Aflibercept in Polypoidal Choroidal Vasculopathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Aflibercept in Polypoidal Choroidal Vasculopathy (NCT02120950), a randomized phase 4 study. The primary outcome is Mean Change in Best Corrected Visual Acuity (BCVA) as Measured by Early Treatment of Diabetic Retinopathy Study (ETDRS) Letter Scores From Baseline to Week 52 - Last Observation Carried Forward (LOCF).

2. Clinical Question

Both groups received aflibercept injections during the initial run-in period. The arm descriptions state that participants received intravitreal aflibercept every month for the first 3 months, then were randomized at Week 12 to active or sham photodynamic therapy, alongside aflibercept. The available descriptions are truncated, so additional treatment details are not reported in the registry record.

The comparison therefore concerns the treatment strategies assigned after the shared aflibercept run-in, rather than aflibercept versus no aflibercept. The registry record describes a randomized, double-masked, sham-controlled phase 3b/4 study and lists quadruple masking. It enrolled 333 participants and is marked completed. Its stated aim was to collect efficacy and safety data for aflibercept with and without photodynamic therapy in this condition.

3. Trial Design

This was a randomized, parallel-group, phase 4 study sponsored by Bayer. The registry record lists quadruple masking and a sham-controlled design. The trial enrolled 333 participants; the primary endpoint results are reported for 157 participants in the aflibercept-plus-sham-PDT group and 161 in the aflibercept-plus-active-PDT group. The registry lists a start date of 2014-05-29, primary completion on 2016-08-12, and status as completed.

Participants received intravitreal aflibercept during a shared run-in period: the arm descriptions specify injections every month for the first 3 months. At Week 12, participants were randomized to aflibercept plus sham PDT or aflibercept plus active PDT, with PDT described as applying to subjects qualifying for rescue treatment. The registry record does not report further detail in the truncated arm descriptions, including the complete criteria or treatment procedures.

The primary analysis used the Full Analysis Set, defined in the record as including all randomized subjects. The primary endpoint was mean change in best corrected visual acuity from baseline to Week 52, using ETDRS letter scores and the Last Observation Carried Forward approach. The registry record identifies 14 outcome measures and 15 analyses, but a complete prespecified statistical analysis plan, the trial's original sample-size justification, and details of interim analyses are not reported in the registry record.

A non-randomized aflibercept group appears in the adverse-event record, but it is not one of the two randomized groups in the primary efficacy comparison. Its role and selection process are not reported in the registry record. The randomized comparison should therefore be read as a comparison between the two assigned aflibercept-based strategies, not as a comparison involving that non-randomized group.

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, 428 subjects were screened, of them 95 were failed in screening. Remaining 333 subjects received at least one treatment. Of them, 15 subjects discontinued study participation before week 12 and were not randomized. Remaining 318 were randomized.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Full Analysis Set (FAS) included all randomized subjects

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: Baseline characteristics is reported in Full analysis set which included all randomized subjects (N=318).

6. Primary Endpoint

The registry lists the primary outcome as Mean Change in Best Corrected Visual Acuity (BCVA) as Measured by Early Treatment of Diabetic Retinopathy Study (ETDRS) Letter Scores From Baseline to Week 52 - Last Observation Carried Forward (LOCF), measured over From Baseline to Week 52.

The primary endpoint is the mean change in best corrected visual acuity (BCVA) from baseline to Week 52, measured with Early Treatment of Diabetic Retinopathy Study (ETDRS) letter scores and analyzed using Last Observation Carried Forward (LOCF). The unit is letters correctly read. BCVA is an assessment of visual function; the registry describes testing the study eye and fellow eye at study visits using a standard procedure adapted for Age Related Eye Disease Study (AREDS).

In that procedure, participants read from a 70-letter chart at a starting distance of 4 meters. Each line contains 5 letters, and the lines become smaller down the chart. Participants read until they reach a line where at least three letters can be read, and their score reflects the number of letters correctly identified. A change in the score summarizes the direction and average amount of change in measured visual acuity across the analysis population.

Using a continuous score preserves information about the amount of change, rather than reducing each participant's result to a simple improved-or-not category. It can therefore describe an average group change and a between-group difference. It does not, by itself, describe every participant's experience or establish how important a given change is to an individual. The registry record does not report a threshold for interpreting the clinical importance of a score change.

7. Results Posted in the Registry

• Aflibercept + Active PDT: mean 10.80 versus 10.70 on control; difference 0.10 (95% CI -2.32 to 2.52), standardized effect d = 0.01; z-test p = 0.935.

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 Subjects Who Avoided at Least 15 Letters Loss in ETDRS at Week 52

• 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 + Active PDT: 96.9% (156/161) versus 97.5% (153/157) on control; risk difference -0.6 percentage points (95% CI -4.2 to 3.1), risk ratio 0.99 (0.96–1.03); unadjusted two-proportion z-test p = 0.764.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Aflibercept + Active PDT and the control. The interval gives the range of effects that remain compatible with the data.

The posted secondary endpoint concerns the proportion of subjects who avoided at least 15 letters loss in ETDRS at Week 52. Its broad pattern is consistent with the primary endpoint in that the registry's analyses do not establish a clear difference between the randomized groups. The endpoint uses a threshold, whereas the primary analysis compares average letter-score change, so the two findings are related but not identical evidence.

The registry lists 14 outcome measures and 15 analyses, while one secondary outcome is posted in the available results. The registry record does not report the complete set of secondary results or a full account of how they were selected and analyzed. Consequently, the available secondary result cannot establish the pattern across all outcomes that may have been assessed.

Unadjusted secondary results carry less weight when many outcomes or analyses may be considered. As a general statistical explanation, examining multiple outcomes increases the chance that some results appear noteworthy by chance, even when there is no corresponding underlying effect. Adjustment procedures or a prespecified hierarchy can address aspects of this problem, but whether they were planned or used is not reported in the registry record. The secondary outcome should therefore be treated as supportive context, not as independent confirmation of efficacy or a substitute for the primary endpoint.

Differences in endpoint definition also matter. A threshold-based percentage counts participants on one side of a cutoff, while a mean summarizes the magnitude of scores across the group. Similar overall patterns can add context, but do not erase the uncertainty around either estimate. The registry record does not report a multiplicity strategy, so the confirmatory status of the posted secondary analysis is not clear.

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

• Percentage of Subjects Who Avoided at Least 15 Letters Loss in ETDRS at Week 52

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is continuous: each participant has a letter-score change, and the reported group value is a mean. A mean difference compares the average outcome between groups. The recalculated estimate uses the active-PDT group relative to the sham-PDT group, so a positive value indicates a higher average change in the active-PDT group under that subtraction order. The direction of the estimate should always be read alongside the group ordering and outcome definition.

What does the confidence interval describe?

As a general statistical explanation, a confidence interval expresses the uncertainty around an estimated effect under the assumptions of the method used to construct it. A wider interval indicates less precision; a narrower interval indicates greater precision. An interval that includes zero for a difference is compatible with no difference under that analysis, as well as with some values on either side of zero. It does not assign a probability to the true effect being within the particular interval.

The registry reports an ANCOVA estimate for the primary outcome, while the recalculation is an unadjusted estimate derived from posted group means, standard deviations, and group sizes. ANCOVA is a method for comparing an outcome between groups while accounting for covariates included in the model. Which covariates were included and how the model was specified are not reported in the registry record. The recalculation does not incorporate such adjustment; it is a simple summary-statistic comparison. The estimates should therefore be understood as results from different analytical approaches, not as duplicate computations of the same model.

Why report both analyses?

The sponsor-reported result records the trial's posted ANCOVA analysis. The unadjusted recalculation provides a transparent comparison based on the summary statistics. The two results are useful for different reasons: the reported model is the registry's own analysis, while the recalculation makes the basic group contrast accessible without implying details about model covariates that are not documented. Neither should be read without its confidence interval and the description of the endpoint.

What does the p-value mean?

As a general explanation, a p-value describes how incompatible the observed data are with a specified null hypothesis under the assumptions of a statistical test. It is not the probability that the null hypothesis is true, and it does not measure the size or importance of an effect. A large p-value does not prove that two treatments are equivalent. Here, the posted primary p-values do not supply evidence of a clear difference, but interpretation also depends on the effect estimates, confidence intervals, analysis methods, and trial design.

The unadjusted recalculation reports a p-value of 0.935, and the registry's ANCOVA analysis reports p = 0.548. They are not interchangeable because they arise from different analyses. The registry record does not report the detailed statistical analysis plan needed to determine all prespecified testing choices or adjustments.

What does the secondary endpoint add?

The secondary outcome is binary: it classifies whether a subject avoided at least 15 letters loss in ETDRS at Week 52. The reported percentages describe the proportion meeting that definition in each group. The risk difference compares those proportions by subtraction, with the active-PDT group relative to the sham-PDT group in the recalculation. A confidence interval around a risk difference describes uncertainty in that absolute contrast. The registry also posts a Cochran-Mantel-Haenszel analysis, which is a method for comparing categorical outcomes while accounting for strata. The registry record does not report the stratification details for this analysis.

Continuous and binary endpoints answer different questions. The mean change uses the full range of observed scores, while the binary endpoint reduces outcomes to whether a threshold was met. Turning a continuous measure into a category can make a result easier to describe but discards information about the size of changes within each category. The secondary endpoint can complement the primary result, but it should not replace it.

Why can over-dispersion matter?

As a general statistical explanation, over-dispersion occurs when observed variability is greater than a model assumes. If a model understates variability, it can make standard errors too small and intervals too narrow; if it accounts for variability appropriately, uncertainty estimates are more credible. The primary endpoint is analyzed as a continuous measure with a reported standard deviation, and the registry does not report an over-dispersion assessment or a model issue of this kind. It would therefore be inappropriate to infer that over-dispersion affected the trial results.

The primary endpoint uses LOCF, a method that carries a participant's last observed value forward for a later missing outcome. As a general explanation, this assigns a value rather than leaving the later outcome unobserved, and its validity depends on assumptions about missingness and change over time. The registry record does not report the amount or pattern of missing data, the time points at which observations were carried forward, or sensitivity analyses evaluating this choice. Those omissions limit assessment of how missing observations may have influenced the estimate.

11. Confidence Intervals and Precision

The primary endpoint estimates are not precise enough to pin down a single small between-group difference. In the simple unadjusted recalculation, the mean difference is 0.1 letters and the 95% confidence interval ranges from -2.32 to 2.52. The interval includes zero and extends to values on both sides of it. Thus the posted summary statistics are compatible with a range of possible differences, not just the point estimate.

The sponsor-reported ANCOVA result is -0.7 letters, with a 95% confidence interval from -2.9 to 1.6. It also spans zero. Its interval is not identical to the unadjusted interval, consistent with the fact that the two estimates come from distinct analyses. The registry record does not report enough model detail to explain the difference more specifically.

For the secondary binary endpoint, the recalculated risk difference is -0.006, with a 95% confidence interval from -0.042 to 0.031. The sponsor-reported treatment difference in percentage is 0.6, with a 95% confidence interval from -3.1 to 4.3. Both intervals encompass zero, and the posted results do not establish a clear difference in the proportion meeting the threshold.

As a general statistical explanation, confidence intervals describe uncertainty under the analysis assumptions; they do not guarantee that the true effect lies in the interval or indicate the probability of a treatment being better. The width of an interval reflects both the amount of information and variability in the data, alongside the method used. The primary endpoint's standard deviations are 11.3 letters and 10.7 letters in the sham-PDT and active-PDT groups, respectively. The uncertainty should be considered along with the distinction between a mean score change and a threshold-based secondary outcome.

12. Planning a Similar Trial: Sample Size

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

The planning figures are participants per arm, not total events. This follows the stated planning setup for these continuous and binary outcomes. Each row uses a different fraction of the observed effect as the effect to detect: 100% of the observed effect, 75% of the observed effect, or 50% of the observed effect. The original design assumptions and sample-size justification for the trial are not reported in the registry record; these figures are planning illustrations based on the observed effect, not the trial's original design calculation.

The planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The column for 80% power gives the estimated participants per arm for a design with an 80% chance of detecting the chosen effect under those assumptions, if that effect is real and the assumptions hold. The column for 90% power gives the corresponding participants per arm for a higher target chance of detecting that same effect.

Smaller effects require more participants to distinguish them from random variation with the same planned power and significance level. That pattern is reflected by the planning rows: using a smaller fraction of the observed effect leads to larger participant requirements. For example, the primary-outcome illustration ranges from 189,954 participants per arm for planning for 100% of the observed effect to 759,813 participants per arm for planning for 50% of the observed effect at 80% power. These are design illustrations, not evidence about how likely the completed trial was to find a result.

This is not observed power. It does not retrospectively measure the trial's success or the probability that its findings are true. It shows how the stated planning assumptions translate into hypothetical group sizes for selected effect sizes.

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 = 0.100; pooled standard deviation σ = 11.000.
2. n = 2 × (1.96 + 0.842)² × 11.000² / 0.100² = 189,953.0, rounded up to 189,954 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 <- 0.100000000000001                      # observed difference in means
sigma <- 11.0002934368226                     # 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(2120950)
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 = 189,954 (80% power), 254,294 (90% power)
 75% of observed effect: n per arm = 337,695 (80% power), 452,077 (90% power)
 50% of observed effect: n per arm = 759,813 (80% power), 1,017,173 (90% power)
power.t.test: 189954 
Simulated power at n = 189,954 per arm: 0.800 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The registry's sponsor-reported primary analysis is an ANCOVA comparison, with a mean difference (net) of -0.7 letters, a 95% confidence interval from -2.9 to 1.6, and p = 0.548. The posted recalculation is an unadjusted comparison derived from the group summary statistics; it gives a mean difference of 0.1 letters, a 95% confidence interval from -2.32 to 2.52, and an unadjusted p-value of 0.935.

These estimates should not be treated as contradictory readings of one identical calculation. The ANCOVA result is the registry-reported analysis, while the recalculation does not adjust for model covariates. The registry record does not specify which covariates were included in the ANCOVA or provide enough information to reproduce it. The recalculated result is useful as a transparent summary-statistic comparison, but it cannot replace the sponsor's model-based result or explain its choices.

Both analyses have confidence intervals spanning zero and neither shows a clear between-group difference in the primary outcome. The registry marks no discrepancy between the posted and recalculated results. That does not make the methods interchangeable; it indicates that the record does not flag a discrepancy requiring the sponsor's analysis to take precedence under a discrepancy rule.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists 14 outcome measures and 15 analyses, but the available results include one secondary endpoint. A complete prespecified analysis plan, including the primary and secondary testing sequence, is not reported in the registry record. The record also does not report whether the investigators used a multiplicity adjustment, a hierarchical testing strategy, or another method to control the chance of false-positive findings across outcomes.

As a general statistical explanation, multiplicity arises when several hypotheses are tested. The more results examined, the greater the opportunity for an apparently unusual finding to arise by chance. This is why isolated secondary p-values should not be interpreted in the same way as a single prespecified primary test unless the testing plan and any adjustment are understood. The posted secondary result is best read as descriptive or supportive evidence, with caution about its role in a wider set of outcomes.

The primary endpoint was analyzed in the Full Analysis Set, which the registry defines as all randomized subjects. The amount of missing outcome data, reasons for missingness, and the number contributing to each analysis are not reported in the registry record. The endpoint title specifies Last Observation Carried Forward. As a general explanation, LOCF fills a missing later measurement with a participant's last observed measurement. This can introduce bias if the assumptions required for that substitution do not hold.

The registry record does not report sensitivity analyses using alternative missing-data methods, an assessment of whether missingness differed by group, or details on exclusions from the analysis. It therefore does not permit a full appraisal of how missing observations affect the findings. The record also does not report interim analyses, stopping rules, or a sample-size justification for the trial's original design. These are gaps in the available record, not evidence that such procedures were or were not used.

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: retinal pigment epithelial tear (6.7%), sudden cardiac death (6.7%), acoustic neuroma (6.7%), senile dementia (6.7%), pneumonia (1.9%).

The adverse-event record reports serious adverse events affecting 27 participants in the aflibercept-plus-sham-PDT group and 25 participants in the aflibercept-plus-active-PDT group. It also lists 4 affected participants in a non-randomized aflibercept group. The numbers at risk were 157, 161, and 15, respectively. The non-randomized group is not part of the randomized efficacy comparison, and these figures should not be used as if it were a randomized arm.

Other adverse events affected 59 participants in the sham-PDT group, 49 in the active-PDT group, and 3 in the non-randomized group. Deaths recorded were 3, 0, and 1, respectively. The record lists retinal pigment epithelial tear, sudden cardiac death, acoustic neuroma, and senile dementia at 6.7% each among the top serious-event terms, followed by pneumonia at 1.9% and arrhythmia at 1.3%. These listings do not establish that an event was caused by treatment.

Counts alone do not account for event timing, severity details, recurrence, or attribution. The registry record does not report enough information to make those judgments. Safety comparisons should also account for the non-randomized group's different status and size; descriptive figures are not proof of a treatment-related difference.

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

The registry results describe mean visual-acuity score changes over the specified period and a secondary threshold-based outcome. In the primary endpoint, both randomized groups had positive mean changes, and the posted analyses do not establish a clear difference between aflibercept with sham PDT and aflibercept with active PDT. The confidence intervals show that the estimated difference remains uncertain. This is not proof that the strategies are identical, nor does it establish equivalence or non-inferiority.

The comparison is between two aflibercept-based strategies after a shared initial run-in. It does not compare aflibercept with no treatment. The results also apply to the trial's defined population and analysis, not automatically to every person with a related eye condition. The registry describes subjects with the polypoidal choroidal vasculopathy subtype of wet age-related macular degeneration, and the primary analysis population is the Full Analysis Set.

Mean change and the proportion avoiding a specified loss are group summaries. They do not indicate what happened to every participant, and the mean cannot show the distribution of individual changes. The registry record does not report a threshold for deciding whether the observed average change is clinically important. Statistical uncertainty and clinical interpretation are related but distinct questions.

The findings also depend on how outcomes were measured and missing data were handled. BCVA was assessed using ETDRS letter scores, and the primary endpoint specifies LOCF. The registry record does not report the amount or pattern of missing data or sensitivity analyses. Those omissions limit the conclusions that can be drawn about robustness to alternative missing-data assumptions.

Finally, posted adverse-event counts provide descriptive safety information, but do not alone establish causation or comparative safety. The non-randomized group should not be interpreted as an equivalent randomized comparator. Taken together, the registry supports a cautious reading of the posted group summaries and uncertainty estimates, rather than a broad claim beyond the measured outcomes and trial comparison.

18. Why This Trial Matters Statistically

This trial illustrates why a treatment comparison needs more than a difference between two group means. The unadjusted difference is small, but its confidence interval also communicates uncertainty about a range of possible differences. The sponsor-reported ANCOVA provides a separate estimate using a different analytical approach. Reading the point estimates, intervals, and methods together is more informative than relying on a p-value alone.

It also shows the importance of identifying the actual comparator. Both randomized groups received aflibercept; the randomized contrast concerns active versus sham PDT alongside aflibercept after the shared run-in. The result therefore addresses the incremental comparison represented by those strategies, not the effect of aflibercept against no treatment.

The outcome definitions illustrate a common distinction in clinical research. A continuous visual-acuity score captures average change, while a threshold-based secondary outcome describes the proportion meeting a categorical definition. These can give complementary perspectives, but they do not answer precisely the same question. Their interpretation also depends on clear reporting of analysis populations and missing-data procedures.

Finally, the registry record makes visible limits to interpretation: the full analysis plan, multiplicity strategy, original sample-size justification, and details about missing observations are not reported. Recognizing these gaps is part of statistical interpretation. It prevents over-reading a non-significant result as proof of no difference and prevents unadjusted secondary findings from being treated as definitive.

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.

The registry record does not provide a complete protocol or statistical analysis plan. Covariates in the sponsor-reported ANCOVA, details of the Cochran-Mantel-Haenszel stratification, the testing hierarchy, and any multiplicity adjustment are not reported. Without these details, the model-based analysis and the confirmatory status of secondary results cannot be fully assessed.

The primary outcome specifies LOCF, but the record does not report how much data were missing, why observations were missing, or how missingness differed between groups. It also does not report sensitivity analyses using alternative assumptions. This limits assessment of how robust the primary estimate is to the treatment of missing data.

The arm descriptions are truncated after describing the run-in and randomization, and the registry record does not provide complete details of eligibility for rescue PDT or the remaining treatment procedures in those descriptions. The non-randomized aflibercept group appears in the safety record, but its selection and role are not reported. It should not be treated as a randomized comparison group.

Although 333 participants were enrolled, endpoint results are reported for the two randomized groups with their stated group sizes. The record does not explain the difference between enrollment and the groups contributing to the posted primary analysis. The registry lists 14 outcome measures and 15 analyses but posts one secondary endpoint, so the full results context is not available. The original design assumptions, sample-size justification, and details of interim analyses are also not reported in the registry record.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Aflibercept in Polypoidal Choroidal Vasculopathy — NCT02120950.
• Registry record last updated 2020-12-02; status last verified 2020-11.
• Results first posted 2019-01-15.
• 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

NCT02120950 is a completed randomized phase 4 study of aflibercept with sham PDT versus aflibercept with active PDT in subjects with polypoidal choroidal vasculopathy. The record lists quadruple masking, a parallel-group model, and enrollment of 333 participants. Both groups received aflibercept during the initial run-in; randomization to active or sham PDT occurred at Week 12.

The primary endpoint was mean change in BCVA ETDRS letter score from baseline to Week 52 using LOCF in the Full Analysis Set. The sponsor-reported ANCOVA and the unadjusted recalculation both have confidence intervals spanning zero and do not establish a clear between-group difference. The available secondary result has a similar broad pattern, but multiplicity details are not reported.

The record includes serious and other adverse-event counts, but the figures are descriptive and do not establish causation. Important design and analysis details, including the original sample-size justification and missing-data sensitivity analyses, are not reported in the registry record.