A Phase 1/2 Study of AURN001 in Subjects With Corneal Edema Secondary to Corneal Endothelial Dysfunction (ABA-1): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase 1/2 Study of AURN001 in Subjects With Corneal Edema Secondary to Corneal Endothelial Dysfunction (ABA-1) (NCT06041256), a randomized phase 1, phase 2 study. The primary outcome is Percentage of Participants Achieving ≥15-letter Improvement in Best-corrected Visual Acuity (BCVA) at Month 6 - Imputed Data.

2. Clinical Question

The study also aimed to assess safety and included secondary outcomes for BCVA and central corneal thickness. The primary endpoint is a responder measure: it records whether a participant reached the specified improvement threshold, rather than the average change in visual-acuity score. That makes the question clinically interpretable as the frequency of a substantial letter-score gain, but it does not describe every aspect of vision or the distribution of individual changes.

3. Trial Design

The registry identifies NCT06041256 as a Phase 1/2, randomized, prospective, parallel-arm study sponsored by Aurion Biotech. It lists enrollment of 97 and a completed status. The recorded study start was 2023-10-18, and the primary completion date was 2024-10-25. The official title describes a multicenter study; the record does not provide further site details in the registry record for this analysis.

Five groups appear in the primary outcome results: Y-27632 100 µM, neltependocel (1.0 × 10^6), and AURN001 containing neltependocel at 2.5 × 10^5, 5.0 × 10^5, or 1.0 × 10^6, each combined with Y-27632 100 µM. The brief summary describes a single injection and frames the comparisons as examining the different doses and the contribution of the individual components.

The registry’s masking information is not fully consistent: its design field records quadruple masking, while the official title says double-masked. Which roles were masked is not reported in the registry record. The allocation method beyond randomization, the original design assumptions, and the details of how the study was conducted at each site are also not reported in the registry record.

The primary outcome is a Month 6 binary responder measure in the Full Analysis Set. The recorded analysis includes missing-data rules that classify participants with missing measurements, rescue surgery before Month 6, or discontinuation before Month 6 as non-responders. The registry lists seven secondary outcomes, while six secondary outcome results are posted. The number of analyses recorded is 21, so interpretation should account for the breadth of outcomes and comparisons rather than treating each result as an isolated confirmatory finding.

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: A total of 97 participants were enrolled and received the study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set.

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: Full Analysis Set comprised of all randomized participants who received any amount of study drug during intracameral injection.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants Achieving ≥15-letter Improvement in Best-corrected Visual Acuity (BCVA) at Month 6 - Imputed Data, measured over Month 6.

The primary endpoint is the percentage of participants achieving a ≥15-letter improvement in BCVA at Month 6. BCVA was measured using the Early Treatment Diabetic Retinopathy Study (ETDRS) method with standardized Sloan letter charts. The registry describes one correct letter as one point and identifies a gain of ≥15 letters, equivalent to 0.3 LogMAR or 3 lines, as clinically meaningful.

A responder endpoint turns a continuous vision score into a clear threshold-based outcome: each participant is classified according to whether the specified gain was reached. The percentage can therefore describe how commonly that degree of improvement occurred in each group. It does not show the size of gains among responders, the amount of change among non-responders, or the full spread of visual-acuity outcomes. A participant just below the threshold and one with no improvement are both classified as non-responders for this endpoint.

The endpoint uses the study eye only. Month 6 data that were missing, or unavailable after rescue surgery or study discontinuation before Month 6, were imputed as non-response. This rule makes those cases count against the responder percentage rather than excluding them from the endpoint’s classification. It is important when interpreting the estimates because the posted percentages represent outcomes under that imputation rule, not simply the observed measurements among participants with a recorded Month 6 assessment.

7. Results Posted in the Registry

• Neltependocel (1.0 × 10^6): 44.4% (8/18) versus 14.3% (3/21) on control; risk difference 30.2 percentage points (95% CI 2.8 to 57.6), risk ratio 3.11 (0.97–10.00); unadjusted two-proportion z-test p = 0.037.
• AURN001 (2.5 × 10^5 Neltependocel + Y-27632 100 µM): 10.5% (2/19) versus 14.3% (3/21) on control; risk difference -3.8 percentage points (95% CI -24.1 to 16.6), risk ratio 0.74 (0.14–3.95); unadjusted two-proportion z-test p = 0.720.
• AURN001 (5.0 × 10^5 Neltependocel + Y-27632 100 µM): 36.8% (7/19) versus 14.3% (3/21) on control; risk difference 22.6 percentage points (95% CI -3.8 to 48.9), risk ratio 2.58 (0.78–8.58); unadjusted two-proportion z-test p = 0.100.
• AURN001 (1.0 × 10^6 Neltependocel + Y-27632 100 µM): 50.0% (10/20) versus 14.3% (3/21) on control; risk difference 35.7 percentage points (95% CI 9.2 to 62.3), risk ratio 3.50 (1.12–10.90); unadjusted two-proportion z-test p = 0.014.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Baseline in BCVA at Month 6

• 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 errors.
• Result:
  • Neltependocel (1.0 × 10^6): mean -5.10 versus -25.50 on control; difference 20.40 (95% CI 3.11 to 37.69), standardized effect d = 0.74; z-test p = 0.021.
  • AURN001 (2.5 × 10^5 Neltependocel + Y-27632 100 µM): mean -15.70 versus -25.50 on control; difference 9.80 (95% CI -7.25 to 26.85), standardized effect d = 0.36; z-test p = 0.260.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Neltependocel (1.0 × 10^6) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between AURN001 (2.5 × 10^5 Neltependocel + Y-27632 100 µM) and the control. The interval gives the range of effects that remain compatible with the data.

Change From Baseline in Central Corneal Thickness (CCT) at Month 6

• 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 errors.
• Result:
  • Neltependocel (1.0 × 10^6): mean -7.60 versus 67.50 on control; difference -75.10 (95% CI -134.31 to -15.89), standardized effect d = -0.80; z-test p = 0.013.
  • AURN001 (2.5 × 10^5 Neltependocel + Y-27632 100 µM): mean -13.80 versus 67.50 on control; difference -81.30 (95% CI -139.81 to -22.79), standardized effect d = -0.86; z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Neltependocel (1.0 × 10^6) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for AURN001 (2.5 × 10^5 Neltependocel + Y-27632 100 µM) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary outcomes cover both change in BCVA and change in central corneal thickness at Month 6, along with additional timepoint and responder outcomes. The results therefore offer measures that complement the primary Month 6 threshold outcome: continuous BCVA change preserves more information about score movement, while CCT assesses corneal thickness rather than visual acuity itself.

Across the posted Month 6 continuous comparisons, the direction of the BCVA and CCT estimates generally points toward differences between some study groups and Y-27632, but the pattern is not identical across measures or groups. This broad pattern is relevant context for the primary responder result, not a direct confirmation of it. Crossing the ≥15-letter threshold and changing the average BCVA score are different questions, and a group-level average cannot identify how many individuals crossed that threshold. CCT is a separate anatomical measure and does not substitute for a vision outcome.

The sponsor reports ANCOVA for the posted continuous comparisons. Recalculations from the summary means and standard errors are unadjusted approximations, while ANCOVA estimates may account for model covariates. The sponsor’s adjusted results should therefore be used to describe the registry’s reported secondary analyses; the recalculations are not a replacement.

The registry lists seven secondary outcomes, with six secondary outcome results posted, and the record identifies 21 analyses. Multiple outcomes and pairwise comparisons create opportunities for apparently notable results to arise by chance when many tests are examined. The registry record does not report whether a multiplicity adjustment or hierarchical testing plan was used. Without that information, unadjusted secondary p-values carry less weight than a prespecified primary analysis and are best regarded as supportive or exploratory rather than definitive evidence.

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

• Change From Baseline in BCVA at Month 6
• Change From Baseline in Central Corneal Thickness (CCT) at Month 6
• Percentage of Participants Achieving ≥15-letter Improvement in BCVA at All Timepoints - Observed Data
• Change From Baseline in BCVA at All Other Timepoints
• Change From Baseline in CCT at All Other Timepoints
• Percentage of Participants Achieving ≥10-letter Improvement in BCVA at All Timepoints - Observed Data

9. Statistical Interpretation

10. Statistical Methods Explained

What does a response percentage represent?

The primary outcome is binary: each participant is classified as having achieved or not achieved the ≥15-letter improvement threshold at Month 6. The response percentage is the share classified as responders within a group. This is different from a mean change in BCVA, which summarizes the average amount of change and can reflect improvements that do not reach the responder threshold. Neither summary fully describes the distribution of individual outcomes.

The endpoint’s missing-data rule is part of the definition used for the posted result. Participants with missing Month 6 BCVA measurements, rescue surgery before Month 6, or study discontinuation before Month 6 were imputed as non-responders. Thus, the estimates incorporate a specified assumption about those cases. The registry record does not report alternative imputation analyses or sensitivity analyses for this endpoint.

Why compare risk differences?

A risk difference expresses the difference between two groups’ response proportions on an additive scale. A value above zero indicates a higher response proportion in the first comparison group as defined by the analysis; a value below zero indicates a lower proportion. The recalculated comparisons are unadjusted and use the posted group summaries. They do not control for baseline characteristics or reproduce a model-based adjustment.

A confidence interval around a risk difference gives a range of values compatible with the data and the method’s assumptions. If the interval includes zero, the data do not clearly distinguish a difference in either direction using that interval as the criterion. If it excludes zero, the estimated difference is less compatible with zero under the same assumptions. This is not a measure of the probability that a particular hypothesis is true, and it does not capture every source of uncertainty, such as limitations in the design or missing-data assumptions.

Why does the registry report Fisher Exact tests?

Fisher Exact is a method for comparing categorical outcomes in two groups. It is useful when the data consist of responder and non-responder counts and group sizes are limited, because its calculation uses the observed categorical counts rather than relying on a large-sample approximation for the test. The registry reports Fisher Exact methods for the primary pairwise comparisons and gives differences in response rates, confidence intervals, and p-values.

A p-value measures how compatible the observed data are with a specified null model, under the assumptions of the test. It is not the probability that the null model is true, and it does not measure clinical importance. A small p-value is not proof that a finding will be reproduced, while a larger p-value does not establish that groups are equivalent. The size and precision of the estimated difference, the study design, and the analysis plan all matter.

Why can recalculated and sponsor results differ?

The recalculated risk differences and p-values are simple unadjusted re-calculations from the posted summary statistics. The registry’s own primary results report Fisher Exact analyses. Differences can arise from the specific procedure used to calculate the estimate, interval, or test, and from details that cannot be reconstructed from group-level summaries. The record flags a discrepancy between the recalculation and the sponsor’s reported analysis; for interpretation, the sponsor’s analysis takes precedence. The recalculation is useful as a transparency check, not as a replacement for the sponsor’s result.

The secondary continuous outcomes are reported as least-squares means and analyzed by the sponsor using ANCOVA. ANCOVA compares groups while adjusting for covariates included in the model. The registry results give adjusted least-square mean differences, confidence intervals, and p-values. The recalculations for those outcomes are unadjusted approximations based on posted means and standard errors, so they need not match the ANCOVA results. Details of the full model specification and covariates are not reported in the registry record.

The secondary outcome summaries also report standard errors. A standard error describes the estimated precision of a group mean; it is not the same as the spread of individual participant values. A large standard error generally corresponds to less precise estimation, while the value depends on both the variability of the data and the amount of information available. The registry reports the secondary outcomes as least-squares means, so these summaries should not be read as raw group averages without qualification.

Why does over-dispersion matter?

Over-dispersion is a general concern when a statistical model assumes less variability than the data contain. If the outcome varies more than the model allows, standard errors can be too small and confidence intervals too narrow, making apparent precision misleading. A binary responder outcome can also be affected by heterogeneity between participants or sites. The registry record does not report a model-based over-dispersion assessment for the primary outcome; Fisher Exact comparisons do not rely on a dispersion parameter in the way some regression models do.

These methods answer related but distinct questions. The binary endpoint asks how many participants crossed a threshold. The continuous BCVA outcome summarizes score change, and central corneal thickness (CCT) measures a different aspect of the cornea. Agreement across outcomes can strengthen a coherent interpretation, but different endpoint definitions, analysis populations, and statistical procedures mean the results are not interchangeable.

11. Confidence Intervals and Precision

The primary response percentages are estimates from groups with the sizes reported in the results. Confidence intervals express uncertainty around a comparison: they identify a range of effect sizes that are reasonably compatible with the observed data under the interval method. Wider intervals indicate less precision. The primary recalculated intervals are broad, so the point estimates should not be interpreted as exact measures of the differences between groups.

For the sponsor-reported primary comparisons, the neltependocel versus Y-27632 difference is 30.2, with a 95% confidence interval from 0.8 to 58.3. The higher-dose AURN001 versus Y-27632 difference is 35.7, with a 95% confidence interval from 5.9 to 61.6. These intervals are compatible with a range of possible differences, not only the reported point estimates. The neltependocel comparison has a reported p-value of 0.072, and the higher-dose AURN001 comparison has a reported p-value of 0.020. The sponsor’s analysis takes precedence over the discrepant simple recalculations.

The recalculated intervals also show why point estimates alone are incomplete. For the lower- and middle-dose AURN001 comparisons, the intervals include zero; for the neltependocel and higher-dose comparisons, they do not. This pattern describes uncertainty under the unadjusted recalculation and does not supersede the sponsor’s own reported tests. Nor does an interval that excludes zero eliminate concerns about small groups, multiple comparisons, missing outcomes, or the applicability of the analysis to other settings.

Confidence intervals are not guarantees that the true effect lies within the stated bounds. Their interpretation relies on the statistical procedure and its assumptions. The registry record does not report all details needed to independently reproduce every analysis, and no interval can resolve uncertainty arising from unreported design choices or selective reporting. Precision should therefore be judged together with the trial’s analysis plan, which is not reported in the registry record.

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 estimates are participants per arm for 80% power and participants per arm for 90% power. They are not total event counts; the total-events convention applies to time-to-event outcomes, whereas this binary responder outcome uses participants per arm. The display relates planning estimates to the observed effect and to smaller fractions of that effect.

The planning illustration assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. For each comparison, the effect to detect is the stated fraction of the observed effect. The 80% power column means the planning calculation targets an 80% chance of detecting an effect of that assumed size under the stated model and assumptions. The 90% power column targets a higher chance under the same assumptions, and consequently generally calls for more participants per arm.

Rows planning for 75% or 50% of the observed effect use smaller assumed effects than the row based on 100% of the observed effect. Smaller effects need more participants to distinguish them from random variation at the same significance level and target power. The estimates can therefore change substantially across the assumed effect sizes. This is not observed power: it is a planning illustration based on the observed effect, not a measure of the trial’s achieved ability to detect an effect.

The original trial design assumptions and any sample-size justification are not reported in the registry record. These illustrations should not be interpreted as the trial’s original enrollment target or as evidence that the study was adequately or inadequately powered. They show how planning requirements depend on the effect size selected and the assumptions stated for the calculation.

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, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.143; treatment proportion p₁ = 0.444; average p̄ = 0.294.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6441 = 1.2624.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6078 = 0.5115.
4. n = (1.2624 + 0.5115)² / (0.3016)² = 34.6, rounded up to 35 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
p0 <- 0.142857142857143                          # control proportion
p1 <- 0.444444444444444                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^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 (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(6041256)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 35 (80% power), 46 (90% power)
 75% of observed effect: n per arm = 58 (80% power), 77 (90% power)
 50% of observed effect: n per arm = 117 (80% power), 156 (90% power)
power.prop.test: 34.6 
Simulated power at n = 35 per arm: 0.814 (20000 replicates)

The simulation draws many pairs of event counts at the planned sample size and counts how often the two-proportion z-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The primary analyses reported by the sponsor use Fisher Exact tests and give differences in response rates with 95% confidence intervals and p-values. The simple recalculations use the posted group summaries to estimate unadjusted risk differences and related statistics. They are not the same analysis and do not adjust for additional information that may have been used in the sponsor’s procedure.

The registry flags a discrepancy between these recalculations and the sponsor’s analysis. For example, the sponsor reports a difference of 30.2 and p = 0.072 for neltependocel versus Y-27632, while the recalculated risk difference is 0.302 with p = 0.037. For higher-dose AURN001 versus Y-27632, the sponsor reports a difference of 35.7 and p = 0.020, while the recalculated risk difference is 0.357 with p = 0.014. These differences should not be resolved by selecting whichever result appears more favorable.

Because a discrepancy is flagged, the sponsor’s own analysis takes precedence for interpretation of the trial’s reported results. The recalculations remain useful as independent, unadjusted checks of the posted summaries, but they cannot establish why the estimates or p-values differ. Further details that would allow a complete reconciliation are not reported in the registry record.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint is a single defined responder outcome, but it is reported across several comparisons. The registry also lists multiple secondary outcomes and analyses. Testing many outcomes or contrasts increases the chance that at least one result will appear unusual under a no-effect model, even when each individual test uses a conventional significance threshold. Statistical adjustment or a prespecified hierarchy can address this issue, but the registry record does not report a multiplicity strategy. It is therefore not possible to determine from the record whether the reported p-values were adjusted or how confirmatory claims were intended to be controlled.

Missing data are particularly relevant to the primary endpoint because participants with missing Month 6 measurements, rescue surgery before Month 6, or discontinuation before Month 6 were imputed as non-responders. This is a stated analysis rule, not a direct observation that each such participant failed to improve. The resulting percentages depend on that classification. The registry record does not report the number of missing measurements or provide alternative analyses using other missing-data assumptions, so the effect of the rule on the estimates cannot be assessed from the registry entries.

The primary population is named as the Full Analysis Set. The record does not report further operational detail about this population in the primary outcome description. Group sizes are shown with the outcome results, but those figures alone do not explain all analysis-population decisions or whether every randomized participant contributed to every analysis.

The record also does not report the trial’s full statistical analysis plan, any interim analyses, or the original sample-size justification. These omissions limit assessment of prespecification, outcome selection, and the intended handling of multiple comparisons. They do not show that a particular analysis was improper; they mean that some safeguards and decisions cannot be evaluated from the registry record.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 5% reporting threshold.

Most frequent serious adverse event terms

Most frequent non-serious adverse event terms

Serious events with the highest arm-level rate: femur fracture (5.6%), hip fracture (4.8%).

The serious adverse event results are reported by group. One serious adverse event was recorded among participants at risk in the Y-27632 100 µM group, and one among those at risk in the neltependocel 1.0 × 10^6 group. No serious adverse events were recorded in the three AURN001 groups. Deaths are listed as 0 in every group. These counts describe the registry’s posted safety results and do not by themselves establish whether an event was caused by an intervention.

Other adverse events were recorded in each group, with the affected-participant counts shown alongside the corresponding at-risk group counts. The record lists Femur fracture at 5.6% and Hip fracture at 4.8% among the top serious adverse event terms. The registry entries do not identify the group attribution for those percentages, so they should not be assigned to a particular arm.

Safety counts require context: the groups are small, and event counts alone do not describe event severity, timing, duration, or causal assessment. The registry record does not report further details about those aspects in the safety details summarized for this analysis. These figures are a descriptive account of recorded adverse events, not a comprehensive estimate of safety in other populations or settings.

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

The results describe how often participants in each randomized group met the Month 6 visual-acuity responder definition, with specified missing or post-discontinuation cases treated as non-responders. The recorded percentages differ across groups, and the sponsor-reported comparisons include estimates with confidence intervals that convey considerable uncertainty. The outcome is relevant to the trial’s stated question, but it is only one measure at one follow-up time.

The findings do not establish that AURN001 or any individual component works or does not work. The trial compares several groups, and the estimates are based on limited group sizes. The record flags a discrepancy between unadjusted recalculations and the sponsor’s analyses; the sponsor’s own analysis takes precedence. The reported p-values should be interpreted in light of the multiple outcomes and comparisons and the absence of a reported multiplicity plan.

A threshold responder outcome does not show the full range of visual-acuity changes. It cannot describe whether non-responders had small improvements, no change, or worsening, nor how far responders exceeded the threshold. The secondary BCVA and CCT outcomes provide different summaries, but they do not eliminate uncertainty in the primary result or establish a complete picture of the clinical course.

The findings also do not establish longer-term outcomes or apply automatically beyond the trial population. The study’s reported Month 6 endpoint and safety counts should be considered as results from this specific randomized Phase 1/2 study. The registry record does not report all design and analysis details needed to assess every potential source of bias, including the original sample-size assumptions, the full statistical plan, and the handling of multiplicity.

18. Why This Trial Matters Statistically

This study illustrates why the definition of an endpoint matters. A threshold-based responder percentage is easy to interpret as the frequency of a specified improvement, but it discards information about the amount of change above or below the threshold. Reading it alongside continuous BCVA change helps distinguish a responder question from an average-change question. CCT adds a separate type of outcome rather than serving as another version of the same measure.

The comparison of a combination product with component groups also raises an important design question: whether observed differences can be attributed to the combination, a component, or dose. The registry describes comparisons of AURN001 doses with neltependocel alone and Y-27632 alone, but does not report a formal component-interaction analysis. Simple pairwise contrasts should not be mistaken for a complete evaluation of how components contribute or interact.

The record further shows why posted sponsor analyses and recalculations from summary statistics must be distinguished. The methods and results are not interchangeable, and a flagged discrepancy makes it particularly important to give precedence to the sponsor’s reported analysis while explaining what the unadjusted check does and does not tell readers.

Finally, multiple endpoints, missing-data rules, and uncertainty intervals shape interpretation as much as point estimates do. The registry’s explicit non-responder imputation rule clarifies one important choice, while the lack of a reported multiplicity plan and full statistical analysis plan leaves other interpretive questions open. These are central statistical considerations when reading a multi-arm clinical trial, not minor technical details.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.
• Participant counts were reconstructed from posted percentages and arm sizes, so small rounding differences are possible.

The primary outcome results are based on relatively small groups, and the confidence intervals are broad. This limits precision and means that the point estimates may not represent the true differences closely. The trial includes several active comparison groups, but the posted primary comparisons use Y-27632 100 µM as the reference for the recalculations and sponsor-reported pairwise results. These contrasts do not answer every possible comparison among groups.

The primary endpoint applies a non-responder imputation to participants with missing Month 6 BCVA, rescue surgery before Month 6, or discontinuation before Month 6. The registry does not report the number of participants affected by each circumstance or sensitivity analyses under alternative assumptions. The resulting response percentages should be understood in the context of this rule.

The record flags differences between the simple unadjusted recalculations and sponsor analyses. The sponsor’s analysis takes precedence, but the registry entries do not provide enough detail to reconcile every difference. For secondary continuous outcomes, the recalculations are approximations based on summary statistics, whereas the reported sponsor analyses use ANCOVA. Details of the complete model specification are not reported.

The registry identifies multiple outcomes and analyses but does not report a multiplicity plan. It also does not report the original sample-size justification, the full statistical analysis plan, or interim analyses. Masking is described inconsistently: the design field says quadruple, while the official title says double-masked; the masked roles are not reported. These limitations restrict assessment of prespecification and the exact conduct of the analyses.

Safety findings are descriptive and the registry entries do not give further event-level detail, such as timing, severity, or causal assessment. Follow-up beyond the stated Month 6 primary outcome is not described in the registry record for this analysis. Conclusions should remain tied to the outcomes and timeframes reported in the registry.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: A Phase 1/2 Study of AURN001 in Subjects With Corneal Edema Secondary to Corneal Endothelial Dysfunction (ABA-1) — NCT06041256.
• Registry record last updated 2025-12-17; status last verified 2025-12.
• Results first posted 2025-12-17.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT06041256 is a completed, randomized Phase 1/2 parallel-arm study sponsored by Aurion Biotech. The official title describes a multicenter, prospective study of AURN001 for corneal edema secondary to corneal endothelial dysfunction. The registry lists enrollment of 97, a start date of 2023-10-18, and a primary completion date of 2024-10-25.

The primary outcome is the percentage achieving a ≥15-letter BCVA improvement at Month 6, with missing Month 6 data and specified pre-Month 6 events imputed as non-response. The posted group percentages range from 10.5% to 50.0%. The registry reports Fisher Exact comparisons, while simple unadjusted recalculations differ; the sponsor’s analysis takes precedence because a discrepancy is flagged.

Secondary results include BCVA and CCT outcomes. Safety results list serious adverse events in two groups, none in the three AURN001 groups, and 0 deaths in every group. The record does not report the original sample-size assumptions, a multiplicity plan, or the full statistical analysis plan.