Dose Ranging Study to Assess the Efficacy and Safety of Voclosporin Ophthalmic Solution in Subjects With Dry Eye Syndrome: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Dose Ranging Study to Assess the Efficacy and Safety of Voclosporin Ophthalmic Solution in Subjects With Dry Eye Syndrome (NCT04147650), a randomized phase 2, phase 3 study. The primary outcome is Number of Subjects With a ≥10 mm Increase From Baseline in Schirmer Tear Test (STT).

2. Clinical Question

This question focuses on whether participants crossed a defined threshold in a measure of tear production. It is different from asking how much the average Schirmer result changed, and it does not capture every possible pattern of change. A participant just below the threshold and one with no improvement are both counted as not meeting the endpoint, while participants who meet or exceed the threshold are counted as meeting it.

The study also posted a secondary measure of change in eye dryness from baseline to 4 Weeks. That measure provides a patient-reported symptom perspective alongside the tear-production endpoint, but it does not replace the primary question. The registry record does not report a broader clinical interpretation of the threshold or establish how a particular change should be understood by an individual participant.

3. Trial Design

The registry describes a multicenter, randomized, double-masked, parallel-group, vehicle-controlled Phase 2/3 clinical trial. The listed enrollment is 508. The study status is completed; its start date is 2019-10-14 and its primary completion date is 2020-09-17. The registry record does not report the trial’s original sample-size justification or the details used to determine its planned enrollment.

Participants were assigned to one of three voclosporin ophthalmic solution concentrations, 0.05%, 0.10%, or 0.20%, or to vehicle ophthalmic solution. Each group’s description specifies treatment in both eyes twice a day over 12 weeks. Randomization and double masking are stated in the record, but the exact procedures for generating the allocation sequence, concealing allocation, or maintaining masking are not reported in the registry record.

The primary endpoint was assessed at 4 Weeks and counted participants with at least a 10 mm increase from baseline in the Schirmer tear test in the study eye. Its listed population is the modified intent-to-treat population. For the posted primary results, the group counts were 12 of 120 for 0.05% VOS, 10 of 119 for 0.10% VOS, 13 of 122 for 0.20% VOS, and 6 of 121 for vehicle. These are endpoint counts and denominators, not a description of the number of participants assigned to each treatment at randomization.

The record lists two outcome measures and posts one secondary outcome, change from baseline in eye dryness. The trial is described as evaluating safety and efficacy, but the registry record does not report enough detail to reconstruct the full protocol, visit schedule, statistical analysis plan, or handling of every analysis population.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Modified intent to treat (mITT) number of subjects achieving ≥10 mm increase improvement at week 4

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 Number of Subjects With a ≥10 mm Increase From Baseline in Schirmer Tear Test (STT), measured over 4 Weeks.

The primary endpoint counts participants whose Schirmer tear test result increased by at least 10 mm from baseline at Week 4 in the study eye. The test measures tear production. The registry describes its scale as having a minimum of 0 mm and no specified maximum. The endpoint is binary: each participant either meets the threshold or does not.

A threshold-based endpoint can make a result easier to interpret as the number of participants reaching a prespecified level of improvement, rather than as an average change that may conceal differences among individuals. But it also discards information about the amount of change. A participant meeting the threshold by a small amount is counted with someone whose increase is larger, and participants who fall short are grouped together even if their changes differ.

The posted primary population is modified intent-to-treat. The registry record does not report the exact operational definition of that population, including any exclusions from the randomized group, or how missing Week 4 measurements were treated. Those details matter because the count and denominator depend on which participants had outcomes included in the analysis.

The measure is one aspect of dry eye syndrome: tear production in the study eye. The secondary measure of eye dryness addresses a symptom rather than the same test result. Neither endpoint alone captures every aspect of the condition, and the registry record does not provide a definition of a clinically important change for either outcome.

7. Results Posted in the Registry

• 0.05% Voclosporin Ophthalmic Solution (VOS): 10.0% (12/120) versus 5.0% (6/121) on control; risk difference 5.0 percentage points (95% CI -1.6 to 11.7), risk ratio 2.02 (0.78–5.20); unadjusted two-proportion z-test p = 0.137.
• 0.10% VOS: 8.4% (10/119) versus 5.0% (6/121) on control; risk difference 3.4 percentage points (95% CI -2.9 to 9.8), risk ratio 1.69 (0.64–4.52); unadjusted two-proportion z-test p = 0.285.
• 0.20% VOS: 10.7% (13/122) versus 5.0% (6/121) on control; risk difference 5.7 percentage points (95% CI -1.0 to 12.4), risk ratio 2.15 (0.84–5.47); unadjusted two-proportion z-test p = 0.098.

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 in Eye Dryness

• 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:
  • 0.05% Voclosporin Ophthalmic Solution (VOS): mean -10.60 versus -7.00 on control; difference -3.60 (95% CI -9.50 to 2.30), standardized effect d = -0.18; z-test p = 0.232.
  • 0.10% VOS: mean -9.30 versus -7.00 on control; difference -2.30 (95% CI -7.93 to 3.33), standardized effect d = -0.12; z-test p = 0.423.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between 0.05% Voclosporin Ophthalmic Solution (VOS) 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 0.10% VOS and the control. The interval gives the range of effects that remain compatible with the data.

The registry posts one secondary endpoint: change from baseline in eye dryness at 4 Weeks. The mean changes were -10.6 for 0.05% VOS, -9.3 for 0.10% VOS, -5.0 for 0.20% VOS, and -7.0 for vehicle. The recalculated unadjusted mean differences versus vehicle were -3.6 and -2.3 for the 0.05% and 0.10% groups, with confidence intervals that include zero. Sponsor-reported ANCOVA results are available for those two comparisons; the registry does not post a sponsor analysis for the 0.20% comparison.

Across the posted secondary results, the estimates vary by dose and do not present a consistent pattern that independently resolves the uncertainty in the primary endpoint. The secondary measure addresses eye dryness, while the primary outcome counts participants crossing a tear-production threshold. They therefore provide different kinds of evidence rather than repeated measurements of exactly the same outcome.

Unadjusted secondary results generally carry less confirmatory weight when many outcomes or comparisons may be examined. In general, testing multiple hypotheses increases the chance of observing an apparently notable result by chance if no correction or prespecified testing hierarchy is used. The registry record does not report whether a multiplicity adjustment or testing hierarchy was used. The secondary findings are best treated as supporting or exploratory evidence unless the full protocol or analysis plan establishes otherwise; the record does not report that plan.

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

• Change From Baseline in Eye Dryness

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary because it records whether each participant met the Schirmer threshold. The group result is therefore expressed as a count and denominator. A risk difference compares the proportion meeting the endpoint in a VOS group with the proportion in the vehicle group. A positive risk difference in these comparisons means the observed proportion meeting the threshold was higher in the VOS group. The recalculated estimates are 0.050, 0.035, and 0.057 for the 0.05%, 0.10%, and 0.20% groups, respectively.

What does a confidence interval add?

In general, a confidence interval describes the range of values reasonably compatible with the observed data under a statistical method and its assumptions. It communicates uncertainty around an estimate; it is not a range containing a fixed proportion of individual participant outcomes, and it does not give the probability that a particular treatment effect is true. For the recalculated risk differences, each interval crosses zero, so the data are compatible with both a positive difference and no positive difference, as well as with some negative differences.

Why are odds ratios also reported?

The sponsor’s analyses used logistic regression and reported odds ratios. In general, an odds ratio compares the odds of an event between groups; odds and risks are related but are not interchangeable measures. An odds ratio of 1 represents equal odds. The sponsor-reported estimates are 2.18 for 0.05% VOS, 1.78 for 0.10% VOS, and 2.41 for 0.20% VOS. Their confidence intervals include 1. The registry record identifies the method as logistic regression but does not report model covariates, coding choices, or other details needed for full reproduction.

What does an unadjusted recalculation mean?

The recalculated comparisons use the posted summary counts and denominators to form simple, unadjusted comparisons with vehicle. In general, an unadjusted comparison does not account for other participant characteristics or model terms. It can help readers understand the scale and uncertainty of the group contrast, but it may not match the trial’s prespecified analysis. The registry record does not report the full statistical analysis plan, so it is not possible to determine from the record whether the sponsor’s model included adjustments or whether the posted analyses were the complete planned set.

How should p-values be read?

In general, a p-value measures how unusual the observed data, or more extreme data, would be under a specified null model and analysis. It does not measure the probability that the null hypothesis is true, the size of an effect, or its clinical importance. The recalculated unadjusted p-values for the primary comparisons are 0.137, 0.285, and 0.098. These are above 0.05, but that threshold alone does not establish that the groups are the same. The estimates and their confidence intervals are essential to interpreting the results.

Why can over-dispersion matter?

Over-dispersion is a general issue for count models when observed variation exceeds what the model assumes. It can make standard errors too small if ignored. The primary endpoint is a participant-level binary outcome summarized as counts, rather than a repeated count of events per participant. The registry record does not describe an over-dispersion assessment or a count-model analysis, so no such analysis can be inferred. For this endpoint, the central statistical considerations are the binary outcome definition, the comparison between groups, uncertainty, and the analysis population.

These explanations describe general statistical concepts. They do not establish which exact model assumptions the trial used beyond the methods named in the registry record. The record does not report the prespecified multiplicity procedure, missing-data method, analysis code, or full model specification.

11. Confidence Intervals and Precision

The risk-difference confidence intervals are wide enough to include zero for each dose comparison. For 0.05% VOS, the estimate is 0.050 with a 95% confidence interval from -0.016 to 0.117. For 0.10% VOS, the estimate is 0.035 with an interval from -0.029 to 0.098. For 0.20% VOS, the estimate is 0.057 with an interval from -0.010 to 0.124. The point estimates are positive, but the intervals include negative values as well as positive ones.

In general, greater precision means a narrower confidence interval, while lower precision means a wider one. The intervals allow a range of plausible risk differences, so they do not pin down the size or direction of the underlying contrast with high precision. The counts meeting the endpoint are limited in each group, and sparse outcomes can contribute to uncertainty; this is a general statistical consideration, not a separate trial finding.

The sponsor’s logistic-regression intervals are also broad: 0.62 to 7.62, 0.49 to 6.45, and 0.70 to 8.30. They include an odds ratio of 1 and leave substantial uncertainty in the odds-ratio scale. Because odds ratios and risk differences use different scales, the numerical interval widths should not be compared directly as if they measured the same quantity.

Confidence intervals address sampling uncertainty under the method used. They do not resolve possible uncertainty from missing outcomes, outcome measurement, analysis choices, or applicability beyond the enrolled population. The registry record does not report enough information to quantify those other sources of uncertainty.

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 figures are planning illustrations based on the observed effect, not the trial’s original design assumptions. For these binary-outcome comparisons, the figures are participants per arm, not total participants or total events. The stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect targeted in each row is the stated fraction 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 gives the illustrative number of participants per arm for a design that would have an 80% chance of detecting the target effect under the stated assumptions, if that effect were the true effect and the assumptions held. The 90% power column gives the corresponding planning number for a 90% chance. These are prospective planning concepts, not descriptions of what happened in this completed trial.

Rows planning for a smaller fraction of the observed effect require more participants per arm. This occurs because smaller differences are harder to distinguish from random variation, all else being equal. The effect estimated in this study may not be the effect that would occur in a future study, so the illustrations should not be treated as guaranteed requirements. They also do not account for unreported design features such as loss to follow-up or the trial’s own analysis strategy. These figures are not observed power.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.050; treatment proportion p₁ = 0.100; average p̄ = 0.075.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.3720 = 0.7291.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.3703 = 0.3117.
4. n = (0.7291 + 0.3117)² / (0.0504)² = 426.2, rounded up to 427 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
p0 <- 0.0495867768595041                          # control proportion
p1 <- 0.1                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4147650)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 427 (80% power), 571 (90% power)
 75% of observed effect: n per arm = 700 (80% power), 936 (90% power)
 50% of observed effect: n per arm = 1,440 (80% power), 1,927 (90% power)
power.prop.test: 426.2 
Simulated power at n = 427 per arm: 0.812 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-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 reports sponsor analyses using logistic regression for each VOS dose versus vehicle. The reported odds ratios are 2.18 for 0.05% VOS, 1.78 for 0.10% VOS, and 2.41 for 0.20% VOS. Their 95% confidence intervals are 0.62 to 7.62, 0.49 to 6.45, and 0.70 to 8.30, with p-values of 0.135, 0.282, and 0.089.

The unadjusted recalculations use the posted counts and denominators to estimate risk differences, yielding 0.050, 0.035, and 0.057. These are not the same statistical measure as the sponsor’s odds ratios. The sponsor’s regression estimates may also reflect model details not reported in the registry record. Accordingly, the two sets of estimates should be compared by their direction and uncertainty, not by matching their numerical values.

Both sets of results leave uncertainty about the treatment-versus-vehicle contrasts: each sponsor-reported odds-ratio interval includes 1, and each recalculated risk-difference interval includes zero. The discrepancy flag is false. The registry record does not provide the full regression specification or enough detail to reproduce the sponsor analysis exactly.

15. Multiplicity, Missing Data and Analysis Populations

Three dose groups are compared with vehicle for the primary endpoint, and the registry also posts a secondary outcome. Considering multiple comparisons raises a general multiplicity issue: when several hypotheses are tested, the chance of at least one apparently significant result can increase. A prespecified strategy may control that risk through an adjustment, a testing hierarchy, or another method. The multiplicity strategy is not reported in the registry record, so the unadjusted p-values should not be read as if a documented family-wise testing plan were known.

The record identifies the primary population as modified intent-to-treat, but does not define exactly who was included in that population. It does not report the number of missing primary endpoint measurements, the method used to handle missing values, or whether sensitivity analyses assessed alternative assumptions. Missing data can affect both the numerator and denominator of a binary endpoint, depending on the analysis method. No particular handling method should be inferred from the posted counts.

The record also does not report the complete analysis plan, including the planned model specification, covariate adjustment, analysis of protocol deviations, or interim analyses. It identifies logistic regression for the sponsor’s primary analyses and ANCOVA for some secondary analyses, but does not provide the details required to evaluate every modeling choice. The registry record does not report the original sample-size justification or the assumptions used to plan the trial.

These omissions do not demonstrate that the trial failed to address multiplicity or missing data; they mean that the registry record does not document how those issues were addressed. The posted estimates remain interpretable as reported summaries, with appropriate caution about the limits of the available analysis information.

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: femur fracture (0.8%), myocardial infarction (0.8%), small intestinal obstruction (0.8%), head injury (0.8%), systemic inflammatory response syndrome (0.8%).

The registry lists serious adverse events for each group alongside the number at risk. The serious adverse event counts were 1 among 127 in the 0.05% VOS group, 3 among 126 in the 0.10% VOS group, 2 among 128 in the 0.20% VOS group, and 3 among 127 in the vehicle group. Deaths were 0, 1, 0, and 0 in those groups, respectively. These are descriptive counts from the posted safety results and are not adjusted comparisons.

The registry lists several serious adverse event terms at 0.8% each: femur fracture, myocardial infarction, small intestinal obstruction, head injury, systemic inflammatory response syndrome, and appendicitis. The record does not provide enough context in this listing to establish causality or compare the risk of a particular event between groups.

Serious adverse event counts are not a complete assessment of safety. The record also lists other adverse events, but the figures alone do not establish whether an event was caused by treatment. The registry record does not report the adjudication process, exposure-adjusted rates, or a full narrative account of each event.

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

The posted primary results show that the number meeting the Week 4 Schirmer threshold was higher in each VOS group than in the vehicle group. The unadjusted risk-difference estimates are positive, but their confidence intervals all include zero. The sponsor’s logistic-regression intervals also include an odds ratio of 1. Taken together, the posted data do not provide a precise estimate that rules out no difference under these analyses.

This does not establish that the treatments and vehicle are equivalent, nor does it prove that a difference exists. A non-significant result is not proof of no effect. The intervals include a range of possible effects, and the registry record does not report a prespecified equivalence or non-inferiority framework. A conclusion of equivalence cannot be drawn from these comparisons alone.

The endpoint is a threshold-based measure of tear production in the study eye at 4 Weeks. It does not on its own describe all symptoms, functioning, longer-term outcomes, or every aspect of dry eye syndrome. The posted secondary eye-dryness measure adds a symptom-oriented outcome, but the record does not provide a broad clinical-importance threshold for interpreting changes in that measure.

The observed differences should not be interpreted as medical advice or as a recommendation for an individual. These trial results describe group-level outcomes in the enrolled study population, under the conditions recorded in the registry. Whether they apply to other populations, treatment schedules, or settings is not established by the registry record.

Overall, the results are best understood as uncertain estimates rather than a definitive answer about efficacy or safety. The registry record documents the trial design and selected outcomes, but important details about analysis plans, missing data, multiplicity, and model specifications are not reported.

18. Why This Trial Matters Statistically

This trial illustrates why an effect estimate and its uncertainty should be read together. The observed primary counts differ across groups, and the recalculated risk differences are positive, but confidence intervals include zero. Looking only at the direction of the point estimates would overlook how much uncertainty remains; looking only at whether a p-value crosses a threshold would discard information about effect size and compatible values.

It also shows why the statistical scale matters. The simple recalculations report risk differences, while the sponsor’s logistic-regression analyses report odds ratios. Both describe comparisons with vehicle, but they answer the comparison on different scales. Their values should not be interchanged or treated as numerically equivalent.

The endpoint definition matters too. Counting participants who cross a threshold is easy to communicate, but it compresses a continuous test result into a yes-or-no outcome. That choice can lose information about the size of individual changes. The secondary measure of eye dryness offers a different perspective, although its results do not eliminate uncertainty in the primary comparison.

Finally, registry reporting determines how much of the analysis can be independently evaluated. Details about multiplicity, missing data, the modified intent-to-treat definition, and the full model are not reported. Their absence from the registry record limits interpretation but does not establish that they were not considered in the study’s conduct.

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 registry record does not report the full protocol or statistical analysis plan. In particular, it does not define the modified intent-to-treat population in detail, describe how missing Week 4 outcomes were handled, or state whether sensitivity analyses were conducted. The exact enrollment process and reasons for any differences between enrollment and endpoint denominators are not reported.

The sponsor’s primary analyses are identified as logistic regression, but the model covariates and other specification details are not reported. The record also does not state how the multiple dose comparisons and secondary outcomes were handled as a family of tests. The unadjusted recalculations therefore provide a transparent descriptive comparison, but do not reproduce a complete prespecified analysis.

The primary endpoint is measured at 4 Weeks, while each treatment regimen is described over 12 weeks. The posted primary result does not establish the pattern of outcomes at other time points. The record does not report a formal dose-response analysis, and the observed estimates do not by themselves establish a monotonic dose pattern.

The secondary outcome is posted for the 0.05% and 0.10% sponsor comparisons, but no sponsor-reported analysis for the 0.20% comparison appears in the record. The reason is not reported. The registry lists safety counts, but does not provide enough context to make causal attribution or a complete comparative safety assessment. These limitations restrict what can be concluded from the registry record without implying that unreported analyses were not performed.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Dose Ranging Study to Assess the Efficacy and Safety of Voclosporin Ophthalmic Solution in Subjects With Dry Eye Syndrome — NCT04147650.
• Registry record last updated 2021-12-10; status last verified 2021-12.
• Results first posted 2021-12-10.
• 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

NCT04147650 is a completed randomized, double-masked, parallel-group, vehicle-controlled Phase 2/3 study of voclosporin ophthalmic solution for dry eye syndrome. It enrolled 508 participants and compared 0.05%, 0.10%, and 0.20% VOS with vehicle, administered in both eyes twice a day over 12 weeks.

The primary endpoint counted participants with at least a 10 mm increase from baseline in the Schirmer tear test at Week 4 in the study eye. The posted counts were 12 of 120, 10 of 119, 13 of 122, and 6 of 121 for the three VOS groups and vehicle, respectively. Recalculated risk-difference intervals include zero for all three comparisons. Sponsor-reported odds-ratio intervals include 1.

The registry also posts change in eye dryness as a secondary outcome and lists serious adverse events and deaths by group. Important analysis details, including the multiplicity strategy and missing-data methods, are not reported in the registry record.