A Phase II Study of RBM-007 Alone and RBM-007 With Eylea® in Subjects With Wet Age-related Macular Degeneration: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for A Phase II Study of RBM-007 Alone and RBM-007 With Eylea® in Subjects With Wet Age-related Macular Degeneration (NCT04200248), a randomized phase 2 study. The primary outcome is Visual Acuity - Continuous.

2. Clinical Question

The trial was a randomized, double-masked, parallel-group phase II study. The clinical question is not simply whether vision changed within a group: it is whether the changes differ between the assigned regimens. The reported comparisons use sham plus RBM-007 as the reference for both RBM-007 plus aflibercept and sham plus aflibercept. That reference matters when reading estimates: the comparison does not directly quantify the difference between the combination arm and aflibercept monotherapy.

The study also assessed safety and other eye-related outcomes. Those outcomes add context, but the primary question concerns the continuous visual-acuity measure at Week 16. The registry record does not report a longer-term primary visual-acuity result in the information summarized for this analysis.

3. Trial Design

NCT04200248 is a completed, randomized, double-masked, parallel-group phase II study sponsored by Ribomic USA Inc. The condition is exudative age-related macular degeneration. The registry records enrollment of 94. Its brief summary describes approximately eighty-one subjects, and the primary-outcome description specifies that results are for the population treated, with 8 subjects discontinuing before treatment.

The three posted arms are Sham + RBM-007, RBM-007 + Aflibercept, and Sham + Aflibercept. The study summary describes four monthly intravitreal RBM-007 injections in the monotherapy regimen and in the combination regimen, with aflibercept dosed every other month in the combination and active-control regimens. The design is active-controlled: the aflibercept-only regimen provides a reference treatment, while sham injections are part of the arm descriptions. “Double masked” indicates that masking was part of the trial design; further details of who was masked and how masking was maintained are not reported in the registry record.

The primary outcome is mean change in Best Corrected Visual Acuity from baseline to Week 16, measured in letters seen. The posted primary summaries give treated-population group means and standard errors. The registry lists visual acuity as a continuous primary outcome and lists categorical visual acuity, macular thickness, macular volume, fibrosis, and ocular safety among secondary outcomes. Two of the posted secondary outcomes include numerical summaries in the record.

The registry records a start date of 2019-12-02, primary completion on 2021-11-19, and status as completed. The original protocol’s statistical analysis plan, intended sample-size justification, and details of allocation concealment are not reported in the registry record. The numerical comparisons are unadjusted contrasts based on the posted summary statistics, not a substitute for a sponsor-reported adjusted analysis.

4. Participant Flow and Accounting

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

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Data presented for population treated (8 subjects discontinued before treatment)

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: Intent to treat

6. Primary Endpoint

The registry lists the primary outcome as Visual Acuity - Continuous, measured over Week 16.

The primary endpoint is the mean change in Best Corrected Visual Acuity from baseline to Week 16, expressed in letters seen. A change score describes how the measured visual acuity at follow-up differs from the baseline measurement. Reporting the mean change gives a group-level summary of the direction and average magnitude of change, while the standard error describes the precision of that estimated mean.

Visual acuity is directly relevant to the condition under study because it measures visual performance using a standardized letter-based assessment. It is a continuous outcome, so the analysis can retain gradations in change rather than reducing each participant’s result to a category. That can make between-group summaries more informative than a simple count of people classified as improved or not improved, though the mean alone does not reveal the full distribution of individual responses.

The endpoint is assessed at Week 16. It therefore represents a specified follow-up snapshot, rather than an outcome over the entire course of treatment or a direct measure of long-term durability. The trial summary says that safety, efficacy, and durability were assessed, but the primary endpoint described in the registry is the mean visual-acuity change at Week 16. Other questions about durability require results at later time points, which are not reported in the primary-outcome information used.

The registry states that the primary outcome population was treated and that 8 subjects discontinued before treatment. That population definition should be kept in mind when interpreting the reported means: these summaries are not explicitly described as an intention-to-treat analysis of everyone randomized.

7. Results Posted in the Registry

• RBM-007 + Aflibercept: mean -1.60 versus -6.10 on control; difference 4.50 (95% CI -0.28 to 9.28), standardized effect d = 0.49; z-test p = 0.065.
• Sham + Aflibercept: mean 2.40 versus -6.10 on control; difference 8.50 (95% CI 3.80 to 13.20), standardized effect d = 0.93; z-test p = <0.001.

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.

Macular Thickness Change

• 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:
  • RBM-007 + Aflibercept: mean -5.80 versus 36.50 on control; difference -42.30 (95% CI -77.63 to -6.97), standardized effect d = -0.62; z-test p = 0.019.
  • Sham + Aflibercept: mean -16.10 versus 36.50 on control; difference -52.60 (95% CI -87.46 to -17.74), standardized effect d = -0.78; z-test p = 0.003.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RBM-007 + Aflibercept 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 Sham + Aflibercept than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Macular Volume Change

• 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:
  • RBM-007 + Aflibercept: mean 0.01 versus 0.75 on control; difference -0.74 (95% CI -1.08 to -0.40), standardized effect d = -1.13; z-test p = <0.001.
  • Sham + Aflibercept: mean -0.01 versus 0.75 on control; difference -0.76 (95% CI -1.09 to -0.43), standardized effect d = -1.17; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for RBM-007 + Aflibercept 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 Sham + Aflibercept than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The posted secondary results for macular thickness and macular volume follow a directionally consistent pattern across the two comparisons: both aflibercept-containing arms have lower mean changes than Sham + RBM-007 at Week 16. The registry also lists categorical visual acuity, fibrosis change, and ocular safety as secondary outcomes, but numerical results for those listed outcomes are not reported in the registry record used for this analysis.

This broad pattern complements, but does not replace, the primary visual-acuity result. Anatomical measures such as macular thickness and volume describe different aspects of the eye than letter-based visual acuity. Agreement in direction across outcome types can be informative, but it does not show that one measure caused the other or that an anatomical change necessarily corresponds to a particular visual benefit. The record does not provide participant-level associations between these outcomes.

The secondary comparisons are unadjusted, and the registry does not report a multiplicity procedure or a prespecified testing hierarchy for them. When multiple outcomes and comparisons are examined, some apparently noteworthy findings can arise by chance. As a result, secondary p-values carry less confirmatory weight than a single prespecified primary test would carry under a defined analysis plan. Their estimates and confidence intervals remain useful as descriptive evidence, but they warrant cautious interpretation.

The registry record lists five secondary outcomes and reports six outcome measures overall, while numerical summaries are available for only some of the secondary outcomes in the information analyzed. The absence of posted numerical results for an outcome is not evidence that no effect occurred. It means that its result cannot be evaluated from the registry record. A complete assessment would require the outcome definitions, analysis populations, estimates, uncertainty, and multiplicity approach for the full set of secondary outcomes.

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

• Visual Acuity - Categorical
• Macular Thickness Change
• Macular Volume Change
• Fibrosis Change
• Safety - Ocular

9. Statistical Interpretation

10. Statistical Methods Explained

The outcome is continuous and summarized by a mean, which is the arithmetic average of the recorded change scores within a group. A mean is useful for describing the central group result but can conceal variation among participants. The registry reports standard errors alongside the means. A standard error estimates how much the sample mean would vary across repeated samples under a statistical model; it is not the same as the spread of individual participants’ measurements.

What does a mean difference describe?

A mean difference compares the average outcome in one group with the average outcome in a reference group. For the primary endpoint, the posted contrasts use Sham + RBM-007 as the reference. A positive difference means the estimated mean change is numerically higher in the comparison arm than in that reference arm. The estimate is expressed in the same unit as the outcome, letters seen. This contrast is not automatically a comparison between the two arms that do not serve as the reference.

The posted mean differences and confidence intervals are unadjusted recalculations from the arm-level summary statistics. They do not incorporate any covariate adjustment or additional trial-level analysis unless that is explicitly stated in the registry, and no such primary analysis is listed in the analysis information used. The discrepancy flag is false, so there is no recorded discrepancy between these recalculations and a sponsor analysis; no sponsor-reported analysis is listed for these outcomes.

How should the confidence interval be read?

A confidence interval gives a range of estimates compatible with the observed data under the assumptions of the calculation. It communicates precision: a narrower interval indicates less uncertainty about the estimated contrast, while a wider interval indicates more. For a difference in means, an interval that includes zero does not exclude no difference under the calculation. An interval entirely on one side of zero indicates that the range of estimates does not include zero, but it does not by itself establish clinical importance or remove concerns about bias, multiplicity, or generalizability.

The registry’s arm-level uncertainty is reported as standard error, and the pairwise estimates have confidence limits. These quantities are related but answer different questions: the standard error describes uncertainty in an individual group mean, while the confidence interval describes uncertainty in a contrast between group means. The interval should be considered together with the point estimate rather than reduced to a binary label.

What do unadjusted p-values say?

A p-value describes how unusual data at least as incompatible with a specified null model would be, if that model and the calculation assumptions were true. It is not the probability that the null hypothesis is true, nor is it a measure of the clinical importance of a result. The posted p-values are unadjusted. Because several outcomes and comparisons appear in the record, these values do not account for the full multiplicity of statistical testing. The registry record does not report a multiplicity correction or a hierarchy that would identify which tests were intended to be confirmatory.

A small unadjusted p-value can coexist with uncertainty about the size of an effect, and a larger p-value does not prove that groups are equivalent. In particular, the interval and estimate are needed to see whether the data are compatible with a range of potentially different effects. No equivalence margin or non-inferiority margin is reported in the registry record.

Why does over-dispersion matter?

General statistical explanation: over-dispersion occurs when observed variability is greater than a model assumes. If a model understates variability, standard errors can be too small and confidence intervals too narrow, making evidence appear more precise than it is. For a continuous mean, assumptions about the distribution and variability of observations affect inference. The registry’s summary statistics do not provide participant-level distributions, so skewness, outliers, and other features of the outcome cannot be assessed from these means and standard errors alone. The posted recalculations use the available summaries; they do not test whether the underlying data satisfy a particular distributional model.

The sample-size illustrations use a normal approximation and equal allocation between the two arms, with a two-sided significance level of 0.05. They use a stated fraction of the observed effect as the effect to detect. This is a general planning calculation based on the observed contrast, not a reconstruction of the trial’s original design. The registry record does not report the original sample-size assumptions or justification.

Finally, the treated-population definition matters. The registry says that 8 subjects discontinued before treatment, but the information does not specify how missing Week 16 observations were handled, whether imputation was used, or whether all treated participants contributed outcome data. Without that detail, the effect of missingness on the means and contrasts cannot be fully evaluated.

11. Confidence Intervals and Precision

Precision is best judged from the confidence interval alongside the point estimate. For RBM-007 + Aflibercept compared with Sham + RBM-007, the mean difference is 4.5 letters and the 95% confidence interval runs from -0.282 to 9.282. That interval includes zero and spans estimates ranging from a small negative difference to a larger positive difference. The point estimate alone therefore gives an incomplete account of what the data allow.

For Sham + Aflibercept compared with Sham + RBM-007, the estimated mean difference is 8.5 letters, with a 95% confidence interval from 3.802 to 13.2. This interval lies above zero, but it still covers a range of possible effect sizes. The estimate is more precise than an unsupported claim that the true difference equals exactly 8.5 letters.

These intervals describe sampling uncertainty under the calculation assumptions. They do not account for every source of uncertainty. In particular, they do not correct for multiple comparisons, establish that the analysis population was unbiased, or address missing-data assumptions. The registry record does not report an adjusted primary analysis or the method used to handle missing outcome data, so those issues remain unresolved.

Nor does statistical precision settle clinical importance. The record gives the outcome unit as letters seen but does not provide a threshold for a clinically meaningful difference. Thus the interval can be used to assess the range and direction of estimates, but the registry information does not define which values would be important to patients or clinicians.

The reported standard errors describe uncertainty in each arm’s mean, while the confidence intervals describe uncertainty in the between-arm mean differences. Both are useful, but they should not be conflated. The posted summaries offer a quantitative account of precision at Week 16; they do not establish how stable the contrast would be in a different population or over longer follow-up.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They illustrate the size of a future two-arm comparison under stated assumptions and are not the number enrolled in this trial. The calculation assumes a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set to the stated fraction of the observed effect. These assumptions are planning assumptions for the illustration; the trial’s original design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a design with an 80% chance of detecting the specified effect under the calculation assumptions, if that effect is the true effect and the model assumptions hold. The 90% power column gives the corresponding planning count for a 90% chance. Power is a property of a planned study under assumptions, not a measure of how likely the observed result is to be true.

Rows using 100%, 75%, and 50% of the observed effect illustrate progressively smaller target effects. Smaller effects are harder to distinguish from random variation, so they require more participants per arm to achieve the same planned power, all else held fixed. The observed effect can be imprecisely estimated, especially in a relatively small study, so planning directly from it may produce optimistic estimates of future requirements. These figures are not observed power.

The curve should be read as a visual representation of the planning relationship between the assumed effect and the required sample size, not as additional trial evidence. The original enrollment and the treated-population numbers describe this study; the planning values describe hypothetical future comparisons under the stated calculation assumptions.

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 = 4.500; pooled standard deviation σ = 9.207.
2. n = 2 × (1.96 + 0.842)² × 9.207² / 4.500² = 65.7, rounded up to 66 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 <- 4.5                      # observed difference in means
sigma <- 9.20664779582469                     # 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(4200248)
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 = 66 (80% power), 88 (90% power)
 75% of observed effect: n per arm = 117 (80% power), 157 (90% power)
 50% of observed effect: n per arm = 263 (80% power), 352 (90% power)
power.t.test: 66.7 
Simulated power at n = 66 per arm: 0.795 (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

Several statistical questions remain unresolved in the registry record. It does not report whether the primary analysis used a prespecified hierarchy for comparisons, whether any multiplicity adjustment was planned, or whether secondary outcomes were considered confirmatory or exploratory. Because there are several treatment contrasts and multiple listed outcomes, unadjusted p-values should be interpreted as nominal evidence rather than as family-wise controlled findings.

The registry record also does not report the original statistical analysis plan, interim analyses, or the sample-size justification. These details would clarify which contrasts were planned, how the primary endpoint was to be analyzed, and how the investigators intended to control type I error. Their absence prevents a full comparison between the posted results and a prespecified analysis. No claim should be made about whether interim analyses occurred or whether the trial was powered for a particular contrast.

The primary outcome is described for the population treated, and the registry states that 8 subjects discontinued before treatment. It does not report the number of randomized participants included in each analysis population, the handling of participants who discontinued after treatment began, or the approach to missing Week 16 measurements. It is therefore not possible to determine from this record whether the primary analysis was intention-to-treat, per-protocol, or another defined population, or whether missing data were imputed.

These gaps matter because missingness can affect a group mean if participants without measurements differ systematically from those with observed outcomes. Different analysis populations or assumptions about missing outcomes can also change an estimate and its uncertainty. The posted summaries alone cannot establish the direction or size of any such influence.

Finally, the record lists a randomized and double-masked design but does not give enough operational detail to assess allocation concealment or the success of masking. Randomization and masking are important design protections, but their presence in the registry description does not eliminate every potential source of bias. The posted calculations should therefore be read with both the reported design features and the missing analysis details in view.

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: iritis (7.1%), vitritis (7.1%), eye pain (3.6%), neovascular age-related macular degeneration (3.4%), vision blurred (3.4%).

The registry reports serious adverse events for each arm using a safety population whose at-risk counts differ from the primary outcome arm counts. In Sham + RBM-007, 2 serious adverse events are reported among 28 at risk; in RBM-007 + Aflibercept, 2 are reported among 29 at risk; and in Sham + Aflibercept, 1 is reported among 29 at risk. No deaths are reported in any arm.

These are counts, not evidence by themselves that one regimen is safer than another. The record does not provide a statistical comparison of serious adverse events, and the small counts make any comparison uncertain. The listed serious-event terms include Iritis and Vitritis at 7.1% each, Eye pain at 3.6%, and Neovascular age-related macular degeneration, Vision blurred, and Endophthalmitis at 3.4% each. Those percentages are reported terms in the registry; they should not be assigned to a treatment group without supporting group-specific information.

Other adverse events are reported as 15 among 28 at risk for Sham + RBM-007, 17 among 29 for RBM-007 + Aflibercept, and 8 among 29 for Sham + Aflibercept. These figures do not establish causality, severity beyond the serious-event classification, or comparative risk. Follow-up duration and detailed event definitions are not reported in the information.

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

The results show the observed Week 16 group means and unadjusted contrasts for visual-acuity change in this phase II trial. The Sham + Aflibercept arm had a higher mean change than Sham + RBM-007 in the posted comparison, with a confidence interval above zero. The RBM-007 + Aflibercept contrast also had a positive point estimate relative to Sham + RBM-007, but its confidence interval included zero. These are statements about the registry’s reported summaries, not definitive conclusions about treatment effectiveness.

The findings do not establish that RBM-007 plus aflibercept is better or worse than aflibercept monotherapy: the posted comparisons use Sham + RBM-007 as the reference, not a direct combination-versus-monotherapy contrast. Nor do the results show whether any observed change persists beyond Week 16. The study summary mentions durability as an objective, but later primary visual-acuity results are not reported in the information used.

The estimates also do not establish that the differences are clinically important. The registry reports the unit as letters seen, but the information does not specify a threshold for clinical importance. A p-value cannot supply that threshold, and statistical evidence does not on its own establish practical relevance.

These results should not be interpreted as proof of equivalence when a contrast is uncertain, or as proof of a causal explanation for changes in macular measures. The posted p-values are unadjusted, and missing-data handling and the original analysis plan are not reported. The analysis population is described as treated, with 8 subjects discontinuing before treatment. Together, these points limit how strongly the estimates can be generalized or treated as confirmatory.

The most defensible reading is that the trial offers early comparative evidence at a specified follow-up point, with estimates and uncertainty that can inform further study. It does not by itself settle comparative effectiveness, long-term durability, clinical importance, or safety differences.

17. Why This Trial Matters Statistically

This trial illustrates why a randomized comparison must be read through its actual reference groups and endpoints. The study has three regimens, but the posted primary contrasts compare the RBM-007-containing arms and the aflibercept-only arm with Sham + RBM-007. That structure makes it essential to distinguish an estimate relative to the reference from a direct comparison between the two non-reference arms.

It also shows the value of reading an estimate together with its confidence interval. The combination-versus-reference contrast has a positive point estimate, yet its interval includes zero. The aflibercept-only-versus-reference estimate has an interval above zero. These differences in precision and compatibility with zero are more informative than treating p-values as labels, although the unadjusted nature of the tests limits confirmatory interpretation.

The record offers another useful lesson: trial design information and analysis information are not interchangeable. Randomization, double masking, and an active control describe important design features, but they do not reveal the original analysis plan, missing-data methods, multiplicity strategy, or exact analysis populations. Those details are needed to judge how closely the posted results represent the intended primary analysis.

Finally, the case demonstrates why outcome families should be interpreted together but not conflated. Visual acuity is a functional measure, while macular thickness and volume are anatomical measures. A consistent direction across outcome types may be of interest, yet it does not make them interchangeable or prove that one explains another. The registry record supports a measured, descriptive reading of early phase II results rather than a sweeping conclusion.

18. Limitations

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

The primary outcome is reported for the treated population, and the registry notes that 8 subjects discontinued before treatment. The record does not detail how the treated population was defined, how many participants contributed Week 16 measurements, or how missing outcome data were handled. This limits evaluation of possible selection and missing-data effects.

The reported primary comparisons are unadjusted and use Sham + RBM-007 as the reference. They do not directly estimate the difference between RBM-007 + Aflibercept and Sham + Aflibercept. Multiple comparisons and outcomes are present, while a multiplicity plan is not reported. The unadjusted p-values therefore should not be treated as confirmatory evidence across the full set of analyses.

The registry record does not report the original sample-size justification, the statistical analysis plan, or whether interim analyses were conducted. It also does not provide the participant-level distributions needed to assess outliers, skewness, or the extent to which mean summaries represent individual results. The endpoint is measured at Week 16; longer-term primary outcome results are not included in the information analyzed.

Although safety counts are posted, the record does not provide inferential comparisons of adverse events or enough detail to attribute listed serious-event terms to particular arms. The numbers at risk for safety differ from the primary-outcome arm counts, so the populations behind those summaries should not be assumed to be identical.

Finally, the posted record describes the study as phase II and reports enrollment of 94, while its brief summary refers to approximately eighty-one subjects and the primary outcome specifies a treated population. These descriptions concern different record elements; the registry does not explain their relationship in the information. The findings should be interpreted within that reporting context.

19. Related Tutorials

20. Related Statistical Calculators

21. Sources

• ClinicalTrials.gov: A Phase II Study of RBM-007 Alone and RBM-007 With Eylea® in Subjects With Wet Age-related Macular Degeneration — NCT04200248.
• Registry record last updated 2023-06-08; status last verified 2023-04.
• Results first posted 2023-06-08.
• 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

NCT04200248 is a completed, randomized, double-masked, parallel-group phase II study of RBM-007 alone and RBM-007 with aflibercept in exudative age-related macular degeneration. Its active-control arm received sham plus aflibercept. The registry records enrollment of 94 and identifies Ribomic USA Inc as sponsor.

The primary endpoint is mean change in Best Corrected Visual Acuity from baseline to Week 16, measured in letters seen. Results are described for the treated population, with 8 subjects discontinuing before treatment. The posted summaries show different Week 16 mean changes across the three arms and unadjusted contrasts against Sham + RBM-007. Confidence intervals communicate substantial uncertainty for the combination contrast and a positive interval for the aflibercept-only contrast.

The registry also lists secondary outcomes and adverse-event counts. Interpretation is limited by unreported details on the original statistical plan, multiplicity, analysis populations, and missing-data handling. The results describe this trial’s recorded outcomes and do not establish long-term durability or a direct comparison between the combination and aflibercept monotherapy.