A Multi-Center, Randomized, Double Masked, Parallel-Group, Vehicle-Controlled, Clinical Study to Assess the Safety and Efficacy of Reproxalap Ophthalmic Solution in Subjects With Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Multi-Center, Randomized, Double Masked, Parallel-Group, Vehicle-Controlled, Clinical Study to Assess the Safety and Efficacy of Reproxalap Ophthalmic Solution in Subjects With Dry Eye Disease (NCT03404115), a randomized phase 2 study. The primary outcome is Efficacy of ADX-102 on the Ora Calibra® Discomfort & 4-Symptom Questionnaire for Dryness..

2. Clinical Question

The primary measure covers Day 1 through Day 85, with assessments on Days 1, 15, 29, 57, and 85. The comparison therefore concerns the reported change over the assessment period, not a single isolated visit. The registry record does not report a separate primary result for each visit or a secondary outcome result.

3. Trial Design

This was a phase 2b, multicenter, randomized, parallel-group, vehicle-controlled clinical study of reproxalap ophthalmic solution in subjects with dry eye disease. The registry lists the masking as quadruple, while the study title describes the study as double masked. The record does not explain this difference in terminology. The study is marked completed.

Enrollment was 300. The three arms each had 100 participants: Reproxalap at 0.25%, Reproxalap at 0.1%, and vehicle. The study started on 2018-01-02, and primary completion was recorded as 2018-07-11. These dates describe the trial record; they do not establish how long any individual participant was followed.

The primary outcome was change from baseline on the Ora Calibra Discomfort and 4-Symptom Questionnaire for dryness. It was assessed on Days 1, 15, 29, 57, and 85. The endpoint description specifies a mixed model for repeated measures, using baseline score, visit, treatment, and the visit-by-treatment interaction. The outcome population was the intent-to-treat population with observed data only.

The registry record does not report the original sample-size justification, randomization procedures, allocation concealment, detailed dosing schedule, or a full statistical analysis plan. It also does not report protocol deviations or participant flow. Those details cannot be inferred from the enrollment totals or from the posted outcome summaries.

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 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 Efficacy of ADX-102 on the Ora Calibra® Discomfort & 4-Symptom Questionnaire for Dryness., measured over Efficacy assessment period (Day 1 through Day 85) - assessed on Days 1, 15, 29, 57, and 85..

The primary endpoint is change from baseline in dryness measured with the Ora Calibra Discomfort and 4-Symptom Questionnaire. The scale runs from 0, least, to 5, most. A negative change indicates a lower score relative to baseline; the arm-level estimates are reported as least-squares means with standard errors.

The endpoint was assessed repeatedly during the efficacy assessment period, from Day 1 through Day 85, on Days 1, 15, 29, 57, and 85. Repeated measurements can describe the outcome across visits rather than relying on a single assessment. The registry specifies a mixed model for repeated measures, with baseline score, visit, treatment, and the visit-by-treatment interaction included in the model. It does not report the model’s covariance structure or further implementation details.

Using a patient-reported symptom measure makes the outcome relevant to the symptom named in the study question. A change-from-baseline comparison also expresses the result relative to participants’ starting scores. The least-squares mean is a model-based estimate, rather than simply an unadjusted arithmetic average. The record does not state a threshold for clinical importance, so the numerical changes alone do not establish whether a difference would be meaningful to patients.

7. Results Posted in the Registry

• Reproxalap (0.25%): mean -0.70 versus -0.40 on control; difference -0.30 (95% CI -0.54 to -0.06), standardized effect d = -0.35; z-test p = 0.013.
• Reproxalap (0.1%): mean -0.50 versus -0.40 on control; difference -0.10 (95% CI -0.32 to 0.12), standardized effect d = -0.12; z-test p = 0.377.

8. Statistical Interpretation

9. Statistical Methods Explained

The primary outcome is continuous: it is a score on a bounded symptom scale, and the reported results are least-squares means. A continuous outcome can be summarized by a mean, which describes the average score or average change in a group. Here, lower numerical scores correspond to less dryness on the scale’s stated direction, but the endpoint is expressed as change from baseline, so the reported negative values represent reductions relative to baseline.

What does a least-squares mean represent?

A least-squares mean is an estimate derived from a statistical model. It can account for the variables included in that model and need not equal the raw arithmetic average of all observed changes. The registry says the mixed model for repeated measures used baseline score, visit, treatment, and the visit-by-treatment interaction. It does not give further model details, such as the covariance structure or the approach used to estimate degrees of freedom. The estimates should therefore be understood in the context of the stated model, without assuming unreported specifications.

Why model repeated measurements?

Each participant could contribute measurements at multiple scheduled visits. Measurements from the same person are generally related rather than independent; a repeated-measures model can represent that structure while estimating patterns across visits. Including visit allows the model to account for differences in outcome over time, and the visit-by-treatment interaction allows treatment comparisons to vary by visit. The posted primary result is described as a comparison across all time points, rather than a set of visit-specific results. The record does not report separate estimates for each visit.

What is a mean difference?

The mean difference expresses the estimated contrast between one active-treatment arm and vehicle. The posted contrast for 0.25% is -0.3, and for 0.1% it is -0.1. A negative value means the estimated change in the reproxalap arm was more negative than the corresponding vehicle estimate. This is a direction of the numerical contrast, not a judgment about clinical importance. The registry record does not provide a threshold that would define a meaningful difference on this questionnaire.

How should a p-value be read?

A p-value describes how compatible the observed data are with a specified null hypothesis under the statistical model and its assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. The posted p-values are 0.013 for the 0.25% comparison and 0.377 for the 0.1% comparison, and they are unadjusted. The registry record does not report whether or how the study planned to control the overall error rate across multiple comparisons or outcomes.

Why can over-dispersion matter?

Over-dispersion occurs when observations vary more than a statistical model expects. It can make uncertainty estimates too small if the model does not account for the extra variability, which can in turn make intervals too narrow and p-values too small. This is a general statistical issue, not a reported finding in this trial. The registry record does not report an over-dispersion assessment or a diagnostic result for the continuous primary endpoint.

What assumptions underlie the precision estimates?

The arm-level results include standard errors, which describe the estimated uncertainty around the least-squares means. The comparison results include confidence intervals. A confidence interval is a range generated by a statistical procedure intended to capture the underlying comparison at its stated confidence level over repeated use of that procedure, assuming the model and data conditions are adequate. Its width reflects statistical precision, not the probability that a particular value inside it is true. The record does not report further details about how the intervals or p-values were calculated.

What does the reported analysis population mean?

The primary outcome description identifies the intent-to-treat population with observed data only. Intent-to-treat generally refers to analyzing participants according to their randomized group, whether or not they fully adhered to the assigned intervention; that is a general explanation of the term, not a claim about unreported analysis procedures in this trial. The phrase “with observed data only” indicates that the listed population includes observed outcome data, but the registry record does not report the amount or pattern of missing data, imputation methods, or sensitivity analyses. Consequently, the posted estimates do not on their own show whether missingness could have affected the comparisons.

10. Confidence Intervals and Precision

The confidence interval for the 0.25% comparison is -0.536 to -0.064. It lies on the negative side of zero, while its width indicates that the estimate remains compatible with a range of possible differences rather than one exact value. The point estimate is -0.3. The interval communicates uncertainty around that estimate; it does not identify which value is the true effect.

For 0.1%, the interval is -0.322 to 0.122, around a point estimate of -0.1. It includes zero and extends to both negative and positive values. Thus, the posted data are consistent with several possible directions and magnitudes of the comparison. The p-value of 0.377 accompanies this interval, but neither the p-value nor the interval indicates whether any particular difference is clinically important.

The registry reports standard errors of 0.09 and 0.08 for the active-arm least-squares means and 0.08 for the vehicle mean. A standard error describes uncertainty in an estimated mean, not the spread of individual participant scores. The confidence intervals apply to the treatment comparisons and are more directly useful for judging the precision of those contrasts.

Precision depends on the data and the analysis model. The registry record does not report diagnostics, sensitivity analyses, or details of the interval calculation beyond the repeated-measures model description. The intervals should therefore be read as the posted estimates under the analysis as reported, not as guarantees that capture every possible source of uncertainty.

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 for 80% power and participants per arm for 90% power. They are not total trial enrollment figures or total event counts. The illustrations assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. These are planning illustrations based on observed estimates, not the original trial’s sample-size justification; the original design assumptions are not reported in the registry record.

The 80% power column gives an illustrative number of participants per arm for a design with an 80% chance of detecting the assumed effect, if the planning assumptions and model conditions hold. The 90% column uses a higher target chance of detection and correspondingly requires more participants in the listed scenarios. These percentages describe design characteristics under assumptions, not the probability that a result in this trial is true or that a treatment has an effect.

For the 0.25% comparison, planning for 100% of the observed effect gives 127 participants per arm for 80% power and 170 for 90% power. Planning for 75% of the observed effect gives 225 and 301 participants per arm, respectively; planning for 50% gives 506 and 678. For the 0.1% comparison, the corresponding figures are 1,005 and 1,345 for 100% of the observed effect, 1,787 and 2,392 for 75%, and 4,019 and 5,380 for 50%.

Smaller effects are harder to detect, so planning to detect a smaller fraction of the observed effect requires more participants per arm. These calculations are not observed power: they are forward-looking illustrations based on specified assumptions, not a measure of what the completed trial achieved.

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 = -0.300; pooled standard deviation σ = 0.851.
2. n = 2 × (1.96 + 0.842)² × 0.851² / -0.300² = 126.5, rounded up to 127 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 <- -0.3                      # observed difference in means
sigma <- 0.85146931829632                     # 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(3404115)
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 = 127 (80% power), 170 (90% power)
 75% of observed effect: n per arm = 225 (80% power), 301 (90% power)
 50% of observed effect: n per arm = 506 (80% power), 678 (90% power)
power.t.test: 127.4 
Simulated power at n = 127 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.

13. Multiplicity, Missing Data and Analysis Populations

The primary outcome description identifies one endpoint and a repeated-measures analysis across scheduled visits. Two active-treatment comparisons with vehicle are reported. The registry record does not report a prespecified multiplicity strategy, such as an adjustment across those comparisons or a hierarchy for interpreting outcomes. The posted p-values are explicitly unadjusted, so they should not be treated as if the overall chance of a false-positive finding across multiple tests had been controlled.

The record lists one outcome measure and no secondary results. It does not establish whether additional outcomes or analyses were planned in the protocol, whether any were omitted from the registry record, or whether there were interim analyses. The statistical plan beyond the stated mixed-model terms is not reported in the registry record. In particular, the record does not specify a primary significance threshold, a testing sequence, or a strategy for handling multiple visits in the formal inference.

The analysis population is described as intent-to-treat with observed data only. This does not provide a complete account of missingness. The registry record does not report how many outcome measurements were missing, reasons for missingness, the distribution of missing data by arm, imputation procedures, or sensitivity analyses. Since the analysis uses observed data, uncertainty about missing-data patterns is relevant when assessing how fully the estimates represent randomized participants.

The trial enrolled 300 participants, with 100 listed in each arm, but the record does not report participant flow or how many contributed data at each visit. It is therefore not possible to reconstruct visit-level analysis denominators from the posted summary. The record also does not report whether model assumptions were evaluated or how departures from them would have been handled.

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: angina pectoris (1.0%), vertigo (1.0%).

Serious adverse events were reported for 1 of 100 participants in the 0.25% Reproxalap arm, 1 of 100 in the 0.1% Reproxalap arm, and 0 of 100 in the vehicle arm. The record also lists angina pectoris and vertigo as serious adverse event terms, each at 1.0%. It does not identify which arm is associated with each listed term, so those terms should not be assigned to a particular group based on the information reported.

No deaths were reported in any of the three arms. Other adverse events affected 93 of 100 participants in the 0.25% arm, 37 of 100 in the 0.1% arm, and 2 of 100 in the vehicle arm. These are descriptive counts as posted. The registry record does not provide event-level detail for the other adverse events, severity categories, exposure-adjusted rates, or statistical comparisons between groups.

Safety counts alone do not establish whether events were caused by study treatment, and differences in these counts should not be interpreted as causal comparisons without further information. The record does not report detailed adjudication procedures or follow-up details for adverse events.

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

The results describe model-based changes in a dryness questionnaire score during the assessment period. The estimated changes were -0.7 for Reproxalap at 0.25%, -0.5 for Reproxalap at 0.1%, and -0.4 for vehicle. The posted comparisons with vehicle were -0.3 for 0.25% and -0.1 for 0.1%. These estimates summarize the reported outcome and do not, by themselves, establish the practical or clinical importance of the differences.

The 0.25% comparison has a confidence interval entirely below zero, whereas the interval for 0.1% includes zero and extends in both directions. This distinction concerns the statistical uncertainty in the posted contrasts. It is not a direct comparison of the two reproxalap concentrations, and it does not show that their effects differ from each other. The registry record reports no direct test between the concentrations.

Interpretation is limited by information not reported in the registry record. There is no stated threshold for a meaningful change on the questionnaire, no detailed description of missing data or sensitivity analyses, and no reported multiplicity strategy. Although the endpoint description identifies an intent-to-treat population with observed data only and lists the mixed-model terms, further model details are unavailable. These omissions leave uncertainty about clinical interpretation and robustness beyond the estimates and intervals posted.

Safety information is also descriptive. Serious adverse events were reported in the active arms, none in the vehicle arm, and no deaths were reported. The record does not establish causation or provide enough detail to characterize the full clinical context of those events. The findings should therefore be read as the results recorded for this trial and outcome, not as a general conclusion about effects in other populations, settings, or periods of use.

16. Why This Trial Matters Statistically

This trial illustrates why a reported treatment estimate should be read together with its uncertainty. For the 0.25% comparison, the confidence interval lies below zero; for the 0.1% comparison, the interval crosses zero. The point estimates alone would conceal this difference in precision. Intervals make visible the range of values compatible with each posted comparison under the analysis.

The trial also illustrates the distinction between a modeled repeated-measures endpoint and a single-visit outcome. The primary measure was assessed across several visits and analyzed with a mixed model that included visit and a visit-by-treatment interaction. Understanding that structure matters: the primary comparison is reported across time points, while visit-specific results are not reported in the registry record.

Multiplicity is another important statistical issue. Two concentrations were compared with vehicle, and the posted p-values are unadjusted. Without a reported multiplicity strategy, the reader cannot determine how the study intended to account for the set of comparisons when interpreting statistical evidence. Statistical significance in one comparison and not another also does not establish a statistically significant difference between those two comparisons.

The planning illustrations show how assumed effect size influences the number of participants required in a two-arm design. They are based on the observed effects and stated planning assumptions, rather than on the trial’s original design rationale. This distinction is important because planning calculations do not measure the probability that the completed study detected an effect.

Finally, the record gives a useful example of the limits of registry summaries. It reports outcome estimates and adverse-event counts, but not detailed missing-data information, model diagnostics, or a full analysis plan. Statistical interpretation depends not only on the numerical result, but also on the design and analysis details available to assess its reliability.

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 primary comparison is reported across scheduled visits, but visit-specific estimates are not included. The registry record does not report participant counts contributing outcome data at each visit, the amount or pattern of missing data, or sensitivity analyses. The analysis population is described as intent-to-treat with observed data only, leaving the consequences of missing observations uncertain.

Only the mixed-model terms are specified: baseline score, visit, treatment, and visit-by-treatment interaction. The record does not report the covariance structure, model diagnostics, or other implementation details. It also does not state a clinical-importance threshold for the questionnaire score, limiting interpretation of the size of the estimated differences.

There are two active-versus-vehicle comparisons, but no multiplicity adjustment is reported, and the p-values are unadjusted. No direct comparison between concentrations is posted. The registry record also does not report the original sample-size justification, interim analyses, or a full statistical analysis plan. The planning illustrations are not evidence of the assumptions used to design the completed trial.

The safety summaries provide counts but limited context. The record does not report detailed event descriptions for other adverse events, exposure-adjusted comparisons, or attribution procedures. It lists serious adverse event terms without mapping those terms to treatment groups. These limitations constrain how much can be inferred from the posted safety information.

18. Related Tutorials

19. Related Statistical Calculators

20. Sources

• ClinicalTrials.gov: A Multi-Center, Randomized, Double Masked, Parallel-Group, Vehicle-Controlled, Clinical Study to Assess the Safety and Efficacy of Reproxalap Ophthalmic Solution in Subjects With Dry Eye Disease — NCT03404115.
• Registry record last updated 2025-02-06; status last verified 2023-01.
• Results first posted 2025-02-06.
• 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

NCT03404115 is a completed phase 2b randomized, parallel-group, vehicle-controlled study of Reproxalap Ophthalmic Solution for dry eye disease. Enrollment was 300, with 100 participants listed in each of the 0.25%, 0.1%, and vehicle arms. The primary outcome was change from baseline in dryness on the Ora Calibra Discomfort and 4-Symptom Questionnaire, assessed from Day 1 through Day 85.

The reported mean differences versus vehicle were -0.3 for 0.25% and -0.1 for 0.1%. Their confidence intervals were -0.536 to -0.064 and -0.322 to 0.122, respectively. Serious adverse events were reported in 1 participant in each reproxalap arm and none in the vehicle arm; no deaths were reported.

The record describes a mixed model for repeated measures and an intent-to-treat population with observed data only. It does not report a full statistical analysis plan, multiplicity strategy, detailed missing-data handling, or a clinical-importance threshold for the questionnaire.