiority analysis. It does not report the full missing-data algorithm, the numbers and reasons for missing observations by outcome, or sensitivity analyses under alternative assumptions. The primary outcome’s analyzed sample sizes are 292 for K-161 and 306 for vehicle, while the overall enrollment is 644. The registry notes that analysis counts can differ from group totals, with missing data among the possible reasons, but does not give a complete participant flow or a definitive explanation for each count.

Analysis-population definitions, including the precise population used for each sponsor analysis, are not reported in the registry record. The original statistical analysis plan, interim-analysis procedures, and original sample-size justification are also not reported. These details matter because they clarify which participants and hypotheses were intended to support the primary conclusion and how missing data and multiple outcomes were handled. Their absence from the registry record limits independent assessment; it does not establish that the trial lacked such procedures.

16. 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 serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: allergy to arthropod sting (0.8%), rectal abscess (0.8%), suicidal ideation (0.8%), abdominal pain (0.3%), urinary tract infection (0.3%).

For the 12-week groups, the registry record reports serious adverse events in 3 of 321 participants at risk in the K-161 group and 2 of 322 at risk in the vehicle group. In the 40-week extension groups, serious adverse events were reported in 1 of 122 participants at risk in the K-161 group and 2 of 121 at risk in the vehicle group. No deaths are reported in any of these groups.

These are counts of participants affected, not a complete description of event severity, timing, relatedness, or clinical course. The registry lists serious-event terms including allergy to arthropod sting, rectal abscess, suicidal ideation, abdominal pain, urinary tract infection, and leukaemia. The listed terms and reported percentages do not by themselves establish whether an event was caused by study treatment.

The number at risk differs across the 12-week and extension groups, so the extension counts should be read in their own group context. The registry record does not provide enough detail to establish why participants entered or did not enter the extension, or to compare safety statistically. These descriptive figures alone do not establish equivalence of safety between groups.

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

The primary result describes the average change in participant-rated eye dryness over the period from baseline to Day 85. The two groups had negative average changes, and the recalculated between-group contrast was 1.4 mm in the K-161-minus-vehicle direction. Its 95% confidence interval, -2.643 to 5.443 mm, includes zero and allows contrasts in either direction. The data therefore do not precisely identify a distinct average difference between the groups under this unadjusted calculation.

This does not mean that the groups are proven identical. A non-small p-value is not evidence that the true difference is exactly zero, and a confidence interval covering zero can include nonzero values. It also does not establish that either group’s within-group change was caused by the assigned solution. The comparison against vehicle is needed to separate the observed group changes from changes that may occur in both groups.

The record does not report a clinically important threshold for the Eye Dryness Score. Statistical uncertainty therefore cannot be translated into a definitive judgment about whether the range of possible differences would matter to participants. The score is self-rated and captures reported dryness, while secondary measures assess other symptoms or ocular surface features; one type of measure does not substitute for another.

The sponsor’s analysis uses control-based mean imputation, while the recalculated comparison is unadjusted from posted summaries. The sponsor’s estimate and interval are not reported, and the missing-data assumptions cannot be fully evaluated from the registry record. These limitations, along with unreported multiplicity procedures and incomplete results for some listed secondary outcomes, constrain the strength of broader conclusions.

The results are therefore best understood as a description of the posted comparative data and their precision at the stated assessment. They are not a recommendation about treatment, and they do not establish a general conclusion beyond the participants, outcomes, and analyses recorded.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares a participant-rated symptom with a vehicle control in a randomized, masked, parallel-group design. Random assignment and masking are relevant design features for reducing some sources of systematic difference between groups, although the registry record does not describe the detailed procedures used to implement them.

The primary result also illustrates why arm-level changes should not be interpreted in isolation. Both groups had average changes from baseline, but the trial’s comparative question concerns the difference between those changes. The recalculated contrast is small relative to the standard deviations, and its confidence interval spans zero and values in both directions. That distinction is central to reading controlled clinical trial results.

The record gives both a sponsor analysis and enough arm-level summary information for an unadjusted recalculation. Their p-values are close, while the methods differ in how they handle missing data. This makes the role of analytical assumptions visible: summary-statistic calculations can be useful for checking the broad pattern, but they do not replace the sponsor’s full analysis or reveal its unreported estimate and interval.

The trial also demonstrates the importance of distinguishing statistical evidence from clinical importance. No threshold for a meaningful change on the dryness scale is reported, and multiple secondary outcomes appear without a reported multiplicity plan. Both factors affect how much can be inferred from individual estimates or tests. The registry record’s omissions are therefore relevant to interpretation, not merely technical details.

Finally, the safety counts and the 40-week extension are part of the record, but their different group sizes and limited supporting detail call for descriptive rather than definitive comparisons. Reading the efficacy, secondary, and safety results with attention to their populations, methods, and uncertainty keeps conclusions aligned with what is actually reported.

19. Limitations

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

The primary recalculation uses aggregate means, standard deviations, and analyzed counts. It cannot reproduce participant-level adjustments or the sponsor’s control-based mean-imputation analysis. The sponsor’s primary estimate and confidence interval are not reported in the registry record, limiting direct comparison of effect size and precision across methods.

Analysis counts for the primary outcome differ from the overall enrollment. The registry record notes possible reasons such as missing data but does not give a complete account of missing observations, their timing, or reasons by group. The complete analysis-population definitions and sensitivity analyses are not reported, so the effect of missing-data assumptions cannot be fully assessed.

The record lists five secondary outcomes, but results for only three are included in the analyzed information. It does not report a multiplicity strategy for the several measures and analyses. Consequently, unadjusted secondary findings should be given limited confirmatory weight, and the full pattern across all listed secondary outcomes cannot be assessed from the posted results.

The original statistical analysis plan, interim-analysis details, and sample-size justification are not reported in the registry record. The planning illustrations based on observed effects are not substitutes for those design records. A clinically important threshold for the primary score is also not reported, leaving the clinical meaning of the range of plausible group differences unresolved.

The official title describes a 40-week extension, but the record information analyzed does not give sufficient detail about extension entry, treatment assignment, or follow-up completeness. Safety findings are therefore best read as the reported event counts in groups with different numbers at risk, rather than as a fully adjusted comparison or proof of equal safety.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Study to Confirm the Efficacy and Safety of K-161 Ophthalmic Solution for Treatment of Moderate to Severe Dry Eye Disease — NCT05403827.
• Registry record last updated 2025-01-14; status last verified 2025-01.
• Results first posted 2025-01-14.
• 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.

23. Record Summary

The registry record describes a completed Phase 3 randomized, quadruple-masked, parallel-group, vehicle-controlled study of K-161 ophthalmic solution for moderate to severe dry eye disease. Enrollment was 644, and the official title describes 12-week administration with a 40-week extension.

The primary outcome was change in participant-rated Eye Dryness Score from baseline to Day 85. The recalculated unadjusted mean difference was 1.4 mm, with a 95% confidence interval from -2.643 to 5.443 mm and an unadjusted p-value of 0.497. The sponsor reports a control-based mean-imputation superiority analysis with a p-value of 0.502, but its estimate and interval are not reported in the registry record.

Secondary outcome results are incomplete in the information analyzed, and multiplicity procedures, full missing-data details, and the original design assumptions are not reported. Serious adverse event counts and no deaths are reported across the listed 12-week and extension groups.