The RENEW Trial: A Multi-Center, Randomized, Double-Masked, Parallel-Group, Vehicle-Controlled, Adaptive Phase 3 Clinical Trial to Assess the Safety and Efficacy of Subjects With Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for The RENEW Trial: A Multi-Center, Randomized, Double-Masked, Parallel-Group, Vehicle-Controlled, Adaptive Phase 3 Clinical Trial to Assess the Safety and Efficacy of Subjects With Dry Eye Disease (NCT03879863), a randomized phase 3 study. The primary outcome is Subject-reported Ocular Dryness Score (0 - 100 Visual Analogue Scale (VAS)).

2. Clinical Question

The key statistical issue is how to interpret the differences in change scores alongside their uncertainty. The reported reproxalap-versus-vehicle comparisons have confidence intervals that include zero. The registry also lists a difference between the two vehicle schedules, with a confidence interval that does not include zero. These comparisons are not interchangeable with the trial’s stated mixed model analysis: the approximate unadjusted recalculations use posted arm summaries and do not reproduce the repeated-measures model.

3. Trial Design

RENEW is recorded as a completed, randomized, phase 3 trial with a parallel-group model and vehicle control. Its title describes a multicenter study. The registry reports overall enrollment of 422, with a start date of 2019-04-16 and primary completion on 2019-10-04. The trial title calls it double-masked, while the registry’s masking classification is triple. The record does not explain this difference.

Four intervention groups are listed: reproxalap ophthalmic solution (0.25%) QID, vehicle QID, reproxalap QID to BID, and vehicle QID to BID. Efficacy summaries are available for all four groups. The registry reports 85.0, 86.0, 85.0, and 85.0 participants, respectively, in the primary outcome summaries. Adverse-event summaries use different at-risk group sizes: 105, 106, 105, and 106, respectively. These are outcome-specific reported counts; the record does not explain the difference between the efficacy and safety group sizes.

The primary endpoint description says the intervention was administered bilaterally and identifies an Intent-to-treat Ocular Dryness Population with observed data only. The analysis used a mixed model repeated measures approach for change from baseline, with baseline score, treatment arm, visit, and treatment-arm-by-visit interaction as fixed effects. The registry lists an efficacy assessment period from Day 1 through 85, with specified assessments at Weeks 1, 2, 4, 6, 8, 10, and 12. Further operational details of the dosing schedules and the trial’s original design assumptions are not reported in the registry record.

Although the trial title describes the study as adaptive, the record does not report the adaptive features, any interim analyses, or how adaptations were governed. The sample-size planning illustrations associated with the posted summaries are not the trial’s original design calculation. The original sample-size justification and its assumptions are not reported in the registry record.

4. Participant Flow and Accounting

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

Overall Study

Analysis population for the primary outcome, as defined in the registry: Intent-to-treat Ocular Dryness Population with observed data only

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 Subject-reported Ocular Dryness Score (0 - 100 Visual Analogue Scale (VAS)), measured over The efficacy assessment period (Day 1 through 85) was assessed at Weeks 1, 2, 4, 6, 8, 10, and 12; baseline was Day 1..

The primary endpoint is change from baseline in subject-reported ocular dryness, measured on a 0 - 100 Visual Analogue Scale. A score of 0 represents no discomfort and 100 represents maximal discomfort; higher scores indicate a worse outcome. A change score describes how the reported score differed from the baseline assessment. In the posted group summaries, negative changes indicate lower scores compared with baseline, but the summary alone does not describe each participant’s experience or the pattern of change over time.

Patient-reported symptom measures are used to capture a participant’s own assessment of discomfort. Such scores can be analyzed as continuous measurements, allowing a mean change and a difference in mean change to be estimated. The registry reports least-squares means with standard errors from a mixed model repeated measures analysis. This model accounts for the repeated visit structure using fixed effects for baseline score, treatment arm, visit, and the interaction between arm and visit.

The assessment period ran from Day 1 through 85, with outcome assessments at Weeks 1, 2, 4, 6, 8, 10, and 12; baseline was Day 1. The listed endpoint is therefore tied to repeated assessments over a defined period rather than a single isolated measurement. The registry does not provide a separate visit-specific result in the posted primary summary. It also does not report a threshold for interpreting a change as important to participants. Statistical differences in scores should not, by themselves, be treated as a measure of clinical importance.

7. Results Posted in the Registry

• Reproxalap Ophthalmic Solution (0.25%) QID: mean -11.50 versus -15.00 on control; difference 3.50 (95% CI -3.19 to 10.19), standardized effect d = 0.16; z-test p = 0.305.
• Reproxalap Ophthalmic Solution (0.25%) QID to BID: mean -17.80 versus -15.00 on control; difference -2.80 (95% CI -9.17 to 3.57), standardized effect d = -0.13; z-test p = 0.389.
• Vehicle Ophthalmic Solution QID to BID: mean -6.80 versus -15.00 on control; difference 8.20 (95% CI 1.94 to 14.46), standardized effect d = 0.39; z-test p = 0.010.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it is a score on a 0 - 100 scale. A mean summarizes the central value of a group’s measurements, while a change from baseline describes the difference between a follow-up score and the baseline score. The registry reports least-squares means rather than only raw arithmetic means. In general, least-squares means are model-based estimates that account for the terms included in the specified statistical model.

Why use repeated-measures analysis?

Participants were assessed at multiple visits, so measurements from the same person are related rather than independent. A mixed model repeated measures analysis is a general approach for analyzing such data. It can use the pattern of repeated observations and estimate treatment and visit effects within one framework. The registry says its model included baseline score, treatment arm, visit, and the interaction between treatment arm and visit as fixed effects. The interaction allows the modeled arm contrast to vary by visit. The record does not give the covariance structure, estimation method, degrees of freedom method, or model diagnostics, so those details cannot be evaluated from the registry entry.

The endpoint description reports least-squares mean changes with standard errors. A standard error describes the statistical uncertainty in an estimated mean; it is not the spread of individual participants’ scores. A confidence interval expresses a range of values compatible with the estimate and its uncertainty under the model or calculation used. A narrower interval is more precise than a wider interval, all else equal. The registry does not post arm-level confidence limits for the least-squares means, but it does list intervals for the approximate pairwise comparisons.

What do the pairwise contrasts represent?

The approximate unadjusted comparisons are based on posted arm means and standard errors. The mean difference is oriented as the named comparison group’s mean minus the vehicle QID mean. For the QID reproxalap contrast, the means are -11.5 and -15.0 and the difference is 3.5. For the QID-to-BID reproxalap contrast, the means are -17.8 and -15.0 and the difference is -2.8. The vehicle QID-to-BID comparison uses -6.8 and -15.0 and gives 8.2. These are the posted comparison values; they are not additional calculations in this explanation.

The recalculated pooled standard deviations are marked approximate because the arm summaries provide standard errors rather than individual-level variability. Converting summary uncertainty to an estimate of spread requires assumptions, and a simple pooled estimate does not account for the repeated-measures model’s structure. This is why the approximate unadjusted contrasts should be kept separate from the stated mixed model analysis. A p-value is a measure of how incompatible the observed result is with a specified null model under its assumptions; it is not the probability that the null hypothesis is true, nor a measure of clinical importance. The posted p-values are unadjusted and should be read as such.

Why can over-dispersion matter?

In general, over-dispersion means observed variability is greater than a model assumes. When a model underestimates variability, standard errors can be too small and intervals can be too narrow. The primary endpoint is a continuous score, and the registry does not report an over-dispersion assessment or describe this issue for its model. It should therefore be treated as a general modeling consideration, not as a documented problem in this trial.

How should arm-level changes be distinguished from treatment effects?

Within-arm change compares follow-up measurements with the same group’s baseline. A randomized treatment contrast compares changes between groups and is the relevant quantity for separating the groups’ observed trajectories. A mean change in one arm can be negative without demonstrating that the intervention caused that change. The vehicle groups’ changes illustrate why the between-group contrast matters: changes were reported in both intervention and vehicle arms, and the magnitude differed across the two vehicle schedules.

The primary analysis population is described as an Intent-to-treat Ocular Dryness Population with observed data only. In general, an intention-to-treat approach aims to analyze participants according to randomized assignment, regardless of adherence or treatment received. The additional phrase “with observed data only” indicates that the posted description is restricted to available outcome observations, but the record does not explain how missing assessments were handled in the model. It does not report missing-data counts, reasons, imputation methods, or sensitivity analyses. The exact handling of incomplete repeated measurements is therefore not fully assessable.

The registry lists two outcome measures and zero posted analyses. That distinction means the record contains outcome summaries but does not list analyses in the relevant analysis count. No secondary posted results are identified. The original analysis plan, protocol, multiplicity adjustment, interim analysis procedures, and trial-specific sample-size justification are not reported in the registry record. General statistical concepts can clarify what the posted values mean, but they cannot fill those record-level gaps.

10. Confidence Intervals and Precision

The confidence intervals around the approximate unadjusted treatment comparisons are central to interpreting precision. For reproxalap QID versus vehicle QID, the difference is 3.5 and the interval runs from -3.194 to 10.19. For reproxalap QID to BID versus vehicle QID, the difference is -2.8 and the interval runs from -9.167 to 3.567. Both intervals include zero. This means the posted recalculations do not pin down a single direction of difference: values on either side of zero remain compatible with the interval.

These intervals are fairly broad relative to their point estimates, indicating that the estimated contrasts are imprecise. They include a range of possible magnitudes rather than a narrowly determined effect. A confidence interval is not a guarantee that the true value lies within its bounds, and it is not a probability statement about this particular interval. In general, it describes uncertainty under the assumptions of the method used to construct it.

The vehicle QID-to-BID comparison is 8.2, with an interval from 1.938 to 14.46. This interval does not include zero, but it concerns the two vehicle schedules, not a reproxalap-versus-vehicle contrast. Its presence does not resolve the uncertainty in either drug comparison. Each interval pertains to a different comparison and should be interpreted on its own terms.

The confidence intervals are for approximate unadjusted comparisons derived from posted summary statistics, not the stated mixed model repeated measures treatment contrasts. The record does not post model-based confidence intervals for those primary treatment contrasts. Consequently, the intervals describe precision for the recalculated comparisons, and not necessarily the uncertainty from the trial’s specified primary analysis.

11. 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 illustrations based on the observed effect and assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning scenario uses the stated fraction of the observed effect: 100%, 75%, or 50%. These are planning assumptions for the illustrations; the trial’s own original design assumptions and sample-size justification are not reported in the registry record.

The 80% power column gives the estimated number of participants per arm for a planning design with 80% power under those assumptions. The 90% power column gives the corresponding number per arm for 90% power. In general, power describes the chance that a design will detect a specified effect if that effect is present, under the assumptions used for the calculation. It is not a measure of whether an observed trial result is true or clinically important.

For the QID reproxalap comparison, the illustration ranges from 639 participants per arm for 100% of the observed effect at 80% power to 3,422 participants per arm for 50% of the observed effect at 90% power. For reproxalap QID to BID, the corresponding listed range is 905 to 4,842 participants per arm. For the vehicle schedule comparison, it is 103 to 547 participants per arm. The full set of planning values also includes the 75% scenarios.

Smaller effects require more participants to detect with the same planned power, which is why the illustrations increase as the effect fraction decreases. These figures are not observed power and do not explain the original enrollment target. They are retrospective planning illustrations based on observed estimates, which may themselves be uncertain.

12. 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 = 3.500; pooled standard deviation σ = 22.329.
2. n = 2 × (1.96 + 0.842)² × 22.329² / 3.500² = 638.9, rounded up to 639 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 <- 3.5                      # observed difference in means
sigma <- 22.3294529143824                     # 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(3879863)
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 = 639 (80% power), 856 (90% power)
 75% of observed effect: n per arm = 1,136 (80% power), 1,521 (90% power)
 50% of observed effect: n per arm = 2,556 (80% power), 3,422 (90% power)
power.t.test: 639.9 
Simulated power at n = 639 per arm: 0.798 (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.

13. Multiplicity, Missing Data and Analysis Populations

The registry lists multiple intervention groups and more than one outcome measure, while the primary endpoint was assessed at several visits. When many comparisons or outcomes are examined, the chance of at least one apparently unusual result can increase. Statistical methods may address this multiplicity through prespecified testing sequences or adjustments, but the registry record does not report a multiplicity strategy or identify which contrasts were designated as confirmatory. The posted unadjusted p-values should therefore not be interpreted as adjusted for multiple comparisons.

The primary endpoint description identifies an Intent-to-treat Ocular Dryness Population with observed data only. It also specifies a mixed model repeated measures analysis. The registry does not report how many outcome observations were missing, the reasons for missingness, or whether missingness differed by arm. It does not report the model’s assumptions about missing data, any imputation method, or sensitivity analyses. Without those details, the effect of incomplete observations on the estimates cannot be assessed from this record.

The registry reports 422 enrolled participants, but the primary outcome summaries use arm counts of 85.0, 86.0, 85.0, and 85.0. The safety summaries use 105, 106, 105, and 106 participants at risk. The record does not explain why the reported counts differ by outcome, so no specific reason should be inferred. The outcome summary population is explicitly described as observed data only.

The trial title describes an adaptive design, but the record does not report whether interim analyses were conducted, what adaptation rules were used, or whether any adaptations occurred. The original protocol-level analysis plan, missing-data plan, and trial-specific sample-size assumptions are not reported in the registry record. Zero analyses are listed in the analysis count, and no secondary results are posted. These omissions limit assessment of confirmatory status and the full analysis process.

14. 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: acute kidney injury (1.0%), gastroenteritis salmonella (1.0%), hypoxia (1.0%), pneumonia (1.0%), spinal compression fracture (0.9%).

The registry reports serious adverse events by intervention group, alongside the number at risk. The counts are 3 of 105 for reproxalap QID, 3 of 106 for vehicle QID, 1 of 105 for reproxalap QID to BID, and 2 of 106 for vehicle QID to BID. Deaths are listed as 0 in each group. These are counts reported in the record; they do not establish whether an event was caused by study treatment.

The registry also lists serious-event terms with percentages: Acute kidney injury, 1.0%; Gastroenteritis salmonella, 1.0%; Hypoxia, 1.0%; Pneumonia, 1.0%; Spinal compression fracture, 0.9%; and Peripheral arterial occlusive disease, 0.9%. The record does not specify a group assignment for these listed terms in the summary, so they should not be attributed to a particular arm based on this information alone.

Adverse-event summaries are descriptive. The numbers of participants at risk differ from the efficacy-summary group sizes, and the registry does not explain that difference. The serious-event counts do not by themselves provide a comparison adjusted for exposure duration, background risk, or other factors.

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

The posted outcome summaries describe how ocular dryness scores changed in the four randomized groups and provide approximate contrasts between selected groups. For the two reproxalap-versus-vehicle comparisons, the approximate unadjusted confidence intervals include zero. The estimates therefore leave uncertainty about both the direction and magnitude of the differences. The registry’s posted summary does not supply the model-based treatment contrasts from its stated repeated-measures analysis.

The scores are participant-reported measures of discomfort, with higher scores indicating worse symptoms. A change in the score is a statistical description, but the record does not state what magnitude would be meaningful to participants. Statistical uncertainty and clinical importance are separate questions. Neither a point estimate nor a p-value alone establishes whether a difference would matter in practice.

The contrast between vehicle QID to BID and vehicle QID has an interval that does not include zero, but it is not the primary drug-versus-vehicle question. It should be interpreted as a comparison between vehicle schedules within this trial’s posted summaries. It does not establish a reproxalap effect.

The registry reports serious adverse-event counts and deaths by group, but these summaries do not establish causation or provide a complete assessment of comparative safety. The listed serious-event terms are not linked to specific groups in the record summary. Interpretation is further limited by unavailable information on missing observations, multiplicity, the adaptive design procedures, and the original statistical plan.

Accordingly, the posted data are best read as descriptive and approximate evidence about the reported score changes, accompanied by uncertainty. They do not, on their own, establish a treatment benefit, lack of benefit, or complete safety profile. They are not medical advice and do not replace the trial’s full protocol-level analysis or clinical judgment.

16. Why This Trial Matters Statistically

RENEW is statistically interesting because its registry record combines a repeated-measures primary outcome with four treatment schedules and an explicitly adaptive trial title. Those features make the distinction between the stated primary model and simple arm-summary comparisons particularly important. The mixed model repeated measures analysis uses baseline, treatment arm, visit, and their specified interaction structure; the approximate recalculations use posted summary statistics and do not reproduce that analysis.

The score was assessed at multiple visits, making the trajectory over time relevant to the endpoint description. A single arm-level change cannot capture all modeled visit patterns, and an unadjusted summary comparison cannot substitute for the repeated-measures contrast. Readers need to distinguish within-group changes from randomized between-group comparisons, and distinguish approximate recalculations from results of the stated model.

The registry also illustrates how the same outcome scale can generate different contrasts depending on which arms are compared. The two drug-versus-vehicle comparisons have intervals including zero, while the vehicle-schedule comparison has an interval that does not. This reinforces the need to identify the scientific question each contrast answers before interpreting an estimate or p-value.

Finally, the sample-size illustrations make visible the sensitivity of planning to the effect size assumed: smaller target effects require larger per-arm enrollment under the listed assumptions. Because the calculations use observed effects rather than the original design rationale, they are useful only as planning illustrations. The registry’s lack of detail on adaptive procedures, multiplicity, missing data, and the original sample-size justification sets clear limits on what can be inferred statistically.

17. 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 original sample-size justification, even though the trial title describes an adaptive phase 3 design. It also does not detail any interim analyses, adaptation rules, or whether adaptations occurred. The retrospective planning illustrations are based on observed effects and cannot recover those original design decisions.

The primary analysis is described as a mixed model repeated measures analysis, but the record does not provide model-based treatment contrasts, confidence intervals, or p-values. The covariance structure, estimation details, model diagnostics, and approach to incomplete repeated observations are also not reported. The unadjusted comparisons are approximate recalculations from summary statistics, so they should not be mistaken for the trial’s specified model analysis.

Multiplicity procedures are not reported despite the presence of several arms and repeated visits. The record does not provide missing-data counts, reasons for missing assessments, or sensitivity analyses. It describes the outcome population as observed data only, but does not explain why efficacy counts differ from safety counts. The registry’s masking classification also differs from the double-masked wording in the trial title, without an explanation of the discrepancy.

The registry does not report a threshold for clinically meaningful change on the dryness scale. The serious-event term percentages are not linked to specific groups in the summary, and the event counts alone do not establish causality. These limitations constrain interpretation of both comparative efficacy and safety from the posted record.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: The RENEW Trial: A Multi-Center, Randomized, Double-Masked, Parallel-Group, Vehicle-Controlled, Adaptive Phase 3 Clinical Trial to Assess the Safety and Efficacy of Subjects With Dry Eye Disease — NCT03879863.
• Registry record last updated 2025-01-23; status last verified 2025-01.
• Results first posted 2025-01-23.
• 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.

21. Record Summary

The registry describes RENEW as a completed randomized phase 3, parallel-group, vehicle-controlled trial of reproxalap ophthalmic solution (0.25%) in subjects with dry eye disease. Overall enrollment was 422. The trial title describes a multicenter, double-masked study, while the registry classifies masking as triple.

The primary outcome was change from baseline in subject-reported ocular dryness score on a 0 - 100 Visual Analogue Scale, analyzed as a least-squares mean with standard error using mixed model repeated measures. The record posts arm summaries and approximate unadjusted comparisons, but not model-based treatment contrasts. The confidence intervals for the two reproxalap-versus-vehicle recalculations include zero.

The registry lists serious adverse-event counts, no deaths in any group, and planning illustrations based on observed effects. Details of the original sample-size justification, multiplicity plan, missing-data handling, and adaptive procedures are not reported in the registry record.