Study of VVN001 Ophthalmic Solution in Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of VVN001 Ophthalmic Solution in Dry Eye Disease (NCT04556838), a randomized phase 2 study. The primary outcome is Inferior Corneal Fluorescein Staining.

2. Clinical Question

The trial was designed to evaluate safety and tolerability and explore efficacy activity. Its primary outcome was a continuous score, so the central comparison concerns average change between randomized groups, not the proportion of subjects who crossed a threshold. The posted results give group means and standard deviations, together with recalculated unadjusted comparisons against vehicle. They do not give a sponsor-reported analysis for the primary outcome.

The registry record also lists total and regional corneal fluorescein staining and eye dryness as secondary outcomes, each assessed at Day 84. These measures add context but do not replace the prespecified primary question. The record does not report the protocol’s definition of a clinically important difference or the criteria used to judge an individual response. Consequently, the statistical comparisons describe differences in group averages and their uncertainty; they do not, by themselves, establish the clinical importance of a difference.

3. Trial Design

This was a Phase 2a, randomized, vehicle-controlled, parallel-group trial of VVN001 ophthalmic solution in subjects with dry eye disease. The registry describes the study as multicenter and double-masked. Its masking classification is quadruple, and the official title describes the trial as double-masked; the registry record does not explain the relationship between those labels or identify which groups of people were masked.

The randomized arms were VVN001 1%, VVN001 5%, and vehicle. The trial record lists enrollment of 169. For the primary outcome, the posted group summaries are based on subjects evaluable at Day 84: 54 in the 1% arm, 53 in the 5% arm, and 51 in the vehicle arm. These endpoint sample sizes need not represent the full enrollment, and the record does not describe the reasons subjects were not evaluable for this measure.

The primary outcome was mean change from baseline in inferior corneal fluorescein staining at Day 84. Total corneal fluorescein staining, regional corneal fluorescein staining, and eye dryness were listed as secondary outcomes at the same timeframe. The record classifies these outcomes as continuous measures reported as means with standard deviations.

The study started on 2020-12-03, reached primary completion on 2021-12-01, and is recorded as completed. VivaVision Biotech, Inc is listed as the sponsor. The registry record does not report the original sample-size justification, detailed allocation procedures, analysis populations beyond the primary endpoint description, or the statistical analysis plan. Those omissions limit what can be inferred about the intended analysis and how closely the posted summaries reflect it.

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: Sample size reflects number of subjects evaluable at Day 84

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 Inferior Corneal Fluorescein Staining, measured over Day 84.

The primary endpoint is mean change from baseline in inferior corneal fluorescein staining at Day 84. It is reported as a score on a scale, with a mean and standard deviation for each randomized arm. The endpoint description states that negative change indicates improvement and that, depending on an individual subject’s baseline, the measure can range from -4 to +4.

Fluorescein staining is used to assess staining of the corneal surface. As a general statistical and clinical concept, a continuous measure can capture variation across a range of scores rather than reducing outcomes to a yes-or-no category. Comparing average changes can therefore describe whether groups moved in different directions and the size of the group-level separation. It does not show how every subject changed, and an average difference does not tell how many individuals experienced a particular level of change.

The comparison is based on change from baseline, rather than only the Day 84 score. This focuses the outcome on the observed shift over the study period. The registry record does not report a threshold for a clinically meaningful change, nor does it explain how baseline values were incorporated into the analysis beyond the endpoint’s stated change-from-baseline definition. The result should therefore be read as a difference in mean score change, with its uncertainty, rather than as a direct measure of individual benefit.

7. Results Posted in the Registry

• VVN001, 1%: mean -0.69 versus -0.72 on control; difference 0.03 (95% CI -0.28 to 0.34), standardized effect d = 0.04; z-test p = 0.848.
• VVN001, 5%: mean -0.97 versus -0.72 on control; difference -0.25 (95% CI -0.57 to 0.07), standardized effect d = -0.30; z-test p = 0.120.

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.

Total Corneal Fluorescein Staining

• 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:
  • VVN001, 1%: mean -1.75 versus -0.79 on control; difference -0.96 (95% CI -2.02 to 0.10), standardized effect d = -0.35; z-test p = 0.077.
  • VVN001, 5%: mean -2.60 versus -0.79 on control; difference -1.81 (95% CI -3.03 to -0.59), standardized effect d = -0.57; z-test p = 0.004.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VVN001, 1% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for VVN001, 5% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Regional Corneal Fluorescein Staining

• 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:
  • VVN001, 1%: mean -0.20 versus -0.11 on control; difference -0.09 (95% CI -0.39 to 0.21), standardized effect d = -0.12; z-test p = 0.558.
  • VVN001, 5%: mean -0.52 versus -0.11 on control; difference -0.41 (95% CI -0.74 to -0.08), standardized effect d = -0.48; z-test p = 0.014.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VVN001, 1% and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for VVN001, 5% than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

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:
  • VVN001, 1%: mean -28.70 versus -19.90 on control; difference -8.80 (95% CI -19.65 to 2.05), standardized effect d = -0.31; z-test p = 0.112.
  • VVN001, 5%: mean -22.20 versus -19.90 on control; difference -2.30 (95% CI -12.69 to 8.09), standardized effect d = -0.09; z-test p = 0.664.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between VVN001, 1% 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 VVN001, 5% and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the pattern is mixed rather than uniform across measures and concentrations. Some recalculated comparisons have estimates in a direction favoring a larger decrease in the VVN001 arm, while others are close to zero or have intervals that include differences in either direction. The secondary outcomes therefore add descriptive context but do not yield one consistent pattern that can be read independently of the primary result.

The secondary measures are related to the primary endpoint because they include other corneal fluorescein staining summaries, as well as eye dryness. They are not interchangeable with inferior corneal staining: each captures a different measure, and their observed variability and scales differ. A result on a secondary endpoint does not change the numerical primary comparison or resolve the uncertainty in its confidence intervals. In particular, secondary findings should not be treated as confirmation of the primary outcome when the primary contrasts themselves remain uncertain.

The registry record lists three secondary outcomes and gives recalculated unadjusted comparisons, but it contains no reported analyses for those outcomes. Without a reported analysis plan or multiplicity procedure, the nominal p-values do not account for the number of comparisons examined. When several hypotheses are tested, the chance of observing at least one apparently small p-value by chance increases. This is a general statistical concern, not proof that any particular secondary finding is spurious.

For that reason, the secondary results carry less weight than a prespecified, multiplicity-controlled confirmatory analysis would carry. Their most defensible role is to describe the overall pattern and indicate areas that might warrant evaluation in a study designed around a clearly specified hypothesis. The registry record does not establish whether the secondary analyses were planned as confirmatory or exploratory, and that status is not reported in the registry record.

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

• Total Corneal Fluorescein Staining
• Regional Corneal Fluorescein Staining
• Eye Dryness

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous and summarized by a mean and standard deviation for each arm. A mean describes the group’s average change, while the standard deviation describes how spread out the individual measurements are around that average. These summaries are useful for understanding the location and variability of the observed scores, but they do not reveal the full distribution or the experience of each subject.

What does the mean difference represent?

The recalculated mean difference compares each VVN001 arm with vehicle. It is formed from the difference between the two posted group means, with the VVN001 arm compared against the vehicle arm. For the primary endpoint, a negative difference means the VVN001 group had a more negative average change than vehicle; a positive difference means its average change was less negative. Because the endpoint description says negative change indicates improvement, the direction of this difference can be interpreted relative to that sign convention. A difference remains a group-average contrast, not a statement about every subject.

The observed primary mean differences are 0.03 for VVN001 1% versus vehicle and -0.25 for VVN001 5% versus vehicle. These are simple unadjusted recalculations from posted means and standard deviations. They should be distinguished from an analysis that might adjust for baseline values, account for repeated measurements, or use other variables. The registry record does not report an adjusted primary analysis or the statistical model used by the sponsor.

How should the confidence interval and p-value be read?

A confidence interval gives a range of values compatible with the observed data under the calculation’s assumptions. In general, a narrower interval indicates greater precision, while a wider interval indicates more uncertainty about the size and direction of the difference. For the primary comparisons, both intervals include zero, the value corresponding to no mean difference. This means the recalculated intervals do not rule out no difference at the conventional interpretation of the interval.

A p-value describes how unusual results at least as incompatible with a null hypothesis would be under that hypothesis and the statistical assumptions. It is not the probability that the null hypothesis is true, and it does not measure the magnitude or clinical importance of an effect. The unadjusted p-values are 0.848 for VVN001 1% and 0.12 for VVN001 5%. These values are not substitutes for examining the estimates and their confidence intervals. The registry record does not report a sponsor-conducted analysis corresponding to these recalculated comparisons.

Why do standard deviations and sample sizes matter?

The precision of a comparison depends in part on the amount of variation in the outcome and the amount of information in each group. Greater variability makes it harder to distinguish a group difference from random variation, all else being equal. The primary standard deviations were 0.77, 0.81, and 0.83 in the VVN001 1%, VVN001 5%, and vehicle arms, respectively. The evaluable group sizes were 54, 53, and 51. These are the endpoint-specific counts, not a replacement for the registry’s overall enrollment figure.

As a general statistical concept, random assignment supports comparison between groups by reducing systematic differences at assignment, but it cannot eliminate chance imbalance or uncertainty. Masking can reduce the influence of expectations on outcome assessment or conduct, although the registry record does not describe how masking was implemented. Neither design feature removes the need to examine missing outcome data, analysis decisions, and the precision of the estimates.

What does “unadjusted” mean in this context?

The comparisons do not account for multiplicity across the several outcomes and treatment contrasts. They also do not incorporate a stated adjustment for baseline values or other covariates. The posted data support transparent arithmetic comparisons of group summaries, but they cannot reproduce a more complex sponsor analysis that is not reported. Since the record indicates no posted analyses, the recalculated estimates should be interpreted as descriptive statistical comparisons rather than as a reconstruction of the trial’s full planned analysis.

There are three secondary outcomes and two VVN001-versus-vehicle comparisons for each outcome, in addition to the two primary comparisons. Testing several hypotheses increases the opportunity for some apparently notable results to arise by chance. General methods for addressing this include prespecifying a hierarchy or adjusting the threshold for multiple testing. The registry record does not report a multiplicity procedure, so the unadjusted secondary p-values should be treated as exploratory rather than as confirmatory findings.

11. Confidence Intervals and Precision

Precision is best judged by reading the estimated difference together with its confidence interval, not by looking at the group means or p-value alone. For VVN001 1% versus vehicle, the primary estimate is 0.03 and its interval runs from -0.277 to 0.337. The interval spans zero and includes differences in both directions. For VVN001 5% versus vehicle, the estimate is -0.25 and the interval runs from -0.565 to 0.065. This interval also spans zero, although its point estimate is more negative.

The intervals do not establish that the true difference is exactly zero. Rather, they show that the posted summaries are compatible with a range of possible differences, including no difference. The interval for the 5% contrast also includes a positive value, so the data do not settle the direction of the population difference. The 1% estimate is close to zero, but its interval likewise allows differences on either side of zero.

Standard deviations in the three primary groups range from 0.77 to 0.83, while endpoint-evaluable group sizes range from 51 to 54. These quantities help explain why precision is limited: group averages are estimated from a modest number of observations in the presence of individual variation. A confidence interval reflects this uncertainty, but it does not account for unreported issues such as missing-data assumptions or multiplicity adjustments.

The confidence intervals discussed are from simple recalculations using the posted summaries. The registry record does not report sponsor-generated confidence intervals or a model-based primary analysis. The stated bounds should therefore be understood as unadjusted estimates under the recalculation, rather than as a complete representation of every uncertainty in the trial.

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 events. They are illustrative calculations based on the observed effect, not the trial’s original design calculation. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, a normal approximation, and an effect to detect equal to the stated fraction of the observed effect. The registry record does not report the trial’s own original sample-size assumptions or justification.

The 80% power column gives the participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions, if that effect were the true difference. The 90% power column gives the corresponding planning number for a 90% chance. These are target design characteristics, not statements about what happened in the trial.

Rows for 100%, 75%, and 50% of the observed effect illustrate how the calculated requirement changes as the assumed effect becomes smaller. A smaller effect is harder to distinguish from random variation, so more participants per arm are needed to reach the same planned power, all else being equal. These illustrations use the observed effect as their anchor, which may not represent the effect in a future study.

This is not observed power. The figures are prospective planning illustrations and should not be used to infer the probability that the trial’s result is correct or to replace interpretation of the confidence intervals. Planning calculations also do not address missing data, departures from the stated assumptions, or adjustment for multiple outcomes unless those features are explicitly incorporated. The registry record does not report that these illustrations were the sample-size method used to design the trial.

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 = 0.030; pooled standard deviation σ = 0.800.
2. n = 2 × (1.96 + 0.842)² × 0.800² / 0.030² = 11,154.2, rounded up to 11,155 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 <- 0.03                      # observed difference in means
sigma <- 0.799688653006639                     # 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(4556838)
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 = 11,155 (80% power), 14,933 (90% power)
 75% of observed effect: n per arm = 19,830 (80% power), 26,547 (90% power)
 50% of observed effect: n per arm = 44,617 (80% power), 59,730 (90% power)
power.t.test: 11155.1 
Simulated power at n = 11,155 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. Multiplicity, Missing Data and Analysis Populations

The posted results include a primary endpoint, three secondary outcomes, and comparisons of each VVN001 concentration with vehicle. Considering multiple endpoints and contrasts creates a multiplicity issue: even when no treatment differences exist, testing many hypotheses can produce some small p-values by chance. This is a general statistical property of repeated testing.

The comparisons described in the statistical interpretation are unadjusted recalculations. The registry record does not report a multiplicity adjustment, a testing hierarchy, or a strategy for controlling the overall type I error across outcomes and contrasts. The unadjusted p-values should therefore be read as nominal evidence for individual comparisons, not as evidence that the full family of comparisons meets a prespecified error-control standard. No sponsor-reported analyses are listed in the record, so the sponsor’s handling of multiplicity is not reported in the registry record.

Missing-data handling is also not reported in the registry record. The primary outcome description says that the sample size reflects subjects evaluable at Day 84, and the posted endpoint counts are smaller than the overall enrollment. The record does not explain why some subjects were not evaluable, whether missing values were imputed, or whether sensitivity analyses assessed how missingness could affect the results. Those details matter because an analysis restricted to observed endpoint values can be influenced if outcome availability is related to treatment assignment or to the outcome itself.

The record does not report whether the primary analysis used an intention-to-treat, modified intention-to-treat, per-protocol, or other analysis population. It identifies the evaluable Day 84 sample for the primary outcome, but that description alone does not define the full analysis set or establish the handling of randomized subjects who lacked an endpoint measurement. The original analysis plan, model specification, interim analyses, and sample-size justification are not reported in the registry record.

Randomization and masking are features of the trial design, but they do not answer these analysis questions. Without the missing details, the recalculated results remain useful for describing posted group summaries, while their correspondence to any planned inferential analysis cannot be assessed.

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 2% reporting threshold.

Most frequent non-serious adverse event terms

The registry lists serious adverse events for groups described as at risk: 56 in the VVN001 1% arm, 57 in the VVN001 5% arm, and 56 in the vehicle arm. The posted number affected by serious adverse events is 0 in each group. Deaths are also reported as 0 in each group. No serious adverse event terms are listed.

These counts indicate what was recorded in the registry for the stated groups and period; they do not establish that no other safety events occurred. For other adverse events, the posted affected counts are 3 for VVN001 1%, 6 for VVN001 5%, and 2 for vehicle, using the corresponding groups at risk. The record does not provide event descriptions in the listed safety summary, severity, timing, or an analysis comparing event rates.

Safety counts should be read separately from the efficacy comparisons. The groups at risk for these safety summaries differ from the endpoint-evaluable counts used for the primary outcome. The registry record does not report further details about event collection or attribution, so these figures provide a limited summary rather than a complete account of safety.

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

The primary results describe mean change in inferior corneal fluorescein staining at Day 84 among subjects evaluable for that outcome. All three group means were negative, which the endpoint description identifies as the direction of improvement. The relevant contrasts with vehicle were small in the 1% arm and more negative in the 5% arm, but both unadjusted confidence intervals included zero. Thus, the posted summaries do not precisely establish the size or direction of a difference between either VVN001 concentration and vehicle.

That interpretation is not equivalent to saying that the treatments have no effect. An interval that includes zero can arise when the data are compatible with no difference and with some differences in either direction. Conversely, a negative point estimate does not establish a reliable or clinically important difference. The registry record does not report a threshold for clinical importance, and the recalculated comparisons are not adjusted analyses reported by the sponsor.

The secondary outcomes provide additional observations, but they involve multiple measures and contrasts and are not accompanied by a reported multiplicity plan. They should be treated as exploratory context rather than as independent confirmation of the primary result. Safety counts show no serious adverse events or deaths listed in the registry groups, alongside posted counts for other adverse events; these summaries are not a complete description of all safety information.

The study is recorded as a completed Phase 2a trial with enrollment of 169. Its findings describe the posted results for this study and its Day 84 measures. They do not establish what would be observed in other populations, over other timeframes, or under a different analysis. The registry record does not report the original statistical plan, missing-data methods, or sponsor analyses needed to assess those questions in greater detail.

17. Why This Trial Matters Statistically

This trial illustrates why a group mean alone is not enough to interpret a clinical comparison. Each arm had a negative mean change in the primary staining score, but the relevant question is whether the change differed between a VVN001 arm and vehicle. The point estimates, uncertainty intervals, and endpoint sign convention must be considered together to understand what the posted data can support.

It also shows the distinction between an observed estimate and the precision of that estimate. The 5% primary comparison has a negative point estimate, yet its interval crosses zero. The estimate’s direction is not the same as certainty about the population difference. Similarly, the 1% estimate is close to zero, but its interval still allows differences on both sides of zero. These examples help explain why statistical interpretation should not reduce to a threshold based on a p-value.

The record also makes the limits of registry reporting visible. Endpoint-evaluable sample sizes are reported, but missing-data methods and the analysis population are not. Several secondary comparisons appear, but a multiplicity plan is not reported. Recalculations from summary statistics can make group contrasts easier to interpret, while remaining distinct from the sponsor’s full analysis, which is not posted.

Finally, the planning illustrations show how assumed effect size and target power relate to participant requirements. They are useful for understanding design trade-offs, but they are not a measure of the strength of evidence in the completed trial. Taken together, these features make the study a useful example of reading estimates, intervals, design information, and reporting gaps as parts of one statistical interpretation.

18. Limitations

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

The primary endpoint summaries are based on subjects evaluable at Day 84, while overall enrollment is listed separately. The registry record does not report why some enrolled subjects lack an evaluable primary outcome, how missing data were handled, or whether any sensitivity analyses were performed. This leaves uncertainty about how well the posted endpoint summaries represent all randomized subjects.

The posted comparisons are unadjusted recalculations from group summary statistics. The registry record lists no reported analyses, so it does not provide a sponsor-reported model, adjusted estimate, or analysis plan against which to compare the simple contrasts. The record also does not report a multiplicity strategy for the primary and secondary comparisons. These limitations are especially relevant to interpretation of the secondary outcomes.

The primary endpoint description supplies a scale range that can vary depending on baseline, but the registry record does not give a clinical-importance threshold or explain how baseline values were handled in an inferential model. The summary statistics do not show the distribution of individual outcomes or the number of subjects whose measurements changed by a particular amount. The trial’s original sample-size justification and statistical assumptions are not reported; the planning figures are illustrative calculations based on observed effects, not evidence of the original design rationale.

The registry describes the study as both double-masked in its official title and quadruple-masked in its masking classification, without clarifying the masking roles. Safety reporting is limited to the posted affected counts and does not include details on event type, severity, timing, or attribution. These reporting gaps constrain interpretation beyond the specific summaries available for this trial.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: Study of VVN001 Ophthalmic Solution in Dry Eye Disease — NCT04556838.
• Registry record last updated 2023-12-13; status last verified 2023-12.
• Results first posted 2023-02-28.
• 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

NCT04556838, titled “Study of VVN001 Ophthalmic Solution in Dry Eye Disease,” is recorded as a completed Phase 2a randomized, vehicle-controlled, parallel-group trial sponsored by VivaVision Biotech, Inc. The study enrolled 169 subjects and evaluated VVN001 ophthalmic solution at 1% and 5% against vehicle. The record describes the study as multicenter and double-masked, and classifies masking as quadruple.

The primary outcome was mean change from baseline in inferior corneal fluorescein staining at Day 84, with negative change indicating improvement. The posted primary comparisons are recalculated and unadjusted; both confidence intervals include zero. The record lists total and regional corneal fluorescein staining and eye dryness as secondary outcomes. It also reports no serious adverse events or deaths in the listed groups, with other adverse event affected counts reported by arm.

The registry record does not report sponsor analyses, a multiplicity plan, missing-data methods, or the original sample-size justification. Those omissions limit conclusions about the intended analysis and the broader interpretation of the results.