Study of the Effects of High Dose Aflibercept Injected Into the Eye of Patients With an Age-related Disorder That Causes Loss of Vision Due to Growth of Abnormal Blood Vessels at the Back of the Eye: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study of the Effects of High Dose Aflibercept Injected Into the Eye of Patients With an Age-related Disorder That Causes Loss of Vision Due to Growth of Abnormal Blood Vessels at the Back of the Eye (NCT04423718), a randomized phase 3 study. The primary outcome is Change From Baseline in BCVA Measured by the ETDRS Letter Score at Week 48.

2. Clinical Question

3. Trial Design

The registry describes a randomized, double-masked, active-controlled, parallel-group phase 3 study of high-dose aflibercept in people with neovascular age-related macular degeneration. Its masking field specifies quadruple masking. The study lists Bayer as sponsor, an enrollment of 1011, a start date of 2020-08-11, primary completion on 2022-07-27, and a completed status. These record details describe the trial; they do not by themselves establish how participants were recruited, how allocation was concealed, or how masking was maintained. Those details are not reported in the registry record.

The listed groups were Aflibercept 2q8, Aflibercept HDq12, and Aflibercept HDq16. The comparator schedule was 2 mg every 8 weeks after a loading phase during Years 1 and 2; in Year 3, its description switches to high-dose aflibercept adjusted to individual response. The high-dose schedules began after an initiation phase, with intervals adjusted according to individual response. The arm descriptions do not provide the full dosing algorithm or the criteria used to change intervals.

The primary outcome was change from baseline in BCVA on the ETDRS letter scale at Week 48. The primary analysis population included randomized participants who received at least one dose, with the estimand mainly based on a hypothetical strategy. The registry lists 12 outcome measures and 19 analyses. It does not report the original sample-size justification, the planned non-inferiority margin, or a complete statistical analysis plan in the registry record described for this record. Consequently, those design choices cannot be reconstructed from the posted group summaries alone.

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: Overall, 1395 participants were screened, of whom 383 participants did not complete screening, 1 participant was randomized in error although he/she did not complete screening and had withdrawn consent. A total of 1011 participants were randomized in nearly equal numbers to 1 of the 3 treatment groups.

Main Study

Reasons for not completing this period:

Extension Phase

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set: included all participants who had been randomly assigned to study treatment and who received at least 1 dose of study treatment. Estimand mainly based on hypothetical strategy.

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: included all participants who had been randomly assigned to study treatment and who received at least 1 dose of study treatment.

6. Primary Endpoint

The registry lists the primary outcome as Change From Baseline in BCVA Measured by the ETDRS Letter Score at Week 48, measured over At baseline and Week 48.

The primary endpoint measures change from baseline in best-corrected visual acuity (BCVA) at Week 48, using the ETDRS letter score. BCVA was assessed in the study eye at a distance of 4 meters. The scale runs from 0, the worst score, to 100, the best score. The registry reports least-squares mean changes and standard errors for each treatment group.

Visual acuity is a direct measure of visual function and is relevant to a trial of neovascular age-related macular degeneration because the condition affects vision. A change score describes how the measure differs from baseline by the specified follow-up time; it is not the same as the score at Week 48 alone. Least-squares means are model-based group estimates rather than simple raw averages. The registry’s full model specification is not reported in the registry record, so the exact adjustments and assumptions behind those estimates cannot be evaluated from the summary information.

The endpoint is useful for comparing group-level changes, but it does not describe every participant’s experience. A group mean can conceal variation in individual outcomes, and the summary does not show how many participants improved, stayed similar, or worsened by particular amounts. The registry also lists a Week 60 BCVA change as a secondary outcome; it should not be confused with the Week 48 primary endpoint.

7. Results Posted in the Registry

• Aflibercept HDq12: mean 6.06 versus 7.03 on control; difference -0.97 (95% CI -3.06 to 1.12), standardized effect d = -0.07; z-test p = 0.364.
• Aflibercept HDq16: mean 5.89 versus 7.03 on control; difference -1.14 (95% CI -3.16 to 0.88), standardized effect d = -0.09; z-test p = 0.270.

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 Measured by the ETDRS Letter Score at Week 60

• 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:
  • Aflibercept HDq12: mean 6.37 versus 7.23 on control; difference -0.86 (95% CI -2.83 to 1.11), standardized effect d = -0.07; z-test p = 0.392.
  • Aflibercept HDq16: mean 6.31 versus 7.23 on control; difference -0.92 (95% CI -2.78 to 0.94), standardized effect d = -0.07; z-test p = 0.332.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept HDq12 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 HDq16 and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With no Intraretinal Fluid (IRF) and no Subretinal Fluid (SRF) in Central Subfield at Week 16

• 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:
  • Aflibercept HDq12: 61.6% (205/333) versus 51.6% (173/335) on control; risk difference 9.9 percentage points (95% CI 2.4 to 17.4), risk ratio 1.19 (1.04–1.36); unadjusted two-proportion z-test p = 0.010.
  • Aflibercept HDq16: 65.0% (217/334) versus 51.6% (173/335) on control; risk difference 13.3 percentage points (95% CI 5.9 to 20.7), risk ratio 1.26 (1.10–1.43); unadjusted two-proportion z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Aflibercept HDq12 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 proportion with the event is statistically higher for Aflibercept HDq16 than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Percentage of Participants Gaining at Least 15 Letters in BCVA From Baseline 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:
  • Aflibercept HDq12: 20.7% (69/334) versus 22.1% (74/335) on control; risk difference -1.4 percentage points (95% CI -7.6 to 4.8), risk ratio 0.94 (0.70–1.25); unadjusted two-proportion z-test p = 0.652.
  • Aflibercept HDq16: 21.7% (73/337) versus 22.1% (74/335) on control; risk difference -0.4 percentage points (95% CI -6.7 to 5.8), risk ratio 0.98 (0.74–1.31); unadjusted two-proportion z-test p = 0.893.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept HDq12 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 HDq16 and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover different aspects of vision and retinal anatomy, and their overall pattern is not identical across measures. The Week 16 fluid outcome shows higher reported percentages in the high-dose groups than in Aflibercept 2q8, while the Week 48 measures of letter gains and the Week 60 BCVA changes show broadly similar group estimates. These outcomes provide context alongside the primary Week 48 average change, but they do not replace it or resolve the uncertainty in the primary comparison.

The registry lists 12 outcome measures and 11 posted secondary outcomes. The outcomes have different measurement scales, time points, and analysis populations, so their estimates should not be combined into a single overall effect. Some are continuous changes, while others are percentages meeting a threshold or having a specified fluid status. A result on one measure does not automatically imply the same pattern on another.

In general, multiple outcomes create multiplicity: when many hypotheses are examined, chance findings become more likely unless the analysis plan addresses that issue. The registry record does not report a complete multiplicity strategy for these secondary analyses. The unadjusted recalculations are therefore exploratory and carry less weight than a prespecified primary analysis with a defined testing strategy. The secondary results can help describe the range of outcomes measured, but they should not be treated as independent confirmation of the primary finding without information on prespecification, adjustment, and the full analysis plan.

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

• Change From Baseline in BCVA Measured by the ETDRS Letter Score at Week 60
• Percentage of Participants With no Intraretinal Fluid (IRF) and no Subretinal Fluid (SRF) in Central Subfield at Week 16
• Percentage of Participants Gaining at Least 15 Letters in BCVA From Baseline at Week 48
• Percentage of Participants Achieving an ETDRS Letter Score of at Least 69 (Approximate 20/40 Snellen Equivalent) at Week 48
• Change in Choroidal Neovascularization (CNV) Size From Baseline to Week 48
• Change in Total Lesion Area From Baseline to Week 48
• Percentage of Participants With no Intraretinal Fluid (IRF) and no Subretinal Fluid (SRF) in the Center Subfield at Week 48
• Change From Baseline in Central Subfield Retinal Thickness (CST) at Week 48

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: it is a numerical change in ETDRS letter score. The registry reports a least-squares mean for each group, with standard error as the accompanying measure of uncertainty. A standard error describes uncertainty in an estimated mean; it does not describe how widely individual participants’ scores varied. The registry does not give the standard deviation for the endpoint, and the reported standard errors should not be read as individual-level variability.

What does a mean difference represent?

A mean difference compares the estimated change in one group with the estimated change in the comparator group. The simple recalculations use the posted group summaries and are unadjusted. The negative estimates indicate that the high-dose group’s posted mean change was lower than the comparator’s mean change in these calculations. A difference near zero would indicate similar estimated group means, while a difference farther from zero would indicate greater separation. Whether a separation is important depends on clinical context and the trial’s prespecified decision criteria, which are not fully reported in the registry record.

Why are there different analyses?

The recalculations are not the same as the sponsor’s reported mixed-model analyses. The sponsor reports differences in least-squares means, confidence intervals, p values, and non-inferiority classifications. Model-based estimates can account for features of the analysis specified in the statistical model, whereas a simple calculation from summary values does not reproduce that model. The full model details and non-inferiority margin are not reported in the registry record. Since the record identifies a discrepancy, the sponsor’s own analysis takes precedence; the recalculations are supplementary checks rather than replacements for the trial analysis.

What does non-inferiority mean?

In general, a non-inferiority study asks whether an intervention is not unacceptably worse than a comparator, using a margin defined before analysis. The margin sets the largest difference that the study would regard as acceptable for that purpose. A confidence interval and the prespecified margin must be considered together to evaluate the claim. The registry labels the posted primary comparisons as non-inferiority analyses, but the margin is not reported in the registry record. The listed p values, without the margin and fuller analysis context, are insufficient to independently verify the non-inferiority conclusion.

What is the role of the confidence interval?

In general, a confidence interval gives a range of values compatible with the data under the analysis and its assumptions. It helps show both the direction and precision of an estimate. When an interval includes zero for a difference, the data do not clearly distinguish the estimate from no difference at the corresponding confidence level. That observation does not prove that the groups are equivalent, nor does it by itself answer a non-inferiority question. The latter requires the relevant margin and analysis plan.

Why can binary outcomes use different methods?

Some secondary outcomes are percentages, such as the proportion meeting a specified fluid or visual-acuity criterion. Those outcomes describe whether participants met a condition rather than the average value of a continuous measure. The registry includes a Cochran-Mantel-Haenszel analysis for the Week 16 fluid outcome and Week 48 gain-of-letters outcome. In general, this method can compare categorical outcomes while accounting for strata. The stratification details are not reported in the registry record. Simple recalculations of binary outcomes are unadjusted and should not be treated as reproductions of the sponsor’s stratified analysis.

Why can over-dispersion matter?

In general, over-dispersion occurs when observed variation in count data exceeds what a simple statistical model assumes. If present and ignored, uncertainty estimates may be too small, making results appear more precise than warranted. The primary endpoint is a continuous score, not a count outcome, and the registry summary does not report an over-dispersion assessment. This general issue is therefore not a claim about the analysis used in this trial; it illustrates why the model and outcome type matter when interpreting statistical methods.

The primary analysis population includes randomized participants who received at least one dose, and the estimand is described as mainly based on a hypothetical strategy. In general, an estimand specifies the treatment effect of interest and how events such as treatment changes or missing outcome measurements are handled. The registry does not report enough detail to reconstruct all estimand components or the missing-data procedures. Those omissions limit independent assessment of how the analysis relates to the randomized treatment assignment.

11. Confidence Intervals and Precision

For the primary endpoint, the simple unadjusted recalculation for HDq12 versus Aflibercept 2q8 is -0.97, with a 95% confidence interval from -3.063 to 1.123. For HDq16 versus Aflibercept 2q8, it is -1.14, with a 95% confidence interval from -3.164 to 0.884. Each interval spans values below and above zero. Thus, these calculations leave uncertainty about the direction of any underlying difference, as well as its size.

The sponsor’s model-based intervals are -2.87 to 0.92 for HDq12 and -2.97 to 0.69 for HDq16, both at the 95% level. They also include zero. These intervals come from the sponsor’s mixed-model analyses and are not interchangeable with the recalculated intervals. Differences between intervals can arise because the analyses use different methods and assumptions. The sponsor analysis takes precedence for interpreting the trial’s reported result, but the registry record does not provide all details needed to independently assess the model or its non-inferiority margin.

In general, a confidence interval is a way to express statistical uncertainty around an estimate, conditional on the analysis and its assumptions. A narrower interval indicates greater precision than a wider interval for the same outcome and analysis. An interval that includes zero does not demonstrate equivalence, and the interval alone cannot establish clinical importance. For a non-inferiority question, the interval must be judged against the prespecified margin; that margin is not reported in the registry record. The standard errors accompanying the group estimates provide another measure of estimation uncertainty, not the range of individual responses.

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 based on the observed effect, not the trial’s original design assumptions. The stated assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For these continuous outcomes, figures are participants per arm. The record’s general guidance says time-to-event tables report total events, but these primary-endpoint illustrations are not time-to-event figures.

The 80% power column describes the planned number of participants per arm that would give an 80% chance of detecting the specified effect under the listed assumptions, if that effect and assumptions were correct. The 90% power column uses a higher target chance of detection and therefore generally requires more participants per arm. These are design-planning quantities, not a statement about what the completed trial was capable of demonstrating after its results were observed.

Each row scales the effect being targeted: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. Smaller effects are harder to distinguish from random variation, so the illustrations require more participants per arm as the assumed effect becomes smaller. The observed effect is an uncertain estimate, and basing a planning exercise on it can produce optimistic or unstable projections, especially when it is small. These calculations are not observed power. The original sample-size justification and assumptions used to design the trial are not reported in the registry record. The figures should therefore be read as conditional illustrations, not as evidence that the trial was adequately or inadequately sized for its original objective.

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 = -0.970; pooled standard deviation σ = 13.831.
2. n = 2 × (1.96 + 0.842)² × 13.831² / -0.970² = 3,191.5, rounded up to 3,192 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 <- -0.970000000000001                      # observed difference in means
sigma <- 13.8310020367041                     # 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(4423718)
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 = 3,192 (80% power), 4,273 (90% power)
 75% of observed effect: n per arm = 5,674 (80% power), 7,596 (90% power)
 50% of observed effect: n per arm = 12,767 (80% power), 17,091 (90% power)
power.t.test: 3192.5 
Simulated power at n = 3,192 per arm: 0.805 (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 sponsor’s primary analyses are reported as mixed-model comparisons of least-squares means and are labelled non-inferiority. The reported difference for HDq12 is -0.97 with a 95% confidence interval from -2.87 to 0.92; for HDq16 it is -1.14 with a 95% confidence interval from -2.97 to 0.69. The registry also lists p values of 0.001 and 0.001. The confidence intervals include zero, and the p values should be interpreted in the context of the sponsor’s specified non-inferiority analysis rather than as ordinary tests of a difference.

The simple recalculations produce the same reported point estimates, but their confidence intervals and unadjusted p values differ from the sponsor’s analyses. The recalculations use posted summaries and do not reproduce the mixed model. Because the record flags a discrepancy, the sponsor’s own analysis takes precedence for the trial’s inferential result; the recalculations are only supplementary, unadjusted checks. The registry does not report the non-inferiority margin or enough of the statistical plan to verify the sponsor’s conclusion independently. The reported p values alone cannot establish that the non-inferiority criterion was met.

15. Multiplicity, Missing Data and Analysis Populations

The record lists multiple outcome measures and analyses, including a primary Week 48 visual-acuity outcome and secondary outcomes at several follow-up times. In general, testing many outcomes or comparisons increases the chance that at least one result appears notable by chance. Statistical plans can address this through a hierarchy of tests, adjustment procedures, or by designating some analyses as exploratory. The multiplicity strategy for this trial is not reported in the registry record, so the role of any adjustment cannot be established from the summaries.

The primary analysis population is defined as the full analysis set: participants randomly assigned to treatment who received at least one dose. This differs from a strict intention-to-treat description that includes every randomized participant regardless of treatment received. The registry says the estimand is mainly based on a hypothetical strategy. In general, that means the treatment effect is framed under a hypothetical condition for certain post-randomization events, but the precise events and implementation are not detailed in the record summary.

Missing outcome data can affect both the population represented by the estimates and the uncertainty around them. The registry’s primary endpoint summary does not report the amount or pattern of missing Week 48 data, the assumptions made about missingness, or sensitivity analyses that test alternative assumptions. Those details are not reported in the registry record. Without them, it is difficult to judge how robust the estimates are to incomplete follow-up or deviations from the planned treatment strategy.

The sponsor’s reported analysis method is a mixed model, but the complete model specification, covariates, handling of intercurrent events, and multiplicity procedures are not reported in the registry record. The registry also does not report the non-inferiority margin. These are important elements for interpreting a non-inferiority result, because the analysis population, missing-data assumptions, and margin jointly shape the conclusion. Their absence does not invalidate the posted estimates, but it limits independent evaluation of how the reported conclusion was reached.

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: cataract (2.4%), urinary tract infection (1.9%), osteoarthritis (1.9%), pneumonia (1.5%), coronary artery disease (1.4%).

The registry reports adverse-event counts for serious events, other events, and deaths across treatment groups and specified follow-up periods. For Week 0- 96, the serious-event counts are 69 of 336 for Aflibercept 2q8, 83 of 335 for HDq12, and 72 of 338 for HDq16. The corresponding death counts are 12, 11, and 7. The record also reports combined high-dose counts and longer follow-up groups, including Week 0- 156. These are registry counts, not adjusted comparisons.

Counts should be read alongside the at-risk group sizes and follow-up period named for each group. The groups and periods are not interchangeable: the Aflibercept 2q8/HD group over Week 0- 156 reflects the schedule described in the arm record, while the high-dose groups have their own follow-up summaries. Serious-event terms listed most often include cataract, urinary tract infection, osteoarthritis, pneumonia, coronary artery disease, and COVID-19, with the registry recording percentages for those terms.

The registry summaries do not establish that a treatment caused an event or explain differences in exposure time, event severity beyond the serious-event classification, or individual clinical histories. They also do not provide a complete comparative safety analysis in this summary. Counts and listed terms should be understood descriptively, not as stand-alone evidence that one schedule is safer than another.

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

The primary results describe average change in a visual-acuity score over the specified follow-up period among the analysis population. The posted group estimates were 7.03 for Aflibercept 2q8, 6.06 for HDq12, and 5.89 for HDq16. The sponsor’s comparison estimates were close to the unadjusted recalculated point estimates, but the registry record also shows that the analysis methods and intervals differ. The record labels the sponsor analyses as non-inferiority, while the margin needed to evaluate that label is not reported.

These results do not show that every participant experienced the group-average change. A mean summarizes a distribution and can conceal varied responses. They also do not by themselves establish whether a numerical difference matters to patients, whether one schedule is preferable, or whether the result applies to people who would not have met the trial’s eligibility criteria. Full eligibility details and additional contextual information are not reported in the registry record.

The confidence intervals express uncertainty under their respective analyses. Their inclusion of zero is not proof that the treatments are identical, and it is not by itself a test of non-inferiority. That interpretation requires the prespecified margin, analysis plan, and appropriate handling of missing data and post-randomization events. Those details are not fully reported in the registry record.

The secondary outcomes add descriptive information about visual acuity and retinal findings, but multiple outcomes and analyses raise interpretive questions when the multiplicity strategy is not reported. Safety counts likewise provide a descriptive account over specified follow-up periods; they do not establish causation or a comparative safety conclusion. Overall, the registry supports a careful account of the posted estimates and their limits, not a broad claim about treatment effects beyond the measured outcomes and population.

18. Why This Trial Matters Statistically

This trial is statistically interesting because it compares alternative dosing schedules of the same active drug and frames the primary comparisons as non-inferiority. That design asks a different question from a conventional superiority comparison: the central issue is whether any loss relative to the comparator stays within a prespecified acceptable margin. The registry does not report that margin, so the label and estimates can be described, but the decision threshold cannot be independently assessed.

The outcome is a continuous visual-acuity change measured on a defined scale, and the record supplies both group estimates and uncertainty measures. That makes it possible to distinguish the point estimate from the precision around it. The sponsor’s model-based analysis and the simple unadjusted recalculations also illustrate why statistical summaries are method-dependent: similar point estimates do not guarantee identical intervals or p values.

The record additionally includes outcomes at other times and measures, plus adverse-event summaries across follow-up periods. Together, they illustrate the value of considering outcome definitions, time points, analysis populations, and multiplicity rather than treating a single p value as a complete account. The trial’s randomized design is relevant to its comparative purpose, while the available registry summaries still leave important methods and missing-data details unreported.

For biostatisticians and clinical researchers, the key lesson is to separate descriptive estimates, model-based inference, and the criteria for a non-inferiority conclusion. The result is not interpretable from a numerical difference or p value alone; the margin, analysis plan, endpoint definition, and uncertainty all matter.

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 are specific to the information available for this trial. The registry describes a comparator schedule that changes in Year 3, from Aflibercept 2q8 during Years 1 and 2 to high-dose aflibercept adjusted for individual response. Therefore, the Week 48 comparison concerns the earlier described treatment schedules, while longer-term summaries should be interpreted in light of the changing regimen. The full dosing and interval-adjustment rules are not reported in the registry record.

The primary result is a least-squares mean change, but the complete model specification and covariate details are not included in the record summary. The sponsor’s analyses are labelled non-inferiority, yet the non-inferiority margin is not reported. The primary analysis uses a full analysis set that excludes randomized participants who did not receive at least one dose, and the estimand is mainly based on a hypothetical strategy. The registry summary does not explain all events covered by that strategy or how they were handled.

The amount and pattern of missing endpoint data, missing-data assumptions, and sensitivity analyses are not reported in the registry record. Nor is the full multiplicity approach for the many outcomes and analyses. These omissions limit independent assessment of robustness and of how secondary findings should be weighed. The simple recalculations are unadjusted and do not reproduce the sponsor’s model-based analysis.

Finally, adverse-event counts are descriptive summaries over different treatment groups and follow-up periods. They do not account in this presentation for exposure duration or establish event causality. These limitations concern interpretation of the registry summaries; they do not establish that the trial itself lacked procedures or analyses that are not described in the record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study of the Effects of High Dose Aflibercept Injected Into the Eye of Patients With an Age-related Disorder That Causes Loss of Vision Due to Growth of Abnormal Blood Vessels at the Back of the Eye — NCT04423718.
• Registry record last updated 2025-08-29; status last verified 2025-08.
• Results first posted 2023-09-06.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT04423718 is a completed randomized phase 3 study sponsored by Bayer, with an enrollment of 1011. It compares high-dose aflibercept schedules with Aflibercept 2q8 in neovascular age-related macular degeneration. The primary outcome is change from baseline in BCVA on the ETDRS letter score at Week 48, analyzed in a full analysis set of randomized participants who received at least one dose.

The sponsor reports mixed-model non-inferiority analyses for the two high-dose groups. Simple recalculations from posted summary statistics are unadjusted and differ in their uncertainty estimates; the sponsor analysis takes precedence. The registry record does not report the non-inferiority margin, the complete statistical plan, or several details needed to assess missing data and multiplicity. Secondary outcomes and adverse-event counts add context, but should be interpreted descriptively with those limitations in mind.