Trial of Microplasmin Intravitreal Injection for Non-Surgical Treatment of Focal Vitreomacular Adhesion. The MIVI-TRUST (TG-MV-007) Trial.: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Trial of Microplasmin Intravitreal Injection for Non-Surgical Treatment of Focal Vitreomacular Adhesion. The MIVI-TRUST (TG-MV-007) Trial. (NCT00798317), a randomized phase 3 study. The primary outcome is Proportion of Subjects With Nonsurgical Resolution of Focal Vitreomacular Adhesion at Day 28.

2. Clinical Question

3. Trial Design

NCT00798317 is a completed phase 3 trial sponsored by ThromboGenics. The registry describes a randomized, double-masked, placebo-controlled, multicenter, parallel-group design. The trial studied an intravitreal injection of ocriplasmin 125µg against an intravitreal placebo injection in participants with focal vitreomacular adhesion. The registry enrollment is 326. The listed arm sizes are 245 for ocriplasmin and 81 for placebo; these are the recorded arm figures, not a basis for inferring details about the randomization procedure.

The recorded study start was 2008-12, and primary completion was 2010-06. Its status is completed. The primary endpoint was measured at Day 28 and concerned nonsurgical resolution of focal vitreomacular adhesion. The endpoint description specifies assessment by a masked Central Reading Centre using optical coherence tomography. These details identify the primary outcome and its measurement approach, but do not supply the reading manual, adjudication process, or thresholds used to classify resolution; those details are not reported in the registry record.

The registry lists total posterior vitreous detachment at Day 28 as a secondary outcome. Although the record identifies the broad design and intervention groups, it does not report further details of treatment administration, visit schedules beyond endpoint timeframes, inclusion and exclusion criteria, or the planned statistical analysis. The trial's original sample-size justification and design assumptions are not reported in the registry record. These gaps limit how much can be reconstructed about the protocol from the registry alone, even though the primary comparison and its posted results are available.

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: Intention-To-Treat (ITT), Last Observation Carried Forward LOCF)

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 Proportion of Subjects With Nonsurgical Resolution of Focal Vitreomacular Adhesion at Day 28, measured over Day 28.

The primary endpoint is the proportion of participants with nonsurgical resolution of focal vitreomacular adhesion at Day 28. It is a binary outcome at the participant level: each participant is classified according to whether the specified resolution was observed by the assessment time. The registry describes the analysis population as intention-to-treat with last observation carried forward for missing outcome values. It also specifies that resolution was determined by masked Central Reading Centre assessment of optical coherence tomography images.

A binary endpoint is useful when the clinical question concerns whether a defined event or state has occurred, rather than the amount of change on a continuous scale. Reporting the proportion in each group makes the outcome directly interpretable as the frequency of the defined endpoint among participants in that group. Comparing these proportions estimates how the endpoint frequency differed between randomized groups in this trial. The registry's precise endpoint definition matters: the result concerns the recorded criterion for nonsurgical resolution at Day 28, not every possible measure of visual function, longer-term status, or need for later procedures.

Masked image assessment can reduce the influence of knowledge of assigned group on outcome classification. The registry identifies a masked reading centre, but does not report the operational details of masking or image adjudication. Nor does the endpoint alone describe the full benefit-risk profile. Interpretation therefore needs to remain tied to this outcome, its specified timepoint, and the analysis population and missing-data approach recorded for it.

7. Results Posted in the Registry

• Ocriplasmin 125µg: 25.3% (62/245) versus 6.2% (5/81) on control; risk difference 19.1 percentage points (95% CI 11.6 to 26.7), risk ratio 4.10 (1.71–9.84); 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.

Proportion of Subjects With Total Posterior Vitreous Detachment (PVD) at Day 28

• 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:
  • Ocriplasmin 125µg: 10.6% (26/245) versus 0.0% (0/81) on control; risk difference 10.6 percentage points (95% CI 6.8 to 14.5); unadjusted two-proportion z-test p = 0.002.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the proportion with the event is statistically higher for Ocriplasmin 125µg than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

The registry lists one secondary endpoint: total posterior vitreous detachment at Day 28. Its posted group pattern is directionally consistent with the primary result, in that the endpoint is recorded more often in the ocriplasmin arm than in the placebo arm. The secondary endpoint concerns a related anatomical outcome, but it is not the same outcome as nonsurgical resolution of focal vitreomacular adhesion. A result on one does not establish the other, and the registry does not report an analysis relating individual participants' secondary and primary outcomes.

The secondary analysis is unadjusted. When several outcomes are examined, the chance of obtaining at least one apparently notable result by chance can increase unless the analysis plan accounts for multiple testing. Adjusting for multiplicity can change how confirmatory a secondary p-value is considered. The registry does not report a multiplicity procedure or identify a hierarchy for interpreting outcomes. Accordingly, an unadjusted secondary result generally carries less confirmatory weight than a prespecified primary result, particularly when the trial's full analysis plan is unavailable.

The secondary endpoint can add context to the primary outcome because both address aspects of vitreomacular anatomy at the same recorded timepoint. However, the registry record does not give a detailed rationale for the endpoint, the statistical plan for secondary outcomes, or information about whether the analysis was confirmatory or exploratory. It is best read as supportive descriptive evidence within the posted results, rather than as an independent replication of the primary finding. Its interpretation also remains subject to the same broad limitations of endpoint timing, missing-data reporting, and uncertainty about analysis choices.

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

• Proportion of Subjects With Total Posterior Vitreous Detachment (PVD) at Day 28

9. Statistical Interpretation

10. Statistical Methods Explained

The primary outcome is a percentage of participants with an event, so the basic comparison is between two proportions. The registry gives the group proportions and also records a sponsor analysis using Fisher Exact and an odds ratio. A separate unadjusted recalculation is presented as a risk difference. These approaches summarize the same binary endpoint on different scales; they do not represent different outcomes.

What does a risk difference describe?

A risk difference is the proportion in one group minus the proportion in the comparison group, expressed on an absolute scale. It describes the separation between the observed group proportions. A confidence interval around that estimate indicates a range of values compatible with the data and the calculation method, under the interval's assumptions. When an interval does not include the no-difference value, that is consistent with statistical evidence against equal proportions at the corresponding confidence level. The interval is still an estimate of uncertainty, not a guarantee that the true effect lies within its bounds.

The recalculated risk difference is unadjusted: it compares the posted group summaries without adjustment for other variables. This makes it relatively transparent, but it does not account for covariates or any analysis features not represented in the summaries. The registry record does not report an adjusted primary risk-difference model. It is therefore appropriate to interpret the recalculation as a simple group-level comparison rather than as a reproduction of every feature of the trial's analytic process.

Why use an odds ratio?

An odds ratio compares the odds of an event in one group with the odds in another. Odds and proportions are related, but they are not interchangeable measures. An odds ratio is not a percentage-point difference, and its numerical size should not be described as a direct multiplication of the event proportion. The sponsor reports an odds ratio from a Fisher Exact analysis. Fisher's exact test is a method for assessing association in a two-by-two table, with inference based on the observed counts and the null comparison. The registry reports the sponsor's odds ratio, confidence interval, and p-value; it does not provide a detailed statistical analysis plan explaining all implementation choices.

A p-value describes how unusual data at least as incompatible with the null comparison would be under the test's assumptions if that null were true. It is not the probability that the null is true, and it does not quantify the size or clinical importance of a difference. The reported p-value of <0.001 is evidence against equal odds under the sponsor's specified test. Interpretation should consider it alongside the group proportions and interval estimates, rather than treating it as a stand-alone measure of effect.

What does masking contribute?

The registry describes the trial as double masked and says a masked Central Reading Centre assessed optical coherence tomography images for the primary endpoint. Masking can limit bias when participants, study personnel, or outcome assessors might otherwise be influenced by knowledge of treatment assignment. The record does not detail which roles were masked, how masking was maintained, or how possible unmasking was handled. Randomization is intended to make assigned groups comparable on average, but the registry information alone does not establish every operational safeguard or demonstrate balance on every characteristic.

How should the analysis population be understood?

The primary endpoint specifies an intention-to-treat population and last observation carried forward. Intention-to-treat generally means participants are analyzed according to randomized assignment, regardless of treatment received or adherence, although the precise implementation can vary and is not fully. Last observation carried forward uses the most recent available measurement in place of a later missing measurement. This can preserve an analysis population, but it relies on assumptions about what an unobserved outcome would have been. Its appropriateness depends on the timing and reasons for missingness and on the outcome's course. Counts of missing observations and sensitivity analyses are not reported in the registry record.

More generally, over-dispersion is relevant when a statistical model assumes less variability than the data show. It can make standard errors too small and intervals too narrow if ignored. That issue is a general statistical consideration, not a reported feature of this binary-outcome analysis. The registry does not describe an over-dispersion model or any such adjustment. The principal interpretive safeguards are to distinguish the absolute risk-difference summary from the odds-ratio analysis, retain the uncertainty shown by the intervals, and recognize that the posted record does not specify every analysis choice.

11. Confidence Intervals and Precision

Confidence intervals communicate uncertainty around an estimated group comparison. The sponsor's primary analysis reports an odds ratio of 5.13, with a 95% confidence interval from 1.97 to 17.00. This interval is broad: the data are compatible with a range of odds-ratio magnitudes, not just the point estimate. Its lower bound is above the no-association value for an odds ratio, which aligns with the reported p-value of <0.001. The interval does not state the probability that the true value is within these particular bounds.

The recalculated risk-difference interval is presented on a different scale from the sponsor's odds-ratio interval. A risk difference describes absolute separation in proportions, whereas the odds ratio compares odds. Their interval widths cannot be compared directly as if they used the same units. The group percentages are useful for understanding the observed endpoint frequency, and the confidence intervals are useful for understanding uncertainty in the corresponding comparative estimates. Both are needed for a measured interpretation.

Precision is affected by the amount of information in the data, including the number of endpoint events and the allocation of participants between groups. The registry gives arm sizes and event counts for the primary comparison, but does not report a precision target or the original assumptions used to plan the trial. The apparent width of an interval should therefore be read as a feature of the posted estimate, not as proof that the trial had a particular planned precision. Confidence intervals also do not resolve uncertainties about missing-data assumptions, endpoint measurement, or generalizability. They quantify sampling uncertainty under the analysis approach, not every source of uncertainty relevant to interpretation.

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 illustration gives participants per arm, not total events. Its rows consider planning for 100% of the observed effect, 75% of the observed effect, and 50% of the observed effect. For each assumed effect, the columns state participants per arm for 80% power and participants per arm for 90% power. The 80% column means that, under the stated planning assumptions, a study of that per-arm size would have an 80% chance of detecting an effect of the specified size at the chosen significance level. The 90% column describes the corresponding chance at a higher power target.

The assumptions listed for this illustration are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. The effect to detect is the stated fraction of the observed effect. The planning counts are 56 participants per arm for 80% power and 75 for 90% power when planning for 100% of the observed effect; 87 and 116 when planning for 75%; and 167 and 222 when planning for 50%. These are hypothetical planning figures based on the observed effect, not the trial's original design targets. The original sample-size assumptions are not reported in the registry record.

Smaller effects are harder to distinguish from random variation, so planning to detect a smaller effect requires more participants under these assumptions. The figures are planning illustrations, not observed power; observed power is not a useful substitute for interpreting the estimated effect and its confidence interval after the trial. The unequal recorded arm sizes in the trial also differ from the equal-allocation assumption used for this illustration, so the planning values should not be read as a description of the trial's actual design.

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 = 0.062; treatment proportion p₁ = 0.253; average p̄ = 0.157.
2. First term: z_1−α/2 × √[2p̄(1−p̄)] = 1.96 × 0.5150 = 1.0094.
3. Second term: z_1−β × √[p₀(1−p₀) + p₁(1−p₁)] = 0.842 × 0.4969 = 0.4182.
4. n = (1.0094 + 0.4182)² / (0.1913)² = 55.7, rounded up to 56 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 <- 0.0617283950617284                          # control proportion
p1 <- 0.253061224489796                          # 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(798317)
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 = 56 (80% power), 75 (90% power)
 75% of observed effect: n per arm = 87 (80% power), 116 (90% power)
 50% of observed effect: n per arm = 167 (80% power), 222 (90% power)
power.prop.test: 55.7 
Simulated power at n = 56 per arm: 0.828 (20000 replicates)

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

14. Analyses Reported by the Sponsor

The sponsor's posted primary analysis uses Fisher Exact and reports an odds ratio of 5.13, with a 95% confidence interval from 1.97 to 17.00 and p <0.001. The unadjusted recalculation reports an odds ratio of 5.15, with an interval from 1.992 to 13.31. The two point estimates are close, while the reported interval limits differ. The registry does not mark a discrepancy between the sponsor result and the recalculation.

These estimates should not be treated as competing answers to different clinical questions: both concern the primary binary endpoint and compare the same randomized groups. Differences in estimates or interval limits can arise from analytic details, but the reason for the interval difference is not reported in the registry record. The sponsor's result is the trial's own reported analysis; the recalculation is an unadjusted summary from the posted group statistics. The recalculation does not replace details of the sponsor's analysis plan, which are not reported in the registry record.

Both analyses indicate that the posted primary endpoint comparison is inconsistent with equal group outcomes under their respective calculations. Their uncertainty intervals also show that the exact magnitude is less certain than the direction of the observed comparison. The sponsor's odds ratio should be interpreted as an odds comparison, not as the absolute difference between group percentages.

15. Multiplicity, Missing Data and Analysis Populations

The registry identifies a primary endpoint and a secondary endpoint, but it does not report a multiplicity adjustment, a testing hierarchy, or a statistical analysis plan explaining how multiple outcomes were to be interpreted. Multiplicity matters because examining several outcomes can raise the chance of at least one apparently strong result even when no corresponding underlying difference exists. This does not invalidate an outcome result, but it affects how much confirmatory weight an unadjusted secondary result should carry. The secondary endpoint's unadjusted analysis should therefore be interpreted more cautiously than a result protected by a prespecified multiplicity strategy.

The primary endpoint population is described as intention-to-treat with last observation carried forward. The registry does not report the number of missing primary endpoint measurements, reasons for missingness, timing of last available observations, or sensitivity analyses using other assumptions. Last observation carried forward is a specific way of handling missing measurements, but the record does not explain the protocol's rationale for choosing it or how it was implemented in detail. Missingness may affect estimates if participants with unobserved outcomes differ systematically from those with observed outcomes, and the registry alone cannot show whether that concern changes the result.

The record does not report detailed analysis populations for the secondary endpoint, a per-protocol analysis, or adjusted analyses. It also does not give subgroup plans, stopping rules, interim analyses, or details of how deviations from the intended analysis were handled. These items are not reported in the registry record; their absence from the record does not establish that they were absent from study documents. The available information supports a focused reading of the posted primary and secondary comparisons, while limiting conclusions about the complete analysis strategy and the robustness of results to alternative analytic decisions.

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: macular hole (6.2%), vitreous adhesions (1.2%), visual acuity reduced (1.2%), macular oedema (1.2%), retinal detachment (1.2%).

The registry reports serious adverse events affecting 33 of 245 participants in the ocriplasmin group and 11 of 81 in the placebo group. It separately reports other, non-serious adverse events affecting 105 of 245 and 22 of 81, respectively. These are counts of participants recorded as affected within each category, not estimates of whether an event was caused by study treatment. The registry's adverse-event summary does not provide event-level timing, duration, severity grading beyond the serious classification, or an attribution assessment for these group totals.

The most frequently listed serious adverse-event terms include Macular hole at 6.2%, and Vitreous adhesions, Visual acuity reduced, Macular oedema, Retinal detachment, and Femur fracture at 1.2% each. These registry terms are useful for identifying what was recorded, but do not by themselves establish a causal relationship or indicate how events were distributed across time. Deaths are not reported in the registry record. The event summaries should be read alongside the efficacy endpoint and with awareness that the registry does not supply fuller safety narratives or a detailed safety analysis plan.

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

The posted results show a higher observed proportion of Day 28 nonsurgical resolution of focal vitreomacular adhesion in the ocriplasmin arm than in the placebo arm. The sponsor's statistical analysis reports evidence against equal odds for this endpoint, and the unadjusted recalculation points in the same direction. This is a statistical description of the randomized groups and the endpoint recorded in this trial.

The result does not mean that every participant assigned to ocriplasmin experienced resolution, nor that no participant assigned to placebo did. Group proportions describe frequencies, not individual predictions. The result also does not, by itself, establish the size of any effect in a different population or under a different outcome definition. The primary measure is specific to nonsurgical resolution at Day 28, assessed by masked Central Reading Centre optical coherence tomography evaluation. It should not be taken as a result for longer-term outcomes, other aspects of vision, or all possible consequences of the condition.

A small p-value is not the probability that the treatment has no effect, and it does not measure clinical importance. The confidence interval gives a range of values compatible with the data and method, but it does not incorporate every uncertainty, including the unreported details of missing data and the full analysis plan. The registry's safety counts are separate from the efficacy comparison and do not establish causation.

In short, the record supports a difference in the posted primary endpoint comparison and provides uncertainty estimates, while leaving important questions about generalizability, longer follow-up, missing-data robustness, and broader safety interpretation outside what is reported. The result should be understood as evidence about this trial's recorded endpoint, population, and timepoint, rather than as a complete account of all possible outcomes.

18. Why This Trial Matters Statistically

This trial illustrates why a clinical result is best read through its endpoint definition, effect measure, and uncertainty interval together. The primary outcome is a binary event assessed at a defined timepoint, so the group proportions provide an accessible starting point. The sponsor's odds ratio and the recalculated risk difference then express the contrast on different scales. Seeing those summaries as complementary rather than interchangeable helps prevent a relative measure from being mistaken for an absolute percentage-point change.

The example also shows the value of examining precision, not only statistical significance. The sponsor's confidence interval spans a broad range of odds-ratio values even though its lower limit is above the null value. That combination illustrates that evidence for a group difference and uncertainty about its exact magnitude can coexist. Statistical evidence should not be confused with certainty about the magnitude or with proof of broader clinical importance.

Other features matter to interpretation. Masked central image assessment is relevant because the primary endpoint depends on classifying an imaging outcome. The intention-to-treat and last-observation-carried-forward description makes missing-data handling visible, while the lack of missingness counts and sensitivity analyses limits assessment of robustness. The secondary outcome offers related context, but its unadjusted status and the absence of a reported multiplicity plan counsel against treating it as an equivalent confirmatory test.

Finally, the planning illustration demonstrates how assumptions affect sample-size requirements: planning for smaller effects calls for more participants under the stated framework. Those figures are not a reconstruction of the original design. Together, these points make the trial a useful case for separating the posted data, the analysis summaries, and the additional information needed for a fuller appraisal.

19. Limitations

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

The registry record leaves several trial-specific details unavailable. It does not report the eligibility criteria, baseline characteristics, or participant flow, so the composition of the study population and the handling of exclusions cannot be evaluated from this record alone. The record gives the primary analysis population as intention-to-treat with last observation carried forward, but does not report missing outcome counts, reasons for missingness, or sensitivity analyses. This makes it difficult to assess how much the primary comparison might depend on the missing-data approach.

The record does not report the original sample-size justification or the assumptions used to plan the trial. The separate planning illustration is based on the observed effect and should not be mistaken for the trial's design rationale. Details of the randomization sequence, allocation concealment, masking procedures, imaging adjudication, and the full statistical analysis plan are also not reported in the registry record. Nor are subgroup results or longer-term results for the primary endpoint posted in the registry record described for this trial.

The primary outcome is specific to nonsurgical anatomical resolution at Day 28. It cannot by itself answer questions about durability, other visual outcomes, later procedures, or outcomes in populations not characterized in the registry. The secondary result is unadjusted, and a multiplicity strategy is not reported. The adverse-event section gives group totals and selected serious-event terms, but not detailed event narratives, attribution, or deaths. These limitations do not negate the posted comparison; they define what the registry record can support and what remains uncertain.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Trial of Microplasmin Intravitreal Injection for Non-Surgical Treatment of Focal Vitreomacular Adhesion. The MIVI-TRUST (TG-MV-007) Trial. — NCT00798317.
• Registry record last updated 2014-12-17; status last verified 2014-04.
• Results first posted 2013-01-30.
• 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

NCT00798317 is a completed phase 3 randomized, double-masked, placebo-controlled, multicenter, parallel-group trial sponsored by ThromboGenics. It studied intravitreal ocriplasmin 125µg against intravitreal placebo in participants with focal vitreomacular adhesion. Recorded study dates are 2008-12 for start and 2010-06 for primary completion, with registry enrollment of 326.

The primary endpoint was nonsurgical resolution of focal vitreomacular adhesion at Day 28, assessed by masked Central Reading Centre optical coherence tomography evaluation. The registry reports a higher endpoint proportion in the ocriplasmin arm than in the placebo arm, with a sponsor-reported Fisher Exact odds ratio and an unadjusted recalculation on the risk-difference scale. A related secondary endpoint concerns total posterior vitreous detachment at Day 28.

The record also reports serious and other adverse-event counts. Important interpretive details—including the original sample-size assumptions, multiplicity approach, missing-data counts, and detailed analysis plan—are not reported in the registry record.