Study to Assess the Clinical Efficacy and Safety of Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) in Patients With Branch Retinal Vein Occlusion (BRVO): Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Study to Assess the Clinical Efficacy and Safety of Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) in Patients With Branch Retinal Vein Occlusion (BRVO) (NCT01521559), a randomized phase 3 study. The primary outcome is Participants Who Gained at Least 15 Letters in Best Corrected Visual Acuity (BCVA) at Week 24 - LOCF.

2. Clinical Question

The clinical question is comparative rather than a comparison with no treatment: both groups received an active intervention, and the control group could receive IAI under rescue criteria. Random assignment and double masking are reported. The registry record does not report the exact eligibility criteria, baseline characteristics, or the procedures used to maintain masking. Those details matter when judging how closely the studied participants and treatment delivery resemble any other setting, and they cannot be inferred from the outcome figures alone.

3. Trial Design

This was a phase III, randomized, double-masked, active-controlled, parallel-group study. The registry record lists enrollment of 183 and a study duration of 52 weeks. It reports a start date of 2012-04, primary completion in 2013-08, and a completed status. The primary endpoint was assessed from baseline to week 24, before the end of the stated study period.

The two groups were intravitreal aflibercept injection and macular laser photocoagulation. In the IAI group, the stated regimen was 2 milligrams every 4 weeks through week 24, then every 8 weeks through week 48; laser rescue could be used at week 36. In the laser control group, participants received laser at baseline and then according to re-treatment criteria through week 24. They could start IAI at week 24 if rescue criteria were met. The recorded control-arm description ends before its post-rescue injection schedule is complete, so that detail is not reported in the registry record.

The primary outcome results include 90 participants in the laser group and 91 in the IAI group. The outcome-specific denominators are not necessarily the same for every secondary measure; for example, the NEI VFQ-25 results use 87 and 88 participants. The registry record does not report the method used to generate the random allocation sequence, allocation concealment procedures, the identity of masked parties, or the trial's original sample-size assumptions. It also does not report interim-analysis plans or a detailed statistical analysis plan. These gaps limit reconstruction of the design and analysis decisions, even though the central comparison and primary outcome are described.

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 281 participants who were screened for inclusion in the study, 183 were enrolled (started) and 183 received treatment.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: FAS

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 enrolled subjects who received any investigational product, had a baseline best corrected visual acuity (BCVA) assessment, and at least 1 post-baseline BCVA assessment.

6. Primary Endpoint

The registry lists the primary outcome as Participants Who Gained at Least 15 Letters in Best Corrected Visual Acuity (BCVA) at Week 24 - LOCF, measured over Baseline to week 24.

The primary endpoint counts participants who gained at least 15 letters in BCVA from baseline to week 24. BCVA was measured with the Early Treatment Diabetic Retinopathy Study (ETDRS) protocol at every visit through week 24. The endpoint is binary: each participant either met the stated threshold or did not. It is therefore interpreted as a count or proportion of participants, rather than as an average change in vision across the group.

A threshold endpoint can make a clinically interpretable change easier to describe: it asks how many participants crossed a prespecified level of improvement, rather than how much the group mean changed. But it also discards some information. A participant who gains more than 15 letters and one who gains exactly 15 letters both count as meeting the threshold, while a smaller gain does not. The registry record does not report the rationale for choosing this threshold, nor whether it was the sole primary outcome in the original protocol.

The analysis is identified as FAS and uses LOCF to impute missing data. LOCF carries a participant's last observed value forward to the later assessment; it is an assumption about the unobserved endpoint, not a direct measurement. How many values were missing, when they were last observed, and whether other imputation approaches were examined are not reported in the registry record. Consequently, the endpoint should be read as a week 24 comparison under the stated analysis and imputation method, not as a complete set of observed week 24 measurements.

7. Results Posted in the Registry

• Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321): 52.7% (48/91) versus 26.7% (24/90) on control; risk difference 26.1 percentage points (95% CI 12.3 to 39.8), risk ratio 1.98 (1.33–2.93); unadjusted two-proportion z-test p = <0.001.

8. Secondary Efficacy Endpoints

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

Change From Baseline to Week 24 in BCVA Score - LOCF

• 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:
  • Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321): mean 17.00 versus 6.90 on control; difference 10.10 (95% CI 6.48 to 13.72), standardized effect d = 0.81; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically higher for Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in Central Retinal Thickness (CRT) at Week 24 - LOCF

• 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:
  • Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321): mean -280.50 versus -128.00 on control; difference -152.50 (95% CI -208.56 to -96.44), standardized effect d = -0.79; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change From Baseline in the National Eye Institute Visual Function Questionnaire - 25 (NEI VFQ-25) Questionnaire Total Score at Week 24 - LOCF

• 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:
  • Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321): mean 7.70 versus 6.30 on control; difference 1.40 (95% CI -2.08 to 4.88), standardized effect d = 0.12; z-test p = 0.430.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary endpoints, the pattern is not uniform across every measurement. The posted results show a positive adjusted contrast for mean BCVA change and a negative adjusted contrast for central retinal thickness change, with reported confidence intervals that exclude zero. For the NEI VFQ-25 total score, the reported adjusted confidence interval includes zero and its p-value is 0.083. This broad pattern offers supporting information on measured visual acuity and retinal structure, while the patient-reported visual-function outcome is less decisive in this analysis.

These measures address related but distinct domains. BCVA change captures letter-reading performance, central retinal thickness is an anatomical measure, and the NEI VFQ-25 is a questionnaire-based total score. Their results cannot be collapsed into a single overall treatment effect or treated as interchangeable confirmation of the primary threshold endpoint. The primary outcome asks how many participants reached a particular gain threshold; secondary measures describe average changes on their own scales.

Secondary results generally carry less evidential weight when multiple outcomes are tested without a reported adjustment strategy. Each additional test creates another opportunity for a result to appear statistically notable by chance. The registry record does not report whether multiplicity was controlled, what hierarchy may have been prespecified, or whether the listed endpoints were confirmatory or exploratory. The secondary p-values should therefore be interpreted as endpoint-specific results, not as a single multiplicity-adjusted body of evidence.

The secondary analyses also use LOCF, and their sample sizes differ across measures. The record does not give a full account of missing observations or sensitivity analyses. Those limitations are relevant when comparing the secondary pattern with the primary result. Together, the endpoints provide complementary descriptions, but they do not remove uncertainty about missingness, multiplicity, or the broader meaning of the measured changes.

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

• Change From Baseline to Week 24 in BCVA Score - LOCF
• Change From Baseline in Central Retinal Thickness (CRT) at Week 24 - LOCF
• Change From Baseline in the National Eye Institute Visual Function Questionnaire - 25 (NEI VFQ-25) Questionnaire Total Score at Week 24 - LOCF

9. Statistical Interpretation

10. Statistical Methods Explained

The main endpoint is binary because it records whether each participant did or did not gain at least 15 letters. For a binary outcome, a group count and its denominator describe how often the event occurred in that group. A between-group effect can be expressed as an absolute difference in event proportions, a relative risk, or an odds ratio. These quantities answer related but distinct questions: an absolute difference compares event frequencies on the same scale, while relative measures compare them as a ratio. The registry's sponsor analysis is reported as a net mean difference, and the raw count-based re-calculation uses unadjusted summaries. Their estimates need not be identical because the methods and adjustment differ.

What does the reported analysis do?

The registry reports a Cochran-Mantel-Haenszel analysis for the primary outcome. In general, this method can combine comparisons across strata while accounting for stratification. The specific stratification variables and implementation details are not reported in the registry record, so the analysis should not be described as adjusted for any particular factor. The reported result is a net mean difference of 26.6, with a 95% confidence interval from 13.0 to 40.1 and p < 0.001.

The re-calculated binary summaries are simple, unadjusted calculations from posted group counts. They do not recreate the sponsor's analysis, use its model, or account for any strata. In general, unadjusted summaries are valuable for transparency, but an adjusted sponsor analysis is the primary reported inferential result when the registry records one. The discrepancy flag is false, and no discrepancy-triggered precedence issue is identified.

How should the secondary mean comparisons be read?

The three secondary endpoints are continuous measures analyzed as changes from baseline. The registry reports ANCOVA for each, presenting an adjusted net mean difference, confidence interval, and p-value. In general, analysis of covariance (ANCOVA) estimates a group contrast while accounting for selected covariates, often including a baseline measure. The covariates and model specification used in these analyses are not reported in the registry record. The posted arm means and standard deviations are descriptive; the ANCOVA result is the reported inferential comparison and can differ from an unadjusted mean difference.

For mean outcomes, a confidence interval describes uncertainty in the estimated difference in group means under the fitted model. It does not describe the range of individual participants' outcomes. The posted p-values and intervals address the model-based contrast for each endpoint; they do not automatically adjust for testing multiple outcomes.

Why does over-dispersion matter?

General statistical context: for count outcomes, a model that assumes variance is determined by the mean can be too restrictive when the observed variability is greater than that assumption allows. This extra variability is called over-dispersion; ignoring it can make standard errors too small and confidence intervals too narrow. The primary endpoint is a participant-level binary outcome, not a count of recurrent events. The registry record does not report an over-dispersion assessment or a count model for this endpoint, so over-dispersion should not be attributed to the analysis.

What does LOCF assume?

LOCF means last observation carried forward. In general, it fills a missing later assessment with the participant's last observed value, treating that value as a proxy for the unobserved outcome. This can be convenient but assumes that the last recorded value remains an appropriate representation at the target time. If outcomes change after the last visit, the imputed values may not reflect the unobserved measurements. The direction and extent of any bias depend on the reasons and timing of missingness, which are not reported in the registry record. The primary endpoint and listed secondary outcomes are marked LOCF, but the number of missing observations and sensitivity analyses are not reported.

The primary analysis population is called FAS. That label is retained as recorded; its exact operational definition is not reported in the registry record. It should not be assumed to be identical to every possible definition of intention-to-treat. The registry does report group denominators for each endpoint, but it does not explain all differences between those denominators and the enrolled total.

General statistical context: a p-value measures how incompatible data are with a specified null hypothesis under the analysis assumptions. It is not the probability that the null hypothesis is true, and it does not measure the size or clinical importance of an effect. An interval communicates a range of values compatible with the data and model at its stated confidence level. Neither quantity addresses systematic error, unreported analyses, or external validity on its own.

11. Confidence Intervals and Precision

The primary sponsor analysis reports a net mean difference of 26.6 with a 95% confidence interval from 13.0 to 40.1. The interval lies above zero, so the reported adjusted contrast is compatible with positive differences across the interval's stated range under the analysis model. The interval is more informative than the p-value alone because it conveys both the estimated direction and the uncertainty around the estimate. It does not imply that all participants experienced a benefit of that size, nor does it describe the distribution of individual outcomes.

The simple unadjusted binary comparison is based on 24 events among 90 participants in the laser group and 48 among 91 in the IAI group. A separately recalculated risk ratio is 1.978, with a 95% interval from 1.334 to 2.933. These relative figures give a different scale from the sponsor's reported net difference. The two should not be substituted for one another, and the raw comparison does not reproduce the stratified sponsor analysis.

For the secondary mean outcomes, the reported adjusted intervals vary in width and in whether they include zero. The BCVA change comparison is reported as 10.5, with a 95% interval from 7.1 to 14.0. The central retinal thickness comparison is -148.6, with a 95% interval from -179.8 to -117.4. The NEI VFQ-25 comparison is 2.6, with a 95% interval from -0.3 to 5.5. These sponsor analyses use ANCOVA. The intervals communicate uncertainty under those models, but their width alone does not establish clinical importance.

In general, a confidence interval reflects sampling uncertainty under the model and analysis assumptions. It does not include every source of uncertainty, such as possible bias from missing outcomes, choices about multiplicity, or limitations in how participants were selected. These aspects are not resolved merely because an interval is reported. No additional precision should be inferred beyond the registry's displayed values.

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 fractions of the observed effect, not the trial's original design calculations. They assume a two-sided significance level of 0.05, equal allocation between two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. For the binary and continuous outcomes in this record, the figures are participants per arm, not total events. The convention for time-to-event outcomes would instead be total events, but no time-to-event outcome is presented among these calculations.

The 80% power column gives the estimated number of participants per arm for a future study to have an 80% chance of detecting the chosen effect under those assumptions, if that effect and the model assumptions are correct. The 90% power column uses a higher chance of detection and therefore generally calls for more participants. For example, planning for the full observed primary effect gives 55 participants per arm for 80% power and 72 for 90% power; planning for 75% of that observed effect gives 94 and 126, respectively; planning for 50% gives 204 and 272.

Smaller target effects are harder to distinguish from random variation, so more participants are needed for the same stated power. The same pattern applies across outcomes, including the continuous secondary measures. The calculations are not observed power: they are forward-looking illustrations conditional on assumed effect size, significance level, allocation, and approximation. They do not show the probability that the completed trial's result is true or the probability that a future trial will succeed.

The registry record does not report the original sample-size justification, target effect, allowance for losses to follow-up, or its planned power. These illustrations therefore should not be read as a reconstruction of the trial's own design. Nor do they account for changes in the analysis model, multiplicity strategy, or missing-data handling beyond the listed assumptions.

13. How the Sample Size Is Derived

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

Formula

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

Worked calculation for this trial

1. Control proportion p₀ = 0.267; treatment proportion p₁ = 0.527; average p̄ = 0.397.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.6920 = 1.3562.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.6669 = 0.5613.
4. n = (1.3562 + 0.5613)² / (0.2608)² = 54.1, rounded up to 55 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 <- 0.266666666666667                          # control proportion
p1 <- 0.527472527472527                          # 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(1521559)
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 = 55 (80% power), 72 (90% power)
 75% of observed effect: n per arm = 94 (80% power), 126 (90% power)
 50% of observed effect: n per arm = 204 (80% power), 272 (90% power)
power.prop.test: 54.1 
Simulated power at n = 55 per arm: 0.812 (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 registry's reported primary analysis is a Cochran-Mantel-Haenszel comparison, with a net mean difference of 26.6, a 95% confidence interval from 13.0 to 40.1, and p < 0.001. The simple re-calculation from posted counts is unadjusted and summarizes the observed event proportions. Because the calculations answer the comparison using different methods, their effect estimates and uncertainty measures are not expected to be identical.

For the secondary continuous outcomes, the sponsor reports ANCOVA estimates. Those adjusted estimates are 10.5 for BCVA change, -148.6 for central retinal thickness change, and 2.6 for NEI VFQ-25 change. The recalculations from group means are unadjusted and are useful as checks on the direction and scale of descriptive differences, but they do not reproduce ANCOVA. The covariates used in ANCOVA are not reported in the registry record.

The discrepancy flag is false. The sponsor's own analysis therefore remains the relevant registry-reported inferential analysis, while the simple recalculations serve as transparent, unadjusted summaries. If a discrepancy were flagged, the sponsor's own analysis would take precedence; that condition does not apply to this record. The registry record does not provide enough detail to recreate the sponsor models fully.

15. Multiplicity, Missing Data and Analysis Populations

The primary endpoint and three secondary outcomes are reported, but the registry record does not report a multiplicity adjustment, a testing hierarchy, or a distinction between confirmatory and exploratory secondary analyses. When several hypotheses are tested, the chance of at least one apparently positive result can increase. General statistical practice may address this through prespecified ordering or adjusted thresholds, but no particular approach can be attributed to this trial from the registry record. The primary outcome should be distinguished from the secondary results rather than treating every p-value as equivalent evidence.

Missing values were handled using last observation carried forward for the primary endpoint and the three listed secondary endpoints. LOCF substitutes a previous observed value for a missing later value. This method relies on an assumption about how a participant's outcome would have evolved after the last measurement. If that assumption is not realistic, the estimate may be biased; the direction cannot be determined without information about the missingness pattern and outcome trajectories. The number and timing of missing assessments, reasons for missingness, and sensitivity analyses are not reported in the registry record.

The primary outcome population is identified as FAS, but the exact definition of that population is not reported in the registry record. The record lists endpoint denominators, but does not explain all participant exclusions or the relationship of each analysis population to the randomized groups. It also does not report a per-protocol analysis or a detailed intention-to-treat specification.

Interim monitoring and stopping rules are not reported in the registry record. The original statistical analysis plan, including whether interim comparisons or multiplicity controls were planned, is likewise not reported. These absences do not demonstrate that such procedures were or were not used; they mean that these features cannot be evaluated from the registry information. Conclusions should remain tied to the stated analysis method, endpoint, and available documentation.

16. Safety Results

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

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: anaemia (2.2%), pneumonia (2.2%), dehydration (2.2%), atrial fibrillation (1.1%), atrioventricular block second degree (1.1%).

The safety figures report serious adverse events in 10 of 92 participants at risk in the macular laser group and 13 of 91 at risk in the IAI group. Other adverse events are listed for 30 of 92 and 25 of 91, respectively. These are counts with their recorded denominators; they are descriptive summaries and do not establish that treatment caused an event or that one group is safer. The registry record does not report detailed event definitions, exposure-adjusted rates, or a statistical comparison for these figures.

The serious-event terms listed include anaemia, pneumonia, and dehydration at 2.2% each, and atrial fibrillation, atrioventricular block second degree, and bradycardia at 1.1% each. The record does not provide an arm-specific breakdown for these listed terms in the information available, so they should not be assigned to a particular group. Death counts are not reported in the registry record.

Safety interpretation also depends on observation time, event ascertainment, severity criteria, and exposure. Although the study duration is described as 52 weeks, the registry record does not provide enough detail to compare individual exposure time or determine whether all events were collected under identical procedures. The figures should therefore be read as reported event counts, not as a complete causal assessment.

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

The primary endpoint documents more participants reaching the threshold gain in the IAI group than in the laser control group at week 24: 48 of 91 compared with 24 of 90. The registry's sponsor analysis reports a positive net difference with a 95% confidence interval above zero and p < 0.001. These observations describe the randomized trial comparison under the specified analysis, including LOCF handling of missing values.

They do not show that every participant gained vision, that the average participant had the same response as the group result, or that the result will necessarily apply to people outside the trial. A threshold-based outcome compresses a range of individual changes into a yes-or-no classification. The reported contrast concerns the frequency of crossing the threshold, not the full distribution of BCVA outcomes.

The result also does not establish the effect of IAI compared with no intervention. The comparator was active laser treatment, with IAI available as rescue for control participants who met criteria. The registry record does not report how many control participants received rescue, so the effect of that treatment pathway on outcomes cannot be isolated from the posted result. Nor does the week 24 primary endpoint alone answer questions about persistence or later outcomes through the study's 52-week duration.

The confidence interval and p-value express uncertainty under the reported analysis, not certainty about cause, clinical importance, or future results. They do not address unreported multiplicity procedures, missing-data sensitivity, or all aspects of trial conduct. The supporting outcomes add context but are not replacements for the primary comparison, and the patient-reported endpoint's interval includes zero.

Safety counts are descriptive, and the registry record does not provide enough event-level information to establish causation or fully compare risks. Overall, the posted evidence should be interpreted as a trial-specific statistical finding, bounded by its population, comparator, endpoint definition, follow-up point, analysis choices, and registry-level reporting.

18. Why This Trial Matters Statistically

This trial offers a clear example of how the same clinical comparison can be described on multiple statistical scales. The primary endpoint is a binary threshold outcome, so raw event counts, absolute contrasts, relative measures, and a stratified sponsor analysis each emphasize different features of the data. Reading the group counts alongside the sponsor's estimate helps distinguish the observed proportions from a model-based analysis.

It also illustrates why a confidence interval matters alongside a p-value. The reported primary interval indicates the range of adjusted differences compatible with the analysis, while the p-value alone would not convey the size or precision of the contrast. Secondary endpoints show why a single trial can offer different degrees of evidence across distinct outcomes: visual acuity, retinal thickness, and questionnaire score are related but not identical measures.

LOCF is another instructive feature. An imputation method affects how missing outcomes contribute to the estimate, and the absence of detailed missingness information limits assessment of that assumption. Likewise, the registry record's lack of information about multiplicity and the original sample-size rationale makes it important not to overinterpret multiple endpoint results or treat planning illustrations as the study's design calculation.

Finally, the comparison is active-controlled and includes a rescue option, not a simple contrast between treatment and no treatment. That design feature affects the question the primary estimate answers. The record demonstrates how trial design, endpoint definition, analysis method, and reporting completeness together determine what can be concluded statistically.

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 trial-specific details needed to assess applicability and reproducibility are not reported in the registry record. Eligibility criteria and baseline characteristics are not included in the registry record, so the comparability of the enrolled population with other patient groups cannot be judged. Although allocation is listed as randomized and masking as double, the randomization sequence, allocation concealment, and identities of those masked are not reported.

The study is described as 52 weeks, while its primary endpoint is at week 24. The primary result therefore does not characterize the entire follow-up period. The number of participants who received rescue IAI in the control group is not reported, and the post-rescue schedule description is incomplete. The record consequently does not permit a detailed assessment of treatment exposure after rescue or the extent to which rescue influenced outcomes.

The primary analysis is labeled FAS, but that population's exact definition is not reported. LOCF was used for the primary and secondary outcomes, while missing-value counts, reasons, and sensitivity analyses are not reported. The registry record also does not report the original sample-size justification, interim monitoring, multiplicity procedures, or full model specifications. For the ANCOVA analyses, the covariates are not specified; for the Cochran-Mantel-Haenszel analysis, the stratification variables are not specified.

Safety summaries provide counts but not enough event-level or exposure information to establish causal relationships or make a complete comparative risk assessment. These limitations do not invalidate the posted results; they constrain how fully the methods and broader implications can be evaluated using the registry record alone.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Study to Assess the Clinical Efficacy and Safety of Intravitreal Aflibercept Injection (IAI;EYLEA®;BAY86-5321) in Patients With Branch Retinal Vein Occlusion (BRVO) — NCT01521559.
• Registry record last updated 2014-11-13; status last verified 2014-11.
• Results first posted 2014-11-13.
• 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 registry record describes a completed phase III, randomized, double-masked, active-controlled, parallel-group trial of intravitreal aflibercept and macular laser photocoagulation for macular edema secondary to BRVO. Enrollment was 183, and the study is described as lasting 52 weeks.

The primary endpoint was the number of participants gaining at least 15 letters in BCVA by week 24, assessed using the ETDRS protocol and analyzed with LOCF in a population identified as FAS. The sponsor reported a Cochran-Mantel-Haenszel net mean difference of 26.6, with a 95% confidence interval from 13.0 to 40.1 and p < 0.001. Secondary outcomes covered BCVA change, central retinal thickness, and NEI VFQ-25 score, analyzed using ANCOVA.

The record also reports serious and other adverse-event counts. Original design assumptions, detailed missing-data information, multiplicity procedures, and several model specifications are not reported in the registry record. The posted results are most appropriately interpreted within these design and reporting limits.