Ocular Tolerability of Voclosporin Ophthalmic Solution Versus Restasis® in Subjects With Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Ocular Tolerability of Voclosporin Ophthalmic Solution Versus Restasis® in Subjects With Dry Eye Disease (NCT03597139), a randomized phase 2 study. The primary outcome is Change From Baseline in Drop Discomfort Post Dose Instillation on Day 1.

2. Clinical Question

The registry describes the study objective as evaluating tolerability, efficacy, and safety. The primary endpoint focuses on an immediate ocular symptom after instillation; it does not by itself cover all aspects of tolerability, efficacy, or safety. The posted results also include symptom assessments on Day 28, which provide information about selected symptoms over the treatment period. They do not replace the primary comparison or establish a conclusion about every aspect of the trial objective.

The comparison is between two active ophthalmic treatments, not between treatment and no treatment. Accordingly, the primary result addresses the relative difference in the specified discomfort measure between the assigned groups. It does not directly estimate how either treatment compares with no treatment or with another unstudied option.

3. Trial Design

This was a randomized, parallel-group phase 2 study. The registry lists single masking and describes the study as investigator-masked. It does not specify in the registry record which other people, if any, were masked. Random allocation is intended to make treatment assignment independent of participants’ characteristics on average, while masking can reduce the influence of expectations on care or assessment. Neither feature guarantees that all sources of bias are absent.

The assigned treatments were 0.2% voclosporin ophthalmic solution and 0.05% cyclosporine ophthalmic emulsion (Restasis®). Both were given twice daily in both eyes for 28 days. The comparator is an active treatment, so the study estimates a difference between these regimens under the trial conditions rather than a difference from placebo or no treatment.

The registry reports enrollment of 100. The primary outcome lists 51 participants in the voclosporin group and 49 in the comparator group. The stated primary analysis population is Intent to Treat. The registry record does not report the detailed rules used to define that population, the number contributing data at each assessment, or how missing outcome measurements were handled.

The trial started on 2018-08-13, had primary completion on 2018-11-09, and is listed as completed. The primary endpoint was assessed on Day 1, one minute after the first dose instillation. The posted secondary outcomes include symptom measures assessed on Day 28. These different assessment times answer different questions: the primary endpoint concerns immediate post-dose discomfort, while the later symptom measures describe changes at the end of the stated treatment period.

The registry record does not report the original sample-size justification, the assumptions used for the trial's design, or whether interim analyses were planned or performed. The planning illustrations associated with the posted summary results are separate calculations based on observed effects; they should not be read as documentation of the original design.

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

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Intent to Treat

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 Change From Baseline in Drop Discomfort Post Dose Instillation on Day 1, measured over 1-minute Post Dose 1 installation (Day 1).

The primary endpoint is change from baseline in drop discomfort after dose instillation on Day 1. The assessment was made one minute after the first dose. Participants rated discomfort using an individual symptom severity visual analog scale running from 0, meaning no discomfort, to 100, meaning maximal discomfort. The endpoint is continuous: it can represent a range of symptom severity rather than assigning each participant to a simple yes-or-no category.

Measuring change from baseline is intended to describe how the reported symptom shifts from a participant’s starting assessment. A post-dose assessment at a specified time is relevant to ocular tolerability because it captures discomfort close to instillation. It is a focused measure, however. It does not summarize all possible eye symptoms, the duration of any discomfort beyond the assessment time, or the complete experience of treatment over 28 days.

The registry identifies the analysis population as Intent to Treat and reports group means with standard deviations. The group summaries give mean values of 7.9 for voclosporin and 3.5 for the comparator. The posted endpoint description establishes the scale’s direction: larger scores indicate more discomfort. Interpretation of the between-group estimate therefore depends on that direction and on the stated contrast, voclosporin relative to the comparator.

This endpoint is one component of the broader stated objective, which includes tolerability, efficacy, and safety. It should not be treated as a complete measure of any of those domains. The registry record does not report a threshold defining a clinically important difference for this scale, so the statistical estimate alone cannot identify whether a particular difference would be important to participants.

7. Results Posted in the Registry

• Voclosporin Ophthalmic Solution (VOS): mean 7.90 versus 3.50 on control; difference 4.40 (95% CI -1.78 to 10.58), standardized effect d = 0.28; z-test p = 0.163.

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 Drop Discomfort Post Dose Instillation on Day 28

• 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:
  • Voclosporin Ophthalmic Solution (VOS): mean 11.80 versus 6.10 on control; difference 5.70 (95% CI -1.84 to 13.24), standardized effect d = 0.30; z-test p = 0.139.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voclosporin Ophthalmic Solution (VOS) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Burning/Stinging Post Dose Instillation on Day 28

• 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:
  • Voclosporin Ophthalmic Solution (VOS): mean -12.30 versus -20.10 on control; difference 7.80 (95% CI -3.71 to 19.31), standardized effect d = 0.26; z-test p = 0.184.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voclosporin Ophthalmic Solution (VOS) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Foreign Body Sensation Post Dose Instillation on Day 28

• 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:
  • Voclosporin Ophthalmic Solution (VOS): mean -19.70 versus -20.70 on control; difference 1.00 (95% CI -12.48 to 14.48), standardized effect d = 0.03; z-test p = 0.884.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Voclosporin Ophthalmic Solution (VOS) and the control. The interval gives the range of effects that remain compatible with the data.

The registry lists 11 posted secondary outcomes, including symptom assessments such as drop discomfort, burning or stinging, foreign body sensation, photophobia, eye pain, dryness, itching, and a total symptom score. Three secondary comparisons are detailed in the registry record: Day 28 drop discomfort, Day 28 burning or stinging, and foreign body sensation. Across those detailed summaries, the point estimates are not all in the same direction, and their confidence intervals include zero. The registry record does not support treating this subset as a complete account of every posted secondary result.

These assessments complement the primary result by describing selected symptoms at later or differently specified assessment times. The primary endpoint concerns drop discomfort one minute after the first dose on Day 1; Day 28 outcomes address a different time point and, for some measures, a different symptom. They therefore offer related but not interchangeable evidence. The secondary findings do not overturn or resolve the uncertainty in the primary comparison.

Multiple outcomes create a multiplicity issue: the more comparisons examined, the greater the opportunity for apparently notable results to occur by chance if each is interpreted in isolation. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for these outcomes. Unadjusted secondary p-values therefore carry less weight than a result from a clearly specified primary analysis, and should be considered exploratory rather than definitive. The registry record also does not give clinical-importance thresholds for these symptom measures, limiting interpretation of the size of the observed changes.

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

• Change From Baseline in Drop Discomfort Post Dose Instillation on Day 28
• Change From Baseline in Burning/Stinging Post Dose Instillation on Day 28
• Change From Baseline in Foreign Body Sensation Post Dose Instillation on Day 28
• Change From Baseline in Photophobia Post Dose Instillation on Day 28
• Change From Baseline in Eye Pain Post Dose Instillation on Day 28
• Change From Baseline in Eye Dryness Post Dose Instillation on Day 28
• Change From Baseline in Itching Post Dose Instillation on Day 28
• Change From Baseline in the Total of All Individual Symptom Severity Assessment Scores

9. Statistical Interpretation

10. Statistical Methods Explained

The methods reported for the primary comparison include a sponsor analysis using ANCOVA and an unadjusted recalculation based on posted group summaries. These methods answer related but not identical statistical questions. Reading them together requires attention to the estimate, its uncertainty, the scale’s direction, and the population and assessment time to which the result applies.

What does the mean difference represent?

The recalculated mean difference is defined as the voclosporin group mean minus the comparator group mean. For the primary endpoint, the estimate is 4.4 mm. A positive value means the observed average score was higher in the voclosporin group, and the scale description says a higher score indicates more discomfort. The difference is a contrast between group averages; it does not mean that every participant had a score change of that size. Individual experiences can vary around each group mean.

The posted group standard deviations are 17.95 for voclosporin and 13.3 for the comparator. A standard deviation describes the spread of participant-level observations around a group mean. It is not the uncertainty in the estimated mean itself, and it is not a confidence interval. A larger standard deviation indicates greater variation among observed scores, while the precision of the group comparison also depends on the amount of information available and the statistical method used.

Why is the confidence interval useful?

A confidence interval gives a range of values compatible with the data under the assumptions of the analysis. For the recalculated primary comparison, the 95% interval extends from -1.776 to 10.58 mm. This interval includes zero, a value representing no mean difference under the stated contrast. It also includes differences in either direction. The interval therefore communicates uncertainty about both the size and direction of the underlying difference.

A 95% confidence interval is not a statement that there is a 95% probability that the true effect is inside this particular interval. In general statistical terms, the confidence level describes the long-run coverage behavior of the interval procedure under its assumptions. The practical reading is that wider intervals leave more uncertainty about the possible effect sizes than narrower intervals. It is also important that statistical compatibility with zero does not demonstrate equivalence: an equivalence claim requires a defined margin and an appropriate design and analysis.

What does the p-value add?

The unadjusted p-value for the recalculated primary contrast is 0.163. In general, a p-value measures how unusual results at least as incompatible with a specified null hypothesis would be if that null hypothesis and the statistical model were correct. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. A p-value should be read alongside the estimate and confidence interval, not as a stand-alone verdict.

The sponsor-reported ANCOVA analysis gives p = 0.149. ANCOVA, or analysis of covariance, estimates a group difference while accounting for one or more covariates included in the model. The registry record identifies the method and reports the estimate, interval, and p-value, but does not report the covariates, model details, or other implementation choices. Those details cannot be inferred from the method label alone.

Why can the recalculation differ from ANCOVA?

The recalculation is a simple unadjusted comparison derived from the posted summary statistics. It does not reproduce an adjusted model. ANCOVA can account for baseline or other measured variables if they were included in the model, and its estimate and uncertainty can therefore differ from a comparison using only group-level means and standard deviations. The registry record does not state which covariates were included. The two estimates should be described according to their respective methods, not treated as interchangeable calculations.

The recalculated confidence interval and p-value are also based on the statistical assumptions used for the simple comparison. The sponsor’s reported analysis is the trial’s stated analysis. The registry record does not flag a discrepancy, but the sponsor analysis remains the relevant reported ANCOVA result. The recalculation is useful as a transparent, unadjusted check of the posted summaries; it is not a replacement for the sponsor's model.

What does standard deviation contribute?

For a continuous endpoint, a mean summarizes the average level, while the standard deviation describes the spread of observed scores. The comparison's uncertainty depends in part on this spread: more variability makes it harder to estimate a group difference precisely when the available sample is held fixed. In general, a measure of standardized effect expresses a mean difference relative to a measure of variability. Such measures can help describe scale-independent magnitude, but they do not determine clinical importance. The primary interpretation is clearest in the original scale units, where the endpoint is defined.

Statistical models also rely on assumptions about the data and analysis. The registry record identifies the endpoint as continuous and reports an ANCOVA analysis, but it does not report diagnostic checks, transformations, model assumptions, or a strategy for departures from those assumptions. No conclusions about those procedures can be drawn from the posted result alone.

How should the analysis population be understood?

The registry names Intent to Treat as the primary population. In general, an intention-to-treat approach analyzes participants according to their randomized assignment, regardless of adherence, which can preserve the benefit of randomization. The exact operational definition can vary, and the registry record does not provide its detailed rules. It also does not report how missing measurements were handled, whether all randomized participants contributed to each analysis, or whether sensitivity analyses were conducted. Those omissions matter because the analysis population and missing-data method can affect the estimate and its uncertainty.

Overall, the methods support a careful reading: use the reported ANCOVA as the registry’s own primary analysis, use the unadjusted recalculation as a separate summary-based comparison, and interpret both with their confidence intervals and the endpoint’s direction in mind. Neither a p-value nor a single estimate resolves questions about clinical importance, missing data, or the full set of outcomes.

11. Confidence Intervals and Precision

The primary recalculated mean difference is 4.4 mm, with a 95% confidence interval from -1.776 to 10.58 mm. The interval extends across zero, so it is compatible with no average difference as well as with differences in either direction. This is not a precise estimate of the direction or size of the underlying group contrast. The interval's endpoints also show that the data remain compatible with more than one potentially relevant magnitude; the registry record does not supply a clinical-importance threshold with which to judge those magnitudes.

The sponsor-reported ANCOVA estimate is 4.6, with a 95% confidence interval from -1.7 to 10.9. It likewise includes zero and allows for effects in either direction. The sponsor result and unadjusted recalculation have similar direction and broadly similar ranges, but their estimates are derived using different methods. Their similarity does not remove the uncertainty expressed by either interval.

In general, precision is reflected in the width of an interval: narrower intervals indicate less uncertainty about the estimated effect, while wider intervals leave a broader range of plausible values. Precision depends on the observed variability, available information, and the analysis method. A confidence interval does not show the distribution of individual participants' responses; it describes uncertainty about a group-level effect.

The secondary comparisons also have intervals that cross zero in the summaries reported in detail. This indicates uncertainty in those estimates too. Their intervals should be interpreted in light of the fact that multiple outcomes were assessed and no multiplicity adjustment is reported. A result that is not statistically distinguishable from zero is not evidence of equivalence, and an interval alone cannot establish whether a difference would matter to participants.

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 for 80% power and participants per arm for 90% power. They are not total sample sizes or total event counts. In general, power is the probability that a study will reject a specified null hypothesis under a particular assumed effect and analysis, if those assumptions hold. The 80% and 90% columns illustrate different target probabilities of detecting the stated effect under the planning assumptions; the higher target generally calls for a larger planned number of participants per arm.

The illustrations assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. The calculations are based on the observed effect and are planning illustrations, not the trial's original design assumptions. The original design assumptions and sample-size justification are not reported in the registry record. These figures are not observed power.

Rows describing planning for 100% of the observed effect use the observed effect as the hypothetical target. Rows for planning for 75% of the observed effect use a smaller target, and rows for planning for 50% use a still smaller target. Smaller effects are harder to distinguish from random variation, so detecting them under the same assumptions requires more participants per arm. This relationship is why the figures rise as the assumed effect becomes a smaller fraction of the observed effect.

The illustrations should be treated as conditional calculations, not as a recommendation for a future trial. They do not establish that the observed effect is the true effect, that the assumptions are realistic, or that a particular target is clinically important. The registry record does not report a clinically meaningful difference for the primary scale. Planning a study would require a justified target effect and a protocol-specific analysis plan, neither of which can be recovered from these illustrations alone.

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 = 4.400; pooled standard deviation σ = 15.844.
2. n = 2 × (1.96 + 0.842)² × 15.844² / 4.400² = 203.5, rounded up to 204 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 <- 4.4                      # observed difference in means
sigma <- 15.8438956892629                     # 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(3597139)
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 = 204 (80% power), 273 (90% power)
 75% of observed effect: n per arm = 362 (80% power), 485 (90% power)
 50% of observed effect: n per arm = 815 (80% power), 1,090 (90% power)
power.t.test: 204.5 
Simulated power at n = 204 per arm: 0.799 (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 reports an ANCOVA comparison of final values, with a mean difference of 4.6, a 95% confidence interval from -1.7 to 10.9, and p = 0.149. This is the sponsor's own reported analysis. The registry record does not report the covariates or further model specifications used in ANCOVA, so the adjustment cannot be reconstructed from the listed results.

The recalculated comparison uses the posted group means and standard deviations without adjustment. It gives a mean difference of 4.4 mm, a 95% confidence interval from -1.776 to 10.58 mm, and an unadjusted p-value of 0.163. The estimates are similar in direction and magnitude, but they are not the same calculation. An adjusted model can produce a different estimate and interval from a summary-based unadjusted comparison.

The registry record does not identify a discrepancy between the sponsor result and the recalculation. The sponsor analysis should be read as the study's reported analysis; the recalculation is supplementary context rather than a replacement. Both intervals include zero and both analyses leave uncertainty about the direction and size of the group difference. Neither result alone establishes equivalence or clinical importance.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary outcome and lists multiple secondary outcomes. However, the registry record does not report a multiplicity-control procedure, a testing hierarchy, or a prespecified strategy for interpreting the secondary comparisons as a family. When multiple hypotheses are tested, the chance of at least one apparently unusual result can increase if each is assessed separately at the same threshold. In general, adjustment or a prespecified hierarchy can help manage that issue. Without the reported plan, the unadjusted secondary results should not be treated as if each were an independent confirmatory test.

The record lists the primary analysis population as Intent to Treat, but does not give its operational definition. It also does not report how missing values were handled, the amount of missing outcome data at each time point, or whether participants with incomplete measurements were excluded or handled using a model-based method. Missingness can matter if the likelihood of an unavailable measurement is related to symptoms, treatment assignment, or other participant characteristics. The registry record does not provide enough information to assess that possibility.

The registry reports an ANCOVA method for the primary comparison but does not specify the covariates, model details, or assumption checks. It does not report whether a per-protocol or other analysis population was used as a sensitivity analysis. Nor does the record describe interim analyses or provide the original statistical analysis plan. These items are not reported in the registry record, so no claim can be made about whether they were planned or performed.

These reporting gaps do not invalidate the posted estimates, but they limit how fully the analysis can be evaluated. The primary result can be interpreted using the reported estimate, interval, and stated method, while uncertainty remains about missing-data handling and some model details. Secondary results deserve particular caution because the multiplicity approach is not reported.

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 3% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events in 0 participants in the voclosporin group and 0 participants in the comparator group. It reports 0 deaths in both groups. For other adverse events, the record lists 10 participants affected in the voclosporin group and 6 in the comparator group. These are the counts recorded in the safety summary, not estimates of the probability of harm attributable to a treatment.

The serious adverse event counts and the other adverse event counts are separate categories in the registry summary. A count of zero serious adverse events in these groups means none were recorded in that category in the posted results; it does not establish that serious events cannot occur. The record does not supply serious-event terms because none are listed. It also does not describe the types, severity, timing, duration, or treatment relatedness of the other adverse events in this summary.

Safety comparisons require attention to the scope of reporting and the period observed. The treatments were given for 28 days, and the record does not provide details needed to characterize risks beyond the reported counts. These figures should be read descriptively and should not be used alone to infer causation or make a broad safety comparison.

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

The primary finding is an estimated mean difference of 4.4 mm in Day 1 post-instillation drop discomfort, with the point estimate favoring a higher discomfort score in the voclosporin group because higher scores indicate more discomfort. The 95% confidence interval includes zero and extends in both directions. The sponsor-reported ANCOVA estimate is 4.6, with a confidence interval that also includes zero. The posted data therefore leave substantial uncertainty about the magnitude and direction of the between-group difference.

This result does not establish that the treatments are equivalent. Equivalence is a specific claim that differences fall within a justified margin, and the registry record does not report such a margin. It also does not establish that voclosporin is superior or inferior on the primary outcome. A point estimate alone is not sufficient to make either claim, particularly when the confidence interval includes zero.

The result also does not establish whether the estimated difference is clinically important. The endpoint is measured on a 0 to 100 scale, but the registry record does not report a minimal important difference or another threshold for interpreting clinical relevance. Statistical uncertainty and clinical importance are related questions, but they are not the same question.

The primary measure captures discomfort one minute after the first dose on Day 1. It does not describe every aspect of ocular tolerability throughout the 28-day treatment period. Secondary symptom assessments offer additional, but still selective, information. The registry's safety counts describe recorded events and do not by themselves establish treatment causation or fully characterize safety.

The findings apply to the randomized groups and outcomes reported in this phase 2 study. They do not answer how either regimen compares with no treatment, how results might differ in other populations, or what effects would occur over a longer period. Those questions are not resolved by the posted results.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical comparison should be read through its endpoint definition, estimate, and uncertainty together. The primary question is narrow and time-specific: reported discomfort one minute after the first dose on Day 1. Stating that detail prevents a result on immediate post-instillation symptoms from being mistaken for a broad judgment about treatment tolerability over the full course.

The study also demonstrates the distinction between a randomized comparison and proof of a particular treatment effect. Randomization provides a basis for comparing assigned groups, but the observed estimate remains uncertain. The confidence interval includes zero, so the posted primary data do not provide a precise estimate of the direction of the difference. A non-significant p-value is not evidence that the groups are identical, and a positive point estimate is not by itself evidence of a meaningful difference.

Comparison of the ANCOVA result with the unadjusted recalculation makes the role of method visible. The sponsor analysis is the reported trial analysis, while the recalculation is based on group summary statistics. Their estimates are close, yet each has its own assumptions and interpretation. This distinction is useful when evaluating trial results reconstructed from summary data.

Finally, the record lists several secondary outcomes but does not report how multiplicity was handled. That matters because isolated secondary results have a different evidential status from a prespecified primary analysis. The study therefore offers a practical example of why endpoint hierarchy, analysis details, missing-data reporting, and clinical-importance thresholds are important parts of statistical interpretation, not administrative details.

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 leaves several trial-specific limitations in the public statistical description. It does not report the original sample-size justification or design assumptions, so the enrollment cannot be assessed against a documented target effect or planned precision. The separate planning illustrations use observed effects and should not be mistaken for the trial's original design calculations.

The outcome is a self-reported discomfort rating assessed at a defined time after instillation. That focus is relevant to immediate discomfort but captures only one aspect of ocular tolerability. The primary assessment is on Day 1, whereas treatment continued for 28 days; the registry record does not provide a primary endpoint measuring the entire treatment period. The record also does not report a clinical-importance threshold for the scale.

The registry lists single masking and describes the study as investigator-masked, but does not say which other parties were masked. It reports ANCOVA without identifying covariates or further model details. It does not report missing-data procedures, outcome-specific completeness, sensitivity analyses, or a multiplicity strategy. These omissions limit assessment of robustness, particularly for secondary outcomes.

The safety summary provides counts for serious adverse events, other adverse events, and deaths, but the record does not give detailed event terms or the characteristics needed to evaluate timing, severity, or attribution for the other adverse events. The study is phase 2 and the reported treatment period is 28 days; the registry results therefore do not establish longer-term safety or address outcomes beyond those posted.

These limitations define what can be concluded from the registry record. They do not show that a particular method was absent; they mean the relevant details are not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Ocular Tolerability of Voclosporin Ophthalmic Solution Versus Restasis® in Subjects With Dry Eye Disease — NCT03597139.
• Registry record last updated 2021-07-08; status last verified 2021-05.
• Results first posted 2021-07-08.
• 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 NCT03597139, a completed randomized, parallel-group phase 2 study comparing 0.2% voclosporin ophthalmic solution with 0.05% cyclosporine ophthalmic emulsion (Restasis®) in subjects with mild to moderate dry eye disease. Both regimens were given twice daily in both eyes for 28 days. The study is listed as single-masked and investigator-masked.

The primary outcome was change from baseline in drop discomfort one minute after the first dose on Day 1, assessed on a 0 to 100 visual analog scale. The posted unadjusted recalculation estimates a mean difference of 4.4 mm, with a 95% confidence interval from -1.776 to 10.58 mm. The sponsor-reported ANCOVA estimate is 4.6, with a 95% confidence interval from -1.7 to 10.9. Both intervals include zero. The record also lists Day 28 symptom outcomes and safety counts, with no serious adverse events or deaths reported in either group.

The registry record does not report the original sample-size justification, multiplicity approach, detailed missing-data procedures, or a clinical-importance threshold for the symptom scale. The results should therefore be interpreted as estimates for the reported outcomes and analysis, with uncertainty about their clinical importance and some analysis details.