Study to Assess the Efficacy, Safety, and Tolerability of Intravitreal Aflibercept Compared to Laser Photocoagulation in Patients With Retinopathy of Prematurity: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Efficacy, Safety, and Tolerability of Intravitreal Aflibercept Compared to Laser Photocoagulation in Patients With Retinopathy of Prematurity (NCT04101721), a randomized phase 3 study. The primary outcome is Percentage of Participants With Absence of Active Retinopathy of Prematurity (ROP) and Unfavorable Structural Outcomes From Baseline to Week 52 of Chronological Age.

2. Clinical Question

3. Trial Design

This was a randomized, controlled, multi-center, phase 3 study with a parallel-group design. The registry lists retinopathy of prematurity as the condition, Regeneron Pharmaceuticals as the sponsor, and a planned enrollment of 127. The recorded start date was 2019-10-30, primary completion date was 2022-08-18, and status is completed. The registry reports no masking.

Participants were assigned to aflibercept or laser photocoagulation. At baseline, the aflibercept group received a single intravitreal injection per eligible eye; the laser group received laser treatment in each eligible eye. The primary analysis used the full analysis set, defined as randomized participants who received any study treatment, and analyzed participants according to their baseline assignment. The posted primary results list 93 participants in the aflibercept group and 27 in the laser group.

The primary outcome was assessed from baseline to week 52 of chronological age. Secondary outcomes covered the need for a second treatment modality, recurrence of retinopathy of prematurity, and ocular and non-ocular treatment-emergent adverse events and serious adverse events. The registry lists five outcome measures and posts four secondary outcomes. The record does not report the randomization ratio, the number of centers, or further details about the conduct of randomization. It also does not report the trial’s original sample-size justification or the assumptions used to plan enrollment.

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 127 participants randomized, 33 were randomized to laser and 94 were randomized to aflibercept. Six of the 33 participants randomized to laser were withdrawn before receiving any study intervention (5 due to Parent/Guardian and 1 due to Physician decision); One of the 94 participants randomized to aflibercept was withdrawn before receiving any study intervention due to Parent/Guardian. In total, 120 participants (27, laser group; 93, aflibercept group) received at least 1 study treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full analysis set (FAS): All randomized participants who received any study treatment. Analysis on the FAS was performed according to the treatment assigned at baseline (as randomized).

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 (FAS): All randomized participants who received any study treatment. Eyes analyzed includes all treated eyes.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Participants With Absence of Active Retinopathy of Prematurity (ROP) and Unfavorable Structural Outcomes From Baseline to Week 52 of Chronological Age, measured over Baseline to week 52 of chronological age.

The primary endpoint is the percentage of participants with absence of active retinopathy of prematurity and unfavorable structural outcomes from baseline to week 52 of chronological age. Active disease was defined as retinopathy of prematurity requiring treatment. Unfavorable structural outcomes were retinal detachment, macular dragging, macular fold, or retrolental opacity.

The endpoint combines disease activity and specified structural findings into a participant-level response. When both eyes were enrolled, both had to meet the endpoint for the participant to count as a responder. When only one study eye was enrolled, response was determined by that eye. This definition makes the participant, rather than each eye separately, the unit represented by the reported percentage.

Such a combined endpoint can describe whether a participant met several clinically specified conditions by the assessment time. It should not be read as a measure of the degree of improvement, the timing of any event, or the separate frequency of each structural outcome. Those details are not reported in the primary endpoint result. The measure is used to compare the proportion meeting the response definition in the two assigned groups; it does not, by itself, establish why participants did or did not meet the definition.

7. Results Posted in the Registry

• Aflibercept 0.4 mg: 79.6% (74/93) versus 77.8% (21/27) on control; risk difference 1.8 percentage points (95% CI -15.9 to 19.5), risk ratio 1.02 (0.82–1.28); unadjusted two-proportion z-test p = 0.840.

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.

Percentage of Participants Requiring Intervention With a Second Treatment Modality From Baseline to Week 52 of Chronological Age

• 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 0.4 mg: 15.1% (14/93) versus 18.5% (5/27) on control; risk difference -3.5 percentage points (95% CI -19.8 to 12.9), risk ratio 0.81 (0.32–2.05); unadjusted two-proportion z-test p = 0.664.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept 0.4 mg and the control. The interval gives the range of effects that remain compatible with the data.

Percentage of Participants With Recurrence of ROP Through Week 52 of Chronological Age

• 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 0.4 mg: 39.8% (37/93) versus 29.6% (8/27) on control; risk difference 10.2 percentage points (95% CI -9.7 to 30.0), risk ratio 1.34 (0.71–2.53); unadjusted two-proportion z-test p = 0.337.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept 0.4 mg and the control. The interval gives the range of effects that remain compatible with the data.

The secondary outcomes cover additional treatment, recurrence, and ocular and non-ocular treatment-emergent adverse events and serious adverse events. Across the posted comparisons, the direction is not uniform: the primary response and second-treatment-modality estimates are numerically in one direction, while recurrence is numerically in the other. This mixed pattern is descriptive and does not establish a consistent advantage across outcomes.

The secondary outcomes provide context for interpreting the primary endpoint, but they measure different events and should not be treated as interchangeable confirmation of the primary result. A participant may meet the primary response definition and still have a later recurrence or require another treatment modality. The registry’s outcomes do not provide a single combined interpretation of those events, and they should be considered according to their separate definitions and time frames.

The registry posts adjusted analyses for the second-treatment and recurrence outcomes, while the recalculations are unadjusted. The method for the adjusted analyses is not reported in the registry record. No sponsor p-values are posted for those comparisons. The simple recalculated tests are unadjusted and should be considered exploratory descriptions rather than a family of confirmatory tests.

In general, examining multiple outcomes increases the chance that some differences may appear notable by chance, particularly if many tests are interpreted without accounting for multiplicity. The registry does not report a multiplicity procedure or a hierarchy for interpreting secondary outcomes. For that reason, unadjusted secondary results carry less weight than a prespecified primary analysis and should not be used alone to draw strong conclusions. The secondary findings can identify questions for further evaluation, but they do not settle the primary comparison or establish effects on outcomes not measured in the record.

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

• Percentage of Participants Requiring Intervention With a Second Treatment Modality From Baseline to Week 52 of Chronological Age
• Percentage of Participants With Recurrence of ROP Through Week 52 of Chronological Age
• Percentage of Participants With Ocular Treatment-emergent Adverse Events (TEAEs) and Treatment-emergent Serious Adverse Events (TESAEs)
• Percentage of Participants With Systematic (Non-ocular) TEAEs and TESAEs

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is binary at the participant level: a participant either met the response definition or did not. The posted percentages summarize the proportion responding in each assigned group. A risk difference expresses the difference between those proportions; positive values in the posted comparison correspond to a higher response proportion in the aflibercept group relative to laser. The recalculated estimate is 0.018, and its confidence interval runs from -0.159 to 0.195. These are unadjusted calculations from the posted group summaries.

What does a risk difference describe?

In general, a risk difference puts two event proportions on an additive scale. It is useful for describing the absolute separation between groups. A value near zero describes little separation in the observed proportions, while an interval that includes zero does not rule out differences in either direction. The estimate should be read with its interval rather than as a precise fixed effect. The posted percentages and risk-difference estimate use different displayed scales, so the figures should not be compared as if they were identical units.

The recalculation also reports a risk ratio and an odds ratio. In general, a risk ratio compares event proportions by division, while an odds ratio compares the odds of an event. These measures answer different versions of the comparison and are not interchangeable with a risk difference. Their intervals are also broad: the posted risk ratio is 1.023 with a confidence interval from 0.816 to 1.283, and the odds ratio is 1.113 with a confidence interval from 0.394 to 3.142. The registry does not identify these recalculated measures as the sponsor’s primary analysis.

What does the p-value add?

The unadjusted recalculation reports p = 0.84. In general, a p-value describes how compatible the observed data are with a specified null model, under the assumptions of the analysis. It is not the probability that the null hypothesis is true, nor does it quantify the size or clinical importance of a difference. A p-value also does not replace the confidence interval: the interval communicates a range of effects compatible with the data under the method used. The sponsor analysis does not post a p-value for the primary comparison.

The sponsor result is reported as an adjusted difference with a 95.1% confidence interval and a non-inferiority classification. The adjustment method, covariates, model details, and margin are not reported in the registry record. In general, adjustment means the comparison is estimated using a specified model or accounting for selected factors. Without those details, the adjusted estimate cannot be reproduced or fully assessed from the registry entry alone. The recalculation is deliberately simpler and unadjusted; it should not be substituted for the sponsor’s analysis.

Why does the analysis population matter?

The full analysis set includes randomized participants who received any study treatment, analyzed according to treatment assigned at baseline. This preserves the baseline assignment in the stated analysis population, while excluding randomized participants who received no study treatment under the registry’s definition. The record does not report the number of randomized participants who did not receive treatment, the handling of missing endpoint observations, or additional populations used for the sponsor analysis. Those details could affect how the reported estimate should be understood, but should not be inferred.

The endpoint also combines active disease requiring treatment with specified unfavorable structural outcomes. For participants with both eyes enrolled, both eyes had to satisfy the endpoint. In general, a composite or combined response definition can be informative as a summary, but it can conceal differences among its components. The registry does not post component-specific primary estimates, so the overall response result cannot show which component contributed most to a participant’s outcome.

For binary outcomes, uncertainty depends on both the observed proportions and the amount of information in each group. A smaller group generally contributes less information than a larger group when other factors are comparable. Here, the group sizes are 27 and 93 for the primary result, and the confidence interval is broad. In general, this makes it important to avoid treating small differences between point estimates as precise evidence. No further model assumptions for the sponsor’s primary analysis are reported in the registry record.

11. Confidence Intervals and Precision

The primary recalculated risk difference is 0.018, with a confidence interval from -0.159 to 0.195. The interval crosses zero and extends in both directions, indicating that the posted summaries do not pin down the direction or size of the difference precisely. It is substantially more informative to consider this range than to focus only on the point estimate.

The registry’s sponsor analysis gives an adjusted difference of 1.81 and a 95.1% confidence interval from -15.71 to 19.33. This interval also spans zero. The sponsor’s estimate is adjusted, while the recalculation is unadjusted; their scales and analysis methods should not be treated as identical. The method used to produce the adjusted interval is not reported in the registry record.

In general, a confidence interval expresses uncertainty in an estimate under the analysis method and assumptions used. It is not a range that guarantees the true effect lies within its limits, and it does not assign equal probability to all values inside the interval. A wide interval signals limited precision, while an interval that includes zero leaves room for effects in either direction when zero represents no difference. The group sizes of 27 and 93 provide context for the uncertainty, but do not by themselves explain all of it.

The reported interval is not a clinical acceptability range. The non-inferiority margin and its rationale are not reported in the registry record, so the interval cannot be used to evaluate how it relates to a prespecified margin. The posted figures support a cautious reading of the magnitude and direction of the primary comparison rather than a definitive claim about equivalence or a clinically meaningful difference.

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 planning figures are illustrative calculations based on observed effects, not the trial’s original design justification. For these binary outcomes, the listed figures are participants per arm, not total participants. The planning 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 set to the stated fraction of the observed effect. The trial’s own original design assumptions are not reported in the registry record.

The 80% power column gives the estimated participants per arm for a hypothetical study designed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning figure for a 90% chance. In general, higher target power requires more participants when other assumptions are held constant. These are planning illustrations and are not observed power.

Rows for planning for 100%, 75%, and 50% of the observed effect show how the assumed effect size changes the required sample size. A smaller effect is harder to distinguish from random variation, so it requires more participants under the same planning assumptions. These figures should be interpreted as conditional illustrations, not as estimates of what the completed trial would have needed under its actual protocol, which is not reported.

The outcome-specific figures can differ because each outcome has a different observed effect and event pattern. They should not be read as recommendations or as evidence that a given sample size guarantees a particular result. The registry’s planning assumptions specify equal allocation, whereas the posted primary analysis groups contain 93 and 27 participants. The planning calculations do not explain that observed group-size pattern or replace the trial’s unreported design rationale. No total-event planning figures apply to the binary outcomes described in this record.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, p₀ and p₁ are the control and treatment proportions, and p̄ is their average.

Worked calculation for this trial

1. Control proportion p₀ = 0.778; treatment proportion p₁ = 0.796; average p̄ = 0.787.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5793 = 1.1354.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.5791 = 0.4874.
4. n = (1.1354 + 0.4874)² / (0.0179)² = 8,199.5, rounded up to 8,200 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
p0 <- 0.777777777777778                          # control proportion
p1 <- 0.795698924731183                          # treatment proportion
n_per_arm <- function(power, frac = 1) {
  q1 <- p0 + (p1 - p0) * frac               # smaller effect = fraction of the observed difference
  pbar <- (p0 + q1) / 2
  z_b <- qnorm(power)
  ceiling(round((z_a * sqrt(2 * pbar * (1 - pbar)) + z_b * sqrt(p0 * (1 - p0) + q1 * (1 - q1)))^2 / (q1 - p0)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (unrounded n per arm)
cat("power.prop.test:", round(power.prop.test(p1 = p0, p2 = p1, power = 0.80)$n, 1), "\n")

# Simulation: how often does the z-test reject at the 80%-power sample size?
set.seed(4101721)
n    <- n_per_arm(0.80)
reps <- 20000
x0 <- rbinom(reps, n, p0); x1 <- rbinom(reps, n, p1)
ph <- (x0 + x1) / (2 * n)
z  <- ((x1 - x0) / n) / sqrt(ph * (1 - ph) * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(z) > z_a, na.rm = TRUE), reps))

Output from running the code

100% of observed effect: n per arm = 8,200 (80% power), 10,977 (90% power)
 75% of observed effect: n per arm = 14,689 (80% power), 19,664 (90% power)
 50% of observed effect: n per arm = 33,300 (80% power), 44,579 (90% power)
power.prop.test: 8199.5 
Simulated power at n = 8,200 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor’s primary analysis is reported as an adjusted difference of 1.81, with a 95.1% confidence interval from -15.71 to 19.33, and is classified in the registry as non-inferiority. The method used to adjust the estimate and the non-inferiority margin are not reported in the registry record. The registry also does not post a p-value for this analysis.

The recalculation uses only the posted group summaries and is unadjusted. It reports a risk difference of 0.018, with a confidence interval from -0.159 to 0.195 and p = 0.84. Because the sponsor result is adjusted and the recalculation is unadjusted, they answer related but not identical statistical questions. Their numeric scales also differ, so they should not be compared by directly subtracting one estimate from the other.

The recalculated primary result does not contradict the sponsor’s reported analysis, but it cannot reproduce or verify the sponsor analysis without its method and margin. The registry record reports no discrepancy between the sponsor result and the recalculation. The sponsor’s own analysis therefore remains the primary reported analysis, while the recalculation provides a transparent, simple comparison of the posted proportions.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies one primary endpoint and lists four posted secondary outcomes. It does not report whether a formal multiplicity adjustment was used for the secondary analyses, whether outcomes were ordered in a testing hierarchy, or whether any secondary result was intended to support a confirmatory claim. The reported recalculated p-values are unadjusted. Without a stated plan for handling multiple comparisons, those values should be interpreted cautiously rather than as independent confirmation.

Multiplicity matters in general because testing several outcomes can increase the chance of at least one apparently unusual result even when no underlying effects exist. Adjusting for multiplicity or prespecifying an order of testing can address that concern, but neither approach should be assumed. The registry’s record does not report the statistical analysis plan details needed to determine how the family of outcomes was handled.

The full analysis set is defined as randomized participants who received any study treatment, analyzed according to treatment assigned at baseline. This explains the stated population for the primary result, but does not describe every analysis population used by the sponsor. The registry record does not report how missing data were handled, whether participants with no week 52 assessment were excluded or otherwise accounted for, or whether sensitivity analyses examined alternative assumptions about missing outcomes.

It also does not report whether interim analyses were conducted, whether stopping boundaries were used, or how the sample size was originally justified. Those elements should not be inferred from the completed status or from the planning illustrations based on observed effects. The available registry entry gives the endpoint definitions, stated analysis population, posted estimates, and some analysis classifications, but leaves these aspects of the statistical plan unreported.

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: apnoea (7.4%), retinal detachment study eye (7.4%), bronchiolitis (3.7%), pneumonia (3.7%), pneumonia viral (3.7%).

The registry lists serious adverse events affecting 12 of 27 participants at risk in the laser group and 32 of 93 participants at risk in the aflibercept group. Other adverse events are listed for 12 of 27 participants at risk in the laser group and 40 of 93 participants at risk in the aflibercept group. The record lists zero deaths in the laser group and one in the aflibercept group.

The most frequently listed serious-event terms include Apnoea and Retinal detachment Study Eye, each reported as 7.4%. Bronchiolitis, Pneumonia, Pneumonia viral, and Apnoeic attack are each listed as 3.7%. These are registry-listed event terms, not a comparison adjusted for differences between groups. The registry information does not establish that an event was caused by the assigned treatment.

In general, safety counts should be read with their at-risk denominators and with the event definitions and observation period in mind. The record lists serious and other adverse event totals but does not provide further details about event duration, severity grading, relatedness assessments, or individual participants’ clinical circumstances. The counts are descriptive and do not by themselves establish a difference in safety between groups.

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

The posted primary percentages describe the proportion of participants who met a combined definition of no active retinopathy of prematurity and no specified unfavorable structural outcome by week 52 of chronological age. The primary recalculation estimates a small positive risk difference for aflibercept relative to laser, but its confidence interval includes zero and extends in both directions. The sponsor’s adjusted analysis is reported separately as non-inferiority, with a confidence interval that also spans zero.

These results do not establish that the treatments are identical. A confidence interval spanning zero indicates that the data do not precisely distinguish the groups on the stated scale; it does not prove the absence of a difference. Conversely, the numerical difference in the point estimates does not establish a reliable or clinically important effect. The non-inferiority classification cannot be fully assessed from the registry entry because the margin and analysis method are not reported.

The endpoint is participant-based and has a specific two-eye rule. It does not describe the result for each eye separately, the separate contribution of each endpoint component, or the course of disease between assessments. The secondary outcomes add information about further treatment and recurrence, but their unadjusted interpretation is limited by the absence of a reported multiplicity approach.

The results also do not establish what would happen in populations or settings not described by the registry record. The posted analysis population, group sizes, assessment time, and outcome definitions delimit what the estimates represent. Safety counts are descriptive and do not establish treatment causation. Taken together, the results support a cautious statistical reading of the measured outcomes in this trial, not a general clinical recommendation.

18. Why This Trial Matters Statistically

This trial illustrates why a point estimate is not enough to understand a randomized comparison. The primary response percentages are close, but the uncertainty interval around the recalculated difference spans zero and allows differences in either direction. Reading both the estimate and its interval gives a more complete account than treating the point estimate as a definitive result.

It also illustrates the distinction between an adjusted sponsor analysis and an unadjusted recalculation. Both can be informative, but they are based on different analytical approaches. The sponsor result is classified as non-inferiority, while important details needed to evaluate that classification, including the margin and analysis method, are not reported in the registry record. Transparent reporting of these details is essential for independent interpretation.

The endpoint definition shows how participant-level results can depend on eye-level rules and combined outcome components. A percentage of participants meeting a composite response is not the same as a percentage of eyes meeting it, and it does not reveal which component determined each result. The different directions across secondary outcomes also demonstrate why multiple outcome results need to be interpreted within a stated analysis plan.

Finally, the planning illustrations are not a substitute for the original design rationale. Their sample-size requirements depend on explicit hypothetical assumptions and on effects observed in the trial. Distinguishing those illustrations from actual design calculations, and distinguishing planning power from observed results, helps prevent retrospective estimates from being mistaken for trial evidence.

19. Limitations

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

The registry record leaves important features of the statistical plan unreported. It does not give the original sample-size justification, the non-inferiority margin, the method and covariates for the adjusted analyses, or the procedures used to handle missing primary outcome data. It also does not report interim analyses or a multiplicity procedure for the secondary outcomes. Those omissions limit independent assessment of the sponsor’s confirmatory analysis.

The primary endpoint combines active disease requiring treatment with several unfavorable structural outcomes, and the result is reported at the participant level. The registry does not post separate estimates for the endpoint components or separate outcomes by whether one or both eyes were enrolled. This limits the detail available about what drove the combined response result.

The primary result lists 93 participants in the aflibercept group and 27 in the laser group. The record does not explain the group-size pattern or provide enough detail to infer its causes. The confidence interval around the unadjusted comparison is broad, which limits precision. The assessment period for the primary endpoint ends at week 52 of chronological age, so the posted primary result does not describe outcomes beyond that time.

The registry lists serious and other adverse-event counts but does not report detailed event-level circumstances, relatedness assessments, or further safety analysis methods. The secondary recalculations are unadjusted, and the registry does not state how multiple secondary comparisons should be interpreted. These limitations concern the available registry reporting and do not establish that any particular analysis or event was handled incorrectly.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Efficacy, Safety, and Tolerability of Intravitreal Aflibercept Compared to Laser Photocoagulation in Patients With Retinopathy of Prematurity — NCT04101721.
• Registry record last updated 2023-07-20; status last verified 2023-07.
• Results first posted 2023-07-20.
• 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

NCT04101721 is a completed, randomized, parallel-group phase 3 study comparing intravitreal aflibercept with laser photocoagulation in participants with retinopathy of prematurity. The registry reports no masking and lists 127 planned participants. The primary endpoint assessed the percentage meeting a combined disease-activity and structural outcome definition from baseline to week 52 of chronological age.

The posted primary proportions are 79.6 for Aflibercept 0.4 mg and 77.8 for Laser Photocoagulation. The sponsor reports an adjusted difference classified as non-inferiority; the recalculation is unadjusted and has a confidence interval that includes zero. The non-inferiority margin and several details needed to assess the analysis are not reported in the registry record. Secondary findings vary in direction, and the safety figures are descriptive. The results are best read with attention to the endpoint definition, analysis population, uncertainty, and limits of the registry reporting.