A Study to Evaluate AXR-159 Ophthalmic Solution in Patients With Dry Eye Disease: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Study to Evaluate AXR-159 Ophthalmic Solution in Patients With Dry Eye Disease (NCT03598699), a randomized phase 2 study. The primary outcome is Inferior Corneal Staining Score.

2. Clinical Question

3. Trial Design

The registry describes a randomized, parallel-group, vehicle-controlled Phase 2 study with quadruple masking. Its official title characterizes the study as multicenter and identifies safety, tolerability, systemic pharmacokinetics, and pharmacodynamics as areas of evaluation. The brief summary describes two stages: Stage 1 evaluated AXR-159 concentrations of 30 mg/mL or 50 mg/mL, and Stage 2 evaluated 3 mg/mL, 30 mg/mL, or 50 mg/mL.

The record lists an enrollment of 102 and a completed status. It gives a start date of 2018-06-26 and a primary completion date of 2018-12-28. However, the brief summary refers to approximately 430 patients across the two stages. The registry record does not explain how that figure relates to the enrollment figure, the results population, or the reported outcome groups. It is therefore important not to treat the enrollment figure and the outcome-specific group sizes as interchangeable.

The primary posted outcome is the change from baseline in inferior corneal staining at Month 3. The posted comparison is limited to AXR-159 50 mg/mL versus vehicle; results for the other concentrations are not included in the primary outcome summaries presented in the registry record. Although the record lists seven outcome measures and several secondary outcomes, it reports no analyses in the analysis-count field. The registry record does not report the allocation ratio, the original sample-size justification, or the detailed analysis plan.

Randomization is intended to make treatment groups comparable on average, while masking is intended to reduce the influence of expectations on participant care, assessments, and reporting. Those design features support an informative comparison, but they do not remove uncertainty in a modest-sized outcome sample or resolve discrepancies in the record. The available information describes the design, but it does not establish how well the planned procedures were implemented.

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.

Before assignment: All subjects who met the enrollment criteria at the initial screening visit were assigned to a 2-week run-in period on thrice daily topical vehicle. At the conclusion of the run-in period, 102 subjects again met the enrollment criteria and were randomized to either active or vehicle groups.

Overall Study

Analysis population for the primary outcome, as defined in the registry: Modified Intent-to-Treat population with last observation carried forward (LOCF)

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.

Population: Safety Population

6. Primary Endpoint

The registry lists the primary outcome as Inferior Corneal Staining Score, measured over Month 3.

Inferior corneal staining score measures staining in the inferior part of the cornea using the Ora Calibra® Corneal and Conjunctival Staining Scale. The scale ranges from 0 to 4: 0 means none, 1 trace, 2 mild, 3 moderate, and 4 severe. The primary outcome is the change from baseline at Month 3 in the study eye, expressed as a mean in units on a scale. More negative changes indicate a better outcome.

Corneal staining is used as an observable clinical measure of the ocular surface. A change score compares the follow-up score with the baseline score, so the direction of change helps describe whether staining moved toward or away from less severe categories. A mean summarizes the average change in a group, while the standard deviation describes how varied individual changes were around that average.

In the posted result, the mean change was -0.08 in the AXR-159 50 mg/mL group and -0.03 in the vehicle group. The difference between those posted means was -0.05 units. These are group-level summaries, not descriptions of every participant’s response. The registry record does not report the clinical importance threshold for this scale or establish what size of change would be meaningful to patients.

The analysis population is described as Modified Intent-to-Treat with LOCF. LOCF carries a participant’s last recorded observation forward when a later observation is missing. This defines one way of handling missing measurements, but the registry record does not report how many observations were carried forward or the reasons for missing data.

7. Results Posted in the Registry

• AXR-159 Ophthalmic Solution 50 mg/mL: mean -0.08 versus -0.03 on control; difference -0.05 (95% CI -0.27 to 0.17), standardized effect d = -0.09; z-test p = 0.657.

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 Ocular Surface and Disease Index (OSDI) © for Dry Eye

• 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:
  • AXR-159 Ophthalmic Solution 50 mg/mL: mean -8.80 versus -5.00 on control; difference -3.80 (95% CI -9.40 to 1.80), standardized effect d = -0.28; z-test p = 0.183.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AXR-159 Ophthalmic Solution 50 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

Schirmer's Test

• 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:
  • AXR-159 Ophthalmic Solution 50 mg/mL: mean 0.80 versus 1.90 on control; difference -1.10 (95% CI -3.56 to 1.36), standardized effect d = -0.18; z-test p = 0.382.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AXR-159 Ophthalmic Solution 50 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

Tear Film Break-up Time (TBUT)

• 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:
  • AXR-159 Ophthalmic Solution 50 mg/mL: mean -0.14 versus -0.18 on control; difference 0.04 (95% CI -0.42 to 0.49), standardized effect d = 0.03; z-test p = 0.879.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AXR-159 Ophthalmic Solution 50 mg/mL and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary outcomes cover symptom reporting, tear production, tear-film stability, redness, and conjunctival staining. At Month 3, the available summary-statistic comparisons for OSDI, Schirmer’s Test, and TBUT do not show a clear, precise separation between AXR-159 50 mg/mL and vehicle: their confidence intervals include zero. The registry record lists additional secondary measures, but does not provide posted results for all of them in the secondary summaries.

The overall pattern does not supply a consistent set of precise secondary estimates that would strengthen the primary finding. It should be considered alongside the primary result, which also has a confidence interval including zero. The secondary measures assess related but distinct aspects of dry eye disease, so agreement or disagreement among them can be informative, but they are not interchangeable with inferior corneal staining and do not replace the primary endpoint.

The secondary comparisons are unadjusted. When many outcomes are tested, the chance of at least one apparently unusual result can increase, even if no true differences exist. Adjustment procedures or a prespecified testing hierarchy can address this concern, but neither is reported in the registry record. The record also lists no reported analyses in its analysis-count field. Accordingly, any nominal p-values or apparent patterns across secondary outcomes should be treated as exploratory rather than confirmatory.

Absence of precise evidence in these summaries does not prove that every measure is unaffected. The intervals communicate uncertainty, and the registry record does not report clinical importance thresholds for these measures or an analysis plan for interpreting them collectively. The secondary evidence is therefore best used as contextual information about the breadth and consistency of the posted outcome pattern, not as an independent basis for a definitive treatment conclusion.

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

• Total Ocular Surface and Disease Index (OSDI) © for Dry Eye
• Schirmer's Test
• Tear Film Break-up Time (TBUT)
• Conjunctival Redness Score
• Total Lissamine Green Conjunctival Staining

9. Statistical Interpretation

10. Statistical Methods Explained

The primary endpoint is continuous: each participant has a change score, and the reported group summaries are means with standard deviations. A mean difference compares the average change in the AXR-159 50 mg/mL group with the average change in the vehicle group. With the ordering used for the posted comparison, the estimate is -0.05. Since more negative changes represent better outcomes, a negative difference points toward a larger average reduction in staining in the AXR-159 group. This direction is a description of the estimate, not a conclusion that the treatment caused a benefit.

What does the standard deviation describe?

The standard deviation describes the spread of participants’ change scores around their group mean. The primary outcome standard deviations were 0.65 for AXR-159 50 mg/mL and 0.447 for vehicle. They are not confidence limits and do not indicate how precise the mean difference is on their own. Greater variation generally makes a group mean less precise when other features, including the number of observations, are held fixed. The pooled standard deviation of 0.561 is used in the posted standardized comparison.

What is a standardized difference?

The standardized difference, -0.089, puts the mean separation in units of pooled variability. This can help describe the magnitude of an estimate across measures with different scales, but it does not translate directly into clinical importance. Whether a particular score difference matters clinically depends on interpretation of the measure and an accepted meaningful-change threshold. Such a threshold is not reported in the registry record.

How should the p-value be understood?

The p-value of 0.657 is an unadjusted measure of how compatible the observed estimate is with a null model of no mean difference, under the assumptions of the comparison. It is not the probability that the null hypothesis is true, and it is not the probability that the result arose by chance. It also does not measure the size or clinical importance of a difference. Because the registry record does not report an adjusted analysis, the posted p-value does not account for multiple outcomes or multiple concentration comparisons.

Why does the confidence interval matter?

The 95% confidence interval from -0.271 to 0.171 gives a range of estimates compatible with the posted summary data under the calculation assumptions. Its inclusion of zero means that no mean difference is within that range. Values on either side of zero are also included, so the data do not pin down the direction of the underlying difference precisely. A confidence interval is not a guarantee that the true difference lies in the particular interval, nor does it account for bias, missing-data assumptions, or unreported analytical choices.

What is meant by an unadjusted summary-statistic calculation?

The comparison uses the posted group means, standard deviations, and outcome sample sizes to estimate a difference and its uncertainty, without a reported covariate-adjusted model. Such a calculation is useful for describing the results in a consistent way, but it may not reproduce the sponsor’s intended analysis. The registry record lists no analyses in its analysis-count field and does not describe a statistical model, adjustment variables, or treatment of the study stages. Thus, the calculated comparison should not be confused with a fully documented prespecified analysis.

The treatment allocation was randomized, but the available outcome summaries do not show baseline characteristics, adherence, or missingness by group. Randomization helps support comparisons by reducing systematic differences at assignment, but it does not guarantee identical groups in a particular sample, and it cannot correct all forms of missing outcome data or measurement error. Details of randomization implementation and any procedures to account for the stages are not reported in the registry record.

How does LOCF affect interpretation?

The primary analysis population is identified as Modified Intent-to-Treat with last observation carried forward. In general, LOCF substitutes a participant’s last available measurement for a later missing measurement. This approach can retain participants with incomplete follow-up, but it assumes that the carried-forward value is a reasonable stand-in for the unobserved value. That assumption may not hold if the outcome changes over time. The record does not report the amount or pattern of missing data, the number of values carried forward, or sensitivity analyses using alternative missing-data assumptions.

Finally, standard deviations and means compress participant-level data into summary statistics. They do not show the distribution’s shape, potential outliers, or whether responses varied in ways that a mean alone obscures. The posted calculation also does not establish causality on its own: interpretation depends on design conduct, follow-up, endpoint measurement, and analysis choices, some of which are not described in the registry record. The statistics are best read as an uncertain estimate for the recorded endpoint, not as a complete account of all study evidence.

11. Confidence Intervals and Precision

The mean difference in inferior corneal staining change was -0.05 units, with a 95% confidence interval from -0.271 to 0.171. This interval is wide enough to include zero and estimates in both directions. It therefore conveys meaningful uncertainty about whether the average change differed between the groups and about the direction of any underlying difference.

In general, a confidence interval describes the range of values that are reasonably compatible with the data and the assumptions used to calculate it. Under repeated use of the same method in comparable studies, intervals constructed this way would cover the true parameter at the stated confidence level. For an individual study, it is not correct to treat the interval as a probability statement about where the true value lies. The interval also does not include uncertainty from every possible source, such as bias, missing data, or choices not described in the registry record.

The primary comparison included 50.0 participants in the AXR-159 50 mg/mL outcome group and 47.0 in the vehicle outcome group. The group standard deviations were 0.65 and 0.447, respectively. The observed mean difference is small relative to the pooled standard deviation of 0.561. Both the sample sizes and variability contribute to the precision of the estimate; the confidence interval is the most direct summary of that precision.

The unadjusted p-value of 0.657 is consistent with the interval’s inclusion of zero, but the interval offers more information by displaying the range of effect estimates compatible with the comparison. Neither the p-value nor the interval establishes equivalence. An equivalence conclusion would require a prespecified margin and an analysis designed to evaluate that question. Such a margin and analysis are not reported in the registry record.

Precision should also be distinguished from clinical importance. The registry record does not specify a minimum clinically important change for this staining scale. Thus, even a more precise estimate would need a clinical reference point to determine whether the difference was meaningful. The available interval indicates uncertainty; it does not by itself resolve the clinical interpretation.

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 participants or total events. They are illustrations based on the observed effect and are not the original design calculation for the trial. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; the target effect is the stated fraction of the observed effect. The registry record does not report the trial’s original sample-size assumptions or justification.

The 80% power column describes the planned number of participants per arm that, under those assumptions and for the chosen target difference, would yield an 80% chance of detecting that difference using the specified test. The 90% power column describes a higher chance of detection under the same assumptions and therefore requires more participants per arm. These are prospective planning quantities, not a measure of how likely the posted result is to be true.

The planning values depend strongly on the effect size chosen. Planning for 100% of the observed effect gives 1,976 participants per arm for 80% power and 2,646 for 90% power. Planning for 75% of the observed effect gives 3,513 participants per arm for 80% power and 4,703 for 90% power. Planning for 50% of the observed effect gives 7,904 participants per arm for 80% power and 10,581 for 90% power. Smaller target effects require more participants because a smaller separation between group means is harder to distinguish from random variation.

These calculations use the observed estimate as a planning anchor, which can be unstable when estimates are imprecise. They are illustrations rather than a recommendation or a reconstruction of the sponsor’s planning process. This is not observed power: it does not tell whether the trial had a particular probability of detecting its result after the outcome data were collected. The figures also depend on assumptions that may not hold exactly in a future study, including equal allocation and the normal approximation.

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 = -0.050; pooled standard deviation σ = 0.561.
2. n = 2 × (1.96 + 0.842)² × 0.561² / -0.050² = 1,975.8, rounded up to 1,976 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 <- -0.05                      # observed difference in means
sigma <- 0.560955144092833                     # 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(3598699)
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 = 1,976 (80% power), 2,646 (90% power)
 75% of observed effect: n per arm = 3,513 (80% power), 4,703 (90% power)
 50% of observed effect: n per arm = 7,904 (80% power), 10,581 (90% power)
power.t.test: 1976.8 
Simulated power at n = 1,976 per arm: 0.801 (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 record lists seven outcome measures and identifies a primary endpoint alongside secondary measures. The registry record does not report how the investigators handled multiplicity, whether outcomes were organized into a testing hierarchy, or whether any adjustment was planned. When multiple outcomes, doses, or time points are examined, the probability of at least one nominally notable result can increase. Unadjusted comparisons should therefore be interpreted cautiously, especially when they are not accompanied by a documented prespecified analysis plan.

The primary comparison and the secondary comparisons are simple unadjusted calculations from posted group summaries. The registry record lists no analyses in its analysis-count field, and no sponsor-reported inferential model is described in the outcome information. Covariate adjustment, handling of the study stages, and any interim analyses are not reported in the registry record. Those omissions limit the ability to determine whether these comparisons correspond to the study’s intended confirmatory analysis.

The primary population is described as Modified Intent-to-Treat with LOCF. This names an analysis population and a missing-data method, but the record does not state how many participants had missing Month 3 values, how many observations were carried forward, or why data were missing. It also does not report a sensitivity analysis under alternative missing-data assumptions. LOCF can be convenient, but carrying a prior value forward may not represent an outcome that would have been observed later; the impact depends on how outcomes evolve and why measurements are absent.

The record’s enrollment information also warrants caution. It states enrollment of 102, while the brief summary describes approximately 430 patients across two stages. The record does not explain the relationship between those figures or how the reported outcome populations relate to each. In addition, the primary summary group sizes differ from the adverse-event groups at risk. The record does not explain the population definitions behind those differences. These issues do not establish that the posted calculations are wrong, but they make it important to keep each result attached to its stated population and denominator.

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 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: post procedural haemorrhage (2.1%).

For serious adverse events, the registry reports 0 affected among 54 at risk in the AXR-159 50 mg/mL group and 1 affected among 48 at risk in the vehicle group. Deaths are reported as 0 in both groups. These are descriptive counts for the reported safety groups; they do not establish that a treatment caused or prevented an event, and rare events can be difficult to compare in groups of this size.

The record also reports other adverse events in 34 of 54 at risk in the AXR-159 group and 7 of 48 at risk in the vehicle group. These are listed separately from serious adverse events and should not be combined with them. The registry identifies Post procedural haemorrhage as the top serious term and gives 2.1%, but does not clearly specify in the available summary which group or denominator that term refers to.

Safety counts are not the same as a comprehensive assessment of risk. Interpretation depends on event definitions, duration of observation, exposure, ascertainment, and participant characteristics. The registry record does not provide enough detail to resolve those issues or to determine the causes of individual events. No medical conclusion should be drawn from these descriptive counts alone.

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

The posted primary result describes the average Month 3 change in inferior corneal staining for AXR-159 50 mg/mL compared with vehicle, in the stated Modified Intent-to-Treat population using LOCF. The point estimate is -0.05 units, in the direction of a more favorable change for AXR-159 under the scale definition. Its 95% confidence interval, from -0.271 to 0.171, includes zero and spans estimates in either direction. The result is therefore uncertain about the magnitude and direction of the underlying mean difference.

This does not establish that AXR-159 is effective, ineffective, equivalent to vehicle, or clinically important. The registry record does not report an equivalence margin or a meaningful-change threshold. A p-value of 0.657 is not proof of no effect, and the confidence interval does not show that all clinically relevant differences have been excluded. The interpretation is further limited by the absence of a documented sponsor analysis in the posted outcome information and by unreported details about missing measurements and multiplicity.

The finding applies only to the reported concentration, comparator, endpoint, time point, and population. The study’s summary describes evaluation of other concentrations, but their primary outcome comparisons are not included in the posted summaries. A result for AXR-159 50 mg/mL cannot be transferred to the other concentrations or to outcomes not reported. Nor can an average group result predict how a particular participant would respond.

The registry’s safety figures are descriptive and should be interpreted separately from the efficacy endpoint. They do not establish a causal safety profile, especially without fuller information on follow-up, event ascertainment, and group definitions. Overall, the record offers a limited and imprecise comparison rather than a definitive answer about treatment effects or clinical use.

17. Why This Trial Matters Statistically

This trial is statistically informative because it illustrates the difference between the direction of an estimate and the strength of evidence supporting that estimate. The primary mean difference is negative, which favors AXR-159 under the endpoint’s scoring direction, but the confidence interval includes zero and extends to estimates in the opposite direction. Reading only the point estimate would overstate what the data establish; reading only the p-value would hide the range of plausible estimates. Both the estimate and its precision are needed.

It also demonstrates why a non-significant result is not the same as evidence of equivalence. The registry does not report a prespecified equivalence margin, and the interval remains compatible with differences in both directions. A lack of statistical significance cannot establish that the groups are sufficiently similar for a clinical purpose.

The planning illustrations show how sample-size requirements depend on the effect chosen for future detection. Smaller target effects require more participants per arm under the stated assumptions. These figures are not observed power and do not reconstruct the original trial design. They illustrate the way precision and design assumptions interact, while emphasizing that an observed effect is an uncertain basis for planning.

Finally, the record highlights how transparent reporting affects interpretation. The enrollment figure and brief-summary estimate do not align, outcome-specific group sizes differ from safety denominators, and detailed multiplicity and missing-data information are absent. These gaps do not erase the posted estimates, but they limit how confidently readers can connect them to the full study design and analysis. Statistical interpretation depends not only on calculations, but also on clear definitions of populations, outcomes, and analysis choices.

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 outcome evidence is limited to the posted comparison of AXR-159 50 mg/mL with vehicle. Although the study summary describes other concentrations, their primary outcome results are not included in the available primary summaries. It is not possible to infer dose patterns or compare concentrations from this result alone.

The registry gives an enrollment of 102, while the brief summary describes approximately 430 patients across two stages. The record does not explain the discrepancy or how the posted outcome population relates to the overall study. The primary outcome groups have 50.0 and 47.0 participants, while the serious-adverse-event groups at risk are 54 and 48. The record does not report the population definitions or reasons for these differences.

The analysis information is limited. The registry reports no analyses in its analysis-count field, and the posted comparisons are unadjusted calculations from summary statistics. The statistical analysis plan, covariate adjustments, multiplicity strategy, and any interim analyses are not reported in the registry record. The amount and pattern of missing outcome data, the number of LOCF substitutions, and sensitivity analyses are also not reported.

The record does not provide a clinically meaningful threshold for the staining score, baseline characteristics for the outcome groups, or detailed distributions of individual change scores. The mean and standard deviation cannot show all aspects of the response distribution. Finally, the reported primary result is at Month 3, and the registry record does not provide enough detail to assess the completeness of follow-up or how the two study stages were incorporated in the analysis.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Study to Evaluate AXR-159 Ophthalmic Solution in Patients With Dry Eye Disease — NCT03598699.
• Registry record last updated 2023-10-13; status last verified 2023-09.
• Results first posted 2023-10-13.
• 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

The registry describes a completed, randomized, quadruple-masked, parallel, vehicle-controlled Phase 2 study of AXR-159 in patients with dry eye disease. The primary posted comparison is AXR-159 Ophthalmic Solution 50 mg/mL versus vehicle for change in inferior corneal staining at Month 3 in the Modified Intent-to-Treat population with LOCF. Mean changes were -0.08 and -0.03, respectively; the mean difference was -0.05, with a 95% confidence interval from -0.271 to 0.171 and an unadjusted p-value of 0.657.

The estimate favors AXR-159 in direction but is imprecise and compatible with no mean difference. The registry record lists no analyses in its analysis-count field, does not report a multiplicity strategy or detailed missing-data information, and does not explain the difference between enrollment of 102 and the brief summary’s approximately 430 patients. The posted result should be interpreted as a limited comparison for the reported endpoint, concentration, time point, and population.