Prospective Randomized Controlled Study of Intravitreal Injection of Bevacizumab for Proliferative Diabetic Retinopathy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Prospective Randomized Controlled Study of Intravitreal Injection of Bevacizumab for Proliferative Diabetic Retinopathy (NCT01854593), a randomized phase 4 study. The primary outcome is Reoperation.

2. Clinical Question

3. Trial Design

The registry describes a prospective, randomized, double-masked, parallel-group, phase 4 study. Enrollment was 69. The study status is completed; the start is recorded as 2012-05 and primary completion as 2013-08. Nihon University is listed as the sponsor.

The intervention was 0.16 mg/0.05 ml intravitreal bevacizumab one day before vitrectomy. The comparison group received a sham injection one day before vitrectomy. The registry record does not identify which parties were masked, how the random sequence was generated, or how assignment was concealed. Further design details, including eligibility criteria and the original sample-size rationale, are not reported in the registry record.

The primary outcome was vitreoretinal reoperation due to recurrent vitreous hemorrhage, assessed at 1 month. Secondary outcomes listed in the record include intraoperative and postoperative hemorrhage, vitreous vascular endothelial growth factor concentration, endolaser photocoagulation, iatrogenic retinal tears, surgical time, and visual-acuity outcomes. The registry lists 12 secondary outcome measures. Numerical results for all secondary measures are not reported in the registry record.

For the primary outcome, the reported group sizes were 32 in the bevacizumab and vitrectomy group and 34 in the sham injection and vitrectomy group. These are the denominators attached to the posted outcome results; further details about the analysis population and participant flow are not reported in the registry record.

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

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 Reoperation, measured over 1 month.

The primary endpoint counts participants who underwent vitreoretinal reoperation because of recurrent vitreous hemorrhage during the 1-month timeframe. It is a binary outcome at the participant level: each participant either had the specified event or did not, as recorded for this endpoint. The registry reports 1 event in the bevacizumab and vitrectomy group and 7 in the sham injection and vitrectomy group.

This endpoint captures a clinically consequential event that could lead to another operation after the initial vitrectomy. It is narrower than counting any postoperative hemorrhage: the reoperation must be due to recurrent vitreous hemorrhage. Postoperative vitreous hemorrhage is also listed as a separate secondary outcome, so the two endpoints should not be treated as interchangeable.

The 1-month timeframe defines the period covered by the primary result. Events outside that period are not represented by this endpoint as reported. The registry does not report further endpoint-adjudication rules, such as how recurrent hemorrhage was defined or how the reason for reoperation was confirmed.

7. Results Posted in the Registry

• Bevacizumab and Vitrectomy: 3.1% (1/32) versus 20.6% (7/34) on control; risk difference -17.5 percentage points (95% CI -32.3 to -2.6), risk ratio 0.15 (0.02–1.17); unadjusted two-proportion z-test p = 0.030.

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.

Intra Operative Hemorrhage

• 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:
  • Bevacizumab and Vitrectomy: mean 0.63 versus 1.30 on control; difference -0.67 (95% CI -1.25 to -0.09), standardized effect d = -0.55; z-test p = 0.025.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Bevacizumab and Vitrectomy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Postoperative Vitreous Hemorrhage.

• Endpoint type: Binary: the number of participants with the event, compared as proportions.
• Test: Unadjusted two-proportion z-test, with a Wald 95% confidence interval for the risk difference.
• Result:
  • Bevacizumab and Vitrectomy: 9.4% (3/32) versus 38.2% (13/34) on control; risk difference -28.9 percentage points (95% CI -48.1 to -9.7), risk ratio 0.25 (0.08–0.78); unadjusted two-proportion z-test p = 0.006.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically lower for Bevacizumab and Vitrectomy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Vascular Endothelial Growth Factor Concentration in Vitreous

• 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:
  • Bevacizumab and Vitrectomy: mean 25.00 versus 1,315 on control; difference -1,290 (95% CI -1,678 to -902.41), standardized effect d = -1.56; z-test p = <0.001.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Bevacizumab and Vitrectomy than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Among the secondary outcomes with numerical results reported in the registry record, the observed directions generally favor the bevacizumab and vitrectomy group on the measures presented: surgical bleeding-related measures and postoperative vitreous hemorrhage were lower, as was vitreous vascular endothelial growth factor concentration. These outcomes are related to the clinical and biological context of the primary question, but they measure different things. A surgical observation, a postoperative event, and a laboratory concentration are not interchangeable evidence for the reoperation endpoint.

The secondary findings can provide context for the primary result by describing other aspects of surgery and postoperative course. They do not independently confirm the primary finding. The registry lists 12 secondary outcome measures, but numerical results for all of them are not reported in the registry record. No single summary across these outcomes is reported, and combining them into one conclusion would obscure their distinct definitions and scales.

Unadjusted secondary results carry less weight because multiple comparisons increase the chance that at least one result appears notable by chance. The registry does not report whether the secondary outcomes were arranged in a prespecified testing hierarchy or whether p-values were adjusted for multiplicity. Their results are best treated as exploratory context, interpreted alongside the primary endpoint, uncertainty, and the limits of the record rather than as a collection of independent confirmations.

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

• Intra Operative Hemorrhage
• Postoperative Vitreous Hemorrhage.
• Vascular Endothelial Growth Factor Concentration in Vitreous
• Endolaser Photocoagulation
• Iatrogenic Retinal Tears
• Surgical Time
• Postoperative Best Corrected Visual Acuity
• Best Corrected Visual Acuity Change

9. Statistical Interpretation

10. Statistical Methods Explained

What does the risk difference describe?

A risk difference compares the proportion of participants with an event in one group with the proportion in the other. For this trial, the recalculated risk difference is -0.175 for bevacizumab and vitrectomy relative to sham injection and vitrectomy. Its negative sign indicates fewer observed primary events proportionally in the intervention group. Unlike a relative measure, a risk difference is expressed on the absolute probability scale. The registry also reports event counts and group sizes, which give the underlying context for the estimate.

A confidence interval describes a range of values compatible with the observed data under the calculation's assumptions. It conveys uncertainty around an estimate; it is not a guarantee that the true effect lies in that particular interval. The primary interval extends from -0.323 to -0.026. Its endpoints are both negative, while its width reflects that the estimate remains uncertain. An interval is not a substitute for considering study design, outcome definition, and completeness of follow-up.

What does a p-value tell the reader?

A p-value evaluates how compatible the data are with a null model of no group difference, given the test and its assumptions. It does not measure the probability that the null model is true, and it does not quantify clinical importance. The registry reports Fisher Exact for the primary comparison, with p=0.033. The unadjusted recalculation is p=0.03. A result below a conventional threshold is not proof that an effect is real or that it will recur; a result above a threshold would not prove equality either.

Fisher Exact is a method for comparing categorical event counts and is commonly useful when counts are small. The primary outcome has relatively few observed events in both groups, making an exact test a suitable way to assess the count comparison without relying on a large-sample approximation. The reported analysis is a superiority-or-other test; the registry does not report a noninferiority margin or an equivalence framework.

How should continuous outcomes be read?

For continuous outcomes, the registry presents group means and standard deviations. A mean is a measure of the center of the observed values; a standard deviation describes their spread. The recalculated mean difference compares the group means, with a negative value indicating a lower mean in the bevacizumab group for the reported direction of comparison. For intraoperative hemorrhage, the registry reports a Wilcoxon (Mann-Whitney) test. This rank-based test compares the distributions of observations using their ranks; it is not simply a test of the difference between means. Thus, the displayed means and standard deviations describe the data, while the reported test assesses a different feature of the data through ranks.

The same distinction matters for vitreous vascular endothelial growth factor concentration. The registry reports a mean and standard deviation for each group and a Wilcoxon (Mann-Whitney) test. The concentration values have a wide spread in the sham group as reported, but the registry does not provide enough distributional detail to characterize the shape of the data. A rank-based test can be useful when distributional assumptions for a mean-based test may not be appropriate; that is a general statistical rationale, not a claim about the analysis plan used by the investigators.

Why does over-dispersion matter?

Over-dispersion means that observed variability is greater than a statistical model assumes. In general, ignoring over-dispersion can make standard errors too small and confidence intervals too narrow, producing more apparent precision than the data justify. This is a general consideration for count outcomes and other variable data, not a reported feature or adjustment in this trial. The registry does not report an over-dispersion assessment or a model-based analysis for the primary endpoint.

The secondary outcomes do not all have the same scale. Some are event counts, some are continuous measurements, and some concern procedures or surgical observations. Their methods and interpretations should therefore be tied to the outcome being measured rather than treated as interchangeable tests. The registry's reported methods include Chi-squared for postoperative vitreous hemorrhage and Wilcoxon (Mann-Whitney) for the listed continuous outcomes. Full analysis specifications, including any adjustment variables, are not reported in the registry record.

What is the role of unadjusted analyses?

An unadjusted comparison describes the observed group contrast without accounting for other variables. It can be informative in a randomized study, but the registry record does not state whether the sponsor's analysis included any covariate adjustment beyond the reported test. The recalculated estimates are simple unadjusted re-calculations from the posted summary statistics. They should not be interpreted as replacing a fuller prespecified analysis if one exists outside the registry record. The record does not report such a plan.

Multiple testing is another general concern. If many outcomes are tested, some may appear statistically notable by chance even when no real difference exists. The record lists multiple secondary outcomes but does not report a correction strategy, a hierarchy, or which secondary outcomes were designated confirmatory. This limits how strongly individual secondary p-values can be interpreted.

11. Confidence Intervals and Precision

Precision concerns how narrowly an estimate is determined by the available data. The primary risk-difference estimate is -0.175, with a confidence interval from -0.323 to -0.026. This interval remains on the negative side of zero, but it covers a range of effect sizes rather than identifying one exact value. The relatively small event counts are important context: when outcomes are uncommon and group sizes are limited, estimates can be sensitive to a small number of events.

The confidence interval gives more information about magnitude and uncertainty than the p-value alone. A p-value summarizes compatibility with a null model under a test; it does not show the range of plausible effect sizes. The interval does not account for every possible source of uncertainty, such as incomplete follow-up, endpoint misclassification, or limitations in the analysis population. Details about these issues are not reported in the registry record.

For the secondary outcomes, the precision varies by measurement and estimate. Their confidence intervals, where recalculated values are available, should be read in relation to the scale of each endpoint. A mean difference in a laboratory measure is not directly comparable to a risk difference in a participant-level event. The registry's posted numerical results do not establish how precisely every listed secondary outcome was estimated, because numerical results for all 12 secondary outcome measures are not reported in the registry record.

Precision is distinct from importance. A narrow interval can indicate a more tightly estimated result without showing that the effect matters clinically; a wider interval can leave substantial uncertainty even when a point estimate appears large. Interpretation should therefore consider the endpoint definition, timeframe, event counts, and the uncertainty around the estimate together.

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 illustrations report participants per arm for the binary and continuous outcomes discussed in this analysis; they are not total event counts. The stated calculation assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is set as a stated fraction of the observed effect. The original trial's own sample-size assumptions and justification are not reported in the registry record.

The 80% power column gives the number of participants per arm that the planning calculation estimates would be needed to have an 80% chance of detecting the specified effect under those assumptions. The 90% power column gives the corresponding planning number for a 90% chance. These are design-planning quantities, not probabilities that this completed study detected an effect. For example, planning for 75% of the observed primary effect gives 110 participants per arm for 80% power and 146 participants per arm for 90% power.

The rows use different fractions of the observed effect. A smaller effect is harder to distinguish from random variation, so the planning calculation requires more participants to attain the same power. The illustrations use an effect estimated from this trial, which can be uncertain and may not match an effect in a future study. They should be read as conditional planning scenarios rather than a recommendation or a reconstruction of the trial's original design. This is not observed power.

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 = 0.206; treatment proportion p₁ = 0.031; average p̄ = 0.119.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.4572 = 0.8961.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4402 = 0.3705.
4. n = (0.8961 + 0.3705)² / (-0.1746)² = 52.6, rounded up to 53 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 <- 0.205882352941176                          # control proportion
p1 <- 0.03125                          # 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(1854593)
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 = 53 (80% power), 70 (90% power)
 75% of observed effect: n per arm = 110 (80% power), 146 (90% power)
 50% of observed effect: n per arm = 279 (80% power), 373 (90% power)
power.prop.test: 52.6 
Simulated power at n = 53 per arm: 0.850 (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 reports the sponsor's primary analysis as Fisher Exact, with p=0.033. The simple unadjusted recalculation from posted summary statistics gives a risk difference of -0.175, a confidence interval from -0.323 to -0.026, and an unadjusted p-value of 0.03. The registry record does not flag a discrepancy between the sponsor analysis and the recalculation.

The two p-values are close but are not identical. The sponsor's analysis is the reported trial analysis; the recalculated result is a separate unadjusted calculation from the posted summaries. The estimate and interval add information about the direction, magnitude, and uncertainty of the group contrast that a p-value alone does not convey. Neither calculation reveals the details of participant-level data or any aspects of the analysis not reported in the registry record.

The registry does not report a detailed statistical analysis plan against which to assess whether the sponsor analysis followed prespecified methods, nor does it report adjustment variables or sensitivity analyses. The recalculation should therefore be read as a transparent summary-statistic comparison, not as a replacement for the sponsor's trial analysis or an independent reanalysis of individual participant data.

15. Multiplicity, Missing Data and Analysis Populations

The registry reports a primary outcome and multiple secondary outcome measures. Testing several outcomes raises a general multiplicity concern: the more comparisons considered, the greater the chance of finding one or more apparently notable results by chance. This does not mean a secondary result is necessarily spurious; it means that the strength of evidence cannot be assessed from an individual unadjusted p-value alone when the testing plan is unknown.

A multiplicity strategy can include adjusting the significance threshold, controlling an error rate, or specifying an ordered testing hierarchy. Whether any such approach was used is not reported in the registry record. The record also does not report which secondary outcomes, if any, were confirmatory rather than exploratory. The posted secondary p-values should therefore be interpreted cautiously and should not be treated as if they came from a single prespecified test.

Missing-data handling is also not reported in the registry record. The posted denominators for the primary endpoint are 32 and 34, but the record does not explain whether all randomized participants contributed data, whether anyone was lost to follow-up, or how missing endpoint observations were handled. An analysis population, such as intention-to-treat or per-protocol, is not reported in the registry record. These details matter because exclusions or missing outcomes can affect the comparability created by randomization.

The registry does not report whether sensitivity analyses were conducted to examine alternative assumptions about missing outcomes, protocol deviations, or endpoint classification. It also does not report an interim-analysis plan or stopping rules. These absences do not show that such procedures were or were not used; they limit what can be concluded from the registry record alone.

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 0% reporting threshold.

For serious adverse events, the registry reports 0 affected participants in the bevacizumab and vitrectomy group, with 32 at risk, and 0 affected participants in the sham injection and vitrectomy group, with 34 at risk. The registry also reports 0 participants with other adverse events in each group, using those same group-specific at-risk counts.

These figures describe what was recorded for the reported adverse-event categories and groups. They do not establish that no adverse events of any kind occurred, nor do they rule out uncommon harms. The deaths field is not reported for either group; it should not be interpreted as a reported zero. The record does not provide further detail on adverse-event definitions, severity, timing, or collection procedures. Safety interpretation is therefore limited to the categories and counts recorded in the registry.

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

The primary data show fewer observed reoperations due to recurrent vitreous hemorrhage in the bevacizumab and vitrectomy group than in the sham injection and vitrectomy group during 1 month. The recalculated risk difference and its confidence interval describe the direction and uncertainty of that observed contrast. The sponsor-reported Fisher Exact result and the recalculation are statistical summaries of the trial comparison, not guarantees about what would occur in another setting.

The result does not by itself establish that bevacizumab caused the observed difference, that the same result would occur in other populations or clinical settings, or that every outcome would move in the same direction. Randomization is an important design feature for comparing groups, but the registry record does not report enough detail about participant flow, missing outcomes, or analysis populations to assess all potential sources of bias.

The endpoint is specifically reoperation due to recurrent vitreous hemorrhage within 1 month. It does not represent every postoperative outcome, all hemorrhages, longer-term vision, or later reoperations. The record lists secondary visual-acuity and surgical outcomes, but numerical results for all listed secondary measures are not reported. No conclusions about unreported outcomes or longer-term effects follow from the primary result alone.

Statistical evidence and clinical importance are related but distinct. The p-value addresses compatibility with a null model under a test; the estimate and interval describe the size and uncertainty of the observed difference. The registry record does not report a threshold for what magnitude of difference would be clinically important. The findings should therefore be understood as a comparison of observed trial outcomes, not as medical advice or a treatment recommendation.

18. Why This Trial Matters Statistically

This study illustrates why event counts, effect estimates, confidence intervals, and p-values should be read together. The primary outcome is a participant-level event, and the posted counts are small enough that each event contributes materially to the comparison. Reporting only a p-value would conceal the size and direction of the observed contrast; reporting only a point estimate would conceal its uncertainty.

The endpoint also shows the importance of precise definitions. Reoperation due to recurrent vitreous hemorrhage is distinct from any postoperative vitreous hemorrhage. The registry lists both as outcomes, with different roles in the analysis. Keeping the definitions and timeframes separate prevents an outcome with a broader definition from being mistaken for the primary event.

The secondary outcomes demonstrate a further statistical issue: a trial can assess multiple domains, but a collection of unadjusted findings is not equivalent to one confirmatory result. Without a reported hierarchy or multiplicity procedure, secondary evidence should be interpreted with appropriate caution. The record also illustrates the value of transparent reporting of analysis populations, missing-data procedures, and original sample-size rationale, details that are not reported in the registry record.

Finally, planning calculations based on an observed effect are conditional illustrations, not evidence about the power of the completed trial. They depend on assumptions and on an effect estimate that itself has uncertainty. Separating planning quantities from observed results helps prevent a common misreading of post hoc sample-size displays.

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 gives limited information about how participants entered and moved through the study. Eligibility criteria, baseline characteristics, the randomization procedure, allocation concealment, and the parties included in double masking are not reported in the registry record. Without those details, the design cannot be assessed fully for selection, implementation, or balance issues.

The posted primary group sizes are 32 and 34, and the event counts are low. This makes the estimate sensitive to a small number of outcome classifications or events. The record does not report a detailed endpoint definition beyond reoperation due to recurrent vitreous hemorrhage, how outcomes were adjudicated, or how complete follow-up was at 1 month.

The analysis population and missing-data procedures are not reported in the registry record. It is therefore not possible from the registry information alone to determine whether the analysis retained all randomized participants or how missing observations were treated. A detailed statistical analysis plan, including covariate adjustment, sensitivity analyses, multiplicity handling, and interim monitoring, is also not reported.

The registry lists 12 secondary outcome measures, but numerical results for all measures are not reported in the registry record. This limits evaluation of the full secondary-outcome picture and raises uncertainty about selective outcome reporting. Follow-up for the primary outcome is 1 month; longer-term results are not reported for that endpoint in the record. The original trial sample-size assumptions are not reported, so the planning illustrations based on observed effects should not be mistaken for the study's own design justification.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Prospective Randomized Controlled Study of Intravitreal Injection of Bevacizumab for Proliferative Diabetic Retinopathy — NCT01854593.
• Registry record last updated 2014-07-14; status last verified 2014-06.
• Results first posted 2014-07-14.
• 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 record describes a completed, prospective, randomized, double-masked, parallel-group, phase 4 study sponsored by Nihon University. Enrollment was 69. One group received intravitreal bevacizumab 0.16 mg/0.05 ml one day before vitrectomy; the comparator group received a sham injection one day before vitrectomy.

The primary outcome was vitreoretinal reoperation due to recurrent vitreous hemorrhage within 1 month. The posted counts were 1 participant in the bevacizumab group and 7 in the sham group. The registry reports a Fisher Exact p-value of 0.033; the unadjusted recalculation gives a risk difference of -0.175 with a confidence interval from -0.323 to -0.026 and p=0.03.

The registry lists 12 secondary outcome measures, but numerical results for all are not reported in the registry record. Serious and other adverse-event counts were recorded as 0 in each group; deaths are not reported. Details on missing data, analysis populations, multiplicity, and the original sample-size rationale are not reported in the registry record.