A Phase III Multinational Multicenter Investigator-Masked Randomized Active-Controlled Trial Comparing the Efficacy and Safety of DE-130A With Xalatan® in Patients With Open-Angle Glaucoma or Ocular Hypertension: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase III Multinational Multicenter Investigator-Masked Randomized Active-Controlled Trial Comparing the Efficacy and Safety of DE-130A With Xalatan® in Patients With Open-Angle Glaucoma or Ocular Hypertension (NCT04133311), a randomized phase 3 study. The primary outcome is Intraocular Pressure (IOP) Change (mmHg) at Week 12.

2. Clinical Question

3. Trial Design

The registry describes a completed Phase III, multinational, multicenter, randomized, active-controlled, parallel-group trial. Its title characterizes the trial as investigator-masked, while the registry’s masking classification is double. The record does not explain how masking was implemented or which trial roles were masked beyond the title description.

The listed enrollment is 386. That registry figure describes enrollment, whereas the endpoint-specific counts describe participants evaluable for a particular outcome and timepoint. Those figures need not match: the primary analysis population required post-baseline measurements, and the secondary outcomes have their own reported analysis counts. The registry states that the Full Analysis Set included randomized participants who received at least one dose and provided at least one post-baseline intraocular pressure measurement at peak and trough timepoints separately.

The initial treatment comparison covered 3 months. After 12 weeks, the registry describes DE-130A/DE-130A as continuing DE-130A once daily for an additional 12 months, and Xalatan®/DE-130A as switching from Xalatan® to DE-130A once daily for an additional 12 months. That later period was open label. The posted primary endpoint and secondary outcomes discussed in the record are assessed at Week 12, so they address the initial randomized comparison rather than the full open-label follow-up.

The registry lists Santen SAS as sponsor. The start date is 2019-04-10, primary completion is dated 2022-02-03, and status is completed. Details of the allocation sequence, stratification, concealment, site distribution, and the trial’s original statistical plan are not reported in the registry record. The posted results therefore support a description of the registered design and outcomes, but do not fill in unreported operational or planning details.

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.

Period 1 Double Masked Treatment Period

Reasons for not completing this period:

Period 2 Open Label Treatment Period

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized subjects who received at least one dose of the study medication and provided at least one post-baseline IOP measurement at peak and trough timepoints separately. The number analyzed are participants evaluable for the outcome measure at Week 12 (09:00) timepoint.

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 Intraocular Pressure (IOP) Change (mmHg) at Week 12, measured over Week 12 (09:00) peak timepoint.

The primary endpoint is change from baseline in peak intraocular pressure, measured in mmHg, at Week 12 at the 09:00 timepoint. The registry describes measurements with a calibrated Goldman applanation tonometer in the morning at 9:00 am ± 1 hour. The posted result is a least-squares mean change for each treatment group, accompanied by a standard error, and a mean difference between groups.

As a continuous endpoint, this measure retains information about the magnitude of change rather than reducing each participant’s measurement to a binary category. In general, a continuous outcome can be useful when the scientific question concerns differences in average measurements between groups. The least-squares means are model-based group estimates; they are not necessarily the same as simple arithmetic averages. The registry says that the primary analysis used a Mixed-Effects Model for Repeated Measures, but does not report the full model specification or covariates.

Intraocular pressure is the measurement chosen for the trial’s primary efficacy question in participants with open-angle glaucoma or ocular hypertension. The posted endpoint is specific: it concerns change from baseline at the peak timepoint at Week 12. It should not be read as a summary of every pressure measurement, every follow-up visit, or the open-label period. The registry’s rationale for selecting this endpoint and timepoint is not reported in the registry record.

7. Results Posted in the Registry

• Xalatan®: mean -8.20 versus -8.80 on control; difference 0.60 (95% CI -0.11 to 1.31), standardized effect d = 0.17; z-test p = 0.096.

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.

Corneal Fluorescein Staining (CFS) Change From Baseline (First Key Secondary Endpoint)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Xalatan®: mean -0.41 versus -0.71 on control; difference 0.30 (95% CI 0.10 to 0.50), standardized effect d = 0.45; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Xalatan® than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Ocular Surface Disease (OSD) Symptoms (Average of 3 Symptoms); Second Key Secondary Endpoint

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard errors.
• Result:
  • Xalatan®: mean -0.17 versus -0.26 on control; difference 0.09 (95% CI -0.07 to 0.25), standardized effect d = 0.15; z-test p = 0.281.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Xalatan® and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes concern corneal fluorescein staining and ocular surface disease symptoms, both assessed at Week 12. At a broad level, their posted estimates point toward larger reductions in the DE-130A group, but the strength of evidence is not uniform across the two measures. One secondary contrast has an unadjusted interval that does not include zero, while the other has an interval that includes zero. This is a mixed pattern rather than a consistent set of equally precise findings.

These outcomes complement the primary intraocular pressure endpoint by addressing different measured aspects of the trial. They do not substitute for the primary endpoint, and their results do not change the uncertainty around the primary contrast. The secondary findings may add context to the overall profile of measured outcomes, but they should be considered alongside their own analysis counts, uncertainty, and the absence of reported multiplicity adjustment.

Unadjusted secondary results carry less weight when several outcomes are examined because each additional statistical test creates another opportunity for a result to appear notable by chance. In general, a multiplicity strategy can control the overall chance of false-positive conclusions across a family of tests. The registry does not report a multiplicity procedure or a hierarchy governing these secondary endpoints. Therefore, a nominally notable unadjusted result should be treated as exploratory evidence rather than as definitive confirmation. The registry also lists four outcome measures, while only two secondary endpoints are posted in the record; explanations for the other measures are not reported in the registry record.

The secondary results can help identify questions for further evaluation, but they do not establish a complete account of effects on ocular surface measures. Their interpretation depends on outcome definitions, missing-data handling, and analysis choices, some of which are not detailed in the registry record. The overall reading is that the secondary pattern is suggestive in one measure and uncertain in another, with no reported adjustment that would support treating the set as a single confirmatory family.

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

• Corneal Fluorescein Staining (CFS) Change From Baseline (First Key Secondary Endpoint)
• Ocular Surface Disease (OSD) Symptoms (Average of 3 Symptoms); Second Key Secondary Endpoint

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous, and its reported group summaries are least-squares means with standard errors. A least-squares mean is a model-based estimate of a group’s average outcome. In general, model-based means can account for specified features of the analysis, such as repeated measurements or covariates, whereas a raw average is calculated directly from the observed values. The registry identifies an MMRM analysis, but its detailed model terms and any adjustment variables are not reported in the registry record.

What does a repeated-measures model do?

In general, a Mixed-Effects Model for Repeated Measures (MMRM) analyzes outcome measurements collected at multiple timepoints while recognizing that measurements from the same participant are related. That relationship matters: treating repeated measurements from one participant as if they came from unrelated people can misrepresent the uncertainty. A mixed-effects framework can model the correlation among a participant’s repeated measurements and estimate group patterns over time, subject to its specified structure and assumptions.

The registry says the primary endpoint analysis used MMRM, but it does not report the covariance structure, fixed effects, interaction terms, or exact handling of missing observations. It is therefore possible to explain the general purpose of the method, but not to reconstruct the trial’s precise model from the registry record. The posted endpoint is at Week 12; the description of a repeated-measures model does not mean that the Week 12 estimate alone summarizes every visit or the later open-label follow-up.

How should the standard error be read?

A standard error describes the estimated sampling uncertainty of an estimate. In general, it tends to be smaller when an estimate is more precise and larger when it is less precise, though its interpretation depends on the model and data. The primary group standard errors are 0.25 for DE-130A and 0.26 for Xalatan®. They are not standard deviations of individual participant measurements and do not describe the spread of individual responses. The record labels the reported dispersion as standard error.

The comparison is a mean difference between the Xalatan® and DE-130A estimates. Its direction follows that ordering: a positive reported contrast means the Xalatan® estimate is numerically higher than the DE-130A estimate. Since both group changes are negative, “higher” in this context means less negative, not an increase from baseline. This distinction helps prevent confusion between the direction of the within-group changes and the direction of the between-group contrast.

What does a confidence interval add?

In general, a confidence interval communicates uncertainty around an estimated effect. It gives a range of values that are compatible with the data and analysis under the method used; it is not a range containing a stated proportion of individual participant outcomes. For the primary comparison, the reported interval extends from -0.107 to 1.307. Because zero lies within this interval, the posted result does not rule out a zero difference at the confidence level used for that interval. The confidence level itself is not stated alongside the primary endpoint in the registry record.

How should the p-value be understood?

The posted unadjusted p-value for the primary comparison is 0.096. In general, a p-value evaluates how unusual data at least as inconsistent with a specified null hypothesis would be if that hypothesis and the analysis assumptions were true. It is not the probability that the null hypothesis is true, nor the probability that a result arose “by chance.” The registry calls the value unadjusted; it does not report an adjustment for testing multiple endpoints or comparisons.

A p-value should not replace the estimated contrast or its confidence interval. The estimate describes the observed model-based contrast, while the interval conveys precision and the p-value expresses evidence relative to a null model under a particular testing procedure. Neither answers whether a difference is clinically important. No threshold for clinical importance is reported in the registry record.

What can be inferred from the displayed effect summaries?

The registry comparison also includes an approximate pooled standard deviation and a standardized effect estimate. In general, standardizing a mean difference expresses it relative to a measure of outcome variability, which can help describe magnitude on a scale independent of the outcome’s measurement units. The posted values are d = 0.171 and pooled standard deviation = 3.502. The standard deviation is described as approximate, because the underlying group summaries are model-based estimates and standard errors rather than a direct report of raw participant-level variability. Such derived summaries do not replace the original mmHg-scale contrast.

The registry’s endpoint-specific counts are 188 for DE-130A and 189 for Xalatan®. These are the counts attached to the primary endpoint summaries, not a re-statement of the overall enrollment figure. Counts differ across outcomes in the posted record; an endpoint’s count reflects the participants included in that outcome’s analysis and should not be assumed to be identical to the count for another measure. The record does not provide a participant flow account explaining each difference.

Finally, the comparison calculation is marked as having no discrepancy. That is relevant when reading recalculated unadjusted summaries alongside the posted means: there is no flagged conflict in this record. It does not supply missing model details or validate assumptions that cannot be checked from the posted summaries. General statistical explanations describe what these methods mean; they are not additional claims about unreported trial procedures.

11. Confidence Intervals and Precision

The primary group means are estimated with standard errors of 0.25 and 0.26 mmHg. The reported between-group mean difference is 0.6 mmHg, with a confidence interval from -0.107 to 1.307. The interval includes zero, so the estimated contrast is not sharply separated from no difference by this interval. It also extends into positive values, meaning the data remain compatible with a range of positive contrasts under the stated analysis. Precision is about the uncertainty surrounding the estimate, not whether a treatment is beneficial.

A confidence interval is useful because it shows more than a single point estimate. In general, narrower intervals indicate greater precision, while wider intervals leave a broader range of effect sizes compatible with the analysis. The interval should not be interpreted as containing a fixed share of individual participant outcomes. It pertains to uncertainty in the estimated group contrast, given the model and assumptions. The registry does not identify the confidence level used for the primary interval in the endpoint entry.

The standard errors describe uncertainty in each least-squares mean, while the contrast interval describes uncertainty in the difference between those means. They are related quantities but are not interchangeable. The registry does not provide participant-level measurements or enough model detail to reconstruct the interval independently. The interval therefore belongs to the posted analysis and should be read as reported, rather than treated as a fully reproducible calculation from the summary values alone.

Precision also differs from clinical importance. Even a precise estimate would need interpretation against a meaningful threshold, and no such threshold is reported in the registry record. Conversely, uncertainty does not prove that there is no difference. The appropriate reading is that the point estimate is modest on the reported mmHg scale and the interval leaves uncertainty about the direction and magnitude of the between-group contrast.

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 event counts. The sample-size illustration uses the observed effect as its reference and shows scenarios for detecting the full observed effect, 75% of the observed effect, and 50% of the observed effect. The assumptions listed for the illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the effect to detect is the stated fraction of the observed effect. These are planning assumptions for the illustration, not the original trial design assumptions, which are not reported in the registry record.

The 80% power column describes the number of participants per arm that the illustration estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect and the assumptions were correct. The 90% power column uses the corresponding target of a 90% chance. These are design-planning targets for hypothetical future studies, not statements about the trial’s observed power. The illustration is not observed power.

The figures increase as the effect to detect becomes smaller. This is a general feature of sample-size planning: a smaller difference is harder to distinguish from sampling variation, so more participants are generally needed under otherwise similar assumptions. The values depend on the assumed effect, significance level, allocation, and approximation. They should not be interpreted as a recommendation or as evidence that the completed trial was designed using the displayed calculation. The registry’s own original sample-size justification and design assumptions 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 = 0.600; pooled standard deviation σ = 3.502.
2. n = 2 × (1.96 + 0.842)² × 3.502² / 0.600² = 534.8, rounded up to 535 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 <- 0.600000000000001                      # observed difference in means
sigma <- 3.50208060063348                     # 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(4133311)
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 = 535 (80% power), 716 (90% power)
 75% of observed effect: n per arm = 951 (80% power), 1,273 (90% power)
 50% of observed effect: n per arm = 2,140 (80% power), 2,864 (90% power)
power.t.test: 535.8 
Simulated power at n = 535 per arm: 0.795 (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 lists a primary outcome and two posted key secondary endpoints. It identifies the secondary endpoints as corneal fluorescein staining change from baseline and ocular surface disease symptoms, averaged across three symptoms. The posted comparisons are marked unadjusted. A prespecified strategy for controlling multiplicity, such as an order for testing endpoints or an adjustment to the testing threshold, is not reported in the registry record.

Multiplicity matters because testing several outcomes can increase the chance of at least one apparently unusual result even when no true effect exists for any outcome. In general, procedures for handling multiple comparisons define how evidence is assessed across a group of tests. Without a reported strategy, the secondary p-values should be read as unadjusted, endpoint-specific evidence. They do not establish that the trial met an overall error-rate target across all outcomes.

The primary outcome description names the Full Analysis Set and gives its inclusion criteria: participants had to be randomized, receive at least one dose, and provide at least one post-baseline intraocular pressure measurement at peak and trough timepoints separately. The Week 12 primary summary has outcome-specific analysis counts. The registry does not provide a fuller flow of participants by reason for exclusion, withdrawal, or missing measurement, nor does it describe a separate per-protocol analysis population.

Missing-data handling is important in repeated-measures analyses because participants may not contribute measurements at every scheduled timepoint. The record identifies MMRM but does not report the assumptions used for missing observations, the amount or pattern of missingness, imputation procedures, or sensitivity analyses. General descriptions of MMRM cannot establish which assumptions were applied in this trial. The original statistical analysis plan and detailed protocol are not reported in the registry record.

These omissions do not invalidate the posted estimates, but they constrain independent evaluation of their robustness. Interpretation should distinguish the reported model-based findings from unreported details about multiplicity and missingness. The absence of a posted adjustment also means that the secondary findings should not be treated as though a family-wise testing procedure had been documented.

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 0% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: acute heart failure (0.5%), bilateral pulmonary thrombosis (0.5%), patient diagnosed with bladder cancer (0.5%).

The registry reports serious adverse events and other adverse events for four named groups: DE-130A, Xalatan®, DE-130A/DE-130A, and Xalatan®/DE-130A. In the initial groups, the serious-event counts are 1 for DE-130A and 2 for Xalatan®. The later regimen groups each have 0 reported serious events. The record lists 193 at risk in each initial group, 71 in the DE-130A/DE-130A group, and 66 in the Xalatan®/DE-130A group. These are the registry’s group-specific figures; they should not be added together to infer a distinct participant total, because the record does not explain how the treatment-period groups relate at the participant level.

For other adverse events, the posted counts are 35 for DE-130A, 42 for Xalatan®, 21 for DE-130A/DE-130A, and 21 for Xalatan®/DE-130A. The corresponding at-risk counts are 193, 193, 71, and 66. Death counts are 1, 0, 0, and 0 in those groups, respectively. The registry lists acute heart failure, bilateral pulmonary thrombosis, and patient diagnosed with bladder cancer among the top serious terms, each shown as 0.5%.

These counts describe what the record reports, not comparative rates adjusted for exposure time or a causal assessment. The registry does not provide event timing, duration, relatedness, severity details beyond the serious-event classification, or a complete narrative for each event. The open-label follow-up groups should be read separately from the initial randomized comparison.

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

The primary result is an estimate of the difference in mean change from baseline in peak intraocular pressure at Week 12. It describes the measured endpoint in the analyzed participants under the registry’s stated MMRM approach. The estimated group changes are both negative, and the posted contrast is 0.6 mmHg. Its confidence interval includes zero, so the result leaves uncertainty about whether the group means differ and, if they do, by how much.

This finding does not establish that one treatment is clinically better than the other. Statistical significance, even when present, is not the same as clinical importance; conversely, a result that does not meet a statistical threshold does not prove equivalence. The registry does not report an equivalence or noninferiority margin, nor a threshold for a clinically meaningful change. Without such criteria, the result should not be converted into a claim of equivalence, superiority, or lack of effect.

The primary result applies to the specified Week 12 peak measurement and the analysis population described for that endpoint. It should not be generalized automatically to other timepoints, trough measurements, the open-label treatment period, or outcomes not posted in detail. The secondary outcomes concern separate measures and have their own uncertainty; they do not establish the primary endpoint result or resolve its interval.

Safety counts are descriptive. They report adverse events in the named groups but do not, by themselves, demonstrate that an event was caused by a study treatment or establish a comparative safety profile. The record does not provide the details needed for such causal or exposure-adjusted interpretation.

In general, a randomized active-controlled trial can support a comparison between assigned groups when its conduct and analysis are appropriate. Here, the registry describes randomization and posts model-based results, but does not include all design and analysis details needed for a complete independent appraisal. The most defensible conclusion is therefore limited to the reported estimates, their uncertainty, the specified timepoint, and the information actually recorded.

17. Why This Trial Matters Statistically

This trial is statistically interesting because it combines a randomized active-control comparison with a continuous primary endpoint and a repeated-measures analysis. These features make it important to distinguish the estimated group changes from the between-group contrast. A decrease within each group is not itself evidence that the treatments differ; the comparison of interest is the contrast between the groups and its uncertainty.

The use of least-squares means and MMRM also illustrates why model-based results should be interpreted alongside the analysis description. Repeated observations from the same participant are generally correlated, and a repeated-measures method is intended to account for that structure. Yet readers need model details to evaluate the specification and missing-data assumptions. The registry identifies the method but does not report enough detail to reproduce or fully assess it.

The record also illustrates the difference between a trial’s original design and a post hoc planning illustration based on an observed effect. The planning figures are useful for showing how sample size depends on the effect one seeks to detect, but they do not reveal the trial’s original justification or confer evidence about its observed power. That distinction matters when using results to plan future research.

Finally, the secondary outcomes and safety figures need different interpretive approaches. Unadjusted testing across multiple outcomes raises multiplicity concerns, while adverse-event counts are descriptive and do not establish causality. Separating these questions keeps the interpretation proportionate to the information available in the registry record.

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.

Several trial-specific limitations arise from the scope of the posted record. The primary endpoint is restricted to the Week 12 09:00 peak timepoint, and the registry does not provide a full series of numerical results across all measurement times. The later 12-month treatment period is described as open label, but the posted primary result concerns the initial comparison. This record therefore does not support a detailed quantitative account of the longer follow-up.

The primary endpoint counts are specific to participants evaluable at that outcome and timepoint. The registry does not include a detailed participant flow or explain why endpoint counts differ from the enrollment figure and from counts for secondary outcomes. It also does not report the extent or pattern of missing data. Since the primary analysis used MMRM, missing-observation assumptions and sensitivity analyses would be relevant to a full assessment, but they are not reported in the registry record.

The registry gives limited detail about the statistical model. It names MMRM and reports least-squares means and standard errors, but does not report model terms, covariance structure, covariate adjustments, or the confidence level for the primary interval. The original sample-size assumptions and justification are also not reported in the registry record. The planning illustration is not evidence of those original choices.

Multiplicity procedures for the secondary outcomes are not reported, and the posted secondary comparisons are unadjusted. The registry lists four outcome measures but posts two secondary endpoints in the record. The reasons the remaining outcomes are not represented in the posted results are not reported. Safety information is likewise limited to group counts and selected serious-event terms; event timing, relatedness, and exposure-adjusted comparisons are not reported in the registry record.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase III Multinational Multicenter Investigator-Masked Randomized Active-Controlled Trial Comparing the Efficacy and Safety of DE-130A With Xalatan® in Patients With Open-Angle Glaucoma or Ocular Hypertension — NCT04133311.
• Registry record last updated 2024-05-28; status last verified 2024-05.
• Results first posted 2024-05-28.
• 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

NCT04133311 is a completed Phase III randomized, active-controlled, parallel-group trial comparing DE-130A with Xalatan® in people with open-angle glaucoma or ocular hypertension. The initial comparison lasted 3 months and was followed by a 12-month open-label period using DE-130A. The primary outcome was change from baseline in peak intraocular pressure at Week 12. The posted group estimates were -8.8 mmHg for DE-130A and -8.2 mmHg for Xalatan®, with a mean difference of 0.6 mmHg and a confidence interval that includes zero.

The registry also posts Week 12 results for corneal fluorescein staining and ocular surface disease symptoms. Their overall pattern is not uniformly precise, and the comparisons are unadjusted. Serious and other adverse-event counts are reported for the initial and later treatment groups, but the record does not provide enough event detail for causal interpretation. The registry identifies MMRM for the primary analysis, while important details about model specification, missing data, multiplicity, and the original sample-size plan are not reported in the registry record.