Effect of Intravitreal VEGF-Trap Eye on Polypoidal Choroidal Vasculopathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Effect of Intravitreal VEGF-Trap Eye on Polypoidal Choroidal Vasculopathy (NCT01950741), a na phase 4 study. The primary outcome is Percentage of Patients Lose Visual Acuity Less Than 15 Letters.

2. Clinical Question

Statistically, the central question is descriptive: among the patients included in the specified analysis, what proportion met the visual-acuity threshold at 12 months? A single-group study can characterize outcomes after the intervention, but without a concurrent comparator it cannot isolate the intervention’s effect from other explanations for the observed outcomes. The record also lists secondary measures, including visual-acuity changes, visual-acuity thresholds, polypoidal-lesion resolution on angiography, and a visual-function questionnaire. Numerical findings for those measures are not reported in the registry record.

3. Trial Design

The registry identifies NCT01950741 as a completed Phase 4, single-group study sponsored by Pusan National University Hospital. Enrollment is recorded as 48. The allocation field is not applicable, masking is listed as none, and the model is single group. Those design features mean that the study did not randomly assign participants between intervention and control groups, and it had no concurrent control arm for a treatment comparison.

The intervention was aflibercept injected into the vitreous cavity. The arm description states a dose of 2 mg, with injections monthly for the initial three injections and then every other month at months 4, 6, 8, and 10. The description calls this a total of 7 injections over 1 year. There is a wording difference within the record: the official title describes a “Single Dose Study,” while the arm description specifies a repeated-injection schedule. The registry does not explain that difference, so the schedule is best understood from the detailed arm description without inferring a protocol rationale.

The stated primary endpoint was assessed at 12 months. The record says 45 patients completed the study and that data for 5 were inadequate for the primary analysis; 40 were included in the per-protocol set. These numbers describe the flow and analysis population as recorded, but the registry does not give further detail about why data were inadequate or how missing observations were handled.

The record lists the study as starting in 2013-09 and reaching primary completion in 2015-05. Although the record is marked completed, numerical results for the primary endpoint and listed secondary outcomes are not reported in the registry record. No analysis entries are listed. The study can therefore be described by its design and planned measures, but its treatment outcomes cannot be quantitatively evaluated from the posted results.

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.

Overall Study

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Among 45 patients who completed the study, data of 5 were inadequate for the analysis. Forty patients were included in the analysis as per protocol set.

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.

6. Primary Endpoint

The registry lists the primary outcome as Percentage of Patients Lose Visual Acuity Less Than 15 Letters, measured over 12 months.

The primary endpoint is titled “Percentage of Patients Lose Visual Acuity Less Than 15 Letters” and has a 12-month timeframe. In plain terms, it concerns the proportion of the analysis population whose visual-acuity loss stayed below the stated 15-letter threshold. The record does not report the observed percentage, so the endpoint’s value cannot be interpreted from the registry entry.

Visual acuity was assessed using the Early Treatment Diabetic Retinopathy Study (ETDRS) chart. The record describes a scale from 0 letters read to a maximum possible score of 100 letters, and states that 85 letters is equivalent to 20/20. Higher scores represent better functioning. This provides a standardized way to record visual-acuity performance and to express change in terms of letters read.

As a general statistical point, a threshold endpoint can be easier to communicate than a continuous score: it classifies whether an individual’s change meets a prespecified criterion. That simplification also discards detail. People just on opposite sides of a threshold may have similar changes, while people within the same category may have quite different changes. A continuous change measure can retain more of that information, though it may be less immediately interpretable.

The record’s primary population was the per-protocol set, not every enrolled participant: it states that 40 patients were included after the completion and data-adequacy exclusions described in the record. Without the outcome count or percentage, and without an uncertainty interval, neither the observed frequency nor its precision can be assessed.

7. Why No Re-analysis Is Shown

8. Statistical Interpretation

9. Statistical Methods Explained

Statistical interpretation begins by distinguishing a study question from a study result. The primary endpoint names a 12-month visual-acuity threshold, and the record describes how visual acuity was measured. Those details define the quantity the study intended to examine. They do not reveal the observed percentage. Since no numerical primary result or analysis is reported in the registry record, there is no estimate to interpret or test.

What does a single-group design estimate?

In general, a single-group study can describe outcomes among people who received an intervention. If baseline and follow-up measurements are available, it can also describe within-group change. But a within-group change is not automatically an estimate of the intervention’s causal effect. Without a concurrent comparison group, the observed trajectory can also be influenced by the condition’s natural course, selection into the study, measurement processes, other care, or changes over time. Random assignment and a suitable comparison help address some of those alternative explanations; this study is recorded as single group, with no allocation and no masking.

That design distinction is especially important when a title or outcome description uses language about an intervention’s “effect.” The title expresses the topic under evaluation, while the design determines what comparisons the data can support. The record describes no randomized control comparison, so it cannot support a direct estimate of the difference between aflibercept and another treatment from this study alone.

What does a confidence interval contribute?

As a general concept, a confidence interval presents a range of estimates compatible with the data under the statistical method used. It conveys sampling uncertainty around an estimate; it does not correct bias, establish causality, or guarantee that the true value lies within the interval. A narrow interval usually indicates greater statistical precision than a wide one, while the substantive meaning still depends on the endpoint and design. Neither an interval nor a point estimate for the primary outcome is reported in the registry record, so its precision cannot be assessed.

Why does the analysis population matter?

The record says the primary analysis used the per-protocol set. Per-protocol analyses generally include participants who meet specified adherence or eligibility conditions, although the precise rules can differ by protocol. Such an analysis may answer a question about outcomes among those included in that set, but exclusions can affect how representative the estimate is of everyone enrolled. Here, the record states that 45 patients completed the study, data for 5 were inadequate for analysis, and 40 were included in the per-protocol set. The reasons for inadequacy, the handling of missing data, and the criteria for the set are not reported in the registry record. It is therefore not possible to assess the effect of those exclusions.

How should threshold outcomes be read?

The primary endpoint classifies patients by whether visual-acuity loss was less than the stated threshold. In general, dichotomizing a measured change makes a result easier to summarize as a proportion, but removes detail about the magnitude of individual changes. The choice and prespecification of the threshold matter: changing it can change the percentage classified as meeting the outcome. The record identifies the threshold and timeframe, but does not provide an observed count, percentage, or analysis method for that outcome.

The ETDRS chart supplies a letter-based measurement scale. As a general point, a standardized instrument can improve consistency in measurement, but measurement reliability does not resolve design limitations or missing data. Nor does a scale description reveal the distribution of observed scores. The record’s separate listing of visual-acuity change as a secondary outcome could in principle complement a threshold measure, but the numerical change result is not reported in the registry record.

What do the planning assumptions mean?

The sample-size material is described as a planning illustration based on an observed effect, not as the study’s own design calculation. Its stated assumptions are a two-sided significance level of 0.05, equal allocation between two arms, a normal approximation, and an effect to detect expressed as a stated fraction of the observed effect. Those are hypothetical planning assumptions, not evidence that this single-group study used a two-arm design. The registry record does not report the protocol’s sample-size justification, and the illustration should not be described as observed power. Planning calculations ask what sample size might be needed under assumptions; they do not measure the probability that an observed result is true or demonstrate that a completed study had adequate power.

As a general matter, power calculations depend on the assumed effect, variability, significance level, allocation, and analysis method. If those assumptions do not match the eventual study, the resulting planning estimate may not describe the design actually used. Since this study has no concurrent comparator, the two-arm planning assumptions should not be mistaken for a feature of its allocation. The record also does not provide a posted numerical primary result from which to assess an observed treatment contrast.

Finally, the record lists no analysis entries. This means the posted entry does not document inferential procedures or results. The statistical methods used for the primary outcome, including any model, adjustment, or interval estimation, are not reported in the registry record. Without those details and the outcome data, a reanalysis or independent check of the primary claim is not possible from the registry record.

10. Exact Estimates for Each Arm

No two-arm comparison is shown for this trial, but each arm's result can still be summarized with exact interval estimates computed from the posted counts. The Clopper-Pearson interval is exact and conservative; the Wilson interval is a common closer-to-nominal alternative; the Bayesian credible interval uses a uniform Beta(1, 1) prior. For small groups the three can differ noticeably.

R code and output

arm    <- c("Aflibercept")
n      <- c(40)
events <- c(35)
for (i in seq_along(n)) {
  ci <- binom.test(events[i], n[i])$conf.int          # Clopper-Pearson exact interval
  cr <- qbeta(c(0.025, 0.975), 1 + events[i], 1 + n[i] - events[i])   # Bayesian, uniform Beta(1,1) prior
  wi <- (function(x, n) { p <- x / n; z <- qnorm(0.975); d <- 1 + z^2 / n
    c((p + z^2 / (2 * n) - z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d, (p + z^2 / (2 * n) + z * sqrt(p * (1 - p) / n + z^2 / (4 * n^2))) / d) })(events[i], n[i])
  cat(sprintf("ARM|%s|%d|%d|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f|%.1f\n", arm[i], n[i], events[i], 100 * events[i] / n[i],
              100 * ci[1], 100 * ci[2], 100 * wi[1], 100 * wi[2], 100 * cr[1], 100 * cr[2]))
}

ARM  Aflibercept  40  35  87.5  73.2  95.8  73.9  94.5  73.8  94.4

11. Multiplicity, Missing Data and Analysis Populations

The record lists a primary endpoint and several secondary outcomes. Considering multiple outcomes can raise a multiplicity issue: in general, the more statistical tests or claims examined, the greater the chance that at least one result may appear notable by chance if no adjustment or prespecified hierarchy is used. A protocol may address this through a testing order, an adjustment method, or a clear distinction between confirmatory and exploratory outcomes. Such a plan is not reported in the registry record, so it is not possible to determine how multiplicity was handled.

The registry names secondary measures that include visual-acuity change, visual-acuity thresholds, polypoidal-lesion resolution on ICG angiography, and a VFQ-25 score. The entry does not provide numerical findings for these outcomes. It also does not report analysis entries, so no testing hierarchy, adjusted p-values, or other multiplicity procedures can be evaluated. The primary result itself is not reported in the registry record.

Missing data also require attention. The record says that among 45 patients who completed the study, data for 5 were inadequate for the primary analysis, leaving 40 in the per-protocol set. It does not explain why the data were inadequate, whether the issue concerned the endpoint measurement or another criterion, or what assumptions were used for missing observations. The registry does not report imputation, sensitivity analyses, or an analysis of all enrolled participants. No conclusion about the direction or size of any missing-data effect can be drawn from the information recorded.

The per-protocol population should therefore be kept distinct from the enrolled group and from the completion count. The listed analysis population is specific to the primary outcome and does not establish how other outcomes were analyzed. Further detail about analysis populations, exclusions, missingness, and multiplicity is not reported in the registry record.

12. 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: death (2.1%).

The safety summary lists an Aflibercept group with 47 at risk for serious adverse events and 1 affected; for other adverse events it lists 47 at risk and 4 affected. These are registry-listed counts, not estimates from a comparison with another group. Since the study had a single group, the figures do not establish comparative safety relative to a control or another treatment.

The record also lists “Death” among the top serious adverse-event terms, with 2.1%. The separate deaths field is not populated. The registry does not explain how that term-level percentage relates to the serious-event count, whether the term represents an event or an affected participant, or why the separate deaths field is blank. It is therefore important not to infer an unreported death count or reconcile the entries by calculation.

In general, adverse-event summaries need context: how events were defined and collected, how long participants were monitored, and whether counts refer to events or people can affect interpretation. The posted summary does not supply enough detail to answer all of those questions. These figures should be read as the safety information recorded in the registry, not as proof of causation or as a complete account of risk.

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

The record shows that a completed single-group study was organized to evaluate aflibercept in treatment-naive PCV, with a specified injection schedule and a 12-month visual-acuity endpoint. It also identifies the ETDRS chart as the measurement instrument and describes the per-protocol analysis population. These details help explain the research question and how the principal outcome was intended to be assessed.

What the record does not show is the observed primary-outcome percentage. No numerical result for that endpoint, confidence interval, or inferential test is reported in the registry record. Thus, the posted information cannot establish how many patients met the threshold, how precisely that proportion was estimated, or whether any observed change was statistically compatible with a range of possible values. The listed secondary outcomes also lack numerical results in the registry record.

The absence of a comparator limits the conclusions even if an outcome estimate were available. In general, an outcome observed after treatment in one group cannot by itself separate treatment effects from the natural course of illness, selection, measurement variation, or other influences. The single-group design is useful for describing what was observed in the treated group, but it does not provide a randomized contrast.

The safety summary records adverse-event counts and a serious-event term, but its entries do not establish comparative risk or resolve the relationship between the listed term and the separate deaths field. The posted summary should be interpreted as limited registry safety information rather than a complete causal assessment.

Accordingly, the appropriate conclusion is about the record’s content: it documents a study design, intervention schedule, endpoint, and analysis population, but not a quantitative efficacy result. The completed status does not fill that reporting gap. Neither a favorable nor an unfavorable treatment conclusion can be drawn from the missing outcome data, and the sample-size planning illustration should not be treated as observed power or as evidence of the study’s findings.

14. Why This Trial Matters Statistically

This study is statistically informative as an example of why design and reporting must be read together. The registry describes an intervention and a clinically relevant visual-acuity threshold, but the single-group design determines the scope of inference. A descriptive outcome in one group is not equivalent to a controlled estimate of treatment effect. Recognizing that distinction prevents a study title or treatment-focused objective from being mistaken for evidence of a causal comparison.

The endpoint also illustrates a common trade-off in outcome definition. A threshold proportion can be readily communicated, while a continuous visual-acuity change can preserve more information about the range and magnitude of changes. The record lists both kinds of outcome, but reports no numerical results for either. Without those values, readers cannot assess the endpoint’s observed frequency or compare the threshold result with the change measure.

Analysis populations are another important feature. The record specifies a per-protocol set and reports exclusions from the primary analysis due to inadequate data. That makes clear that the primary analysis did not include every person described in the enrollment record, but the reasons and missing-data methods are not reported. Transparent reporting of these details is essential because analysis choices can affect both the interpretation and generalizability of an estimate.

Finally, the record illustrates why planning calculations must be separated from results. The described sample-size assumptions concern a hypothetical two-arm planning illustration, whereas the registered study is single group. Such an illustration is not the trial’s design justification and is not observed power. Taken together, these features show why a careful statistical reading considers endpoint definition, comparator structure, analysis population, missingness, and the completeness of outcome reporting before drawing conclusions.

15. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information recorded for this study. First, the registry describes a single-group design with no concurrent comparator. That prevents a direct randomized comparison and limits causal interpretation of any within-group outcome. Second, numerical results for the primary endpoint and named secondary outcomes are not reported in the registry record. Without estimates, the outcome pattern and its precision cannot be evaluated.

The primary analysis used a per-protocol set. The record says 45 patients completed the study, data for 5 were inadequate for the analysis, and 40 were included in that set. It does not state why the data were inadequate, define the per-protocol criteria, or describe missing-data handling. This leaves uncertainty about the impact of the exclusions and about the population represented by the analysis.

The record also lists masking as none. Lack of masking can, in general, affect outcome assessment or participant reporting, although the effect depends on the outcome and measurement process. The entry does not describe safeguards or explain how outcome assessment was conducted beyond identifying the ETDRS chart.

There is a wording difference between the official title’s “Single Dose” phrasing and the arm description’s repeated injections over 1 year. The registry does not explain this difference. The record also does not report a sample-size justification, a detailed statistical analysis plan, interim-analysis information, or a multiplicity procedure. These details should be treated as unreported, rather than inferred from the planning illustration. Finally, the safety summary includes a serious-event term with a percentage while the separate deaths field is blank; the record does not explain the relationship between those entries.

16. Related Tutorials

17. Related Statistical Calculators

18. Sources

• ClinicalTrials.gov: Effect of Intravitreal VEGF-Trap Eye on Polypoidal Choroidal Vasculopathy — NCT01950741.
• Registry record last updated 2016-04-29; status last verified 2016-03.
• Results first posted 2016-04-29.
• 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.

19. Record Summary

NCT01950741 is recorded as a completed Phase 4, single-group study sponsored by Pusan National University Hospital. It evaluated aflibercept for treatment-naive polypoidal choroidal vasculopathy, with a 2 mg intravitreal injection schedule described as 7 injections over 1 year. The primary endpoint concerned the percentage of patients with visual-acuity loss below the stated letter threshold at 12 months, measured using the ETDRS chart.

The record describes 45 patients as completing the study and 40 as included in the per-protocol primary analysis after data for 5 were deemed inadequate. It lists secondary visual-acuity, angiographic, and questionnaire outcomes. However, numerical efficacy findings and inferential analyses are not reported in the registry record. The single-group design also provides no concurrent control comparison. The posted record therefore documents study design and outcome definitions, but does not support a quantitative conclusion about the primary result.