Efficacy and Safety of RTH258 Versus Aflibercept - Study 1: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Efficacy and Safety of RTH258 Versus Aflibercept - Study 1 (NCT02307682), a randomized phase 3 study. The primary outcome is Change From Baseline in Best Corrected Visual Acuity (BCVA) (Letters Read) at Week 48 - Study Eye.

2. Clinical Question

3. Trial Design

This was a Phase 3, randomized, double-masked, multicenter, parallel-group study comparing brolucizumab with aflibercept. The official title describes a two-year study and three treatment arms. The registry reports enrollment of 1775, a start date of 2014-12-08, primary completion on 2017-04-22, and completed status. These administrative details describe the trial record; they do not establish how many participants contributed data to each particular endpoint.

The arms were brolucizumab 3 mg, brolucizumab 6 mg, and aflibercept 2 mg. All three regimens began with injections at Day 0, Week 4, and Week 8. The brolucizumab maintenance regimen could be every 8 or every 12 weeks, while the aflibercept maintenance regimen was every 8 weeks. The registry descriptions do not provide the full rules used to determine maintenance intervals.

The primary outcome was change from baseline in best corrected visual acuity at Week 48 in the study eye. The primary analysis population was the Full Analysis Set using last observation carried forward. The endpoint description says one eye contributed to the analysis and defines baseline as the last measurement before first treatment.

The registry lists 33 outcome measures and 712 analyses, with 32 secondary outcomes posted. Detailed protocol information about allocation procedures, masking implementation, the planned statistical analysis, sample-size justification, interim analyses, and handling of multiplicity is not reported in the registry record. The enrollment figure should therefore not be mistaken for the analysis count at every endpoint.

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: Of the 1775 subjects enrolled in the study, 693 were exited prior to randomization as screen failures. This reporting group includes all randomized subjects.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) - 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: This analysis population includes all randomized subjects who received at least 1 IVT injection of study treatment (Full Analysis Set).

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in Best Corrected Visual Acuity (BCVA) (Letters Read) at Week 48 - Study Eye, measured over Baseline, Week 48.

The primary endpoint measured change in best corrected visual acuity (BCVA) from baseline to Week 48 in the study eye. BCVA was assessed with spectacles or other visual corrective devices using Early Treatment Diabetic Retinopathy Study testing at 4 meters. Results were recorded as letters read correctly. The registry defines baseline as the last measurement before first treatment and states that a gain in letters indicates improvement. One eye contributed to this endpoint.

BCVA provides a standardized continuous measure of visual performance, so the trial could compare average changes across randomized groups. A continuous outcome retains information about the size of change rather than reducing the result to a binary category such as improved or not improved. The reported arm summaries are means and standard deviations, which describe average change and variability among the observations included in the analysis.

The primary endpoint is one component of the trial’s assessment. It captures visual acuity at a specified follow-up visit, while secondary measures include average changes across visit periods and treatment-interval status. Those outcomes address related but distinct questions and should not be treated as interchangeable with the Week 48 primary endpoint.

The Full Analysis Set with last observation carried forward was the stated primary analysis population. The registry does not provide the missing-data assumptions or sensitivity analyses that would help assess how carrying forward an earlier observation affected the endpoint estimate.

7. Results Posted in the Registry

• Brolucizumab 6 mg: mean 6.40 versus 5.90 on control; difference 0.50 (95% CI -1.54 to 2.54), standardized effect d = 0.04; z-test p = 0.631.
• Aflibercept 2 mg: mean 7.00 versus 5.90 on control; difference 1.10 (95% CI -0.85 to 3.05), standardized effect d = 0.08; z-test p = 0.269.

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.

Average Change From Baseline in BCVA (Letters Read) Over the Period Week 36 Through Week 48 - Study 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:
  • Brolucizumab 6 mg: mean 6.50 versus 6.00 on control; difference 0.50 (95% CI -1.49 to 2.49), standardized effect d = 0.04; z-test p = 0.623.
  • Aflibercept 2 mg: mean 6.90 versus 6.00 on control; difference 0.90 (95% CI -1.00 to 2.80), standardized effect d = 0.07; z-test p = 0.354.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Brolucizumab 6 mg and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept 2 mg and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Subjects With Positive q12 (Every 12 Weeks) Treatment Status at Week 48

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Brolucizumab 6 mg: 0.6% (2/360) versus 0.6% (2/358) on control; risk difference -0.0 percentage points (95% CI -1.1 to 1.1), risk ratio 0.99 (0.14–7.02); unadjusted two-proportion z-test p = 0.996.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Brolucizumab 6 mg and the control. The interval gives the range of effects that remain compatible with the data.

Proportion of Subjects With Positive q12 Treatment Status at Week 48 Within the Subjects With no q8 (Every 8 Weeks) Treatment Need During the First q12 Cycle (Week 16, Week 20)

• Endpoint type: Binary: the percentage of participants with the event (counts rebuilt from the posted percentages and group sizes).
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Brolucizumab 6 mg: 0.9% (2/222) versus 1.0% (2/208) on control; risk difference -0.1 percentage points (95% CI -1.9 to 1.8), risk ratio 0.94 (0.13–6.59); unadjusted two-proportion z-test p = 0.948.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Brolucizumab 6 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes extend the primary question in several directions: average BCVA change over periods of visits, change at individual post-baseline visits, and whether participants met a treatment status involving every-12-week dosing. Some outcomes assess status over a broader follow-up period, and some restrict the analysis to participants without a need for every-8-week treatment during an initial interval. Together, these outcomes describe visual acuity over time and treatment-interval experience rather than only the Week 48 change.

For the posted continuous secondary outcomes, the group averages and recalculated comparisons generally follow the same broad pattern as the primary endpoint: the average changes are close across the active treatment groups, and the unadjusted contrast intervals include zero. The treatment-status outcomes report proportions with substantial uncertainty in the recalculated contrasts. These patterns can provide context, but they should not be treated as independent confirmation of the primary result or as proof of equivalence.

Secondary outcomes are related to the primary endpoint but answer different questions. Averages over a span of visits can smooth short-term variation, while a Week 48 value concerns a single visit. Treatment-status measures concern dosing interval criteria rather than visual acuity itself. Agreement across these measures may be reassuring about consistency, but differences are also possible because the outcomes, analysis groups, and timeframes are not identical.

Many outcomes and analyses are listed in the registry, and the multiplicity strategy is not reported in the registry record. In general, when many comparisons are examined, isolated small p-values or apparently favorable patterns can occur by chance. Unadjusted secondary findings therefore carry less inferential weight than a prespecified primary analysis with a clearly reported testing plan. The full sponsor analyses for secondary outcomes are not all listed in the presented record, so the secondary pattern should be interpreted descriptively rather than as a set of definitive tests.

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

• Average Change From Baseline in BCVA (Letters Read) Over the Period Week 36 Through Week 48 - Study Eye
• Proportion of Subjects With Positive q12 (Every 12 Weeks) Treatment Status at Week 48
• Proportion of Subjects With Positive q12 Treatment Status at Week 48 Within the Subjects With no q8 (Every 8 Weeks) Treatment Need During the First q12 Cycle (Week 16, Week 20)
• Proportion of Subjects With Positive q12 Treatment Status up to Week 96
• Proportion of Subjects With Positive q12 Treatment Status at Week 96 Within the Subjects With no q8 Treatment Need During the Initial q12 Cycle (Week 16, Week 20)
• Change From Baseline in BCVA (Letters Read) at Each Post-baseline Visit - Study Eye
• Average Change From Baseline in BCVA (Letters Read) Over the Period Week 4 to Week 48/96 - Study Eye
• Average Change From Baseline in BCVA (Letters Read) Over the Period Week 12 to Week 48/96 - Study Eye

9. Statistical Interpretation

10. Statistical Methods Explained

The main endpoint is continuous: each participant’s BCVA change is measured in letters, and the registry reports group means with standard deviations. A mean gives the average observed change within a group. A standard deviation describes how dispersed individual changes are around that group average. A standard deviation is not a confidence interval for the mean and does not show how certain the estimated treatment contrast is.

What does a mean difference describe?

A mean difference compares two group averages, with the order of groups determining its sign. In the recalculations, the reference is brolucizumab 3 mg. A positive estimate means the other group’s posted mean is higher in this unadjusted comparison; a negative estimate means it is lower. The recalculated values use the posted summary statistics and are not adjusted for covariates or other trial features. They are not a substitute for the sponsor’s analysis. Since the record flags a discrepancy, the sponsor’s own analysis takes precedence.

Why are the sponsor estimates different?

The sponsor reports least squares mean differences from ANOVA, whereas the recalculations are simple, unadjusted comparisons of posted means. A least squares mean is an estimate from a statistical model, and an ANOVA comparison can account for the model specified by the analysis. Differences in estimands, adjustment, analysis populations, or implementation can yield estimates that differ from a simple contrast. The registry record does not report enough detail to identify the particular reason for the discrepancy. It would not be appropriate to infer that the two methods are estimating precisely the same quantity.

The sponsor labels its reported analyses as non-inferiority. In general, a non-inferiority analysis asks whether the data rule out a loss larger than a prespecified acceptable margin. The confidence interval and the margin are interpreted together; a p-value by itself is not enough to determine the conclusion. The non-inferiority margin, hypotheses, and full testing procedure are not reported in the registry record. Therefore, the listed analyses can be described as sponsor-reported non-inferiority analyses, but the margin-based decision cannot be independently reconstructed from the registry information.

What does a confidence interval contribute?

In general, a confidence interval expresses the uncertainty around an estimated quantity under the assumptions of its statistical method. For a difference, an interval that includes zero is compatible with no difference under that method, but it does not prove that the groups are equivalent. For a non-inferiority question, the relevant boundary is the non-inferiority margin, not simply zero. The sponsor’s intervals are posted with its least squares mean differences; the recalculated intervals concern unadjusted mean differences and should not be substituted for the sponsor’s inferential procedure.

The primary analysis population is described as the Full Analysis Set with last observation carried forward. In general, last observation carried forward replaces a missing later measurement with an earlier recorded value. This approach can make assumptions about what would have happened after the last observation. Its validity depends on the missingness process and the clinical course; the registry record does not report the missing-data sensitivity analyses needed to assess robustness. No missing counts or reasons should be inferred from the summary information.

Why can secondary outcomes be harder to interpret?

The registry includes multiple outcome measures and analyses, including repeated-visit changes, period averages, and proportions with treatment-interval status. In general, testing many outcomes or comparisons increases the chance of at least one apparently notable result arising by chance if no multiplicity adjustment is applied. The statistical plan and multiplicity procedure are not reported in the registry record. For that reason, secondary findings should be read as supporting or exploratory evidence unless their prespecification and error-control approach are known.

For binary outcomes, a proportion describes the fraction of the analysis group meeting a defined status. A confidence interval around a proportion describes uncertainty in that estimate. The registry also supplies recalculated comparison statistics for some secondary outcomes, but these do not replace sponsor analyses. In general, sparse event counts can make binary contrasts imprecise, and ordinary approximations may be less reliable when counts are small. This is a general statistical caution, not a claim that a particular secondary result is invalid.

Power is the probability, under a specified model and assumed effect, that a planned test will reject its null hypothesis. The planning figures accompanying these results use a stated illustrative calculation, not the trial’s original design calculation. They are not observed power. Observed power cannot repair uncertainty in an estimate or add information beyond the effect estimate and its confidence interval.

11. Confidence Intervals and Precision

Precision concerns how narrowly the data estimate a quantity. For the recalculated primary comparison of brolucizumab 6 mg with brolucizumab 3 mg, the unadjusted mean difference was 0.5 letters and its 95% confidence interval was -1.541 to 2.541. For aflibercept 2 mg compared with brolucizumab 3 mg, the unadjusted difference was 1.1 letters and its 95% confidence interval was -0.850 to 3.05. These intervals include zero and span both negative and positive contrasts. They therefore leave uncertainty about the direction and size of the unadjusted differences.

The sponsor-reported least squares mean difference for brolucizumab 3 mg compared with aflibercept was -0.6, with a 95% confidence interval from -2.5 to 1.3. For brolucizumab 6 mg compared with aflibercept, the reported difference was -0.2, with a 95% confidence interval from -2.1 to 1.8. These are model-based sponsor estimates and are the relevant reported analyses for interpreting the trial’s stated non-inferiority assessment. The registry record does not give the non-inferiority margin, so the intervals cannot be assessed against that criterion from the record alone.

In general, a confidence interval is not a probability statement that the fixed treatment effect lies within the particular interval. It describes the range of values compatible with the data and method at the stated confidence level. A broad interval indicates less precision than a narrow one. Neither a confidence interval crossing zero nor a non-significant conventional p-value proves equivalence, absence of an effect, or clinical irrelevance.

Variability in individual BCVA changes is reflected in the posted standard deviations. The group means are estimates, not predictions for each participant. Interpretation should distinguish that individual-level variation from uncertainty in a group contrast. The registry does not report additional details such as confidence intervals for all arm means or a clinically important difference threshold.

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 sample-size figures are planning illustrations calculated from the observed effect, not a record of how the trial’s original size was chosen. For continuous outcomes, the displayed values are participants per arm. The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The assumed effect is the stated fraction of the observed effect. The time-to-event convention would be total events, but the outcomes discussed for this study are not time-to-event planning rows.

The 80% power column gives the illustrative number of participants per arm that would be needed, under those assumptions, for an 80% chance of detecting the specified effect if that effect were the true one. The 90% power column uses a higher target chance of detection and consequently requires more participants under the same assumptions. These are design calculations for hypothetical future studies, not evidence about the probability that the observed result is true.

Rows that plan for 75% or 50% of the observed effect assume a smaller target difference. Smaller effects are harder to distinguish from random variation, so they require more participants under the stated assumptions. The observed effect may itself be uncertain, particularly when the estimate is small or imprecise; using it as a planning value does not make it a dependable forecast of a future effect.

These figures are not observed power. They should not be read as a retrospective score of whether the trial was adequate, nor should they override the confidence intervals or the sponsor’s reported analysis. The registry record does not report the original sample-size justification or the assumptions used when designing the trial.

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 = 0.500; pooled standard deviation σ = 13.954.
2. n = 2 × (1.96 + 0.842)² × 13.954² / 0.500² = 12,225.8, rounded up to 12,226 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 <- 0.5                      # observed difference in means
sigma <- 13.9536911527993                     # 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(2307682)
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 = 12,226 (80% power), 16,367 (90% power)
 75% of observed effect: n per arm = 21,735 (80% power), 29,097 (90% power)
 50% of observed effect: n per arm = 48,904 (80% power), 65,468 (90% power)
power.t.test: 12226.7 
Simulated power at n = 12,226 per arm: 0.804 (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. Analyses Reported by the Sponsor

The registry’s sponsor-reported primary analyses are ANOVA estimates of least squares mean differences, classified as non-inferiority analyses. The recalculations are simple, unadjusted comparisons based on posted group means and standard deviations. They address the same named endpoint but are not the same analysis method or necessarily the same estimand.

The sponsor reported a least squares mean difference of -0.6 for brolucizumab 3 mg compared with aflibercept, with a 95% confidence interval from -2.5 to 1.3 and p < 0.001. For brolucizumab 6 mg compared with aflibercept, the estimate was -0.2, with a 95% confidence interval from -2.1 to 1.8 and p < 0.001. The registry record identifies these as non-inferiority analyses. Their p-values should not be interpreted as ordinary tests showing that the treatments differ in average BCVA change.

The registry flags a discrepancy between sponsor analyses and recalculated contrasts. Accordingly, the sponsor’s own analysis takes precedence. The recalculations are useful as a transparent check on the posted summaries, but they cannot replace the model-based sponsor results or resolve why the estimates differ. The non-inferiority margin and enough detail to reproduce the sponsor model are not reported in the registry record. A reader therefore cannot independently verify the margin-based conclusion from the registry information alone.

15. Multiplicity, Missing Data and Analysis Populations

The registry record lists a primary endpoint alongside numerous secondary outcomes and analyses. The primary endpoint is change in BCVA at Week 48. Secondary measures include repeated-visit acuity results, period averages, and treatment-interval status. Examining several outcomes can be useful for understanding different aspects of a trial, but it also raises a multiplicity question: how was the overall risk of false-positive findings managed across the planned tests?

The multiplicity adjustment strategy, hierarchy of endpoints, and prespecified testing sequence are not reported in the registry record. Consequently, an unadjusted p-value from an individual secondary comparison should not automatically be read as confirmatory evidence. The registry information does not establish whether a particular secondary analysis was prespecified or whether it was part of a controlled testing family.

The primary population is named as the Full Analysis Set with last observation carried forward. The registry defines baseline as the last measurement before first treatment, and describes one study eye contributing to the primary analysis. Details about participant exclusions, missing observations, reasons for missingness, and sensitivity analyses are not reported in the registry record. Last observation carried forward is a missing-data method; in general, its use requires assumptions about the unobserved outcome after the last measurement. The record does not show how those assumptions were evaluated.

The sample-size assumptions used for the original trial design are not reported in the registry record. The planning illustrations associated with the posted summaries have their own stated assumptions, but they do not document the sponsor’s original design rationale. Interim analyses, stopping rules, and any associated adjustment to the analysis are also not reported in the registry record. These omissions limit independent assessment of how the statistical plan was specified and implemented.

These gaps do not negate the posted results, but they constrain what can be concluded from registry information alone. In particular, they prevent a full audit of multiplicity control, missing-data robustness, and non-inferiority decision rules.

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: pneumonia (2.8%), coronary artery disease (1.7%), cardiac failure congestive (1.7%), chronic obstructive pulmonary disease (1.7%), atrial fibrillation (1.1%).

The registry reports serious adverse event counts and other adverse event counts for each treatment group, with the group at-risk counts also listed. Serious adverse events were reported for 94 of 358 participants in the brolucizumab 3 mg group, 95 of 360 in the brolucizumab 6 mg group, and 114 of 360 in the aflibercept 2 mg group. Other adverse events were reported for 239 of 358, 228 of 360, and 228 of 360, respectively. Death counts were 9, 8, and 12, respectively.

These are descriptive counts, not adjusted comparisons. The adverse-event summary does not establish that an event was caused by treatment, and the counts alone do not account for event timing, duration, severity beyond the serious classification, or differences in exposure. The registry lists pneumonia at 2.8% as the most frequent serious adverse event term shown, followed by coronary artery disease, cardiac failure congestive, and chronic obstructive pulmonary disease at 1.7% each, and atrial fibrillation and cholelithiasis at 1.1% each.

Safety findings should be interpreted alongside the trial’s follow-up and complete adverse-event reporting. Further detail about event definitions, exposure-adjusted analyses, and attribution is not reported in the registry record. These counts are not medical advice and should not be used alone to assess individual risk.

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

The results describe a randomized comparison of brolucizumab at two dose levels with aflibercept in participants with untreated active choroidal neovascularization secondary to age-related macular degeneration. At Week 48, the posted mean BCVA changes were 5.9 letters for brolucizumab 3 mg, 6.4 letters for brolucizumab 6 mg, and 7.0 letters for aflibercept 2 mg. The sponsor reported model-based analyses designated as non-inferiority analyses.

The sponsor’s analyses and the recalculated unadjusted comparisons should not be conflated. The sponsor’s least squares mean estimates and confidence intervals are the controlling reported analyses because the registry flags a discrepancy. The registry does not report the non-inferiority margin, however, so readers cannot fully reconstruct the non-inferiority decision from the posted information. The recalculations provide a simple comparison of the arm summaries, not a replacement for that decision.

These results do not establish that the treatments are identical, that any observed difference is clinically important, or that one treatment is preferable. A confidence interval that includes zero in an unadjusted difference analysis does not prove equivalence. Conversely, a statistically significant p-value in a non-inferiority analysis does not by itself communicate the size or clinical importance of an effect; interpretation depends on the prespecified margin and analysis plan.

The primary endpoint concerns one measure of visual acuity at a specified follow-up visit. Secondary outcomes add information about changes across visits and treatment intervals, but they do not answer every question about vision, durability, or safety. Results apply to the trial setting, populations and endpoint definitions described in the registry, and should not be generalized beyond those details without further evidence. The findings are statistical evidence from a clinical trial, not individualized treatment guidance.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares two doses of an investigational treatment with an active comparator in a randomized, double-masked, parallel-group design. Randomization is intended in general to support fair comparisons by balancing prognostic factors on average, while masking can reduce some forms of measurement and conduct bias. The registry identifies these design features but does not give the procedural details needed to assess their implementation.

The primary endpoint is a continuous measure, allowing the analysis to retain information about the magnitude of BCVA change. Its interpretation also illustrates why the analysis framework matters: the sponsor reported non-inferiority analyses, while summary-statistic recalculations provide ordinary unadjusted mean contrasts. Those methods answer related but distinct inferential questions, and a discrepancy makes it especially important to distinguish the sponsor’s reported analysis from a simple recalculation.

The record also shows why precision and design assumptions matter. The posted means are accompanied by substantial variation, and the estimated contrasts have uncertainty. Planning illustrations based on observed effects are not evidence of observed power and cannot recover the original design rationale. The non-inferiority margin, original sample-size justification, multiplicity plan, and missing-data sensitivity analyses are not reported in the registry record.

Finally, the secondary outcomes and safety counts underscore that a trial can address multiple dimensions of benefit and risk. They require different methods and careful interpretation, especially when many outcomes are posted. The record is useful for understanding the scope and reported findings of the study, while its missing methodological details limit independent reconstruction of the sponsor’s full statistical argument.

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.

Several limitations specific to this record affect interpretation. First, the registry identifies sponsor analyses as non-inferiority analyses but does not report the non-inferiority margin. Without that margin, the least squares mean differences and confidence intervals cannot be independently checked against the decision criterion. The record also does not provide enough model detail to reproduce those sponsor estimates.

Second, the registry flags a discrepancy between the sponsor analyses and simple recalculations from the posted summaries. The recalculations are unadjusted, while the sponsor reports ANOVA least squares mean differences. The reason for the discrepancy is not reported in the registry record. The sponsor analysis takes precedence, but the absence of further detail limits independent reconciliation.

Third, the primary analysis uses last observation carried forward. The record does not report missing-data counts, reasons for missingness, or sensitivity analyses. Because this approach carries an earlier observation forward, conclusions can depend on assumptions about outcomes after the last observed measurement.

Fourth, the multiplicity strategy for the many posted outcomes and analyses is not reported. That makes it difficult to distinguish confirmatory secondary findings from descriptive or exploratory results. The original sample-size justification, interim analyses, and full statistical plan are also not reported in the registry record.

Finally, the available summary information does not provide full context for the safety counts, such as exposure-adjusted analyses or event attribution. The safety figures are descriptive and do not alone establish causality. These constraints do not erase the reported findings, but they narrow the claims that can be supported from the registry information.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Efficacy and Safety of RTH258 Versus Aflibercept - Study 1 — NCT02307682.
• Registry record last updated 2025-01-16; status last verified 2025-01.
• Results first posted 2019-10-31.
• 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

The completed Phase 3 study randomized participants in a double-masked, multicenter, three-arm comparison of brolucizumab 3 mg, brolucizumab 6 mg, and aflibercept 2 mg for neovascular age-related macular degeneration. The primary endpoint was change in BCVA letters read at Week 48 in the study eye, analyzed in the Full Analysis Set using last observation carried forward.

The registry posts arm means and standard deviations, sponsor ANOVA analyses classified as non-inferiority, multiple secondary outcomes, and adverse-event counts. It also flags a discrepancy between the sponsor analyses and unadjusted recalculations; the sponsor’s own analysis takes precedence. The non-inferiority margin, multiplicity approach, original sample-size justification, and missing-data sensitivity analyses are not reported in the registry record. Those omissions limit independent assessment of the full statistical plan and the sponsor’s margin-based conclusion.